Open Mind

PCA part 4: non-centered hockey sticks

March 6, 2008 · 531 Comments

In parts 1, 2, and 3 we’ve looked into the basics of PCA. The essence is that we can view multiple data sets as a vector data set, or as points occupying a (sometimes very) high-dimensional space. The original basis for this space is simply the variables with which we express the raw data; we could call this the canonical basis. In this sense, a “basis” is like a coordinate system for the space, and the canonical basis is the set of variables which define the raw data.


But we don’t have to use just that basis; from a purely geometrical point of view any basis will do. For position in space, e.g., we can define a standard set of x, y, z coordinates, but there’s a great deal of freedom in how to choose even those coordinates. We can pick any point as our origin (where x=y=z=0), as well as any directions for the x-, y-, and z-axes. It simplifies many things if the x-, y-, and z-directions are all perpendicular to each other. It also helps if the distances along each direction are expressed in measures of the same size; if we gave the x-coordinate in meters while y and z were in inches, it could lead to a lot of confusion.

Sometimes there are advantages to a particular basis. For example, we might take as “canonical” coordinates for position, x, y, z coordinates in which the origin is the center of the earth, x points in the direction from the center of the earth to where the prime meridian (which defines longitude 0) meets the equator, y points from the center of the earth toward where longitude 90 deg. East meets the equator, and z points from earth’s center toward the north pole. It’s a perfectly good coordinate system, but if what we’re really interested in is studying the movement of a canoe on a lake, we’ll find it not very convenient. A better choice for the canoe problem, would be to choose a reference point on the lake as our origin (maybe the point on the lake surface where we usually keep the canoe), then choose coordinates so that x points east, y points north, and z points up (this can be referred to as the ENZ system, or “east-north-vertical”). We still have 3 coordinates, which is what we need for a 3-dimensional space, but we’ll find that things are a lot simpler using this system than the other.

We might even reap simplification from the coordinate system itself. Unless we sink the canoe, or lift it high out of the water, we’ll notice that our movements all seem to be restricted to the surface of the water, which conveniently corresponds to z=0. If we took a large number of measurements of position, and performed PCA, we’d likely notice that the last (lowest-variation) PC would be simply the up-down coordinate, and that its variation is tiny compared to the others. This would indicate that we might be able to omit that coordinate (use just the first 2 PCs) without any substantive loss of information, and that would make analysis even simpler and easier.

The real essence of PCA is that it enables us to define a new coordinate system for our data space, one based on the observed variations of the data itself, which gives us an excellent chance to reduce complexity, possibly even reveal some insight. PCA by itself doesn’t alter the data at all, and certainly doesn’t “create” patterns that don’t already exist, it simply offers us new coordinates with which to alter our description of it. A classic example (dealt with in part 1) is the case in which our space is 2-dimensional. The PCs (for normalized data) end up being proportional to the sum, and the difference, between the normalized data values. This does not represent a change to the data — instead of giving x and y we give numbers proportional to x+y and x-y, but the positions don’t change. But as easy as it is to transform from canonical coordinates to sum/difference coordinates, it’s just as easy to transform back. No information is lost, we just look at it from a different viewpoint.

One of the real advantages we may reap is to reduce the number of coordinates we have to use without losing important information. The canoe problem illustrates this perfectly: even if we used some bizarre directions for the coordinate system we would still expect the final PC to be the up-down direction, that its variation would be tiny compared to the others, and that it can probably be discarded without losing anything meaningful. This can be especially desirable when estimating something (like temperature) from a very large number of proxy data sets. Sooner or later we’re likely to do some sort of multiple regression, to calibrate the relationship between our proxies and observed temperature measurements. But if we keep all the proxies, we may have so many degrees of freedom in our “predictor” variables that we end up fitting a lot of the noise in the data, rather than just the signal. This is the classic problem of overfitting, a recurrent problem in analysis, nothing to be sneezed at. So, it’s entirely natural that those who wish to use proxy data sets to estimate past temperature (the most famous being the original “hockey stick” of Mann, Bradley, & Hughes 1998, hereafter called MBH) would use PCA.

If we keep all the PCs, then we don’t reduce the problem of overfitting. But we also have zero information loss, and nobody could accuse anyone of having the massaged the data to achieve a particular result. It’s the same data, just in different coordinates! But when we omit all but the leading PCs, then we might be accused of manipulation by way of our choice of which PCs to include and which to omit. Also, if we keep all the PCs it doesn’t matter whether we normalize the data (so we use the correlation matrix) or not (so we use the covariance matrix). But if we omit PCs, then whether we normalize or not can have a profound impact on the variation present in the various PCs, and could affect our decision which to include and which to omit. In fact, we really don’t even have to zero the data! We can perfectly well do PCA based on variation from the origin rather than the average. But again, it will affect what the individual PCs look like and how much variation they contain, and might therefore affect the decision which to include/omit.

Now to the crux of one of the criticisms levelled against MBH by McIntyre & McKitrick (hereafter MM). The criticism which spurred this series on PCA in the first place is that MBH used non-centered PCA (sometimes called “de-centered” PCA) rather than the usual, centered PCA. In part 1 our very first step was to subtract from each data point the average value of the series — this is the centered case. But MBH, instead, chose to subtract the average value during the calibration interval rather than the entire time span. This makes it non-centered PCA. MM claimed that the hockey stick resulted from the use of non-centered PCA, and that non-centered PCA is just plain faulty anyway.

First let’s dispense with the last claim, that non-centered PCA isn’t right. This point was hammered by Wegman, who was recently quoted in reader comments thus:


“The controversy of Mann’s methods lies in that the proxies are centered on the mean of the period 1902-1995, rather than on the whole time period. This mean is, thus, actually decentered low, which will cause it to exhibit a larger variance, giving it preference for being selected as the first principal component. The net effect of this decentering using the proxy data in MBH and MBH99 is to produce a “hockey stick” shape. Centering the mean is a critical factor in using the principal component methodology properly. It is not clear that Mann and associates realized the error in their methodology at the time of publication.”

Just plain wrong. Centering is the usual custom, but other choices are still valid; we can perfectly well define PCs based on variation from any “origin” rather than from the average. It fact it has distinct advantages IF the origin has particular relevance to the issue at hand. You shouldn’t just take my word for it, but you *should* take the word of Ian Jolliffe, one of the world’s foremost experts on PCA, author of a seminal book on the subject. He takes an interesting look at the centering issue in this presentation.

Wegman’s right about this much: a non-standard centering convention will indeed emphasize the variation of the mean, which turns out to be the main difference between the 20th century and the rest of the time span. What he fails to realize is that that’s the point. He’s also right that the changes associated with it will become more prominent in the PCA analysis, causing those changes to “move up” the PCA list. Again, that’s the point.

PCA (centered or not) doesn’t create patterns at all, they have to be there already even to “exhibit a larger variance.” PCA most certainly cannot “create” a statistically significant relationship between that variation and the observed temperature data. That the relationship is significant emerges from both the regression itself, and the testing done on the verification data (more about that in a moment).

What impact will non-centered PCA really have? Downloading all the data used in MBH and reproducing their analysis is a lot of work, and has already been done (by several researchers), so I decided to take the simpler and easier approach of generating artificial data. I created an artificial temperature time series which follows a distinct “hockey stick” pattern, and also generated 40 separate artificial proxy data time series, all spanning the time interval from 1400 to 1980. I assumed that the temperatures from 1900 to 1980 are known, while those before 1900 are not. The proxy data series were generated by computing a response to the temperature signal and other factors as well. And all the series include random noise. The task is to use PCA to characterize the proxy series, use only a few PCs to characterize it, then determine the relationship between the PCs and observed temperature during the “known” time period (i.e., the calibration interval, from 1900 to 1980), then use that relationship to estimate temperature before 1900. Let’s do this using the non-centered approach of MBH, and the centered approach.

In reality, one wouldn’t use all the known data to calibrate the proxies. Instead, one would use part of the known data, then create the prediction, then check prediction against observation in the remaining part. This is “verificiation,” an independent check on whether or not the method is working. We can’t do this if verification uses the same data we used to calibrate — that would only show that if we fit our proxies to the calibration data, then it fits the calibration data. And we already know that! But this is just an exercise using artificial data, so I’ll skip the verification step.

First let’s use the non-centered method. I subtracted from each proxy series its average during the calibration interval. Then I normalized each series so that they’re all about the same “size.” Then comes PCA. When we do so, the very first PC is by far the biggest one of all, and it looks like this:

noncenterpc1.jpg

It looks strikingly like the (artificial) temperature data:

artitemp.jpg

If we do a regression of temperature against PC1 during the calibration interval, we get this:

noncenterfit.jpg

That’s an excellent fit! If we use the regression line to take the PC1 value and transform it to temperature, we get an outstanding match with actual temperature, not only during the calibration interval but over the entire time span. It appears that the method works excellently, and that PC1 (which dominates the variation) is sufficient to generate it.

Now let’s use the MM approach and see what happens. They claim to reproduce the MBH approach precisely except for the use of non-centered PCA. So this time, we’ll subtract from each proxy series the average value over the entire time span, normalize, and run PCA. This time, the 1st PC looks like this:

centerpc1.jpg

Whoa! That doesn’t look at all like the temperature data. If we now regress temperature against PC1 during the calibration interval we get this:

centerfit1.jpg

It’s fair to say that this fit isn’t very good. In fact, it’s fair to say (and the numbers confirm) that this fit sucks. If we use it to estimate past temperature, the estimate doesn’t match observation. At all. It shows spurious warming in the late 16th century and cooling in the mid-19th century, but no real 20th century warming and certainly no hockey stick.

What’s going on here? Didn’t we use exactly the MBH procedure, except to switch to centered PCA (which should be valid)? We ran the PCA, kept only the 1st PC, did the regression, and generated our estimate. But it came out horribly wrong! But something is going on — because the “standard” choice (centered PCA) gave us the wrong result while non-centered PCA gave the right answer! For this artificial data we already know the answer: temperature looks like a hockey stick. This is what MM did; they ran (centered) PCA on the actual data, kept only the first 2 PCs (as MBH had done), ran the regression, and generated the estimate. But it came out dramatically different from the MBH estimate.

The difference in estimates emphasizes the reason for MBH’s choice of non-centered PCA. Its purpose is to emphasize differences between the 20th century (the calibration interval, actually) and the remainder of the time span. That main difference is the 20th-century temperature increase, so that becomes the prime focus of the PCA results; that’s why most of the variation is in the 1st PC (artificial data) or first 2 PCs (real data), including the 20th-century increase which enables us to estimate the proper relationship between proxies and temperature. None of these factors are created by the non-centered PCA, but they are emphasized by it, bringing the relevant variation high up the list of PCs. That enables us to use just a few PCs and get the correct result.

With centered PCA, all the relevant variation is still there. It’s all still statistically significant. But the analysis has less emphasis on isolating the 20th-century changes, so the variation which correlates strongly with observed temperature change (which is the variation we really want) is still among the leading PCs, but no longer in the 1st PC (artificial data) or first 2 PCs (real data). Properly to reproduce the MBH procedure, when we switch from non-centered to centered PCA we also have to change the selection of PCs — because we can expect that the important variation may not be so high up the PC list as it was when the method itself (non-centered PCA) is chosen to emphasize it.

So let’s do it right. Let’s use centered PCA, but this time let’s not restrict ourselves to only the 1st PC (artificial data) or first 2 PCs (real data) just because that’s what emerged from non-centered PCA. With the artificial data, this time it’s the first two PCs that contain the bulk of the variation. We’ve already seen the 1st PC, here’s the 2nd:

centerpc2.jpg

Lo and behold, there it is! The variation relevant to temperature is still there, it was always there, it’s still among the leading PCs, it always was, but now there are two big PCs instead of just one, and the temperature-related changes are in the 2nd PC. If we regress temperature during the calibration interval against this PC, we get this:

centerfit2.jpg

Now that is a good fit! If we use this regression (more properly, a multiple regression on the first two PCs), it turns out that temperature during the calibration interval is strongly (and significantly) related to the 2nd PC, but not to the 1st PC. When we estimate temperature over the entire time span, we get: a hockey stick. It also matches (quite excellently) the actual temperature (which in this case we know, because it’s artificial data).

All of which emphasizes the fact that PCA doesn’t change the data. It only changes our description of it. The variation in proxies which correlates with temperature was always there, PCA only isolates it in a tractable way. If we use centered PCA, it turns out to be in the 2nd PC, but with non-centered PCA it ends up in the 1st PC. That’s the reason for the choice of non-centered PCA: to make the relevant, i.e. temperature-related, variation end up higher in the PC list. And: it worked.

I’d guess that some of you are thinking, “Can it really be that simple? Did MM really not get this? Did they really discard the relevant PCs just to copy the bare number of PCs used by MBH, without realizing that the different centering convention could move the relevant information up or down the PC list?”

You betcha. When done properly on the actual data, using 5 PCs rather than just 2, the hockey stick pattern is still there even with centered PC — which is no surprise, because it’s not an artifact of the analysis method, it’s a pattern in the data. Here’s a comparison of PC#1 for the North American ITRDB (international tree ring data base) data using the MBH method (red), and PC#4 from using the MM method (blue, which has been adjusted to have the same mean and amplitude as the red curve, but it’s only the relative pattern of variation that matters):

pc1pc4.jpg

Some of you might be thinking, wouldn’t MM have noticed that their fit (the one lacking a hockey stick) failed statistical significance when they did the verification step to check the correctness of their version? Probably yes. Too bad they simply didn’t do the verification step. But independent researchers have replicated the MM procedure and subjected it to verification. It failed.

The MBH hockey stick result has been the target of more scrutiny, criticism, and downright hostility, than perhaps any other aspect of climate science. That may be because there are things to criticize; not necessarily valid ones, but things nonetheless. It may be because it’s one of the things that has had the greatest impact on public perception of global warming, by making the unusual character of modern warming so vivid. It has certainly made Mike Mann one of the most frequent victims of vicious personal attacks (Mike Mann and Jim Hansen seem to be the people most hated by global warming denialists).

The use of non-centered PCA is not the only criticism of the MBH hockey stick levelled by MM. There are several — but as far as I can tell, none of them are any more valid. I have a strong suspicion that they’ll be repeated in reader comments here. Perhaps some day I’ll address those mistakes by MM as well. In the meantime, I have one request: before you raise other issues about the hockey stick, address this one.

UPDATE UPDATE UPDATE:

Readers referred to figure 2 in Wahl & Amman, so here it is (click for a larger, clearer view):

wafig2.jpg

Categories: Global Warming · climate change

531 responses so far ↓

  • caerbannog // March 6, 2008 at 6:57 pm

    In my work, I use the singular-value decomposition (SVD) method from time to time (note to lurkers: you use the SVD method to calculate principal components).

    The very *first* thing I do after computing the SVD is to look at the singular-value magnitudes. Only then will I know what do do next.

    So did M&M do anything more than demonstrate that you can screw things up if you don’t bother to look at the singular-value magnitudes before charging ahead with your data analysis?

  • The Flea // March 6, 2008 at 7:00 pm

    Wow! That’s all I can say right now!!!

    Great post!!

    The Flea

  • Hank Roberts // March 6, 2008 at 7:35 pm

    Ok. One thought — I suspect you’ll want to edit the first post to clarify it as questions arise.

    Can you footnote the actual artificial data sets made up for this illustration?

    1) an artificial temperature time series which follows a distinct “hockey stick”

    2) 40 separate artificial proxy data time series

    3) by computing

    4) the temperature signal (that’s item 1?)

    5) and other factors (what they?)

    6) all the series include random noise. (how created?)

    I know you don’t want to overload the first post, wondering if there’s a way to explain those details via links.

    When you refer out to the actual analyses done with real data, cites to those would help as well.

    I wish I could come scrub your tile or trim your hedges or something to contribute my own skills (grin) to this.

  • dhogaza // March 6, 2008 at 7:49 pm

    Why not just delete those comments that aren’t relevant to your post, i.e. attempts to divert the discussion to “strip-bark samples”, etc?

    Including this one, after you read it? :)

    Great post, BTW.

  • BoulderSolar // March 6, 2008 at 8:07 pm

    Jolliffe’s position on uncentered PCA in the reference you cited is the following:

    “It seems unwise to use uncentred analyses unless the origin is meaningful. Even then, it will be uninformative if all measurements are far from the origin”

    I think this applies for MBH. Please comment

    [Response: In this case, the origin is meaningful (it's the average during the calibration interval), and not all measurements are far from the origin.]

  • Gavin's Pussycat // March 6, 2008 at 8:21 pm

    Very nice explanation, though essentially the same as given by Schmidt and Rahmstorf in 2005 on RC (IIRC; RC is down).

    Reading this, one question came up: what if tree ring growth depends not only on temperature, but on same other factor (moisture? precipitation? we know it does…), but one that does not vary over the calibration period. Say, tree ring growth is a function of temperature and “serendipity”. But serendipity is constant over the 20th century. You can calibrate as much as you like, but you won’t be able to get a coefficient between any of the PCs and serendipity. When calibrating temperature, it’s just as if serendipity doesn’t exist.

    Then, also assume that serendipity varies wildly (or is completely different) during the Middle Ages. Then you may have the situation that also tree ring growth varies wildly, which will be interpreted in the estimation step as temperature variation.

    Clearly this is an insoluble problem with any analysis technique, not only PCA; a causative factor that’s “not there” (does not vary) in the calibration period is just impossible to take into account. That would even be so if PCA tells us about its the existence.

    Am I missing something here? Can there be serendipity-like factors? Note that a requirement is that they significantly and independently (i.e., not through temperature) affect tree ring growth. Is this an argument for including not only tree rings, but as many as possible different types of proxies, like glaciers, whatever, likely to have different dependency patterns on causative factors? Is this mathematically tractable?

    [Response: I think you've hit a nail on the head. In fact I did include a non-temperature factor which influences the proxies. I think the relevant factor is: if the non-temperature factor affects all the proxies in the same way that temperature does, it simply won't be possible to disentangle the influences. But if the temperature affects proxies one way while the other factor affects them differently, or affects different proxies in a different way which can be separated from the temperature influence, then they can be disentangled.

    All of which emphasizes that temperature reconstructions will never lack uncertainty. But the criticisms I've heard so far don't pass muster.]

  • P. Lewis // March 6, 2008 at 8:23 pm

    I have to say that the way you’ve approached this (i.e. the use of artificial data) is IMHO very clever. I look forward to reading it a couple more times in greater depth.

    HB referred to other analyses above, one of which is probably this one by Wahl and Ammann (or their actual paper). However, you don’t need to get hung up on the latter, because the blog post suffices.

  • Zeke // March 6, 2008 at 10:22 pm

    Excellent article Tamino. One thing I might add is an explicit test of MM’s argument that this technique necessarily produces hockey stick shapes. An easy method come to mind:

    Do an uncentered PCA on a randomly generated dataset that exhibits a warm period or two in the past that exceeds present temperatures. See if this warm period drops out of the results.

  • Ian // March 6, 2008 at 10:42 pm

    Boulder Solar re: uncentered analyses,

    Keep going through Jolliffe’s presentation - he elaborates on one instance of “meaningfulness” in a later slide as follows: “One case where uncentred analyses are appropriate is if we can assume that the population means of our variables are zero, although the sample means are not. This is the case when the data are anomalies.”

  • Surly // March 7, 2008 at 1:58 am

    Thanks so much for this series. I struggled through a few of the equations but appreciate the way you worked us through the steps and issues. I am glad to finally get this part as I was really looking forward to reading your take on MBH and the hockey stick issue. Can you, for the sake of those of us who want to discuss this with average people who have little background, give us a take home statement?

    Thanks again.

    [Response: Take-home points:

    * The claim that non-centered (or de-centered) PCA is invalid, is itself invalid.

    * If you switch from non-centered to centered PCA, *and* do the PC selection properly, you get the same hockey stick that MBH got.]

  • Paul Middents // March 7, 2008 at 3:03 am

    Great set of posts. There may not be enough equations to ward off the trolls. I too would be interested in the data refered to by Hank. I’ll even hold the bucket while he scrubs your tile!

  • J // March 7, 2008 at 3:05 am

    Tamino, let me apologize in advance if I’m wrong about this. But here goes.

    Let’s say you have a lot of initial data sets, some of which show a 20th-century trend (”hockey-stickish” data sets), and others of which don’t.

    If you do a PCA with the data centered on the calibration period, you’ll likely end up with a hockey-stickish PC1, because PC1 will be weighted most heavily by the raw data that showed a rising trend during the calibration period.

    If you do PCA with the data centered on the series-wide means, then the hockey-stickish pattern may be relegated to one of the lower PCs.

    Either way, of course, you could select it and use it in a regression model to predict temperature or whatever.

    Now, here’s where I think there may be some fundamental disagreement. Some people may say that’s problematic — essentially, your method preferentially selects a PC component that looks hockey-stickish (in the one case by ensuring that PC1 is primarily based on the most hockey-stickish proxies; in the other case by manually looking through the PCs and picking PC3, 4, 5, or whatever happens to be the most hockey-stickish). In essence, you’re taking a bunch of proxies, some (most?) of which don’t themselves look like a HS, and using PCA to pull out only the part of the total data set that do look like a HS.

    Other people would say that there’s nothing wrong with that — during the calibration period, we know that temperatures were trending upwards, so there’s nothing wrong with a methodology that transforms the original data in such a way that it matches that upward trend.

    I’m afraid I’m not explaining this clearly (or, I may be simply flat-out wrong). But I think this may fall into the gray zone where something isn’t objectively correct or incorrect.

    If you see the MBH method as simply trying to find a transformation of the proxy data that best matches the known 20th century trend, and using that transformed data set to examine the past, this PCA based approach looks fine. On the other hand, if you see the MBH method as trying to faithfully represent the patterns in most or all of the raw proxies, regardless of whether that matches your assumptions about the 20th century trend, then this approach seems suspect.

    Both of these viewpoints actually seem to have some merit to me. But this is all outside my own field and I ought to recognize that I’m not really qualified to comment on this.

    [Response: It is possible to "seek out" a hockey-stick pattern by picking out just the PCs that look like that -- if there is one in there. There might be, but there might not!

    But that's not what MBH did. They used non-centered PCA, then applied strict "selection rules" to choose which ones to keep. They didn't keep just the hockey-stick PC (which in their analysis is the 1st), they also kept the 2nd. Applying the *same* selection rules to the centered case indicates that 5 PCs should be retained, and the hockey stick is mainly in the 4th.

    Also, you can in some cases find a hockey-stick PC if you're looking for it (but not always, it has to be there already), but that *won't* necessarily make it fit temperature very well in the modern era. The 20th century isn't just the blade of a hockey stick, it's rise from about 1915 to 1945, rough constancy 1945 to 1975, and rise again post-1975. More to the point perhaps, it certainly *won't* make the analysis pass significance tests when applied to the verification data.

    MBH didn't "go looking" for a hockey stick. They applied non-centered PCA, standard selection rules, did the regression, confirmed it with verification, and the hockey stick emerged. I guess the real take-home point is that if you use centered PCA, you get exactly the same thing.

    One more thing, which I didn't mention in the post but is surely relevant. You can do the analysis *without* PCA. It suffers from a loss of precisoin because of the vastly greater number of degrees of freedom, but is still valid. And what emerges? A hockey stick. You can also make a random selection of only a limited number of proxies, and repeat that process many times with different random selections, and average the results. The result? A hockey stick.

    The simple fact is that the hockey stick pattern is most assuredly NOT an artifact of the use of non-centered PCA. You get the same thing with centered PCA (using proper, and objective, selection of PCs), with all the proxies as is, and with random subsets of proxies.]

  • Bob North // March 7, 2008 at 4:52 am

    HB/Tamino -
    Thanks for the articles on PCA. I am sure that I will have to go through the whole series as couple of more times before I fill confident in my understanding, though I definitely feel I better understand things as it stands.

    To kind of follow along with Hank R’s question regarding posting the underying simulated data, one thing that struck me was that the correlation of your proxies with PC1 were a “little too good”. I don’t believe you would get that good of correlation if you looked at GISS v Hadcrut v NCDC v UAH v RSS (normalized to the same base period of course). If you could give a little more information on the way you developed your simulated proxies and added noise and made sure they didn’t vary too perfectly witht simulated temperature, it would be helpful to understanding the process. Also, any further thoughts on why the uncentered analysis provided such a better match than the centered analysis would also be helpful.

    One final thing I have been thinking about relative the whole question of using PCA on proxies such as tree rings is this. What if the primary PC actually represents a combination of environmental factors (e.g., some combination of temp, rel. humidity and soil fertility) rather than a single factor such as temperature. Since a PC is nothing more than a mathematical construct, is there any reason why we should assume it would represent a single environmental variable?

    regards,
    Bob North

    [Response: Indeed the fit is a *lot* too good! But it's artificial data for illustration purposes, so it's kinda designed that way.

    In addition to an artificial temperature series I also generated an artificial "other influence" series. Temperature was designed as a hockey stick (actually, to mimic early-20th-century warming, mid-century flattening, then warming) plus random noise. It was flat (except for the random noise) before 1900. For "other influence," I just sketched a smooth curve from 1400 to 1980 in a meandering way, digitized that, and added random noise. The proxies were generated as linear combinations of the two influence curves, plus random noise. Different proxies were given different (random) response rates to both temperature and "other influence."

    The "too-too-good fit" is because there are only 2 influences (real life has many more), the response to the influences was strictly linear (I suspect in real life there's some nonlinearity), and the noise was about the right size but certainly *consistent* (although different) for all the series. Hence it was easy for PCA to separate the signal from the noise, and to separate the two different signal components.

    Finally, it's indeed possible that PCA is isolating a "combined" influence, which is common to all (or most) proxy responses, and is partly but not entirely temperature. PCA really doesn't isolate a temperature influence, or isolate physical processes -- it isolates correlated variation. It's up to the regression on the calibration data to isolate the temperature influence, and it's up to the verification data to show that the relationship is strong enough actually to estimate unknown temperature.]

  • MrPete // March 7, 2008 at 4:53 am

    What’s most interesting to me in this is the challenge of connecting PCx to any specific physical meaning.

  • Ed Davies // March 7, 2008 at 12:12 pm

    Am I right in visualizing that the effect of the centred PCA is to promote the random noise in the data to the first few PCs?

    [Response: No, not random noise. Just plain old random noise is always gonna be far down the list. It can, however, promote (only) one of the meaningful variations by magnifying its total variation.]

  • MrPete // March 7, 2008 at 12:13 pm

    Tamino, you said MBH didn’t “go looking” for a hockey stick. They applied non-centered PCA, standard selection rules, did the regression, confirmed it with verification, and the hockey stick emerged.

    Now we’re getting to the crux of the matter.

    Tamino, haven’t you just clarified for all of us kindergarten stats students ;) that PCA is simply a mathematical transformation of the data, a sophisticated “sorting” if you will? That it brings the “strongest” signal in a sense to the fore? Doesn’t matter what that “signal” means. Correct?

    So, PCA is agnostic with respect to source and meaning of signal. That tells me the interpretation is still key. You need good data. You need good reason to assign physical meaning to that data. Correct?

    More importantly, PCA is a method that will pull a strong signal to the fore in a field of mostly-weak signals. Toss a pile of data in, get the strongest signal out. Correct?

    This also means, if there’s a few strong signals present in a large data collection, most of the data I toss in has little if any impact on the outcome and can be ignored. You said it yourself: it’s a nice method of data reduction.

    The methoddoesn’t care what the “strongest signal” means, doesn’t care if it is truly significant for our study. And most important, the method doesn’t care if that “signal” has any physical validity with respect to what is being studied. That’s all in the hands of the scientist feeding data in and interpreting the information that emerges.

    What Steve demonstrated, and many others have confirmed (most recently Craig Loehle) is that the hockey stick is incredibly dependent on a small portion of the data set. More than anything else, in the proxy series used to create the infamous hockey stick graph, it is dependent on the presence of stripbark BCP data from a tiny region of the world. The rest of the proxies are so weak as to have little impact on the results.

    The hockey stick proves too much. It proves that stripbark data (up to the 1980’s) was nicely calibrated to the temp record for a certain period of time in the 20th century.

    Remove stripbark and the hockey stick begins to melt.

    Substitute a variety of other “hockey stickish” data, that clearly has nothing to do with climate at all (e.g. stock prices) and you get a hockey stick with similar stats.

    But even more telling: update the BCP data itself and you get the “divergence problem.”

    Tamino, it’s good that you’ve elucidated the analytical details of PCA. Don’t lose the forest for the trees. Step back and consider what’s going in and coming out. Dont’ get caught treating it as a magic box where you put in a number, do A, B, C and voila the answer is 42!

    You get the same thing with centered PCA (using proper, and objective, selection of PCs), with all the proxies as is, and with random subsets of proxies.

    Not if you leave BCP out. Various people believe BCP is irrelevant. If so, then it should make no difference at all if one leaves BCP’s out of the equation, shouldn’t it! Same thing with the Polar Urals data.

    There’s nothing wrong with using a method that highlights certain data in a large data set. But it must be used with care. All those “less strong” signals are telling us something as well. So is the “noise.” We can’t presume to know that the signal we’ve found is a temperature signal.

    [Response: You're right that PCA doesn't generate the patterns -- just affects the order of their prominence -- and that it doesn't care about their physical meaning.

    You're quite confident that if we remove the bristlecone pines, the hockey stick falls apart (and indeed that's a totally separate issue from PCA). But according to what I've seen, MM got *that* part wrong too!]

  • fred // March 7, 2008 at 12:47 pm

    tamino, could you explain how, if you just have a set of series, and know nothing about what they represent, and you’ve decided for some reason (not sure why you would do this) not to use the series mean, but the mean of a subset of the series, how do you pick what subset to use? Is there some mechanical method which does not depend on prior knowledge of what is in the data?

    Or is this the wrong question?

    [Response: I'm not aware of any mechanical, set procedure. I think the motivation in this case was to emphasize the differences between the mean of the calibration interval and that of the preceding centuries, so the average of the calibration interval was chosen as the "origin."

    In retrospect, I'd say it might have been better to use centered PCA -- not because it's mathematically more valid or more precise, but because it's *simpler*, gives essentially the same result, and would have made the result less vulnerable to criticism. But that's a reason relevant to persuasion rather than mathematics.]

  • steven mosher // March 7, 2008 at 1:43 pm

    Nicely done tamino. There are several other problems here that are detailed in this post.

    http://www.climateaudit.org/?p=609#comments

    [Response: He has lots of objections, both methodological and data-related. Don't take McIntyre's word for it; maybe I'll post on that issue (and others) someday.

    Despite all the criticisms that can be levelled against the MBH procedure (valid or no), the overwhelming fact is that you get the hockey stick even if you don't use PCA at all.]

  • George // March 7, 2008 at 1:56 pm

    Did MM really not get this? Did they really discard the relevant PCs just to copy the bare number of PCs used by MBH, without realizing that the different centering convention could move the relevant information up or down the PC list?”

    So, what you are saying is they discarded the hockey stick PC.

    What’s the big deal?

    It was broken anyway, right?

  • dean_1230 // March 7, 2008 at 2:23 pm

    The line in your write-up that caught my attention was the following:

    “But it came out horribly wrong! But something is going on — because the “standard” choice (centered PCA) gave us the wrong result while non-centered PCA gave the right answer!”

    In the case you show, you know that there is a “right answer” and also what the “right answer” is. But assume that you don’t know (as is the case with research, where you may have an idea but aren’t sure and want the data to confirm it). How do you tell that one method is giving the right answer and another method is giving the wrong answer?

    In other words, how do you determine that Uncentered is a better choice than centered when you have no real idea what the “right” answer is?

    You also mentioned that the MM method gives a hockey stick in PC4. Would that show that the hockey stick is a much lower level trend and not nearly as significant as some of the noise that the data has?

    [Response: As stated in an earlier response, PCA doesn't really care about the physical meaning of significant variations. Transforming statistical significance to physical meaning is the job of the regression fit, which is done *after* the PCA. And the regression uses multiple leading PCs, so that's where they get to "battle it out" over which one is really related to the physical variable under consideration (temperature).

    That's one of the reasons that the verification step is crucial. We can *always* get some kind of fit (significant or not) to whatever set of proxies we include. Verification tells us whether or not it's plausible that the relationship is meaningful.]

  • MrPete // March 7, 2008 at 3:43 pm

    Transforming statistical significance to physical meaning is the job of the regression fit

    This is a fallacy. Mathematical analysis cannot produce physical meaning.

    Finding two curves that look the same, or even are the same, is not even suggestive that they mean the same. The meaning must come from outside.

    I sure hope I’m not saying anything surprising here.

    (A fun illustration of the problem is found in Made To Stick. The Curse Of Knowledge is illustrated by the Tappers and Listeners test. Pick a well-known song. Find a friend, tap it out with your finger on a table. How often do you think they’ll be able to guess what song you’re tapping? Most people guess 50%. Actually, only a few percent succeed. Why? The meaning that is so obvious to the Tapper is not inherent in the data.)

    [Response: I'm guilty of a very poor choice of words. But I think most readers got my meaning, which is, that PCA alone doesn't reveal any relationship between signals in the data and the physical process we're trying to model. If there is one, then the regression fit will reveal it -- but even then one must abide by the ever-present caveat that correlation is not causation. That's why the verification step is so important. And even that doesn't constitute proof, just plausibility.]

  • MrPete // March 7, 2008 at 4:01 pm

    You’re quite confident that if we remove the bristlecone pines, the hockey stick falls apart (and indeed that’s a totally separate issue from PCA). But according to what I’ve seen, MM got *that* part wrong too!

    The best current exposition I’ve seen of this proposition is Loehle’s latest, which includes corrections in response to the feedback he got. He explicitly leaves all tree rings out of the picture, just to be conservative about the matter. All of the data is available, so not too hard for interested parties to do their own analysis.

    Loehle’s data is not as pretty as tree-ring-based data, because tree rings are one of the few proxies that can provide accurate dating and annual data values. But stepping back from the minutiae, doesn’t an unbiased observer have to sit up and take note when leaving out one class of data changes the hockey stick so significantly? Here is his reconstruction, including CI bounds.

    [Response: Loehle's reconstruction is a (rather bad) joke. Readers should examine this.]

  • steven mosher // March 7, 2008 at 4:31 pm

    Tamino, you didnt read the post.

    The post illustrated the point you made. It did so
    well before you posted this. So you are kinda late to this debate.

    The issue is not whether PCA can effectively mine data. The issue is can it reliably mine data.
    and what confidence can you put on that mining

    Have a look at all the tests.

    What does the mann method produce when you
    have an inverse hockey stick in your noise?

    What does the method produce when your “noise” really DOES have a signal?

    Stipulated. if you feed manns method a Real signal and noise, it will pull a signal out. DUH.
    Now feed it other food. watch out for bones in the throat

    That’s not a robust test. Feed it a

    [Response: I suspect your comment somehow got truncated.

    In any case, you and McIntyre are really clutching at straws; the desperation to discredit the hockey stick is almost hilarious. It reminds me of the con artist in Huckelberry Finn, who refuses to admit the falseness of his claims even under the most extraordinary evidence.

    Whether you use non-centered PCA, or centered PCA, or *no PCA at all*, you get a hockey stick. Unless of course you commit other errors with the effect of suppressing it.]

  • steven mosher // March 7, 2008 at 4:56 pm

    Tamino,

    You seem like a fair guy to me. You have an opinion. That’s unavoidable. It’s not a capital crime. We all have them. At times you express your opinion in ways that inflame others. Other times not. I like that. Lighting a fire under people’ s butt moves them to action. The outcome is the outcome.

    Read the post. Address the issues.

    #1. the data mining issue.
    #2. The Missed signal issue
    #3. The performance against noise signals
    that are ‘upside down’

    M&M never questioned the ability of non center ed PCA to data mine signal out of noise.

    That is not the question. The question is this.

    HOW do we verify that the SIGNAL MINED
    is , in fact, a signal?

    The method will mine a signal. prove it’s gold
    and not iron pyrite

  • fred // March 7, 2008 at 4:58 pm

    So are you saying that it makes no material difference which subset of the data you take the mean of? One subset is as good as another?

  • MrPete // March 7, 2008 at 5:05 pm

    Tamino, you’re just appealing to authority by linking to the RC posting. Even the valid RC complaints only apply to the original paper without corrections. Do your own work. Loehle’s work is no joke.

    I for one am not desperate to discredit the hockey stick. I’m desperate to find good data and good analysis.

    My frustration is that when I stand in front of a Bristlecone Pine (Almagre is visible in the distant mountains outside my window right now)… it is painfully obvious that stripbark data is not a temp proxy. Yet people persist in acting as if it were so. That is the rather bad joke.

    You can cover it up with fancy analysis. You can take potshots at the details. But Loehle did a very simple thing: he removed just bad data from the proxy pile, and the entire picture changed. Nobody has challenged that, including RC.

    You want to try, go ahead. Because it sure appears that Loehle, and others, have falsified the hockey stick premise.

    Leave out the known-bad small fraction of the data, and you don’t get The Stick.

    Try it, Tamino. Falsify Loehle. It should be simple, right? You’ve made the claim several times that the HS will show up no matter what, unless you “commit other errors.”

    All “we” are asking you to do is leave the tree rings out. Do your analysis. If it’s that easy to falsify Loehle, you’ll have a nice feather in your cap.

    [Response: Perhaps some time (maybe even soon) I'll post about Loehle. But it's important to realize that while I take (and sometimes fulfill) requests, I don't do challenges or demands.

    In fact I think it's a very common (and very effective) strategy of denialists simply to keep throwing stuff -- whether it has a point or not -- at climate science. It keeps a lot of us busy doing less-than-useful stuff, and enables the opposition to "set the pace" for the discussion. If some day I *do* falsify Loehle, it doubt it'll be a "feather in my cap." It'll just be an invitation for denialists to throw the *next* piece.]

  • Christopher // March 7, 2008 at 5:07 pm

    Any chance you could post some code to this? I’m still working thru the first 3 PCA posts and simply want to do what you did step by step. For some reason I’ve always had a hard time with PCAs. Any code (R, Matlab, pseudo-code even) would be very helpful, for me anyway, to have this finally sink in. Also, some caveats as the when to use PCA. That might sound broad but one of my laments as a past graduate student having to take a fair amount of stats coursework is that you are given canned examples with the right tool already picked. I always wanted a more practical angle where you have a problem and first need to figure out which tool in the toolbox is best. So any such rules of thumb, cardinal assumptions about your data, and the like… that you could offer based on your experience would be very helpful.

    Another comment: I’ve always found it odd that the MBH debate figures so prominently (maybe this is my perception). In terms of debunking or supporting AGW I’ve always thought it was meaningless. I’m more interested in the ice core data and how current trends fit in (they don’t).

  • George // March 7, 2008 at 5:10 pm

    Bulldog says:

    It reminds me of the con artist in Huckelberry Finn, who refuses to admit the falseness of his claims even under the most extraordinary evidence.

    Perhaps it should be renamed the “Hucky-stick” debate.

    [Response: Thanks for a good chuckle.]

  • J // March 7, 2008 at 5:26 pm

    fred writes:

    So are you saying that it makes no material difference which subset of the data you take the mean of? One subset is as good as another?

    If you’re going to be using the PCA to estimate some thing like, say, temperature, then you want to use a subset for a time period when you have known temperature data to use as calibration. Thus, the mean is calculated for the 20th century, when temperature data are already known. It wouldn’t be useful to calculate a mean for, say, the 17th century, because we don’t have calibration data for that period.

  • dhogaza // March 7, 2008 at 5:35 pm

    Towards the beginning of this thread, I posted …

    Why not just delete those comments that aren’t relevant to your post, i.e. attempts to divert the discussion to “strip-bark samples”, etc?

    And sure enough …

    What Steve demonstrated, and many others have confirmed (most recently Craig Loehle) is that the hockey stick is incredibly dependent on a small portion of the data set. More than anything else, in the proxy series used to create the infamous hockey stick graph, it is dependent on the presence of stripbark BCP data from a tiny region of the world.

    And the CA crowd are off to the races.

    I think McIntyre and the brighter inhabitants of CA have figured out long ago that M&M’s “shattering” of the hockey stick via statistical analysis has failed, despite Wegman’s supporting testimony. I imagine this is why there’s so much effort to undermine the legitimacy of the proxy data.

    But it’s a bit humorous to watch the performance here. HB writes a fine series on PCA and rather than say, “OK, McIntyre was wrong about that”, what we see is an attempt to shift the discussion to another topic altogether …

    Now, something specific …

    Tamino, you’re just appealing to authority by linking to the RC posting. Even the valid RC complaints only apply to the original paper without corrections.

    The corrections ignored most of the valid RC complaints, therefore those complaints apply equally well to the very partially corrected paper.

  • dhogaza // March 7, 2008 at 5:40 pm

    My frustration is that when I stand in front of a Bristlecone Pine (Almagre is visible in the distant mountains outside my window right now)… it is painfully obvious that stripbark data is not a temp proxy.

    *how* is it “painfully obvious”? One thing science teaches us is that things that seem intuitively obvious are often just wrong.

  • John Cross // March 7, 2008 at 7:02 pm

    steven mosher: you wouldn’t be visiting “Tammy town” since it ” is a fun place to explore rhetorical probing missions.”

    It seems like it.

    Regards,
    John

  • Lazar // March 7, 2008 at 7:05 pm

    MrPete,

    More than anything else, in the proxy series used to create the infamous hockey stick graph, it is dependent on the presence of stripbark BCP data from a tiny region of the world. The rest of the proxies are so weak as to have little impact on the results.

    In that case, when excluding bristlecone pine series and not using PCA at all, there should not be a ‘hockey-stick’ result. Then can you explain Wahl & Amman 06, Figure 2, green line?

    PS, after excluding bristlecone pine series, Wahl & Amman compute much inferior (but marginally significant) verification scores over the 15th century, suggesting that there is a scarcity of proxy data extending back to 1400, but also that BCP series are NH temperature proxies.

  • Hank Roberts // March 7, 2008 at 7:34 pm

    “rhetorical probing missions”

    Is that line from one of the troll listservs? It sounds so familiar.
    http://www.hyphenologist.co.uk/killfile/anti_troll_faq.htm

    The organized ‘missions’ disrupting conversations have long been part of life on the Net.

    Note the IP numbers used for the record. Save them. Some day web hosts will catch up with the Usenet folks in the anti-spam and anti-troll techniques, and they’ll be useful.

  • David B. Benson // March 7, 2008 at 7:40 pm

    Tamino — This is, once again, excellent!

    I currently understand the need for determining which PCAs to use prior to exploring the data, yes? But I have no conception of how to go about deciding which PCAs to use.

    Enlightment is kindly requested.

    [Response: The procedure used by MBH is this: study the spectrum of eigenvalues (the variance attached to each PC). Compare that to what would be expected if the signal were noise (with the same autocorrelation structure as the data). Those PCs whose eigenvalues are significantly higher than expected from noise, are included in the regression.]

  • cce // March 7, 2008 at 7:56 pm

    Isn’t one of the main reasons for including the BCPs (strip bark or otherwise) is that they contain an ENSO signal? Isn’t that why they strengthen the verification scores?

  • Lazar // March 7, 2008 at 8:07 pm

    Loehle… no areal weighting, no idea as to how well the series represent local or global temperatures, no verification stats, only eight series beyond 1935, out of a total of eighteen. It remains a joke.

    The corrections ignored most of the valid RC complaints, therefore those complaints apply equally well to the very partially corrected paper.

    Indeed.

  • BoulderSolar // March 7, 2008 at 8:36 pm

    After reading this post and McI post about PCA I see there is some talking past each other in a technical sense. The assumption made in MBH is that the “signal” (ie temperature) extracted in a PCA analysis MUST match the temperature in the calibration period. This means that the PC selected is one which has the best correlation to the calibration data. For MBH noncentered procedure it is PC1 and PC2. For a centered procedure it is not PC1.

    MM shows that by doing this, a real signal in the proxy data gets lost if your criteria is for best correlation in the calibration period. This can happen especially because of the very few data points in the calibration period for the proxies.

    I can see valid points for both approaches. What makes me lean toward MM’s viewpoint is that they showed how totally random proxies would always produce the hockey stick. Tamino actually confirms this when he insists that the only valid PC to use in a centered analysis is the one with the hockey stick.

    [Response: That's not what I said at all. I stated that objective criteria must be applied to selecting PCs, and the *same* criteria must be applied when using centered as non-centered PCA. Nor did I use only the "hockey stick" PC when doing the centered analysis on the artifical data. I used both the first 2 PCs in a multiple regression, and it turned out that the regression itself indicates that the 1st is no real indicator of temperature. The reason the correlation graph shows only the 2nd (hockey stick) PC is that I wanted to graph the correlation, which for 2 predictors requires a 3-D graph -- and those are far less clear than 2-D graphs (this is, after all, a blog post for illustrative purposes).

    And by the way, the mistake about non-centered PCA being invalid (which according to some reader comments, McIntyre now disavows) isn't the only mistake in the MM analysis. It's *really* not a good idea to take McIntyre's analysis, or blog posts, at face value.]

  • Lazar // March 7, 2008 at 8:43 pm

    Steven Mosher,

    Read the post. Address the issues.

    I believe that HB already has…

    #1. the data mining issue.

    which seems a non-issue, to quote HB; “a non-standard centering convention will indeed emphasize the variation of the mean, which turns out to be the main difference between the 20th century and the rest of the time span. What he fails to realize is that that’s the point. He’s also right that the changes associated with it will become more prominent in the PCA analysis, causing those changes to “move up” the PCA list. Again, that’s the point.” — HB

    #2. The Missed signal issue

    Eh?… here McIntyre has decided a priori, that is without reference to anything physical or to any aim of any experiment, (i.e. entirely arbitrarily), what he calls the (artificial) ’signal’ and what he calls the (artificial) noise, and then claims, falsely, that the signal is ‘missed’ by an MBH methodology to which the data has no relevance or meaning. Of course the ’signal’ is in a higher order PC, and an actual experiment would consider whether or not to include the higher order PC, but since the data has no relevance to any actual experiment, the point is moot and entirely tangential to anything MBH have done.

    #3. The performance against noise signals that are ‘upside down’

    M&M never questioned the ability of non center ed PCA to data mine signal out of noise.

    That is not the question. The question is this.

    HOW do we verify that the SIGNAL MINED
    is , in fact, a signal?

    HB again; “PCA most certainly cannot “create” a statistically significant relationship between that variation and the observed temperature data. That the relationship is significant emerges from both the regression itself, and the testing done on the verification data”

  • RomanM // March 7, 2008 at 8:44 pm

    You wouldn’t care to share your data with the rest of us so that we might try some experiments of our own with it, would you? It might be interesting to see what it looks like.

    Apart from the fact that your post is based on a sample of size one, you neglected to address the other side of the coin - does this non-standard methodology also create hockey sticks when they are not present in the data?

    [Response: Sigh... It doesn't -- certainly none that will pass verification. But I didn't address the issue of bristlecone pines, or tree ring data in general, or how well the instrumental record serves to calibrate proxies, or any number of others. This post is about the criticism that non-centered PCA invalidates the MBH analysis. It doesn't.

    I also get the impression that certain folks would like to take *artificial* data, created only to illustrate a point, for a blog post no less, and subject it to an "audit." No thanks -- I've got way better things to do.]

  • Lazar // March 7, 2008 at 9:08 pm

    cce;

    Isn’t one of the main reasons for including the BCPs (strip bark or otherwise) is that they contain an ENSO signal? Isn’t that why they strengthen the verification scores?

    Wahl & Amman suggest so;

    MM directly note the link between
    bristlecone/foxtail pines and precipitation (p. 85, MM05b), which is exactly the kind of largescale pattern registration that the MBH CFR method takes as axiomatic because large portions of this region are known to have important ENSO/precipitation teleconnections (cf. Cole and Cook, 1998; Rajagopalan et al., 2000). Since ENSO has a strong role in modulating global temperatures as well as affecting regional precipitation patterns, a CFR method of temperature reconstruction can effectively exploit regional ENSO/precipitation teleconnections that register in proxy data.

    RomanM;

    you neglected to address the other side of the coin - does this non-standard methodology also create hockey sticks when they are not present in the data?

    Eh? Sigh… HB has just shown, over a series of four extensive posts, that PCA does not “create” anything that is “not present in the data”.

  • MrPete // March 7, 2008 at 9:11 pm

    dhogaza, *how* is it “painfully obvious”? One thing science teaches us is that things that seem intuitively obvious are often just wrong.

    Exactly. I don’t know if this is an east-west thing, but it seems so. Scientists sitting on the eastern seaboard of the USA, or perhaps even those who live in the hot desert of Arizona, may conjecture that tree growth is temp limited — because that’s how it works where they live. Sadly, their intuition is failing them in other places.

    On the eastern seaboard, there’s generally plenty of precipitation, and even more there’s plenty of humidity. (Gotta love those 100-100 summer days :) ) You can look at a USDA plant hardiness map and see nice bands that correlate well with minimum temperature going right up the east coast. In Pennsylvania, as Tamino pointed out earlier, temperature is pretty consistent over wide areas. Same as in upstate NY where I spent a lot of growing-up years.

    Now let’s go to the high mountains of Colorado and Southeast California. First obvious thing: Here in Colorado, it is dry. Not quite desert-dry, but incredibly dry. In a good year, there’s some moisture to help trees grow well. In a bad year, there is almost none. How snow collects, how sun melts it (or not), and how the snowmelt flows makes a huge difference. On Almagre, BCP’s are found in protected spaces where snowmelt water exists.

    It’s also windy here. In other places, 40-60mph wind with gusts to 80 might be considered a small hurricane. Here? That’s a nice storm. We batten down the hatches and hope the homes under construction don’t blow away. I’ve had a wind gust break the deadbolt lock on our front door. With wind like that, slopes and hills make a huge difference in microclimate. Our home garden is placed specifically to avoid the wind. Makes all the difference in plant growth. Same thing on Almagre. BCP’s are in places at least somewhat protected from the worst wind. (And if not — then a storm is just as likely to destroy the tree as a nearby tree falls.)

    Third, there are a variety of other important factors when you’re at altitude. The available soil is not deep. Nutrients are hard to come by. Thus geology is a major factor — anything that causes available nutrients to vary over time. A good gullywasher storm can significantly change the available nutrients for many many trees.

    Finally, and most important: look at the trees. Whole bark trees grow reasonably uniformly. Strip bark trees grow irregularly. One look and it is obvious: strip bark trees are trying to recover from the damage they’ve sustained. (Dig in on that and you’ll find plenty of science — including astounding things we’re learning about plant hormones and how roots and shoots “talk” to ensure there’s an appropriate balance of nutrients, etc.)

    All the things I’ve mentioned are huge factors. They’re so obvious to plant growth experts, like gardeners, that when my wife made a presentation to the Colorado Master Gardeners** about BCP tree ring studies, the room filled with laughter at the suggestion that temp was the major signal here. And that was a room filled with pro-AGW people. They couldn’t believe their ears.

    I’m not suggesting that temp is completely irrelevant here in the mountains, but it’s proven to be less significant than other factors by plant biologists here, and it is less significant as a practical matter to those who do high altitude gardening.

    Perhaps this helps the reader understand why I’m a big advocate of multidisciplinary science. The challenges we face require the insight and understanding of folks from many areas of expertise. Climatology is one important specialty, but so is statistics, dendrobiology, geology and more.

    Tamino’s posting is a great intro to the math. But as he’s pointed out, the math does not do provide a physical interpretation of the data.

    [Just between me, you and the fencepost, I have a hunch. You can score me on this in a hundred years or so :)… my gut sense is that many stripbark measurements will tend to show a “recent” growth spurt, simply because the tree is trying to survive. If it fails, it’s dead and we don’t measure it. (Once seriously stripped, the bark never heals completely.)

    BTW, I’m not trying to draw attention away from Tamino’s very good exposition on PCA math. Gotta get the math right. We also must get other parts right. Some things have a bigger impact than others. And of course the most important by far is to know what you’re looking at. We can yell about numbers all day long but if we don’t even know what the numbers mean, their value is unimportant.

    ** PS Master Gardeners are volunteers who disseminate research-based advice, carefully limiting their statements to scientifically tested material published by the state university systems across the nation. A great use of tax dollars to promote good science!

  • Lazar // March 7, 2008 at 9:17 pm

    HB;

    I stated that objective criteria must be applied to selecting PCs, and the *same* criteria must be applied when using centered as non-centered PCA.

    I would say that if excluding a PC
    a) greatly alters the shape of the reconstruction, and b) reduces scores over a verification period, then it should not be excluded.
    Would those be ‘objective’ criteria?

  • BoulderSolar // March 7, 2008 at 9:31 pm

    Tamino,

    The verification procedure used in your and MBH’s PCA is the correlation during the 20th century temperature. This is what I refer to as the hockey stick. This is also one of your “objective criteria”. The point that I think MM seems to make is that by doing so the best PC will not produce the actual temperature for prior years. They illustrate this by using totally nontemperature dependent data sets which still produce good verification (i e hockey stick).

    As a test of this what if your test data had a temperature record which had large scale variations higher than during the verification period and that the proxy data had the limited amount of data points during the verification period that MBH had. Would we see the good correlation to actual temperature for prior years?

    I appreciate your time and effort to explain this. However your snipe about not taking anything McI posts at face value is a bit ironic coming from one who hides behind an alias

  • RomanM // March 7, 2008 at 9:33 pm

    I agree that bristlecones, calibration, etc. are important considerations to MBH, but peripheral to what you are doing here. There is also a serious problem due to the fact that proxies are time series whose correlation structure has a serious impact on the correlation or covariance matrix used to extract the PCs. However, I maintain that it is not at all clear what impact using uncentered series may have on creating hockey sticks and this is central to your demonstration.

    It is unfortunate that you seem to have so little confidence in the correctness of your analysis that it prevents you from allowing someone else to look at it. There are simply too many imprecise statements in your post that it raises questions about exactly what it was that you did:

    “I created an artificial temperature time series which follows a distinct “hockey stick” pattern, and also generated 40 separate artificial proxy data time series, all spanning the time interval from 1400 to 1980.” … “The proxy data series were generated by computing a response to the temperature signal and other factors as well. And all the series include random noise.” … “Then I normalized each series so that they’re all about the same ’size’.”

    These statements could mean just about anything. How correlated (both timewise and between each other) were your proxies? How strong was the “signal” compared to other variation. Hown variable was the time signal outside the calibration time period? Were you doing correlation or covariance PCs - how did the “normalizing” affect those results? What were the relative sizes of the eigenvalues? You are trying to convince us that this method is “correct” based on this one constructed example so answers to these questions are pretty important. I had thought that the data might provide some of the answers.

    Lazar:

    I must have missed some of the posts which contained the “proofs” that you refer to. They aren’t in the textbook that I am currently using.

    [Response: Permit me not to believe you. Here's what I think you're aiming at. If I put the data online, you'll find fault whether it's valid or not. If I make the computer code available online, you'll find fault whether it's valid or not. If I then demonstrate that your supposed fault is faulty, you'll either disbelieve the proof or find another fault. Etc., etc., ad infinitum. You'll never stop.

    That's *exactly* what McIntyre has done to the MBH results. Despite every one of his criticisms being shown to be faulty, he either maintains that it's not so, or moves on to another one -- all so he can keep attention focused on the idea that the hockey stick is wrong, rather than the simple fact that the globe is getting warmer due to human activity. It's a very effective application of the old adage, "the best defense is a good offense." But I'm not gonna play your game; I really do have way better ways to spend my time. One would hope that you do too.

    What's next? Will you try to force WordPress to disallow any posts that don't have their data archived for universal web access? Am I next in line after Al Gore to be taken to court in a lawsuit?]

  • MrPete // March 7, 2008 at 9:40 pm

    One more brief interlude from the math, then I’ll quit (gotta do my bookkeeping :-) )

    Something perhaps helpful on precipitation vs temp… which speaks to things like ENSO teleconnection etc as well. Some good studies have been done to examine tree growth at an incredibly fine scale — to see at what time of year the “annual growth” occurs, etc. What they found is that all the significant tree ring growth takes place in the spring (at snowmelt time.) If conditions are good for growth then, you get good growth. If not, you don’t.
    The growth is essentially nonexistent and also independent of climate variations that take place during the rest of the year (other than the fact that major storms, deep freeze, fire, etc can cause great damage and put the tree into “recovery” mode…)
    Sorry, I don’t have the reference handy. Perhaps someone else can supply. Truly a fascinating study!

    Back to your regularly scheduled PCA math lesson :)

  • Lazar // March 7, 2008 at 9:41 pm

    BoulderSolar;

    The verification procedure used in your and MBH’s PCA is the correlation during the 20th century temperature. This is what I refer to as the hockey stick. This is also one of your “objective criteria”. The point that I think MM seems to make is that by doing so the best PC will not produce the actual temperature for prior years.

    No, the data is ‘trained’ over the period 1902-1980, but the verification period is 1854-1901. To pass, the reconstruction scores need to be significant over both periods.

  • Spence_UK // March 7, 2008 at 9:43 pm

    Ermmm… no.

    The MBH98 PCA approach mines for hockey stick shaped data. What this means is that:

    1. Historical temperature is hockey stick shaped - MBH98 method will produce a hockey stick shape

    2. Historical temperature is NOT hockey stick shaped - MBH98 method will produce a hockey stick shape, IF just one “rogue” hockey stick proxy unrelated to temperature is used.

    All you seem to have done is demonstrated is (1), which we already knew. Unfortunately you have failed to touch on the real issue, which is (2).

