Peer review as scholarly conformity

Chapter 5 of Suppression Stories by Brian Martin (Wollongong: Fund for Intellectual Dissent, 1997), pages 69-83.

 
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Quality control. Who could disagree with that? When a scholar sends an article to an academic journal, the editor has to decide whether or not to publish it. The article has to be relevant to the subject matter covered by the journal, and also high quality. In what are called "refereed journals," the editor relies on other scholars - the referees or reviewers - to judge the article. Each referee writes a report on the article, judging it in various ways, and recommends whether the article should be published unchanged, resubmitted with changes, or rejected outright. The editor weighs up the comments and recommendations of the referees and makes a decision.

The process can be quite elaborate. Some social science journals seek reports from four or five referees, and then after revisions there may be a second or even third round of refereeing. It's said to be all in the cause of quality control.

I've had plenty of experience with the refereeing system as an author. Most of my articles in scientific journals - such as in mathematical modelling and in astrophysics - went through the refereeing process. This was straightforward and seldom caused problems. Scientific journals typically use one or two referees, and most of them publish a majority of articles submitted. The topics on which I was working were fairly orthodox, which may be another reason there were few problems.

In the social sciences, a smaller fraction of submitted articles are actually published. Typically, more referees are used and they are more likely to recommend rejection. Over the years, I've had dozens of articles published in refereed social science journals, but an even larger number of rejections.

The process of judging an article by sending it to referees is a form of what is called peer review - the referees and editor are said to be "peers," namely people in the field with similar values and standards. Peer review is also involved in assessing grant applications, job applications, promotions and book proposals at scholarly publishers.

Although the rationale for peer review is quality control, it's obvious that the process can be used to suppress dissent. It's a powerful method: peer review can be used to block publications, appointments, promotions and grants. Most importantly, it is very difficult to demonstrate that bias is involved. Usually referees are anonymous: only their reports are made available. Members of selection committees carry out their deliberations in secret: only a decision and perhaps a brief justification is needed.

It is very difficult to collect systematic information about the role of peer review in squashing dissent. But in the course of looking into suppression I've come across a few dramatic cases.

 

Research grants

As you may remember, Clyde Manwell was threatened with dismissal after he and Ann Baker in 1971 wrote a letter to the Adelaide Advertiser about pesticides. Clyde had been a recipient of grants from the Australian Research Grants Committee, the main funder of university research in Australia. But then in 1972, just after the attack was launched on him, he was unsuccessful. He continued to be unsuccessful for the rest of the 1970s, even though his publications put him among the top 1% of scholars in terms of productivity. Clyde documented his experiences in an article published in the Australian science journal Search in 1979.

One of the more well-known cases of suppression via cutting off research grants involved Thomas Mancuso, an epidemiologist at the University of Pittsburgh. Mancuso was funded by the Atomic Energy Commission to study the effects of low-level ionising radiation on the health of workers at the AEC's nuclear reprocessing plant at Hanford, Washington. The project began in 1965, before the rise of popular concern about nuclear power. In the 1970s the issue of the health effects of low-level ionising radiation had become a hot potato for the promoters of nuclear power.

In 1974, another researcher, Samuel Milham, published findings showing an increased risk of cancer among Hanford workers. The AEC requested that Mancuso repudiate Milham's findings, but Mancuso refused on the grounds that his study was not yet complete. So the AEC organised a review of Mancuso's project. Citing two unfavourable reviews, one of which recommended termination and transfer of the project, the AEC terminated Mancuso's work and transferred the work to Battelle West, a private contractor.

On the basis of this information, there can be little more than a suspicion of foul play. But because of the politically sensitive issues involved, the termination of Mancuso's project was investigated by Congress. It turned out that there were actually six reviews of the project, not just two. Four of the six reviewers were favourable; the AEC had cited only the two unfavourable ones. Furthermore, the director who took over the study at Battelle West was a former employee at the AEC who was the very same reviewer who had recommended termination and transfer.

In each of these two cases, the person receiving the research money was doing work potentially threatening to vested interests, namely the pesticide establishment in Manwell's case and the nuclear establishment in Mancuso's case. In each case, the denial of research grants occurred in the context of a highly contentious social issue in which there was a pattern of suppression. Finally, in each case the apparent bias in research funding could be exposed through inconsistencies in peer review.

