Models and Meaning Change: A Brief Introduction to the Work of Mary Hesse 

Steven French*

Mary Hesse was one of the most significant figures in twentieth-century history and philosophy of science, not only because of her academic research, but also for the role she played in further developing and enhancing the field at the institutional level (for a useful biography see ‘Website in Honor of Mary Hesse’: http://www.collodel.org/hesse/#). She was instrumental in the formation of the Division of History and Philosophy of Science at the University of Leeds, where she was a lecturer in mathematics, before she moved to University College, London; and from there, she moved to the Department of History and Philosophy of Science at Cambridge, where she was eventually appointed to a Professorship. Not only was she Vice-President of the British Society for the History of Science and President of the Philosophy of Science Association, as well as being elected to the British Academy, but more importantly—as far as we are concerned at least!—she was Editor of the British Journal for the Philosophy of Science during a time of considerable change for the field as a whole (and wrote an astonishing number of book reviews while in that role).

Here I have chosen a selection of her papers, together with some notable responses, from the pages of the British Journal for Philosophy of Science. We begin with her first ever paper in the philosophy of science (Hesse [1952]), published in the second issue of the journal while she was still in the mathematics department at Leeds. She begins with a critique of Bridgman’s account of the meaning of physical concepts in terms of operational definitions, using the example of Dirac’s formulation of quantum mechanics to argue that such an account cannot capture the nature and role of such concepts in modern physics. In particular, she insists that despite the significance given to observables in quantum mechanics, these cannot be straightforwardly related to the kinds of measurements that are typically carried out in practice. Instead, she suggests, the meaning of concepts in quantum physics is grounded in the analogy with the relevant elements of classical physics. Thus, ‘Dirac's discussions about measurement and observability become meaningful if we realise that he has in his mind, not practically possible experimental measurements, but a highly idealised system of particles like those considered in classical dynamics’ (p. 291) —with the crucial difference that we cannot assume the particles to possess definite positions and momenta when not observed. Of course, one might suggest that the role of such analogies is limited to the heuristic development of the theory and that they will eventually be eliminated. However, Hesse suggests, not only would the resulting theory be unwieldy, it would also be unable to accommodate new observations, ‘because one of the main functions of an analogy or model is to suggest extensions of the theory by considering extensions of the analogy, since more is known about the analogy than is known about the subject matter of the theory itself’ (p. 291).

Together with her subsequent work on models in physics (Hesse [1953]), these papers laid the basis of her classic text on models and analogies in science, which remains widely cited and for which she is perhaps most well-known. In her 1953 paper, she draws attention to two important points regarding scientific hypotheses: First, ‘Mathematical formalisms, when used as hypotheses in the description of physical phenomena, may function like the mechanical models of an earlier stage in physics, without having in themselves any mechanical or other physical interpretation.’ (pp. 198–9). What Hesse meant by this is that if hypotheses are to have heuristic value, they need to be capable of being understood independently of the data that can be deduced from them. A good example of this would be the famous billiard-ball model of a gas, the ‘further ramifications’ of which can be used to extend the kinetic theory of gases, thereby generating more questions that can then be answered via experiment.

The second point is that ‘most physicists do not regard models as literal descriptions of nature, but as standing in a relation of analogy to nature’ (p. 201). Here Hesse goes beyond her previous work in distinguishing two senses of analogy as used in physics: we may say that one branch of physics is analogous to another and may thus be used as model of the other on the basis of identical mathematical formalisms, such as in the case of the theories of heat and electrostatics; or we may say that the billiard balls are analogous to gas molecules, in which case we have identity of mathematical structure between the model and nature, where ultimately the analogy reduces to a correspondence between numerical consequences of the model and numerical experimental results.

The wide variation in types of models is then illustrated by drawing on the history of science in the form of a survey of nineteenth-century aether models, with Hesse noting that all the ‘real’ work was done by the mathematical model, with the mechanical counterparts added as an afterthought, ‘in the mistaken belief that it endowed the mathematics with a respectability it would not otherwise possess’ (p. 212). This then allows her to identify two characteristics of models: formal rules, such as the axioms and rules of inference of a mathematical formalism; and what she calls ‘pointers’, which can be found in the ‘haze’ of mathematical and physical associations surrounding the model and by means of which the model can be further extended. An example would be the suggestion of new formal rules similar to the original set, as when modifications to the laws of collision for gas molecules were suggested by elasticity in the billiard-ball model. Here we see the roots of what she was later to call the ‘neutral’ analogy that she insisted was essential to scientific progress.