    In statistical language, MBH98 has no power to determine whether history was hockey stick shaped or not, because it is predisposed to producing hockey stick shaped output, even if there is just one rogue hockey stick proxy. Von Storch demonstrated this with German unemployment and McIntyre demonstrated it with tech stocks.

    Another way of putting it: the hockey stick shape is built into the MBH98 assumptions. Likewise here, by assuming there is a hockey stick shape up front, you have also put your conclusions into your assumptions.

    McIntyre understood this; Wegman understood this; Von Storch understood this; the GRL reviewers understood this. Evidently still not everyone does.

    That said, if you think you’ve got a point, write it up and submit to GRL. Here’s a tip: it won’t get published, because it misses the point. That’s why Steve’s work got published, and yours won’t.

    [Response: Here's a tip for you: faulty results (like MM) get published all the time, even in GRL. And far more often in "Energy & Environment." Von Storch at least had the honesty to *admit* his mistake.

    As for illustrating the faulty nature of MM's work, that too made it to the peer-reviewed literature: Wahl & Amman, Climatic Change, DOI 10.1007/s10584-006-9105-7, and Amman & Wahl, Climatic Change, DOI 10.1007/s10584-007-9276-x, to name just a few.]

  • dhogaza // March 7, 2008 at 9:44 pm

    HB said, quite clearly

    one would use part of the known data, then create the prediction, then check prediction against observation in the remaining part. This is “verificiation,” an independent check on whether or not the method is working. We can’t do this if verification uses the same data we used to calibrate — that would only show that if we fit our proxies to the calibration data

    Yet BoulderSolar persists in believing that

    The verification procedure used in your and MBH’s PCA is the correlation during the 20th century temperature.

    No, that’s the period used for calibration, not verification.

    HB didn’t do the verification work in his post, indeed stated explicitly that he’d skip that step in his example, for simplification.

  • dhogaza // March 7, 2008 at 9:47 pm

    However your snipe about not taking anything McI posts at face value is a bit ironic coming from one who hides behind an alias

    The use of one’s real name doesn’t change the usefulness of their arguments one bit. Nor does the use of a pseudonym. That’s an ad hominem attack on your part.

    Have you ever read The Federalist Papers?

  • cce // March 7, 2008 at 9:52 pm

    Forgive me if this has already been tried, but if the BCPs contain a signal for ENSO, PDO, or whatever, isn’t that easy to test? We have the new Ababneh chronology that the Auditors keep talking about. We have various indexes, (this one going back to 1850 and beyond, http://jisao.washington.edu/datasets/globalsstenso/). Don’t we have everything we need?

  • Lazar // March 7, 2008 at 10:01 pm

    RomanM;

    I must have missed some of the posts which contained the “proofs” that you refer to.

    Then I would suggest you read the first sentence in this blog entry.

  • Spence_UK // March 7, 2008 at 10:09 pm

    Tamino -

    Faulty work gets published in peer review all the time - agreed, but that applies equally to MBH98 and Amman and Wahl. Note that got rejected from GRL too, just like your post here would. Seems like E&E and Climatic Change are two peas in a pod.

    Anyway, a challenge to you. In your response to RomanM on the same point I made:

    “Apart from the fact that your post is based on a sample of size one, you neglected to address the other side of the coin - does this non-standard methodology also create hockey sticks when they are not present in the data?”

    you replied:

    “[Response: Sigh… It doesn’t — certainly none that will pass verification. ”

    OK, so if the hockey stick is “artificial” and not in the original data, the verification period will have problems. Now, you’ve tested the quality of the match with those pretty scatter plots above (very informative, thanks for those).

    How about plotting from MBH98 - just the final data set for the 1400AD step, so you don’t have to do all the work, the data is publically available - a scatter plot for the calibration period, and a scatter plot for the verification period. All fair, using the techniques you’ve applied above. And we can see for ourselves, using your own methods, how well the MBH98 verification performs for the 1400AD step.

    If you don’t want to do it, I’ll happily do it for you and link it here in the comments. Just let me know.

  • Otto Kakashka // March 7, 2008 at 10:13 pm

    MrPete,

    perhaps you should take a look at Rossi et al., 2007: Evidence of threshold temperatures for xylogenesis in conifers at high altitudes.

    http://www.springerlink.com/content/978017037815120w/

    First line of abstract: “Temperature is the most important factor affecting growth at high altitudes.”

  • null{} // March 7, 2008 at 10:20 pm

    tamino/HB, a most excellent direct response to the technical issues mentioned by RomanM // March 7, 2008 at 9:33 pm.

  • dhogaza // March 7, 2008 at 10:22 pm

    The MBH98 PCA approach mines for hockey stick shaped data. What this means is that:

    2. Historical temperature is NOT hockey stick shaped

    Even if your first statement were true, which it’s not, your second statement does not follow.

    And it flies in the face of the fact that other analysis done by others, which doesn’t use PCA at all, reveals …

    a hockey stick.

    Your argument boils down to “it’s not a hockey stick because I don’t believe it’s a hockey stick”.

  • BoulderSolar // March 7, 2008 at 10:25 pm

    Like the replies! I’m learning. So after doing a PCA we pick the PC(s) which have the best correlation to the verification period. In this case the verification period is just prior to the calibration period. The question that is paramount is that by doing this do we get the actual temperature for prior periods? Why does using the NASDAC index still produce a result which passes verification?

    [Response: No! We don't "pick the PC(s) which have the best correlation to the verification period." We pick the PCs which pass the selection criteria -- all of them. Then we regress temperature against *all* those PCs (multiple regression) during the calibration period. It turns out that those which don't correlate with temperature get very low coefficients in the expansion, and so end up having very little impact on the reconstruction (which is as it should be); those that do correlate with temperature get larger coefficients and *do* end up having a significant impact on the reconstruction (which is as it should be).

    Only *then* do we check the reconstruction against observed temperature during the verification period. That's "verification." It seems to be the one step that critics consistently omit.

    The level of illogic, and falsehoods about what I've said or intended to say or meant, has become downright disturbing.]

  • MrPete // March 7, 2008 at 10:39 pm

    Tamino, you said about Steve M’s assertions: Despite every one of his criticisms being shown to be faulty…
    I’m sorry but that’s a bit much, unless you are saying Wegman was full of it. If so, we’ve got quite the scientific tussle going here, don’t we?! As a peanut gallery observer, this is sounding like more he said / she said argument.

    Hard part is that us non-experts have no way to evaluate the assertions.

    Looks to me like Steve and Tamino need to sit down and have a face to face chat. You’re talking past one another. As real people, I’m confident much would be better understood if you both found a way to talk it over.

    Speaking of which, Lazar, I’m sorry but I can’t help you with your question. I don’t have access to the papers nor diagrams you refer to. I can answer field questions and a bit more, but will bow out from the math food fights. I’m not a player in that game.

  • MrPete // March 7, 2008 at 10:55 pm

    Tamino, something you just said confused rather than enlighted. Probably my own stupidity :)

    [PC's] that do correlate with temperature get larger coefficients and *do* end up having a significant impact on the reconstruction…
    Only *then* do we check the reconstruction against observed temperature during the verification period. That’s “verification.”

    So all this is to say:
    * We use PCA to pull out the strongest “signal” curves, i.e. the curves with largest non-noise wiggles, so to speak.
    * We regress against an (arbitrary, hopefully) calibration period (C) to find the best match.
    * We then test (validate) against a different period (V), to discover if the signal fits both calibration (C) and verification (V) periods.

    Sounds to me like the argument over “mining for desired signal” is really a question of which of the following is going to emerge. Either

    a) There’s a “signal” that matches both C and V. We then assume it is temperature.
    b) There’s a “signal” that matches C but not V. Hypothesis falsified.
    c) No signal matches C. Hypothesis falsified.

    The problem seems to be: how probable is it that a C+V match is actually temperature?

    One side argues “highly probable; if it were not temp it wouldn’t match.”

    Other side argues “not so probable. In fact, we can plug in almost any kind of random or arbitrary ’stick-ish’ data and get the same result. The method just pulls out hockey sticks.”

    Leaving aside the acrimony. my question is: how DOES one calculate the probability or CI that the signal is actually temp? How does such a calculation take into account the results found by plugging in other essentially random sticklike data that produces statistically similar results? On the surface, it would seem the method is not actually telling us much.

    IIRC, someone created a stick-generator that used the MBH method plus random noise to generate hockey sticks. If so, the fact that the method produces results that pass C+V seems less than exciting.

    Where am I confused?

    [Response: Generally, "stick generators" don't pass verification. There's also a bit of a logical inconsistency in the phrase "essentially random sticklike data."

    Then of course there's the fact that even if a result is ridiculously improbable -- say 1 in 10,000 (which is plenty to claim statistical significance), if you try to find it 10,000 times you probably will. Such an effort is called a "fishing expedition."

    And of course there are other pesky facts ... like if you use centered PCA you get a hockey stick. If you don't use PCA at all, you get a hockey stick.

    There's no absolute guarantee, no Godlike assurance from on high, that the signal which mimics temperature in the calibration interval, and reproduces it correctly during the verification interval, is actually caused by temperature. There's *always* a chance (possibly a ridiculously tiny chance) that the result it due to accident.]

  • dhogaza // March 7, 2008 at 10:58 pm

    I’m sorry but that’s a bit much, unless you are saying Wegman was full of it.

    Well, yes, that’s essentially what HB said, didn’t you read the post carefully?

    In his post, HB said…

    First let’s dispense with the last claim, that non-centered PCA isn’t right. This point was hammered by Wegman, who was recently quoted in reader comments thus

    followed by the quote (which you can read above).

    HB then goes on to say

    Just plain wrong. Centering is the usual custom, but other choices are still valid; we can perfectly well define PCs based on variation from any “origin” rather than from the average. It fact it has distinct advantages IF the origin has particular relevance to the issue at hand. You shouldn’t just take my word for it, but you *should* take the word of Ian Jolliffe, one of the world’s foremost experts on PCA, author of a seminal book on the subject.

  • Lazar // March 7, 2008 at 11:05 pm

    In statistical language, MBH98 has no power to determine whether history was hockey stick shaped or not, because it is predisposed to producing hockey stick shaped output, even if there is just one rogue hockey stick proxy. Von Storch demonstrated this with German unemployment and McIntyre demonstrated it with tech stocks.

    Am I reading you correctly? Are you implying that, supposing the real temperature history is not ‘hockey stick’ shaped, i.e. it has ‘warm’ 15th century values, and you have 94 proxy series which correlate with that assumption, and use one ‘rogue’ series of tech stock figures to represent a ‘flat’ 15th century and 20th century upturn, as a 95th proxy, and you feed all that through the MBH98 method, decentered PCA, regression, and verification, that you will a) get a reconstruction with a ‘flat’ 15th century, that b) gets a significant score over the calibration period, and c) also over the verification period?
    If not, then what are you saying?
    Thanks in advance.

  • Lazar // March 7, 2008 at 11:09 pm

    MrPete,

    Speaking of which, Lazar, I’m sorry but I can’t help you with your question. I don’t have access to the papers nor diagrams you refer to.

    No problem, but the Wahl & Amman paper is available online, and might be worth reading…

  • Mike D // March 7, 2008 at 11:09 pm

    You can use any of the trees you want as long as they match the temp some where at some time.
    Such as trees in No. Am. that match temp in Europe. Who cares it is only Climatoligy

  • Boris // March 7, 2008 at 11:14 pm

    The issue of Bristlecone pines is interesting, but yet another red herring offered up by hole punchers.

    1. BCP are a temperature proxy.
    2. The NAS recommended that BCP (strip bark) not be used in temp reconstructions because it appears to be affected by CO2 fertilization.
    3. MBH are aware of this issue and account for it in their analysis.

    I haven’t investigated whether or not the BCP are the key proxy, but I strongly believe this is BS because McIntyre and company have repeatedly misled people on what the NAS report on surface temp. reconstructions actually said.

  • BoulderSolar // March 7, 2008 at 11:23 pm

    Tamino,

    Thankyou for your patience here. I am an EE with no climate and limited statistics background. Can you enumerate the “selection criteria” for the PCs?

    Again the crucial test is whether this type of PCA analysis actually produces the real temperature prior to the verification period. Since your data set did not have any significant variation prior to the “hockey stick” what would happen if there was a robust variation in temperature during that time? Would we see that with the same PCA analysis?

    [Response: The procedure used by MBH is this: study the spectrum of eigenvalues (the variance attached to each PC). Compare that to what would be expected if the signal were noise (with the same autocorrelation structure as the data). Those PCs whose eigenvalues are significantly higher than expected from noise, are included in the regression. The expected eigenvalue spectrum (and confidence intervals) for a given autocorrelation structure can be estimated by Monte Carlo simulations (a fanciful term for a large number of computer simulations).

    Whether or not a reconstruction reproduced a robust variation in past temperature, depends on whether or not the *proxies* show the response to it. One assumes that they would (in fancy terms, that the relationship between temperature and proxies is "stationary").]

  • JeanS // March 7, 2008 at 11:34 pm

    There is a lot of rubbish is this post! Too sad, you had a couple nice post about PCA, and now you write this. For anyone who does not have technical skills to undeestand this issue, I strongly suggest that you complete ignore this post. Or take it to your stats professors, they’ll explain you.

    Here are a few points that really caught my eye:

    1) Centering is the usual custom, but other choices are still valid; we can perfectly well define PCs based on variation from any “origin” rather than from the average.

    BS. It does not matter how many times you or some other people repeat this lie, it won’t make it true anyhow. Citing Jolliffe does not help: nowhere in his presentation nor in the book he advocates centering on partial average. The reason is simple: by not centering, you loose all your theoretical properties (such as those you nicely developed in the previous posts). In other words, you loose meaning of you transformation. Other “conventions” just lead to ad-hoc, arbritary (orthogonal) transformations.

    [Response: I must have really hit the bulls-eye with this post, because now I can *smell* the desperation.

    No matter how often, brashly, or rudely you repeat the assertion that "you loose [sic] meaning,” it won’t make it true. Your own words are unambiguous: you assert that non-centering itself is not valid (there’s no other interpretation of “by not centering, you loose [sic] all your theoretical properties…” etc.). But Jolliffe flatly contradicts you (that’s what his presentation is about), so you brush that off with the pathetic statement that he doesn’t specifically mention using a partial average.

    Jolliffe’s entire presentation is about the fact that centering is not an essential aspect of PCA. But because he doesn’t specifically mention choosing a partial average, you feel free to ignore his point. That of course enables you to repeat the crap about non-centered PCA being invalid. Now *that* is rubbish, and particularly stinky rubbish to boot.

    I suspect that you *know* your amateurish claim is bullshit, but you’re *counting* on readers not having the expertise to catch your lie.]

    2) Wegman’s right about this much: a non-standard centering convention will indeed emphasize the variation of the mean, which turns out to be the main difference between the 20th century and the rest of the time span. What he fails to realize is that that’s the point. He’s also right that the changes associated with it will become more prominent in the PCA analysis, causing those changes to “move up” the PCA list. Again, that’s the point.

    What a spin-doctor you are! Why would you want to emphasize series whose 20th century average deviates much from the overall average? This is exactly what Mann’s “non-centered PCA” is doing: it rewards series whose average on the chosen calibration period differs from the overall average. Do you have some a priori knowledge to justify that?

    [Response: It turns out to emphasize exactly the series that correlate with temperature. Imagine that.]

    3) You example is extremely misleading, to say the least.

    PCA is not capable of separating different signals in general. So if you have, say k factors and n-dimensional observation space and you project your data to k dimensions (with normal PCA), you do get rid of most of noise, but the k projected factors are essentially an arbitrary orthogonal transformation of the originals plus some remaining noise. That is, after PCA you can not expect you signals be separated unless you have, say, one extremely strong component. You need other methods such as the Independent Component Analysis.

    But that’s not the point in MBH, if properly done. What you want is to reduce your data (tree ring indecies) to those determing k factors. The separation (of temperature, moisture etc. factors) is expected to happen later. Again, this is achieved by the centered PCA, but not by the “non-centered convention”. Now in your example you use all the factors to generate your pseudoproxies. This is not the case for the question under study: those proxy sets contain a few series (e.g. bristleconde pines) that do not represent the “overall general variation in data set” (i.e., are not factors determining most series). Normal PCA handles that nicely by putting that “variation” to a low numbered PC, which gets disregarded as noise. On the other hand, “non-centered” Mannian “PCA” tuned to pick up the 2oth century mean vs. overall mean difference places that noise incorrectly to high ranked PC, and gets passed to the future stages of the algorithm.

    [Response: Bullshit. It's the abandonment of valid PC selection procedures that enabled MM to discard exactly the variation that corresponds to the hockey stick. Unfortunately, that particular variation *should* have been included according to objective selection criteria. As a result it's no surprise that the MM result fails verification.]

    So if you have any intellectual honesty left, you could try the following experiment:

    - generate 70 (eg white noise) proxies with approximately the same overall mean, and then artificially lower the 20th century of one of the proxies (an outlier series). Run centered and Mannian PCAs on that data set.

    [Response: Try this experiment: do the analysis of the actual data with *centered* PCA, and without repeating the other mistakes of MM. Wait, that's already been done. Result: hockey stick. Do the analysis *without PCA at all*. Wait, that's already been done too. Result: hockey stick. Try selecting random subsets of the proxies. Oh my, that's been done too. Result: hockey stick.

    You prove by example that there are people who will go to *any* length to discredit the hockey stick. That pretty well defines a lack of intellectual honesty.]

  • John Cross // March 8, 2008 at 12:00 am

    Hank Roberts: I kid you not, the phrase (including “rhetorical probing missions” ) is a direct quote from a post Steve Mosher made over at CA in regards to this site!

    Hansen’s Bulldog: Man did you ever make a good call when you said: “In the meantime, I have one request: before you raise other issues about the hockey stick, address this one.” Of course it doesn’t stop them from doing it!

    Regards,
    John

  • luminous beauty // March 8, 2008 at 12:03 am

    The mechanical correlation between plant growth and annual temperature variation can be and has been empirically determined to be physically caused. It is not spurious.

    One can prove it to one’s own satisfaction with an environmentally controlled grow room. Or just take up gardening for a number of years.

    None of these proxies were selected just because they correlate strongly to the calibration interval, but because from multiple lines of corroborating evidence, painstakingly accumulated over decades, researchers have developed strong physical reasons to expect they really are proxies for temperature.

  • kim // March 8, 2008 at 12:15 am

    This is complete rubbish.

    H/t JeanS
    =======

    [Response: WOW!!!. How interesting. I have to wonder why you give a "H/t" to JeanS, and repeat his assertion of "rubbish," even before his comment has appeared -- 'cause just like this post, it's in the moderation cue at this very moment. I smell a conspiracy; are the CA people are so stung by this post that they're organizing a mob to assault my blog?

    Not gonna happen.]

  • MrPete // March 8, 2008 at 12:30 am

    Lazar, thanks for the pointer. Now, with respect to your question: can you explain Wahl & Amman 06, Figure 2, green line?

    Looks to me like we’re unable to even comment on it. The green line doesn’t show up in the “hockey stick” section at all, so it’s a bit hard to see what’s going on.

    I’ve learned enough from watching these arguments to know that it is not as simple as reading the “surface” of a paper like this and deciding whether the claims made are correct. The devil’s in the nit-picky details. For example, apparently WA isn’t using the same data — correlation 0.7 with MBH data.

    AFAIK, the only serious comment made on this WA paper at CA can be found in the comment (not main post) section here. A hint, if you’re new to browsing CA: in that thread, “Jean S”, “UC” and Steve M are serious stats people. Others are mostly lurkers.

    I’ll be curious to see what else is said in the days to come.

    [Response: I've updated to post to show WA figure 2.]

  • Spence_UK // March 8, 2008 at 12:43 am

    Lazar,

    No, that’s not what I’m saying. You’ve inserted assumptions which are not part of my argument, and indeed not even part of the MBH98 assumptions. For example, your statement “correlate with that assumption” is just peculiar. I’m not sure how you go about correlating a data series with an assumption. If you mean do the series correlate with the global mean temperature, then no, that isn’t an assumption that even goes into MBH98. In fact, the proxies are not even required to correlate with local gridcell temperatures (and good job too, because most of them don’t). Remember the signal to noise is low, and the residuals are highly autocorrelated, because they have confounding factors (that’s why they are called “proxies”). If there was a simple correlation, we wouldn’t have to worry about all of these complex procedures to try and tease temperature out. I’ve probably just misunderstood your point here, so feel free to restate it in clearer terms.

    Secondly, I assume you are aware that there are two PCA steps in MBH98, one of which is uncentred and one which is centred. If you want to expand this discussion to the whole suite, you have missed that step. What’s the rationale for using different forms of PCA? If the uncentred method is so great, why use a different method elsewhere? If there are no clear justifications as to why one should be used in one location and the other elsewhere, then it leaves a degree of freedom within the study to fine tune the results, which in turn lowers the effective statistical significance of the results (not dissimilar to the form described by Burger and Cubasch in their 2005 paper).

    Your point (c) is obscure. Why would tech stocks pass verification tests? As Tamino notes, this would not be expected. Indeed, MBH98 itself fails multiple verification tests - it doesn’t even pass RE when properly benchmarked (as per McIntyre’s reply to Huybers, which also addresses Wahl and Amman’s claim and is the reason WA were rejected from GRL)

    Anyhow, it looks like Steve McIntyre is, at some point, likely to post a response to this which will likely argue the points better than I will here, so I would recommend you read that when it becomes available. He should put the case more clearly and more succinctly than I do.

  • Lazar // March 8, 2008 at 12:45 am

    Boris,

    1. BCP are a temperature proxy.
    2. The NAS recommended that BCP (strip bark) not be used in temp reconstructions because it appears to be affected by CO2 fertilization.
    3. MBH are aware of this issue and account for it in their analysis.

    Good points. Again, Wahl & Amman show a 20th century upturn without BCP series, and here is the upturn again, produced without including any dendro series whatsoever.

  • Lazar // March 8, 2008 at 1:13 am

    I’m still struggling to get to terms with what Steven Mosher;

    The issue is not whether PCA can effectively mine data. The issue is can it reliably mine data. and what confidence can you put on that mining

    [...]

    Stipulated. if you feed manns method a Real signal and noise, it will pull a signal out. DUH.
    Now feed it other food. watch out for bones in the throat

    [...]

    M&M never questioned the ability of non center ed PCA to data mine signal out of noise.

    That is not the question. The question is this.

    HOW do we verify that the SIGNAL MINED
    is , in fact, a signal?

    The method will mine a signal. prove it’s gold

    and Spence_UK;

    The MBH98 PCA approach mines for hockey stick shaped data. What this means is that:

    1. Historical temperature is hockey stick shaped - MBH98 method will produce a hockey stick shape

    2. Historical temperature is NOT hockey stick shaped - MBH98 method will produce a hockey stick shape, IF just one “rogue” hockey stick proxy unrelated to temperature is used.

    … are claiming.

    That decentered PCA emphasizes, and increases the chance of selection, of series that diverge from the 20th century calibration period mean?
    Yes.
    That those series might not be temperature proxies?
    Yes.
    But they might just as well be?
    Yes.
    That, the logical counterpoint, decenterd PCA de-emphasizes series which do not deviate from the 20th century calibration period mean?
    Yes.
    That those series might be temperature proxies?
    Yes.
    But they might also not?
    Yes.

    So, in other words, PCA just selects patterns, but doesn’t care either way with whether those patterns either correlate to, or in fact represent, anything physical such as temperature.
    Which HB has pointed out.
    Isn’t that why MBH98 do linear regression and validation statistics against atemperature data? Do your criticisms in have anything at all to do with PCA?

    So, I’ll ask again, in response to Spence_UK;

    In statistical language, MBH98 has no power to determine whether history was hockey stick shaped or not, because it is predisposed to producing hockey stick shaped output, even if there is just one rogue hockey stick proxy. Von Storch demonstrated this with German unemployment and McIntyre demonstrated it with tech stocks.

    Am I reading you correctly? Are you implying that, supposing the real temperature history is not ‘hockey stick’ shaped, i.e. that it has instead ‘warm’ 15th century values, and you have 94 proxy series which correlate with that assumption, and use one ‘rogue’ ‘hockey-stick’ series of tech stock figures to represent a ‘flat’ 15th century and 20th century upturn, as a 95th proxy, and you feed all that through the MBH98 method, decentered PCA, regression, and verification, that you will a) get a reconstruction with a ‘flat’ 15th century, that b) gets a significant score over the calibration period, and c) also over the verification period?
    If not, then what are you saying?
    Thanks in advance.

  • MrPete // March 8, 2008 at 1:26 am

    LB, The mechanical correlation between plant growth and annual temperature variation can be and has been empirically determined to be physically caused.

    That’s quite a general statement. And yes it’s true in the general case. One could substitute a variety of other metrics for “temperature” and still have a valid statement.

    The challenge is to determine whether it is true for a particular species in a particular environment. There can be any of a number of limiting factor(s) to growth.

  • MrPete // March 8, 2008 at 1:56 am

    Tamino, no worries about conspiracies or time travel :) — Jean S’s “rubbish” quote was simply from his CA comment. What a world we live in when people can kinda-sorta track conversations all over the planet in real time!

    I’m glad to see some experts engaging with one another. It’s a “vigorous discussion” :-) but hopefully something good will emerge from it all.

    You’re *all* reasonable people with reasonable perspectives. Obviously can’t all be correct about every point made here… so some things will ultimately be shown incorrect. That’s ok — science thrives that way.

    [Response: You might be right, but I still smell a rat. I suspect I'll be deluged with critical comments from regulars at CA who hate this post almost as much as they hate Mike Mann, Jim Hansen, and the hockey stick. The result will be endless back-and-forth which will ultimately serve to confuse rather than enlighten readers.

    What they do in their house is their business. This is my house.]

  • dhogaza // March 8, 2008 at 2:07 am

    Well, it’s going to be interesting, given this quote by McIntyre

    Some of the contortions that people make on behalf of the Stick are quite amazing. I’ll post on this in due course.

    (he’s speaking of HB’s post)

    It will be interesting to see if he attempts a coherent attack on HB’s statistics or if he armwaves like his supporters here are doing.

    It would also be a bit more interesting if he were to post here where the readership isn’t quite so worshipful as it is at CA.

  • Lazar // March 8, 2008 at 2:20 am

    Bear in mind, HB, before taking Jean S too seriously, that he has previously…

    a) claimed that removing the ‘hockey stick’ PC ‘preserves the temperature signal in the proxy data’.
    b) Criticized MBH98 regarding potential for “overfitting”, whilst ignoring, or forgetting, the validation period. Isn’t reference to a ‘validation period’ the standard way by which ‘overfitting’ is understood/taught? Perhaps Jean S can explain, he claims to teach stats.
    c) signed onto this nonsense criticizing the employment of RE in MBH98, see, if you place a small ‘random’ wiggle (11 points) right on top of a small section of data (11 points) far away from the mean of a 113 point calibration period, you may find that the small wiggle matches the small section of data better than the calibration mean. You ignore the lack of an RE score over the calibration period, as the ‘random’ data doesn’t exist for it, and you ignore that the circumstances under which MBH98 get high RE scores include a 78 pojnt calibration period and 58 point validation period.

  • Lazar // March 8, 2008 at 2:30 am

    Spence_UK,

    assumption = supposing the real temperature history is not ‘hockey stick’ shaped
    correlate with that assumption = proxy series correlate with a real temperature history that is not ‘hockey stick’ shaped

    If this still is not clear, please reiterate.
    Thanks.

  • Spence_UK // March 8, 2008 at 3:01 am

    Lazar,

    Thanks, but this:

    correlate with that assumption = proxy series correlate with a real temperature history that is not ‘hockey stick’ shaped

    is not an assumption in MBH98, and indeed is not evident in the data set, for the reasons explained above. Correlations between proxies and both global and local temperatures are often insignificant, particularly for tree rings; if they were significant, we wouldn’t need to be doing this complex procedure to tease the temperature signal out.

    Having thought about it, we are opening a whole can of worms here that is likely to drag this thread way off-topic. I’ll explain my reasoning.

    Tamino has raised a discussion here on the narrow point of the PCA decentring issue. If you want to investigate that in isolation, that is one thing. If you want to address the whole MBH98 study, you have to fully understand the entire algorithm and assumptions that go into it, AND you have to take into account the interplay between the PCA decentring and several other issues that Steve McIntyre raised. You can’t disaggregate the PCA effect and look at the whole algorithm - the interplay between the problems are important. Such a discussion would just explode, in fact I might go so far as to suggest you could write an entire blog on the topic ;)

    For this reason, I will focus on the narrow topic of PCA rather than the wider issue of MBH98: your characterisation of PCA (”emphasising” or “de-emphasising” signals) isn’t really a good one to help understand the issue here - it really rotates the data matrix with the goal of reducing the dimensionality by aligning the common signals along the principle axes. What you want to avoid is aligning an outlier signal on one of those principle axes and inflating its “variance” (which isn’t really even a good measure variance in the decentred case) - which is exactly what decentred PCA can end up doing, as illustrated by McIntyre and Wegman. Promoting outliers as significant common signals in this case is an undesirable property for such a statistical tool to have, which is why the short-segment centring PCA of this type is (as far as I know) never used by statisticians.

  • Lazar // March 8, 2008 at 3:07 am

    Jean S;

    This is not the case for the question under study: those proxy sets contain a few series (e.g. bristleconde pines) that do not represent the “overall general variation in data set” (i.e., are not factors determining most series). Normal PCA handles that nicely by putting that “variation” to a low numbered PC, which gets disregarded as noise. On the other hand, “non-centered” Mannian “PCA” tuned to pick up the 2oth century mean vs. overall mean difference places that noise incorrectly to high ranked PC, and gets passed to the future stages of the algorithm.

    And how do you presume to know that the PC is noise?
    Because it represents 8% of variance under centred PCA?
    Why does 8% demarcate noise, is it some kinda magic number?
    What if the signal, i.e. that which relates to temperature, is a small component of variance?
    How do you tell?
    Oh, that’s right, you do regression and test with stats.
    And when we remove the ‘hockey stick’ PC the scores drop to zero or negative over the calibration and validation intervals.
    And if we procede without using PCA so that nasty ‘hockey stick’ doesn’t dominate the other series beyond it’s natural (actually, arbitrary) bounds, we still get a hockey stick. And good scores.
    As HB has pointed out.
    Repeatedly.
    In the post you describe as rubbish.

    So if you have any intellectual honesty left, you could try the following experiment:

    - generate 70 (eg white noise) proxies with approximately the same overall mean, and then artificially lower the 20th century of one of the proxies (an outlier series). Run centered and Mannian PCAs on that data set.

    If you “have any intellectual honesty left”, you’ll try to describe what the point is, that you’re, presumably, trying to make…

  • George // March 8, 2008 at 3:30 am

    If the hockey stick shape is indeed an artifact of PCA, as some claim, then why do I see it when I look at this?

    Apparently I am not completely alone, since at least one other person (Eli) sees it too.

    Then again, perhaps it is a characteristic common to all humans. Perhaps we have actually evolved as a species to just look at data and automatically do de-centered PCA.

    Possible, but I’d have to say not likely. What evolutionary advantage would it give (other than perhaps to hockey players)

    I understand the point of illustrating the issue to those not familiar with PCA (and can appreciate that some have their very identity riding on the “debunking” of the hockey stick), but if the hockey stick shape is independent of whether one uses PCA, isn’t it sort of a waste of time to debate the issue ad nauseam?

  • Lazar // March 8, 2008 at 3:33 am

    MrPete,

    Looks to me like we’re unable to even comment on it. The green line doesn’t show up in the “hockey stick” section at all, so it’s a bit hard to see what’s going on.

    ‘Hockey stick’ refers both to an upturn in 20th century temps and relatively flat temps extending from the 15th to 19th centuries (actually it’s only the flatness of the 15th century which is at dispute).
    The reason you can’t see the green line in the 20th century is because it’s right on top (or underneath) of the instrumental temperature record and the decentered PCA reconstruction.

    The green line is the reconstruction using no PCA at all, and no bristlecone pine series.

    I’ve learned enough from watching these arguments to know that it is not as simple as reading the “surface” of a paper like this and deciding whether the claims made are correct. The devil’s in the nit-picky details. For example, apparently WA isn’t using the same data — correlation 0.7 with MBH data.

    Probably the relevant quote from WA06 is;

    Our emulation of the MBH98 results is shown in Figure 1. The Northern Hemisphere mean surface temperature reconstruction (WA) is nearly identical to the original MBH98 reconstruction (Fig. 1, red and grey lines). The slight differences are related to our methodological simplifications of using a consistent annual time step throughout the
    Feb 24, 06 Wahl and Ammann Climatic Change, in press 26 reconstruction process and equal weighting of the proxies.

  • MrPete // March 8, 2008 at 3:59 am

    Tamino said: this is my house.

    Of course. And the brief “rubbish” quote that alarmed you was written without noting where it came from… so no surprise at all that you were upset. [How's anyone to know who/where/how people are communicating beyond what you can see?! Craziness.]

    Lazar said: Probably the relevant quote from WA06 is…

    Could be. Except the “0.7 correlation” is with respect to the data before any analysis, if I’m understanding correctly what Steve M said in the CA thread linked above. So no reconstruction or weighting involved. Supposedly the same source data, obtained from Mann.

    What a mess. In my most numeric work — demographic analysis — when things got this contentious we’d slow down, expand our data until we could see exactly what was same/different, and then move forward. It helps if one has cooperative people all around who want to get the various methods and data sources in sync. In this case, that’s not a valued goal (yet).

    Well, maybe someday. At least the various parties are interacting now. I’m an optimist that this will work out over time. :-)

    ‘night all. Combine this with some bookkeeping nightmares and my head hurts :-)

  • Lazar // March 8, 2008 at 4:01 am

    Spence_UK,

    For this reason, I will focus on the narrow topic of PCA rather than the wider issue of MBH98

    Ok, in which case am I correct in assuming that focus applies below; that you are restricting your claims to the use of (decentered) PCA?

    In statistical language, MBH98 has no power to determine whether history was hockey stick shaped or not, because it is predisposed to producing hockey stick shaped output, even if there is just one rogue hockey stick proxy. Von Storch demonstrated this with German unemployment and McIntyre demonstrated it with tech stocks.

    In which case,

    In statistical language, MBH98 has no power to determine whether history was hockey stick shaped or not

    Agreed.

    because it is predisposed to producing hockey stick shaped output

    No, not because decentred PCA is predisposed to producing a certain type of pattern, but because PCA “doesn’t care either way with whether those patterns [elicited] either correlate to, or in fact represent, anything physical such as temperature”, regardless of the centering mechanism. Which is why regression and statistical tests and selection of suitable proxies etc.

    Again, I must ask you, when you write;

    In statistical language, MBH98 has no power to determine whether history was hockey stick shaped or not, because it is predisposed to producing hockey stick shaped output, even if there is just one rogue hockey stick proxy. Von Storch demonstrated this with German unemployment and McIntyre demonstrated it with tech stocks.

    … could you explain what are the point(s) you are trying to make?

    You can’t disaggregate the PCA effect and look at the whole algorithm - the interplay between the problems are important. Such a discussion would just explode,

    Unfortunately I think that was doomed from the start, unless HB starts heavily censoring. Primarily because the various issues are so difficult if not impossible, to meaningfully, as TCO puts it, disaggregate. E.g. one can’t easily speak of the relevance of decentered PCA without describing the effects on the reconstruction, the aims of MBH98 etc.

  • Lazar // March 8, 2008 at 4:25 am

    Spence_UK,

    Your point (c) is obscure. Why would tech stocks pass verification tests? As Tamino notes, this would not be expected.

    So why raise the issue of tech stocks at all? MBH98 is the reconstruction and the verification stats. No (or different) verification stats, no result as exists in MBH98.

    Correlations between proxies and both global and local temperatures are often insignificant, particularly for tree rings; if they were significant, we wouldn’t need to be doing this complex procedure to tease the temperature signal out.

    … doesn’t the movement of the ‘hockey stick’ from PC4 to PC1, and the reduction (to abject failure) in verification stats when excluding the ‘hockey stick’ PC, suggest that the decentered method is rather effective at teasing the temperature signal out?

  • bouldersolar // March 8, 2008 at 4:56 am

    What would happen if the verification and calibration periods were switched? Should we expect the reconstruction to be the same?

    Can anyone enlighten me on how many data points each proxy had during the calibration and verification periods?

    Emotions running high but I do still see nuggets of info that is helpful.

  • Christopher // March 8, 2008 at 5:18 am

    “I also get the impression that certain folks would like to take *artificial* data, created only to illustrate a point, for a blog post no less, and subject it to an “audit.” No thanks — I’ve got way better things to do.”

    I feel this might have been directed at me. I have no intention of auditing a single thing, nor the hubris to assume that would even be valuable. My goal is to understand the whole PCA bit and your example seems like a useful place to start as I have some background in biometeorology and see great value, for me personally, to figure out PCAs, and I’m interested in the whole thing. Like I said before, this whole debate and diatribe is so irrelevant wrt AGW. I’m not sure why people get so upset about it. It’s like AGW requires MBH98, which is just boggling.

  • Hank Roberts // March 8, 2008 at 5:39 am

    Good pointer, that, to the AR4:

    “McIntyre and McKitrick (2005a,b) raised further concerns about the details of the Mann et al. (1998) method, … using Principal Components Analysis. The latter may have some theoretical foundation, but Wahl and Amman (2006) also show that the impact on the amplitude of the final reconstruction is very small (~0.05°C; for further discussion of these issues see also Huybers, 2005; McIntyre and McKitrick, 2005c,d; von Storch and Zorita, 2005).”

    M’n'M get credited appropriately, they pointed out a method issue that makes a quantifiable difference (in the North American number). Five percent of a degree C isn’t insignificant. Well, actually …. maybe it is.
    Did anyone check the significance?

  • MarkR // March 8, 2008 at 5:53 am

    This has all been done to death before. Read what Wegman (”a professional statistician for some 38 years. I have served as editor of the Journal of the American Statistical Association and served as coordinating editor, associate editor, member of the editorial board and a
    number of other editorial roles for many journals during this time period. I am
    currently on the Board of Directors of the American Statistical Association as the
    publications representative and will become the Chair of their Publications Committee as of 1 January, 2007.”) had to say in front of the US Congress:

    “Without attempting to describe the technical detail, the bottom line is that, in the MBH original, the hockey stick emerged in PC1 from the bristlecone/foxtail pines. If one centers the data properly the hockey stick does not emerge until PC4. Thus, a substantial change in strategy is required in the MBH reconstruction in order to achieve the hockey stick, a strategy which was specifically eschewed in MBH. In Wahl and Ammann’s own words, the centering does significantly affect the results.”

    http://www.climateaudit.org/?p=2322

  • fred // March 8, 2008 at 6:02 am

    Lazar Are you implying that, supposing the real temperature history is not ‘hockey stick’ shaped….and you feed all that through the MBH98 method, decentered PCA, regression, and verification, that you will a) get a reconstruction with a ‘flat’ 15th century, that b) gets a significant score over the calibration period, and c) also over the verification period?

    That’s what I think, rightly or wrongly, both McIntyre and Wegman are saying.

    Spence says “short-segment centring PCA of this type is (as far as I know) never used by statisticians.” It was my own impression too. I would really like a textbook reference to the contrary showing in detail the recommended method of doing it.

    It would also help if we could ban the expression ‘intellectual honesty’ from this debate - which should be about something perfectly objective, the use of statistical methods. Helps not in the slightest.

  • Armagh Geddon // March 8, 2008 at 9:02 am

    Tamino, I would just like to congratulate you on your calm, dispassionate, professional and objective approach to this issue. Well done.

  • James Lane // March 8, 2008 at 9:03 am

    I’ve been using PCA in social science applications for over 20 years.

    As a general point, I would say that applied PCA is not a black-box procedure but requires a lot of iteration and inspection of the data, especially the identification possible outliers.

    When you run PCA, the first thing you do is ID the series that load heavily on each component. If I looked at my PC1 and determined that it consisted mainly of high altitude BCPs from California, I’d be very concerned that I have an outlier. I certainly wouldn’t think “that’s the temperature signal!”

    OTOH, If I looked at my PC4 and determined that it consisted mainly of high altitude BCPs from California, I’d be less concerned, but more interested in assigning meaning to the higher order components. If you’re going to interpret PC4 as the temperature signal, what’s the signal in the other PCs?

    Anyway, you’d go and have a good look at the raw data for these possible outliers, and you’d run PCA again with and without them, to see the effect on the “face-validity” of the solutions.

    Then you have to deide how many PCs to retain for the regression stage. Tamino may have given the impression that this is all mechanical “nothing to see here” but in fact it’s an inexact science. There are at least a dozen “rules” for component retention. Take your pick.

    After the centering issue was raised, Mann invoked Preisendorfer’s Rule N to allow retention of PC4 (and hence the BCPs) in the centered scenario. In fairness to Mann, he did use Preisendorfer on his temp PCA (different part of the method) although it’s not discussed in the context of the proxy network.

    (BTW, it would be fascinating to know what the actual eigenvalues for the PCs under the centered and decentered options for MBHx).

    But PC retention is very important, as the regression stage doesn’t “care” about the order of the PCs, the percentage of variance explained or the interpretation of the component. Again, in practice you’d run the regression with 2, 3, 4 & 5 PCs and see how the results vary.

    That’s how it’s done in the real world.

    Finally, it seems to me that the centered/ decentered debate (while interesting) is essentially a side-show. It’s all about getting the BCPs into your reconstruction. Of course you can do that without PCA. In fact, many of the non-PCA reconstructions include Mann’s PC1!

  • Mike N. // March 8, 2008 at 11:34 am

    hey John Cross, you’re a cool guy, just don’t sweat the technique on a brotha like steven mosher, c’mon. He’s funny; plus he gets into downright dirty Detail in his analyses.

  • mikep // March 8, 2008 at 12:36 pm

    This discussion is losing sight of the simple issues. The MBH reconstructions was supposed to be of the Northern Hemisphere temperature. There are too many data series, it was claimed, to do a sensible regression of temperature against all the potential proxies, which are supposedly highly correlated with each other anyway. One standard solution is to use
    PCA as a purely mathematical transform of the original series to give components which desribe the dominant pattern of variation in the data and reduce the number of variables to put on the LHS of the regression. These components may or may not have a physical interpretation. Mannian PCA (which no one who just read the original article would have known he was using, incidentally) instead efficiently looks for those components in the data with a deviation from the mean at the end. It answers a different question from standard PCA. And it efficiently picks up hockey sticks. This has never been in dispute. What this means in practice is that the Mannian PC1 picks out a very small number of series, notably the bristlecone pines, which correlate well with temperature in the 20th century and gives them a very heavy weighting. What mannian PCs don’t do is represent the dominant pattern of variation in the sum total of the original proxy data. In other words, for practical purposes MBH could have thrown away most of their data and just gone to the regression step using the bristlecones and a few other similar series. And yes, of course if you systematically mine for data with the “right” shape you will get decent verification stats.

    But the claim to be reconstructing the Northern hemisphere temperature rests on using bristlecones as a kind of “Standard Candle” for the Northern Hemisphere temperature. If we had good reasons independently for thinking they did act as standard candles well and good. But let’s bear in mind.
    There is no physical theory or independent data that says bristlecone pines accurately ( and linearly) track temperature.
    The bristlecone ring widths do not correlate with local temperatures. Indeed the original collectors thought the 20th century growth spurt was caused by carbon fertilisation.
    Most importantly the best test of all, seeing if bristlecones track late 20th century and early 21st century temperatures, is failed badly. This is the so-called divergence problem.
    What all this suggests to me is that MBH is a essentially a classic example of the well known “spurious regression” problem (NB this is not simple name-calling but a well-defined phenomenon first discussed by Yule in teh 1920s and, following on the work of Novel prize-winning econometrician Clive Granger now standard fare in most modern econometric textbooks i.e not something particularly esoteric).

  • Lazar // March 8, 2008 at 1:04 pm

    James Lane,

    Anyway, you’d go and have a good look at the raw data for these possible outliers, and you’d run PCA again with and without them, to see the effect on the “face-validity” of the solutions.

    Then you have to deide how many PCs to retain for the regression stage. Tamino may have given the impression that this is all mechanical “nothing to see here” but in fact it’s an inexact science. There are at least a dozen “rules” for component retention. Take your pick.

    I have a lot more sympathy for that approach than the approach described by Wegman;

    Wahl and Ammann reject this criticism of MM based on the fact that if one adds enough principal components back into the proxy, one obtains the hockey stick shape again. This is precisely the point of contention. It is a point we made in our testimony and that Wahl and Ammann make as well. A cardinal rule of statistical inference is that the method of analysis must be decided before looking at the data. The rules and strategy of analysis cannot be changed in order to obtain the desired result.

    He’s saying you would have to guess beforehand (a fraught process) which, and how many, PCs to include. If your guess is wrong, if you include irrelevant PCs, or worse, if you exclude the signal you’re interested in, you would have to pack up tools and go home. After spending years collecing data. According to his ‘rules’, the correct decision process is the worse one. It doesn’t work in the real world. The worse error in logic is that, he ignores “the rules and strategy of analysis” were changed when M&M altered the centering mechanism.

    Finally, it seems to me that the centered/ decentered debate (while interesting) is essentially a side-show.

    Then HB is correct, decentered PCA is not per se wrong.

    It’s all about getting the BCPs into your reconstruction. Of course you can do that without PCA.

    As Wahl & Amman show, the hockey stick shape back to 1400 is not dependent on the presence of bristlecone pine series if you do the analysis without PCA, but the verification stats most definitely are. Those to me are strong grounds for including bristlecone pine series.

    Anyway, thanks for your input.

  • Lazar // March 8, 2008 at 1:25 pm

    mikep,

    And yes, of course if you systematically mine for data with the “right” shape you will get decent verification stats.

    a) The verification stats are not dependent on ‘data mining’ for the ‘right’ (hockey stick) shape, but on the scarcity of data.

    b) Neither is the hockey stick shape dependent on ‘data mining’.

    Eg…

    If you do not use PCA, and therefore do not mine for the ‘right’ shape, the hockey stick shape (flat) over 1400-1450 (and upturn over the 20th century) remains, and the verification stats unchanged.
    If you then exclude bristlecone pine series, the hockey stick shape still does not change.
    But the verification stats do change over the 1400AD step.
    When M&M obtained their spurious 15th century warmth, and failed verification stats, they removed a lot more than bristlecone pine series.

    Regards

  • luminous beauty // March 8, 2008 at 1:31 pm

    MrPete,

    Yes temperature sensitivity in plants is dependent on environment. A tree in a certain environment might be more or less sensitive to confounding factors.

    Your assignment as a budding dendroclimatologist is to determine where to find environments in which confounding factors are minimalized.

    Think you can do it? How many tree cores from how many locations do you think it will take?

  • Barton Paul Levenson // March 8, 2008 at 1:38 pm

    BoulderSolar writes:

    [[However your snipe about not taking anything McI posts at face value is a bit ironic coming from one who hides behind an alias]]

    How many times are we going to see this same stupid charge repeated? HB/Tamino is “hiding behind an alias, hiding behind an alais, hiding behind an alias.” Nya nya na nya nya. Grow up, for Christ’s sake.

  • Hansen's Bulldog // March 8, 2008 at 1:40 pm

    You know that prank where you take a paper bag, fill it with manure, set it on somebody’s porch, light it on fire, and ring the doorbell? The plan is to get the homeowner to open the door and stomp on the bag trying to put out the fire, so he’ll end up spreading crap all over his porch, his shoes, and whatever else might be nearby. This morning I found another burning bag of crap on my doorstep. I’m not gonna stomp on it. I’m not gonna bring it into the house either.

  • Lazar // March 8, 2008 at 2:00 pm

    Stephen Mosher writes at CA;

    Tammy town is a fun place to explore rhetorical probing missions. When Tammy said he was doing PCA I figured he would get to the decentered issue. I even praised him for educational efforts. Now, we shall see how he extricates himself. Should be good theater. Popcorn is on me.

    Well Steven, I’m a little underwhelmed so far. Some rather confused claims expressed by yourself, the Steve McIntyre post you link, and some others here, seem to boil down to…

    1) PCA is the factor which isolates temperature signal from proxy data.

    Wrong. In MBH98 it is PCA + regression against temperature data + statistical tests on the model, and PCA is not necessary.

    2) If you apply decentered PCA to tech stock series of a ‘hockey stick’ shape, that the method might (except eigenvalues aren’t mentioned) select series that bear no relation to temperature, and you conclude therefore the MBH98 decentered method, and from 1), therefore MBH98 itself, is wrong, wrong, wrong.

    Nope. Tech stock series can be selected by centered PCA if you include enough series, or indeed if you do no PCA at all. I’m not entirely sure, but this may be why MBH98 don’t include tech stock series in their data, and why they b) apply regression against temperature data, and c) test the results of that regression against temperature data. PCA identifies and weighs patterns based on variance, not a relation to a specific physical quantity. The amount of variance may or may not be related to the amount of signal contained, of any physical quantity that we desire to measure. The decentered method in MBH98 is an informed guess which turned out to be correct.

    3) Dear old Jean S concludes that a PC with 8% variance must be noise. Wrong for the previous reasons. Also note, a rough guide to a likely safe noise threshold is 100%/number of series, which, over the 1400AD step, 100%/22 < 5%.

    Pass the popcorn.

  • dhogaza // March 8, 2008 at 2:45 pm

    hey John Cross, you’re a cool guy, just don’t sweat the technique on a brotha like steven mosher, c’mon. He’s funny

    Yeah, he’s funny, alright. MBH98 is a fraud equivalent to Piltdown Man. Yeah, I’m ROTLMAO over his wit.

  • fred // March 8, 2008 at 2:45 pm

    Tamino, any comment on this?

    http://www.uoguelph.ca/~rmckitri/research/PCnotes.pdf

    very different angle on it.

    [Response: I'll have to study it before I can comment. The first thing I notice is that it appears to be by McIntyre and/or McKitrick, so it's no surprise there's a different angle.]

  • luminous beauty // March 8, 2008 at 2:55 pm

    “The bristlecone ring widths do not correlate with local temperatures. Indeed the original collectors thought the 20th century growth spurt was caused by carbon fertilisation.”

    Yes. When carbon fertilization is corrected for, high correlation with local temperatures is confirmed.

    So much for the diversion problem.

  • Lazar // March 8, 2008 at 2:59 pm

    Fred,

    That’s what I think, rightly or wrongly, both McIntyre and Wegman are saying.

    Spence_UK now says that is not what he is claiming, and I’ve come to believe it is also not what Steve McIntyre and some others are claiming.

    If not, then I want the claim clearly enunciated and signed on the dotted line. Then proven.

    Spence says “short-segment centring PCA of this type is (as far as I know) never used by statisticians.” It was my own impression too. I would really like a textbook reference to the contrary showing in detail the recommended method of doing it.

    No, Fred, nooo! HB’s work allows you to understand what PCA does to the data, what decentering does to PCA, and how those mesh with the aims of MBH98. I won’t accept you falling back on an appeal to authority to defend M&M’s criticisms. Make an effort to understand. Please.

  • Hank Roberts // March 8, 2008 at 3:10 pm

    There’s one climatologist, as far as I know, participating at CA, that’s Dr. Curry.

    Who wrote on the dot.earth blog recently, replying to Andy Revkin’s invitation for argument there:

    “… I am astonished to see such tilting at windmills ….
    … For the record, I view the IPCC 4th Assessment Report to be the best available statement of the state of climate science at the time it was written. Policy makers do not have a better document or analysis from which to work with in grappling with the myriad of issues associated with climate change.

    … we need to do more and better science, and more extensive assessments. We are wasting time attacking each other’s credentials and motives. Andy Revkin is right in desiring to switch the focus to policy, management and technology solutions to these complex issues.

    — Posted by Judith Curry

    http://dotearth.blogs.nytimes.com/2008/01/24/earth-scientists-express-rising-concern-over-warming/#comment-10491
    … we need to do more and better science, and more extensive assessments. We are wasting time attacking each other’s credentials and motives. Andy Revkin is right in desiring to switch the focus to policy, management and technology solutions to these complex issues.”

    — Posted by Judith Curry

    http://dotearth.blogs.nytimes.com/2008/01/24/earth-scientists-express-rising-concern-over-warming/#comment-10491

  • Hank Roberts // March 8, 2008 at 3:21 pm

    Last “paste” in my previous hiccuped, once is enough

  • George // March 8, 2008 at 3:38 pm

    The goal posts seem to be moving …even as Bulldog writes.

    First, McIntyre et al claimed that it was decentered-PCA that “created” the hockey stick shape….

    Then, when it was shown that this was not the case — indeed that you can do the analysis without even using PCA (which is probably only a surprise to some statisticians and spectroscopists who treat PCA like it was the greatest thing since sliced bread) — they transitioned smoothly (watch carefully or you might miss it) into “the strip-bark bristlecones are not valid temperature proxies”

    *…and, as everyone knows, hockey sticks are always made from Bristlecone pine, because of the tree’s inherent hockey-stick shape.

    Don’t believe it? Visit a stand of Bristlecones some time. Every branch is “hooked” at the top. It may be genetic or it might just be the prevailing winds at the top of mountain ridges where the trees grow (or perhaps a combination of the two).
    At any rate, word has it among those in the know about this kind of stuff that you can make a great number of hockey sticks from just one tree, with virtually no waste!

    I’m really glad that we are having this conversation because a lot of people are unaware of the latter important fact.

  • luminous beauty // March 8, 2008 at 3:40 pm

    A question for all those CAuditors who believe they know everything there is to know about dendroclimatology.

    Consider a single core sample in which there is poor correlation to local temperature as ascertained only from annual ring widths:

    Can you disaggregate the temperature signal from confounding factors? What other measurements besides annual ring width would you use?

  • MrPete // March 8, 2008 at 3:42 pm

    LB sez: “Your assignment as a budding dendroclimatologist is to determine where to find environments in which confounding factors are minimalized.”

    I’m 100 meters away from a nice greenhouse :-)

    Personally, and speaking with others who have significant bio experience, I’m cautious about ever finding such an environment. My null hypothesis is that it does not exist.

    Back to the books… certainly a lively discussion here!

    [Totally OT but hopefully lightening the atmosphere a bit... why do we need greenhouses at 7000+ ft altitude? Sure, extending the growing season is one. Not much grows when the night time low is 10F. However, even more pertinent to a successful growing season is: avoiding hail (ever seen 50cm of hail fall? How about 5-6cm hailstones? Ouch!), wind, and other craziness. My wife has developed a mini-greenhouse technique for gardening, involving PVC hoops and plastic to make "Conestoga Wagons." Even with that, our outdoor tomatoes were decimated in last fall's hail storm. Punched right through all but the toughest materials.]

  • MrPete // March 8, 2008 at 3:50 pm

    LB,

    a) We sure don’t claim to know all about d-c. Far from it. More like, there’s a lot of disciplines involved in understanding this stuff. Some of us have expertise in surprisingly-related areas that too easily are ignored.

    b) There’s been extensive discussion of your question. Google Almagre on CA.

    c) Our Starbucks adventure did involve other measures. Check out the provenance files. Not sure what if anything will emerge from all that. Also not sure if some of the other analyses, like soil samples, have or will turn into useful data. We accomplished the primary field goals; other data may or may not have been successfully collected and processed.

  • George // March 8, 2008 at 4:28 pm

    Judith Curry quote:

    ‘We are wasting time attacking each other’s credentials and motives.”

    Actually, the entire problem is the “we”.

    By and large, the “we” are not scientists and I would guess that the vast majority of them have little to no idea what they are talking about when it comes to climate science.

    Scientists (at least the ones who pay attention outside science) know who the “we” are and it is very easy for them to recognize that the vast majority of the “we” have no background whatsoever in the relevant scientific areas they are critiquing. The “we” are simply speaking gibberish, as far as the scientists are concerned. And most scientists simply ignore them.

    In the pre-internet age, these people, the vast majority of whom do not publish in scientific journals, would never get the time of day and their complaints would fall only on the ears of their (unfortunate) spouse and perhaps fellow workers.

    But, for worse, in this case their “voice’ has been amplified by a factor of 1000 or even 1,000,000 — at least when it comes to the public perception — for no other reason that they have a blog that is popular among the contrarian crowd and that their nonsense gets air time (amplified yet again) on FOX News.

  • Spence_UK // March 8, 2008 at 4:36 pm

    Lazar,

    I understand your question now, and appreciate the scientific style in which your question was posed. Your question is, in essence, does this problem matter? Does the rest of the algorithm cope with artefacts introduced by the decentred PCA?

    I don’t have time to go into great detail now, but my answer would be - yes, it does. A simple test is to apply trendless noise to the algorithm both before and after the decentred PCA step - which McIntyre effectively did in his reply to Huybers. There is no temperature signal going in, so we should get no real difference on the output. But there is a huge difference - the RE significance without decentring is 0.0, the RE significance with decentring is 0.54. Clearly, the step which is supposed to be throwing out the non-temperature data is failing to deal with what the decentred step is providing it. I’ll touch on my view as to why this might be below.

    Robustness is the second issue, and the results of MBH98 were specifically claimed to be robust. Robustness in statistics is achieved by removing sensitivity to outliers, not increasing it. See here for example:

    http://en.wikipedia.org/wiki/Robust_statistics

    For an uncontroversial example, imagine averaging 100 time series containing consistent signal and orthogonal noise. You should get a tenfold improvement in signal to noise. If I throw out 10 samples, I get a trivial loss of 5% of my signal to noise. If that tiny change substantially changes my conclusions, it should be of great concern - what if I had only taken 90 samples? If I took 110, could it change my conclusions again?