Manwell had an outstanding publication record, which was dependent on favourable reports from journal referees. Why were journal referees so favourable and grant referees negative? A plausible explanation is that the journal referees - most of whom were from other countries judging an article submitted to a journal published outside Australia - knew nothing about Manwell's activities and just judged his work, whereas the grant referees - or the grant body's panel members - were local scientists who were prejudiced by the stigma attached to Manwell's activities or the attack on him.

Similarly, Mancuso's project was judged favourably by a majority of the reviewers, throwing into question the AEC's action. In each of these cases, ironically, it is peer assessments that can be used to expose apparent biases in peer review.

It is only very blatant cases that can be exposed in this fashion. In many other cases, there may be a suspicion that suppression is responsible, but no way to get further than this.

Peter Springell referred me to a 1974 article in the British Medical Journal by David Horrobin, who documented bias by research grant referees against innovative applications. Horrobin was able to obtain referees' reports for quite a few unsuccessful applications. Horrobin's evidence was the best I had seen. Indeed, it's still the best I've seen. It seems that investigations of bias in awarding research grants are few and far between.

Most scholars are unwilling to make a big issue about biases in research funding. They are afraid that they will obtain a reputation as a troublemaker and be unable to obtain funding in the future. A common informal view is that it is easier to obtain funds for conventional projects. Those who are eager to get funding are not likely to propose radical or unorthodox projects. Since you don't know who the referees are going to be, it is best to assume that they are middle-of-the-road. Therefore, a middle-of-the-road application is safer. It's difficult to say whether this view is correct, but many people believe it to be so and the few obvious cases of suppression don't help to change it.

 

Dental profession dominance

When a particular viewpoint holds sway through an entire field of study, it is difficult indeed for challengers to gain a hearing. The dominance of profluoridation views within the dental profession is a good example. From the 1950s, when fluoridation became accepted and promoted by dental associations in most western countries, until today, it has been extremely difficult for anyone to publish an article critical of fluoridation in any dental journal. This also applies, to a lesser extent, to medical and scientific journals, where profluoridation editors and referees often hold sway as well.

However, it's hard to prove rejections of antifluoridation articles are due to profluoridation bias. After all, the antifluoridation articles submitted may have been no good. And, to be sure, there are plenty of poorly argued antifluoridation writings around. Nevertheless, there are a few suggestive bits of evidence.

George Waldbott, the most prominent and influential opponent of fluoridation in the US for several decades, wrote numerous scientific papers. He also sometimes encountered difficulties getting his articles critical of fluoridation published. One revealing indication of the source of his problems came at a court hearing in Dublin. Being quizzed by a lawyer on his testimony, he was asked "How did it happen that the Journal of the American Medical Association, the Annals of Internal Medicine, the Journal of Gerontology, and Annals of Allergy turned down your articles on fluoride poisoning?" This question was an obvious attempt to undermine his credibility as a competent scientist. But the question revealed something else besides its intent. Waldbott noticed that the four journals mentioned were the only ones that had ever rejected any of his submissions. But how would the lawyer know about the rejections? US Public Health Service officials were there in the courtroom advising the lawyer. Waldbott concluded that the editors must have used USPHS officials as referees and then told the USPHS about the rejections.

One of the leading critics of fluoridation in Australia is dentist and researcher Geoffrey Smith. When I interviewed Australian profluoridationists, one of them told me that Smith couldn't get anything published in scholarly journals, but only in the unrefereed letters-to-the-editor section of the New Zealand Dental Journal. Smith himself told a different story. He said that he was given an extremely hard time by referees for the Australian Dental Journal and so was unable to get anything published there. But he said he had no difficulty getting articles critical of fluoridation published in international (that is, non-Australian) refereed scientific journals. He sent me a pile of them.

Mark Diesendorf told me about his difficulties getting antifluoridation articles published. For example, on one occasion he submitted an article to the Australian journal New Doctor, which is mildly critical of the medical establishment. A guest editor rejected it because "it might encourage the antifluoridationists." Mark was told about the rejection over the phone, never receiving a written reply.