    Of course, McIntyre performed this test and found that by eliminating particular samples, the conclusions changed markedly. The reason for this is not just the decentred PCA, but the whole algorithm; clearly, having an up front process that can promote outliers is not a good start to developing a robust algorithm. Note that once you have identified a lack of robust to one small group of samples, you cannot reinstate it by testing against throwing out other groups.

    The failure of the step that selects temperature signals is not suprising. Inject trendless noise into the decentred PCA, and you get a band-limited step function out, with the centre of the step around 1902. The band limiting is a function of the colour of the injected trendless noise. This might be, say, a rising ramp from 1902 to around 1940, followed by a plateau from 1940 to 1980. That sounds to me like it might well be close enough to the historical temperature record for the algorithm to grab it with both hands. Looking at the proxy weights out of the algorithm does indeed support this.

  • fred // March 8, 2008 at 4:52 pm

    Lazar, stats is not my field. Are you saying there is no textbook or reference manual published in which how to do decentered PCA is is explained at somewhat greater length, and with some worked examples. We can find plenty of stuff on how to apply every other stats technique. There must be some material someplace on how to do this, besides Tamino’s blog!

  • Phil B. // March 8, 2008 at 6:14 pm

    Tamino, I just got through rereading MBH98 and I am a bit confused about your above post. MBH98 did a PCA on 1082 monthly grid cell temperatures during the calibration period and then averaged the PCs to obtain annual temperature PCs. MBH98 then regressed the proxies sets in a stepwise manner against the largest variance temperature PCs to obtain weights for each proxy to reconstruct the temperature PCs. IMO, Dr. Mann centered the proxies around the calibration period so he didn’t have to calculate offset terms as the grid cell temp PCs had zero means. Did I miss the PCA on the proxies?

    I was surprised that you did your PCA on synthesized data rather than actual proxy data that MBH98 used. Dr. Mann has made the data readily available and the files are relatively small. I think that it’ s useful to perform PCA on the proxies sets and look at scree plots of the eigenvalues/singular values. Caerbannog, as the first commenter, suggests that this is what he would do. I performed a PCA on MBH98 proxy set data 1400.dat for the 1400AD to 1980AD period (22 proxies) and the scree plot looks like what one might see from noise, but I would welcome your observations.

    Phil B.

  • Gavin's Pussycat // March 8, 2008 at 6:20 pm

    It warms this old furry feline heart to see some territorial instinct on display here… go get them Bulldog!

  • nanny_govt_sucks // March 8, 2008 at 7:07 pm

    [Response: Bullshit. It’s the abandonment of valid PC selection procedures that enabled MM to discard exactly the variation that corresponds to the hockey stick. Unfortunately, that particular variation *should* have been included according to objective selection criteria. As a result it’s no surprise that the MM result fails verification.]

    I’m confused. In the comments of the first part of this series you said:

    “Indeed there aren’t hard-and-fast rules about how many PCs to include in all cases.”

    So, what are “valid PC selection procedures “, and what are “objective selection criteria”?? It would seem that you are talking about hard-and-fast rules here.

    [Response: There aren't any hard and fast rules to cover all cases. In fact, Jolliffe mentions case in which the low-variance PCs can be what you're really looking for (like outlier detection). But MBH applied a procedure for selection. MM didn't follow that procedure when claiming to emulate them, just copied the bare number included.]

  • TCO // March 8, 2008 at 7:37 pm

    Did the MBH article mention the use of the decentered transform? Should this aspect of methodology been shared?

  • Ron Cram // March 8, 2008 at 8:37 pm

    Tamino,

    Did you bother to ask any statisticians about your post before posting it? You are not just opposing McIntyre and McKitrick. You are going up against Wegman and Von Storch and Zorita as well. Von Storch and Zorita published a peer-reviewed article on this topic. They found McIntyre was correct that decentering the data was wrong and resulted in an artificial hockey stick. They also claimed it didn’t “matter.” I had a long email exchange with Zorita about this. I asked how it could not matter and Zorita replied that it was because MBH had so many other errors. Von Storch and Zorita believe in global warming. They just want to see science done correctly. MBH was not.

    If you really think you are correct here, you should try to have your analysis published in a journal. If you can find a lazy editor willing to publish it, I can guarantee a clear thinking rebuttal from one of any number of well known statisticians.

  • Surly // March 8, 2008 at 9:07 pm

    Can some kind soul link to whatever article discusses adjustments to account for BCP carbon fertilization and the resulting temperature reconstruction? The claims that the hockey stick is “broken” seem to be based on the two issues: MBH’s PCA methodology and BCP CO2 fertilization. I am trying to get a handle on both those claims on the part of the “auditors” and would appreciate some references. Thanks!

  • nanny_govt_sucks // March 8, 2008 at 9:58 pm

    But MBH applied a procedure for selection.

    What was the MBH procedure for selection of PCs? Where is it described?

  • MrPete // March 8, 2008 at 10:14 pm

    Surly,
    There was a 2006 discussion of this at CA with a dendroclimatologist. He’s been studying BCP’s etc at Cirque Peak, a wetter location (near Sequoia N.P.).

    There’s conjecture that stripbark growth is due to fertilization, but it doesn’t really fit. We have an alternate hypothesis in development that is essentially non-climatic in nature. The following quote from the linked discussion may be helpful.

    To tie into the present PCA discussion… this is what makes statistical analysis interesting. If the physical evidence doesn’t really match the parameters you know, it is important to be very cautious about presuming that a good statistical “fit” actually means something.

    I (and probably most others) am not really certain how strip bark growth relates to photosynthetic area, root area and other metrics that drive conifer growth. It is also quite possible that the strip bark growth mechanism has little to do with climate - in which case the models for strip bark growth and normal trees might be quite different. I am not aware of any studies that have looked at this- not really my area of expertise.

  • dhogaza // March 8, 2008 at 10:15 pm

    I had a long email exchange with Zorita about this. I asked how it could not matter and Zorita replied that it was because MBH had so many other errors.

    List them. As presented, this is an empty assertion, since we have no way of verifying 1) whether Zorita said that 2) whether he was correct 3) whether you’re even telling the truth about having had such an exchange in the first place.

  • dhogaza // March 8, 2008 at 10:25 pm

    The claims that the hockey stick is “broken” seem to be based on the two issues: MBH’s PCA methodology and BCP CO2 fertilization.

    Given that you don’t need to use MBH’s PCA methodology to get a “hockey stick” from the data, why is this even an issue ten years later?

    Is there any reason other than to smear Mann as being incompetent, dishonest, or both?

  • John Cross // March 8, 2008 at 11:14 pm

    Nanny: You must have missed the part of Tamino’s post where he said “I have one request: before you raise other issues about the hockey stick, address this one.”

    So can you please point me to the part of your discussion where you addressed this. Thanks,

    John

  • TCO // March 8, 2008 at 11:16 pm

    Dghosza: Yes, there are reasons other than persecuting poor Mike to examine this work and look for errors. Importance of the result to policy. Sheer math/science interest. And note, it’s not just about “other methods give the same error”. In school, you get marked off if you have two errors that correct for each other for instance. This is not solely an advocacy issue. There is also a dimension of using proper stats methods.

    Maybe the Zorita comment is empty. But then maybe many blog comments are empty. These things are relative. Sure, I’d LOVE to have a complete discussion from Zorita of what he means and how it happens. But the comment in and of itself is interesting to me. As it encapsulates a concept. A concept that cuts both ways…against Mann…and against Steve M. IOW, the step while flawed is compensated for with other effects. The way that this cuts against McI is that he has been unwilling (and sophistic) in describing the exact nature and impact of each posited flaw. McI tries to conflate things so that the headliner issue decentering carries the weight of other aspects of the algorithm. Also, Zorita is one of the few (Huybers another) that I really trust to look at this thing without rhetoric games that I (an opinion, but based on 43 years on the planet and lots of science and lots of debates on science and observation of human nature) see from Mike and Steve.

  • Surly // March 8, 2008 at 11:16 pm

    dhogasa, that is precisely why it is still alive because this is not about evidence or science but about smearing and raising doubt. In my experience on various unrelated forums, “skeptics” inevitably bring up the hockey stick as proof that global warming is wrong. They dredge up the PCA argument and BCP argument and I for one would like to be able to respond . The “hockey stick is broken” meme is still out there circulating in the public debates and I don’t have anything to post in response to it. I can at least point to this post to respond to the PCA issues, but the BCP argument remains.

  • Hank Roberts // March 8, 2008 at 11:19 pm

    Look, he didn’t use the best possible tool in the best possible way to get the correct result, he just got the correct result (within 0.05 degree C, as noted).

    The 0.05 degree C error is proof he wasn’t perfect.

    Notice none of the climate scientists even get involved in these discussions any longer? Nobody who’s published in the field previously has even a “submitted to” paper online.

    Hobby horse stampede.

  • TCO // March 8, 2008 at 11:35 pm

    Hank: how do you know he got the right result? Have you been in a time machine to check the MWP? Lots of other reconstructions (Moberg, Esper) have different MWPs. Also, the Burger 2005 paper shows how different methods choices can make large differences in the recons (see the spaghetti graphs).

    If you’re just talking about there being a .05 difference, but about McI inflating it…well…I sympathize. McI has a nasty tendancy to conflate things, to resist disaggregation and examination of scale.

    BTW, if he DID use the wrong method, why is it so hard to get an admission? Why the refusal to just rerun with correct method? That is ego science…and I know ego scientists.

  • Hank Roberts // March 9, 2008 at 12:00 am

    >admission
    Read subsequent papers; methods are always improved. The only time you find an ‘admission’ is something like the Christy mistake where he did admit an error, or the journal where the editors resigned after publishing a bad paper. That’s how you tell an error in a profession.

    If everyone still used the same methods used 20 years ago you’d think that was proof they were doing the wrong thing too, wouldn’t you?

    You folks setting yourselves up as judges are like the people in the bleachers shouting at the players on the field who you’re there to watch.

    They’re not there for your coaching.

  • Lee // March 9, 2008 at 12:32 am

    TCO says:
    “Why the refusal to just rerun with correct method? That is ego science…and I know ego scientists.”

    TCO, I strongly, strongly (did I say strongly, strongly enough?) disagree. That is normal science.

    When someone’s early work is improved by later analyses, one does not normally go back and redo the early work with the new methods. The published improved analyses ARE the improved analyses. Good scientists take the improvements and corrections and apply them to new work going forward.

    Why should Mann go back and redo this founding (and therefore by definition least sophisticated) work, when there are many subsequent improved works already out there?

    To me, the continued hammering on the founding paper by Stevie Mac et al is an avoidance of the newer work - and it does not place any onus on Mann to redo the founding work.. This seems especially true since I spent more time than I like to admit poring through CA trying to figure out what the hell they were saying in their occasional scattershot comments on the newer work. It has become hard for me to believe that the incredible obfuscation of argument by SM over there is entirely accidental - he’s too smart for that. The fact that he engages in what is IMO dishonest behavior - altering his posts without notice, for example - doesn’t help.
    Why should Mann go back and redo superceded work because someone like SM refuses to stop chewing on it?

  • JCH // March 9, 2008 at 12:50 am

    Whoops.

    Well, if he did, would all these baying boobs of bountiful boo-boos finally shut the fiddlesticks up?

  • TCO // March 9, 2008 at 1:03 am

    If it was in error, he should admit the error. There is something truculent about both Mann and McI.

  • Hank Roberts // March 9, 2008 at 1:08 am

    Remember you’re in the bleachers. You’re part of the audience, and screaming instructions at the player is merely recreation.

    The important papers around the editorial resignations are here, as references –see links at July 1.
    http://www.arp.harvard.edu/sci/climate/journalclub/

    That’s an example of a mistake.

    This is an example of finding a mistake:

    Correcting Temperature Data Sets
    John R. Christy, Roy W. Spencer;, Carl A. Mears, Frank J. Wentz;, Steven C. Sherwood, and John R. Lanzante
    Science 11 November 2005 310: 972-973 [DOI: 10.1126/science.310.5750.972] (in Letters)

    ……correction being used by Christy and Spencer for the lower…troposphere had the opposite sign from their correction for the middle troposphere sign, we knew that something….
    We question why Christy and Spencer adopted … found a previous error in their methodology……

    Read the followups to see Christy et al. acknowledge that a mistake was made, and subsequent corrections propagating through other people’s work who had relied on the mistaken paper:
    http://www.sciencemag.org/cgi/search?session_query_ref=rbs.queryref_1205024415139&COLLECTIONS=hw1&JC=sci&FULLTEXT=%28christy+AND+sign+AND+error%29&FULLTEXTFIELD=lemcontent&RESOURCETYPE=HWCIT&ABSTRACTFIELD=lemhwcompabstract&TITLEFIELD=lemhwcomptitle

  • Surly // March 9, 2008 at 1:55 am

    “It has become hard for me to believe that the incredible obfuscation of argument by SM over there is entirely accidental - he’s too smart for that. ”

    Agreed. One recent post regarding Hansen has the “I don’t mean to suggest any wrong-doing, but” tone to it. Too many posts there do the “When did you stop beating your wife”trick and while SM is unwilling to say it outright , the other posters aren’t so reticent. Then SM says he’s too tired to clean up the posts. Sure.

  • George // March 9, 2008 at 2:15 am

    TCO says:

    “If it was in error, he should admit the error. There is something truculent about both Mann and McI.”

    Why? What difference does it make?

    As far as the science is concerned, even if Mann got the “right answer for entirely the wrong reason”, that would not matter one bit.

    The only thing that matters is whether his conclusion is correct — and if the analysis done without using PCA also yields a hockey stick (which it does), then whether Mann did the PCA analysis correctly is basically moot as far as the science is concerned.

    Johannes Kepler made errors in his calculations and nonetheless got the right answer.

    No one tries to claim today that “his findings are bunk because he made arithmetic errors”. That would be absurd.

    From the standpoint of science, the only thing that matters is that he was right.

  • MrPete // March 9, 2008 at 3:33 am

    From the standpoint of science, the only thing that matters is that he was right.

    Unprovable.

    Methods and data are important for many reasons, not least because others use the same or similar methods and data. If bad data and methods are reused significantly in a small community, you get a “consensus” that’s built on a house of cards.

    When methods are obfuscated such that others are unable to replicate the work, and the methods cannot be confirmed as having statistical validity, we’re left not knowing if the results are correct or not.

    Worse, when earlier work does not disclose statistical methods, and years later after the methods are decoded, it is discovered the earlier work did not use standard statistical methods… do we just say “hey, move on” and ignore the issue?

    Do we sit by quietly if the same “game” is being played with newer work? What should be done if “alternate” or “refined” statistical analysis techniques are employed? And details are not disclosed? And the new techniques are not run through statistical peer review for validation?

    I suppose we should appreciate that as creative entrepreneurialism in 21st century science?

  • John Mashey // March 9, 2008 at 3:50 am

    TCO mentioned “Importance of the result to policy.”

    As far as I can tell, none of this has the slightest importance for policy. [It's wonderful tutorial.]

    Suppose a) we had 2000 years’ of current-technology temperature data [time amchine] or b) We didn’t have any of the data used in MBH before 1500, or c) MBH had never written the papers.

    What, exactly, in case a) or b) or c) would we do going forward? We’d know more in a), a little less in b), and in c), I suspect others would have done similar reconstructions sooner or later.

    Would Greenhouse physics change? Would First and Second Laws of Thermodynamics be repealed? Would the energy imbalance of the Earth disappear?
    I.e., see Fig 2 of http://pubs.giss.nasa.gov/docs/2005/2005_Hansen_etal_1.pdf

    If not, exactly what policy difference is there?

    Anyway, can anyone suggest *exactly* what the policy difference would be?

    All of this seems like: a $B company is losing money, but someone (not even a strockholder) thinks its CFO was off $1 in the 1998 tax returns and they should go back and GET THAT FIXED before they do anything else, and if turned out it was right, well, there’s always 1999.

  • George // March 9, 2008 at 3:50 am

    Mr pete:

    Analysis done without using PCA also yields a hockey stick.

    So, how does it matter one way or the other whether Mann was right or wrong with the PCA analysis?

  • Hank Roberts // March 9, 2008 at 4:02 am

    What matters in science is kind of like what matters in evolution, where fitness is approximated by how many grandchildren you have.

    In science, it’s how many citations build on your work, how many people found something useful to extend, or improve on, or confirm, or even disprove.

    That’s why I pointed to the way the Christie error was handled — it was the basis for quite a few years of other people’s work and a gazillion blog posts; it was in error; it was acknowledged; the papers citing it now point back to the correction and much got rewritten.

    This is why you can click those buttons for subsequent citations at science sites.

    Very few papers have corrections that significant (where a sign change changes the basic conclusion that two things were different — and the conclusion is that they weren’t different after all).

    What matters now is his subsequent work and what others find useful.

    Science isn’t a mighty oak with a single deep root.

    Science is kudzu. It grows at the young new end fresh each time putting roots wherever there’s fresh substance to draw on.

    Science thanks the old work with citations — but it’s moved beyond them.

    That’s why the first step is to replicate — your own lab, your own data collection — the previous work.

    This is why scientists don’t “audit” — they replicate.

    It’s not a religion. Founders are nice people but they’re just people, and their work is no better than it has to be.

    What counts is what’s going on now.
    The people doing science in this area moved on long ago.

    Funny how come so many people want to pretend they’re discussing climate change but don’t talk about current work.

    Why? Know anything about what’s being published these days?

    Scary, isn’t it?

  • MrPete // March 9, 2008 at 4:33 am

    Analysis done without using PCA also yields a hockey stick.

    Depends on the data and methods. Analysis with/without PCA also yields MWP and LIA. So what?

    Me? I just wanna see some good solid studies: well-founded data, well-founded methods, proper CI analysis, etc etc. There’s not much of that in the “contested” arenas at this point.

    Funny how come so many people want to pretend they’re discussing climate change but don’t talk about current work.

    Funny how so many people want to “pretend” (your word, not mine) they’re making progress on climate change research but don’t talk about current data either.

    Hank, I wouldn’t slam the skeptics too much for being a bit behind. It’s easier to crunch through everything when you have a budget, cooperation and visibility.

    Plenty of surprising/confusing material out there to keep everybody curious, AFAIK :)

    (Why does it take so much longer for good data and good work to be published, just because it doesn’t fit the received wisdom? No reason to be reluctant to publish divergence-problem data, etc. It’s that stuff that keeps science lively.)

  • TCO // March 9, 2008 at 4:53 am

    The rationale for admitting errors however small is so that we can have real examination of things that moves to truth. This is the way of the scientist, not of the sophist, not of the lawyer. Both McI and Mann are truculent. They refuse to answer questions. Refuse to admit minor errors. I assume they justify this with some feeling that others will seize on admissions to make wider claims of error. And based on what I usually see…I agree that their opponents would do that. But it doesn’t matter. If you are a true scientist. A true mathematician.

  • nanny_govt_sucks // March 9, 2008 at 5:18 am

    Nanny: You must have missed the part of Tamino’s post where he said “I have one request: before you raise other issues about the hockey stick, address this one.”

    Tamino brought this up on this thread, not me. He said: “But MBH applied a procedure for selection.”. I’d like to know what he’s talking about.

  • dhogaza // March 9, 2008 at 5:40 am

    Depends on the data …

    In the context of evaluating whether or not Mann’s statistical approach is valid or not, this is …

    a goalpost move.

    Why do you people always do that?

    Many posts ago (over a 100) I said to HB:

    Why not just delete those comments that aren’t relevant to your post, i.e. attempts to divert the discussion to “strip-bark samples”, etc?

    And that’s EXACTLY what you’re doing when you say “depends on the data”.

    Which, I might add, is a tacit admission that the statistical attacks don’t add up to SQUAT.

    When you move the goalposts, you are tacitly conceding the original point (not that I expect you to be honest enough to admit it).

    Why does it take so much longer for good data and good work to be published, just because it doesn’t fit the received wisdom?

    Prove your assertion. What good data isn’t being published and good work isn’t being published because it doesn’t fit the received wisdom.

    Sorry, as long as HB allows me to post here, I’m not going to allow unsubstantiated bullshit like this appear without my challenging it.

    Prove your statement. Prove that 1) the data you claim is suppressed is “good” and 2) the work is “good” (I presume you mean analysis?) and 3) it is because it doesn’t meant “received wisdom”.

    You do realize that when Hansen etc first started making claims they were laughed out of the house, right? Yet they managed to get published. They never whined the way you are.

  • George // March 9, 2008 at 6:14 am

    Mr Pete claims:

    I just wanna see some good solid studies: well-founded data, well-founded methods, proper CI analysis, etc etc. There’s not much of that in the “contested” arenas at this point.

    And you are the one who decides what is “good”. “well-founded” and “proper”, right?

    How convenient. :)

    Care to tell us what your qualifications are for making such a sweeping judgment?

    University credentials in climate science or a directly relevant area?

    Peer reviewed papers in climate science?

  • Hank Roberts // March 9, 2008 at 6:21 am

    http://www.realclimate.org/index.php/archives/2007/05/hansens-1988-projections/
    and
    http://pubs.giss.nasa.gov/abstracts/1988/Hansen_etal.html
    “… Principal uncertainties in the predictions involve the equilibrium sensitivity of the model to climate forcing, the assumptions regarding heat uptake and transport by the ocean, and the omission of other less-certain climate forcings.”

  • fred // March 9, 2008 at 6:50 am

    I am still puzzling over this question of decentering. Its not my subject of course.

    Can no-one point me to a textbook account of how to do this, with a few worked examples, and some discussion of why it is the same and in what circumstances its the same as conventional PCA? The presentation cited is not what’s meant, I can’t get to a recipe and explanation from it.

    My confusion is something like this. We seem to have a procedure which conventionally is carried out using the mean of the series. Someone carries it out using a mean of a subset. I can’t see how this can be either correct or give the same results as using the mean. Once we start picking something which is not the series mean, can we pick anything? Like, can we pick in a 100 item series either data points 90-100, or else 1, 5, 26,31….etc? If not, why not?

    In fact, to generalize it, why not pick any number at all? If you are not using the series mean, why not just make up a number?

    Obviously you cannot pick anything but the series mean when computing most basic statistics. So why is PCA different?

    Perhaps my professional background with its focus on defined recipes and procedures is getting in the way here, but it is not clear. I can’t tell from the descriptions and comments how to implement this thing, or how to know when its been done correctly. Were one writing a program which would do decentered PCA in some cases but not others, at the moment I’d have no idea how to either write the decentered PCA part, or to write the selection algorithm so it picked the ones where it is appropriate.

    Always knew that sooner or later this was going to lead to learning R. Oh well. There are a couple of good textbooks on that.

    [Response: I don't know if there's a textbook exposition. But textbooks are generally behind the times when it comes to analysis. If you restricted yourself to textbook methods on Fourier or Wavelet analysis, you'd not only be behind the times, in some cases (especially regarding the analysis of unevenly sampled data), you'd actually be in error.

    But for your sake, I'll do *yet another* post in this series. About non-centered PCA in general. I'm working on a post on sea level at the moment (at another reader's request), so it'll have to wait for that.]

  • Patrick Hadley // March 9, 2008 at 10:27 am

    John Mashey asks whether all this is important to policy. On the one hand he is right, the physics of GHG is not in any way dependent on MBH.

    There are however four aspects in which this argument is very important.

    The first two relate to the medieval warm period. The graph used by IPCC in 1995 showed a sustained warm period between 1100 and 1400 AD. Before MBH it was accepted that the MWP was warmer than the present and that this period was a period of general worldwide prosperity.

    If the MWP did exist then it would help (but obviously not prove) two arguments used by sceptics: that the world benefits from warmer temperatures; and that the recent rise in global temperatures is not unprecedented and therefore one cannot argue that just because warming has followed a rise in CO2 it must therefore be caused by this rise.

    The third way in which this argument is important is in questioning the methods and principles of the climate science consensus. If it could be shown that a very influential and widely distributed graph was based on poor scientific methodology and dodgy statistics, this would give critics the chance to question whether other pillars of the AGW argument are similarly defective.

    Fourthly the argument is important because if it can be shown that after serious errors in MBH were proved by McIntyre and McKitrick, the AGW establishment, far from welcoming this criticism as a major contribution to the scientific process, instead mocked MM’s work; and various attempts were made to cover up the errors they found and deny them. If this were true then it would also greatly undermine the credibility of the global warming consensus.

  • Chris O'Neill // March 9, 2008 at 11:02 am

    George:

    If the hockey stick shape is indeed an artifact of PCA, as some claim, then why do I see it when I look at this?

    Indeed, and I could also ask why we see it when it is produced by up-to-date methods such as regularized expectation maximization. I think the answer is that in hockeystick denialism the strategy is to concentrate on an obscure debatable issue (non-centered PCA), even though it is rendered completely insignificant by later developments (the use of regularized expectation maximization instead of PCA), in the hope that enough people won’t realize its complete insignificance. Anyway, it’s still worth annoying the hockeystick denialists (by pointing out their misunderstanding of non-centered PCA) if for no other reason than confirming the understanding of people who are not as well educated as our blog host.

  • MrPete // March 9, 2008 at 12:46 pm

    dhogaza, you said prove…

    Obviously, some of these things are scientific statements, and some are “intent” statements impossible to prove. All one can do is look at evidence and watch.

    ‘twould be nice if someone had time to keep a record of such things, like the truth in advertising folks. I don’t have that kind of time.

    But there’s plenty of evidence out there.

    AR4 was published in 2007. Compare:

    * the speed with which certain “confirming” papers got referenced (with original paper, references, and AR4 dates all piling up at the “finish line” to get hurried into print, even though the “confirming” paper came incredibly close to not being published at all due to its serious problems). Obviously I’m thinking of W&A etc.

    * The lack of uncomfortable data and papers surrounding the infamous Divergence Problem. Happily, some younger dendros have been getting involved recently, yet in general, data from updated tree ring studies gets published and archived with not-quite-glacial slowness (particularly relative to other papers such as mentioned above.) And the young dendros weren’t exactly represented in AR4, although the related data has been reportedly being collected for many years.

    * We have the intriguing case of a grad student working under “H” of MBH fame. After his student’s work was approved as a PhD thesis, the thesis advisor himself still used the old data. And the new data has gone missing. And nothing has been done.

    To echo Hank’s question, why are W&A, H, AR4, etc etc so intent on delving further into propping up the old hockey stick formulation based on old data, when new data has been collected, worked through the grad student slave labor mill (how do you do that cross-out thing, Tamino? :-) ), and certainly ought to be available for analysis and publication.

    From personal experience, it does not take years to move tree ring data from collection straws to usable form.

  • Hansen's Poodle // March 9, 2008 at 1:02 pm

    Tamino, any reason why you refuse to release Jean S’ answer? I hope it’s not censorship and it was lost in cyberspace.

    [copy of JeanS's "answer" removed]

    [Response: It's personal.

    We were having a heated discussion, tempers flared from time to time, passions were aroused, but it was pretty much at least at a *minimal* level of civility -- until JeanS came along. Then it's "repeat that lie" and and "bullshit" and the statement that I have no intellectual honesty, and other things specifically targeted at me, designed to annoy me. Personally. It did. If he chooses to make it personal, so be it. I don't have to host it on my blog.

    The "answer" has more of the same, pretty much repeats the same claims as made in the original, and waves credentials around. I find him offensive, and arrogant on a galactic scale. If that's the way he chooses to argue, that's his choice. I don't have to pollute my blog with it.

    I didn't just make this stuff up. As an earlier comment points out, my rebuttal isn't really my own creation, it borrows heavily from the response on RealClimate by Mike Mann himself, here and here. My main contribution was the exposition. Those who are keen on this issue can find more information there, including discussion of *more* of the mistakes of MM. Highly recommended reading.

    It's crystal clear that he will *never* concede anything, he will *never* let it go, he'll *always* have to get the last word, and it won't be polite either. Hell, McIntyre has been hammering on this for years. It's the unruly but often effective strategy of dominating an argument by volume. I've stated my case, he's made his. I guess they really don't have anything better to do with their time than continue arguing forever; I do.

    I'm confident those who are desperate to know, can read all about it on CA.]

  • fred // March 9, 2008 at 1:22 pm

    http://www.uoguelph.ca/~rmckitri/research/fallupdate04/MM.resub.pdf

    Tamino, it may be a bit different from what you think. Go through the bits about weighting. Or maybe I’m not understanding it, that is possible too.

  • John Cross // March 9, 2008 at 2:16 pm

    Nanny: well, over a half a year ago I submitted a list of replies to some points that you made (you can find it in this thread ).

    You brought that up on that thread and I would like to know what you are talking about. In fact, you have said several times that you were working on an reply. Perhaps you should hold off opening new cans until you can finish your detailed analysis.

    Awaiting your answers.

    John

  • Meltwater // March 9, 2008 at 3:00 pm

    fred said:

    It would also help if we could ban the expression ‘intellectual honesty’ from this debate - which should be about something perfectly objective, the use of statistical methods. Helps not in the slightest.

    On the contrary, people just beginning to do their homework on this issue need to be warned that they will encounter debaters as well as arguments that are intellectually dishonest. Frankly, they need to be warned also that their own sincere questions may be mistaken for such dishonesty because of the extent to which it has come to pollute the debate. mikep said:

    This discussion is losing sight of the simple issues.

    Keeping the simple issues in sight can help keep us honest. One of the simplest is to keep asking: Given the accelerating rate of human unburied carbon emissions, how could a temperature ‘hockey stick’ not result? CO2 is one of several gases that absorb or scatter infra-red photons, mostly from the surface of the Earth, and heat up as their molecules are kinetically excited by the scattering and absorption. This fact of radiation physics was discovered by the likes of J.B.J. Fourier and John Tyndall between 190 and 150 years ago. What physical mechanism could possibly prevent climate sensitivity to so much kinetically excited CO2? A few have been proposed but those proposals have not fared well in the scientific literature. Unless a proposal of greater merit can be advanced then the smart money will still bet that the ‘hockey stick’ is right. Remember, it is part of a larger picture that has been patiently assembled over several half-centuries of peer reviewed science. Temperature measurements, weather observations, paleoclimate core and proxy data, and satellite surveillance together yield a picture of climate that cannot be modeled, reproduced or explained unless the CO2 sensitivity is around 2.3 Celsius or Kelvin degrees, or 4.14° Fahrenheit, at a minimum. People intent on finding fault with the ‘hockey stick’ deserve to have their arguments and their intellectual honesty challenged. For the ‘hockey stick’ to be wrong, a great deal of other science has to be wrong too. How could it all be wrong? Where is a compelling reason to conclude that so much science is wrong? By giving us this lesson on Principal Components Analysis, Hansen’s Bulldog, slash tamino, strengthens our confidence in an alternative explanation: the statistical methods that produced the ‘hockey stick’ are under politically motivated attack, and some of the most prominent attacks are without valid mathematical or scientific foundation.

  • Surly // March 9, 2008 at 3:43 pm

    “If it could be shown that a very influential and widely distributed graph was based on poor scientific methodology and dodgy statistics, this would give critics the chance to question whether other pillars of the AGW argument are similarly defective.”

    And this is the crux in a nutshell — the goal of the denialists (I won’t call them skeptics) is to discredit the hockey stick and thus, they hope, discredit the whole science of global warming. That’s why this is more than an academic debate, although it is that, too. It’s a political and policy debate as well. As long as the meme of the “broken hockey stick” remains in circulation, the other half of its premise — broken theory — will circulate and give denialists something to wave in front of everyone.

  • Hank Roberts // March 9, 2008 at 3:44 pm

    > To echo Hank’s question,

    Don’t put words in my mouth with your dirty hands. You’re getting your material from CA, don’t pretend you’re echoing my question.

    Third derivative of acceleration.

  • P. Lewis // March 9, 2008 at 3:55 pm

    Re George // March 9, 2008 at 6:14 am

    Mr Pete claims:

    And you are the one who decides what is “good”. “well-founded” and “proper”, right?

    How convenient. :)

    Care to tell us what your qualifications are for making such a sweeping judgment?

    University credentials in climate science or a directly relevant area?

    Peer reviewed papers in climate science?

    You forgot one or two probabilities possibilities, George: Climate Audit? Watts Up With That?

  • mmghosh // March 9, 2008 at 4:36 pm

    Mr Hadley

    I do not think that anyone disputes the presence of a medieval warm period in Northern Europe. The point that is made by by the climate scientists consensus, is that it was not a global phenomenon, because it is not found in the paleoclimatology data from the rest of the world.

    The next point about the MWP is that it is really a red herring. And that in the sense that even it were true that a warmer earth could sustain the population of the Middle Ages, the higher temperatures that are seen today and, if they do rise higher, will cause serious problems for an estimated population of 9 billion humans and commercial establishments in 2050.

    Many orders of increases of magnitude of people now live in flood plains - New Orleans or Galveston or Gangetic Bangladesh are examples. We are talking about a possible very large migration of poulations which are not feasible today as they perhaps were in the 1300s.

    As you are aware, the next cycle of warming will include the next next El Nino phenomenon and a rising curve of solar irradiance sometime in the next five years. GHG aggravation of such a warming cycle has the potential for major consequences.

  • George // March 9, 2008 at 4:40 pm

    Mr pete said above

    I just wanna see some good solid studies: well-founded data, well-founded methods, proper CI analysis, etc etc. There’s not much of that in the “contested” arenas at this point.

    When I asked him above about his qualifications/expertise related to climate science that enabled him to make such a sweeping generalization — “There’s not much of that in the “contested” arenas at this point” — I simply got silence

    Perhaps Mr Pete missed my question but I would just point out that expertise in the area in question is highly relevant when assessing the current state of the science.

    After all, if someone with no background in physics says that there’s not much in the way of good science going on in the area of high energy physics today, at a minimum, we need to know whether he was competent to make such an assessment to begin with. We don’t just take his word for it.

    I would note that, without listing EVERY current study, it is virtually impossible to prove the claim that “There’s not much of that in the “contested” arenas at this point.”

    And the implication that what is going on is “not solid”, “not good”, “not well-founded”, “not proper” etc, is highly subjective, at any rate, so such a claim has questionable value, at any rate (IMHO).

    When it comes down to it, we simply MUST rely on the judgment of the person making the statement — which depends a great deal on their knowledge/background in the area they are judging.

    So, Mr. Pete.

    Let me ask you again, upon what climate science-related “expert basis” have you come to the conclusion that “There’s not much of that [well-founded data, well-founded methods, proper CI analysis, etc etc] in the “contested” arenas at this point.”

    If I get no answer about your credentials in climate science or peer-reviewed papers or even links to other non-peer-reviewed papers that you have written, I will have to assume that you have no expertise in the relevant area and therefore are simply not knowledgeable enough to be making such a sweeping assessment.

    …and I will feel confident that i can safely ignore your sweeping claims about how bad the current state of the science is from here on in. :)

  • TCO // March 9, 2008 at 4:57 pm

    Irregardless of denialists trying to shoot down MBH as a pillar of the temple before going after the rest of the building…or of alarmists propping up weak timber because the whole building is so important…THE QUESTIONS themselves are analytically interesting. It’s just so easy for both sides to refuse to engage on specifics because of not trusting the other side. It’s like the refusing to admit an error because the other side will think that it implies more faults elsewhere. WHO CARES. Be UNILATERAL!

    I understand Tammy’s concerns with JeanS. He does spout on so much about credentials. Big whoop that he has a Ph.D. It’s always the weakest ones who insist on being called Doctor. However, Jean does understand the math here better than most of us commentators so it would be interesting to see Tammy and he examine things to deeper levels. I have also found JeanS to be a bit imperious…to get upset at valid even interesting points (the times I’ve gotten “nuggets” by chewing away without knowing the math) if not expressed with knowledge of linear algebra and the like. But the good thing is that Tammy and Jean both know R and linear algebra and the like. So there is not the room for such tangential putdowns of knowledge level to distract from critical disaggregation and examination of issues.

    It’s unfortunate that Tammy sees this as a situation of “public teaching” relying heavily on RC defenses of the Mann paper (Mann is a prominent member of RC…so he’s defending his own work). Instead a fresh look at things would be helpful. Less Bulldog, less Pussycat. More Richard Feynman (he pissed NASA off by asking penetrating question after penetrating question, when they wanted to give fluffy slide presentations…but Dick actually wanted to understand stuff. He told the NASAites, “yes this seems painful, but trust me, I speed up. Taking things apart like this is needed” (or words to that effect, don’t have the book in front of me.)

    (I have a bunch of methodology questions left, which I will post separately. Unfortunately, I don’t know lin alg. or theoretical stats. However, it doesn’t scare me a bit from asking critical questions. I am really cocky enough to show vulnerability.

  • TCO // March 9, 2008 at 5:23 pm

    1. The “canonical” word makes me wince. Reminds me of stat mech that I never understood. Can you say what this means with a simpler word? Please?

    [Response: It's the word commonly used. One might, I suppose, say "standard" or "universal" or "most common," although in this particular case none of those -- not even "canonical" -- necessarily applies.]

    2. With the canoe (great example btw), this feels like an example where we don’t want to standardize. Not only do we not want to inflate the noise (or perhaps slow sinking) of the canoe in the Z direction, we want to understand EW versus NS in terms of absolutes. Am I thinking about this right? Comments?

    [Response: You're quite right. This is a case where we know ahead of time that the units for EW, NS, and vertical, are the same size, and we can fully expect that the errors will be the same size in all directions, while standardization will in fact undo that useful property. So in fact this isn't such a great example -- it illustrates one issue very well, but fails to deal with the normalization issue. For the canoe problem, we should probably use the covariance matrix (no normalization) rather than the correlation matrix.]

  • null{} // March 9, 2008 at 5:30 pm

    George, how are we to determine that you are qualified to evaluate/assess the qualifications of MrPete? Is it necessary for you too also pony up some peer-reviewed papers published in all the right journals, of course. so that we can make that determination.

    “Third derivative of acceleration.”

    I think you mean third derivative of displacement.

  • TCO // March 9, 2008 at 5:38 pm

    3. “The real essence of PCA is that it enables us to define a new coordinate system for our data space, one based on the observed variations of the data itself, which gives us an excellent chance to reduce complexity, possibly even reveal some insight. ”

    Yeah…no…agreed. PCA is this really cool tool for data compression (if you’re short of data space, which isn’t the case much nowadays), for calculational efficiency (similar), and ESPECIALLY for looking for patterns. Everyone who talks about PCA, always mentions it’s strength in terms of initial inspection, pattern finding. But if you KNOW what your input variable of interest is…that’s not initial inspection. I mean in the book SUPER CRUNCHERS (written by a liberal, btw, and very popular), they talk about a model for predicting red wine taste upon aging which is based on two factors (summer temp and something else). Was that honker derived by regression against PCs (leaving part of the data behind) or by regression against the data itself? It’s one thing to find patterns using PCA. Another to do the regressions only against PCs or to declare that temp is concentrated in a particular PC, etc. etc. And what does that mean if temp is “prominent” in PC1 based on the (somewhat unusual and non-documented) acentric standardixation), but not with a normal correlation matrix. (sorry if I wander, I’m drinking bloody maries and typing on the wireless.)

  • fred // March 9, 2008 at 5:59 pm

    “People intent on finding fault with the ‘hockey stick’ deserve to have their arguments and their intellectual honesty challenged.”

    No, they need to have their arguments challenged. The rest is pointless personal insults which get no place.

  • TCO // March 9, 2008 at 6:02 pm

    4. I really don’t get your concern with the overfitting on regressions. So much to the extent, that I wonder if you are not quite considering this correctly. Yes, I know the sheer impertinance of suggesting such! :) Seriously, I can do a regression of temp versus ring width and see the impact and make a model with minimal factors. That’s perfectly normal. People build MC models all the time in chemical engineering and leave all kinds of degrees of freedom left over and never touch a PCA.

    5. There is also an issue (regardless of using PCA or some other form of training and weighting individual series) of how important are the series really? You might see this superimpressive number of proxies…but some are carrying much more weight than others. So that the degrees of freedom and overfitting concern becomes more of an issue. It’s not like having 100 independant predictors. It’s like having 30. Because the rest got fed through the training hopper and rejected. Capisce?

    6. There is also an important issue of what we train on. Is it really reasonable to have local proxies training on the global temp. Fancy it up and call it a “field”, but it is still an ambitious teleconnection. Is there a strong (proven statistically, prior) basis for saying that local proxies measure the global field? And the claims of having worldwide coverage become a bit tricky. You DON’T have a set of global gridded temps like with Hansen and the thermometers. What you have is a global set of “global thermometers”.

  • TCO // March 9, 2008 at 6:05 pm

    Tammy: It’s a great example. And don’t worry that the example spoke against a different aspect. I think it’s nice that we can occasionally reach some understanding despite disagreement on other issues, like the greatness of the Washington Redskins and George Allen. Thanks for kind reply.

    [Response: Agreed on George Allen. I suppose if I mention Bill Belichick I'll get slammed?

    (Note: just humor. Please nobody start a Belichick war.)]

  • Patrick Hadley // March 9, 2008 at 6:12 pm

    mmgosh, I did not intend to introduce a lot of red herrings into the thread by mentioning the MWP, benefits of warming etc, just to give my opinion about why the MBH hockey stick is still an important topic of discussion.

    Incidentally, while I gave four reasons to justify the continued debate about the HS, if Meltwater was right when he wrote ” For the ‘hockey stick’ to be wrong, a great deal of other science has to be wrong too. ” then it would seem that the stakes are even higher.

    [Response: I disagree strongly with the "a great deal of other science has to be wrong too" part. But I don't speak for my readers, just as they don't speak for me.]

  • TCO // March 9, 2008 at 6:21 pm

    I guess anothe vague question/concern that I have is in the method of training for decision to keep/reject proxies (or to weight them). For instance, is this like “wiggle matching” of tree rings themselves, where you really have a lot of individual data points and variability and can really feel good that you have validated a match. Or is this essentially a case of a broady increase in 20th century of both temp and of bcps, but with little “wiggle matching” so that you are really fitting to single data point matching (a trend to a trend). Therefore, we don’t feel as confident in the physical driver as if there were a lot of wiggling and response going on.

  • TCO // March 9, 2008 at 6:33 pm

    Previous was 7, this is 8.

    8. Is there a book or a procedure that tells one, that one should do PCA, throw away the lower PCs and then build a predictive model based on the regression of temp versus higher PCs?

    9. I wonder if we do what I said in 8, how it affects predictive efficiency and cofidence intervals. Let’s say we go back to the wine Super Cruncher’s example. And we use PCA to find some tricky hard to find signal. And then build a predictive model based of off it. Won’t it have huge CIs because the noise is still there (that was a driver for using the PCA to find a tricky signal in the first place). And will one really get better predictive efficiency for wine values in the future? If you were a Bayesian betting man, would you prefer the simple model trained on the data itself or the one trained on the PCA? And this is actually an economic esmple. you really can decide to speculate on new wine….

  • george // March 9, 2008 at 6:36 pm

    Null asks:

    “George, how are we to determine that you are qualified to evaluate/assess the qualifications of MrPete? Is it necessary for you too also pony up some peer-reviewed papers published in all the right journals, of course. so that we can make that determination.”

    I would think that it would be pretty obvious that the answer to your last question is “no.”

    I am not the one making sweeping generalizations about the state of the science (at least in the “contested arena” in question), as Mr. Pete has done above:

    I just wanna see some good solid studies: well-founded data, well-founded methods, proper CI analysis, etc etc. There’s not much of that in the “contested” arenas at this point.

    And as far as assessing Mr. Pete’s qualifications, where did I do that?

    I am merely interested in knowing whether to take him seriously.

    It is important (for me, at least) to know whether he has the relevant background to be making the general claims he has.

    If he has no qualifications (or if he chooses not to answer), I for one, will assume that he is not qualified.

    Others — including yourself — are free to make their own decision in that regard.

    I would note that it is not specific claims/implications (ie, ones that can be checked) that I am questioning. One can assess those based on their own merits. But it is the very broad claims/implications that I question: there are no “good solid studies: well-founded data, well-founded methods, proper CI analysis, etc”.

    Surely, you can see the difference?

  • TCO // March 9, 2008 at 6:50 pm

    10. Jollife presentation:
    A. I don’t understand all the terminology and linear algebra. Is the centering he’s talking about the same as what we talk about? What’s “column centering” or “double centering”? does he ever really adress the issue of Mannian decentering?

    B. Is this the best? There’s no academic paper? No math runs showing how different methods (acentered, decentered) give different numbers in different situations and how one is better for a problem than another?

    C. Jolliffe presentation seems to have several cautions against not centering (slides 21 and 38).

    D. Doesn’t seem like he is really discussing “acentric offsets” as much as to center or not to center (i.e. raw versus mean deducted).

    P.s. if in your response, you can distinguish between places where I just don’t understand Jollife and where we are in disagreement but I have a point, I appreciate it.

  • TCO // March 9, 2008 at 6:53 pm

    1o.e.: If you go to the Jolliffe site itself he has several posters on PCA or presentations on it that are interesting. I couldn’t get understand them all, but they mostly seemed to concern being careful (both positive and negative) about what you say you can accomplish with PCA. Good stuff.

  • John Mashey // March 9, 2008 at 6:54 pm

    Patrick Hadley
    “I did not intend…”

    Really? I’ve seen your posts elsewhere…

    Why don’t you attempt to *answer* the questions I actually asked, rather than write what looks like a standard set of arguments for wanting to argue about MBH *forever*? I’ve seen all these before I asked those questions.

    Did you read the Hansen/Nazarenko paper yet?

    Do you understand the difference between physics-based analysis [which work] and modeling stock market prices [which don't]?

    From this comment in RC, http://www.realclimate.org/index.php/archives/2008/02/antarctica-is-cold/langswitch_lang/index.php?p=529#comment-81391, I rather doubt it.

  • TCO // March 9, 2008 at 6:57 pm

    11. Are you really sure that the acentric centering to promote recent temp rise series “was the point”? Mann has never answered the question as to whether this transform was deliberate. And his write-up in science did not explain the transform or tell the story of how he had done it on purpose?

  • TCO // March 9, 2008 at 7:10 pm

    12. Your comment about what impact will decentering really have (after feeding through the rest of the algorithm) is interesting. McI has been somewhat disingenuous in confounding impact on PC1 versus impact on “the hockey stick”. However, if the impact is minimal, because of the rest of the algorithm, why use this relatively uncommone (and not properly explained in the methods) offset? Also, I believe there is one sentence in MBH where they tout the prominent “signal” in PC1. (There are graphs also.) Given that one has to use the acentric transform to get that, this should be explained. While it may not be important to the end state, it is important to the intermediate.

    [Response: As I said in a response to fred, there are enough points of confusion that I'll do yet *another* post in this series, about non-centered PCA in general. I'll keep your issues in mind. I may even feature them; give me time to consider them in the detail they deserve before deciding. I would like to avoid, if possible, off-the-cuff responses, especially when irritated by juveniles (I'm not referring to you). Perhaps one of the sources of confusion is hurried, knee-jerk comments and responses.

    As I also said to fred, I'm working on a post about sea level (yet another reader request), and it'll have to wait until after that. And I'm just one man, with a job and a family and a *life*. Patience...]

  • nanny_govt_sucks // March 9, 2008 at 7:11 pm

    John Cross, your incessant needling won’t make me get to a response any quicker. Asking for a clarification from Tamino is hardly a “new can”, unless you are implying that Tamino’s response will open a new can of worms, as the saying goes. But why would that be, John? Shouln’t it be easy to point to the MBH procedure for selection of PCs?

  • MrPete // March 9, 2008 at 7:22 pm

    Hank, I get my material from lots of places. I happen to give a lot of links to CA in these responses right now because IMHO they do a pretty reasonable job of assembling material. And, I don’t have a lot of time right now for digging out material, even from my own laptop. (And no, my hands aren’t dirty at the moment — too early for gardening season. Shoes are dirty though — just shot a bunch of tree-trunk photos :-) )

    george, I actually did miss your earlier comment. At the moment, I’m stopping by here on occasion as a break from some Real World stuff… I don’t have much available time.

    First, your recent comments have stretched what I said beyond the breaking point. I would never suggest nor imply that there are no good studies, data or methods in all of climate science. That would be beyond silly.

    I said there’s not much to be found, in the contested areas. I like good work, and want to see better work; hopefully you do too. I’m frustrated and saddened that politics and policy have so greatly intruded on scientific process. It’s apparently inevitable, because good science costs real money. Still, regrettable.

    As for qualifications, there are many ways to evaluate qualifications, as well as contributions. From your question, it’s likely you’ll not be satisfied by any answer I can give. I have exactly zero peer reviewed papers to my name, so you will almost certainly consider my multidisciplinary expertise of little value.

    Not to start an academy vs non-academy war, but more as a lighthearted illustration, I could likewise give you a challenge. Since my expertise and contributions in support of scientific progress are not to be taken seriously, it would be inappropriate for me to unduly influence the work of climate scientists, correct?

    So, my suggestion is that you encourage them to avoid making use of the methods, products and tools that I have significantly influenced over the years. They’re all questionable when it comes to climate science. So, please encourage the climate scientists to stop using computers, databases, geographic information and analysis systems for their work…unless they only use mainframes and punched cards :-) [I'd toss in digital telephones and laser printers as well, but that would be mean :-) ]

    In case you continue to read this posting despite my horrific lack of qualifications, I’ll answer your question a bit more directly: I am a generalist who chose a non-academic route through life. However, I’m hardly disconnected from the scientific arena.

    Meanwhile, back to you, George. What are your peer-reviewed credentials in statistics, seminumerical algorithms, field biology (several specialties), history and management of science, and data management practice? It would seem these are relevant topics to assessing work done in this subarea of climate science. If a reader lacks peer-reviewed expertise, how can they expect to evaluate the expertise of anyone else?

    Personally, I consider “real world” intelligence, education and experience to be just as valuable as rigorous academic analysis. My suggestion: let’s respect one another as intelligent people.

    I’ve said it before; I’ll say it again: what has surprised me no end is that some (climate scientists) have seen value in any of my “citizen science” work. Appreciated, not expected. Certainly doesn’t make me an expert.

  • fred // March 9, 2008 at 7:54 pm

    meltwater, it will help to get talk about different things differently.

    The hockeystick, MBH98 and subsequent papers, could be wrong. Decentered PCA could also be wrong. And it still could be warming due to CO2.

    You don’t have to accept MBH to be convinced by the arguments for CO2 driven warming.

    Then, the amount of this you say is 4 degrees. Well, it may be, but there are two distinct steps, one of which is more certain than the other. One is the 1.2 due to CO2 directly. The other is feedback loops.

    There is different evidence, and differently compelling evidence, for each.

  • TCO // March 9, 2008 at 8:30 pm

    13. How about the autocorrelation? How does that fit into an examination of training? Espeically training versus a broad uptrend period? Versus wiggle mathcing?

  • TCO // March 9, 2008 at 8:48 pm

    (response to (12)): Tammy take your time. I don’t think you should try to have all the answers before having a discussion. If you need time to go over things that’s fine. Also perhaps (impertinant of me, I know) discussion with the internet community will make you think of new things or re-examine some ideas. That’s all fine. No one expects an oracle. The tendancy to “on high professor teaching to adoring acolytes” attitude of the RCers is really annoying. I prefer the brutality of a Univ Chicago grad student of econ seminar.

  • TCO // March 9, 2008 at 8:53 pm

    14. WRT the actual experiment you ran, I didn’t quite get it all intuitively. Partially my fault, I’m sure. I guess, I agree that using the acentered method (for this set of data) allows a smaller choice of PCs. However, I really wonder if one should just use the data itself without all this separating into PCs stuff. I might have some more thoughts (more critical), but am having a hard time getting my head wrapped around what type of data input is reasonable as a test of methods, etc. What is circular. And what the impact of different scenarios of data (with/withouth MWP) would be if one were to have them. I guess at a certain point, I wonder if we are just pickiung the few series that show recent warming (cherry picking) and then by average, they oscillare around zero in the shaft portion of the stick. But I wander…

  • mmghosh // March 9, 2008 at 9:10 pm

    Mr Pete

    I think you have raised some important points.

    While many of us have some mathematical or statistical training at grad school level, I don’t think we can follow linear algebra or even PCA although I think HB has done a great job in explaining as simply as possible.

    All of us have a stake in this debate, though, as global warming and measures to combat them could affect our lives and pockets directly. So I think it is certainly the business of the experts to explain things to concerned laymen - more so than, say, the space program.
    I don’t think having specialised climatology experience is necessary to follow the debate, most of us can read the information in NASA, NCDC, HadCRU and follow the graphs.

    However, the whole apparatus of science, publication in peer-reviewed journals, international conferences, reviews and consensus documents are part of the standard academic processes is designed to provide the public the maximum guarantee that these subjects are debated among experts. In the same way that, say, it is difficult for us to follow medical debates. What I find interesting is the fact that otherwise scientifically minded laymen are willing to listen to the experts in other fields, but somehow reserve a level of vituperation and hostility to the science and scientists in this field, unmatched in other fields. And coupled to this is a strange eagerness to take the work of amateurs as being superior to the professionals.

  • Lazar // March 9, 2008 at 9:10 pm

    Spence_UK,

    Excellent points.
    I’ve read through the GRL paper, response to Huybers (again), and some blog posts.
    There are a few niggles…
    Steve McIntyre has not, to my mind, produced a head-on, convincing response to questions over the issue of persistence (e.g. here and here.)
    Secondly, and if MBH98 really did apply the Preisendorfer selection rule, then that must form part of the test… and I can’t see how one would reliably get ’simulated’ PCs past when comparing two eigenvalue spectrums from essentially the ’same’ source, red noise with the same properties, passed through the same procedure (decentred PCA), unless I’m misunderstanding Preisendorfer here.
    PC1 eigenvalues… I know Steve says they’re not important ‘coz variance is scaled, but there must, surely be some form of selection before that step even if it isn’t Preisendorfer.
    If those are non-issues, then I would agree that decentered PCA does indeed pass red noise through and fool the rest of the algorithm.
    I’ll assume Steve is right.
    Because it’s fun.
    Those are strong theoretical criticisms of MBH98.
    In practise do they matter?
    Use centered PCA and include PCs1-4, and the problem goes away, including issues regarding the benchmarking of RE.
    Or use no PCA.
    Dependency on bristlecones… use no PCA and no bristlecones, the ‘hockey stick’ shape remains over 1400-49AD but the RE scores are lower over the same period though still significant. Use centered PCA, exclude bristlecones, and use PCs1-2, and you get high temperatures in 1400-49, the ‘double-bladed hockey stick’, but scores fail over that period. However, over 1450-49 produces a flat hockey stick and good scores.

  • TCO // March 9, 2008 at 9:13 pm

    sharing of the data and method of your example. While I’m sire that some of the examination of what you did would be annoying or ven flawed, there is a possiblity of other insteresting things coming from it. Looking at type 1 versus type 2 errors.seeing how mehtod and data interact. Etc. etc. And at the end of the day, if it’s good neough to refer to as a toy example, it’s good enough to let people examine and see places where the toy example might be off. You should share the info. And you don’t need to worry about me. I’
    m lazy. I’ll just bug you with little master’s degree thesis questions every post or so…MWAHAHAHAH!

  • TCO // March 9, 2008 at 9:50 pm

    10.f (sorry, was drinking bloodies, forgot a Jolliffe point): Based on the references in the Jolliffe ppt, that presentation was made AFTER the MBH paper came out! Heck, it may have been influenced by the MBH paper and controversy surrounding it. In any case, it was not something that was public for Mann to look at, for reviewers, for readers, etc. WHEN MANN published! So it doesn’t help with the issue of unusualness of the Mannian acentric correction and with Mannian failure to cite and describe his method.

    You’re a physicist (I think). So a knuckle-cruncher example. When I do a conductivity measurement on a sample and write a paper about it, I cite relevant publications in the footnotes within the methods. I will say something like: “Conductivity was measured with the 4-point method using linear spring-loaded tips and a Keithley nano-voltmeter.” Correctional factors for pellet geometry were made from tables of Smits(fn), which uses the method of images to compensate for longer current paths through a finite thickness sample. Pellets were measured by hand using a micrometer and were assumed to be perfect cyclinders despite small warpage, estimated by eye to be less than 10%.” Actually…that’s a little loquacious. But I will cite the Smits paper. You need to see it to know that I did the work properly, that I did not assume a thin film configuration. Also, almost as important, you need to have that footnote, so that you can go out and do good similar science of your OWN. Not just so you can “second check me for mistakes”, but for promotion of proper procedures. Thirdly (related to the first reason) if someone finds some flaw with Smits (1958 Bell Technical Journal) in the future, it makes it easier to still get value out of my work. One may be able to put corrections for instance on top of my work. Important especially if I have not reported every raw form of data (I should, but let’s be real, some of it is in Excel and in lab notebooks).

  • Patrick Hadley // March 9, 2008 at 10:44 pm

    John Mashey, your questions are interesting but are Off Topic for this thread, which is about PCAs and the MBH hockey stick. You argued that the hockey-stick has “no importance for policy”, and in response I mentioned some areas where I thought the question of whether or not the hockey stick was a good representation of global temperature history still had the potential to influence policy makers. I tried to make my post pretty neutral, since I did not want to raise red herrings since this is not the thread on which to discuss those issues, but obviously I failed.

  • George // March 10, 2008 at 12:59 am

    Mr pete says:

    “So, my suggestion is that you encourage them to avoid making use of the methods, products and tools that I have significantly influenced over the years.”

    Thanks for the reply and being honest.

    It’s great that you have worked on computers, databases, geographic information and analysis systems and other tools used by scientists and I commend you for your contribution, but that is largely (if not completely) irrelevant to what I referred to above.

    I wanted to know what your expertise was in the climate science area that would allow you to assess the current state of climate science — in the particular “contested’ arena that you referred to or any other.

    With all due respect, having worked on computers (as have I and a significant fraction of engineers in this country) has no bearing whatsoever on assessing the state of climate science (in the “contested area or any other) — something that I was not the one doing, by the way (so my credentials are irrelevant)

  • TCO // March 10, 2008 at 2:04 am

    I suspect 95% of the commenters here do not hae a basis for making braod statements about the quality of climate science literature. I think you need to have read a lot of it before you can really do so. McI has done that and so has some basis to make such a statement. I do worry a but that he has a bit of a screw looose and that he has not done much peer reviewed work himself. I don’t think mpublication in climate is needed to judge the litareature. Part of getting a Ph.d. is acquirinng a skill that allows you to move to new fields to see where they aer weak or sttrong etc. And people all the time do this as they change workpalces and the like.

  • MrPete // March 10, 2008 at 2:54 am

    George, you misunderstood. I did not mean “worked on” computers. I meant, developed underlying mathematical tools for computation, analysis, data manipulation, analysis and management, that climate (and other) scientists typically assume are working well as they do their work. Not many engineers are familiar with the strengths and weaknesses of computation systems for retaining (or destroying) data integrity as it is mathematically processed.

    Read up on seminumerical algorithms sometime. As Bill Gates once said (only partly in jest), if you can make it all the way through Knuth’s books, give Bill a call — he’d like to hire you.

    I have a bit of experience in professional handling and analysis of quantitative data. Once you’ve addressed issues in a few dozen areas of science, business, medicine, etc… one more is not a big deal. I may not know the mathematical details (at least up front), but I do know what good work looks like, whether at the input, analysis or reporting stage. There’s more, but I’ll stop there.

    As for why I asked you — well, you expressed the sense that you could evaluate whether I’m able to assess the quality of scientific work. I’m suggesting it’s a bit hard to do that from a distance, no matter what measure is used.

    By your measure (which is not unusual, honestly I’m not picking on you :-) ), I’m actually unqualified even in my own arena: I have zero certifications and have only taken two computer classes in my life.

    To consider my background and experience irrelevant and insignificant for the issues at hand is no surprise. As I said earlier, the very nature of your query assured me of your perspective. You’re likely impressed by those who also measure significance by metrics that can be seen from a distance, rather than qualities that can be experienced in person. From that perspective, a lifetime of excellence and influence over science, business, etc has no meaning if not accompanied by the appropriate publications and accolades.

    In my experience, such measures are immaterial. I have had the privilege of great productivity, great influence, etc, all with an unlisted phone number, no advertising, and no acclaim. Try it sometime, it’s incredibly freeing :-)

    Enough of this; it’s really OT. This will be my last on qualifications and such. Any more can be taken to private email or some other venue.

  • MrPete // March 10, 2008 at 3:06 am

    mmghosh, you surfaced an important perspective: “I find interesting is the fact that otherwise scientifically minded laymen are willing to listen to the experts in other fields, but somehow reserve a level of vituperation and hostility to the science and scientists in this field, unmatched in other fields.”

    Let’s leave out the extremists (who hiss with vituperation and hostility.)

    Is this area of science in need of more remediation than most others? In my experience, when the published shenanigans in this subarea are shared with other scientists, leaving all the details out so as to avoid the “heat”… they tend to react with shock, disbelief, or sad laughter. The most mature response tends to be along the lines of “hey, it’s obviously a young science; they’ll eventually clean up their act.”

    If you have yet to see issues worthy of scientific shock and disbelief, I would suggest you have not yet learned to step away from the fray to look at it dispassionately.

  • Hansen's Bulldog // March 10, 2008 at 3:14 am

    I’m posting this to multiple threads. Things have gotten a bit out of hand. The level of hostility is … well … over the top.

    So I urge everyone to try an experiment. For you next comment, make the exact point you wanted to make, but leave the hostility at the door. I really don’t want to censor viewpoints. But as has been pointed out, too much insult not only turns people off, it interferes with communication. Meanwhile, it’s time for me to reconsider my moderation policy … because “moderation” doesn’t seem to apply.

    And please don’t send a comment saying it’s really my fault. I already know.

  • dhogaza // March 10, 2008 at 3:45 am

    Is this area of science in need of more remediation than most others? In my experience, when the published shenanigans in this subarea are shared with other scientists, leaving all the details out so as to avoid the “heat”… they tend to react with shock, disbelief, or sad laughter. The most mature response tends to be along the lines of “hey, it’s obviously a young science; they’ll eventually clean up their act.”

    I want proof. I want cites. I want specific quotes.

    You’re just another internet poster who, AFAIK, is just a random anti-science denialist hack.

    And you continue to post based on personal authority, without back up …

    So, who are those other scientists?

    What exactly are the “shenanigans”?

    If you have yet to see issues worthy of scientific shock and disbelief, I would suggest you have not yet learned to step away from the fray to look at it dispassionately.

    An argument from personal authority.

    Tch, tch.

    Meanwhile, it reached 16C today in PDX, and while the month has overall been warm, we’ve had some cooler days.

  • anonymous // March 10, 2008 at 3:55 am

    If the analysis of MBH were correct, I suspect long ago some professional academic statisticians would have backed them up. There is no downside for them to do so. They would not be picking a fight on a highly politicized topic with their colleagues in atmos or geo.On the contrary, they would be helping them. Yet I have not seen this to be the case. Where I am located Wegman is taken seriously by statisticians. Has any statistician publicly refuted his critique? It is
    very disconcerting to see climatologists continue to defend MBH without at least either finding serious statisticians to back them up or stating explicitly that the analysis they are doing is a new method, and justified by the following papers. I do not need to wade through the discussion here and at CA; I am unqualified to judge it professionally. However, many people are qualified and they are not backing up MBH, but rather remaining silent. It is a rather bizarre situation, really.

  • mmghosh // March 10, 2008 at 4:31 am

    I agree with HB. Thank you for your moderation.

    Part of the attraction of this site is the education that one receives.

    Mr Pete,

    I have plenty of experience with scientific disagreement, and I have been involved in several of them myself. The debate is between the scientists themselves. The point is that this particular debate is being carried out between scientists and laymen about issues which are not issues in science in general.

    I’ll just pick out some examples from the recent past on these threads - Q - is every single datum archived? A - No scientist in any field in my experience archives every single dataset. Q - Why is averaged data used? A - Scientists do it all the time. Q - Criticism based on not understanding the difference in baselines, or understanding what an anomaly is - commented on by HB in the past few posts. A - read up the subject before making basic errors.

    My point is that question of this sort are not made in other disciplines.

    Once again I have gone off topic. I apologise to HB and will comment only on the open thread.

  • EliRabett // March 10, 2008 at 4:48 am

    I think what HB has brought out very well is that people who think about physical systems view mathematics/statistics as a tool. This drives mathematicians/statisticians mad which is OK. Think of Feynman/Dyson, etc.

    I think that the point here is that given the data (and remember that Bradley and Hughes knew the available data, indeed they created a great deal of it), the non-centered PCA was the best choice.

    One more comment. Somewhere above someone claimed that one should choose the depth of the PCs that one will consider before doing the analysis. This is, well, auditory. What one should choose is the criteria for including a PC.

  • John Mashey // March 10, 2008 at 5:32 am

    Edward Wegman got it right:

    ‘As we said in our report, “In a real sense the paleoclimate results of MBH98/99 are essentially irrelevant to the consensus on climate change. The instrumented temperature record clearly indicates an increase in temperature.” We certainly agree that modern global warming is real. We have never disputed this point. We think it is time to put the “hockey stick” controversy behind us and move on.’

    http://energycommerce.house.gov/reparchives/108/Hearings/07272006hearing2001/Wegman.pdf

    They said it in the report that I studied, and then Wegman said again at the later hearing. This was July 2006. That’s about as clear as it gets.

  • Hank Roberts // March 10, 2008 at 5:53 am

    Wegman said it was less than an ideal approach, and that it was time to move on.

    Wegman also said he believed CO2 forms a layer in the atmosphere according to its weight.

    He was right about the conclusion, but he was wrong about his understanding of atmospheric physics.

    But he got the right answer anyhow.

    Time to move on. CO2 is well mixed.

  • fred // March 10, 2008 at 6:35 am

    There is really only one way of getting to the bottom of this thing for yourself. R is freely available to download for all operating systems, and (not speaking from experience yet) cannot be any more difficult than any other high level language or specialist application. So harder than Excel, but probably no harder than Photoshop. Haven’t fired it up yet, though.

    The best regarded introductory book seems to be Dalgaard “Introductory Statistics with R”.

    Another well reviewed introduction is Crawley “Statistics, an Introduction using R”.

    Verzani’s book is apparently the most basic intro. “Using R for Introductory Statistics”.

    There is a Springer text on time series analysis which Tamino probably knows and could comment on.

    And there’s a Cambridge title by Maindonald and Brain “Data Analysis and Graphics Using R: An Example-based Approach”, which has been well recommended to me to learn R with. Amazon reviews differ, some being very positive on it, others less so. Its not cheap.

    The great advantage if we were to do this, is we can very simply for ourselves actually do some PCA without having to struggle with setting the thing up in Excel or some other spreadsheet. Spreadsheets are fine in their place, but for this stuff I can’t see it, its too easy to make mistakes because you’re effectively programming your own statistics package. We can also see whether or not the MBH approach does produce hockey sticks from red noise, and verify all the other contentions.

    And we can get the debate onto a level where content and not insult will dominate.

  • fred // March 10, 2008 at 8:13 am

    meltwater, just to continue the issue of climate sensitivity. People usually say, when the issue of feedbacks is raised, that one is moving to something called denialism if one doubts the existence of positive feedbacks of the level needed to raise the temperature by 3 or 4 degrees.

    There are a number of papers (naturally from authors who were instantly then labelled denialists, if they had not already been!) which argue that the total sensitivity of global temperatures to a doubling of CO2 is around 1 degree. Maybe the most thought provoking line of argument on this comes from the observation that the preindustrial level of 280ppm has risen to the recent level of 380ppm. Because the effects of CO2 are not linear, a great deal of the warming from a rise from 280 to 560 must already have occurred. The percentage of the total rise will be greater than the percentage of the rise in CO2 that has already happened.

    So the counter argument is, lets look at how much it has warmed already for that rise, and use that to estimate sensitivity, plotting it on the log curve to allow for decreasing returns as indicated above. Several people looking at this have come to estimates of around 1 degree - which is actually sometimes less than the 1.2 degrees everyone agrees is injected simply from the CO2 effect.

    I don’t know if this argument is right or wrong, or exactly what it shows if its right, but it is not obviously silly or in bad faith. It is quite possible to look at this, accept the physics of CO2 heat absorption, but not be persuaded that it works out in the real world so as to produce sensitivity levels of 4 degrees.

    You don’t have to reject 200 years of science. Its a bit like saying, I know this car has x amount of energy in its tank. If it uses it to some level of efficiency, it should do 100 miles with it. But in fact, owing to the way it is constituted or driven, it may in fact do 50 or 150. This isn’t physics, it is empirical observation of all the various factors and how they work together.

    Motl has an article which summarizes the argument, though it then gets into solar, which is another and perhaps further fetched story. Motl of course is a denialist, which doesn’t shed much light on the argument one way or the other.

    http://lubos.motl.googlepages.com/cep-eng.doc

    Pielke has also argued that land use is a very important driver. Not saying any of these are right, just that reasonable people trying to get to grips with it can accept CO2 heat absorption, while not being convinced of the usual estimates of total climate sensitivity. It is a complicated subject and its quite wrong to think people who are half way through forming opinions on it are in some way bad, or in bad faith.

  • ChrisC // March 10, 2008 at 8:19 am

    Anonymous@10th March 3:55am

    Firstly, the 2006 NRC synethesis report into temperature reconstruction, which according to Pielke Jr. was a “near-complete vindication for the work of Mann et al.” included numerous statistians as authors. These include Prof. Peter Bloomberg, a professor of stats at North Carolina State University, Dr. Douglas Nychka, from NCAR. The relevant IPCC chapters also include various statistians.

    Secondly, Tamino/Hansen’s Bulldog _is_ a professional statistician. I would say this post is is backing up the MBH1998 analysis.

    People ARE backing up MBH, and have been for years. It helps to do some research before making claims such as “However, many people are qualified and they are not backing up MBH, but rather remaining silent.”

    Just as an aside, PCA and SVD are not used solely by statistians. I’ve used both in Signal Processing and physical modelling applications. The input of statistians into trivial applications of the techniques is often not required.

  • fred // March 10, 2008 at 9:18 am

    Couple more useful R sites:

    http://rss.acs.unt.edu/Rdoc/library/pcaMethods/doc/index.html

    the docs on the pca methods package.

    http://cran.r-project.org/other-docs.html

    quite a bit of free docs in pdf form.

  • Don Fontaine // March 10, 2008 at 12:55 pm

    I am one of the guys who sometimes uses the methods people like you invent. Would doing the analysis using nonmetric multidimensional scaling, rather than PCA, have eliminated some of the questions you have had to spend time refuting here? Since NMDS uses ranked data it doesn’t depend on the units of measurement. I suppose you could still subtract out different subsets of the data prior to the analysis creating questions about which choice is best. I learned of NMDS from PRIMER software from Plymouth Marine Laboratory (originally) http://www.primer-e.com/Primary_papers.htm.

  • George // March 10, 2008 at 1:19 pm

    I messed up the closing blockquote for the quote above

    TCO:

    “I suspect 95% of the commenters here do not hae a basis for making braod statements about the quality of climate science literature. I think you need to have read a lot of it before you can really do so.

    Agreed.

    He continues:

    McI has done that and so has some basis to make such a statement.”

    It’s not simply reading that is important.

    It is understanding.

    Does some guy with no background in dendrochronology who starts reading the literature in that area somehow immediately understand the issues better than those who have been working in the area for 30 years?

    Tell me another funny one.

  • Barton Paul Levenson // March 10, 2008 at 1:23 pm

    Mr. Pete posts:

    [[Funny how so many people want to “pretend” (your word, not mine) they’re making progress on climate change research but don’t talk about current data either. ]]

    And why do you suppose that is, especially in this blog? Could it be because you and your pals continually bring up MBH over and over and over and over and over again so that we have to spend most of our time countering your false statements and mistakes?

    You want to talk about the contemporary work? Go read through the last year’s worth of JGR-Atmospheres, J. Atmos. Sci., Monthly Weather Review and Icarus. Bring up a paper there you don’t like, and we’ll talk.

  • MrPete // March 10, 2008 at 1:30 pm

    dhogaza, sorry, I’m not going to do your work for you. I can turn on the lights, but you’ve got to follow the path for yourself. It would be a disservice to you to sit here and get into a big argument while spoon feeding you what is easily available. You need to value the issue enough to go find it. Step back, look at the best material available, assess what is said while ignoring the heat.

    Tamino’s concern about flame wars is well placed. To get past that, we need to develop a higher level of respect for one another. Part of that comes from trusting enough to then invest personally in digging out honest answers.

    [And no, I'll not draw my personal relationships into the public eye. I'm public (more than I'd like but it's wayyy too late), but privacy is valued by many of my friends. Yes, that means I'm limited to sharing "stories" in some cases, which obviously carry no scientific rigor. A limit I place on myself.]

  • Barton Paul Levenson // March 10, 2008 at 1:38 pm

    Patrick Hadley writes:

    [[If the MWP did exist then it would help (but obviously not prove) two arguments used by sceptics: that the world benefits from warmer temperatures; and that the recent rise in global temperatures is not unprecedented and therefore one cannot argue that just because warming has followed a rise in CO2 it must therefore be caused by this rise. ]]

    The latter point is a straw man which reflects a mistaken belief of AGW deniers, apparently including you — that AGW theory is based on some kind of statistical analysis of climate data. Apparently the idea is that scientists said, “Hey, CO2 is rising — and temperature is also rising! The CO2 increase must have caused the temperature increase!”

    No. Wrong. The prediction of global warming from increase CO2 is based on radiation physics. CO2 is a greenhouse gas; John Tyndall proved that back in 1859. That means that the more of it you have in an atmosphere, the warmer the ground is going to get, all else being equal. To avoid it there would need to be some kind of countervailing process, and nobody has been able to find one sufficient to prevent a rise of several degrees this century. Lindzen tried with his “tropical infrared iris” idea, but satellite observations shot that down. Note, by the way, that Lindzen’s denialist argument here was a real scientific hypothesis, that it was accepted by a journal, and that it was rejected simply because empirical tests falsified it.

    If it were somehow proved that the Medieval Warm Period was global, rather than largely confined to Europe, it would not disprove AGW theory at all. It would simply indicate that some other factor back then must have been large enough to cause a huge worldwide temperature anomaly. Maybe the Earth’s albedo was lower then, due to all the sprays of blood from sword-fighting.

  • luminous beauty // March 10, 2008 at 2:12 pm

    anonymouse,

    Wegman was correct as far as he went. Having no knowledge of the nature of the data, one cannot tell a mechanical correlation from a spurious one. If he had bothered to inform himself on the hundred years of research done validating the data, he might have made a different conclusion.

    It was not what Joe Barton asked him to do.

    It is not really a question of statistics. It is a question of whether tree-ring growth has a causal, non-probabilistic relation to climate variation.

    It does. The various ‘divergence’ problems don’t contradict this long established science, but rather suggest, since the mid 20th century, the planet is going through a climatic shift.

    Most professional statisticians don’t work in the physical sciences, but fields like economics and sociology where the data are often, if not typically, probabilistic, and in which causality is infinitely more difficult to determine than in the physical sciences.

  • fred // March 10, 2008 at 2:22 pm

    “CO2 is a greenhouse gas…. That means that the more of it you have in an atmosphere, the warmer the ground is going to get, all else being equal.”

    This is not true, as a matter of science, for two reasons. First that as CO2 rises, incremental rises have diminishing warming effects. The curve is logarithmic. It is not true that the more you have of it the warmer it gets in any unqualified sense.

    Second, because CO2 warming in itself is about 1.2 degrees. What produces the rest of the warming is the alleged amplification of the initial warming.

    The statement makes the whole thing seem much simpler and more certain and one dimensional, and susceptible of simple evidential proof, than it really is.

  • Hank Roberts // March 10, 2008 at 2:45 pm

    > alleged

    See, this is why it’s hard to discuss current science. The old lack of understanding keeps being reiterated.

    Lawyer language, yet.

    Waster of time.

  • Martin Vermeer // March 10, 2008 at 2:46 pm

    This is not true, as a matter of science, for two reasons. First that as CO2 rises, incremental rises have
    diminishing warming effects. The curve is logarithmic

    Well, we got this far. Do you know what a logarithmic curve looks like? Don’t you agree that it goes monotonously up?

    …and by the way, what in “all else being equal” exceeded your power of comprehension?

  • dhogaza // March 10, 2008 at 2:53 pm

    I’m not going to do your work for you. I can turn on the lights, but you’ve got to follow the path for yourself. It would be a disservice to you to sit here and get into a big argument while spoon feeding you what is easily available. You need to value the issue enough to go find it. Step back, look at the best material available, assess what is said while ignoring the heat.

    More handwaving from Mr. Pete.

    Without specific information, I’m afraid I’m going to have to rely on the IPCC reports. Nothing I see there supports your statement that climate science is in a laughable state, and that other scientists who look at the field believe it to be laughable.

    You really think I’ll consider someone who considers CA to be a reliable source to be a reasonable judge as to the state of climate science?

    You do write with a clear, arrogant, condescending style that I imagine you believe masks the fact that you rarely say anything of substance. Doesn’t work with me, sorry.

  • Ian // March 10, 2008 at 3:09 pm

    fred,

    You mentioned papers arguing that “total sensitivity of global temperatures to a doubling of CO2 is around 1 degree” - were you thinking of Stephen Schwartz? If so, have a look at James Annan’s take on it (I found his criticisms apt and convincing): http://julesandjames.blogspot.com/2007/08/schwartz-sensitivity-estimate.html .

    In short, Schwartz has a couple of calculation errors and a strange assumption of a 5-yr fixed climate response.

    If this is not what you meant, then when looking at the amount of atmospheric warming so far, are you factoring in that the oceans have kept atmospheric temp from rising as much as it would have in their absence?

  • P. Lewis // March 10, 2008 at 3:26 pm

    fred

    To a first approximation for CO2 forcing, Delta(F) = a ln(c/c_{0}), where Delta(F) is the change in forcing, a is a constant (value unimportant here), c is CO2 final concentration and c0 is CO2 initial concentration. Plug some figures in for, say a doubling of CO2 from 100 to 200 ppm, 150 to 300 ppm, 200 to 400 ppm, 250 to 500 ppm.

    Actually, you should be able to do this in your head, because it doesn’t really matter what the actual result is for this illustration.

  • George // March 10, 2008 at 3:33 pm

    Fred says

    This is not true [that "the more of it you have in an atmosphere, the warmer the ground is going to get, all else being equal.”] as a matter of science, for two reasons. First that as CO2 rises, incremental rises have diminishing warming effects. The curve is logarithmic. It is not true that the more you have of it the warmer it gets in any unqualified sense.”

    Actually, Fred, is is strictly true that “the more of it [GHG] you have in an atmosphere, the warmer the ground is going to get, all else being equal.”

    To say that the ground gets “warmer” just means its temperature goes up. It says nothing at all about how it goes up with increasing concentration of GHG’s — exponentially, linearly, logarithmically etc.

    “Logarithmic warming” with GHG concentration increase is still “warming”.

    Though the amount of warming (temperature increase) for a given incremental increase in GHG concentration does diminish as the concentration increases (as you correctly point out), as long as the concentration continues to increase, so does the warming (all else being equal).

  • Gavin's Pussycat // March 10, 2008 at 3:33 pm

    fred:

    Because the effects of CO2 are not
    linear, a great deal of the warming from a rise from 280 to 560 must already have occurred. The percentage of
    the total rise will be greater than the percentage of the rise in CO2 that has already happened.
    So the counter argument is, lets look at how much it has warmed already for that rise, and use that to estimate
    sensitivity, plotting it on the log curve to allow for decreasing returns as indicated above. Several people
    looking at this have come to estimates of around 1 degree - which is actually sometimes less than the 1.2
    degrees everyone agrees is injected simply from the CO2 effect.

    Yes, this has been studied. If you do it properly, you have to take into account that the ocean takes up a large
    amount of the greenhouse energy imbalance, slowing down the observed warming. For sensitivity you have to look at
    equilibrium warming, i.e., the (hypothetical) temperature reached after the ocean has had time to warm up as
    well.

    Let’s do that: we observe some 0.7 deg C for 385 ppm, i.e., 1.375x pre-industrial, the 2log of which is 0.46.
    The sensitivity to doubling is then 0.7/0.46 = 1.5 deg C.

    Now take the ocean heat storage into account. According to most studies, some 0.6 deg C is “missing” from the
    observed 0.7 deg C, most of it on the Southern hemisphere where the oceans are. Equilibrium heating would be
    0.7 + 0.6 = 1.3 deg C (BTW don’t mix this up with your 1.2 deg doubling sensitivity. Apples and oranges. Just in
    case.) Now we get a doubling sensitivity of 1.3/0.46 = 2.8 deg C.

    (Did you read the article on RC on Antarctica recently? Discusses also this issue:
    http://www.realclimate.org/index.php/archives/2008/02/antarctica-is-cold
    )

  • Luke Silburn // March 10, 2008 at 3:35 pm

    Fred quoted Barton:
    “CO2 is a greenhouse gas…. That means that the more of it you have in an atmosphere, the warmer the ground is going to get, all else being equal.”

    and then said in reply:
    “This is not true, as a matter of science, for two reasons. First that as CO2 rises, incremental rises have diminishing warming effects. The curve is logarithmic. It is not true that the more you have of it the warmer it gets in any unqualified sense.”

    Sorry, what? How does a logarithmically-declining warming effect mean that ‘the more you have of it the warmer it gets’ becomes an untrue statement?

    Regards
    Luke

  • luminous beauty // March 10, 2008 at 3:54 pm

    fred,

    Once again. The uncertainty in feedback response goes both ways. The likelihood that it is less than the agreed mean value from several methods of calculation is the same that it is greater.

    One cannot honestly argue for one direction of uncertainty without simultaneously arguing for the other, given you have no physical reason for doing so.

  • elspi // March 10, 2008 at 3:54 pm

    Fred brings the stupid:
    “The curve is logarithmic. It is not true that the more you have of it the warmer it gets in any unqualified sense.”

    Fred, the log is a strictly increasing function.
    Therefore, IT IS TRUE THAT THE MORE YOU HAVE OF IT THE WARMER IT GETS.

    Furthermore fred, the part of the function that we have witnessed in the modern era is very close to being linear.

    Venus, on the other hand, has the property that any additional CO_2 will not change things much. (The point being that the concentration is so high that the curve is almost horizontal)

    If it ever gets to that point on Earth, we will all be WELL DONE anyway.

    Also there is a feed back loop. It see how it works, try opening a can of soda at 120F.

    How much simpler could it be?

  • Nick Barnes // March 10, 2008 at 4:37 pm

    fred:

    This is not true, as a matter of science, for two reasons. First that as CO2 rises, incremental rises have diminishing warming effects. The curve is logarithmic. It is not true that the more you have of it the warmer it gets in any unqualified sense.

    Um, yes it is. A logarithmic relationship is still monotonic. “The more [...] the warmer [...]” describes any monotonic relationship. The more you press on the accelerator of a car, the faster it goes. Not linear, but monotonic. The higher a mountain you climb, the thinner the air is. Not linear, but monotonic. The louder the denialists shout, the flimsier their arguments. Not linear, but monotonic.

  • luminous beauty // March 10, 2008 at 4:52 pm

    fred,

    The last time I looked at a logarithmic curve, the abscissa value continues to increase as the ordinate value tends to infinity. It is only the rate of increase that goes down.

  • chriscolose // March 10, 2008 at 4:57 pm

    I finally have a more detailed of the greenhouse effect here, and a second part on the runaway and anti greenhouse effects in Part 2. http://chriscolose.wordpress.com/

    CO2 is a greenhouse gas. CO2 WILL warm the surface. The logarithmic relationship in absorption is already accounted for when people say that its doubling will result in x amount of warming. The best constraints on climate sensitivity clearly show around 3 C (such as work on the LGM). It is not true that we should have gotten most warming already, and you can work out that the rest of the way to 560 is nearly the same RF as what we got so far. In addition, you still need to consider positive feedbacks, the fact climate sensitivity applies only at equilibrium and so we still have more to go, and the fact that aerosols have offset warming. Getting climate sensitivity over the last few decades is not a great idea, but the rise so far clearly indicates a sensitivity beyond the planck response. It is true you need positive feedbacks to get to 3 C, but these are not just “alleged.” There is subtantial evidence to back their existence.

    Gonig back to this topic, I am really not sure it matters much anymore. The comments that a MWP being warm shows that warmth is a good thing is nonsense on several grounds. For one thing, small amounts of warmth have shown to be disastrous to many cultures (see the drought effects on the Mayans). I suppose the fact that Viking agriculture faired a bit better in Greenland is a sign that the world will be a much more prosperous place, but that is not the best global indicator. Next, a lot of conditions are different today such as the amount of infrastructure and people on the coasts, popualtions, etc. Finally, the temperature projections don’t stop at 2008, they keep rising. So, what we are gonig to get could potentially make current warmth (or medieval warmth) quite small. It should not be too hard to think that getting 3 C in 100 years can have large consequences.

  • RomanM // March 10, 2008 at 5:07 pm

    So far it appears that the discussion on the use of uncentered “PCs” as a statistical procedure you and your supporters have been advocating their use through arm waving that it was a perfectly good and valid technique which does exactly what one wants it to do. But no one has offered any evidence to support that claim other than vague references to their statisticians knowing more than someone elses statisticians. So I decided to do some investigation for some facts. However, I think some explanation of how things work in mainstream statistics might be in order for some of your readers. If someone produces a new methodology or statistical procedure, they first specify all of the assumptions that are needed for the data or situation where the procedure will be applied. Then, under those assumptions, they derive the properties of the results showing, as the
    case may be, that the results are unbiased for what is being estimated, what impact the randomness inherent in the situation may have, determining optimality of results, etc. If the assumptions are reasonably satisfied and if the procedures are followed as set out, then you know how to interpret what you get at the end of the procedure. Should someone alter the assumptions or change the procedure in any way, it is incumbent on them to provide clear evidence that either the procedure
    still works as before or to derive new results that incorporate the changes. Any modifications not supported by such evidence would be considered invalid.

    I found a book on Principal Components on the web and did some reading on centered and uncentered “PCs”. On p. 392 of this book I ran across some interesting statements:

    “(i) the columns of X are left uncentred, that is xij is now the value for the ith observation of the jth variable, as originally measured;

    (ii) both rows and columns of X are centred, so that sums of rows, as well as sums of columns, are zero.

    In either (i) or (ii) the analysis now proceeds by looking at linear functions of x whose coefficients are the eigenvectors of X’X, with X now non-centred or doubly centred. Of course, these linear functions no longer maximize variance, and so are not PCs according to the usual definition, but it is convenient to refer to them as non-centred and doubly centred PCs, respectively.

    If the data are such that the origin is an important point of reference, then this type of analysis can be relevant. However, if the centre of the observations is a long way from the origin, then the first ‘PC’ will dominate the analysis, and will simply reflect the position of the centroid.”

    There are several things that seem to be relevant to the issues here. The first is that “uncentred PCs” are in fact NOT PCs although some people may still refer to them as such. The author actually refers to centering at the origin, but the same observation applies to centering at any other chosen point as a new origin. Because this is a drastic change to ordinary PC thory, the procedure needs genuine justification for the results to be interpretable in any meaningful fashion. It also means
    that eigenvalues no longer are measures of “explained variability” and methods of choosing the number of eigenvectors (not PCs) are also not applicable. The author of the book (oh, did I mention the title - Principal Component Analysis by Prof. I.T. Jolliffe) does not seem to give any references to this technique from the mainstream statistical literature. I presume that he would have done so had such references existed.

    The last part of the quote relates to the hockey stick. He does say that if the origin is meaningful then “this type of analysis can be relevant”. Whether centering at an arbitrary interval in time over a short range of the data is “an important point of reference” is certainly questionable. But the important issue is that if the center chosen is far from the average of the entire data, the first eigenvector will dominate the results as a function of that diference.

    What does this mean exactly? Let’s do a little math. I’m sure that you will correct me if I make an error - it’s been known to happen. What effect does choosing another centre other than the average have on the matrix which is used to determine the “PCs” for the Tamino example and the MBH data. If I understand the centering procedure correctly, a little algebra says that you can get that matrix by starting with the ordinary covariance matrix of the data and then inflating values on the diagonal by adding (basically) the square of the difference between the average of the variable in the section chosen for the centering and the average over all of the variable’s data. This means that variances” of variables which have past values simiar to the present will not be altered. However, the corresponding terms for variables whose earlier values are much lower (or much higher) than present (including hockey stick proxies) will increase by possibly large amounts. The “covariances” will
    also change but that will tend mainly to increase the size of first eigenvalue. As you well know, an eigenanalysis of a covariance type matrix puts a heavy emphasis on those variables whose “variances” are larger and a much smaller weight to the others. The net effect is to pick out the HS - not because it is necessarily the right answer - but, because the altered mathematics of the situation does so automatically, right or wrong. On the other hand, any proxies that might indicate
    that the past and present are similar will receive a much smaller role in determining the PC because of the center chosen. This is what Prof. Jolliffe referred to in the last part of the above quote.

    Does Prof. J. advocate the use of this methodology? A quote from his powerpoint on To Centre or Not to Centre:

    “Standard EOF analysis is (relatively) easy to understand – variance maximisation

    For other techniques it’s less clear what we are optimising, and how to interpret the results

    There may be reasons for using no centering or double centering, but potential users need to understand and explain what they are doing”

    Sounds lukewarm. Indeed, users DO need to understand the effects of AND EXPLAIN what they are doing and not present it as a magic black box.

    [Response: I'd say there are some minor errors here -- the first which springs to mind is that non-centering effects more than the diagonal elements of the covariance matrix -- but they're simple misunderstandings which don't alter the fact that you've put your finger squarely on some of the important issues involved. I'm not saying I agree (or disagree), but you have focused attention on some places where it actually belongs.

    I really do want to contribute to understanding of those issues, but it's pretty clear by now that they're complex enough to deserve more than just a response to a comment. That's why (as I stated earlier) I'm planning yet another entry in the series, on non-centered (no longer really PCA) PCA in general. But there's more to life than PCA and hockey sticks, so I'm not changing my plan to do a sea level post first. Also, a member of my wife's immediate family has passed away (he lived a long, good life and "died with his boots on" so it's not as tragic as it may seem) which takes more of what may be the most valuable quantity of all -- time -- so I'll have to ask readers to stretch their patience a little further.

    I'll also say that commentary at one point became rather contentious, then got downright nasty, but has now begun to focus more clearly. We might actually be making some progress.]

  • RomanM // March 10, 2008 at 5:09 pm

    Sorry about the format of the previous post. I pasted it from Notepad and it came out as poetry! Can it be fixed?

    [Response: *mostly* fixed.]

  • Hansen's Hamster // March 10, 2008 at 5:11 pm

    “Um, yes it is. A logarithmic relationship is still monotonic. “The more […] the warmer […]” describes any monotonic relationship. The more you press on the accelerator of a car, the faster it goes. Not linear, but monotonic. The higher a mountain you climb, the thinner the air is. Not linear, but monotonic. The louder the denialists shout, the flimsier their arguments. Not linear, but monotonic.” Hmmm… is this thesis peer reviewed?

  • caerbannog // March 10, 2008 at 5:23 pm

    Just a question for the hockey-stick auditors. When are you going to wrap up your auditing of Mann’s nearly decade-old reconstruction and turn your attention to the more recent reconstructions that roughly agree with Mann’s original work?

    [Response: How many roads must a Mann walk down, before they call him a Mann ...

    (apologies to Bob Dylan)]

  • RomanM // March 10, 2008 at 5:35 pm

    Thank you for fixing the initial post.

    My comment that “the “covariances” will
    also change but that will tend mainly to increase the size of first eigenvalue. ” is exactly an agreement with you that the off diagonal elments are affected as a product of the two differences between centre and mean for the two variables involved.

  • Gavin's Pussycat // March 10, 2008 at 6:03 pm

    One more comment. Somewhere above someone claimed that one should choose the depth of the PCs that one will consider before doing the analysis. This is, well, auditory. What one should choose is the criteria for including a PC.

    Wasn’t it simply “if the result changes significantly if you include more, you should include more”?

  • dhogaza // March 10, 2008 at 6:05 pm

    I’ll also say that commentary at one point became rather contentious, then got downright nasty, but has now begun to focus more clearly. We might actually be making some progress.

    Not really. They’re just over at CA engaging in scientific arguments like … name-calling. Yes. That seems to be the major rebuttal to your post and your follow-ups. Calling you names apparently proves you wrong.

    [Response: I'm not surprised if *they* aren't making progress. But I hope that *we* are. And "we" doesn't include "them."

    As for calling me names ... the more time and effort they waste doing that, the less they have to work other mischief.]

  • Hank Roberts // March 10, 2008 at 7:08 pm

    They don’t need to work at trolling if you go there looking. That’s a monkey-jar trap. Eschew!

  • MrPete // March 10, 2008 at 7:51 pm

    dhogaza, I’m surprised I need to say this. Look at the stated purpose of IPCC. The reports are only scientifically “robust” to the extent that the reported science is in line with the (political/policy) purpose of IPCC. Y’gotta dig deeper than IPCC to get a good scientific picture. IPCC will not publish anything out of line with their defined purpose.

  • luminous beauty // March 10, 2008 at 8:17 pm

    “If the data are such that the origin is an important point of reference, then this type of analysis can be relevant. However, if the centre of the observations is a long way from the origin, then the first ‘PC’ will dominate the analysis, and will simply reflect the position of the centroid.”

    Is it important that Mann’s reconstruction is calculated beginning with the most recent data and working back in time?

    One might think.

  • John Mashey // March 10, 2008 at 8:28 pm

    HB: this is a great series.

    When you do part 5, might you consider talking some about uncertainty, error bars, etc? It’s clear that lots of people don’t seem to understand what they mean in such reconstructions or in general.

    Personally, although I understand the lure of a compelling graphic when trying to summarize material for a general audience:

    MBH** had lots of caveats and clear (& substantial) error bars:
    http://holocene.meteo.psu.edu/shared/articles/mbh98.pdf, http://www.ncdc.noaa.gov/paleo/pubs/mann_99.html
    Eyeballing these, I’ll admit I don’t understand why the pre-1400AD bars aren’t bigger, but I don’t care much.

    The IPCC TAR, Fig 2.21 had several reconstructions, and the AR4’s TS.20 has even more, and AR4s section 6.6 even more.
    http://www.ipcc.ch/pdf/assessment-report/ar4/wg1/ar4-wg1-chapter6.pdf

    My take was that the original MBH’s were heroic early attempts to extract signal from noisy, minimal data, and a bunch of years of studies have been close enough [Fig 6.10 of AR4, p467 in printed version.] that’s exactly what I’d expect experimental studies to look like. I’d be *astonished* if they all came out with the same line and tiny error bars.

    re: Wegman
    Wegman is clearly a world -class statistician, but cannot be accused of overly-favoring Mann & co, so when I say he got “it” right, I meant the part I quoted. (”move on”) He clearly got other things wrong, as statisticians sometimes do when they get outside their own turf. Statisticians are always niggling at others for not using statistics right, but there are not enough statisticians around for there to be one looking at every single paper in the world upfront, especially in universities, but even in the old Bell Labs, where we had *awesome* statisticians like John Tukey and Joseph Kruskal. if you wrote a paper for external publication, it had to be reviewed by 2 divisions outside your own. Guess where papers with serious stat in them went? Did people learn to check out anything tricky with them first? (yes) And people did lots of approximate”back-of-the-envelope” stat, which was often good enough.

    Tukey wrote:

    “Far better an approximate answer to the right question, which is often vague, than an exact answer to the wrong question, which can always be made precise.”

  • cce // March 10, 2008 at 8:42 pm

    Re: Support from statisticians

    Everyone should listen to the NRC Panel press conference. Because until something major comes around that changes things, they will be the final word on these issues, not Mann, McIntyre, Wegman, or Tamino.
    http://video.nationalacademies.org/ramgen/news/isbn/0309102561.rm

    This is from statistician Peter Bloomfield:
    “Subsequent work has carried out very similar analyses with principal components replaced by much simpler methods like simple averaging and has arrived at essentially very similar reconstructions. So the committee reviewed that and other statistical issues that had been identified in that first analysis and while finding that the issues are real but that they had a minimal effect, not a material effect, on the reconstruction.”

    “[Mann et al’s methods] were all quite reasonable choices. I think in some cases a lot of subsequent, hard work by others in following up on that have showed that some of those choices could have been made better, but they were quite plausible at the time. I would not have been embarrassed by that work at the time, had I been involved in it and I certainly saw nothing that spoke to me of any manipulation or anything other than an honest attempt at constructing a data analysis procedure.”

  • dhogaza // March 10, 2008 at 9:54 pm

    MrPete …

    The Intergovernmental Panel on Climate Change (IPCC) was created in 1988 by the World Meteorological Organization (WMO) and the United Nations Environment Programme (UNEP) to “assess the scientific, technical, and socio-economic information relevant for the understanding of the risk of human-induced climate change.”

    Nothing there to support your claim of predetermined results of the assessment process.

    This:

    The reports are only scientifically “robust” to the extent that the reported science is in line with the (political/policy) purpose of IPCC. Y’gotta dig deeper than IPCC to get a good scientific picture. IPCC will not publish anything out of line with their defined purpose.

    is simply false if your claim is that their “defined purpose” is to promote the AGW hypothesis.

  • MrPete // March 10, 2008 at 10:16 pm

    cce, why should scientists be paying attention to a press conference?

  • TCO // March 10, 2008 at 10:44 pm

    George:

    Part of getting your Ph.D. is getting the balls and experience to move into alternate fields. I have done it in psych and econ and alternate science fields. Not every person can do that well…but many scientists can.

    I’m not so sure about McI. I think he has some fundamental problems in terms of fairness and disaggregation and organized presentation. So you have to tak him for what he’s worth. I think he does surface interesting questions.

    I know a lot of people here on both the right and left are more interseted in winning the war. And that’s fine. It could be an important war. But I’m more interested in intellectual curiosity. And in an occasional trollish blogfight. And drinking and eating.

  • TCO // March 11, 2008 at 12:01 am

    Tammie:
    A. Sorry about your wife’s male rel. You are my favorite lib. Pretty cool and fair for an alarmist. Actually rab is ok too. Well you know…smart for a marine. ;)

    B. Actually very cool of you to engage RomanM. good on ya man.

    C. buncha other comments, but I don’t feel like rebutting the Groundhog like arguments of others.

  • per // March 11, 2008 at 12:05 am

    joliffe’s powerpoint shows several ways that PC analysis can go wrong, and offers no specific comment on MBH or MM. It does finish with a clear admonishment that users of non-centred PCA must “explain what they are doing”. One wonders how Tamino would apply this advice to MBH, who didn’t even write in their original methods that they were doing non-centred PCA.

    It is fascinating to see Tamino berating Wegman (http://www.galaxy.gmu.edu/stats/faculty/wegman.html). Strangely, when Gerry North, chair of the NRC review panel, was asked to comment on the wegman report, he said that the findings of the wegman and NRC panels on the statistical issues were very similar. Why is it that eminent scientists agree with Wegman ?

    Tamino himself points out that the non-centred pca pushes the spurious PC to be more prominent, and says this is the point. MBH’98 specifically emphasises that their PC1 is the dominant component of variance. It certainly takes the shine off when you admit that the “dominant component of variance” is an artefact of your analysis method.

  • elspi // March 11, 2008 at 12:31 am

    per brings the stupid^2

    “Tamino himself points out that the non-centred pca pushes the spurious PC to be more prominent, and says this is the point.”

    Actually he said that the non-centered pca pushes the temperature signal PC to be more prominent, which, for the non-short-bus crowd,
    is indeed the WHOLE POINT.

    In his example, the non-centered pca is better than the centered pca, just as it was in MBH98.

  • cce // March 11, 2008 at 1:00 am

    MrPete,

    Scientists are free to do what they will, but it would be wise for the public to listen to the NRC Press Conference and keep in mind their findings the next time someone tries to tell them “the Hockey Stick was broken by the NAS” or “the Hockey Stick is bad science,” or “no one supports Mann” or similar falsehoods.

  • TCO // March 11, 2008 at 1:09 am

    I read the McI posting. A translation:

    Para 1: no math/science content. Quote whining, expressed in a pompous manner.

    Para2: no math/science content: Blathering about the context of literature. APomctually here, I agree with his point against Tammy and perhaps Tammy starting to as well.

    Para3: Pompously expressed but probably has a point about the Mann lack of description of methods. Not really math/science.

    Para4: Basically a math/science point here, but still one that cuts both ways and at times shows McI to be sophistic (for instance he will complain about aspects of methodology as independant errors, yet refurse to show that they are compensated for or that they do not actually cause the effect alleged (acting singly).

    Para5: Some science content here. Some disorganized mixing of issues. The explanatory point on temp and proxy PCs…is explanatory. There is a later bit of kitchen sink excusism (that is not proven) wrt precip series. The point about time dependance is fundamentally interesting, but not well developed.

    Para 6: A really, really long meandering nonsequitery para. I think you could boil it down from 8 lines to 1: “Mann’s code shows that he used rule N with temp data.”

  • TCO // March 11, 2008 at 1:19 am

    Para 7: Another overly long para that could be boiled down to “Preisendorfer” is a good ref. Not sure that that is earth-shaking, but at least the para is slightly more readable, slightly less pretentious.

    Para8: An interesting point is buried in here. I sorta notice the same thing with Jollife: that climate PCA is usually concerned with some sorts of wave like looking patterns across regions. Not sure how this differs with MBH, if there is some stochastic to continuous issue…or some difference in z’s of interest (in one case caring about the regional look and using methods to look at that, and in another honed in on a global average and perhaps not needing same methods).

    Para9-11: If the “purpose of the post is not to discuss short centering”, why does he do so? Such meandering is p….ompous. However the points made and the quotes from Presie are quite relevent. A small nit is that “not centering” is not well differentiated from short centering.

  • TCO // March 11, 2008 at 1:31 am

    Para 12: Interesting, reasonable point per se…but inserted in isolation. It means something to a general argument (strained one) that McI likes to have about what is “conventional”. In any case, as it’s put in isolation, with no development even to the usual arguments, it serves no purpose. In addition, I really wish he would move beyond this tendancy to try to prove himself right versus really fairly examining correlation versus covariance. I learned about this much better and more fairly by reading medical stuff on the web. Looking only at the McI defenses, would not well explain to one when to use corr and when cov. (He gets so wrapped in rhetoric, that he misses science explanation and intuition.)

  • MrPete // March 11, 2008 at 1:38 am

    elspi, what’s interesting here is how “better” is determined. Only analogy that comes to mind right now, and this is obviously stupid and simplistic yet perhaps good for us peanut gallery folk:

    “round(avg(max(1,5,3,4))) is better than max(round(avg(1,5,3,4))), because it better fits the reference value (which is 5).”

    Both methods are valid ways to use the functions. Unfortunately, the example is silly because there’s no physical theory supporting either formula. And that’s why fitting sample data to reference data is not enough. One must have a physical basis for the analysis method.

  • Spence_UK // March 11, 2008 at 1:47 am

    Lazar, many thanks for the reply, raising further good points. I may be a little rusty on some of this stuff, although your questions are helping to remind me of some of it!

    With regard to the AR1 significance, yes the outcome was significant (albeit only just, but significance is a pass/fail anyway) using the original test applied by Mann (for which, I believe, example Scree plots exist). However, it is true that the analysis conducted by Ritson does tend to suggest that the AR1 model is not a good one. But the model applied by McIntyre was the same one used by Mann in the original study - so if you argue that McIntyre’s method is inappropriate, then you are arguing that Mann’s method is inappropriate. Sounds like a thorny issue from both sides! Ironically, I believe the signficance occurs because the standard statistical test doesn’t really work properly for short segment decentred PCA, because the mathematical properties are not well understood…

    That said, there are still other compelling reasons not use decentred PCA (in addition to the statistical significance). I discussed the reasons I felt the selectivity would be compelling to the regression step, but I did not define the mathematical relationship that leads to this, which I think is worthwhile.

    Beforehand, a brief non-controversial example. If I were to try to estimate temperature from a large set (say 1000 time series) of noisy data with long histories, I could just average, or I could select the 100 that best correlate with instrumental data in recent times. As with any other form of selectivity, this could affect the significance requirements of my results, which would become more demanding. If the goal of my study was to prove that my long histories correlate well with the instrumental record, such a selectivity step would be a disaster because it would insert my conclusions into my assumptions.

    So, what of the selectivity imposed by short segment decentred PCA? For the AD1400 step, the “variance” will be inflated in relation to the difference between the 1400-1901 mean and the 1902-1980 mean. Now, firstly, I would like to see an a priori justification of this selectivity; secondly, I would doubt any conclusion related to the relative temperatures of these periods based on an algorithm that contained such selectivity.

    To me, the three reasons (inflated significance requirements, unjustified selectivity which impinges on conclusions, poor mathematical understanding of consequences) are good enough cause to drop the short-segment PCA. The persistence issue you raise is a valid point, but I would be deeply uncomfortable arguing a modern-medieval temperature relationship based on the remaining assumptions.

    OK, so if we say - let’s assume uncentred PCA is the better way to go until a better argument is put forward for its case. You raise some interesting points on the uncentred PCA case, but I’ve waffled on enough for now - maybe I’ll address these another time. Meanwhile, I would draw your attention to the most recent post at CA which discusses PC selection, which acknowledges one of the loose threads you highlight.

  • TCO // March 11, 2008 at 1:51 am

    para 13-14: seems like decent stuff, although not developed to a complete point.

    Para 16-18: good point on use of PCA for exploration of spaces vice as a method of processing. I would like to see a fuller description on the concept of PCing and throwing away and then model buliding on that versus just doing regressions.

    Para 19-20: This part is a bit slick here. He is correct that the under N PCs are not gauranteed to be significant (even the first is not). However, I’m not sure how that relates to an argument of truncations (where a more conservative approach is to include more…actually to the extent of not even doing PCA and just doing MC.) Also, at this point, the continued references to source materials (appeal to authority) rather than demonstration of points by math itself, starts to drag.

  • TCO // March 11, 2008 at 2:15 am

    21-22: nice explanatory science content. Although all agree that not much turns on it. the vieled kvetching against correlation matrix is mildly off, but again…little turns on it.

    23-26: Actually a pretty interesting detail-type point about what the meaning of “rule N” is. apparently Mann did not exactly use what was out of Priesie or if he did, did not show the validation study to show his thumbrule rationale.

    27: bit of non-disaggregation here. there is a methodology issue here…and a data issue. And McI just can’t seem to get his head wrapped around the 2 by 2 matrix comprised of right/wrong for both method and data separately. It’s just a mental block with him. Probably comes from never having done designed experiments, full factgorials, etc.

    28-29: some blathering about “moved goalposts” where McI fails to appreciate that it’s not the time basis of when he complained about things, but that he tends to confound things and tries to have one potential flaw take the numeric impact of several.

    29 further: poor concluding paragraph where he kitchen sink like brings in other issues of general Mann badness (like verification stats) that he does not have the room to develop and that are not needed for examination of former issues.

  • Lazar // March 11, 2008 at 3:10 am

    Okay, I’ve been fiddling about with R and have a few results.
    I think I now understand Steve McIntyre’s (and Ross McKitrick’s) argument, something as follows…
    … decentered PCA applied to red noise creates a ‘hockey stick’ PC1, so there is a danger in doing decentered PCA of emphasizing sommat which is just noise.
    … the 1400AD step is highly dependent on the PC1 from the back-to-1400AD North American ITRDB network, which they claim is ‘mainly’ bristlecone pine.
    … if you supply red noise in place of the NA ITRDB network, the decentered PCA may ’shape’ a PC1 hockey stick in a way that resembles
    instrumental temperature enough to fool the algorithm.
    … he concludes MBH98 were wrong when they benchmarked significance by regressing red noise against temperature without first passing through decentered PCA. MBH98 RE benchmark significance at 0.0 (99%).
    … in the GRL paper (MM2005a), M&M try to do just that by passing red noise through decentered PCA, but, as far as I can make out, they don’t emulate the ‘full’ MBH98 algorithm, as I understand it.
    … I don’t understand why they didn’t.

    In order to obtain more accurate significance benchmarks, we regressed each of the 10,000 simulated PC1s against the MBH98
    northern hemisphere temperature series (the ’sparse’ subset used in MBH98 for verification
    )
    in the 1901-1980 calibration period — a procedure which more closely emulates actual MBH98 methods.

    Benchmark signficance at 0.59.

    Huybers commented,
    M&M did not carry out an (undisclosed) variance scaling step, resulting in inflated RE scores. With variance scaling, Huybers reported benchmark significance same as MBH98, 0.0.

    M&M respond, Huybers did not implement the variance scaling step correctly, and after implementation according to MBH98 code, M&M benchmarked signficance at 0.54.

    Steve’s R code for creating ‘red noise’ PCs is here, and the Wahl & Amman R code for emulating MBH98 is here.
    I reproduced their (WA) verification score for the 1400AD step, 0.48, then substituted two red noise ‘hockey stick’ PCs, lifted straight from 2004GL021750-hockeysticks.txt, for the PC1 and PC2 used to represent the NA ITRDB network. Ran the simulation. RE score 0.18 this time, lower but still significant according to MBH98.
    Tried again with another two red noise ‘hockey sticks’, 0.34 this time, quite high.
    Are the red noise proxies contributing?
    Remove both red noise proxies, down to 20 proxy indicators now and no NA ITRDB, and the score is not much different, 0.27.
    For fun, substitute a red noise ‘hockey stick’ for all 22 proxies / PC summaries, and the score is… -1.48.
    I need to do more runs, graph the results, and double check.
    Am I doing something wrong here (anything obvious)?
    Anyone else wanna have a go?
    PS, graphed the 22 proxies, apart from the 2 NA ITRDB PCs and one other, 8 out of the remaining 19 proxy indicators have a ‘hockey stick’ shape.

  • fred // March 11, 2008 at 3:23 am

    Luminous, you said “It is not really a question of statistics. It is a question of whether tree-ring growth has a causal, non-probabilistic relation to climate variation. It does.”

    This may be a misunderstanding of the issue (though I’m not totally confident of having understood it). There is a purely statistical issue. Even after you have accepted that tree rings are a temperature proxy, you’re only a small part of the way to the HS. You have no HS yet. You just have a series of what you believe to be temperature observations. But if you just plot them all on a chart, they will not be very informative, because they have so much random variation. They are very noisy. Its the submarine problem. You are listening for propeller noises, but the ocean is a noisy place, and if there is a signal, its obscured by the other noises.

    You have at this point a large number of series of data, too many, and have to simplify them to make sense of them. If memory serves, MBH had about 1,000 series and a much larger number of data points. The question is, what do they show and how do you display it.

    One thing you might try is averaging them - simply plotting the means by date. This has been done, and it also looks trendless, (which does not mean it really is).

    You could also do standard PCA. This does show a trend, but (apparently, I’ve not done it) where the first PC is also trendless.

    The contention of M&M, which was endorsed by Wegman, is that the method used by MBH takes some of the 1,000 series, and gives a stronger weight to them. The claim is also that it gives a stronger weight to those series with strong rises in the 20C. The amounts of the weighting have been calculated. The contention is that BCPs from Sheep Mountain have nearly 400 times the weight of other series.

    This gives rise to the remark, which sounds like a jibe but is not, that they could have simply used the BCPs by themselves and thrown out the rest of the data.

    I don’t think Tamino has addressed this issue in his posting, or that any of the other defenders of MBH have done so. As a matter of statistics, this seems not be a correct procedure. This is what M&M tried to show by applying the method to trendless red noise. Their contention was that if you do it, you get a HS shape 99% of the time. If this is true, then the HS as shown around the world is an artifact of the method.

    Continuing with the logic, the issue in all this is not simply whether there is an HS shape someplace in the data, but how important it is. How much of the variation in the data does it represent? The contention is that it is there OK, but represents under 10%, if you do PCA properly. That is, it is the fourth principal component not the first and not of any great significance. If however you do PCA in the way that MBH did it, not using the mean of the series, but the mean of a subset of it, it shows up as the first PC and represents most of the observations.

    It is not enough to say ‘you still get the HS’. You will always get it as long as any of your series has it. The question is whether it represents most of the data, or only a tiny proportion of it. Is it PC1 or PC4? This is the real issue.

    You see that the issue is independent of what you think of the relation of tree rings to temperatures. Even after you agree they measure temperature, the question remains, what your temperature series mean and what shape are they. This is the reason why it is a statistical question.

  • dhogaza // March 11, 2008 at 3:49 am

    “round(avg(max(1,5,3,4))) is better than max(round(avg(1,5,3,4))), because it better fits the reference value (which is 5).”

    Both methods are valid ways to use the functions. Unfortunately, the example is silly because there’s no physical theory supporting either formula. And that’s why fitting sample data to reference data is not enough. One must have a physical basis for the analysis method.

    There may be no physical theory, but surely, given your expertise (as expressed elsewhere), you understand that delaying an integer-to-floating point conversion, especially when later combined with an explicit rounding from float to int, is not a bad thing?

  • George // March 11, 2008 at 4:01 am

    TCO

    Part of getting your Ph.D. is getting the balls and experience to move into alternate fields.

    Perhaps, but I’d say just as (if not more) important is leaning to recognize ones own limitations and ignorance (especially outside one’s own narrow field).

    Sometimes (more often than not?) when one attempts to characterize the current state of a scientific area that is not one’s own, one merely makes a fool of oneself.

    Even Nobel caliber scientists have fallen into this trap.

  • fred // March 11, 2008 at 4:04 am

    A brief comment on this question of CO2 again. It really is misleading to say in this context and without qualification that the more CO2 you have, the higher the temperature. The real situation is that raising CO2 from 280ppm to 380 has a largish effect. Raising it from 380 to 480 has a much smaller one. From 480 to 580 a still smaller. And so on. Yes, its literally a continuing rise for ever. But it needs qualification.

    “The more CO2, the higher the temperature, with decreasing effects up to about x%, when the effect becomes insignificant”.

    This would be a correct, and less alarmist, way to put it.

    It is also true to say that this effect, for doubling of CO2 from 280ppm, is 1.2 degrees. The evidence required for feedback amplifying this 1.2 degree increase is quite different from the evidence for the warming from CO2. Not that it does not exist. But it is quite different. If we discover feedbacks don’t exist or are negative, or even are higher than the IPCC supposes, no modification of laws of physics will be needed. Whereas to refute or increase the warming effect of CO2, the laws of physics would have to be changed.

    To say this is not an sort of ‘ism’, its just stating facts. You can only get to proper assessments of AGW if you disentangle the different elements. Doing which is, to disentangle yet another thing, completely different from being a “denialist”. It is rather like the difference between finding out what the doctrine of the Real Presence is, as opposed to the heresy of denying it.

  • dhogaza // March 11, 2008 at 5:11 am

    So over at CA, where McIntyre “demolishes” Tamion, we have the other Mc posting:

    It’s very telling that Tamino fails to link to a single one of our papers

    Well, yes, it’s very telling. Why should he or anyone else?