Although Mark encountered immense obstacles in getting his articles on fluoridation published, he kept trying. His greatest triumph came in 1986 when his article "The mystery of declining tooth decay" - which argued that the evidence that fluoridation was responsible for major reductions in tooth decay was inadequate - was published in Nature, one of the world's most influential scientific journals. This article, with its visibility and prestigious location, gave the antifluoridation cause an enormous boost. The profluoridationists did what they could to undermine it. Rather than write a reply for publication, which would have admitted that the issue was worth debating, Graham Craig of the Sydney University Dental School wrote a rebuttal that was circulated in profluoridation circles. When I interviewed Australian profluoridationists, one of them told me that Mark's article was not refereed. Mark sent me the referee's report. Another profluoridationist told me that Australian scientist Michael Briggs - later exposed for scientific fraud - had published in Nature, implying that Mark's article might be little better.

Even a single article in a key professional journal, such as Mark's article in Nature, can have an enormous impact when the issues are hotly contested and one side is excluded from presenting its case. The antifluoridationists scour the scientific literature looking for any findings that might support their cause. No wonder editors and referees occasionally admit their concern that publication of an article might aid the antifluoridationists. Of course, the usual referees' reports never say such a thing. They are couched in terms of scientific and other inadequacies of the paper. Furthermore, probably the usual motivation for rejecting an antifluoridation article submitted to a journal is simply that the evidence and logic don't measure up. No conspiracy theory is required. Most profluoridationists genuinely believe that there is little or no substance behind criticisms of fluoridation. You can call this suppression, but perhaps a better description is domination by a standard viewpoint.

When one viewpoint is so dominant that critics face enormous obstacles getting articles published, the temptation is to not even try. There is a journal, Fluoride, that regularly publishes scientific work critical of fluoridation. It is relatively easy to publish criticisms there, so why hit your head against a brick wall by submitting articles to dental journals? Because so few critical articles are submitted to mainstream journals, it is easy for supporters of the standard view to say that there is really no critical work of substance to publish anyway.

In investigating suppression, it is very difficult to document cases of bias in peer review. The fluoridation debate is a good place to find examples because there is a pattern of other types of suppression and a reasonable explanation of why suppression should occur. Even so, the cases of peer review bias usually depend on revealing discrepancies in peer review. Waldbott was able to publish in lots of journals; the profluoridationists knew about each of his rejections. Geoffrey Smith could publish in numerous non-Australian scientific journals but not in the Australian Dental Journal. Mark Diesendorf published his work in Nature and other scientific journals but had enormous difficulty when submitting to dental and medical journals.

Fluoridation is only one area out of many where dissenting ideas are prevented from appearing in journals. But who is to say that dissenting ideas are any good? I'm occasionally contacted by people who believe that their brilliant discoveries are being suppressed. I try to be open-minded. But I always keep in mind that just because an idea is rejected does not mean that suppression is involved. Some of the writings that have come my way are incoherent and illogical, at least in my judgement. Nevertheless, there might be a grain of truth in even the least plausible claim. I have only a finite amount of time and energy and therefore have to choose carefully which cases to pursue.

 

An AIDS orthodoxy

One of the original cases of suppression of environmental scholarship that I studied was the attempt to block publication of Fight for the Forests by philosophers Richard and Val Routley. In the years since I have kept contact with each of them. To make things confusing, they each changed their last names. Val became Val Plumwood and Richard became Richard Sylvan.

In 1990 Richard sent me a bundle of material that he had received from Louis Pascal. Pascal had developed a theory on the origin of AIDS, but had had difficulty getting it published. The editor of the philosophy journal Inquiry - which had earlier published two of Pascal's articles - suggested a few people who might help in getting his new work published. One of them was Richard.

I wrote to Pascal in April 1990, telling him about my work on intellectual suppression, making some suggestions for getting his work published and sending copies of some of my writings. Thus began an ongoing correspondence and a major project for me.

The conventional theory of AIDS is that HIV (human immunodeficiency virus), the virus thought responsible for AIDS, came to humans from monkeys or chimpanzees, who have similar viruses called SIVs (simian immunodeficiency viruses). Transmission is thought to have occurred by a hunter getting monkey blood into a cut, through a monkey bite or some other such means. It's supposed to have happened in Africa, probably around the late 1950s according to the rate at which variants of HIV have been evolving. After the initial transfer to humans, HIV spread through human-to-human contact.

Pascal's theory was that AIDS originated from contaminated polio vaccines used in Africa in the late 1950s. The vaccines were grown on monkey kidneys, as they still are. The vaccine thus might have been contaminated by SIVs. A particular batch of Hilary Koprowski's vaccine was given to hundreds of thousands of people in central and west Africa from 1957 to 1959, in the regions that now have some of the world's highest rates of HIV infection. Furthermore, the vaccine was given to many small children, including ones less than a month old. The significance of this is that children's immune systems are undeveloped. Depressing the immune system is one of the ways used to transfer viruses from one species to another. Needless to say, there's much more that could be said about the issue, but this gives a feeling for what's involved.

Pascal developed his theory in 1987 and soon wrote a short article making the case. The issue is not just of historical significance. If AIDS came from contaminated polio vaccines, then there remains a danger that other viruses are being transferred to humans through vaccines. Furthermore, operations such as transplanting a baboon liver into a human - which requires drugs to suppress the immune system - may be a means for other species-to-species virus transfers, with potentially devastating consequences.

Pascal sent his papers to leading scientific journals: Nature, Lancet and New Scientist. Nature rejected it with only brief explanation. Lancet rejected it without giving a reason. New Scientist replied two years later, saying that the article was being refereed, but didn't write again.

These rejections don't prove a lot. It's very difficult to get published in any of these journals at the best of times. Pascal faced extra difficulties. He wrote from a private address in New York City. Some editors assume that any submission from a private address is no good. After all, they reason, any scholar of quality should be working for a university or some other institutional employer. Another difficulty was that Pascal's papers weren't perfectly in the scientific mould. They weren't exactly in the formal, impersonal, logically structured style that is expected in scientific journals, although they weren't too far off.

Most editors and referees expect that anyone wanting to have their work published must adapt to the system. Authors are expected to write in the standard style, to cite other work in the usual fashion and to prepare their submissions in orthodox fashion. Anyone who does things a different way is likely to be rejected out of hand. That may be what happened to Pascal.

Pascal's view was different. In his view, he had proposed a theory that, if correct, would point to the need for immediate action to stop further diseases through simian-to-human virus transmission. In addition, it offered insights into how to deal with AIDS, for example by finding monkeys or chimpanzees with SIVs similar to HIV and seeing how they survive with the infection. Pascal believed that editors had a responsibility either to reject his theory on the basis of specific refutations or to publish it. Whether or not he wrote in the standard fashion was a side issue when millions of human lives were at stake.

A colleague sent me an article by David Horrobin in the Journal of the American Medical Association that made this point well. Horrobin argues that the point of peer review, at least in biomedical science, should be improving care to patients, not quality control.

Although Pascal's submissions may have been rejected just because of his lack of an institutional address and the style of his writing, there was another explanation. Pascal's theory was very threatening to the scientific establishment, especially medical researchers. If it was accepted that polio vaccinations had led to the deadly disease AIDS, it would be an incredible blow to the prestige of medicine. The credibility of vaccinations would be undermined, and many more people might refuse to be vaccinated.

In medical circles, vaccination is virtually unquestionable. There are a few critics, but they are mostly outside the medical research community. Certainly among my peers in the social science community, vaccination is defended most vehemently. On a computer conference dealing with social aspects of science and technology, the subject of vaccination came up in 1993. The very idea that parents might not have their children vaccinated was greeted with outrage by some scholars on the conference. And they are the ones who are supposed to be willing to study the evidence as well as vested interests on both sides of issues.

Pascal wasn't the only one having problems getting his work about polio vaccines and AIDS published. Two professors from South Africa, Gerasimos Lecatsas from the Department of Virology at the University of Southern Africa and Jennifer Alexander from the Department of Microbiology at the University of the Witwatersrand, had also encountered difficulties. Their comments about polio vaccines and the origin of AIDS were much briefer, less specific and more tentative than Pascal's. But even their short comments about a possible link were rejected by several journals. One of their submissions on the topic was published as a letter-to-the-editor in the South African Medical Journal. A group of scientists responded in a later issue by calling Lecatsas and Alexander's letter "reprehensibly irresponsible misinformation" and "recklessly wild and unscientific information." This sort of rhetoric gives some idea of the passions aroused by this theory.