  • Bob North // March 11, 2008 at 5:12 am

    Having waded through all of this, I guess one fundamental question remains: Given the various climatic/weather/local site factors that do affect tree ring growthm(or many of the other proxies), are we trying to tease too much out of the available data, regardless of statistical technique? I have no doubt that there is some temperature signal in tree rings (probably more of a growing season signal than an actual annual signal) but as rightly pointed out by MrPete (I think, it was so long ago), there are a lot of other factors that affect plant growth, even in areas where, in theory, growing season temperture is a dominant limiting factor.

    Also, I am probably wrong, but I seem to remember from reviewing various papers some time ago, that the correlations between temperature and tree ring width and max wood density are ok, but not great. Based on all this, I seriously doubt that we can nail down the average global temperature 800 years ago to within a few tenths of a degree C.

    Now, as noted above, none of this really affects the basic premise that CO2 is a greenhouse gas and that man has the potential to significantly affect global climate, whether through GHG emissions or land use changes, etc. What it does affect is the conclusion that the current temperatures are unprecedented and the extent to which limited future warming (1-3 degrees C)will be “catastrophic”.

    Finally, HB if you could address more clearly in your next post on PCA why the centered PCA didn’t pick up the hockey stick in your hypothetical example, but the decentered “PCA” did pick it up, it would be much appreciated. I am not sure that you answered this question when you responded to my previous post early on in this thread.

    Regards,

    [Response: But the centered PCA *did* pick up the hockey stick -- it was in PC2 rather than PC1. Likewise, with the actual data it's picked up by centered PCA, mainly in PC4 rather than PC1.]
    Bob North

  • dhogaza // March 11, 2008 at 5:20 am

    McKittrick makes an interesting claim:

    I guess Tamino also hasn’t inspected the CENSORED folder or grasped the meaning of what was in it. Without the BCP’s the decentering doesn’t matter since the remaining series all have stable means, and no hockey stick emerges in any PC.

    So now they’re conflating two supposed evils, without justification AFAICT

    1. BCP proxies are bad.

    2. Including them in the analysis shows that decentered PCA is bad.

    3. The hockey stick doesn’t appear w/o BCPs, no matter what analysis you do (false, others have done this)

  • per // March 11, 2008 at 9:00 am

    “Actually he said that the non-centered pca pushes the temperature signal PC to be more prominent, which, for the non-short-bus crowd,
    is indeed the WHOLE POINT.”

    well, he has made a synthetic example where he gets different results with the two methods. But the example doesn’t prove the general case; it is just an isolated example.
    “Wegman’s right about this much: a non-standard centering convention will indeed emphasize the variation of the mean, which turns out to be the main difference between the 20th century and the rest of the time span. What he fails to realize is that that’s the point. ”
    This is fixing the analysis method, so that you get the result that you desire. This is a faulty approach.
    joliffe goes out of his way to say that you must explain why you use a non-centred PCA, because it can introduce artefacts. Saying that it gives the “result” you want is not a scientific explanation. Saying that it emphasises variation from the mean (the 20th century increase) means that you know you are fixing the results. Again, not science.

  • MrPete // March 11, 2008 at 11:15 am

    dhogaza, don’t miss the joke…

    “surely… you understand that delaying an integer-to-floating point conversion… is not a bad thing?”

    I sure do. I suppose my example may have been more successful than expected! The rounding is obfuscation in this case. Surely you understand how avg(max(…)) is both similar to and quite different from max(avg(…)) … and both in a “silly” way :-)

    Solve the riddle: what do these expressions reduce to (in general, ignoring the specific data)?

  • MrPete // March 11, 2008 at 11:33 am

    George, “Sometimes (more often than not?) when one attempts to characterize the current state of a scientific area that is not one’s own, one merely makes a fool of oneself.”

    Well said! So the trick is to understand what “one’s own” area(s) are.

    Personally, I have confidence about a very restricted set of knowledge that’s actually “mine.”

    For the rest, I listen broadly and try to see things from a variety of perspectives, recognizing that many areas of expertise will bring valuable understanding to a particular set of issues.

    That’s different from expecting the experts in a single area to be the sole authority for issues that fall more or less into their bailiwick.

    Another way of putting it: I’ve found that, even for brilliant experts, today there are very few applied issues (brain freeze - not sure that’s the right term at 5am :-) ) that 100% fall into “their” area of science or knowledge. What do you think?

    To be extreme, show me a piece of nature where a single scientific specialty “owns” all knowledge relevant to that bit. Isn’t the world “naturally” multidisciplinary?

    (Interesting, I started searching for definitions of “climate science” — it’s not universally agreed what that actually is.)

  • Meltwater // March 11, 2008 at 12:54 pm

    Patrick Hadley wrote:

    Incidentally, while I gave four reasons to justify the continued debate about the HS, if Meltwater was right when he wrote ” For the ‘hockey stick’ to be wrong, a great deal of other science has to be wrong too. ” then it would seem that the stakes are even higher.

    Hansen’s Bulldog, aka tamino, added:

    [Response: I disagree strongly with the “a great deal of other science has to be wrong too” part. But I don’t speak for my readers, just as they don’t speak for me.]

    And fred said:

    meltwater, it will help to … talk about different things differently.

    The hockeystick, MBH98 and subsequent papers, could be wrong. Decentered PCA could also be wrong. And it still could be warming due to CO2.

    You don’t have to accept MBH to be convinced by the arguments for CO2 driven warming.

    All these comments left me thinking that in my own earlier comment I carelessly mis-phrased what I was trying to say. I did not mean to suggest that the soundness of the overall case for anthropogenic global warming (AGW) somehow immunizes the Mann et al. (MBH98) ‘hockey stick’ against error or criticism. Nor did I mean to imply that any possible refutation of MBH98 would also discredit the overall case. Frankly, I did not realize then that my comment could be taken in such ways, although it seems obvious now.

    When I asked—

    Given the accelerating rate of human unburied carbon emissions, how could a temperature ‘hockey stick’ not result?

    —and then asserted—

    For the ‘hockey stick’ to be wrong, a great deal of other science has to be wrong too.

    —I intended to argue broadly that some sort of ‘hockey stick’ temperature graph has to be right, not necessarily that the specific MBH98 graph has to be right.

    I wrongly imagined that by saying “a temperature ‘hockey stick’” in my question I had made this clear. Regrettably, I undid any such clarity when I said “the ‘hockey stick’” in my assertion, which apparently referred to MBH98.

    I’m sorry that my verbal clumsiness wasted so much time and bandwidth, and I ask you all to look away from that, focusing instead on my intended point:

    Since human unburied carbon emissions have driven CO2 concentrations upward in a manner that would make a ‘hockey stick’ shape on a graph of atmospheric composition over the last few hundred thousand years,

    —and since we know from radiation physics that atmospheric CO2 molecules absorb IR, get kinetically excited and heat the surrounding gas,

    —the smart money would bet that a resulting ‘hockey stick’ shape would be found on a graph of global mean temperatures over a comparable time-span.

    Indeed, for such a shape not to result would mean something surprising, like a physical mechanism that prevents climate sensitivity to CO2, and/or a great deal of other science being wrong.

    Now that I have phrased my point more carefully, I ask you all, including Hansen’s Bulldog: Do you still disagree? If so, why?

    [Response: I agree that for such a shape not to emerge would be surprising. But there's one caveat. So far we seem to have experienced about 0.75 deg.C modern warming (depends on exactly where you start, but that's in the ballpark). Climate sensitivity (to forcing, not to doubled CO2) seems to be around 0.75 deg.C/(W/m^2) (not precise but in the ballpark). So we might have experience comparable warming (or cooling) in the not-too-distant past IF there was a forcing change of about 1 W/m^2 sustained long enough for its impact to be felt, or a greater forcing change for a more brief time. This is implausible but not impossible.]

  • Surly // March 11, 2008 at 2:06 pm

    According to one poster over there, MM’s breaking the hockey stick saved the world from needless destruction. I feel so relieved.

  • fred // March 11, 2008 at 2:24 pm

    “with the actual data it’s picked up by centered PCA, mainly in PC4 rather than PC1″

    Yes, but that is the point at issue, surely? PC1 explains most of the variation. PC4 explains very little. Its not a small thing to demote the HS from PC1 to PC4. Its the difference between it being the main trend, and something quite close to noise, no?

  • Hank Roberts // March 11, 2008 at 2:35 pm

    dz, it’s a monkey trap. There are dozens of blogs making claims about beliefs. Copying that stuff here is second hand, why bother? It’s ’see what they said’ if attributed. If not attributed, it’s just copypaste tactical stuff (A stinging remark! I’ll go pretend it’s mine by pasting it into a climate blog).

    You realize they fish for goats, don’t you? Don’t let them catch yours!

    Review the copious notes, there’s extensive documentation on how it’s long been done on Usenet. Recognize this, don’t be caught up in copypaste.

    alt.syntax.tactical FAQ - Dealing with Trolls Crossposting and Flames:
    Playtime (1 off trolling) * Tactical (long term trolling by a single character) * Strategic (long term trolling using multiple characters and different …
    http://ddi.digital.net/~gandalf/trollfaq.html

  • George // March 11, 2008 at 2:40 pm

    I’m still a little unclear exactly why PCA would be used in this case.

    How (or more to the point is) the answer obtained with PCA somehow superior (more reliable, more robust, etc) than the answer obtained with simpler, more straightforward less manipulative, techniques?

    It strikes me that sometimes itis better to do less data processing than more.

    I guess the main question for me is this:

    Why change the data representation with PCA at all if there is the possibility that it might introduce ambiguity in the final result? (depending on which components are selected, in this case)

    If one has to include a certain (possibly unspecified) number of the components to be certain that one has not missed something important, what has one gained?

  • Tom C // March 11, 2008 at 2:44 pm

    So over at CA, where McIntyre “demolishes” Tamion, we have the other Mc posting:

    It’s very telling that Tamino fails to link to a single one of our papers

    Well, yes, it’s very telling. Why should he or anyone else?

    Why? Because then they could read the papers themselves and would realize how Tamino has distorted the content.

  • Meltwater // March 11, 2008 at 2:45 pm

    Quoting me, fred responded:

    “People intent on finding fault with the ‘hockey stick’ deserve to have their arguments and their intellectual honesty challenged.”

    No, they need to have their arguments challenged. The rest is pointless personal insults which get no place.

    A more civil and reasonable discourse of the kind fred invites would be wonderful but, in the world we have, I am sadly sure that challenging arguments alone is not enough.

    If it were enough, why do denialist polemics like that of Singer and Avery keep repeating arguments that were scientifically refuted long ago? To give only two of many examples:

    Singer and Avery suggest that human activity is too ‘puny’ to affect the climate even though Högbom and Arrhenius showed more than a century ago that accessible coal and oil suffice if combusted to multiply the atmospheric concentration of CO2 several times over, and that merely doubling CO2 can change the climate.

    Singer and Avery suggest that the IR spectral bands absorbed by CO2 could be saturated, and more CO2 can be added to the atmosphere with relative impunity after saturation. This was a respectable view back in 1900 when Knut Ångström reported an experiment that seemingly confirmed it, but E.O. Hulburt challenged it as early as 1931, Lewis D. Kaplan had proved aspects of it wrong by 1952, and Gilbert N. Plass finished it off in 1956. There has not been any scientific basis for the spectroscopic saturation argument for more than half a century.

    Laypeople can be forgiven for not knowing how thoroughly the arguments for and against AGW have been weighed in the scientific literature over several generations. Yet some prominent ‘experts’ exploit such popular ignorance by repeating long-refuted arguments, with no other motive than to prevent timely political action to curtail unburied carbon emissions. Naomi Oreskes discusses them and their agenda on this video.

    Their behavior is not so easily forgiven. Not only are they intellectually dishonest; tragically, their dishonesty has prevailed. It is probably now too late for timely emissions curtailment. Disastrous warming sufficient to destroy whole cities and bioregions has likely become inevitable. Less timely action, which at best can only minimize the harm to come, is the most we might be able to manage now.

    We are all emitters, and we all share the blame for what’s coming. But the people who deliberately misled and still mislead the public deserve more blame than the rest of us. If we let their intellectual dishonesty go unchallenged, they will keep ‘swift-boating’ real science and real scientists, and thereby continue to thwart even the less timely emissions curtailment of which some prospect still remains.

  • fred // March 11, 2008 at 3:49 pm

    George

    “How (or more to the point is) the answer obtained with PCA somehow superior (more reliable, more robust, etc) than the answer obtained with simpler, more straightforward less manipulative, techniques?”

    I haven’t yet done PCA in anger, so treat this with caution. Maybe an analogy will help, imagine a text consisting of words in half a dozen languages. We can’t read it. If we can extract the English in one piece, we can read some of it. Then the Dutch…etc. Or we are listening for screw noises in a noisy ocean. Can’t distinguish them. Signal processing can do a better job than our eyes and ears and brains unaided.

    All you’re really doing with PCA is to extract the signal, or signals, from the noise. The key part is how important the extracted signal is as a percent of the whole. PC1 is usually going to explain a lot of what there is to be explained. PC4 and lower, very little.

    If you just look at the raw data you will see noise. This doesn’t mean there is no signal however.

    Have a look at Ross McKitrick
    “What is the Hockey Stick Debate About?”, fig 6. Whether or not you agree with the paper, the diagram shows the process. Remember, just because you can’t see it with the naked eye does not mean it is not there.

  • chriscolose // March 11, 2008 at 4:10 pm

    Meltwater, I definitely agree. There is a line between “skepticism” and “lying” and Singer and co. have crossed that a long time ago.

    What escapes me is why AGW arguments are held to such a high standard (i.e., bad proxy usage, and we never hear the end of it for a a decade now), but the denial propaganda is allowed to regurgetate the same garbage such as “CO2 lags temperature, so now AGW” or “1940-70 cooling, so no AGW” and you simply hear more of it, even after it is invalidated. Because the science is there, we have much more interesting things to talk about than conspiracies and dwelling on decade-old arguments which didn’t work out.

    What is strange to me is that this whole hockey stick argument can somehow be taken as a criticism of the enhanced greenhouse effect. The hockeystick doesn’t really show the warming, but rather a slow decline in temperatures over a long time, until an enhanced greenhouse effect kicks in (and this is based more in the instrumental record, and not so much PCA). The argument that an as warm as, or warmer than today MWP invalidates AGW is high level nonsense, as the medieval warmth is not part of the attribution effort. It also says nothing about what will happen in the future.

  • George // March 11, 2008 at 4:48 pm

    fred claims:

    “It really is misleading to say in this context and without qualification that the more CO2 you have, the higher the temperature.”

    Misleading? How so?

    The statement as it stands is quite correct on its own.

    Fred rationalizes:

    … it needs qualification.

    “The more CO2, the higher the temperature, with decreasing effects up to about x%, when the effect becomes insignificant”.

    This would be a correct, and less alarmist, way to put it.

    No, specifying an effective “cutoff” would not be a correct way to put it.

    It would, however, be a more subjective way to put it, that much is certain.

    Words like “insignificant”, “alarmist”, etc are subjective. Insignificant compared to what? By what measure? Alarmist by whose definition?

    To say that “more CO2 will lead to more warming– all else being equal” is quite accurate. Adding subjective qualifications to the statement makes it less — not more — accurate.

  • David Holland // March 11, 2008 at 5:08 pm

    When Michael Mann mentioned Ian Jolliffe on RC in connection with his non centred PCA, I could not see that the link he gave helped him. When he didn’t answer question as to whether Jolliffe endorsed his method I asked Jolliffe myself and this was his reply dated 25th Feb 2005:

    “I’m afraid that I can’t offer you much enlightenment. I did not hear Michael Mann on the Today programme. Nor do I know what ’seminal work’ you refer to, or how or why he references me. From your email it may be a talk I gave in Cape Town last year, which was a brief review of alternative centerings - I can’t see that it said enough to used as a recommendation.
    My one (anonymous) interaction with Mann, his co-workers and his critics was last year when I acted as a referee for an exchange of views submitted to Nature. After a couple of iterations I came to conclusion that I simply could not understand what was being done sufficiently well to judge whether Mann’s methodology was sound, but I certainly would not endorse it. At least one other referee came to same conclusion. Although the exchange was not published in Nature I believe it may have appeared on a web site. I don’t know whether the methodology noted in your email is the same as that which referees found too opaque and/or complicated to understand.”

  • David Holland // March 11, 2008 at 5:37 pm

    Chriscolose says,

    “What is strange to me is that this whole hockey stick argument can somehow be taken as a criticism of the enhanced greenhouse effect.”

    In the Attribution Chapter 12 of the TAR you can read why. It says on page 702:

    We expect, however, that the reconstructions will continue to improve and that palaeo-data will become increasingly important for assessing natural variability of the climate system. One of the most important applications of this palaeoclimate data is as a check on the estimates of internal variability from coupled climate models, to ensure that the latter are not underestimating the level of internal variability on 50 to 100 year time-scales.

  • Barton Paul Levenson // March 11, 2008 at 5:48 pm

    anonymous writes:

    [[If the analysis of MBH were correct, I suspect long ago some professional academic statisticians would have backed them up. ]]

    They did. Fourteen other studies replicated MBH’s results. Read the NAS report.

  • George // March 11, 2008 at 5:54 pm

    Fred says:

    “Remember, just because you can’t see it with the naked eye does not mean it is not there.”

    Fred. I know what PCA is, but I am trying to understand how it is superior in this case to simple methods that also extract the signal from the noise. Averaging combined with piecewise linear regression is the one that comes immediately to mind.

    My question was really directed to Bulldog or someone else who is not only conversant with PCA but with lots of other data analysis techniques (including linear regression, which Bulldog uses quite a bit, at any rate)

    In this case, I actually can see it [the hockey stick] with the naked eye!

    Sure, the eyes/brain sometimes play tricks, but I have done enough spectroscopic analysis to appreciate that the power of the human eye/ brain combination should not be underestimated when it comes to finding patterns in noisy data. In fact, I’d say that in some cases, the human eye/brain combination is unmatched by even the best data analysis software running on the most powerful computers.

    …which, combined with the fact that simple techniques often work quite well in extracting a signal from noise, makes me wonder “why all the fuss over PCA”?

  • Barton Paul Levenson // March 11, 2008 at 5:54 pm

    fred writes:

    [[“CO2 is a greenhouse gas…. That means that the more of it you have in an atmosphere, the warmer the ground is going to get, all else being equal.”

    This is not true, as a matter of science, for two reasons. First that as CO2 rises, incremental rises have diminishing warming effects. The curve is logarithmic. It is not true that the more you have of it the warmer it gets in any unqualified sense.]]

    Which part of “warmer” did you think included “is not on a logarithmic basis?”

  • Layman // March 11, 2008 at 6:02 pm

    Per Wegman:

    “If the variance is artificially increased by decentering, then the principal component methods will “data mine” for those shapes. In other words, the hockey stick shape must be in the data to start with or the CFR methodology would not pick it up… Most proxies do not contain the hockeystick signal. The MBH98 methodology puts undue emphasis on those proxies that do exhibit the hockey-stick shape and this is the fundamental flaw. Indeed, it is not clear that the hockey-stick shape is even a temperature signal because all the confounding variables have not been removed.”

    The issue is that Mann’s method inappropriately amplifies signals from one set of proxies in a way that drowns out all other signals. De-Centering is a non-standard technique. It is incumbent on Mann to justify its use. For now, I assume it mines for hockey sticks unless shown otherwise.

  • per // March 11, 2008 at 6:06 pm

    “They did. Fourteen other studies replicated MBH’s results. Read the NAS report.”

    you may not understand that “replication” has a specific meaning; it means exact repetition. There may have been fourteen other reconstructions, but there are not 14 replications. In fact, even wahl and ammann were unable to exactly replicate MBH’s results. The shocking thing is that they were able to exactly replicate M&M.

    For the record, the fourteen similar studies have many of the same problems as MBH. That is why theNAS panel concluded right in the summary, that the error in reconstructions going back before thermometers is unquantifiable. In science terms, it is difficult to think of a more damning criticism.

  • Barton Paul Levenson // March 11, 2008 at 6:14 pm

    fred writes:

    [[It really is misleading to say in this context and without qualification that the more CO2 you have, the higher the temperature.]]

    No matter how many times you say this, it still won’t be true.

    [[ The real situation is that raising CO2 from 280ppm to 380 has a largish effect. Raising it from 380 to 480 has a much smaller one. From 480 to 580 a still smaller. And so on. Yes, its literally a continuing rise for ever. But it needs qualification.

    “The more CO2, the higher the temperature, with decreasing effects up to about x%, when the effect becomes insignificant”.

    This would be a correct, and less alarmist, way to put it.]]

    It would be an absurdly Pollyannish way to put it, since it gives the mistaken impression that we don’t have to worry too much about CO2 rising. We do. And your “no further effect” level is not reached even on Venus, which has 88 bars of CO2, a surface temperature averaging 735.3 K, and on which, according to Bullock’s simulations, you could probably reach 900 K under varying atmospheric conditions. The upper limit is irrelevant to any real planet, at least in this solar system.

    ]]

  • dhogaza // March 11, 2008 at 6:18 pm

    My one (anonymous) interaction with Mann, his co-workers and his critics was last year when I acted as a referee for an exchange of views submitted to Nature. After a couple of iterations I came to conclusion that I simply could not understand what was being done sufficiently well to judge whether Mann’s methodology was sound, but I certainly would not endorse it.

    This is a far cry from “Mann’s methodology was wrong” or “the hockey stick is broken”.

  • Chris O'Neill // March 11, 2008 at 6:31 pm

    fred:

    “The more CO2, the higher the temperature, with decreasing effects up to about x%, when the effect becomes insignificant”.

    This would be a correct, and less alarmist, way to put it.

    No it would not be correct and it would be a denialist way to put it. There is no “x%, when the effect becomes insignificant” that we would want to go anywhere near. Maybe the effect is insignificant on Venus but I hope you’re not suggesting we go anywhere near that situation. Although it is true that by the time we get to 560 ppm the effect of each new molecule of CO2 will be half what it was at 280 ppm, I don’t think this is going to keep us out of trouble. The warming from one doubling of CO2 is a very serious issue indeed.

    It is also true to say that this effect, for doubling of CO2 from 280ppm, is 1.2 degrees. The evidence required for feedback amplifying this 1.2 degree increase is quite different from the evidence for the warming from CO2. Not that it does not exist. But it is quite different. If we discover feedbacks don’t exist or are negative, or even are higher than the IPCC supposes, no modification of laws of physics will be needed.

    Which is an academic question anyway because the warming produced by CO2 alone, according to the laws of physics, is only 26% of the empirically observed warming and only a bit more than that including non-feedback gases such as N2O and CH4, i.e. without feedbacks there would only be a bit more than 26% of the empirically observed greenhouse effect.

  • fred // March 11, 2008 at 6:34 pm

    If anyone wants to check out BPL’s statement, the report is here:

    http://www.nap.edu/catalog.php?record_id=11676

    It would be helpful to have a reference for where the fourteen other studies replicating MBH are mentioned. I don’t recall them from a first reading, and didn’t find them on a superficial second glance. Which does not prove they are not there. But it would help if someone could point to exactly where they are.

  • fred // March 11, 2008 at 6:45 pm

    George, the point is not really a combative one, and it is surely reasonable. When we say in ordinary English that the more you get of A the more you get of B, most people would assume that it happens in roughly equal proportions.

    What they would not expect is that for every extra pound or gallon of A you get less and less more of B. The more gas you have, the further you can drive on that tank. Not that adding gas to your tank is subject to a law of diminishing returns.

    When this isn’t so, we usually are very careful to caution people. As in, for instance, we don’t just say the faster you are going, the further it takes to brake. We are very careful to say that its not linear. The same with speed and pedestrian deaths. We don’t just say, the faster you are going, the greater the risk of death. We are careful to indicate that risk of death rises faster than speed. This is why we have the shorthand ‘law of diminishing returns’. Its because of the general assumption of linearity, which people expect to have exceptions signalled to them.

    I am not a great advocate of raising CO2 levels, it seems at best imprudent. But I am a great advocate of careful characterization, and one ought to be clear in speaking about the relationship that it is far from linear. Its not JUST a question of the more you add the hotter it gets. We should follow the usual conventions in making this clear and explicit.

    In the same way, its not JUST a question of the less you have, the cooler. Think about this the other way. If everyone is right, and if we should be reducing CO2 at some point, it will not either be very useful to tell people the more you take out the cooler it will get. You’re going to have to explain that at first, what you take out will have little effect, but that as you keep it up, later takeouts will have more and more. There will be pain without gain at the start. Just as there will be gain without very much pain at the end, going the other way.

  • Chris O'Neill // March 11, 2008 at 6:49 pm

    fred:

    The key part is how important the extracted signal is as a percent of the whole. PC1 is usually going to explain a lot of what there is to be explained. PC4 and lower, very little.

    No, that’s not the key part. The key part is which PC has the signal that we want (e.g. temperature). If there are stronger PCs that do not correlate with our signal then they are just noise. Being stronger doesn’t give them any special significance at all. Just means they are something we are not interested in.

  • Will Richardson // March 11, 2008 at 7:13 pm

    Re: Levenson @ 5:48

    No, the NAS report referred to other studies, most of which use similar analyses as MBH and the same data sets, including Mann’s improperly derived PC1, but did not examine those studies to determine whether those studies suffered from the same errors and weaknesses contained in MBH. Those other studies cannot be deemed independent when they use the same data, in the same way as in MBH. The NAS report did state that NAS agreed with McIntyre’s and Wegman’s statistical criticism of MBH, and agreed that the bristlecone proxies should not be used. All of the fourteen studies NAS referenced used some form of the bristlecone proxies.

  • per // March 11, 2008 at 7:29 pm

    “The key part is which PC has the signal that we want (e.g. temperature). If there are stronger PCs that do not correlate with our signal then they are just noise. Being stronger doesn’t give them any special significance at all. Just means they are something we are not interested in.”

    this is wrong. The whole point in having all these proxies, is that they are meant to behave as thermometers, each representing the temperature in a different part of the world. That is why it was so important for MBH to say that PC1 was the dominant pattern of variance, because it suggests that temperature was the dominant cause of variation.

    If you are simply using the PCA to select for a few records which show a correlation with temperature, then you might as well throw the other records out; but then, you would have no basis for saying that your method was a global (or northern hemisphere) reconstruction of temperature.

    And for the record; it isn’t a god-given truth that any of the proxies studied are actual accurate temperature proxies. If you actually test this in a PCA/ verification analysis, and you find that only 8% of the signal (PC4) gives a borderline significant (if that) association with temperture record, then you have a very shaky basis for even believing that the PC is a temperature proxy.

  • luminous beauty // March 11, 2008 at 7:37 pm

    “One of the most important applications of this palaeoclimate data is as a check on the estimates of internal variability from coupled climate models, to ensure that the latter are not underestimating the level of internal variability on 50 to 100 year time-scales.”

    One might think this means that a higher level of past internal variability means that some larger portion of temperature increase from the instrumental record might be due more to internal variation than EGE.

    One would be wrong.

    It would mean a greater natural variation upon which the EGE must then be added for the purpose of model projections. It just means more wobble in the curve. It doesn’t diminish the greenhouse effect. In fact, it suggests the opposite. A system that is more sensitive to unforced internal oscillation is likely to be more sensitive to external forcing as well.

  • dhogaza // March 11, 2008 at 7:50 pm

    Per:

    That is why theNAS panel concluded right in the summary, that the error in reconstructions going back before thermometers is unquantifiable. In science terms, it is difficult to think of a more damning criticism.

    Not quantifiable, huh?

    Less confidence can be placed in large-scale surface temperature reconstructions for the period from A.D. 900 to 1600. Presently available proxy evidence indicates that temperatures at many, but not all, individual locations were higher during the past 25 years than during any period of comparable length since A.D. 900. The uncertainties associated with reconstructing hemispheric mean or global mean temperatures from these data increase substantially backward in time through this period and are not yet fully quantified.

    Gee, not exactly what the summary actually says, is it, Per?

    And what, exactly, is damning about a summary that concludes:

    The basic conclusion of Mann et al. (1998, 1999) was that the late 20th century warmth in the Northern Hemisphere was unprecedented during at least the last 1,000 years. This conclusion has subsequently been supported by an array of evidence that includes both additional large-scale surface temperature reconstructions and pronounced changes in a variety of local proxy indicators, such as melting on ice caps and the retreat of glaciers around the world, which in many cases appear to be unprecedented during at least the last 2,000 years.

    The reason why we say the NAS report declared that Mann was right in his basic conclusion is because, AS YOU CAN READ YOURSELF, that’s exactly what the summary says.

    What’s damning, Per, is your playing “fast and loose” with the report. Don’t worry, others on your side have assured us that playing “fast and loose” isn’t dishonest, apparently it’s just fine to do so…

  • mikep // March 11, 2008 at 7:59 pm

    But we just get back to the point that in MBH nearly all the hockey stick series are bristlecone pines. The reconstruction therefore depends not on the whole proxy set but on a tiny subset, and therefore in no sense a northern hemisphere reconstruction except insofar a bristlecone pines have a reliable relationship - unlike everything else - not with local temperatures but with the Northern hemisphere temperature. There are very good grounds for doubting that bristlecone pines do act as such standard candles. The best evidence for this is that their growth does not correlate with late 20th century temperature increases. Ever since M&M isolated which series were picked out (nb not created) for differential weighting by de-centred PCA this has been the issue. (And incidentally M&M were well aware that conventional PCA put the bristlecones and hence the hockey stick in PC4 - it’s discussed in their 2005 articles). The danger is of spurious regressions. That’s the point of repeating the MBH exercise with stock prices instead of bristlecones: stock prices do just as well as bristlecones in predicting temperature. This suggests we need to dig a bit deeper than simple verification stats before we conclude we have have found a magic species whose growth. almost alone among trees, acts as an accurate thermometer (and not for local, but for hemispheric temperatures).

  • dhogaza // March 11, 2008 at 8:36 pm

    I didn’t post enough of that report, but I imagine most here are familiar with it, and with the fact that they state that they think Mann’s conclusions are “plausible”. Which outside the report, members have stated was meant to mean “more likely than not”.

  • David Holland // March 11, 2008 at 8:50 pm

    Barton Paul Levenson said:

    “They did. Fourteen other studies replicated MBH’s results. Read the NAS report.”

    I read it and they do not. You should read what those involved in the NRC (NAS) Report said (under oath) to the Whitfield Subcommittee in the hearing transcript.

    1 Ralph Cicerone President of NAS who set up the NRC Panel said Wegman was credible on statistical issues.

    2. Gerald North, Chairman of the NRC panel and panel member Peter Bloomfield both said they agreed with Wegman and the NRC report says pretty much the same as Wegman.

    3. Gerald North said in written answers “for the record”:

    “I may have mistakenly mentioned the “two to one odds” figure in the oral press release of the report, and it may also have appeared in some press accounts, but it does not appear in the report, and I avoided using it in my sworn testimony.

    In our view it is not possible to quantify all of the inherent uncertainties associated with reconstructing surface temperatures from proxy data, which in turn precludes assigning numerical probabilities to statements regarding the unique nature of recent warmth.”

    Now what is true is that the NRC panel looked at virtually the same studies, as did the IPCC Chapter 6 including Wahl and Ammann and Rutherford et al as well as M&M and made not one criticism of M&M but all the ones that you’ve been told of here of Mann et al. - PCA, Bristlecones and verification failure.

    So my question is, how do the IPCC guys figure a probability of up to 90% based on the same proxies which they admit have problems and are “not entirely independent”?

  • Hank Roberts // March 11, 2008 at 8:53 pm

    > stock prices instead of bristlecones:
    > stock prices do just as well as
    > bristlecones in predicting temperature

    Citation please? I’m very curious to look at the tulip stock bubble. Was that the MWP? This may be important.

    They looked at the full history of stock trading, many centuries’ worth -right?

    Any subsequent citations in later journal articles, please?

  • BoulderSolar // March 11, 2008 at 8:59 pm

    Tamino,

    You said:
    “Did they really discard the relevant PCs just to copy the bare number of PCs used by MBH, without realizing that the different centering convention could move the relevant information up or down the PC list? You betcha”

    In MM2005 they stated:

    “Under the MBH98 data transformation, the distinctive contribution of the bristlecone pines is in the PC1, which has a spuriously high explained variance coefficient of 38% (without the transformation – 18%). Without the data transformation, the distinctive contribution of the bristlecones only appears in the PC4, which accounts for less than 8% of the total explained variance.”

    So it looks like you owe them a retraction.

  • David Holland // March 11, 2008 at 9:03 pm

    And as for “pausible” meaning more likely than not, look it up. My dictionary says of statements it means “specious, seeming reasonable or probable” and of persons “persuasive but deceptive” .

    And who are the et al in Rutherford’s paper? IPCC do not say but it’s Mann Bradley Hughes Briffa and Jones. Briffa was a Chapter 6 lead author and so was Ammann’s boss at UCAR.

  • Chris Colose // March 11, 2008 at 9:04 pm

    Fred, using decent numbers, say

    5.35 * ln(380/280) = 1.6 W/m2
    5.35 ln (560/380)= 2.07 W/m2

    This means we still have a bit more from the rest of the way to 560 than we had so far, but you also need to consider what aerosols have done, as well as “in the pipeline” warming from thermal intertia, and non-linear effect of feedbacks. We have obviously already included the logarithmic relationship, and under busness-as-usual scenarios out to 2100 it may be possible to even triple pre-industrial CO2. We’re already talking over 3 degrees, which is rather significant. At no point will further CO2 have no effect, so I really do not know what your point is.

  • cce // March 11, 2008 at 9:08 pm

    It’s worth repeating, once again, that the Hockey Stick emerges if you just averaged the proxies together, or if you remove the BCPs entirely. The BCPs are included because they strengthen the verification of the early part of the reconstruction. And the reason that the NRC report doesn’t quantify the likelihood of modern temps vs historical temps (thus relying on statements of “high confidence,” “less confidence” and “plausible”) is because it’s an expert opinion or judgment call.

  • Lazar // March 11, 2008 at 9:14 pm

    If I were to use Steve’s code to generate red noise series for each (individual) proxy in the 1400AD step, form ‘hockey stick’ PC summaries where appropriate, and substitute these for Wahl & Amman 06 proxy series and see what comes out; what the shapes are, what the scores are, and then do the run 100 times, benchmark RE at 99%, and compare with MBH98… would that be a fair and relevant evaluation? Will I be doing anything obviously stupid? Anyone, yes, no?
    If the results show MBH98 is significant, does it refute the possibility that MBH98 resulted from a decentered PCA pulling ‘hockey sticks’ from noise?
    Dependency on bristlecones, and the potential for decentered PCA to give low mean values of the 1400-1901AD period are separate issues that have, I think, been succesfully refuted by Wahl & Amman 06.

  • cce // March 11, 2008 at 9:28 pm

    It was not Gerald North who referred to 2:1 odds (~”Less Confidence” in the NRC report, ~”Likely” in the IPCC language), it was Peter Bloomfield, a statistician on the panel. John Wallace, an atmospheric physicist, also said that it was “likely.” They didn’t want to get into assigning numbers because they are arbitrary. The IPCC assigns numbers because policymakers demand them. Otherwsie, people sit around debating ambiguous language like we are doing now.

  • per // March 11, 2008 at 9:31 pm

    dear dhogaza
    thanks for your interesting post. It is a year or so since last I looked at the NRC report, so I think my recall is pretty good.
    “The uncertainties associated with reconstructing hemispheric mean or global mean temperatures from these data increase substantially backward in time through this period and are not yet fully quantified.”
    let’s go through this step by step, because you need a helping hand. If I ask you currently if we can quantify the uncertainty in reconstructions, then - according to the NRC report- the answer is “not yet fully”. You may have difficulty parsing this; so let me make it simple for you. NO.

    If we can’t “yet”, “fully” quantify something, it’s unquantifiable.

    I am also amused by your suggestion that the NRC supported Mann’s conclusions by saying that they are “plausible”. Science is about rigorously testing hypotheses, colloquially referred to as proof. Plausible is a word you use to describe the latest James Bond film or episode of Baywatch.

    Since you don’t seem so good at numbers, “more likely than not” includes ratios like 50.001: 49.999.

    All of which is a long, long way from the entirely spurious 95% confidence limits in MBH. Just ask yourself the simple question; if the NRC believed in MBH’s 95% confidence limits, why didn’t they say so ? why are they saying not yet, fully quantified ?

  • per // March 11, 2008 at 9:37 pm

    David Holland nails it with Gerry North’s comment. It is very clear, it is sworn testimony, and North was the chairman of the NRC panel.

    Dhogaza, i invite you to read what North said, and consider it carefully.

  • Paul G // March 11, 2008 at 9:47 pm

    = dhogaza said: =

    ==”they state that they think Mann’s conclusions are “plausible”. Which outside the report, members have stated was meant to mean “more likely than not”.”==

    “Probable” means “more likely than not”. Plausible is much weaker, inside the report, or outside of it.

  • dhogaza // March 11, 2008 at 9:57 pm

    And as for “pausible” meaning more likely than not, look it up. My dictionary says of statements it means “specious, seeming reasonable or probable” and of persons “persuasive but deceptive” .

    Members *explained* what they meant by “plausible”. I’m not depending on a dictionary definition, I’m depending on what THEY’VE said they mean.

    I’m certain you know this. I’m certain you don’t care.

  • dhogaza // March 11, 2008 at 10:02 pm

    and of persons “persuasive but deceptive”

    Nice. A claim that the report accused Mann of deceptiveness. Just one more slander.

  • Hank Roberts // March 11, 2008 at 10:02 pm

    >plausible … dictionary

    Citatin, please? What’s your dictionary?

    It appears “plausible” is used one way in academic research and the opposite way in rhetoric and debate. Curious.

    A few selections from the online American Heritage® Dictionary of the English Language: Fourth Edition. 2000.

    5) recension.
    …1. A critical revision of a text incorporating the most plausible elements found in varying sources. 2. A text so revised. Latin recnsio, recnsion-, a reviewing,…

    6) implausible.
    …Difficult to believe; not plausible. im·plausi·bili·ty -NOUN im·plausi·bly …

    8) plausive.
    …1. Showing or expressing praise or approbation; applauding. 2. Obsolete Plausible. From Latin plaudere, plaus-, to applaud….

    9) convincing.
    …1. Serving to convince: a convincing argument; a convincing manner. 2. Believable; plausible: a convincing story. See synonyms at valid. con·vincing·ly

    10) believable.
    …Capable of eliciting belief or trust. See synonyms at plausible. be·lieva·bili·ty -NOUN be·lieva·bly -ADVERB…

    ——————-
    Flammable! Inflammable!

  • Hank Roberts // March 11, 2008 at 10:05 pm

    The earlier results:

    Search Results for “plausible”
    http://www.bartleby.com/61/

    1) sophism.
    …1. A plausible but fallacious argument. 2. Deceptive or fallacious argumentation. Middle English sophime, sophisme, from Old French sophime, from Latin sophisma,…

    2) plausible.
    …1. Seemingly or apparently valid, likely, or acceptable; credible: a plausible excuse. 2. Giving a deceptive impression of truth or reliability. 3. Disingenuously…

    3) credible.
    …1. Capable of being believed; plausible. See synonyms at plausible. 2. Worthy of confidence; reliable. Middle English, from Latin crdibilis, from crdere, to believe….

    4) sophistry.
    …Inflected forms: pl. soph·is·tries1. Plausible but fallacious argumentation. 2. A plausible but misleading or fallacious argument….
    ——————————–

    Would anyone care to illustrate sophistry?

  • mikep // March 11, 2008 at 10:07 pm

    The work on stock prices - actually high-tech stocks can be found at

    http://www.climateaudit.org/?p=370

  • mikep // March 11, 2008 at 10:36 pm

    CCE you say that
    ” the Hockey Stick emerges if you just averaged the proxies together, or if you remove the BCPs entirely.”
    M&M have done the clacualtions - see their 2005 E&E article and the answer they get is
    “If de-centered PC calculation is carried out (as in MBH98), then MM-type results
    still occur regardless of the presence or absence of the PC4 if the bristlecone pine
    sites are excluded, while MBH-type results occur if bristlecone pine sites (and PC4)
    are included. Mann’s FTP site [Mann, 2002–2004] actually contains a sensitivity
    study on the effect of excluding 20 bristlecone pine sites5 in which this adverse
    finding was discovered”

    No one to my knowledge has ever shown this to be wrong.

  • David Holland // March 11, 2008 at 10:54 pm

    Hank

    Pocket Oxford, Sixth Edition, 1982.

    But what really matters is what Gerry North said the NRC meant by it. The IPCC say that second half of last century was 66 to 90% likely to be exceptional. The NRC have the honesty to say they that believe it is but that the data does not allows a numerical probability to be calculated.

    If you take into account the vested interest of the lead authors and review editors of AR4 Ch 6 it was like asking turkeys to vote for Christmas to expect them to admit the conclusions that they were a part of in 2001 were wrong.

  • cce // March 11, 2008 at 11:01 pm

    Here are the relevent sections from Jerry North’s followup questions of his testimony:
    http://frwebgate.access.gpo.gov/cgi-bin/getdoc.cgi?dbname=109_house_hearings&docid=f:31362.wais
    http://frwebgate.access.gpo.gov/cgi-bin/getdoc.cgi?dbname=109_house_hearings&docid=f:31362.pdf

    This is the definition of plausible used by the NRC Panel:
    “Our working definition of ‘plausible’ was that the assertion is reasonable, or in other words there is not a convincing argument to refute the assertion. We used this term to describe our assessment of the statement that ‘the last few decades of the 20th century were warmer than any comparable period over the last millennium’ because none of the available evidence to date contradicts this assertion. In our view it is not currently possible to perform a quantitative evaluation of recent warmth relative to the past 1,000 years that includes all of the inherent uncertainties associated with reconstructing surface temperatures from proxy data. This precludes stronger statements of confidence, but it does not mean that the assertion is false. In fact, all of the large-scale surface temperature reconstructions that we examined support the assertion that global-mean temperatures during the last few decades of the 20th century were unprecedented over at least the past 1,000 years, and a larger fraction of geographically diverse proxy records experienced exceptional warmth during
    the late 20th century than during any other extended period from 900 A.D. onward.”

    North on Wahl and Amman and von Storch:
    “My personal impression of these two papers is that the quote cited above (From the report: ‘In practice, this method, though not recommended, does not appear to unduly influence reconstructions of
    hemispheric mean temperature’) still applies, that is, none of the statistical criticisms that have been raised by various authors unduly influence the shape of the final reconstruction. This is attested to by the fact that reconstructions performed without using principal components yield similar results.”

    North on Strip Bark:
    “In summary, it appears that there is a carbon dioxide fertilization effect in some trees, but not in all the places where the samples used in the Mann et al studies were taken. Also note that this section of the report discusses the calibration of tree-ring records since atmospheric carbon dioxide levels started to increase around 150 years ago. Hence, in context, what the clause “strip-bark samples should be avoided for temperature reconstructions” was intended to convey is that strip-bark samples from the mid-19th century to the present are very difficult to calibrate against instrumental records of temperature, and the easiest solution is therefore not to use them. However, strip-bark data are considered suspect only after the modern increase in atmospheric carbon dioxide concentrations. This is why other studies that rely on strip-bark pine records only use them to infer past temperatures prior to 1850 (e.g., Biondi et al. 1999).”

    (Mann attempted to correct for cO2 fertilization)

    North on the Hockey Stick error bars and whay the do and do not mean:
    “As noted in our report, these error bars provide an indication of how well the reconstructed temperatures match observations during the ‘calibration period,’ but they do not represent all of uncertainties inherent in reconstructing surface temperature from proxy data. The actual uncertainties in the reconstruction would be somewhat larger, and difficult to quantify.”

    North on the Wegman Report:
    “Dr. Wegman’s criticisms of the statistical methodology in the papers by Mann et al were consistent with our findings. Our committee did not consider any social network analyses and we did not have access to Dr. Wegman’s report during our deliberations so we did not have an opportunity to discuss his conclusions. Personally, I was not impressed by the social network analysis in the Wegman report, nor did I agree with most of the report’s conclusions on this subject. As I stated in my testimony, one might erroneously conclude, based on a social network analysis analogous to the one performed on Dr. Mann, that a very active and charismatic scientist is somehow guilty of conspiring or being inside a closed community or ‘mutual admiration society’. I would expect that a social network analysis of Enrico Fermi or any of the other scientists involved with the development of modern physics would yield a similar pattern of connections, yet there is no reason to believe that theoretical physics has suffered from being a tight-knit community. Moreover, as far as I can tell the only data that went into Dr. Wegman’s analysis was a list of individuals that Dr. Mann has co-authored papers with. It is difficult to see how this data has any bearing on the peer-review process, the need to include statisticians on every team that engages in climate research (which in my view is a particularly unrealistic and unnecessary recommendation), or any of the other findings and recommendations in Dr. Wegman’s report. I was also somewhat taken aback by the tone of theWegman Report, which seems overly accusatory towards Dr. Mann and his colleagues, rather than being a neutral, impartial assessment of the techniques used in his research. In my opinion, while the techniques used in the original Mann et al papers may have been slightly flawed, the work was the first of its kind and deserves considerable credit for moving the field of paleoclimate research forward. It is also important to note that the main conclusions of the Mann et al studies have been supported by subsequent research. Finally, while our committee would agree with Dr. Wegman that access to research data could and should be improved, as discussed on page 23 of the prepublication version of our report, we also acknowledge the complicated nature of such mandates, especially in areas such as computer code where intellectual property rights need to be considered.”

    Note that they agreed that the statistical methods of the Hockey Stick could have been better, but what you will not find is a statement from North or anyone else on the panel saying that any of these flaws were significant or that the Hockey Stick was “bad science.”

  • Lazar // March 11, 2008 at 11:05 pm

    MrPete,

    I’ve learned enough from watching these arguments to know that it is not as simple as reading the “surface” of a paper like this and deciding whether the claims made are correct. The devil’s in the nit-picky details. For example, apparently WA isn’t using the same data — correlation 0.7 with MBH data.

    if I’m understanding correctly what Steve M said in the CA thread linked above

    You might have been pretty tired at the time! The quote refers to a paper by Bo Li (Casper Amman is a coauthor), which uses data purportedly from MBH99, that is proxy series which stretch back to 1000AD. (See comments #12, #15, #21, #22 and #29 again).

    The data in Wahl & Amman 2006 is from MBH98, the same data downloaded from the same ftp site used by Steve McIntyre.
    Steve has commented here on WA06;

    The order of the proxies in Ammann is a little different from MBH and Ammann provides no index for the proxies. In the AD1400 roster, the Stahle/SWM PC1 usually in the 16th spot occurs in the 22nd spot. I don’t plan to examine other steps. A first small difference - rounding before normalization of proxies. As far as I can tell, Mann’s practice is to normalize without rounding. Ammann sometimes rounds to the first decimal place before rounding. The differences can be as much as 0.15 Ã?Æ’ (e.g. below for the Tasmania temperature reconstruction. I don’t suppose that it matters much, but, if he’s trying to replicate, it would be easier to do little things the same. Otherwise, our proxy data set in our MBH98 replication is virtually identical to Ammann.

    I’m progressing nicely with the process of parsing Ammann. The correlation between our AD1400 emulations of the MBH98 reconstructed PC1 is 0.9993201! See illustration below. The emulations are virtually identical up to scaling/centering. W-A do not use archived MBH temperature PCs, but re-calculate them; this appears to account for scaling differences identified so far (and they should get washed out).

    The correlation between our coefficents and theirs is 0.9992717. There’s a difference in scaling - I’m not sure why right now, but I can’t see why it would matter (since it merely affects downstream coefficients).

    All in all, this is looking pretty good so far. One could scarcely have contemplated that WA should replicate our results so accurately. The irony is delicious.

    … so, back to the question!

    More than anything else, in the proxy series used to create the infamous hockey stick graph, it is dependent on the presence of stripbark BCP data from a tiny region of the world. The rest of the proxies are so weak as to have little impact on the results.

    … how does this explain the green line in figure 2 of WA06 (which HB reproduces in the post body), showing a hockey stick result when bristlecone pine series are excluded :-)

  • per // March 11, 2008 at 11:16 pm

    “Dependency on bristlecones, and the potential for decentered PCA to give low mean values of the 1400-1901AD period are separate issues that have, I think, been succesfully refuted by Wahl & Amman 06.”
    hmm. Presumably you are referring to Figure 4 of W&A, where the exclusion of bristlecones (the purple or pink lines) raise the temperature in the 1400s by 0.5 Celsius ? I am just struggling with how that is a refutation ?

  • Hank Roberts // March 11, 2008 at 11:24 pm

    This is why you have to read the primary sources. Not what other people say they said.

  • Hank Roberts // March 11, 2008 at 11:25 pm

    > high tech stocks, CA
    Well duh. Let’s see if the current stock market crash and current flattening of temperature hold up.

    Maybe spending money does correlate with burning fuel. Do ya think?

  • Lazar // March 11, 2008 at 11:28 pm

    mikep,

    M&M have done the clacualtions - see their 2005 E&E article and the answer they get is “If de-centered PC calculation is carried out (as in MBH98), then MM-type results still occur regardless of the presence or absence of the PC4 if the bristlecone pine sites are excluded, while MBH-type results occur if bristlecone pine sites (and PC4) are included.

    I suspect excluding bristlecone pine series reduces the prominence (variance) of the ‘hockey stick’ pattern which is contained in other series, and is then effectively censored by PCA.
    Even so, the hockey stick does not disappear. 15th century values in MM05b are much lower than in MM03 and do not exceed mid 20th century warmth. What changes is that the reconstruction score fails validation for the 1400AD step; it has no ’skill’ as MBH98 put it.
    Excluding bristlecone pine series and no PCA produces, again, the hockey stick, but this time the reconstruction passes (just) significance tests for 1400AD.
    All of which suggest the ‘hockey stick’ is real, and that reconstructive skill depends on its presence, which in turn depends on the presence of bristlecone pine series when doing PCA.

    Fred,

    All you’re really doing with PCA is to extract the signal, or signals, from the noise. The key part is how important the extracted signal is as a percent of the whole. PC1 is usually going to explain a lot of what there is to be explained. PC4 and lower, very little.

    Sometimes the signal is small relative to the noise… so you use a small part of the data… a danger in doing so is spurious correlation… which is why they do cross-validation.

  • cce // March 11, 2008 at 11:30 pm

    The IPCC authors are required to assign likelihoods (”unlikely,” “more likely than not,” “likely,” “very likely” etc) which have underlying probabilities. They don’t have the luxury of wishy-washy language. In the expert opinion of the TAR’s authors, AR4’s authors, and at least two of the NRC Panel’s authors, it is “likely”/66%/ or 2:1 odds that it is warmer now than at any time in the previous millennium.

  • per // March 11, 2008 at 11:40 pm

    “Note that they agreed that the statistical methods of the Hockey Stick could have been better, but what you will not find is a statement from North or anyone else on the panel saying that any of these flaws were significant or that the Hockey Stick was “bad science.””

    this is profoundly misleading; the NRC panel was NOT an investigation into MBH, but into the science of reconstructions. They didn’t opine on the conduct of MBH, or say that MBH was good (saintly ?) or bad (evil ?). So your idea that you can read something into the NRC’s failure to criticise MBH is misguided.

    What the NRC panel did do is set out good practice, as opposed to bad practice. And here, they identified several issues of bad practice (which are used in MBH). Selection of proxies, particular proxies, PCA methods, verification statistics; these should all be other than the methods used in MBH.

  • David Holland // March 11, 2008 at 11:51 pm

    cce, I have the transcript.
    At no time and in no place did the NRC Panel say the peer- reviewed studies of M&M or Wegman were “bad science”. Sure Gerry North didn’t like social network analysis but he made the point that they had not looked at it and he did say in the verbal session and under oath (page 74) that he did not dispute the methodology or the conclusions of Wegman. That is a fact. Lets be fair, when he first saw the “hockey stick” North is reported to have said in 2000,
    ” There are too many independent pieces of evidence, and there’s not a single piece of contradictory evidence,. . . . The planet had been cooling slowly until 120 years ago, when, bam!, it jumps up, . . . We’ve been breaking our backs on [greenhouse] detection, but I found the 1000-year records more convincing than any of our detection studies.”

    North and most of the NRC panel are on the record as “believers”. Only other “believers” think they exonerated Mann et al. I think it is to their credit that they said what they did and to the eternal shame of the IPCC that they said what they did.

    Its late in the UK so I’m signing off but I’ll look in ASAP .

  • Nick Moon // March 11, 2008 at 11:55 pm

    It’s no great surprise that when you do an MBH style PCA on some hockey stick data it produces a hockey stick. (Both groups - the hockey team and the climate sceptics would have predicted that). But it’s slightly surprising that when you do a straight PCA (ie as per MM) on your artificial hockey stick data you don’t get a hockey stick.

    That’s worth thinking about, it’s the unexpected results that should make us sit up. If you took ahockey stick and then synthesised artificial proxies from it - by adding different amounts of data - the first principal component should be the best correlated information within the data - so why isn’t it the hockey stick?

    Then I notice from some of your annotations of various comments that the proxies aren’t just composed of hockey stick and random data. You also have some additional data signal called ‘other influence’ which you’ve added in.

    So I think you need to show us a graph of your ‘other influence’ data perhaps alongside your second (MM style) PC1 graph.

    If it turns out they match - then you really have led us all on a wild goose chase :-)

    [Response: I think you need to look at Wahl & Amman. When you do straight PCA you *do* get a hockey stick, unless you make yet another mistake as MM did. When you do NO PCA you get a hockey stick.]

  • Lazar // March 12, 2008 at 12:05 am

    As the AR4 notes;

    McIntyre and McKitrick (2005a,b) raised further concerns about the details of the Mann et al. (1998) method, principally relating to the independent verification of the reconstruction against 19th-century instrumental temperature data and to the extraction of the dominant modes of variability present in a network of western North American tree ring chronologies, using Principal Components Analysis. The latter may have some theoretical foundation, but Wahl and Amman (2006) also show that the impact on the amplitude of the final reconstruction is very small (~0.05°C; for further discussion of these issues see also Huybers, 2005; McIntyre and McKitrick, 2005c,d; von Storch and Zorita, 2005).

    So, it doesn’t work in practice, does it work in theory?

  • cce // March 12, 2008 at 12:16 am

    It is profoundly misleading to use the NRC report to discredit the MBH papers, which is something skeptics do a the drop of a hat.

    The methods used were reasonable and the flaws discovered to date are not significant. That is the truth that skeptics need to acquaint themselves with. The existence of flaws does not make the science bad, or the conclusions invalid.

  • cce // March 12, 2008 at 1:03 am

    David, I wasn’t talking about Wegman or MM’s statistics (and BTW, MM have one peer reviewed paper). I was talking about the Mann papers and the contention that they were “bad science” (as Wegman alleges). i.e. “method wrong + answer correct = bad science.” What 10 years, congressional hearings, an NRC report, and several followup papers have concluded is the methods weren’t the best, but not “wrong” no matter what kind of games people play with words.

    And, of course North believes AGW, no doubt due to the overwhelming amount of evidence behind it. Wegman, on the other hand, apparently finds “no net warming since ‘98″ to be a convincing argument against.

  • TCO // March 12, 2008 at 1:05 am

    [Q]Perhaps, but I’d say just as (if not more) important is leaning to recognize ones own limitations and ignorance (especially outside one’s own narrow field).

    Sometimes (more often than not?) when one attempts to characterize the current state of a scientific area that is not one’s own, one merely makes a fool of oneself.

    Even Nobel caliber scientists have fallen into this trap.[/Q]

    George, I agree with that. I’m not mostly trying to defend someone, but to explore issues. There are all kinds of generality versus example, necessary versus sufficient etc. But at the end of the day, life should be about being a critical thinker. that’s what our grade school teachers wanted.

  • Chris O'Neill // March 12, 2008 at 1:13 am

    per:

    For the record, the fourteen similar studies have many of the same problems as MBH. That is why theNAS panel concluded right in the summary, that the error in reconstructions going back before thermometers is unquantifiable. In science terms, it is difficult to think of a more damning criticism.

    This is what the NAS panel actually said in their summary:

    The uncertainties associated with reconstructing hemispheric mean or global mean temperatures from these data increase substantially backward in time through this period and are not yet fully quantified.

    We can’t trust anything per says.

  • TCO // March 12, 2008 at 1:55 am

    TCO evaluation of most recent McI posting. Much terser this time. Thank God.

    A. Paragraphs starting out “As has previously been said” can be excised with no loss in information and a gain in style. This case is no exception.

    B. Poor SM has been so pre-occupied by irrelevant arguments that he can not address interesting ones. I gues that’s why he’s had time to write 1000 blog posts since his last (and only) real science paper. The horrors of those debaters on the other side. It’s all their fault that McI can’t do real work.

    C. McI fills in needless characterizations like “breathlessly reports”, when he could better say “says”. Reading stuff in the peer reviewed literature would be a pleasure because they would cut all that crap out.

    D. Buncha good points by McI on the “what Tammy claimed that McI claimed”. Kinda misses the science issues. But seems to cast doubt on Tammy doing proper reading of McI. For what that’s worth. A lot to McI, I guess. He’s more interested in defending honor or destroying it than in learning math.

    E. Not sure if this affects the whole 4 versus 1 PC thingie, but McI glides past explanation of his change of TWO FACTORS at one time (correlation versus covariance and centering versus decentering). Huybers nailed him well for that.