One of Pascal's correspondents sent his article to the Journal of Medical Ethics, whose editor asked Pascal to write a different article for submission there. Pascal wrote a long and passionate article. It was too long. In May 1991, the editor, Raanan Gillon, wrote to Pascal in a rhetorical overstatement that "There is just no way that I can publish a 19,000 word paper even if I thought that it was going to save millions of lives as you suggest (and I have to say that I remain unconvinced by this speculation)." Gillon underlined the word "millions."

In my correspondence with Pascal, I offered to arrange publication of his paper if he was unsuccessful elsewhere. This was not an offer made lightly. There were several reasons why I was inclined to help promote Pascal's work. First, his letters and articles revealed a keen, logical, meticulous intellect. When I or someone else raised a query about some small component of his analysis, Pascal would reply with detailed logical arguments and references to relevant evidence. He had thought through his ideas far more carefully and comprehensively than most scientists I had met.

Second, Pascal's theory had highly important social implications. It concerned a deadly disease and possible new diseases. It also had implications for medical research and peer review. Third, Pascal's article was well written, engaging, dealt with both scientific and social issues, and raised perspectives of interest to social analysts of science. Finally, Pascal had tried unsuccessfully to publish his work in scientific journals. Thus there were plenty of reasons for me to put time and effort into publishing and promoting Pascal's work. At the time, though, I didn't anticipate how much time and effort would eventually be involved!

At the University of Wollongong, a certain amount of university money is allocated for research, most of which goes to groups of researchers. I was in a group called Science and Technology Analysis. One thing we did was produce a series of "working papers," usually but not always written by members of our group, which we could circulate to interested people. I arranged for Pascal's paper, rejected by the Journal of Medical Ethics, to be published in the working paper series. I did the work to get the text in the format for working papers, checking it all with Pascal. It was printed and ready for distribution in December 1991.

I began by sending copies to 25 people whose names were given to me by Pascal. I also sent copies to colleagues interested in intellectual dissent, to various journals, to science journalists and to people who wrote in for their free copy. Pascal's paper was a hit. I sent out hundreds of copies and some recipients made lots of photocopies themselves for further distribution. This was one way around the journal rejections.

Quite independently of Pascal, the same theory was developed years later by Blaine Elswood, an AIDS activist from San Francisco. Elswood knew an investigative journalist, Tom Curtis, and tried to get him interested in pursuing the story. Curtis in turn encouraged Elswood to write up and publish his work in a scientific journal. Curtis finished first. He put in an enormous effort investigating the issues, developing the ideas further and interviewing leading researchers. His article "The origin of AIDS" appeared in Rolling Stone in March 1992. Rolling Stone? Yes, it's a rock magazine. It does run some "serious" articles. And because of its large circulation, it has an enormous impact. Soon there were stories in major newspapers and scientific journals. Nature would not publish Pascal's article but it ran a story about the Rolling Stone article. Of course, most prominent scientists who were quoted opposed the theory. But at least it was on the agenda.

I wrote to Elswood and then Curtis to put them in contact with Pascal. In fact I corresponded with lots of people about the issue, as well as sending out copies of Pascal's article. In this way I gained a good idea of what was going on concerning the theory. One key development was that Raanan Gillon, editor of the Journal of Medical Ethics, wrote an editorial in which he explained why the JME had not published Pascal's article. He recommended it as worthy of serious consideration and gave full details about how to obtain it from us at the University of Wollongong. So although JME did not publish Pascal's article, our independent publication of it, followed by the JME editorial, made many people seek it out.

Meanwhile, Elswood collaborated with Ray Stricker to produce a technical article describing the theory. They submitted it to British Medical Journal, where it was rejected. They then tried Research in Virology. In February 1992, famous AIDS researcher Luc Montagnier wrote back very encouragingly, implying that it would be published. Months passed. Eventually the board of Research in Virology said that they would only publish a much shorter, letter-length submission. In addition, Elswood and Stricker were asked to remove all their discussion of monkey virus SV40 which was known to have contaminated polio vaccine given to millions of people worldwide. (SV40 is different from SIV, the virus thought to have been transmitted to humans to become HIV.) Elswood and Stricker complied. After further delays, their letter appeared in mid 1993, accompanied by a note from the editors that challenged and disowned Elwood and Stricker's claims. This theory was not welcome!