  • Chris O'Neill // March 12, 2008 at 2:22 am

    cce:

    Note that they (the NRC panel) agreed that the statistical methods of the Hockey Stick (MBH9x) could have been better,

    Which indeed is now done and is now usual practice, e.g.:

    Rutherford, S., M.E. Mann, T.J. Osborn, R.S. Bradley, K.R. Briffa, M.K. Hughes, and P.D. Jones. 2005.
    “Proxy-based Northern Hemisphere surface temperature reconstructions: sensitivity to method, predictor network, target season, and target domain.” Journal of Climate18:2308-2329.

    Discussions of out-of-date methods such as PCA are sensibly of academic or historical interest only.

  • dhogaza // March 12, 2008 at 3:01 am

    Wegman, on the other hand, apparently finds “no net warming since ‘98″ to be a convincing argument against.

    And that CO2, because of its mass, is concentrated disproportionately at the surface, where it’s going to kill us all undoubtably as we add more to the atmosphere.

    Imagine, Wegman has “broken the hockey stick”, has also shown us that global warming isn’t happening because he agrees with a statement that cherry-picks 1998, and now has shown us that the REAL danger from increased CO2 levels is suffocation!

    Wow. It’s quite amazing.

  • cce // March 12, 2008 at 3:48 am

    Since my comment about averaging the proxies is being discussed on CA, I will clarify that the proxies have to be weighted by area.

    WA scenario 3 (above) shows the affect of removing the BCPs.

  • fred // March 12, 2008 at 6:50 am

    Well, the bottom line, at least before deadlines permit me to come to grips with R, is that no-one has been able or willing to supply a stats text or article in which decentered PCA is either justified or explained in sufficient specificity that you can tell exactly how and when to implement it.

    No-one has come forward and said these are the other areas it is routinely used in - medicine, finance, construction …etc. And one can understand why, it does not seem to have any theoretical validity.

    No-one has been able to explain why it is not significant that the difference between standard and decentered PCA is that the HS emerges either as PC1 or PC4. This seems to be a key issue. Its the difference between saying that high cholesterol level is the best predictor of heart attacks, and saying that 80% of the incidence is accounted for by genetic heritage, and cholesterol level is a minor contributing factor in some cases.

    No-one has refuted the claim that decentered produces HSs at high PC levels from a set of series of which the HS shape is a tiny proportion.

    Specifically, McKittrick’s claim about weighting has not been addressed. The claim you recall is that a few HS shaped proxies are given a weight around 400 times greater than others by this method and gives rise to the remark that if some proxies are such very good indicators, why not use only them?

    If we just focus on the point at issue: was the statistical treatment of their data by MBH a legitimate and correct one, the answer so far is no. They didn’t do it right.

    If your surgeon recommended you undergo a given procedure on the basis of this kind of evidence, you would go elsewhere.

    Its counter productive to defend this stuff any more. It just gives ammunition to skeptics. The right thing to do polemically is admit MBH is wrong, and move on. Until that is done, its going to distract attention from the critical issue, which seems to be CO2 sensitivity.

    Tamino, it is probably necessary to have one more post about PCA, which looks like it may turn out to be a difficult one to write. But perhaps the next topic to get to would be CO2 sensitivity. This is surely the core issue in AGW today?

    [Response: I had actually started working on a post about climate sensitivity, but got seriously sidetracked. Next is sea level, then the final (let's hope!) installment on PCA, then it would indeed be good to address the issue of sensitivity; it is indeed one of the core scientific issues.]

  • James // March 12, 2008 at 9:06 am

    [blockquote]

    cce:

    Note that they (the NRC panel) agreed that the statistical methods of the Hockey Stick (MBH9x) could have been better,

    Which indeed is now done and is now usual practice, e.g.:

    Rutherford, S., M.E. Mann, T.J. Osborn, R.S. Bradley, K.R. Briffa, M.K. Hughes, and P.D. Jones. 2005.
    “Proxy-based Northern Hemisphere surface temperature reconstructions: sensitivity to method, predictor network, target season, and target domain.” Journal of Climate18:2308-2329.

    Discussions of out-of-date methods such as PCA are sensibly of academic or historical interest only. [/blockquote]

    Oh, come on, Rutherford et al (co-authors include MB & H) recycle the MBH proxies.

    I’m amazed by the concept that scientific papers have some sort of use-by date. If it is crap now, it was crap then.

  • David Holland // March 12, 2008 at 9:18 am

    Chris,

    After all the huffing and puffing, Rutherford et al only goes from 1400 AD to - well you tell me. It disappears on the IPCC Fig 6.10 about the same time as Briffa’s. None of these reconstructions, which the NRC say are “murky” before 1400 show the the warming of the recent decades that their authors say they prove to be exceptional over 1300 years.

    It not just PCA that is out of date. So are the proxies that are used. Not only are they poor indicators of the past no one is confident enough of their ability to tell the future to go back and update them for the last 3 decades or so. The match between these proxies and the instrumental record is pathetic. In Mann’s case it was so pathetic from 1854 to 1902 that he did not plot it in the TAR.

    I do not want to discourteous but this is not what I call science.

  • Nick Moon // March 12, 2008 at 9:20 am

    [quote]Response: I think you need to look at Wahl & Amman. When you do straight PCA you *do* get a hockey stick, unless you make yet another mistake as MM did. When you do NO PCA you get a hockey stick.[/quote]

    I think you missed my point. I don’t need to look at WA - I wasn’t talking about the real world - I was talking about Tamino’s virtual world. IN your world, you know that the temperature followed a hockey stick. It’s your world, you are it’s Creator - and you are all knowing - in that world ;-) You created a set of ‘temperature’ proxies using a Hockey Stick curve and random errors. But when you did your second PCA (zero’ing over the entire dataset), the Hockey Stick didn’t show up - at least as PC1.

    Look at the PC1 you did get and look at your ‘other influence’ data - are they the same?

    If they are then you’ve just demonstrated exactly why centereing over the entire dataset is the right thing to do and the MBH way is wrong.

    If I’m right, you have inadvertently created a set of proxies which actually aren’t very good temperature proxies - they are slightly better proxies for ‘other influence’. That might be a bit like using tree-ring data that turned out to be a better proxy for, say, rainfall than temperature.

    And the MBH PCA only spots the hockey stick but the more orthodox PCA quite rightly identifies all the signals in the data and weights them appropriately.

    Show your ‘other influence’ data :-)

  • Chris O'Neill // March 12, 2008 at 9:27 am

    mikep:

    But we just get back to the point that in MBH nearly all the hockey stick series are bristlecone pines. The reconstruction therefore depends not on the whole proxy set but on a tiny subset,

    This is absolute garbage. The proxy with the highest weight in the MBH98 1400 network reconstruction is treeline 11, followed by noamer PC01 (which includes the bristlecones). For the record, the proxies and their relative weighting (obtained using Wahl and Ammann’s MBH98 emulation) in the 1400 network reconstruction are:

    “treeline 11″, 7.19
    “noamer PC01″, 5.69
    “quelc1-o18 0.5″, 3.67
    “quelc2-o18 0.5″, 3.67
    “fenno-new”, 3.61
    “tasmania”, 3.60
    “quelc2-accum 0.5″, 3.20
    “moro007 0.5″, -2.93
    “noamer PC02″,2.58
    “fran010 0.33″,-2.34
    “npatagonia 0.75″,2.3
    “svalbard”,-2.27
    “westgreen-o18 0.5″,1.98
    “fran009 0.33″,-1.64
    “seprecip-ga 0.33″,1.23
    “quelc1-accum 0.5″,-1.11
    “Stahle-sw PC01″,1.08
    “yakut 1.5″,-0.86
    “urals-new”,-0.53
    “seprecip-sc 0.33″,0.48
    “moro008 0.5″,0.38
    “seprecip-nc 0.33″,-0.04

    I can’t see the weighting concentrated on a “tiny subset” here.

  • John A // March 12, 2008 at 9:47 am

    Tamino:

    Response: I think you need to look at Wahl & Amman. When you do straight PCA you *do* get a hockey stick, unless you make yet another mistake as MM did. When you do NO PCA you get a hockey stick

    You *do* get a Hockey Stick if the BCPs are included. If they are excluded then even a decentered Mannian PCA can’t produce a Hockey Stick.

    All of this is covered in M&M (E&E, 2005).

    Oh, and Wahl & Amman confirmed that the verification R2 was ~0 meaning the model had no skill.

    So where’s the beef, Tamino?

    The BCPs are central to the Hockey Stick shape and without them, even the Mannian PCA won’t find a Hockey Stick shape to mine. With the BCPs with proper centering, the Hockey Stick appears in the PC4. So what? The BCPs produce the Hockey Stick shape, but they are not temperature proxies - therefore the correlation between the Hockey Stick and the instrumental “global mean temperature” is a spurious correlation and meaningless.

    Back to you Tamino. We’re still waiting for some insight.

  • David Holland // March 12, 2008 at 9:51 am

    cce

    About Enrico Fermi.

    I was not around at that time, but the history that I have read does not speak of consensuses of thousands and settled science. Certainly there were no enviros hectoring from the sidelines. There were unquestionably “cliques” in the US, UK Germany and probably Russia, but they were in competition. No one was sure until the bomb worked. Multiple research paths were followed and we did not have monopoly organisation telling us or the scientists what the “truth” was. The public was told very little.

    I have no problem with “cliques” in science or say in our political parties, police or public prosecutors office. They are bound to occur. My problem would be when those “cliques” include people in our judiciary.

    If it is to be trusted by those that have deep and conscientious concerns about climate science as well those content to believe what they are told, the IPCC, which is the judiciary of climate science, should be independent of the “cliques”. It is not.

  • Lazar // March 12, 2008 at 9:56 am

    Describing the effects of removing bristlecone pine series, Steve McIntyre’s characterization seems to have led some of his readers to believe the hockey stick shape disappears. This is simply not true.

    If you…

    a) directly exclude bcp series, and do MBH decentered calculations, include PC1 and PC2, or

    b) directly exclude bcp series, and do MM centered and standardized PCA, include PC1 and PC2, or

    c) directly exclude bcp series, and do MM centerd and not standardized PCA, include PC1 and PC2, or

    d) directly exclude bcp series and do not do PCA at all, or

    e) indirectly exclude bcp series by doing MM centered and not standardized PCA, include PC1 and PC2

    you still get the hockey stick shape, with the possible exception of c), a low and flat 15th century warmth relative to 20th century trend, i.e. the ’stick’ and the ‘blade’.

    In the original MBH reconstruction, peak 15th centure warmth is about 0.7 degC lower than the late 20th century. By excluding bcp, that changes to…

    a) ~ 0.5 degC
    b) ~ 0.5 degC
    c) ~ 0.3 degC
    d) ~ 0.6 degC
    e) ~ 0.5 degC

    The meaningful impact is on verification scores such as the reconstruction fails validation, but this does not occur for example e), and it only occurs in the other examples for the 1400-1450AD period, all examples pass validation from 1450AD onward.

    See Wahl & Amman 2006, scenarios 3, 5 (d), and 6 (a,b,c), and figures 2, 3 and 4.

    Here’s how Steve McIntyre describes it…

    If a centered PC calculation on the North American network is carried out (as we advocate), then MM-type results occur if the first 2 NOAMER PCs are used in the AD1400 network (the number as used in MBH98), while MBH-type results occur if the NOAMER network is expanded to 5 PCs in the AD1400 segment (as proposed in Mann et al., 2004b, 2004d). Specifically, MBH-type results occur as long as the PC4 is retained, while MM-type results occur in any combination which excludes the PC4. Hence their conclusion about the uniqueness of the late 20th century climate hinges on the inclusion of a low-order PC series that only accounts for 8 percent of the variance of one proxy roster.

    and he cites Wegman…

    Without attempting to describe the technical detail, the bottom line is that, in the MBH original, the hockey stick emerged in PC1 from the bristlecone/foxtail pines. If one centers the data properly the hockey stick does not emerge until PC4. Thus, a substantial change in strategy is required in the MBH reconstruction in order to achieve the hockey stick, a strategy which was specifically eschewed in MBH. In Wahl and Ammann’s own words, the centering does significantly affect the results

    which leads JohnA to the conclusion…

    without that one proxy in the network, the decentered method has no hockey stick shapes to mine, and no hockey stick results

    The BCPs are central to the Hockey Stick shape and without them, even the Mannian PCA won’t find a Hockey Stick shape to mine.

    Mike B…

    the hockey stick IS the bristlecone pines, and that the bristlecone pines ARE the hockey stick PC.

    Did Mike Mann manufacture the Hockey Stick? No. But he did sort through a large pile of branches and roots until he found one that looked like a Hockey Stick, tossed out the rest, hoisted the HS above his head and then ran through the streets of Athens yelling “Eureka!”

    Ross McKitrick…

    if you take out the BCPs the hockey stick disappears

    Steven Mosher…

    They still think it’s about the BLADE. It’s the shaft, the flat shaft.

    Still we’re at comment #38 and none of the stats geniuses who I am assured are knowledgeable on this issue have bothered to correct misconceptions.

    By the way, the statement in the MM05b paper;

    In the MBH98 de-centered PC calculation, a small group of 20 primarily bristlecone pine sites, all but one of which were collected by Donald Graybill and which exhibit an unexplained 20th century growth spurt (see Section 5 below), dominate the PC1. Only 14 such chronologies account for over 93% of the variance in the PC1, effectively omitting the influence of the other 56 proxies in the network.

    … is flat out wrong, as PC2 is also selected.

  • per // March 12, 2008 at 10:20 am

    Chris O’Neill may want to explain how something that is “not yet fully quantified” can be quantified. If you cannot (yet, fully, …) quantify something, it is unquantifiable.

    “Discussions of out-of-date methods such as PCA…”
    unfortunately, science doesn’t work like that. PCA is a perfectly good method, and is not out of date. The method of MBH 98 was either appropriate (and doesn’t need changing), or had problems, in which case the problems must be identified and addressed. The notion that they have moved to a completely different method, but their original method was good, is not consistent.

    Finally, wahl and ammann provide a table 2, which shows their various scenarios. W&A emphasise that the bristlecones often show no relationship to local temperature. scenario 3 is no pc and no bristlecones. scenario 6 is no bristlecones/gaspe and PC. there are substantial differences between this and mbh 98, as for scenarios 1, 3 also

  • sdw // March 12, 2008 at 10:53 am

    hi Tamino and guests,

    I’m a lurker, and just want say thanks for your posts. I understand this is your blog, and you can do with it as you wish, but perhaps you might like a viewer suggestion.
    Please don’t censure the discussions. This is not what one sees in the engineering/science/political posts at CA, rather only here and at RC.

    I have a science degree, an engineering degree and writing up my doctoral thesis and if these studies have taught me one thing, it is that the only ‘evil’ in science is the suppression of argumentation.

    I always hear that censoring is required, because one can’t argue with ridiculous assertions, however this is in itself a terrible notion. Whether you like it or not, the readers at CA are scientists, engineers and professionals that hold an opposing view and the scientific merit of these views will only be established via full and open discussion.

    I really do wish that everyone would just grow up, and get back to our core passion, that is, the discovery of natural truths unbiased from extraneous factors.

    best regards, SDW

    [Response: It should be crystal clear just from reading the comments here, that I don't censor dissenting opinions. I do censor nonsense and irrelevancy, and when a pompous ass (certainly not referring to you) leaves personal insults at my door he should expect his comments to vanish and he may just be banned.]

  • Armagh Geddon // March 12, 2008 at 11:50 am

    Hey TCO,

    Seems that you are casting yourself as an ‘informed critic’ rather than a producer/director. I would be interested to see your efforts at documenting the issues as you see them.

  • george // March 12, 2008 at 12:00 pm

    To my “Even Nobel caliber scientists have fallen into >>this trap.”
    TCO replies:

    I agree with that. I’m not mostly trying to defend someone, but to explore issues. There are all kinds of generality versus example, necessary versus sufficient etc. But at the end of the day, life should be about being a critical thinker. that’s what our grade school teachers wanted.

    Context, context, context.

    We were (or at least I was) specifically discussing people (like McIntyre) who venture far afield from their area of expertise to expound upon the (dismal?) state of climate science or one of its subfields (eg, dendrochronology).

    A PhD (or even MS) may give a person “balls” (your word), but so do steroids.

    Being a “critical thinker” involves more than just “being critical”. The second part seems to get lost on some.

  • MrPete // March 12, 2008 at 12:03 pm

    dhogaza, there are five relevant possibilities, as I’ve posted somewhere in the recent past: AGW, NGW (natural global warm…), NGR (randomness), NGC, AGC (seems highly unlikely, eh!)

    In assessing AGW, IPCC clearly avoids significant discussion of serious evidence for any other scenario, including the null hypothesis, and thus leaves itself open to a form of selection bias.

    Thus, even if I’m generous enough to say they’re not officially promoting one view, the effect can easily end up being the same.

    Lucia’s got an interesting calculation of 21st century trend data, with CI’s, showing that the actual data from 2001 on appears to fall completely outside the IPCC range of possibilities. Just one line of evidence that something might be fishy.

  • Peter Thompson // March 12, 2008 at 12:13 pm

    TCO @ 1:55 E) MM reply to Huybers as published in GRL deals specifically and clearly with your point, it’s linked on CA, McI assumes people can and will take the time to read available info.

  • David Holland // March 12, 2008 at 12:26 pm

    cce, you say, “The IPCC authors are required to assign likelihoods”

    They are not. You can find the internationally agreed “Principles Governing IPCC Work”, on the IPCC website. They say,

    “The role of the IPCC is to assess on a comprehensive, objective, open and transparent basis the scientific, technical and socio-economic information relevant to understanding the scientific basis of risk of human-induced climate change, . . .”

    The NRC conclusion that we can not as yet put a numerical probability on reconstructing ancient temperatures is a valid peer-reviewed conclusion, not from a bunch of sceptics but from 12 of the best and most respected scientists in the US who are honest enough to say we think its warmer now than ever it is not possible to say how likely we are right.

    I have no problem with the “hockey team” (just look at the list of lead authors of Ch 6) at the IPCC concluding something different but they should follow the agreed Principles that say,

    “Differing views on matters of a scientific, technical or socio -economic nature shall, as appropriate in the context, be represented in the scientific, technical or socio-economic document concerned”

    That is what the authors are “required” to do. The Review Editors are the umpires and under the Principles they are “required” to,

    “ensure that all substantive expert and government review comments are afforded appropriate consideration, advise lead authors on how to handle contentious/controversial issues and ensure genuine controversies are reflected adequately in the text of the Report.”

    But hey, all the WGI Review Editors that matter are in the “team” and since no one, certainly not the governments that pay for this pantomime, reads the reports they are “required” to submit, they say little or nothing about the sham that passes for expert review. The treatment of the reconstructions is risible. Mitchell says more than the rest saying,

    “There will inevitably remain some disagreement on how they have dealt with the reconstructions of the last 1000 years”

    Too right! But where in the IPCC report do the authors explain it? Less than a fifth of a page. And when the Reviewer for the Govt of the USA says that Wahl and Amman should be scrubbed because when it was considered and reviewed it didn’t have the verification tables it need to pass peer review and which corroborate M&M, how did the authors respond? They said “Rejected. Its allowed under the rules.” Yey, right!

    If the IPCC was under UK jurisdiction rather than the UN’s, AR4 WGI Chapter 6 would be challenged in the Court.

    I am pleasantly surprised, and grateful, not to have felt the Bulldog’s teeth in my neck but must now turn to other matters. I doubt I will convert many of you and unless I see some statistically valid, and full archived, science you won’t convert me, not from denying anything – I don’t - but from doubting that that there is any evidence that would be accepted outside “the team” for alarming AGW. But as North says, that does not mean it isn’t true. Incidentally, my car does 50 to our English gallons, my wife’s does 60 mpg, and between us we only do 10k miles a year. We are double glazed fully insulated and I haven’t flown for ages. But I can’t stop China building two coal fired stations a week, so heck, I admit it – I hope you guys are wrong.

  • David Holland // March 12, 2008 at 12:34 pm

    Sorry guys should have been a “but” in line 12!

  • MrPete // March 12, 2008 at 12:36 pm

    lazar,
    My first observation of W&A’06 is that they felt free to make some significant adjustments in their work: they did some simplifications in their replication of MBH, and used a different basic approach to calibration/verification vs M&M (disagreeing with M&M’s). I’m in no position to evaluate the arguments on that, but can only observe that there’s a potential for apples and oranges here. It may be stated as “the same” or “no substantial difference” but when the protagonists themselves describe the changes they’ve made, I don’t believe any of us who lack *serious* stats background can evaluate if those changes are significant or minor.

    W&A claim they reproduced the MBH results, M&M say they came close but did not achieve reproduction. Can we say who is correct? One thing I appreciate about Steve M’s approach: when comparing two chronologies, he typically shows not only the two graphs but also the difference, which allows the reader to quickly see how well the two curves match. A quick look at W&A figure 1 says “close but not quite” to me. Is it significant? I dunno.

    Now with respect to the repeatedly-questions “green line” of W&A figure 2. As I said earlier, it’s hard for me to read this graph very well– the green line is behind other lines. I wish it had been separately reproduced!

    But I do refer you to M&M’s own isolated graph of the exact same data (p10, fig 6), done in 2003. Don’t have the underlying data for either one. Eyeballing W&A06 green line and M&M’s figure six — they look essentially the same to me. (BTW, I don’t assume the green line extends all the way to the present. It can’t, any more than the light blue line can extend into the distant past.)

    Also note another set of W&A’s own results similarly showing that leaving BCP’s out produces essentially trendless noise.

    Not sure what the argument is over the green line.

    Anyway, it’s been fun. I’ve got some pressing Real World challenges. I know I’ve left one or two loose threads, and hope to get back sooner than later. Hope so! A good “vigorous discussion” :-)

    [Response: What you fail to mention is that in the graphs you link to, the curves without a hockey stick are labelled "without merit." That means they failed verification testing.]

  • Meltwater // March 12, 2008 at 1:04 pm

    fred said:

    There are a number of papers (naturally from authors who were instantly then labelled denialists, if they had not already been!) which argue that the total sensitivity of global temperatures to a doubling of CO2 is around 1 degree.

    Please feel free to cite any papers whose conclusions you think we should consider.

    Watson 2007 warns that ‘present models tend to under-predict the eventual, equilibrium climate change due to a given increase in atmospheric CO2’ and that ‘uncertainty will only start to decrease as we actually observe what happens to the climate’.

    Watson 2007 agrees with you, fred, that ‘while the basic mechanism of greenhouse-gas forcing of climate is well understood, the multiple, mostly positive, feedback loops that amplify this effect are not’. Unlike you, however, Watson looks for the ‘combined effect of many of these feedbacks’ in ‘the record of past climate’ where the results indicate high, not low, sensitivity to CO2 doubling.

  • dean_1230 // March 12, 2008 at 1:37 pm

    TCO said:

    “D. Buncha good points by McI on the “what Tammy claimed that McI claimed”. Kinda misses the science issues. But seems to cast doubt on Tammy doing proper reading of McI. For what that’s worth. A lot to McI, I guess. He’s more interested in defending honor or destroying it than in learning math.”

    I agree that it misses the science issue, but it directly gets at Tamino’s assertion that MM is fundamentally flawed. Here’s what Tamino said about MM’s method:

    “I’d guess that some of you are thinking, “Can it really be that simple? Did MM really not get this? Did they really discard the relevant PCs just to copy the bare number of PCs used by MBH, without realizing that the different centering convention could move the relevant information up or down the PC list?”

    You betcha. When done properly on the actual data, using 5 PCs rather than just 2, the hockey stick pattern is still there even with centered PC — which is no surprise, because it’s not an artifact of the analysis method, it’s a pattern in the data.”

    Tamino clearly implies that MM’s paper had no hockey stick because they selectively ignored it. That’s just not true! They didn’t ignore it. They showed it. They just showed it in PC4 and said the relevance was around 8%. You comment that McI is more interested in defending his honor… but it seems to me that he’s most interested in making sure his work is accurately described. There’s no shame in that goal and it’s strange that you imply there is.

    As to your point about missing the science, I don’t think that’s the point of this whole series of articles. This series of articles is about statistical methodologies, not science.

    and to everyone (cce, for one) who has said that the science isn’t bad if you got the “right” answer using a bad method, I wholeheartedly disagree. If you used a bad method, you have no idea if the answer is correct. The scientific method depends on making sure you use the right method. And advances are made when the methods improve. The method is everything in science!

  • Barton Paul Levenson // March 12, 2008 at 2:04 pm

    fred posts:

    [[If anyone wants to check out BPL’s statement, the report is here:

    http://www.nap.edu/catalog.php?record_id=11676

    It would be helpful to have a reference for where the fourteen other studies replicating MBH are mentioned. I don’t recall them from a first reading, and didn’t find them on a superficial second glance. Which does not prove they are not there. But it would help if someone could point to exactly where they are.]]

    Try pages 111 and following.

  • Barton Paul Levenson // March 12, 2008 at 2:18 pm

    David Holland writes:

    [[North and most of the NRC panel are on the record as “believers”. ]]

    Yes, that’s so true, and it’s so disgraceful. The same thing happened to me when a panel considered my electro-narco-magnetic universe theory (ENMU)! All the panelists were relativity believers! But they were believed just because they had Ph.D.s in physics and I was an unemployed security guard, typing for 18 hours per day in a tiny room with a single naked lightbulb hanging overhead from a frayed cord. This kind of thing is what holds back science from the brilliant advances of the unconventional thinker. Galileo… Velikovsky… burned Copernicus at the stake… vindication… enshrined in the pantheon of supergeniuses!!!!!!!!

  • luminous beauty // March 12, 2008 at 3:05 pm

    From MBH98:

    “We isolate the dominant patterns of the instrumental surface-temperature data through principal component analysis.”

    That is a centered PCA over the whole of the calibration period to which the proxy indicators are then calibrated.

    There is no PCA of the proxies.

    The notion that it is a decentered pca of the proxies is comparing apples to road apples.

    M&M and Wegman are out of their trees and rooting around in manure.

  • per // March 12, 2008 at 5:04 pm

    “In the original MBH reconstruction, peak 15th centure warmth is about 0.7 degC lower than the late 20th century. By excluding bcp, that changes to…

    a) ~ 0.5 degC
    b) ~ 0.5 degC
    c) ~ 0.3 degC
    d) ~ 0.6 degC
    e) ~ 0.5 degC”

    err, yes, you got that right. If you take out a couple of californian tree proxies, the whole temperature of the northern hemisphere changes by 0.3-0.6C. And you are suggesting that this method is credible ?

    I am also fascinated by your analysis of verification statistics. The fact that a particular data set make the data “significant” is not an argument for saying that the data set should be included. The fact that you “need” bristlecones in the reconstruction (which show no relationship with their local temperature) to get the whole thing to give a “significant” result, is a fairly severe indictment of the method.

  • per // March 12, 2008 at 5:33 pm

    i would be interested in Tamino’s perspective. Tamino particularly mentioned Jolliffe as an acknowledged expert, that we should listen to.

    David Holland // March 11, 2008 at 5:08 pm
    specifically notes that he asked Jolliffe about PCA and MBH. According to Holland, Jolliffe specifically refuses to endorse the methodology of MBH’98, and even states that he was unable to understand the description of the methodology in MBH’98.
    Is there anything here that would give you cause for concern ?

    [Response: If I recall correctly, Jolliffe stated that he didn't understand the methodology adequately to say whether it was valid or not. That argues persuasively for his honesty, and even admirable humility.

    Your comment seems to imply that Jolliffe made some damning indictment of the methodology. That's cause for concern.]

  • dhogaza // March 12, 2008 at 5:56 pm

    Please don’t censure the discussions. This is not what one sees in the engineering/science/political posts at CA, rather only here and at RC.

    McIntyre deletes posts, and edits others.

    What are you talking about?

  • dhogaza // March 12, 2008 at 6:02 pm

    About Enrico Fermi.

    I was not around at that time, but the history that I have read does not speak of consensuses of thousands and settled science. Certainly there were no enviros hectoring from the sidelines. There were unquestionably “cliques” in the US, UK Germany and probably Russia, but they were in competition. No one was sure until the bomb worked.

    Not sure why this is relevant, but the physicists were sure of the physics, and in the case of the uranium gun design (little boy) so certain of the engineering that they didn’t bother testing it before dropping it on Hiroshima.

    In the case of the plutonium implosion design, the physics was certain, it was the engineering, particularly of the conventional explosives and the highly synchronized fusing that was in doubt.

    Like so many denialist claims, upon inspection this one proves to be false.

  • cce // March 12, 2008 at 7:15 pm

    Some choice quotes from the AR4 WG1 Uncertainty Guidance
    http://ipcc-wg1.ucar.edu/wg1/Report/AR4_UncertaintyGuidanceNote.pdf

    “Be prepared to make expert judgments and explain those by providing a traceable account of the steps used to arrive at estimates of uncertainty or confidence for key findings”

    “Develop clear statements for key findings that are quantitative and give explicit time frames as far as possible”

    “A likelihood or probability of occurrence can be determined for an event or for representative
    outcomes, e.g. based on multiple observations, model ensemble runs, or expert judgment: State any assumptions made and estimate the role of structural uncertainties. Describe likelihoods using the calibrated language given in Table 4 or present them quantitatively”

    “To avoid the uncertainty perceived by the reader being different from that intended, use language that minimizes possible misinterpretation and ambiguity. Note that terms such as “virtually certain”, “probable”, or “likely”, can engage the reader effectively, but may be interpreted very differently by different people unless some calibration scale is provided.”

    Note table 3 and table 4.

    Scientists might like the word “plausible” but it is isn’t very useful for policy decisions. When AR4 authors use such descriptions, they come with numbers attached.

    As far as the appropriateness of the AR4 reviewers are concerned, I am forced to wonder about the credibility of the reviewers of a “journal” like E&E.

  • MrPete // March 12, 2008 at 7:42 pm

    Tamino responded “What you fail to mention is that in the graphs you link to, the curves without a hockey stick are labelled “without merit.” That means they failed verification testing.

    If I’m understanding this whole thing reasonably well at a high level, that’s part of the point.

    If (for sake of analysis) we accept that

    a) the MBH method highly weights a particular data series (NA tree rings)…

    b) That data series does link to the calibration data.

    c) The other data may or may not link to the calibration data.

    Then would it not make sense that

    d) with the “heavily weighted” data in place there’s good verification, and

    e) without that data, bad verification simply means the other data may not be a good match for the calibration data?

    Or am I way off base?

    (And, am I correct in understanding that even if everything verifies nicely, according to the experts who have weighed in on these methods, we’ve really learned nothing other than a clue as to which proxy series might have meaning with respect to the question at hand? That some serious further insight is needed to apply physical meaning to the statistical correlation.)

    Back to my day job :)

  • TCO // March 12, 2008 at 10:24 pm

    armagh:

    Definitely a sidewalk supervisor, not a producer.

    I have written a lot about various things as I read them, primarily on Climate Audit. You can read those posts (many old ones). I don’t think it’s appropriate to wreck this thread with an “ask TCO”. We can take this to “Open” if you want, or go to some other blog, like Climate Skeptic or BigCityLiberal where a lot of free play is allowed. Cool, man?

  • TCO // March 12, 2008 at 10:29 pm

    George: I know that your context of interest is McI and is he qualified or not, right or not. Because I know how you view things, I gave preemptory caveats. I say again, my interest is not purely in McI defense or excortiation, but in thinking about how to think. Within that dimension, the question of how we critically examine things, how much expertise is required, etc. is a (to me) profoundly interesting one. I read something the other day that said that the smarter someone is (or maybe it was the more expertise they have), the more knowledgeable of the limitations in their understanding they are.

    [Response: Which flatters Jolliffe in the extreme. As far as I can tell, he's the only one to state that he didn't understand the process well enough to opine on whether or not it's valid -- yet he seems to be the one person everyone agrees is expert on the subject of PCA in general.]

  • TCO // March 12, 2008 at 10:32 pm

    Pete: If you read the old threads on CA, you will find evidence that I have read and thought a lot about the McI response. I could still be wrong of course. But I have read the thing. BTW, I have also corresponded with Huybers.

  • mikep // March 12, 2008 at 11:57 pm

    Luminous beauty before you accuse people of being out of their trees and rooting around in manure you ought to do your home work. MBH use PCA -type analysis for both temperature and proxy data. The point is that they have too many temperature observations and too many proxies to work with. The point of the temperature PCAs is to have something to calibrate the proxy PCAs against.

  • Lazar // March 13, 2008 at 12:52 am

    per,

    If you take out a couple of californian tree proxies,

    14 proxies.

    the whole temperature of the northern hemisphere

    The average reconstructed temperature over approximately five non-contiguous years in the 15th century.

    changes by 0.3-0.6C.

    Changes by 0.1-0.4 C.

    0.7 - 0.6 = 0.1
    0.7 - 0.3 = 0.4

    And you are suggesting that this method is credible ?

    What I’m suggesting is; “Describing the effects of removing bristlecone pine series, Steve McIntyre’s characterization seems to have led some of his readers to believe the hockey stick shape disappears. This is simply not true.”

    I am also fascinated by your analysis of verification statistics. The fact that a particular data set make the data “significant” is not an argument for saying that the data set should be included.

    That is an empty assertion.

    If inclusion of data improves cross-validation, that suggests the data contains signal since a) it is improving the fit, and b) that improvement is unlikely to be due to spurious correlation during calibration. Those are arguments for inclusion.

    The fact that you “need” bristlecones in the reconstruction

    Over the 1400-1450AD step.

    (which show no relationship with their local temperature)

    Which we’re not trying to measure.
    However, I would appreciate a cite for your assertion?

    to get the whole thing to give a “significant” result,

    Not true when including the proxies as they are (no PCA.)

    is a fairly severe indictment of the method.

    Non-sequitur, sorry.

  • luminous beauty // March 13, 2008 at 2:18 am

    mikep

    The RPCs (reconstructed PCs) of the proxy series are individually determined by singular value decomposition from the instrumental PCA. No PCA is performed on the proxies for the purpose of reconstruction.

    You should actually read MBH98 and not rely on the confused, conflated and distorted misrepresentations on CA.

  • per // March 13, 2008 at 2:26 am

    dear lazar
    accepting what you say:
    if you take out 14 californian tree proxies, and the whole temperature of the northern hemisphere changes by 0.1-0.4C in the 15th century, are you suggesting that this method is credible ?
    yes or no would be helpful.

    there are those who would submit that a hockey stick with a 0.4C deflection in the handle is more akin to a “U” than a hockey-stick.

    “If inclusion of data improves cross-validation, that suggests the data contains signal since a) it is improving the fit, and b) that improvement is unlikely to be due to spurious correlation during calibration.”
    you really do not have a clue. The arguments for inclusion of a proxy (that it measures temperature) have to be separate from your statistical test of that relationship. Arguing that the statistical significance makes spurious correlation unlikely is silly; the statistics makes no comment on the cause of the correlation. It is especially silly when you know that the verification method used (RE) is inadequate, and that r2 analysis shows the correlation is appalling.

    You gloss over the poor relationship of bristlecones with the local temperature as if it doesn’t matter. Can you explain to me how a tree growth proxy that does not correlate with local temperature can somehow tell me about the entire northern hemisphere ? This really goes to the heart of why you include these proxies, or if the association you find is entirely spurious.

    You can look at the original reference (Graybill and Idso, 1993) or you can look at the NRC/NAS report, which reviews the use of strip-bark pines.

    Finally, I don’t see why you say non-sequitur. MBH used a pca method, to reconstruct temperature in 1400-1450. According to W&A (scenarios 6a-c), taking out a bunch of north american trees makes the reconstruction fail. I do not see how you can argue that this method is not severely problematic on these grounds alone; how can you have a northern temperature method that relies so much on californian/gaspe proxies ?

  • Lazar // March 13, 2008 at 3:26 am

    MrPete,

    Is this area of science in need of more remediation than most others? In my experience, when the published shenanigans in this subarea are shared with other scientists, leaving all the details out so as to avoid the “heat”… they tend to react with shock, disbelief, or sad laughter. The most mature response tends to be along the lines of “hey, it’s obviously a young science; they’ll eventually clean up their act.”

    Most of us can share anecdotes…
    A friend who works on protein folding, told me about someone who submitted work to peer review whilst knowing (and not disclosing) it to be fatally flawed. That friend also described quite nasty and bitter rivalries between different approaches to measuring the same damn variable in the same field, each party is quite dismissive of the methods, work, and average personal integrity of the other. Point is, scientists can be dismissive of other fields, and divisions within their own, without good reason. Most of the disputes and the failures in fields other than climate science never go beyond the private sphere. But climate science has had more scrutiny, and yet, I don’t think there’s much bad to show… bad being relative. They’re human. And on the other hand there is a heap load of good, nay excellent work.

  • luminous beauty // March 13, 2008 at 6:12 am

    “if you take out 14 californian tree proxies, and the whole temperature of the northern hemisphere changes by 0.1-0.4C in the 15th century, are you suggesting that this method is credible ?
    yes or no would be helpful.”

    Seeing how the mean of 0.1C - 0.4C is .025C and the 2 sigma CI of MBH’s reconstruction is about ±0.4C…

    YES. Entirely credible.

  • Chris O'Neill // March 13, 2008 at 6:48 am

    James:

    “Note that they (the NRC panel) agreed that the statistical methods of the Hockey Stick (MBH9x) could have been better,”

    Which indeed is now done and is now usual practice, e.g.:

    Rutherford, S., M.E. Mann, T.J. Osborn, R.S. Bradley, K.R. Briffa, M.K. Hughes, and P.D. Jones. 2005.
    “Proxy-based Northern Hemisphere surface temperature reconstructions: sensitivity to method, predictor network, target season, and target domain.” Journal of Climate18:2308-2329.

    Discussions of out-of-date methods such as PCA are sensibly of academic or historical interest only.

    Oh, come on, Rutherford et al (co-authors include MB & H) recycle the MBH proxies.

    If you had been paying attention you would have noticed that the point was about STATISTICAL METHODS, not data.

    I’m amazed by the concept that scientific papers have some sort of use-by date. If it is crap now, it was crap then.

    I’m amazed that so many people have crap attention. (BTW, I was merely pointing out that the statistical methods in MBH9x are superceded and have no special significance, so even if you think they are crap (which they are not), the issue is of zero practical significance.)

  • mikep // March 13, 2008 at 9:14 am

    Luminous beauty you are being disingenuous. To say that no PCA is performed on the proxies for the purposes of reconstruction presumably means that the proxies are already represented by a PC. The arguments is all about what should be included in the reconstruction step. There is no dispute that if you include the PC4 of a conventional PCA in the reconstruction step you get MBH results - this is, for example, stated in one at least of M&M’s 2005 articles. The issue is whether this PC4 is a valid temperature indicator. The issue is, as it always has been, not primarily about PCA but about whether the bristlecones and related species are a valid temperature proxy. And M&M’s nature submission from 2004 - soon after they discovered the undisclosed short-centering issue - makes precisely this point.

  • Nick Moon // March 13, 2008 at 10:07 am

    I’ve posted twice now, suggesting you look at your ‘other influence’ data and the PC1 you get when you did a centered PCA. You’ve ignored this. Is this because you can’t be bothered - fair enough you can’t be expected to take seriously every comment that gets posted onto your blog. But it wouldn’t take you that much effort to make me look like an idiot and put the two graphs up and say - no there is no correlation. Unless of course there is a correlation between PC1 and your other influence data.

    Thing is, I think that using a synthetic data set to test the statistical processes is a very good idea. I think by doing this you are doing good science. I’m just not sure you are getting the answer you weant to get. But a good scientist should stand by the results of their science - even if it disagrees with their personal beliefs.

  • Armagh Geddon // March 13, 2008 at 10:09 am

    TCO,

    You the dude!! I remember your old posts at CA. Some beauties after you had imbibed - a little!

  • Armagh Geddon // March 13, 2008 at 10:12 am

    TCO, again.

    Actually, dude, I don’t want to be too hard on you. You clearly are an intelligent thinker, seeking truth. It’s clear though, that part of you thinks that McI is doing a great job. However, he isn’t doing the job as you think it should be done. Having followed you for quite some time now, I truly would appreciate your unbiased, direct opinion on which way is up!

  • per // March 13, 2008 at 10:29 am

    luminous beauty’s post is a joy to read.
    In fact, it is MBH who incorrectly describe their procedure as a PCA, when SVD is the more correct description of their procedure- as commented on Climate audit.
    MBH state they make RPCs, where the PCs are the principal components of Principal Component Analysis.
    http://en.wikipedia.org/wiki/Singular_value_decomposition

  • per // March 13, 2008 at 1:29 pm

    “Seeing how the mean of 0.1C - 0.4C is .025C ”
    perhaps you mean 0.25 C ?
    that would be half of the confidence interval, or the full confidence interval if the 0.4C figures is correct.

    but you are not addressing the issue of whether the inclusion of californian pines should be able to change the temperature of the entire northern hemisphere by 0.1-0.4C.

    chris o’neill
    “the statistical methods in MBH9x are superceded and have no special significance, so even if you think they are crap (which they are not)…”
    you cannot have it both ways; either the methods of MBH are superceded- in which there is a problem in these methods which has been addressed- or they have not been superceded. You cannot claim “superceded” and then say that there is no problem with what has been “superceded”.

  • RomanM // March 13, 2008 at 1:54 pm

    TCO March 12, 2008 at 1:55 am
    You seem to be a bright guy, but the red-herring criticism:

    E. Not sure if this affects the whole 4 versus 1 PC thingie, but McI glides past explanation of his change of TWO FACTORS at one time (correlation versus covariance and centering versus decentering). Huybers nailed him well for that.

    does not really make sense. Since the Mannian short-centering produces values which are neither correlations nor covariances, how can this be a “change of two factors”? As far as the Huybers comment goes (at http://www.people.fas.harvard.edu/~phuybers/Hockey/Huybers_Comment.pdf ), I couldn’t find anything related to this issue. Huybers just merrily swims along assuming PC business as usual with the Mann-centric eigenvectors and never deals directly with the selection bias of the methodology.

  • George // March 13, 2008 at 2:53 pm

    I wonder:

    How many people posting here (and on Climate Audit) on dendrochronology (Steve mcIntyre, per, John A, mikep, et al) are dendrochronology experts?

    How many have even taken courses specifically in dendrochronology, for that matter? (I’m not talking about a brief introduction to the subject found in most intro geology books. )

    All dendrochronology experts posting here, please raise your mouse finger.

    To others: see if you can spot the problem wit hthe argument: “Mann is wrong because his result depends on tree ring analysis that is flawed/invalid” argument.

    To those who are not dendrochronology experts and who are nonetheless claiming (either explicitly or implicitly) that “the tree ring data upon which Mann and others base their results is not a valid temperature proxy” when people who are experts say otherwise?

    For those who may not be aware, one of the authors of the original Hockey stick paper (the “H” in MBH) is Malcolm Hughes, a researcher at the University of Arizona Laboratory of Tree Ring research and one of the world’s experts on dendroclimatology.

    So, without knowing a great deal about the subject, who you gonna believe?

    A former mineral exploration geologist/analyst (Steve McIntyre) who might have read** some papers on the subject of dendrochronology, a biochemist who posts as “per” (and sometimes other supporting sock puppet characters) or an actual expert on the subject?

    *After McIntyre’s recent demonstrably false claim (since expunged from his blog) that Hansen did not indicate that Scenario B was “most plausible,” when those were Hansen’s very words in the ‘88 Hansen paper that McIntyre was supposedly “critiquing,” I have serious doubts that McIntyre even reads what he critiques. The above case is direct evidence to the contrary.

  • Lazar // March 13, 2008 at 2:53 pm

    per,

    you really do not have a clue. The arguments for inclusion of a proxy (that it measures temperature) have to be separate from your statistical test of that relationship. Arguing that the statistical significance makes spurious correlation unlikely is silly; the statistics makes no comment on the cause of the correlation.

    Those statements are wrong. Try and seperate out the steps from MBH selection of proxies through to subsequent work (M&M, followed by WA).

    It is possible to produce any given correlation from datasets unrelated to the physical quantity of interest, given enough luck; luck depends on the size and statistical properties of the dataset, and the degree of correlation. A regression model may predict hidden values of the quantity of interest if you’re luckier still. How lucky? That’s the question. See under “null hypothesis”. If there’s less than one in a hundred chance that a given correlation can be produced from noise, that’s evidence to support the physical assumptions made in support the data. It could of course be a spurious outcome resulting from luck; nothing in science is ever proven. What the passing of statistical significance tests show is that the ‘noise & some luck’ result is unlikely, and that is evidence in support of the data containing genuine signal. MBH included bristlecone pine series into the analysis based on physical assumptions, subsequent statistical tests support those assumptions, as shown by the fact that when bristlecone pine series are removed, cross-validation scores drop and in some cases fail.

    It is especially silly when you know that the verification method used (RE) is inadequate,

    May be inadequate under certain conditions.

    and that r2 analysis shows the correlation is appalling.

    Signal in the proxies may lead or lag global temperature.
    That relation will vary from proxy to proxy, especially in a multi-proxy study.
    Proxy series are also influenced by other time-varying factors.
    These suggest r2 is unsuitable measure, given the assumptions involved in MBH98.

    if you take out 14 californian tree proxies, and the whole temperature of the northern hemisphere changes by 0.1-0.4C in the 15th century, are you suggesting that this method is credible ?
    yes or no would be helpful.

    Change that to; if you take out 14 californian tree proxies, and the annual average reconstructed temperatures of the northern hemisphere over approximately 5 non-contiguous years in the 15th century change by 0.1-0.4C, are you suggesting this demonstrates that the method is not credible?
    And I would answer that no, it does not show that the method is not credible.

  • Patrick Hadley // March 13, 2008 at 3:28 pm

    Tamino, your comment about Jolliffe
    “Which flatters Jolliffe in the extreme. As far as I can tell, he’s the only one to state that he didn’t understand the process well enough to opine on whether or not it’s valid — yet he seems to be the one person everyone agrees is expert on the subject of PCA in general”

    seems a bit odd. It is you who have argued from his authority by quoting from Jolliffe’s book to support the use of non-centred means.

    When my maths teacher said to me that he could not understand my working I did not take it to mean that the old boy was going a bit simple and that I had passed him by, I assumed that he meant that my methods were not any good. There are plenty of other quotes from Jolliffe - (who is a specialist statistical climatologist)available to show that he definitely does not agree with the MBH methodology.

  • Lee // March 13, 2008 at 3:29 pm

    Oh, good god…

    Look, what happens if y’all ignore MBH9x altogether. What does that gain you? There are 14 subsequent papers that take different approaches to the same question and data, using different statistical techniques and different selection criteria for data inclusion and so on - and arrive at very close to the same answers.

    There is a body of work here. Why the persistent (and personally nasty) attacks on the same founding paper, over and over, largely to the exclusion of the more numerous and later work in that corpus?

  • luminous beauty // March 13, 2008 at 3:47 pm

    per,

    MBH did PCA on the instrumental record. They then did SVD on each proxy series in order to assign reconstructed PC coefficients to each series.

    The purpose of doing PCA had nothing to do with finding correlations between the proxies and past temperatures (they were selected because it was already known that is what they did, including BCPs), but to disaggregate spatial patterns of temperature from the instrumental record.

    Per BCPs. The ‘divergence problem’ is a late 20th century phenomenon. Tree ring growth since the late 50s has diverged from indices well demonstrated to be accurate reflections of local, regional and global climate variability over a couple of thousand years. Whether the cause (for BCPs) is CO2 fertilization or if stripped-bark trees are more sensitive to such than whole bark trees or something else is the subject of much research, but has nothing to do with the confidence dendro folks have with paleo reconstructions. Whatever the cause, the magnitude of the effect is known and the data can be corrected. The correction brings the data into agreement with the instrumental record.

    Steve Mc is trying shovel a hundred pounds of manure into a five pound sack.

  • luminous beauty // March 13, 2008 at 4:18 pm

    per,

    The o.4C difference in the M&M flawed reconstruction has no skill.

    It is so worthless it is not even wrong.

  • AndyL // March 13, 2008 at 6:02 pm

    Luminous

    You say “the magnitude of the effect is known and the data can be corrected”. This can easily be tested

    1) predict the ring widths based on temperature and this effect
    2) re-sample the trees

  • fred // March 13, 2008 at 6:07 pm

    Lee, you need to go to p 114 of BPL’s previously cited link. See if you really agree that there have been 14 independent studies, then look at the chart, and see whether you think that all 14 of them are similar to the famous MBH HS.

    Don’t believe me, go and see for yourself.

    You ask why MBH matters. Only because the AGW community persists in defending it lock stock and barrel. If they were to repudiate it, no-one would care. Everyone would move on to talking about CO2 sensitivity or something seriously relevant to Global Warming.

    Its a mistaken tactic. Its the weakest part of the edifice, and persisting in trying to defend it makes it look as if the whole thing must be as weak. Which it is not. Other parts of the hypothesis are much stronger, but its hard to get to them as long as we cannot admit that MBH is discredited.

  • Chris O'Neill // March 13, 2008 at 6:23 pm

    either the methods of MBH are superceded- in which there is a problem in these methods which has been addressed

    Amazing contortions.

    “the computer has superseded the slide rule”

    Obviously, the slide rule had a problem which has been addressed. Until the computer was invented slide rules gave the wrong answer and no one realized. Now that we use computers, slide rules give the right answer.

  • Chris O'Neill // March 13, 2008 at 6:49 pm

    Chris O’Neill may want to explain how something that is “not yet fully quantified” can be quantified.

    per may want to explain why he needs to shift goal posts.

  • RomanM // March 13, 2008 at 7:17 pm

    Chris O:

    No, you have the wrong comparison. MBH was more like a computer whose programming was fouled up … and it gave the “right” answer.

  • MrPete // March 13, 2008 at 7:46 pm

    Lazar, “But climate science has had more scrutiny, and yet, I don’t think there’s much bad to show… bad being relative. They’re human. And on the other hand there is a heap load of good, nay excellent work.”

    I would remind that we’re in agreement to a large extent: I have huge appreciation for much of the work done in climate science in general. I know and am even related to climate scientists who do great work. Perhaps that’s why I get passionate about the not-so-great stuff: poor science, and defense of poor science, harms everybody.

    I think the hard part of getting past the defensiveness etc, as demonstrated in these blog circles more often than any of us care to admit, is that the blogosphere is more like a set of casual face to face conversations than a set of carefully edited publications. And yet it’s much harder (physically and emotionally) to apologize for blogosphere mistakes and “move on.” Best and worst of both worlds.

    I keep dreaming of everyone having a personal “errata” web page, and anything listed there is off limits for further haranguing :-)

  • Chris O'Neill // March 13, 2008 at 7:52 pm

    per:

    “The key part is which PC has the signal that we want (e.g. temperature). If there are stronger PCs that do not correlate with our signal then they are just noise. Being stronger doesn’t give them any special significance at all. Just means they are something we are not interested in.”

    this is wrong. The whole point in having all these proxies, is that they are meant to behave as thermometers,

    and in the real world can be expected to have a certain amount of noise….

    each representing the temperature in a different part of the world. That is why it was so important for MBH to say that PC1 was the dominant pattern of variance,

    You don’t know what you’re talking about. Have you ever actually read MBH98 properly? When MBH98 talks about “dominant pattern of variance” they are referring to “the dominant patterns of temperature variability in the instrumental record”, page 779, or “the dominant patterns of the instrumental surface-temperature data through principal component analysis (PCA). PCA provides a natural smoothing of the temperature field in terms of a small number of dominant patterns of variability or ‘empirical eigenvectors’”, page 781. They are not talking about the dominant PC that is derived from a localized group of proxies when they say “dominant patterns of variability”.

    If you are simply using the PCA to select for a few records which show a correlation with temperature,

    You seem to be thoroughly confused. PCA is used separately in two different places in MBH98. The first place is a PCA on the instrumental record (referred to in the above quotes) that generates PCs of the instrumental record. The second place is a PCA on proxies that are highly concentrated in particular areas. This second PCA replaces the large number of proxies in a small area with a small number of proxies (in the form of PCs) which are much more suitable for doing the multiple regression against the PCs derived from the instrument record. This second PCA has nothing directly to do with temperature. They’re just PCs of the proxies.

  • per // March 13, 2008 at 8:05 pm

    dear lazar
    if you don’t understand what spurious correlation is, maybe you should pause before telling me i am wrong.

    yes, you are slowly getting there; the bristlecones are in the reconstruction because of physical assumptions; the statistics are an INDEPENDENT test. that means that the physical assumptions are germane; such as that there is no relationship between bristlecone pine growth and local temperature.
    “Signal in the proxies may lead or lag global temperature.
    That relation will vary from proxy to proxy, especially in a multi-proxy study.
    Proxy series are also influenced by other time-varying factors.”
    it is worth reading this again, just to see what you have said; after all, the whole basis of MBH98 is that there is a relationship between temperature, time and the proxies; and you are throwing that out of the window. Needless to say, your comments have no relationship to r2.

    “approximately 5 non-contiguous years in the 15th century change by 0.1-0.4C”
    where do you get your 5 non-contiguous years bit from? Being lazy, i am simply relying on scenarios 6a-c from W&A, and they have an awful lot of change in the 13th century.

  • per // March 13, 2008 at 8:26 pm

    luminous beauty
    “Whatever the cause, the magnitude of the effect is known and the data can be corrected.”
    you are just wrong. If you do not know what the cause is, you cannot correct; it may be that there is no “cause”, and the trees do not correlate with temperature. If you do not know what the cause is, you can’t give any guarantee that similar conditions didn’t pertain in the past 600 years- when you don’t know any of the variables.

  • dhogaza // March 13, 2008 at 9:10 pm

    Perhaps that’s why I get passionate about the not-so-great stuff: poor science, and defense of poor science, harms everybody.

    You can assert this until you’re blue in the face, but it still won’t make it true. MBH was not “poor science”.

    HB, I think I’m done with your blog. The CA crowd just isn’t worth putting up with.

  • per // March 13, 2008 at 9:45 pm

    “That is why it was so important for MBH to say that PC1 was the dominant pattern of variance,”
    apologies, I didn’t remember where this was from. MBH use the phrase here, and not in the Nature paper:
    http://stephenschneider.stanford.edu/Publications/PDF_Papers/MannEtAl2004.pdf
    “This second PCA replaces the large number of proxies in a small area with a small number of proxies (in the form of PCs) which are much more suitable for doing the multiple regression against the PCs derived from the instrument record. This second PCA has nothing directly to do with temperature. They’re just PCs of the proxies.”
    i am confused ? The second pca selects PCs, which are then used to give you a temperature reconstruction by the multiple regression you describe. The second PCA inappropriately weights californian bristlecones, and this has everything to do with the temperature reconstruction.

    [Response: There are several independent applications of PCA in MBH98. PCA is applied to temperature data in order to find *geographic patterns* of temperature. It's also applied to proxy data sets when there are many of the same type from the same region, to reduce their sheer number; this mitigates the problem of overfitting and prevents proxy-dense regions from dominating analysis. And of course, when proxy data sets are in place PCA is applied to identify patterns which may be related to a temperature reconstruction.]

  • luminous beauty // March 13, 2008 at 9:56 pm

    per,

    We don’t know what causes gravity. We can correct for it pretty well.

    If similar conditions pertained in the past it would show up in the data.

    But you might be right. The law of uniformity may have been miraculously repealed, and magic is once again loose in the world.

  • Hansen's Bulldog // March 13, 2008 at 9:57 pm

    HB, I think I’m done with your blog. The CA crowd just isn’t worth putting up with.

    I’ve come to the same opinion.

    Some people uphold contrary opinions, but are able to discourse and willing to listen (fred comes to mind). That kind of disagreement is essential. But others just raise the noise level without contributing enough signal to make it worthwhile, and often are rude about it to boot. I find it particularly irksome that so many false statements have been contributed and *repeated* so often. In the past I’ve tried to contradict falsehoods when they’re posted here, but the volume of misinformation has gotten so great I just can’t keep up with it anymore. As a result, I can understand why a *lot* of people would find this is no longer a good place to get information, exchange ideas, or even debate issues. If I were a reader myself, I’d seriously consider leaving.

    Driving away readers who might actually want to learn something or share information, is exactly opposite to my goal.

    This particular thread has inflamed a lot of passions. I’ll keep it open for a while longer, and continue the policy of “almost anything goes” — I’m not going to change policy in mid-thread. But applying that policy in general has turned out to be a failure. So, starting with the next post (on sea level) I’m no longer letting the abusive or dreadfully-informed dominate the discussion.

  • dhogaza // March 13, 2008 at 10:04 pm

    …I’m not going to change policy in mid-thread. But applying that policy in general has turned out to be a failure. So, starting with the next post (on sea level) I’m no longer letting the abusive or dreadfully-informed dominate the discussion.

    That’s entirely reasonable, thanks. Maybe we can get folks like Hank Roberts back, then …

  • TCO // March 13, 2008 at 10:30 pm

    RomanM: the Mannian method :
    A. Short-centers by subtracting the mean of the 20th century versus the whole series.
    B. divides by standard deviation.

    A is bizarre. B is common. McK in his comparison often tries to make comments about A/notA by running AB versus notAnotB. This is a logical flaw for rhetorical effect. Changing only A versus not A has a bigger effect than changing both A and B.

    The Huybers comment is very illuminating on this aspect. Read the specific part where he gives the adjustment formulas. What McI should have done was run a full factorial and showed exactly what effect is caused by what factors. Burger does this well in his 2005 article.

    Capisce?

  • per // March 13, 2008 at 10:38 pm

    “We don’t know what causes gravity. We can correct for it pretty well.”
    you are not correcting for the causes of gravity, you are correcting for gravity causing effects on other bodies. In the latter case, we know that gravity is the cause.
    “If similar conditions pertained in the past it would show up in the data.”
    how would you know ? According to your premise, we don’t know the cause, and we have no measurement of the cause at the relevant time anyway.

  • TCO // March 13, 2008 at 10:38 pm

    I’m concerned about the coming censorship. While there may be people on my side (I’m on the skeptic side, though not a kool-aid drinker) who repeat trivial or wrong points or are aggressive, there are many such on the pro AGW side as well. The issue of hoi polloi is a common one. I don’t think we’ll have good discussion if you restrict CAers, especially when they start routing your side.

  • Lazar // March 13, 2008 at 10:44 pm

    if you don’t understand what spurious correlation is, maybe you should pause before telling me i am wrong.

    I do understand spurious correlation.
    I also understand various forms of evasion.

    yes, you are slowly getting there; the bristlecones are in the reconstruction because of physical assumptions;

    Yeeesh.

    the statistics are an INDEPENDENT test.

    I wonder what ‘independent’ means.

    that means that the physical assumptions are germane;

    Germane; relevant, pertinent. Yes, it does follow that if certain physical assumptions are a basis for selecting proxy data to include, the physical assumptions are ‘germane’ to what proxy data is included.

    You still haven’t explained the ‘independent’ bit.

    a) is there evidence of a physical relation between two variables?
    b) what is the nature of that physical relation?
    c) can we reject the null hypothesis and with what confidence?
    All three questions are related, as such they are not “independent”.

    it is worth reading this again, just to see what you have said; after all, the whole basis of MBH98 is that there is a relationship between temperature, time and the proxies; and you are throwing that out of the window.

    Sigh… no, I am not, please reread and parse more carefully through your logic circuits.

    I can’t be bothered.

    Rest binned unread.

  • per // March 13, 2008 at 10:59 pm

    “Some of you might be thinking, wouldn’t MM have noticed that their fit (the one lacking a hockey stick) failed statistical significance when they did the verification step to check the correctness of their version? Probably yes. Too bad they simply didn’t do the verification step.”
    dear tamino
    can i pick you up on this ?
    isn’t it the case that M&M GRL (2005) actually has a whole page on analysis of the verification step, including calculation of the verification statistics ?

    Also, wouldn’t it be fair to admit that MBH’98 did not have a clear description of the rule used to retain proxy PCs ? Isn’t it unfair to castigate M&M for emulating MBH incorrectly, when MBH hadn’t made their methodology available in 2003 (i.e. before MBH’s corrigendum paper) ?

    it’s fascinating to hear your comments about “the abusive or dreadfully-informed”; I hope you are able to distinguish that from censorship.

  • TCO // March 13, 2008 at 11:05 pm

    1030PM, meant has a smaller effect.

  • David Holland // March 13, 2008 at 11:21 pm

    Last Friday on BBC Radio Sir David (more dangerous than terrorism) King said, “2 or 3 years ago when I came on your programme I would be challenged sceptics [but] that’s now gone.”

    It has, but that’s only because the BBC do not interview critics any more. RC also tried an open door policy for a very short while. One of the main funding bodies here, NERC, launched their Climate Challenge with a great fanfare just over a year ago year ago. The top UK climate scientist would put the world’s sceptics in their place. After just a few days they were buried and changed the rules to limit the challenge to what they could handle and still did not change a single mind. It was to be the first of many debates, but was the first and last try.

    I can understand the Bulldog not wanting another thread like this and I am grateful that he gave it a try. But you he can’t have it both ways. You can’t have an open debate on an invitation only basis. Debate and democracy are a pain in the but when you are trying to get things done but I would hate to have to live without it. As the cost of climate change is driven home you will have more smart people that had not previously thought about the subject wanting to know if they really have to give up their Chelsea Tractors and Patio Heaters, so you ought to get used to robust debate if you really hope to sustain the AGW bandwagon.

  • David Holland // March 13, 2008 at 11:24 pm

    oops should be a “by” in line 3!

  • Lee // March 14, 2008 at 12:05 am

    fred, yo need to reread what I said.
    I didn’t claim those 14 were independent - where you got that from is beyond me. They are doing equivalent analyses from the same data sets. I said they are using different statistical methods and different criteria for data inclusion

  • dhogaza // March 14, 2008 at 12:28 am

    I don’t think we’ll have good discussion if you restrict CAers, especially when they start routing your side.

    They’re not routing, they’re flooding and causing worthwhile people to leave.

    Look, we all know where CA is. If we want the CA standard drivel we can all go there, right?

    Do you really feel that comments like that NRC (NAS) report’s use of the word “plausible” to describe Mann’s reconstruction as meaning “meant to be deceptive” is what the NRC (NAS) report authors intended to convey?

    Most of what I see here are efforts to prove that Mann is incompetent and/or deceptive, that HB doesn’t know what he’s talking about, that anyone who believes in what climate scientists tell us are idiots, McIntyre is a near god-like figure, blah blah blah.

    All tired, patently false, crap.

  • TCO // March 14, 2008 at 12:57 am

    You can try to censor idiot skeptics and leave smart ones. But it won’t be fair if you leave the alarmist hoi polloi uncensored. And it will be hard to differentiate smart from dumb ones, silliness from POVs that one disagrees with.

  • MrPete // March 14, 2008 at 1:12 am

    Tamino (or anyone else) — by any chance is there a “slash-dot” style blog plugin that allows readers to click on a comment to give it (say) 1-5 stars and thus other readers can raise or lower their “noise level” filter?
    Seems that something like that would be helpful. Nobody’s completely blocked, you can read them if you like, but in general the perspective of the community will set what most people normally see.
    If there’s no obvious answer, I’ll look around and see if I can put something together…

  • Hank Roberts // March 14, 2008 at 1:39 am

    The better the bridge you build,
    and the more traffic on your bridge,
    the bigger the trolls attracted thereunder.

    Remember, when you get into a fight with a troll, the people there to use the bridge won’t be able to tell who’s right, all they’ll see is there’s a fight.

    Lacking threaded browsing (to ignore threads that are digressions), the killfile script is a mediocre help to the extent people quit replying to attempts to disrupt by attracting digression.

    Were it my blog (and this is why I don’t have one!) I’d feel the need to either do as RC does, where you’ll see [edit] replacing witnessing or trolling. Or use the disemvoweling script. Or maybe turn the useless stuff to a pale gray font.

    Or simply replace the rants with the number from the list, Bingo style.

    All that is terribly tedious if you’re trying to have a focused conversation on a topic.

    Only alternative, again one I could wish someone would do, not me, would be parallel topics, one by prearranged invitation with those actually contributing, and another for those who wanted to kibitz. Patiently mine the kibitzing thread to see if anyone shows up contributing substance to the invited discussion. Lot of work.

    ———————————————–
    “It is hard to believe that a man is telling the truth when you know that you would lie if you were in his place.”

    (This, I think, is the real reason for so much copypaste stuff — it’s done by people who’ve no experience actually publishing good science, and so no idea why it’s worth resisting the very natural impulse to disrupt conversations they dislike.)

    “The trouble with fighting for human freedom is that one spends most of one’s time defending scoundrels. ”
    (This is why I so admire our host here.)
    —Henry Louis Mencken

  • per // March 14, 2008 at 2:20 am

    “I do understand spurious correlation.”
    why is it that you have argued that an unlikely event is evidence against spurious correlation ?
    Statistical methods do not identify a spurious correlation; that is why it is called a CORRELATION. Spurious correlations can be extremely unlikely to happen by chance; but still spurious.
    http://en.wikipedia.org/wiki/Spurious_relationship

    re: independence
    if you are using the statistical test to determine whether the relationship between proxies and temperature is good, you cannot use that test to decide which proxies should be included. Otherwise, you are “snooping” the outcome of the statistical test, and bankrupting the procedure. The statistical test has to be independent of your selection of proxies.

    ” no, I am not, please reread and parse more carefully through your logic circuits.”
    yes, you explicitly premised that the relationship between temperature and time was busted ! And the assumptions and methodology of MBH98 require r2 analysis; which MBH use perfectly when the results are convenient to them. They did not use r2 analysis, and it so happens that the r2 analysis shows that the verification statistics for the 14th century are busted.

  • Chris O'Neill // March 14, 2008 at 2:51 am

    RomanM:

    No, you have the wrong comparison.

    I was merely explaining what the word “superseded” means. I feel like a school teacher. Try to pay attention children.

  • dhogaza // March 14, 2008 at 3:08 am

    But it won’t be fair if you leave the alarmist hoi polloi uncensored. And it will be hard to differentiate smart from dumb ones, silliness from POVs that one disagrees with.

    Oh, a reasonable standard is whether or not “alarmists” (stupid-assed term, TCO, if anyone is an “alarmist” it’s McIntyre and his CA gang who repeatedly accuse climate science of being filled with frauds and liars), would be whether or not they are posting something that at least is defensible scientifically (CA and McIntyre, and Watts with his photos, aren’t doing science).

    That would fit the definition of a pro-science blog (you can argue that what CA and McIntyre, and Watts with his photos, do a *better* job than science, but that argument would best be carried elsewhere).

    Only alternative, again one I could wish someone would do, not me, would be parallel topics, one by prearranged invitation with those actually contributing, and another for those who wanted to kibitz. Patiently mine the kibitzing thread to see if anyone shows up contributing substance to the invited discussion. Lot of work.

    I had a similar thought, but with the notion that the kibitzing thread not be monitored, simply not recommended :)

    Or, worse, years ago at photo.net, we had an unstoppably annoying troll. Solution? Let him see his own posts, but hide them from everyone else, but don’t tell him. Server-enforced killfile, not bad, eh?

  • dhogaza // March 14, 2008 at 3:09 am

    This conversation (unsolicited advice-giving to HB) could perhaps spawn a new open thread?

  • Chris O'Neill // March 14, 2008 at 3:36 am

    This particular thread has inflamed a lot of passions. I’ll keep it open for a while longer, and continue the policy of “almost anything goes” — I’m not going to change policy in mid-thread. But applying that policy in general has turned out to be a failure.

    I think dhogaza’s early comment:

    Why not just delete those comments that aren’t relevant to your post, i.e. attempts to divert the discussion to “strip-bark samples”, etc?

    might have been usefully applied because all of those comments are just noise in this thread. I have refrained from commenting on those comments myself except where they were blatantly wrong or had some relevance to the original point.

  • Hansen's Bulldog // March 14, 2008 at 4:49 am

    When moderating comments, I deleted one from this thread by accident — just a slip of the mouse. Please repost.

  • mndean // March 14, 2008 at 5:09 am

    Dhogaza,
    re: photo.net troll
    I remember that! Still go there. I’ve never seen that kind of “feature” in any blog I’ve participated in, though. The greasemonkey script is about the best I’ve seen, and that’s no more than the old killfile/bozo bin. The most inconvenient commenting system will not keep out trolls, unfortunately.

  • Chris O'Neill // March 14, 2008 at 5:17 am

    per:

    I am confused ? The second pca selects PCs, which are THEN used to give you a temperature reconstruction by the multiple regression you describe. The second PCA inappropriately weights californian bristlecones,

    in the non-centered PCA, in your opinion,

    and this has everything to do with the temperature reconstruction

    So what does this have to do with interfering with the process when using centered PCA which is what I was talking about originally? This was:

    “The key part is which PC has the signal that we want (e.g. temperature). If there are stronger PCs that do not correlate with our signal then they are just noise. Being stronger doesn’t give them any special significance at all. Just means they are something we are not interested in.”

    I was clearly talking about using centered PCA. per then starts talking about using non-centered PCA. I think I know who’s confused.

  • David Holland // March 14, 2008 at 11:47 am

    The problem here is well illustrated by dhogaza’s “meant to be deceptive”. He is the only one to use that phrase. I just quoted the Pocket Oxford Dictionary. “Specious” or “deceptive” appears in all the dictionaries I’ve seen. And before doing so I cited exactly what the NRC said they meant by it. “Deceptive” then got repeated 5 times.

    “Fraud” appears twice in this thread, “liar” once. It was not used by me or those with similar views. These are not words that civilised debaters should use. However it is true and fair to say that, in 2005, I heard with my own ears Michael Mann say “Yea” to the question “Have you published the Maths that you used?” I can also cite a web source that says Mann told Christy at the NRC, 2006 public hearings that he did not calculate R2 –“that would be a silly thing to do.” Then I can cite the Fortran code that Mann released after Barton demanded it and say in all fairness that I think Dr Mann was “economic with the actuality”.

    Jolliffe said, politely, he found Mann’s description of what he did “too opaque”. What words are polite to describe his omitting to mention that he tested his reconstruction for the removal of Bristlecones and Gaspe? Or to describe not making it crystal clear that Briffa and Jones’s 1854 to 1902 data was omitted from the world famous “hockey stick” graph in IPCC 2001 Fig 2.20 because it spoils the clean transition from tree ring estimates to equally problematic instrumental estimates of temperature?

    The reason people get thrown out of this sort of thread is not their abuse of the supporters of Mann, but that they reveal the standard of his support.

    This is a very serious debate. A few days ago, in Vancouver, the British High Commissioner Anthony Carey said of climate change, “If we can’t deal with this issue it is going to lead to wars, bloodshed and tremendous international tensions in the future.”

    If we are going to finish up with a trade war you, or if you join with the EU position and eventually elect a president with David King’s views, finish up bombing other people into cutting their emissions, I hope we have a better basis, and plan, than we had for Iraq.

  • Barton Paul Levenson // March 14, 2008 at 11:51 am

    fred writes:

    [[You ask why MBH matters. Only because the AGW community persists in defending it lock stock and barrel. If they were to repudiate it, no-one would care. Everyone would move on to talking about CO2 sensitivity or something seriously relevant to Global Warming.

    Its a mistaken tactic. Its the weakest part of the edifice, and persisting in trying to defend it makes it look as if the whole thing must be as weak. Which it is not. Other parts of the hypothesis are much stronger, but its hard to get to them as long as we cannot admit that MBH is discredited.]]

    Yes, the world would be easier if people would just accept what you say and not argue. Unfortunately, we live in reality, where not everybody agrees with you.

    You are taking as a premise that MBH98 is wrong. We disagree with your premise. Therefore we will disagree with conclusions taken from your premise.

  • Lazar // March 14, 2008 at 11:52 am

    per,

    Statistical methods do not identify a spurious correlation; that is why it is called a CORRELATION. Spurious correlations can be extremely unlikely to happen by chance; but still spurious.

    Yes, so what is your conclusion?
    You’re positing a binary; that a spurious correlation is ‘identified’ or ‘not identified’, with 100% confidence.
    Statistical tests do not prove, they support; the issue is not binary;

    In statistics, a null hypothesis (H0) is a hypothesis set up to be nullified or refuted in order to support an alternative hypothesis. When used, the null hypothesis is presumed true until statistical evidence, in the form of a hypothesis test, indicates otherwise — that is, when the researcher has a certain degree of confidence, usually 95% to 99%, that the data does not support the null hypothesis.

    per,

    if you are using the statistical test to determine whether the relationship between proxies and temperature is good, you cannot use that test to decide which proxies should be included. Otherwise, you are “snooping” the outcome of the statistical test, and bankrupting the procedure. The statistical test has to be independent of your selection of proxies.

    This is why I’m asking you to seperate out the steps.
    Proxies were included on the basis of physical assumptions made by MBH.
    Subsequent work by WA add support to the physical assumptions made for including bristlecone pine series.
    That cross-validation scores decrease when bcp series are excluded was not the basis for including bcp series, it is an argument (in support) that the basis arguments were correct.

    yes, you explicitly premised that the relationship between temperature and time was busted !

    A false binary.
    That proxy data may lag (or lead) NH average annual temperature, and that may vary from proxy to proxy, does not show that the relationship is busted (i.e. there is no relationship).
    That there may be additional, time-varying non-climate effects does not state that there is no relationship between proxy data and NH average annual temperature.

  • Barton Paul Levenson // March 14, 2008 at 11:57 am

    TCO writes:

    [[I don’t think we’ll have good discussion if you restrict CAers, especially when they start routing your side.]]

    Dream on, Dude. You aren’t “routing [our] side.” You and your pals are just repeating the same damn discredited arguments over and over and over and over and over again until our heads explode. Annoying the hell out of the other side is not “routing” them, certainly not if you mean “defeating by argument.”

  • James Lane // March 14, 2008 at 12:44 pm

    Chris:

    “The key part is which PC has the signal that we want (e.g. temperature). If there are stronger PCs that do not correlate with our signal then they are just noise. Being stronger doesn’t give them any special significance at all. Just means they are something we are not interested in.”

    This is not correct. The higher order PCs are not “noise”, they are constructs that explain more of the variance in ring width than your purported temp PC.

    Which raises the question of what the higher order PCs represent. Precipitation? Humidity? Something else?

    Who knows? Personally, I doubt that any of the components in the MBH PC roster have a physical interpretation.

  • dean_1230 // March 14, 2008 at 1:27 pm

    BPL,

    While “rout” might be an extreme, I do believe it is accurate to say that Tamino has not succeeded in convincing any “unbiased reader*” that the non-centered hockey stick is correct.

    Especially if said “unbiased reader” also looks at the CA thread detailing the issues here.

    Note, I’m not saying he’s failed and that these articles have been a waste of time. The tutorial value of these 4 posts are a credit to Tamino and are worth reading regardless of what side one is on.

    But to say that he’s destroyed the criticism leveled against non-centered PCA is overstating things. Jolliffe said that he couldn’t support it as is and Tamino obviously respects and also relies on Jolliffe.

    On the censoring topic, the big fear is that only one side gets censored. For every denialist rant we have, we also have a true-believer claiming that the methods don’t matter and only the answer does. How one decides what to censor is always the problem. I like the idea about borrowing the slashdot method, but not sure how easy it is to implement.

    *This assumes, of course, that there are such things as “unbiased readers” that visit blogs like these.

  • dhogaza // March 14, 2008 at 3:03 pm

    Jolliffe said that he couldn’t support it as is

    He also didn’t say it was wrong. You keep insisting on your own interpretation of words.

    I think an unbiased reader can, for instance, read the NRC (NAS) report and decide for themselves if “plausible” means they felt that Mann’s work was “quite possibly correct” or “deceptive”.

  • non expert // March 14, 2008 at 3:05 pm

    seems you do not address ca’s questions directly, but rather argue a less treacherous course.

  • ChrisC // March 14, 2008 at 4:10 pm

    Hi Tamino/HB

    Just for the record the level of inanity of comments in this blog has really made it difficult to contribute. Back in the day, there used to a robust, informed discussion of your (excellent) work within the comment threads. Many of us (Tim Chase, Hank Roberts and BPL come to mind) had some expertise and could contribute. There were even a few diligent “skeptics”!

    These days I can’t do anything but lurk. There is little point in contributing to the comments, as your post is likely to be lost in the noise. People rant and rave, often without any idea what they’re talking about. As such, I just don’t find it worth getting involved anymore (and as a professional meteorologist, I often thought I could contribute a little to some of your threads).

    Anyhow, I’m ranting now, but please change the comments policy. Keep letting people disagree, but please, run a high pass intelligence filter on comments, to try to get rid of some of the idiocy.

    [Response: Another regular mentioned the same difficulty, and I responded that I agreed. As I said then, I'm not changing policy mid-thread -- but after this thread, a new policy goes into effect.]

  • RomanM // March 14, 2008 at 4:11 pm

    TCO // March 13, 2008 at 10:30 pm

    RomanM: the Mannian method :
    A. Short-centers by subtracting the mean of the 20th century versus the whole series.
    B. divides by standard deviation.
    A is bizarre. B is common. McK in his comparison often tries to make comments about A/notA by running AB versus notAnotB. This is a logical flaw for rhetorical effect. Changing only A versus not A has a bigger effect than changing both A and B.

    I beg to differ with your A and B assessment. Your statement “B. divides by standard deviation” ignores the fact that there are TWO standard deviations. One is the sd of the data over the entire time period for which that data is available, the second is the time period from 1902 to 1980. The former is common, the latter (which according to Huybers is the one used by MBH) is bizarre-squared. Note the effect of doing that - for variables which tend to have similar behaviour over the pre- and post-1902 time periods, the the sd’s will be about the same. On the other hand, if the variable means over the two time intervals are different (HS included), then the sd in the 1902 period will also tend to be (in some cases, much) smaller than the sd calculated for all the data. Dividing by the smaller value will increase the bias already introduced by the short-centering in A. Why would one want to deal with these issues separately - “well, if you do it half-right, you get …” is not a useful observation - they are together a single improper step. It makes more sense to simply show how the overall inappropriate method differs from the proper analysis.
    I couldn’t easily find the spot that you are referring to in Huybers on “the adjustment formulas” (I still work for a living). Could you please be more specific?

    Chris O’Neill // March 14, 2008 at 2:51 am

    RomanM:
    No, you have the wrong comparison.
    I was merely explaining what the word “superseded” means. I feel like a school teacher. Try to pay attention children.

    I think you missed the point of my somewhat tongue-in-cheek response to your post. We children are very grateful for the explanation.

    Tamino:

    A general observation on the dynamics of this particular blog subject: It appears to me that part of the friction was caused by the fact that the subject of the blog was highly technical and appropriate evaluation of the relevant issues was limited more to those individuals who have had sufficient training and background to appreciate what those issues are. Some of the other posters resorted to “argument by authority” (X says this is valid or invalid) or by raising semi-related side issues (e.g. BCPs and proxies in general) or making defensive uninformed statements about the field of statistics and the capabilities of those who do that as a profession. Such diversions can quickly escalate into heated argument and over-the-top reaction such as derogatory name-calling on both sides. I don’t know how this can be avoided, but I would hate to see you have to do (possibly necessary) serious censorship since one of the things I admire is your attitude of not removing many posts which disagree with you.

  • kim // March 14, 2008 at 4:24 pm

    He is waiting in the ring. You may remain in the dressing room; there aren’t many bettors to raise a fuss. But you asked for the match. What would Mann’s Best Friend do?

    Well, he could have let a sleeping dog lie.
    ===========================

  • Chris O'Neill // March 14, 2008 at 5:15 pm

    James Lane:

    “The key part is which PC has the signal that we want (e.g. temperature). If there are stronger PCs that do not correlate with our signal then they are just noise. Being stronger doesn’t give them any special significance at all. Just means they are something we are not interested in.”

    This is not correct.

    Why do I get a feeling of deja vous.

    The higher order PCs are not “noise”, they are constructs that explain more of the variance in ring width than your purported temp PC.

    It’s not up to you or me to decide what the “temperature PC/s” are or are not. That’s the job of the multiple regression. If the multiple regression rejects the stronger PCs, then (like for any proxy that gets rejected), the multiple regression just doesn’t think it has much to do with temperature. If you have a problem with the PCs it chooses, then take it up with it. Has nothing to do with me or Michael Mann or any other person.

    Which raises the question of what the higher order PCs represent. Precipitation? Humidity? Something else?

    Interesting question maybe but regressing against temperature is not expected to answer it.

    Who knows? Personally, I doubt that any of the components in the MBH PC roster have a physical interpretation.

    At least try to remember that most of the proxies in MBH98 are physical measurements.

    Lastly, I’d like to point out that if James Lane and other readers had understood Tamino’s description of regression on proxy PCs at the beginning of this thread, then they wouldn’t be making the incorrect assertions above.

  • caerbannog // March 14, 2008 at 5:30 pm

    A few weeks ago, I attended a lecture given by Dr. Pete Severinghaus at the Scripps Institition of Oceanography. During the followup Q&A session, the topic of Mann’s “hockey-stick” came up (with respect to the 2001 TAR).

    Dr Severinghaus’s view was that he considered Mann’s reconstruction to be a “work in progress” at that time, but that it was a perfectly plausible “first crack” at temperature reconstruction. He certainly did not consider Mann’s work to be bad science.

    It is my view that Mann did not choose the best PCA centering convention, but it is quite clear that the choice had very little impact, given that PCA with proper centering (or no PCA at all) will yield results very similar to Mann’s.

    This obsessing over methodological errors with very minor consequences in work that’s a decade old (all the while completely ignoring more recent and up-to-date studies) should tell folks all they need to know about how little substance the skeptics’ arguments have.

  • Will Richardson // March 14, 2008 at 6:02 pm

    There are two simple “facts” which are not disputed in this discussion.

    1. The bristlecone tree ring records used by MBH and subsequent reconstructions, if they are evidence of past temperature (i.e. are proxies for past temperature), are evidence of past temperature for only one small geographical location.

    2. No matter what form of statistical analysis is used, PCA, decentered PCA, or simple average, if the bristlecones are excluded from Mann’s data, Mann’s conclusions are no longer supported by the data.

    Therefore, Mann’s results and the conclusions drawn from such results, are entirely dependent on a decision to include the bristlecone data, regardless of the method used.

    It necessarily follows that Mann’s claim that his reconstruction is material and relevant to world wide temperature of the past, cannot be substantiated because his results and conclusions depend entirely on one data set from one small geographic location.

    Everything else written here

  • Bob B // March 14, 2008 at 6:09 pm

    So What is your answer to this?

    The question for Tamino. Which is incorrect: the information on retained PCs at the Corrigendum SI? Or the claim that the algorithm illustrated at realclimate was used in that form in MBH98? If there is some other explanation, some way of deriving the Vaganov AD1600 and Stahle/SWM AD1750 using the realclimate algorithm, please show how to do it. I’ll post up data and code for my implementation to help you along. C’mon, Tamino. You’re a bright guy. Show your stuff.

  • MrPete // March 14, 2008 at 7:08 pm

    Christ O’Neill, you’ve missed an important aspect of Tamino’s tutorial.

    All that the analysis can do is highlight certain data sets. It is entirely unable to determine whether any data has “temperature” or any other physical meaning.

    (Tamino, if I’ve got that wrong, please correct me! Things like this do get frustrating over time… for all of us :-) )

  • Joel Shore // March 15, 2008 at 4:04 am

    David Holland says:

    [[What words are polite to describe his omitting to mention that he tested his reconstruction for the removal of Bristlecones and Gaspe?]]

    Didn’t the Mann et al. paper “Northern Hemisphere Temperatures During the Past
    Millennium: Inferences, Uncertainties, and Limitations” published in 1999 discuss the issue of removal of such proxies when they said

    [[It is furthermore found that only one of these series - PC #1 of the ITRDB data -exhibits a significant correlation with the time history of the dominant temperature pattern of the
    1902-1980 calibration period. Positive calibration/variance scores for the NH series cannot be obtained if this indicator is removed from the network of 12 (in contrast with
    post-AD 1400 reconstructions for which a variety of indicators are available which correlate against the instrumental record). Though, as discussed earlier, ITRDB PC#1 rep-
    resents a vital region for resolving hemispheric temperature trends, the assumption that this relationship holds up over time nonetheless demands circumspection. Clearly, a more
    widespread network of quality millennial proxy climate indicators will be required for more confident inferences.]]

    It seems to me like there are better ways to bury an issue than to discuss it in Geophysical Research Letters.

  • fred // March 15, 2008 at 7:49 am

    caerbannog writes:

    “it is quite clear that the choice had very little impact, given that PCA with proper centering (or no PCA at all) will yield results very similar to Mann’s.”

    Only if you think that a component appearing at PC1 or PC4 is “very similar”. If the critics are right, that is tantamount to thinking that 8% (which is the amount that PC4 supposedly explains) is the same as some much higher percentage associated with PC1. It just cannot be, can it? If this were true, PCA would be a rather useless tool.

    The significance of MBH was that up to then, we generally accepted that there were natural fluctuations in climate. During one of these, which had been of a magnitude roughly similar to the present warming, the Vikings had colonized Greenland …. etc.

    MBH seemed to show that natural variability was much lower than we and the IPCC had thought. MWP had not really existed, or had been regional. Modern warming was both global and unprecedented.

    If MBH is discredited, this argument goes. We then have to reassess the evidence that modern warming is unprecedented. Refuting MBH doesn’t refute this claim, it just refutes the most commonly cited evidence for it. Not the same thing, but still quite important to get right, even today.

    It does matter whether modern warming is unprecedented. Lets suppose it is found not to be. One argument is that this proves higher climate sensitivity to forcings of all kinds, hence in particular to CO2. The grounds for this would be that some not particularly huge phenomenon caused the previous rise, consequently new rises can also be caused. So in one version of the argument, the real existence of the MWP, contrary to MBH, would be a reason for alarm. Of course you could make a similar argument about the subsequent cooling on the other side: this variant would argue that the climate cools more readily than MBH suggests.

    The importance of MBH is that it is one view of our climate history for the last 1500 years, one in which climate is stable and constant until the Industrial Revolution changed it. It may not be the most important issue in AGW, that may be CO2 sensitivity, but it is certainly a very important one. We really do need to get a firm grip on the history, if we are to place the current fluctuations in context.

  • fred // March 15, 2008 at 7:51 am

    Sorry, it shouldn’t be ‘MBH suggests’ but ‘AGW suggests’. Aargh!

  • Gavin's Pussycat // March 15, 2008 at 1:14 pm

    I find it particularly irksome that so many false statements have been contributed and *repeated* so often. In the past I’ve tried to contradict falsehoods when they’re posted here, but the volume of misinformation has gotten so great I just can’t keep up with it anymore

    Then don’t! Just delete them. And the responses refuting them. Including mine. I have no special attachment to them (and can reproduce them on seconds’ notice anyway). If you had done this consistently on a zero-tolerance basis, you wouldn’t be in this mess now. Give borderline cases the benefit of the doubt if you must, whatever. Refute in the comments if you must, whatever. But you don’t even owe anybody *that*. You’re being accused of censorship anyway so — whatever.

    I would even go further: catch anyone posting the well known lies, and *all* their comments get flushed from the thread (my prediction: you will lose very little of value). And please clean out old threads retroactively. It’s your site, commenters were warned and cannot derive rights from you failing to act on your promise. This stuff will be up and readable for the future, and the state it is in now makes the comments section of any post five times too big and essentially useless.

    It’s about editorial policy. Do what you promise and stick to it. Perhaps then you’ll get some more real debate on other thlngs than how flat or un-flat the Earth really is.

  • James Lane // March 15, 2008 at 1:43 pm

    Chris,

    I wrote: “The higher order PCs are not “noise”, they are constructs that explain more of the variance in ring width than your purported temp PC.”

    You replied: “It’s not up to you or me to decide what the “temperature PC/s” are or are not. That’s the job of the multiple regression. If the multiple regression rejects the stronger PCs, then (like for any proxy that gets rejected), the multiple regression just doesn’t think it has much to do with temperature. If you have a problem with the PCs it chooses, then take it up with it. Has nothing to do with me or Michael Mann or any other person.”

    I now reply: I was pointing out that the higher-order PCs are not “noise” as you assert. You can call them irrelevant or uninteresting but they are not “noise”, unless you are willing to concede that your temp PC might also be “noise”.

    *

    I said: “Which raises the question of what the higher order PCs represent. Precipitation? Humidity? Something else?”

    You replied: Interesting question maybe but regressing against temperature is not expected to answer it.

    I now reply: Of course it won’t. As the regression is against the temp record, the regression stage more strongly weights the proxies that show sharply increasing ring-widths in the 20th century (i.e. the BCPs).

    MBH didn’t need to address the presentation of the other PCs as under the Mannian method, the “temp signal” was in PC1. If the signal was resident in PC4 (explaining 8% of the variance) I suspect that the reviewers of the paper would have been curious about the higher order PCs. (BTW, Rob Wilson assured me some time ago that dendroclimatologists routinely attempt to ascribe physical meaning to PCs other than temperature.)

    *

    You said: “Lastly, I’d like to point out that if James Lane and other readers had understood Tamino’s description of regression on proxy PCs at the beginning of this thread, then they wouldn’t be making the incorrect assertions above.”

    I now reply: Chris, I have been working with PCA for over 20 years, routinely running regression on components. I don’t know if I know more about PCA than Tamino, but I know that I know a lot more about it than you.

    PS, can someone put me out of my misery and explain how to use blockquotes on this blog.

  • luminous beauty // March 15, 2008 at 1:49 pm

    MrPete,

    You’re right. However, the data in this case are measurements of temperature, time and location. All of which have physical meaning.

  • dhogaza // March 15, 2008 at 4:21 pm

    Statements like this boggle my mind, Fred…

    The significance of MBH was that up to then, we generally accepted that there were natural fluctuations in climate.

    Are you seriously claiming that climate scientists don’t believe that there are natural fluctuations in climate, and the reason they don’t is MBH98?

    Foolish statements of this sort really lower your credibility, I’m afraid.

  • Chris O'Neill // March 15, 2008 at 6:28 pm

    James Lane:

    I now reply: I was pointing out that the higher-order PCs are not “noise” as you assert. You can call them irrelevant or uninteresting but they are not “noise”, unless you are willing to concede that your temp PC might also be “noise”.

    I didn’t say they were noise the last time I posted but if you want to get technical then they are noise relative to the the temperature calibration. I originally said it in the context of the signal, i.e. “If there are stronger PCs that do not correlate with our signal then they are just noise”, i.e. noise as in “does not correlate with our signal”.

    As the regression is against the temp record, the regression stage more strongly weights the proxies that show sharply increasing ring-widths in the 20th century (i.e. the BCPs).

    The Noamer PC01 doesn’t increase that much from 1910 to 1945 (the main period during calibration that world average temperature increased) and the standard deviation of the increase was a fair bit smaller than the standard deviation of Noamer PC01. This is only half the calibration period as well so it can only have a fairly small effect on the regression. In spite of this, MBH have tested the effect of removing this small bias and found its effect was also small in MBH98. They decided to explicitly remove the non-climatic influence from Noamer PC01 in MBH99.

    In any case this issue has nothing to do with using principal components analysis so ought to be outside the scope of this thread.

    I suspect that the reviewers of the paper would have been curious about the higher order PCs.

    Maybe but whether they thought it belonged in the paper is another matter.

    (BTW, Rob Wilson assured me some time ago that dendroclimatologists routinely attempt to ascribe physical meaning to PCs other than temperature.)

    I’m sure they do, but that’s beside the issue of making temperature reconstructions.

    I don’t know if I know more about PCA than Tamino, but I know that I know a lot more about it than you.

    Maybe, but paying attention to what Tamino wrote is another matter. BTW, I’ve used multi-linear analysis for over 30 years.

    how to use blockquotes

    [blockquote] and [/blockquote] with the square brackets replaced with angle brackets.

  • David Holland // March 15, 2008 at 6:34 pm

    dhogaza, Fred’s statement is not foolish.

    It is a hard fact that you and others are choosing to ignore. It is why there is such a desperate effort to defend the indefensible and why it will be attacked anywhere free speech is allowed.

    In the Attribution Chapter 12 of the IPCC TAR, written incidentally by the Review Editor/Umpire of of the AR4 Chaper 6, makes this very clear. It cites Mann and his hockey stick. It says on page 702:

    “We expect, however, that the reconstructions will continue to improve and that palaeo-data will become increasingly important for assessing natural variability of the climate system. One of the most important applications of this palaeoclimate data is as a check on the estimates of internal variability from coupled climate models, to ensure that the latter are not underestimating the level of internal variability on 50 to 100 year time-scales.”

    At the time of the IPCC FAR, before the hockey stick, natural variability was thought to be around 1C. The hockey stick says it is nearer 0.2C. This makes the sensitivity for doubling CO2 much higher and gave a false credibility to the alarming forecasts without which there would be no Kyoto.

  • Chris O'Neill // March 15, 2008 at 6:35 pm

    There are two simple “facts” which are not disputed in this discussion.

    I’m only interested in one set of goal posts at a time and I’m praying for the day when people stop talking about principal components analysis on global warming blogs.

  • David Holland // March 15, 2008 at 6:45 pm

    Pussycat,

    I apologise for the repetition, but will you agree that the above quote from the IPCC TAR is a fact and not ? Any reader that doubts it only has to go to IPCC website.

  • dhogaza // March 15, 2008 at 7:51 pm

    dhogaza, Fred’s statement is not foolish.

    It is a hard fact that you and others are choosing to ignore. It is why there is such a desperate effort to defend the indefensible and why it will be attacked anywhere free speech is allowed.

    In the Attribution Chapter 12 of the IPCC TAR, written incidentally by the Review Editor/Umpire of of the AR4 Chaper 6, makes this very clear. It cites Mann and his hockey stick. It says on page 702:

    “We expect, however, that the reconstructions will continue to improve and that palaeo-data will become increasingly important for assessing natural variability of the climate system…

    If, as Fred asserted, climatologists don’t believe in natural fluctuations (variability) in climate, then why are they interested in assessing natural variability?

  • luminous beauty // March 15, 2008 at 8:29 pm

    “At the time of the IPCC FAR, before the hockey stick, natural variability was thought to be around 1C. The hockey stick says it is nearer 0.2C. This makes the sensitivity for doubling CO2 much higher…”

    This is the opposite of correct. A system more sensitive to internal variability is most likely more sensitive to external forcing.

  • MrPete // March 15, 2008 at 9:05 pm

    LB, I’m not sure what you’re referring to when you assert “You’re right. However, the data in this case are measurements of temperature, time and location. All of which have physical meaning.”

    The modern surface record contains the three items you note. None of this analysis refers to the modern surface record. The analysis is applied to proxies.

    The proxies used in these analyses have well-determined location (presuming the ice cores didn’t travel a significant distance.) And the tree rings have extremely good time basis.

    But not a single proxy contains, nor could it contain, a measurement of temperature. If it did, there would be no need for all this analysis. We’d just pick the temperature-measuring proxy and use it.

    So, what are you referring to?

  • David Holland // March 15, 2008 at 9:37 pm

    Joel Shore,

    Your quotation is correct, but reminds me of the hockey supporter who quoted the very last words of the Wegman report. Both are good debating ploys but that is all. Since you raised it, let me quote the very first words of MBH99 which speak to my point a few posts ago, which is that this is all about low historic climate variability supposedly proving high climate sensitivity.

    “Estimates of climate variability during past centuries must rely upon indirect\proxy” indicators”

    In other words “If we can prove there was low variability in the past before the rise in CO2 that must mean CO2 is the cause of recent warming” Statisticians and scientists know it is not necessarily so but to the politicians and the public it is easily sold as proof.

    We know now what PC1 is all about. What your quote and the paper do not say, but Mann’s ftp directory named BACK_to_1400_CENSORED makes clear, is that just 20 of the 112 series provide the “hockey stick”. With the greatest respect to you all the rest is angels on pinheads. A good salesman will always address the obvious shortcomings, make light of them and hope the customer doesn’t look too closely. It helps if the salesman is also on the purchasing team as well – as of course Mann was.

    Since you raised MBH99, consider the red curve in figure 3a. Why does the caption say it is “Raw Data (AD 1902 – 1998)”, when in fact it is “Instrumental Data from Jones and Briffa [1992], updated by personal communication to 1999, but omitting inconvenient divergent data from 1854 to 1902”?

    One again those paying attention know exactly what they are looking at but the gullible never read the papers and relied upon what they were told.

  • luminous beauty // March 15, 2008 at 9:38 pm

    MrPete,

    The analysis is to correlate the less than complete spacial structure of the proxies to the more statistically skillful spacial structure of the instrumental record centered on mutually coherent time periods. It is the physical feature of tele-connection in the earth’s climate that make this meaningful, not statistical analysis, although statistical analysis does show it is a skillful correlation.

    The proxy measures of tree rings or oxygen isotopic fractions in sea and ice cores, etc., are just as much physical temperature measurements as measuring the thermal expansion of fluids and differing metals or electrical conductivity fluctuations over a strip of platinum are in human made thermometers.

    This has been demonstrated by years of research that preceded MBH98, which they reference at length. It is not some new hypothesis they are hoping to demonstrate.

  • David Holland // March 15, 2008 at 10:04 pm

    Dhogaza,

    I note you don’t debate the IPCC quote.

    As to your question –simple. Those wishing to assert that AGW is serious, are interested in assessing natural variability as LOW. Just as those choosing proxies for reconstructions need to choose (no blind sampling here) ones like Bristlecones to prove their point. If they are seekers of the truth in the scientific tradition why do they not go back and find out what has happened to the same tree ring data, which they previously used but that stopped at 1980 (1960 for Briffa) and see if when brought up to date it matches the last 28 years of temperature? The NRC says they should The IPCC say they should. The US is spending $2 Billion on climate research every year. Surely for a million, topside, some hero is going to prove us sceptics wrong by showing that the Bristlecones and Gaspe trees that Mann used have continued to grow as they did in the past. It seems so simple to me I can’t figure out why we are still debating it.

  • dhogaza // March 15, 2008 at 10:11 pm

    “Estimates of climate variability during past centuries must rely upon indirect\proxy” indicators”

    Perfectly true, simple, straightforward statement. Absent the existence of time machines, there’s no other way.

    In other words “If we can prove there was low variability in the past before the rise in CO2 that must mean CO2 is the cause of recent warming”

    What a stunningly dishonest claim. This in no way follows from the straightforward quote you provide.

  • dhogaza // March 15, 2008 at 10:29 pm

    I note you don’t debate the IPCC quote

    Why would I? It has nothing to do with the fact that Fred’s claim is patently false.

    He said that climatologists don’t believe there’s natural fluctuations in climate, which is just dumb.

    As to your question –simple. Those wishing to assert that AGW is serious, are interested in assessing natural variability as LOW

    Oddly, we just don’t see climatologists arguing that ice ages are a fiction, or that there have been periods of time when the earth has been much warmer than it is today.

    I imagine you’re referencing the MWP, and that you’re arguing against the scientific research which shows that it was a regional, not global, event. Note that this claim doesn’t have anything to do with the limits of natural variation in climate in any general sense.

  • David Holland // March 15, 2008 at 10:30 pm

    luminous beauty,

    You say “A system more sensitive to internal variability is most likely more sensitive to external forcing.”

    Why do you not say it is absolutely definitely so? Is it because this is, no matter well thought of, just another part of the AGW conjecture? It might be true of course. The problem is we do not know nearly enough or have nearly enough data to make models reliable enough to say.

    As for your second paragraph in reply to Pete “I can not believe you are serious”. It is not just the comparison of the physics and biology that matters but the provenance of the data. But your mindset does explain why Mann had no qualms about dumping instrumental temperatures from 1854 to 1902 in favor of his proxy based ones.

  • David Holland // March 15, 2008 at 10:45 pm

    dhogaza,

    I note again , before turning in for the night that you still do not debate the quote from Chapter 12 of the TAR, from which as I understand the “hockey stick” is what gives them confidence that their models were right.

    If this is not the reason you guys are doing an Alamo, what is it? Why not just say heck, he got it wrong?

  • TCO // March 15, 2008 at 11:28 pm

    Chris O’neal:

    Stepping back a second: how well do you think (intuitively, in a betting Bayesian sense) that a PC that is 8% of variation and 4th on the list* will do in true out of sample tests?

    Does it bother you that the “calibration” is done versus global temp versus local?

    How “wiggly” is the calibration? Are we effectively just matching trend to trend? Any danger that the reconrds themselves may have autocorrelation and have trends that are long as such from random walk effects?

    —————————

    It’s a small detail, but I beleive the more appropriate metric may be the correlation matrix (standard deviation divided) PCs. I beleive these will give some story that is intermediate between the PC1 (37%) and PC4 (8%) citations.

  • dhogaza // March 15, 2008 at 11:29 pm

    The problem is we do not know nearly enough or have nearly enough data to make models reliable enough to say.

    Yet this doesn’t stop you from confidently stating that

    As to your question –simple. Those wishing to assert that AGW is serious, are interested in assessing natural variability as LOW…

    So let’s see, climatologists believe that greater sensitivity to natural forcings than is believed would also lead to a greater estimate of the forcing due to increasing CO2.

    Yet you believe that they want to minimize the bounds of natural variation because that, too, would lead to a greater estimate of the forcing due to increasing CO2?

    You seem to have a problem keeping your story straight.

  • dhogaza // March 15, 2008 at 11:31 pm

    I note again , before turning in for the night that you still do not debate the quote from Chapter 12 of the TAR, from which as I understand the “hockey stick” is what gives them confidence that their models were right

    You understand wrong. Modelers have confidence in their models for many, many reasons. This is not the thread for such a discussion, though, and given your track record I suspect you’d make a few “interesting” interpretations of what scientists believe to be true, etc.

  • MrPete // March 16, 2008 at 12:47 am

    LB, “The proxy measures of tree rings…are just as much physical temperature measurements as measuring the thermal expansion…in human made thermometers…This has been demonstrated by years of research that preceded MBH98…It is not some new hypothesis they are hoping to demonstrate.”

    LB, please. Don’t put your foot in your mouth. Go take a look at the principles of dendrochronology (a much simpler science than dendroclimatology, BTW). It is nowhere near as straightforward as you suggest.

    I’ll not bother with a comprehensive list of extremely significant differences; here are two just to get you started. Both of these relate to dendro principles… which provide boundaries to the usefulness of the data. You can look these up to get a beginning sense. Then talk with a dendro expert or two to get a real world feel. Talk with a biologist. Talk with a gardener for that matter about #1 below.

    1) The principal of Limiting Factors. Plant growth is optimal with the right amount of several required resources, such as heat, water, sunlight and nutrients. With too little or too much of these, growth is stunted. Quite frequently (often annually!), plants experience out-of-range conditions under which they cannot grow. And we can’t tell the difference later on. Nor can we tell which factor is the most-limiting factor later on. Nor can we be certain that the limiting factor has been constant throughout the plant’s lifetime. These challenges hardly have an analogy in any realistic modern thermometer.

    2) The Principle of Replication. Unfortunately, it doesn’t apply very well under all conditions. In particular, it doesn’t apply to strip bark BCP’s. We measured growth variation of up to 400% at different times in the past, among different samples from a single tree, let alone multiple trees. That challenge has no analogy with modern thermometry.

    These are not issues that can be swept away through complex statistical manipulations. If the underlying data does not relate to the physical aspect of interest, you can’t make it so simply by finding a correlation. Particularly when taking a new set of data from the same trees in the same place produces results that vary by 400% from the original data set.

    So let’s return to the question: why should we be confident that there’s a temperature signal to be found in the BCP data, and all we need is to do the stats work to find the correlation? Why should we be so confident that we ignore out-of-sample “divergence,” presuming that the rest of our analysis is correct even when the updated tree data no longer matches the temperature signal?

    One must be very careful about presuming the physical meaning of a correlated analysis.

  • MrPete // March 16, 2008 at 12:57 am

    I neglected to bold/emphasize the primary point in #1 — that both under AND over cause lower growth. It’s not monotonic.

    To be clear: how do you read the meter below, whose “bar” rises from 0 to 20, then falls from 20 to 40?

    20 20
    15 25
    10 30 ==
    05 35 ==
    00 40 ==

    There are two small challenges:
    a) What’s that meter reading? It’s the high for the month.

    b) What’s the meaning of the reading? Is it temperature, precipitation, nitrogen availability, or something else? Why do you know that?

    This is what trees give us. Yes, in many cases we can get a good idea of the physical meaning(s). But the stats are not where we learn the physical meaning.

  • Joel Shore // March 16, 2008 at 1:33 am

    David Holland: Basically, what I read from your response is that you have already decided that Mann et al. are guilty of various nefarious deeds and thus you are going to attribute any decision they ever made to say things any differently than you might of wanted them said or to plot things any differently than you might wanted them plotted as some vast conspiracy. Nothing they can do will ever satisfy you. You will always feel it could have been presented differently or whatever and this is a clear sign of nefariousness.

    Of course, if I applied the same conspiratorial point-of-view to your paper in Energy and Environment, I could have a field-day but I won’t engage in such a things (although it is a bit tempting!)

    And, I really don’t think your claims about the reconstructions being used to prove high climate sensitivity hold much water either. For one thing, studies have noted that the instrumental temperature record simply cannot provide very tight constraints on climate sensitivity at the moment. Better estimates are obtained by other means, such as modeling, the climate response to large volcanic eruptions like Mt. Pinatubo, and to past historical events like the glacial - interglacial transition. For another, you are failing to distinguish between true internal variability and responses to (natural) external forcings. Without good knowledge of the external forcings, having such a flat reconstruction is actually a mixed bag: It does imply low internal variability and hence make the late 20th century look more unusual but, to the extent that external forcings like solar also varied over that time period, then it would tend to imply a lower climate sensitivity than a more wiggly reconstruction like Moberg’s does. I believe there is some paper that even demonstrates this.

    So, while it is definitely a useful exercise to determine what the past climate variability has been and can serve some useful purposes, the connection from that to what the climate sensitivity is is subtle and probably involves also making parallel progress in understanding of the natural forcings over that time period.

  • Larry Huldén // March 16, 2008 at 9:10 am

    There was an interesting suggestion by Zeke // March 6, 2008 at 10:22 pm ” Do an uncentered PCA on a randomly generated dataset that exhibits a warm period or two in the past that exceeds present temperatures. See if this warm period drops out of the results.”
    When McIntyre & McKitrick studied the hockey stick they noted that Manns method enhanced recent warming AND compressed variability in the past. As a consequence a warm period in the past, equal to present period, wouldn’t show up.
    May be somebody already has commented on this.

  • David Holland // March 16, 2008 at 2:00 pm

    dhogaza,

    Your story is not too straight . In response to Fred you said,

    “Are you seriously claiming that climate scientists don’t believe that there are natural fluctuations in climate, and the reason they don’t is MBH98?”

    No he didn’t and I haven’t. Fred said,

    “MBH seemed to show that natural variability was much lower than we and the IPCC had thought. MWP had not really existed, or had been regional. Modern warming was both global and unprecedented.”

    The dispute is not between some variability and none and no one else besides you suggested it was. Then you say,

    “So let’s see, climatologists believe that greater sensitivity to natural forcings than is believed would also lead to a greater estimate of the forcing due to increasing CO2.”

    Who said that? We were talking about natural variability not forcings. I know what others believe but that does not mean I do or that they are right. Then you switch to,

    “Modelers have confidence in their models for many, many reasons. This is not the thread for such a discussion”.

    Tell me where you do want to discuss it.

    My story is straight. Regardless of PCA, the Mann et al studies fail verification and are not robust against the removal of 20 out of 112 proxies. If you are so sure these proxies were valid, get out there and update them so that you can show they are still valid for the last 28 years. Why don’t we discuss why no one has? How hard would it be? What are the problems if any? The trees are still there.

    Joel Shore,

    Thanks for mentioning my paper. Anyone that is interested is welcome to read it at http://tinyurl.com/2szwh8 and I’m sure Steve McIntyre at CA will allow you your field day. You will not find the words “nefarious” and “conspiracy” in the paper. You, and in one case the Bulldog, were the only ones, prior to this post, to use either on this thread. But if the cap fits

    All I have done is to point to Mann’s contradictions, which are a matter of provable fact. I have no evidence that they are other than mistakes, even though there are a lot, and I have not suggested otherwise.

    I heard this statement a few hours ago watching an event that saw some well-known self-confident young men brought down a peg or two.

    “Skill is rewarded, mistakes are punished, and that’s how it should be, isn’t it, at this level. These are the finest . . . . . in the world”.

    Regrettably it was not the IPCC assessment of the “hockey stick” and sadly the missing word was “drivers” and not palaeoclimatologists.

  • dhogaza // March 16, 2008 at 2:38 pm

    Look, dude, I quoted fred directly, via cut-and-paste:

    The significance of MBH was that up to then, we generally accepted that there were natural fluctuations in climate.

    and now you’re pretending as though I responded to something else Fred said.

  • dhogaza // March 16, 2008 at 2:42 pm

    Thanks for mentioning my paper.

    Energy and Environment, pfft. The fact that you’re willing to associate yourself with that rag is all I need to know.

  • kim // March 16, 2008 at 2:49 pm

    dhogaza, your response to DH at 2:42 is rhetorically poor.
    ====================

  • TCO // March 16, 2008 at 2:54 pm

    I’m a skeptic and I have a very low opinion of E&E. Actually it makes me feel bad and worried that my side can’t write clear articles and publish them in normal journals.

  • David Holland // March 16, 2008 at 3:05 pm

    And so can I dhogaza, this is Fred’s quote in context. The key words are MUCH LOWER.

    “The significance of MBH was that up to then, we generally accepted that there were natural fluctuations in climate. During one of these, which had been of a magnitude roughly similar to the present warming, the Vikings had colonized Greenland …. etc.
    MBH seemed to show that natural variability was much lower than we and the IPCC had thought. MWP had not really existed, or had been regional. Modern warming was both global and unprecedented.”

    And this was your comment,

    “Are you seriously claiming that climate scientists don’t believe that there are natural fluctuations in climate, and the reason they don’t is MBH98?
    Foolish statements of this sort really lower your credibility, I’m afraid.”

    He was not claiming what you asked and had not made a foolish statement. I think we really have exhausted the topic now.

  • Chris O'Neill // March 16, 2008 at 3:25 pm

    how well do you think (intuitively, in a betting Bayesian sense) that a PC that is 8% of variation and 4th on the list* will do in true out of sample tests?

    Tamino’s test PC2 did extremely well.

  • David Holland // March 16, 2008 at 3:25 pm

    dhogaza, I did not mind being in the company of John Zillman, who wrote the first article in Energy and Environment, nor the other highly respected authors.

    Along with Joel you are welcome to to explain to to the world at large the defects you see in my paper on page 2326 of the winner of the 2007 Best Science Blog award. Or better still write a paper yourself.

  • Boris // March 16, 2008 at 3:42 pm

    David Holland,

    Your paper contained the following statement:

    “The Stern Review2 said “The
    causal link between greenhouse gases concentrations and global temperatures is well
    established, founded on principles established by scientists in the nineteenth century.”
    This is both disingenuous and plainly wrong.”

    Given such a ridiculous position, why should we trust you to fairly and objectively evaluate the hockey stick?

    I guess you could say you were talking about climate sensitivity and not the basic warming caused by CO2. But even then, your discussion of climate sensitivity is just as wrong–if not more so.

  • caerbannog // March 16, 2008 at 3:48 pm


    There was an interesting suggestion by Zeke // March 6, 2008 at 10:22 pm ” Do an uncentered PCA on a randomly generated dataset that exhibits a warm period or two in the past that exceeds present temperatures. See if this warm period drops out of the results.”
    When McIntyre & McKitrick studied the hockey stick they noted that Manns method enhanced recent warming AND compressed variability in the past. As a consequence a warm period in the past, equal to present period, wouldn’t show up.

    Basically, you are saying that if Mann et al were to repeat their computations using centered PCA or no PCA at all, a big MWP should pop up. Is that correct?

  • L Miller // March 16, 2008 at 5:39 pm

    If, as Fred asserted, climatologists don’t believe in natural fluctuations (variability) in climate, then why are they interested in assessing natural variability?

    Unexplained climate variation certainly exists but that doesn’t mean it will remain unexplained forever. As we learn and understand more one would expect the range of these unexplained variations to diminish. Although many of these unexplained variations are clearly natural in origin I suspect some people are attributing a significantly different meaning to the phrase natural variation.

    I suspect they believe that “natural” *IS* the explanation for the variation, and therefore no further understanding is required and no amount of study could ever qualify why these changes occurred. Even if they do believe there was a cause like changes in solar intensity, they really don’t want that looked at to closely because being able to show “it was the sun” back then implies we can also show “it’s CO2 now”

    I very much doubt many climate scientists believe in natural variation of this kind, rather they believe in climate variation with natural causes they can identify and study.

  • David Holland // March 16, 2008 at 6:39 pm

    Boris, we clearly have different views on what “firmly established” means. You might claim the physics of the components of the climate system might are well understood, but even there some controversies exist. But I do not see how you can claim the relationship between cause and effect on any matter is well established when you can’t say within a range of 2 to 1 what the effect of the cause is.

    I am not asking you trust me to fairly and objectively evaluate the hockey stick? We could never persuade each other that we could that. However for anyone that does not have a mindset on the “hockey stick” I have made an attempt to explain the process by which it became accepted and more importantly was recently defended. In researching the subject I have come to realise that the IPCC does not function as its agreed Principles say it should, and that it is in effect unsupervised. So far as I can establish the reports of the Review Editors whose job it is to ensure the Principles were followed have not been read by the officials of any government or (and I have asked the question) by the IPCC panel itself.

    Since no doubt you are happy with the IPCC assessment outcome you may feel that the means justifies the end. That’s a very dangerous precedent to set.

  • Barton Paul Levenson // March 16, 2008 at 10:15 pm

    fred writes:

    [[MBH seemed to show that natural variability was much lower than we and the IPCC had thought. MWP had not really existed, or had been regional. Modern warming was both global and unprecedented.

    If MBH is discredited, this argument goes.]]

    fred, you’re not paying attention. At least 14 subsequent studies have replicated MBH’s results since then. MBH can go and there still won’t be a global midieval warm period or extreme natural variation on short time scales.

  • TCO // March 16, 2008 at 10:38 pm

    Chris: Come on, man. Engage the questions. I can play blog one-upsmanship with the best of them. I have an awful trolling rep. I’m trying to be good. Seriously, step back and take a hack at the questions. Imagine that passions were not inflamed and people on “sides” and we just wanted to canoodle this thing a bit.

  • henry // March 17, 2008 at 12:11 am

    BPL:

    “fred, you’re not paying attention. At least 14 subsequent studies have replicated MBH’s results since then. MBH can go and there still won’t be a global midieval warm period or extreme natural variation on short time scales.”

    Do you include Loehle 07 as one of the 14?

  • fred // March 17, 2008 at 6:47 am

    We need to get a clear view of our climate history over the last 1500 or so years.

    MBH and all the studies based on its proxies and methods have to be put aside now. We are back where we were before. There now seem to have been two episodes of warming, one in late Roman times, one in the Medieval period. Each was followed by cooling, the most recent period being the LIA. Its not clear whether the warmings were as warm as today, less warm, or about the same. There seems to be evidence the MWP was more than regional. We do not seem to know what caused these warmings and coolings.