Elswood and Stricker sent their original paper to the journal Medical Hypotheses, edited by David Horrobin, a long-standing critic of many features of science. I had corresponded with Horrobin concerning intellectual suppression and met him in Sydney one time when he was attending a conference there. Horrobin set up his own pharmaceutical company and yet kept up with his research. He established Medical Hypotheses to provide a forum for unorthodox ideas. Elswood and Stricker's article was published in Medical Hypotheses, but not until after more than a year's delay.

However, these problems were nothing compared to what happened to Tom Curtis. In December 1992, Curtis and Rolling Stone were sued for defamation by Hilary Koprowski, the scientist who developed the polio vaccine used in Africa from 1957 to 1960. This was the vaccine that Pascal, Elswood and Curtis said might be responsible for starting AIDS.

Koprowski's lawsuit had the effect of shutting down most media discussion of the theory. It also was oppressive for Curtis, who had to supply copies of all notes, correspondence and tapes made in researching his article in Rolling Stone. After this, he had a hard time pursuing the polio-vaccine-AIDS story, because he had to tell any informants that their comments might end up with Koprowski's lawyers. He was a freelance journalist, and the case took up time when he could have been researching other stories and making money. The one saving grace was that Rolling Stone covered legal fees. And they were hefty. A year later, the case was settled before testimony even began. Even so, Rolling Stone's legal costs amounted to $500,000. The settlement involved a payment of the grand total of $1 to Koprowski and publication by Rolling Stone of a "clarification" that Curtis considered to be grossly misleading.

Can Koprowski's lawsuit be called a "strategic lawsuit against public participation"? Not according to Canan and Pring's definition of a SLAPP. But there are similarities. It certainly had the effect of shutting down public discussion. Curtis had prepared a second article on AIDS, but Rolling Stone dropped its option to publish it.

I decided that just distributing Pascal's article was not enough. In mid 1992 I wrote an article called "peer review and the origin of AIDS," covering some of the problems faced by the polio vaccine theory. After getting comments on a draft, I sent it to the British Medical Journal, which promptly rejected it. Then I tried BioScience, a general interest journal mainly aimed at biological scientists. BioScience has a feature called "Roundtable" in which opinion pieces are presented. To my delight, my article was accepted. The one "adviser" was favourable. Perhaps it is easier to publish an account about the reception to a challenging theory than to publish an account of the theory itself.

Science, the most influential scientific journal published in the US, remains hostile to the theory. It published a highly critical news story about the Rolling Stone story. Curtis then was able to get a letter published in Science. Koprowski responded with a long and condescending letter. Science then refused to publish Curtis's point-by-point rejoinder.

One supporter of the polio-vaccine-AIDS theory is W. D. Hamilton, professor of zoology at Oxford University and an eminent evolutionary biologist. Hamilton wrote a letter to Science pointing out errors in Koprowski's letter and arguing that the theory warranted consideration. Hamilton's letter was rejected. Then he wrote a personal letter to Daniel Koshland, editor of Science, making a strong appeal about the importance of open discussion of the theory. This letter was the most eloquent that I had read for many a month. But it was unsuccessful. Koshland refused to publish Hamilton's letter.

 

The power of editors

Koshland, like the editors of other major scientific journals, has enormous power. By choosing referees and by making decisions about controversial submissions, such editors have a great influence on the credibility of different viewpoints. When John Maddox, editor of Nature, accepted Mark Diesendorf's article, he gave a giant boost to the critics of fluoridation. Koshland's rejection of all responses to Koprowski's letter is more typical in its perpetuation of orthodoxy.

Investigating biases in peer review is not an easy task. When there is a wider pattern of suppression, then it is reasonable to expect that there will be biases in peer review, but only sometimes is there any evidence that is more than suggestive. Even then, the biases are most easily exposed when there are inconsistencies in peer assessments, for example between countries or different types of journals.

Editors not only have enormous power, but they seldom are subject to peer review themselves. Some of them keep their positions for decades. Potential authors may complain privately about inconsistencies and bias, but they are seldom willing to say anything openly. Their fear is that if they did, they would be discriminated against. As in the case of other types of suppression, the fear of stepping out of line has a much greater effect than the few attacks on dissidents that do occur.