    This does matter, because of the argument from exceptionalism, and that is why MBH (and its offshoots) is more than an obscure 10 year old paper. The argument from exceptionalism is logically valid. It goes something like this: modern warming is unprecedented, unprecedented climate events are worrying. Yes, they are, and the question is whether modern warming really is unprecedented, and that is why MBH mattered, and why we need more and better work to establish yes or no, is MW really unprecedented.

    People sometimes argue that it makes no difference. The argument used goes like this: suppose natural variability is as great as we used to think it was before MBH. Suppose the MWP was as substantial as the early IPCC graph, pre MBH, showed. Then its argued, this shows a high degree of climate sensitivity, and would prove a high sensitivity to CO2.

    This argument is used to suggest that the climate history does not matter. Either way we should worry. However it is logically fallacious. You cannot prove the climate is sensitive to CO2 by citing fluctuations which no-one thinks were caused by it. They are simply irrelevant to the CO2 question in this form of the argument.

    Now it could be that Roman and MWP fluctuations were as large as today’s, and not caused by CO2, and that such fluctuations are common on a scale of thousands of years, but still also be true that CO2 sensitivity is high, and that the present warming is the start of a quite different and much more alarming phenomenon. Just because CO2 did not rise and so did not cause the Roman and MWP warmings does not mean its rise cannot cause catastrophic warming today.

    Therefore, while we should get to the bottom of the climate history question, a more fundamental question is climate sensitivity. AGW really hangs on this in a way that it does not on climate history.

    David H and others, thank you for your support, but perhaps the moral is, not to feed the troll? My own policy is to ignore.

  • sod // March 17, 2008 at 8:06 am

    Do you include Loehle 07 as one of the 14?

    Loehle was forced to correct his paper, because he had misdated several of his proxy series.
    the result is a study, that has its proxies ending in 1935.

    http://www.ncasi.org/Publications/Detail.aspx?id=3025
    (the corrections are at the END of the pdf)

    while the new result still shows a prominent MWP, it does NOT show, that the MWP was warmer than temperatures today or at the end of the 20th century.

    so yes, the Loehle paper DOES confirm the hockey stick.

  • Michael Smith // March 17, 2008 at 11:26 am

    BPL wrote:

    “fred, you’re not paying attention. At least 14 subsequent studies have replicated MBH’s results since then. MBH can go and there still won’t be a global midieval warm period or extreme natural variation on short time scales.”

    David Holland’s paper quotes from Wegman’s conclusions about these additional studies:

    “The social network analysis of authors’ relations suggests that the “independent
    reconstructions” are not as independent as one might guess. Indeed, the matrix
    outlined in Figure 5.8 illustrates the proxies that are used more than one time in
    twelve major temperature reconstruction papers. The black boxes indicate that the
    proxy was used in a given paper. It is clear that many of the proxies are re-used in
    most of the papers. It is not surprising that the papers would obtain similar results
    and so cannot really claim to be independent verifications.”

    That’s from page 16 of David’s report.

  • Michael Smith // March 17, 2008 at 12:40 pm

    sod wrote, concerning Loehle:

    “while the new result still shows a prominent MWP, it does NOT show, that the MWP was warmer than temperatures today or at the end of the 20th century.

    so yes, the Loehle paper DOES confirm the hockey stick.”

    Sod, are you seriously trying to argue that a study which shows “a prominant MWP” CONFIRMS a study that shows little or no MWP?

  • Michael Smith // March 17, 2008 at 12:42 pm

    By the way, I hope all who are posting here will take the time to read David Holland’s paper here:

    http://homepages.tesco.net/~kate-and-david/2007/Holland(2007).pdf

    It doesn’t take long to read and doesn’t require specialized knowledge of math or statistics.

  • sod // March 17, 2008 at 12:46 pm

    “The social network analysis of authors’ relations suggests that the “independent
    reconstructions” are not as independent as one might guess.

    did Wegman analyse the sceptics with a similar method?

    the result of course would be that there are ZERO independent sceptics!
    (of course he shouldn t restrict the network analysis to peer reviewed papers, because that would yield about ZERO sceptics anyway…)

  • MrPete // March 17, 2008 at 12:55 pm

    sod, if “while the new result still shows a prominent MWP, it does NOT show, that the MWP was warmer than temperatures today or at the end of the 20th century.” is confirmation of the hockey stick, then you have a very loose definition of “confirm”

    Are you thinking that’s a seriously useful scientific statement, or are you purposefully trying to diminish what Loehle’s paper demonstrated?

    What your statement neglects to mention: Loehle shows MWP was warmer or at least about as warm as, the 1930’s. Fine, Loehle doesn’t have a comment on today. So what?

    a) 1930’s was vanishingly close to the warmth seen today.

    b) The hockey stick was novel not because of late 20th century warming. It was novel because of a flat handle… no MWP, hardly any LIA.

    If a paper shows MWP was warmer or even almost as warm as 1930’s, and you believe that confirms the hockey stick, I guess it’s gonna be hard to discuss “confirm” or “falsify.”

    Is Loehle’s “handle” (1000-1800 graph) confirming of the Hockey Stick handle? Not that I can see.

    Does Loehle’s graph show MWP warmth similar to early 20th century warmth? Yes, as far as I can tell.

    Are the early and late 20th century temp records similar? AFAIK, the honest answer is: yes in the USA, and controversial for the rest of the world because the data we have is both spotty and highly contested (not just by “denialists”)

    I don’t find Loehle giving strength, assurance, evidence, proof or convincing testimony to the validity of the hockey stick.

    If you want to call that kind of result a “confirmation”… then please tell us what dictionary you use. It is not one I’ve seen before.

    OK, time to start my day… ;)

  • sod // March 17, 2008 at 1:24 pm

    Sod, are you seriously trying to argue that a study which shows “a prominant MWP” CONFIRMS a study that shows little or no MWP?

    the original hockey stick is a reconstruction from 1000 till NOW.
    Loehle does a reconstruction from 0 till 1935.
    these are VERY different periods.

    if you look at the Loehle graph from 1000 till 1935 and then add the warming that we saw since 1935, the MWP becomes a nice knob at the end of the handle.

    http://www.realclimate.org/HockeyStickOverview_html_6623cbd6.png

    if you think that all the Mann et al reconstructions showed a flat handle, then you haven t been looking at the graphs recently!

    ps: if we had this discussion 2 years ago, everyone would have been claiming that the MWP was AFTER 1000….

  • L Miller // March 17, 2008 at 3:19 pm

    David Holland’s paper quotes from Wegman’s conclusions about these additional studies:

    “The social network analysis of authors’ relations suggests that the “independent
    reconstructions” are not as independent as one might guess. Indeed, the matrix
    outlined in Figure 5.8 illustrates the proxies that are used more than one time in
    twelve major temperature reconstruction papers. The black boxes indicate that the
    proxy was used in a given paper. It is clear that many of the proxies are re-used in
    most of the papers. It is not surprising that the papers would obtain similar results
    and so cannot really claim to be independent verifications.”

    That statement alone is enough to completely discredit Wegman. It’s unprofessional hand waving that doesn’t have a place in scientific discussion. He is essentially dismissing a whole field of scientific study out of hand without having g any expertise in thayt field or even having looked at the work itself. Furthermore it’s a tacit admission that the proxy data itself and not the analysis techniques gave rise to the MBH reconstruction.

    “It is clear that many of the proxies are re-used in most of the papers. It is not surprising that the papers would obtain similar results” can only be true if the proxy data really does support the temperature reconstruction in question. I.E. he is dismissing ht proxy data itself even though he has absolutely no relevant qualifications.

  • L Miller // March 17, 2008 at 3:31 pm

    <blockquote?
    We need to get a clear view of our climate history over the last 1500 or so years.

    MBH and all the studies based on its proxies and methods have to be put aside now. We are back where we were before. There now seem to have been two episodes of warming, one in late Roman times, one in the Medieval period.

    How exactly are you reaching that conclusion if you are throwing out all the quantitative data on what temperatures actually were in that period?

  • Armagh Geddon // March 17, 2008 at 4:03 pm

    Just curious, but why is it that no one is answering the question about what happens if the proxies are updated to the present?

    Wouldn’t it be compelling proof if the updated proxies showed a close correlation with temperature?

  • dhogaza // March 17, 2008 at 5:19 pm

    That statement alone is enough to completely discredit Wegman. It’s unprofessional hand waving that doesn’t have a place in scientific discussion.

    Can you imagine Wegman advising FDR when his administration was pondering whether or not to start a crash program to build an atomic bomb?

    “Social network analysis shows that all these nuclear physicists know each other, have worked together, and are using the same experimental results from a handful of researchers. Their results can’t be trusted”.

    And, ironically, the close-knit nature of that community was one of the arguments in FAVOR of the project, in particular the fact that Heisenberg was still in Germany, working for the government …

    Wegman’s handwaving on this subject is as silly as his claim that CO2 forms a layer near the earth’s surface because because it weighs more than more plentiful gasses …

  • Michael Smith // March 17, 2008 at 9:09 pm

    Sod, your various claims are quite confusing.

    First, you claimed that Loehle, as is, “confirmed” the hockey stick.

    Then, you pointed out that Loehle covered ” a VERY different period of time”.

    Next, you claimed that if Loehle were modified by adding the post 1935 instrument record, ” the MWP becomes a nice knob at the end of the handle”.

    And finally, you attempt to suggest that the hockey stick has the same sort of MWP as Loehle.

    The only sense I can make out of your claims is to interpret them as saying that Loehle does not conclusively refute or contradict the hockey stick. Even if that is true, it doesn’t justify the notion that Loehle “confirms” the hockey stick.

  • Michael Smith // March 17, 2008 at 9:19 pm

    L Miller and dhogaza — you are both employing “straw man” arguments.

    Wegman is not, as L Miller claims, “dismissing a whole field of scientific study out of hand without having g any expertise in thayt field or even having looked at the work itself.”

    Nor does he say, as dhogaza implies, that “Their results (the study’s results) cannot be trusted.”

    Wegman’s social networking analysis is only assessing the claim that these other studies are “independent reconstructions”. His analysis casts some doubt on THAT CLAIM, not on the claims of the studies themselves.

  • dhogaza // March 17, 2008 at 9:48 pm

    The only sense I can make out of your claims is to interpret them as saying that Loehle does not conclusively refute or contradict the hockey stick

    Given the uncorrected errors in Loehle’s paper, I think that’s a fairly safe statement.

  • sod // March 17, 2008 at 10:26 pm

    Wouldn’t it be compelling proof if the updated proxies showed a close correlation with temperature?

    Büntgen has some tree proxies reaching up to 2003 (???), if i remember correctly..

    http://www.wsl.ch/staff/jan.esper/publications/Buentgen_2006_JoC.pdf

    notice the hockey stick form…

  • sod // March 17, 2008 at 10:34 pm

    Sod, your various claims are quite confusing.

    sorry if i confused you.

    so slow again:

    if two graphs cover different time intervals, then they will confirm each other, WHEN they look similar over the time they overlap.
    this is the case for Loehle and Mann between 1000 and 1935.

    whether the Loehle reconstruction looks “different” (from what???) before 1000 is completely irrelevant in a comparison with the ORIGINAL hockey stick that only STARTS in 1000.

    (as this discussion is going far off topic, i will copy this post into the open topic and only reply there from now on)

  • Boris // March 17, 2008 at 10:41 pm

    MrPete said:

    “1930’s was vanishingly close to the warmth seen today.”

    This statement is not even close to being correct.

  • dhogaza // March 17, 2008 at 11:37 pm

    Wegman’s social networking analysis is only assessing the claim that these other studies are “independent reconstructions”. His analysis casts some doubt on THAT CLAIM, not on the claims of the studies themselves.

    Whether or not folks know each other or have worked together is irrelevant. It’s just a stupid claim on Wegman’s part.

    Now, onto that deep layer of CO2 that supposedly is suffocating us all, any reason you didn’t back up hero of the hour Wegman on that one?

  • TCO // March 18, 2008 at 1:09 am

    The relationships of the people and the commonality of proxies are TWO ISSUES. People who know each other might be group thinkie (or they might not). If studies tend to use the same proxies than it argues that multiple studies are not independant confirmations (they could still be correct, they’re just not completely separate and additive.)

    People you can argue either one of these issues and argue them for either side, but at least realize that they are different. Otherwise it’s like saying the NY Yankees are the best football team.

    And Wegman’s boner on the CO2, he admitted to. If that invalidates his opinions on statistics, than you are going to have to write everyone on the planet off on everything they say. (BTW, I found Wegman’s social network stuff interesting, but very speculative and tentative. I wish instead that he had dug deeper into the statistics itself. He’s probably there with Jolliffe, Tamino, etc. in not understanding all the details of the Mannian method and of how alternate choices in the method give alternate results. However this is the area of interest, people. This is what this post was about in the beginning. This is an area where I bet Tammy has remaining questions and thoughts.

  • kim // March 18, 2008 at 1:14 am

    C’mon, dhogaza, your 11:37 post is patently absurd. ‘Independent’ and ‘worked together’ are contradictory. Tighten up that rhetoric if you want to be persuasive.
    ========================

  • cce // March 18, 2008 at 2:06 am

    There were three people responsible for the Wegman Report: Wegman, Scott, and Said, and Said was one of Wegman’s former grad students. They were all statisticians, and I suspect that they approached the alleged flaws the same way an English professor approaches a dangling particple, which is to say, a very serious matter. If they were concerned about diverse opinions, they didn’t apply it to themselves.

  • MrPete // March 18, 2008 at 2:27 am

    Boris, c’mon. That statement was with respect to US instrument record. US instrument record says 1930’s and recent decade share warmest years within a very close amount — the whol McIntyre/GISS tiff on that was over adjustment-level data changes that swapped the leaderboard. Some people said the shift was significant, some said it was not… but in either case, they were close enough so that some small adjustments caused the leader list to change. Obviously, they were similar. If they weren’t, it would take a big change to cause any adjustments to the leader list.

  • dhogaza // March 18, 2008 at 2:43 am

    Obviously, they were similar. If they weren’t, it would take a big change to cause any adjustments to the leader list.

    One year does not a decade make …

  • dhogaza // March 18, 2008 at 2:45 am

    Here, dude …

    http://www.nasa.gov/centers/goddard/images/content/169049main_1880_2006_gms.jpg

  • dhogaza // March 18, 2008 at 2:47 am

    Eh, sorry for the repetitive posts, I just realized that Mr. Pete is one of those who are unaware that the lower 48 United States is not the world …

    Mr. Pete, no swap on the leaderboard happened for the GLOBAL mean temperature. 1934 and 1998 for the lower 48 went from being statistically tied to being statistically tied. But not the global average.

  • Boris // March 18, 2008 at 2:52 am

    Loehle’s reconstruction was supposed to be global, not from the US. And if you think the global temps are junk, then how can you place your reliance on a reconstruction calibrated to those temperature records.

  • Bob North // March 18, 2008 at 4:03 am

    Sod -
    Thank you for the reference to the Bungen et al. paper (and the whole paper, not just an abstract). The paper helped show that Dendroclimatology, when done right, actually does have something useful to show us and that correlations between tree rings and temperatures can be pretty darn good.

    However, I disagree about seeing the hockey stick shape. If their temperature reconstruction is a hockey stick, that is one mighty bent handle. The summer month temperatures around 970 AD and ~ 1100 AD appear to be pretty darn similar to the current temperature range. Interestingly, the Buntgen reconstruction seems to show relatively steady summer-month warming since about 1700, with two short and distinctly cooler periods - one around 1816 and one around 1960 or so. Just eyeballing it, it appears that very rapid temperture rise in the last couple of decades of the 20th century just brings us back to the centuries long trend, at least for this proxy set. Interesting stuff.

    Bob North

    BobN

  • Petro // March 18, 2008 at 5:08 am

    dhogaza realized:

    “Eh, sorry for the repetitive posts, I just realized that Mr. Pete is one of those who are unaware that the lower 48 United States is not the world …”

    Mr. Pete’s error is trivial. His claim “1930’s was vanishingly close to the warmth seen today.” has been debunked completely a thousand times during last two years. Anyone looking the global temperature records can see this easily.

    That Mr. Pete still believes his false statement and ejaculates it proudly is just one evidence on the emptiness his argumentation.

  • fred // March 18, 2008 at 8:09 am

    I Miller “How exactly are you reaching that conclusion if you are throwing out all the quantitative data on what temperatures actually were in that period?”

    Easy, though maybe less precise than one would like. Not all the information on past temperatures comes from MBH. Look at the early IPCC reports.

  • MrPete // March 18, 2008 at 11:05 am

    Boris, dhogaza, please don’t waste our time by quoting me out of context. I believe my posting expanded on that statement by saying:
    “Are the early and late 20th century temp records similar? AFAIK, the honest answer is: yes in the USA, and controversial for the rest of the world because the data we have is both spotty and highly contested (not just by “denialists”)
    Did that not make it clear enough?
    We don’t have enough reliable temp data on ROW to say anything about early vs late 20th century. Yes, dhogaza, one can make a graph. One can make all kinds of graphs. Show me an accurate CI on that graph. You can’t, because the ROW temp data can’t hold a candle to the US data, which itself is subject to serious after the fact “correction” based on a lot of assumptions.
    I don’t know why y’all keep defending this stuff. I’m honestly not here to argue about the content of unclear data sets and poorly done analysis. Glad to talk about things we know or can be known, and glad to talk about improving science. Why waste time peering into a muddy lens? Let’s clean the lens or find a better way to see clearly.
    For some reason, you’re bent on defending anything that even *poorly* “proves” AGW.
    What’s next, Royal Jelly and Snake Oil? Let’s stick to science, please.
    Can you hear what James Lane is saying above? Not the surface of his statements, the truth underneath.
    Please… Step back, let go of a particular perspective on what you want the “answer” to be, examine the data and process to see if it is producing real insight and understanding about our world.
    A brief illustration from my background in data analysis…
    Take a few data sets, one has no trend and low variance, one has no trend and high variance, one a sharply increasing trend, one a sharply decreasing trend. Run them through a block box processing algorithm. Now compare to what one sees in the Real World. One of the data sets is a pretty good match to the Real World numbers.
    Does that mean I’ve found a measure for the Real World numbers?
    Can you see that the answer is no? The analysis only helps find a correlation.
    Other work is required to even have a hint about physical implications. This is true across the board.
    This thread has provided ample evidence that a lot of smart people are not skeptical enough about assumptions of causality. Never too late to learn!

  • MrPete // March 18, 2008 at 11:14 am

    Boris, I agree with you when you say, “how can you place your reliance on a reconstruction calibrated to those temperature records.”
    Exactly. What value is there? There is value, yet it’s not as useful as many want to believe.
    We want to be confident that we understand the past and can predict the future. People are actually pretty bad at both (except in things like physics, chemistry, etc.), particularly when it comes to applying science to policy.
    Personally, that’s why I get concerned about overconfidence in poor science. It’s hard enough when we’re applying good science :-)
    I’ll stop now…this isn’t a policy blog and I don’t have the time anyway….

  • Michael Smith // March 18, 2008 at 11:39 am

    Sod, the fundamental conclusion of the hockey stick was that the warming of the late twentieth century was “unprecedented” in the last thousand years. To claim that Loehle “confirms” the hockey stick — simply because Loehle “looks like” a PORTION of the hockey stick — a portion that, according to your claims, does not even include the allegedly “unprecedented warming” — is unsustainable.

  • Michael Smith // March 18, 2008 at 12:22 pm

    dhogaza wrote:

    “Whether or not folks know each other or have worked together is irrelevant. It’s just a stupid claim on Wegman’s part.”

    So in your world, in assessing “independence”, it doesn’t matter that the researchers work together, it doesn’t matter that they use the same data sets to the exclusion of other data sets, it doesn’t matter that they all depend on funding that is only available to those reaching the same conclusion and it doesn’t matter that they mutually support one another’s professional status by “peer reviewing” one another’s work.

    Suppose a doctor diagnosed you with a life-threatening illness based on an MRI and a set of blood tests done in his clinic — and told you that your only hope was a risky, expensive and painful surgery — a surgery which happened to be his primary source of income. If you wanted a “second opinion”, which “second opinion” would be more valuable to you:

    1) A second opinion from another doctor that works with the first doctor in the same clinic, a doctor whose work is reviewed and inspected by the first doctor, who uses the same MRI, who runs the same blood tests, and performs and profits from the same surgical technique.

    Or:

    2) A second opinion from a doctor in a different clinic, a doctor who doesn’t know and has no association with the first doctor, who uses not only MRI but has access to CAT scan and x-rays, who has access to additional blood tests not done by the first doctor and who has no financial intersts in the outcome of your diagnosis.

    You’re telling us that you would consider both of these second opinions to be equally “independent”?

  • Michael Smith // March 18, 2008 at 12:43 pm

    dhogaza wrote:

    “Now, onto that deep layer of CO2 that supposedly is suffocating us all, any reason you didn’t back up hero of the hour Wegman on that one?”

    You know, dhogaza, not only is it logically invalid to claim that one mistaken view on one issue automatically refutes all of one’s conclusions about all other issues, you confess an utterly simplistic, binary view of the world with a statement like that.

  • James Lane // March 18, 2008 at 1:05 pm

    Mr Pete, thanks.

    The point I was trying to make is expressed more succinctly by Preisendorfer himself:

    “The novice practitioner of PCA may well fix at the outset the proper place of PCA in his studies of the atmosphere-ocean system: PCA is a probing tool; it is a preliminary testing device; it is a technique to be used at the outset of a search for the physical basis of a data set; it is some initial ground on which to rest diagnoses, model building and predictions. In sum, PCA is not an end in itself but a means toward an end.”

  • Geoff // March 18, 2008 at 1:43 pm

    In his March 13 comment <a href=”http://tamino.wordpress.com/2008/03/06/pca-part-4-non-centered-hockey-sticks/#comment-14753 here , Luinous Beauty (nice name!) says:

    The ‘divergence problem’ is a late 20th century phenomenon.

    This misstates the point at issue. The tree ring growth of BCPs in the late 20th century does indeed diverge from the patterns seen earlier in the century which are taken as indicators of temperature. However the question is, how do we know that a similar “divergence” did not take place in earlier centuries? Since BCPs are diverging within one century, what is the evidence that they have never diverged before? Cook et. al. (2004) say “Whether or not a similar loss of sensitivity [i.e., divergence] has occurred in the past is unknown with any certainty” although they go on to indicate they believe this divergence is only a northern hemisphere phenomena and since they don’t see a divergence between northern and southern hemisphere in their pre-20th century reconstructions they add “this result suggests that the large-scale loss of climate sensitivity documented by Briffa et al. (1998a, b) is unique to the 20th century, which argues for an anthropogenic cause”. No doubt there are arguments that the “divergence” is unique to the 20th century but this is a long way from proof and even Cook claims that whether earlier divergence may have occurred is “unknown with any certainty”.

    LB continues:

    Tree ring growth since the late 50s has diverged from indices well demonstrated to be accurate reflections of local, regional and global climate variability over a couple of thousand years.

    You are surely aware that BCP tree rings specifically do not correlate with local temperature. In the words of the original BCP study cited by MBH99 (Graybill and Idso, 1993), “It is notable that trends of the magnitude observed in 20th century ringwidth growth are conspicuously lacking in all of the time series of instrumented climatic variables that might be reasonably considered growth-forcing in nature”. They add “One perplexing problem has been the lack of strong, consistent temperature responses in the subalpine chronologies”. This is in line with earlier studies as they cite LaMarche (1974a, 1974b) who “hypothesized that upper treeline bristlecone pine chronologies should provide records of warm season temperatures, at least at low frequencies. He did not, however, develop any reliable quantitative transfer functions between instrumental climate data and ringwidth growth that could support this notion”. And finally they cite Fritts (1969) whose study on BCPs “reported no marked or direct correlation of summer temperature with ringwidth growth”.

    LB further comments:

    Whether the cause (for BCPs) is CO2 fertilization or if stripped-bark trees are more sensitive to such than whole bark trees or something else is the subject of much research, but has nothing to do with the confidence dendro folks have with paleo reconstructions. Whatever the cause, the magnitude of the effect is known and the data can be corrected. The correction brings the data into agreement with the instrumental record.

    In 1998, Briffa comments on the “divergence problem” as follows: “On annual, decadal, and probably even centennial time-scales, tree-ring data are demonstrably reliable palaeoclimate indicators, but where the focus of attention shifts to inferences on century and longer time- scales, the veracity of inferred change is difficult to establish. Furthermore, recent analyses of large regional- scale growth patterns and absolute tree growth changes over recent centuries strongly suggest that anthropogenic influences are increasingly challenging our assumptions of uniformitarianism in tree growth-climate responses. While this clearly represents a problem in interpretation, it also provides challenging opportunities for disentangling different tree-growth signals”. By uniforitarianism of course he means the assumption that tree rings have never “diverged” before.

    Has this challenge been met? In his 2004 overview, Briffa makes the following comment in the abstract, that “… in many tree-ring chronologies, we do not observe the expected rate of ring density [MXD, using density rather than ringwidth but comparable] increases that would be compatible with observed late 20th century warming. This changing climate sensitivity may be the result of other environmental factors that have, since the 1950s, increasingly acted to reduce tree-ring density below the level expected on the basis of summer temperature changes. This prevents us from claiming unprecedented hemispheric warming during recent decades on the basis of these tree-ring density data alone”. He described the divergence and says “The above facts seem to support an inference that some slowly varying factor began to exert a very widespread negative influence on the trend of these MXD data from around the middle of the 20th century, with effects at higher frequency also becoming noticeable in some high-latitude regions. For the time being, we circumvent this problem by restricting the calibration of the density data to the period before 1960. This reduces the potential overlap between temperature observations and density measurements and means that less data can be reserved for independent tests of the validity of predictive equations. This situation is far from ideal, but the alternative, using data after 1960 and thus incorporating non-temperature-related bias when fitting regression equations as a function of density variability, would invariability produce earlier estimates of past temperature that, to some extent, too warm”. So Briffa is claiming we should not use 40+ years of data where the “divergence” exists, but does not offer strong evidence that it hasn’t happened before, and the “corrections” he proposes are (in his own words) “far from ideal”.

    These are some of the reasons no doubt, that the NAS (2006) concluded that the use of ‘strip bark’ trees (which would include BCPs) “should be avoided for temperature reconstructions”.

    LB states the “magnitude of the effect is known and the data can be corrected”. However, it should be noted that there is considerable variation between reconstructions. As Jan Esper (2007) comments “The approximate decadal scale amplitude (difference between the warmest to coldest decade) derived from the Mann et. al. (1999) reconstruction is about 0.5°C, whereas the amplitude reconstructed by Esper et. al. (2002a) and then recalibrated by Cook et. al. (2004a) are both about 1.0°C (see also Moberg et. al. 2005)”. A 0.5°C difference in the results of different studies is significant.

    As Esper concludes (2005) “So, what would it mean, if the reconstructions indicate a larger (Esper et al., 2002; Pollack and Smerdon, 2004; Moberget al., 2005) or smaller (Jones et al., 1998; Mann et al., 1999) temperature amplitude? We suggest that the former situation, i.e. enhanced variability during pre-industrial times, would result in a redistribution of weight towards the role of natural factors in forcing temperature changes, thereby relatively devaluing the impact of anthropogenic emissions
    and affecting future predicted scenarios”.

    It would seem not all dendroclimatologists exactly how and what adjustments are to be made. It would seem the NAS recommends not using BCPs in reconstructions. If you have a different recommendation, perhaps you’d like to cite some references?

    References:

    Briffa, et. al., 1998a, Reduced sensitivity of recent tree-growth to temperature at high northern latitudes, NATURE, | VOL 391, 12 FEBRUARY

    Briffa, et.al., 1998b, Trees tell of past climates: but are they speaking less clearly today?, Phil.Trans. R. Soc., B, London, vol. 353, pages 65-73

    Cook, et. al., 2004, Extra-tropical Northern Hemisphere land temperature variability over the past 1000 years, Quaternary Science Reviews, vol. 23. pages 2063–2074

    Esper, et. al., 2005, Climate: past ranges and future changes; Quaternary Science Reviews, Vol. 24, pages 2164–2166

    Esper, 2007, On Selected Issues and Challenges in Dendroclimatology, in A Changing World, Challenges for Landscape Research, pages 113-152; F. Kienast, O. Wildi, and S. Ghosh (eds)

    Fritts, H.C., 1969, Bristlecone pine in the White Mountains of California; Growth and ring width characteristics; Paper of the Laboratory of Tree-Ring Research, No.4, Univ. of Ariz., Tucson

    Graybill and Idso, 1993, Detecting the aerial fertilization effect of atmospheric CO2 enrichment in tree-ring chronologies; Global Biogeochemical Cycles, vol. 7, No. 1, pages 81-95

    LaMarche, V.C., Jr., 1974a, Frenquency dependent relationships between tree-ring series along an ecological gradient and some dendroclimatic implications; Tree-Ring Bulletin, vol. 34, pages 1-20

    LaMarche, V.C., Jr., 1974b, Paleoclimate from long tree-ring records; Science, vol. 183, pages 1043-1048

  • Boris // March 18, 2008 at 2:12 pm

    Let’s stick to science, please.

    Your first argument for the Loehle construction was that 1930s warmth was equal to today’s warmth. How is this a scientific? What analysis is it based on? What research? Where do you find that there’s a 0.5C error in late twentieth century temperature records? This is utter nonsense. You don’t get to throw out global temperature analysis because you have some vague questions about it.

    This is why the term “denialist” gets thrown around. You deny even that the globe has warmed since the 1930s. That’s something that is confirmed through several different analyses as well as physical observations (migration patterns, mass glacier balance, onset of spring, budding of flowers, sea level rise (including thermal expansion of the oceans.)

    I thought the skeptics had finally agreed that the earth has warmed. Apparently not.

  • L Miller // March 18, 2008 at 2:25 pm

    The relationships of the people and the commonality of proxies are TWO ISSUES. People who know each other might be group thinkie (or they might not). If studies tend to use the same proxies than it argues that multiple studies are not independant confirmations (they could still be correct, they’re just not completely separate and additive.)

    No it means they use the same data sets. There is a limited number of good data sets in most fields of scientific endeavor, and it’s commonplace for them to be independently analyzed. Such independent analysis of the same data gives you confidence that you understand what that data is really telling you.

    To suggest that because people know each other they are guilty of some form of group think is highly unprofessional. If you are going to even imply something like that you had better back it up with some firm evidence, but Wegman does nothing of the kind, and simply resorts to slanderous innuendo.

    I Miller “How exactly are you reaching that conclusion if you are throwing out all the quantitative data on what temperatures actually were in that period?”

    Easy, though maybe less precise than one would like. Not all the information on past temperatures comes from MBH. Look at the early IPCC reports.

    Proxy data is the only way to quantitatively assess past temperatures. After that you have historic but subjective reports of warming, I.E. people said it was warmer but no one ever measured it so no one really knows how much. It’s telling that you would want to throw out newer more precise data favor of older imprecise often unquantified reports simply because that older subjective data says what you want to hear.

    Sod, the fundamental conclusion of the hockey stick was that the warming of the late twentieth century was “unprecedented” in the last thousand years.

    Note that the claim is *warming* is unprecedented, not *warmth*. It seems to be somewhat of a pattern that people from McIntyre’s site don’t seem to understand rates as they make the very same mistake in discussing temperature station data.

  • Boris // March 18, 2008 at 2:43 pm

    “These are some of the reasons no doubt, that the NAS (2006) concluded that the use of ‘strip bark’ trees (which would include BCPs) “should be avoided for temperature reconstructions”.”

    No. The NAS didn’t recommend strip bark because of the CO2 issue:

    The possibility that increasing tree ring widths in modern times might be driven by increasing atmospheric carbon dioxide (CO2) concentrations, rather than increasing temperatures, was first proposed by LaMarche et al. (1984) for bristlecone pines (Pinus longaeva) in the White Mountains of California. In old age these trees can assume a “strip-bark” form, characterized by a band of trunk that remains alive and continues to grow after the rest of the stem has died. Such trees are sensitive to higher atmospheric CO2 concentrations (Graybill and Idso 1993), possibly because of greater water-use efficiency (Knapp et al. 2001, Bunn et al. 2003) or different carbon partitioning among tree parts (Tang et al. 1999). Support for a direct CO2 influence on tree ring records extracted from “full-bark” trees is less conclusive. Increasing mean ring width was reported for Pinus cembra from the central Alps growing well below treeline (Nicolussi et al. 1995). Free-Air CO2 Enrichment (FACE) data for conifer plantations in the Duke Forest (Hamilton et al. 2002) and at the alpine treeline (Hättenschwiler et al. 2002) also showed increased tree growth after exposure to atmospheric CO2 concentrations about 50 percent greater than present. On the other hand, no convincing evidence for such effect was found in conifer tree ring records from the Sierra Nevada in California (Graumlich 1991) or the Rocky Mountains in Colorado (Kienast and
    Luxmoore 1988). Further evidence comes from a recent review of data for mature trees in four climatic zones, which concluded that pine growth at the treeline is limited by factors other than carbon (Körner 2003). While “strip-bark” samples should be avoided for temperature reconstructions…(pages 51-52)

    The DP is discussed a few paragraphs above.

    Also, if you’re going to talk divergence, you should read Rob Wilson’s latest on the issue.

  • null{} // March 18, 2008 at 3:12 pm

    I nominate this thread to be The Longest Ever Having No Clear Objectives and Going Nowhere. Going Round and Round in Circles counts as Going Nowhere.

    [Response: I 2nd the nomination.]

  • luminous beauty // March 18, 2008 at 3:19 pm

    Geoff,

    You separate the corn from the chaff fairly well. Unfortunately, all you can see is the chaff.

    You are selectively exaggerating uncertainty in a way that makes the perfect the enemy of the good.

    It isn’t science, it isn’t skepticism, it is obscurantism. In the end it is a big fat red herring.

    You might think that by teasing at this bit of a loose end, you have unraveled the entire fabric. You haven’t. All you have demonstrated is that the fabric is woven somewhat loosely in this one spot. That isn’t news.

    You should read MBH98 for what it says and not just to spotlight inconsequential weaknesses. You’d realize these problems are addressed and the provisional nature of their rough initial estimate is only that. A rough initial estimate requiring additional research. Additional research that consistently shows their initial estimate to be well in the ballpark.

  • Raven // March 18, 2008 at 4:08 pm

    Boris says:
    “Your first argument for the Loehle construction was that 1930s warmth was equal to today’s warmth. How is this a scientific? What analysis is it based on? What research? Where do you find that there’s a 0.5C error in late twentieth century temperature records? This is utter nonsense. You don’t get to throw out global temperature analysis because you have some vague questions about it.”

    The manipulations applied to the surface record in the name of ‘correcting’ problems with past data make a 0.3-0.5 error quite plausible. Especially when we know the raw data for many parts of the globe shows that the 30s were as warm as today.
    Unfortunately, it is impossible to prove this point one way or the other because we can’t go back in time an properly re-measure the temperatures. This uncertainty means that we should never accept this warming between the peak in the 40s an today as an unassailable fact. It is an assumption. It may be a reasonable assumption given current knowledge but it is still an assumption that could be wrong.

  • dhogaza // March 18, 2008 at 7:35 pm

    The manipulations applied to the surface record in the name of ‘correcting’ problems with past data make a 0.3-0.5 error quite plausible.

    Since the algorithm for correcting is known, you should be able to compute that potential error, rather than handwave.

    Have you done it?

    Especially when we know the raw data for many parts of the globe shows that the 30s were as warm as today.

    “Parts of the globe”, especially that part known as the lower 48, is not the world.

    You’re simply saying “I want to look at the data that agrees with my preconception, and toss at that which doesn’t”.

    This uncertainty means that we should never accept this warming between the peak in the 40s an today as an unassailable fact. It is an assumption

    The fact is not unassailable, obviously it’s under constant attack by denialists (to no avail).

    But to call it an “assumption”? That’s simply a lie.

  • Ian Forrester // March 18, 2008 at 8:24 pm

    Michael Smith said: “You know, dhogaza, not only is it logically invalid to claim that one mistaken view on one issue automatically refutes all of one’s conclusions about all other issues, you confess an utterly simplistic, binary view of the world with a statement like that.”

    It was not just a simple mistake, rather it showed that he had no basic knowledge or understanding of simple chemistry and physics. These two sciences form the basic premises for all of atmospheric and climate science. Why should he be allowed to give his opinion on such matters when he obviously knows nothing about what he is talking about. Without the basic scientific understanding any statistical efforts are completely meaningless. Why do you people have so much difficulty understanding that the science is what is important and the statistics secondary? There are many ways that statistics can be used and different people will have differing views on what is best. That does not make any other view wrong, no matter how loudly and often you say it.

  • Lee // March 18, 2008 at 11:08 pm

    ” Especially when we know the raw data for many parts of the globe shows that the 30s were as warm as today. ”

    “Parts of the globe”, especially that part known as the lower 48, is not the world.

    Actually, this isn’t true even for the ‘lower 48.’ One year in the 30s was as warm as one year in the 90s. But compare the decades overall for the ‘lower 48′, and the 90s were substantially warmer on average than the 30s. The 20-oughts are on track to be warmer yet.

  • Lazar // March 19, 2008 at 12:45 am

    1926-1980 NH temperatures are trended flat, a straight line fit is -0.004C/decade.
    Fitting Wahl & Amman 06 over that period.
    The reconstruction over 1854-1925.
    Compare with the original reconstruction (calibrated over 1902-1980).
    The two side by side.
    Calibration failed significance (just) at RE -0.09.
    Validation RE passed at 0.46, slightly below the original RE 0.48.

  • TCO // March 19, 2008 at 1:45 am

    L Miller: Chill. I said I can argue either side of those proposals. Group think is not equivalent to baby killing and is a known phenemonon in life. In any case, you’re missing the point that I’m differentiating the two aspects of indepence whether you think it’s intemperate to even consider one of them. They still are separable issues. When we muddle things together we get nowhere. Note that this holds whether you’re on the green or the brown side.

  • dhogaza // March 19, 2008 at 2:21 am

    In any case, you’re missing the point that I’m differentiating the two aspects of indepence whether you think it’s intemperate to even consider one of them. They still are separable issues.

    Yes, they are, and if you read what I’ve said closely, you’ll see that I’ve only stated that Wegman’s social networking comments are bullshit.

    The proxy issue is a real one, but it is due to the fact that there are few proxies available that cover suitably long timeframes, and few studies of those few proxies.

    Kind of unavoidable.

  • TCO // March 19, 2008 at 2:55 am

    Dude: Are you L Miller?

  • Barton Paul Levenson // March 19, 2008 at 12:44 pm

    Raven writes:

    [[Especially when we know the raw data for many parts of the globe shows that the 30s were as warm as today.]]

    Try the global average, not the average for “many parts.” Cherry-picking is not a valid use of statistics. All the global temperature series show that the 1930s were not as warm as today. You’re just wrong.

  • L Miller // March 19, 2008 at 2:11 pm

    L Miller: Chill. I said I can argue either side of those proposals. Group think is not equivalent to baby killing and is a known phenemonon in life. In any case, you’re missing the point that I’m differentiating the two aspects of indepence whether you think it’s intemperate to even consider one of them. They still are separable issues. When we muddle things together we get nowhere. Note that this holds whether you’re on the green or the brown side.

    If “groupthink” doesn’t matter why bring it up at all? If it does it’s an unsubstantiated pejorative. You can’t have it both ways. It’s clear from the context that the people bringing it up as an issue mean it to be an ad-hominim attack on the people building the reconstructions in absence of any real technical criticism of the reconstructions themselves. In the wider picture it’s probably a similar to the complaints about a “scientific establishment” you find in almost any garden variety conspiracy theory.

    Whatever definition you use for “independent” needs to be relevant to the discussion at hand. There is zero evidence for any form of “groupthink” and all the use of some common data sources means is that independent analysis of the best available data shows late 20th century warmth is at least as great and probably greater then the height of the medieval warm period. These are the underlying facts and trying to play semantics with the definition of independent won’t change them.

    Not that that is hugely relevant, since the prominent feature of the hockey stick, as I said previously, is its blade. What makes it a hockey stick is the steep rise in the second half of the 20th century. Even if the warmth isn’t unprecedented the rate of warming is.

  • dhogaza // March 19, 2008 at 2:13 pm

    Dude: Are you L Miller?

    You posted somewhat earlier on the fact that it’s two issues, not one, and I’d meant to answer then but had forgotten.

    So, like, loosen up a bit.

  • TCO // March 19, 2008 at 3:37 pm

    So like: stop theing you’re tough.

  • Chris O'Neill // March 19, 2008 at 3:42 pm

    Geoff:

    You are surely aware that BCP tree rings specifically do not correlate with local temperature.

    This is a blatant lie. The correlation coefficient between Noamer PC01 and the temperature record for the area bounded by 118W to 119W and 36N to 38N (from the NCDC is 0.44.

  • Chris O'Neill // March 19, 2008 at 10:00 pm

    BTW, the correlation coefficient between Noamer PC01 and the temperature record for the area bounded by 118W to 119W and 36N to 38N that I stated above is for the overlap period of these two records, i.e. 1880 to 1980.

  • Lazar // March 19, 2008 at 10:40 pm

    Chris,
    How did you get weightings for proxies in the Wahl & Amman 1400AD step?
    Thanks.

  • Chris O'Neill // March 20, 2008 at 3:16 pm

    The correlation coefficient between Noamer PC01 and the temperature record for the area bounded by 118W to 119W and 36N to 38N (from the NCDC) is 0.44.

    I have to confess that the figure I got from NCDC is not correct. There is something wrong with their tool. HOWEVER, the statement:

    You are surely aware that BCP tree rings specifically do not correlate with local temperature

    is still a blatant lie. From another source for the local temperature data, the correlation from 1902 to 1980 is 0.14. Of course there is more involved than this but blatantly wrong statements such as “do not correlate” (which are probably repeated ad nauseum) have to be thrown in the bin.

  • Chris O'Neill // March 20, 2008 at 3:59 pm

    How did you get weightings for proxies in the Wahl & Amman 1400AD step?

    Probably the simplest way to put it is that if the proxies are normalized to one over the calibration period (i.e. resulting sum of squares is one) then the weightings are equal to the correlations between the proxies and the global instrumental temperature PC1.

  • TCO // March 20, 2008 at 4:45 pm

    I have not seen a good paper on this. McIntyre likes to repeat the lack of local correlation like it’s a mantra, but he does not refer to a seminal review paper, nor has he done one himself. (He likes to dick around and do little cherrypicked series for demonstration purposes.) I’m honestly interested in the answer and wish someone would look at this in a more thoughtful manner for publication. Maybe McI’s right. But he hasn’t shown it. Not the way I expect it. And he hasn’t referred to a seminal review paper either.

    The whole thing sucks in the normal manner of things sucking in the climate believer/denier area. No one (except Zorita) really, really wants to do killer analyses.

  • Robin Edwards // March 22, 2008 at 12:00 pm

    First, just a minor comment on correlation coefficients:-

    As quoted in the Chris O’Neill comment on 20 March at 3.16, they are not suitable for appraisal of linear relationships unless their probabilities as well as their actual values are provided.

    If one is really interested in linear relationships the most instructive procedure is to run a simple regression, to provide the essential parameter estimates, and also, and crucially, to provide the regression plot together with confidence intervals (at a conventional probability level, such as 90% or 95%) for both the fitted line and for a further single observation. These intervals are pairs of hyperbole.

    The other thing that strikes me as being rather neglected is the overarching feature that in climate data analyses we are referring to time series, not independent observations.

    I have studied the Mann et al 1400 data quite intensively. The available data consist of 112 columns (observation types) of up to 593 rows (the time variable), and encompass numbers that vary in scale and location over very wide ranges indeed. They seem to consist of groups of data, labelled in ways that give a hint as to their provenance. Of the 112 columns, just 13 are directly related to temperature measurements. ALL the rest are proxies of varying degrees of plausibility, and one must assume from the mere fact that Prof Mann saw fit to include them in his data set that he believes them to be related in some way to actual temperatures. We have to assume that they change in an upward direction if the underlying real climate variable (temperature) moves upward. If this is not the case the whole investigation is nonsense.

    Of the 13 /real/ measures just two are temperatures in their true units. The others have been “standardised” or “normalised” in a way that is not at all clear, since they do not possess the usual property of having mean zero, variance one. Columns 10 and 11 are “Central England Historical” -actually CE Summer temperatures- and “Central Europe Historical” . These are verifiable independently. The others are from what one might term geographical grid areas rather than being named specifically as real sites. These are columns 21 to 31.

    In order to assemble them (sensibly) into an index of a normalised temperature average one has simply to normalise them all and form the average of these values. This must surely be the basis for all calibration of the other 99 proxy variables, about which there has been so much discussion and argument, much of it acrimonious.

    As a starting point it is surely sensible to analyse properly the normalised temperature average over the time span available. Simple plotting of the normalised average (try a spreadsheet) reveals some interesting features. (I can supply GIFs of all the plots if anyone is interested).

    The simple plot shows that recent values up to the end of the data cannot possibly be regarded as “abnormal”. A much more telling analysis is made by forming the cumulative sums of the data columns, or in this case the normalised temperature mean. This reveals one long period of general decline (roughly 1750 to 1850 ) followed by a period of stability (1850 to about 1895), and abrupt increase leading to a short stable period to the mid 1930s, when another period quite sharp increase followed by a relatively stable period to the mid 1950s took place. This was interrupted briefly by the 2nd WW cold period. In the late 1950s a decline followed by a somewhat unstable period to the end of the data in the 1980s.

    Similar analyses of the individual data columns, and of assemblies of these columns into what seem - from the column designations - to be sensible groups - eg columns 1 to 9 are data from tropical seas - give further insight into the general patterns of climate behaviour. In the broadest terms they seem to confirm the real temperature data, but there are many qualifications to this, far too extensive to go into here.

    What strikes me as remarkable is that these analyses could readily have been carried out by anyone who could conceivably be deemed to be appropriately qualified as a peer reviewer of Mann et al 1998. Did they /ever/ look at the actual data beind the famous paper? I doubt it.

    [Response: I think your appraisal is incorrect. For one thing, while estimating confidence intervals for regression coefficients is a valid check of their possibly being meaningful, reserving a subset of data for independent validation (as done in MBH98) is a *better* way.

    Also, there's really no problem normalizing the variables before doing a multiple linear regression for calibration, nor do we need to normalize temperature series for such a calibration. The final result -- a relationship between proxies and temperature -- is exactly the same.

    Regarding proxies, it's not correct that "We have to assume that they change in an upward direction." The assumption is that they vary linearly; if a given proxy decreases as temperature increases, it still provides information useful for reconstruction.

    I don't believe it's correct that "In order to assemble them (sensibly) into an index of a normalised temperature average one has simply to normalise them all and form the average of these values." I also get the impression that you think proxies are calibrated against the few long temperature records in the data. This is simply not the case; perhaps I misinterpret your comment.

    Cumulative sums are an often-useful analysis tool, in my opinion not sufficiently practiced, but they're also characterized by intricate statistical behavior. I worry that without proper interpetation, taking them at "face value" can be misleading.

    I think your closing paragraph is based on your own insufficient understanding of the issues, not on the shortcomings of Dr. Mann or the referees of his paper.

    Thank you for stating so many objections and disagreements without acrimony.]

  • Robin Edwards // March 22, 2008 at 11:11 pm

    Hello,

    I have just read your reply Thanks for being so prompt!

    First, Cumulative sums. Their inadequacies as a forecasting tool are of course manifold, and well known. “Forecasting is a difficult task, especially of the future” and for climate, necessarily a chaotic multi-faceted system I would never attempt it, whatever forecasting tools were at my disposal. However, for examining historic data and attempting to clarify what has happened when the series under scrutiny tends to be dominated by “random” noise, cusums have some very attractive features. In particular, it is their capacity to identify the position and extent of abrupt change in the presence of substantial noise that makes them such a valuable tool for the climate analyst. They can and do provide pointers to help elucidate or suggest suitable underlying models in climate time series. The notion that hypothesising a linear model will always “work” with climate time series is manifestly open to question. For single site data it can be shown trivially to be completely in error. If you do not accept this I suggest that you look at monthly temperature data for Greenland, which provides several sites for examination. Very recently a paper has appeared in which an homogenised south west Greenland temperature series is produced. Just apply cusum technology to that and see what turns up. An hypothesised linear model fitted to the data for the period of, say 1900 to the recent past will produce a highly significant positive slope - local warming proved, one might say - but if one is a bit more careful or takes a bit more thought, something different, and undoubtedly surprising to many, will become very clear indeed. This is that the great majority of warming took place over a few months (or for single sites even more rapidly) in 1922/23 and was of the order of 1.8C. Both prior to and after the step change, temperatures were virtually stable or even tending to decrease slightly. I can provide full details if you wish, with diagrams and regressions. This strange phenomenon seems not to have been recognised by the climate scientists with whose work I am familiar. The above remarks apply equally to individually site data for sites all over the N.W. Atlantic region, such as Upernavik, Nuuk , Jakobshavn, Angmagsalik and Reyjavik.

    The ubiquitous (nearly) nature of abrupt steps, (or periods of very rapid change) in temperatures can be verified by collecting large numbers of climate series and computing cusums relative to their means. I have a few thousand examples, I would guess. Some experience with cusum analysis leads to an amount of “skill” in commenting on the nature of the underlying data. For example, with Mann’s ‘98 data it is easy to see that a number of the columns have already been substantially smoothed prior to inclusion in the data set. Others appear to be genuine raw data. I can explain all this fully if you wish, but a forum like this is probably not the best place.

    Next, my remark concerning the nature of the proxy data was I think treated by you without noticing the whole of the penultimate sentence in Para #5, where I intended to state that if the proxies are not in general positively correlated with the real temperature measurements any conclusions derived from them (the proxies) will be rather difficult to interpret. For the data in question it happens that the cusum patterns indicate that the real data and the proxy groups are telling the same general story, with the very noticeable exception of the tropical sea data.

    I note your comment that the proxies provide useful information for calibration purposes if one can assume that they are linearly (and not necessarily positively) related to real temperatures. I need to think a bit about this in the context of the rather simpler techniques that I’ve used, which do not require a calibration step. However, if I wished to back calculate to presumed temperatures a valid correlation would be required.

    Thus I have no difficulty in accepting that using proxies as well as real data is, in the case of Mann’s data set, quite valid and informative. It is indeed a relief to be convinced of this. What remains a complete mystery to me is why the apparent heavy dependence of Mann’s major conclusion - the famous HS plot - is so dependent on the behaviour and values of one (or perhaps a few?) principal components, which appear to be used as the cornerstone of his conclusions.

    Prof Mann and his co-authors assembled, no doubt with considerable labour, a carefully chosen set of observations made by other scientists, and carried out some computationally intensive statistical procedures in an effort to reduce their functionality - the PC calculations - and then used the PCs themselves as one of their major sources for subsequent numerical treatments. Professor Mann himself provided me with URLs for much of the original data he used. Unfortunately I have not been able to reproduce his calculations, possibly because I am unable to compute PCs for data columns that have missing values. Thus I have accepted the values in the (once published) data, though with some misgivings.

    On the process of “calibration”, I sometimes ask myself why it is necessary at all. If one is sure that the proxy data are indeed meaningful in the context of temperature history, (why use them if this is not so?) all one need do is scale them so that their magnitudes are compatible with other data in the whole array, and produce a summary in the form of an average over the data columns. “Normalising” the columns before averaging is surely the obvious technique to avoid domination of the outcome by those columns whose original values are large and dispersed. Normalising is in my opinion both intuitively satisfying and safe. Should there be a soundly based technical reason to weight the normalised columns by substantially different amounts this can of course be done, but would need to be very carefully argued. In practice, any reasonable weighting of quite a number of columns will have a rather small influence on the outcome of analyses made using their average.

    I’m going to try to add two GIFs here. They are cusum plots of averages of normalised columns of Mann’s data, as described above. They cover the period from 1820 to the end of the years for which all 112 columns are available. One is for the 13 temperature columns, the other for the remaining 99 columns which are proxies of various types. Just look how well they correspond over long time periods.

    Well, that was a failure. I really cannot understand how Windows is supposed to work :-(( In the system I normally use it would take about one second to do this by simple drag and drop. Oh well! Sorry.

    Thanks for your reply. It is all getting very interesting and I look forward to further correspondence.

    Robin

    [Response: The wordpress software (they're the host of this free blog) doesn't allow images in comments.

    If you want to reproduce the analysis of MBH98, you may find valuable resources at this site. It appears to be something of a work in progress, but may be of considerable help in your efforts.]

  • Robin Edwards // March 25, 2008 at 4:54 pm

    Thanks for the link, but I’ll not try to duplicate MBH98. It would be a pure waste of time, I think.

    What I would heartily recommend to /everyone/ who writes in climate change blogs is that they personally collect appropriate data (MBH98 numerical data would be a good start in this case), ice core records, lake deposit records, long instrumental records of actual site temperatures, other millennial reconstructions - Moberg for example, and to do some statistical and graphical analyses for themselves.

    For amateurs, like me, it is simplest not to get involved in arguments about the technical validity of the data. This is probably best left to professionals, although you will probably spot some odd things in MBH98, which is temperature related but includes a group of columns with precipitation data, and even a column from the southern hemisphere. I can only accept what’s there and sigh gently.

    The obvious way to start is to make plots against time. Do this with all 112 columns of MBH98, and have a serious think about the plots, keeping in mind hockey sticks. Then assemble the columns into groups of similar types. You’ll find about 9 groups, depending on how you make the selections. Some are obvious, for example the 13 “temperature” values, though you’ll find that only ONE is in its original units - column 10, Central England Temperature - the others, col 11 and 21-31 are all transforms. To make any sense at all of MBH’s data you will have to standardise them before you do any averaging, for reasons that will become obvious when you do some plotting of individual columns, or compute the column-wise (univariate) statistics.

    Having done all this you will be in a position to make some well-based comments on many of the things being discussed in these pages. It would also be useful to collect the CO2 data from Mauna Loa, which can be examined by assorted statistical and graphical techniques. I’d recommend eliminating the very strong seasonal signal before proceeding with any regression analyses. By taking this preliminary step you will find a remarkably smooth curve that can be fitted to linear or polynomial models. Linear instantly proves to be unhelpful over moderately long periods, but quadratic and cubic models produce really excellent fits to the data. However, do /not/ extrapolate such models in the expectation of being able to make some useful predictions. Extrapolated polynomials are dreadful predictors, which will be obvious simply from their form I’m sure. An exponential fit is likely to be a lot more reliable as a predictor, and indeed turns out to be a decent model, besides having very plausible theoretical backing, which the polynomials do not. From such analyses you’ll spot occasional blips, but in general Mauna Loa is very well behaved, and from the climate aspect could well be adequately described by a linear model over a period of, say 1995 to the present. Thus CO2 is a decent proxy of the time variable on a small time scale! Remember this when you get around to plotting the period from about 1935 to the end of MBH’s data.

    Now it’s worth taking a bit of time thinking about “calibration”. This seems to be term used to describe the relationship of various proxies to real temperatures, and is the heart of the heated discussions regarding principal components, centred of otherwise, scaled or in “original” units.

    Please correct me if I am under a huge misapprehension, but my reasoning is that all calibration attempts /must/ be totally dependent on the sole real temperature record in its original units, or by a two stage process on an average of the behaviour of all 13 records that are directly related to temperature, which again must involve some scaling to ensure that they are equally weighted.

    There’s another factor to be considered in this “calibration”. The temperature records seem to be concentrated in north west Europe. The contentious calibration data seem to me to be based on the south western states of the USA, which is a decent stretch even for so-called tele-connections. How they should relate to data from tropical seas is quite beyond my comprehension, so I look for enlightenment from someone who really knows all the facts and history.

    My view is that “calibration” is an interesting though superfluous exercise. It involves complex and computer-intensive mathematics, and although I realise that this is a wonderful playground for those who enjoy linear (matrix) algebra, I ask where does it lead us?

    Why not take a simple and direct view of the data. In the first instance, accept the wisdom of the scientists who have generated, selected and assembled the primary data. It’s their profession, one supposes, and they should be good at it and impartial in their reporting. Next, take account of the preliminary data processing, which in this context seems to be a praiseworthy attempt to reduce the dimensionality of the extensive data (several hundreds of columns for MBH98, for example) by computing principal components (PCs) of assemblies of related data, such as those of dendrochronological origin, and selecting from them only those that are (conventionally) distinguishable from “noise”. This is often taken as having eigenvalues above some stated magnitude. This, I believe, is the approach taken in MBH98, which enabled the data to be plausibly compressed to 112 columns. Much of the data apparently did not need this preliminary step, since only 29 PCs appear in the published data.

    Thus I would advocate that initially the data be accepted as they are, whatever misgivings one might have, and some analyses undertaken on the lines I’ve suggested above.

    When you’ve done this you will be in a good position to comment on the whole matter without having to rely on the opinions of others, who just might have their own agenda in mind when they write convincingly about the topic, which is the existence, or otherwise, of a general hockey stick shape in the MBH data. Needless to say, I’ve done all this, and much more, over the last 9 years, and I have /very/ strong views on what reasonably can be concluded by an impartial onlooker from the data to hand.

    I would be very willing to contact anyone by “private” email to show what comes out from a more comprehensive analysis than what I’ve outlined here. As you can see from the previous reply, graphics cannot be included in comments to this blog. A shame, but there we are :-((

    Robin

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