In his wide-ranging paper, Achinstein ([1965]) criticizes Hesse’s identification of models and analogies, noting first that with regard to analogies between different branches of physics, some of the laws are similar or identical, but others are not; and that when it comes to models themselves as analogies, many models of systems are not analogues of those systems and neither is an analogue always a theoretical model. In defence of this last claim, he deploys the example of the similarity between the laws of heat and those of electrostatics. But, of course, Hesse would insist that this example is covered by her first sense of analogy, while it is the second sense that is the target of Achinstein’s criticism. And he does acknowledge, in a footnote ([1965], p. 108), that she refines her account in (Hesse [1963]), drawing the distinction between those models that are analogies and those that might more broadly be called ‘theoretical’. The paper concludes with another review of models of the aether, which is taken to support the overall claim that although some models might be described as analogies, others are better understood as ‘theoretical’ models, whereas still others have an intermediate nature.

Granted that some of the details of Hesse’s approach required further refinement (for a review of her ([1963]), see (Ackermann [1965])); nevertheless, her consideration of certain kinds of models as analogies was hugely influential: her work in this area is cited by Kroes ([1989])—who writes that her book is ‘one of the best studies in the field’—Weisberg ([2007]), and Dardashti et al. ([2015]), just to give a few examples from the pages of the BJPS (for an example of ‘failure to cite Hesse’ used as a criticism, see Bailer-Jones [2004]).

Hesse also made significant contributions to the developing critique of what came to be called the ‘received view’ of theories, which took them to be sets of logico-linguistic statements, divisible into ‘theoretical’ and ‘observational’. In her ([1958]) paper, she focuses on the core claim that theoretical and observation statements are related via some kind of ‘dictionary’, and argues that if the latter are to be understood as tests of the former, then the distinction cannot in fact be maintained. Interestingly, she begins by insisting on calling such statements ‘phenomenal’ rather than ‘observable’, to avoid confusion with the use of the latter term in quantum mechanics. Phenomenal statements, then, ‘do not describe what happened on a particular occasion to a particular observer, but what always happens and will happen on sufficiently similar occasions to all normal observers’ (p. 15). However, insofar as such statements are intended to be involved in tests of a theory, their meaning cannot be independent of the statements of that theory, since if they are to have ‘scientific significance’, then there must be appropriate connections between them at a level of meaning higher than that of ‘common sense’ or non-scientific concepts. Here she not only gives the well-known ‘bent stick in water’ example but, noting that it may be objected that this could be understood in terms that are not theory laden, she turns to a more interesting and modern example—that of a scintillation screen recording the detection of neutrinos produced in a nuclear reactor. As she argues, the mere report of such scintillations cannot, as it stands, be related to any relevant theory; it is only when the observation is interpreted in the language of elementary particle physics that the associated statement can count as confirming the theory.

As she goes on to say, ‘To interpret an experiment directly in theoretical terms so that it can be a test of the theory is always to say more than the corresponding phenomenal statements would say, because such interpretation carries with it natural expectations about possible but so far unobserved behaviour which the scientist has to learn, just as the child learns the contextual overtones of ordinary language’ ([1958], p. 20). Given this difference, the correct analogy is not that of a dictionary—translating sentences from English to French, say—but that of the translation of poetry into pedestrian prose. Thus Hesse suggests evocatively that ‘the phenomenal description of an experiment has a relation to the scientist’s theoretical description which is similar to that between Holingshed and Shakespeare’ (p. 21). The hierarchy that extends from phenomenal statements to the theoretical may then be likened to the gradation in degrees of imagination from prose to poetry!

With this in hand, we can understand that it is misleading to call theoretical concepts ‘unobservable’, since all observation involved in testing theories involves some interpretation. In a claim that resonates with subsequent well-known discussions in the field, she insists that the scattering of electrons by gas atoms should be characterized as ‘observed’, although the phenomenal description ‘would mention only white streaks in a cloud chamber’ (p. 23). And she continues by criticizing attempts to draw a distinction between ‘direct’ and ‘indirect’ observation in this regard, arguing that such distinctions do not correspond to any important difference in the way the relevant terms function within the given theory (p. 27). Instead, she insists, we should take each kind of entity to be observed ‘in the ways appropriate to it’ (p. 27). Any difficulties associated with the idea of ‘unobservable entities’ are instead peculiar to quantum physics. There, what is actually ‘unobservable’ is not the entity itself but the state it is in when unobserved; however, this feature, albeit fundamental, has no bearing on the epistemological issues she is concerned with in this work.

Her claim that positivistic philosophy of science does not adequately accommodate the practice of science is further pursued in a number of pieces, including an illuminating review of Rom Harré’s Theories and Things ([1961]). Harré argues that by means of ‘ontological experiments’, the domain of things that may be said to exist can be extended from the observable to the unobservable. Underpinning such an extension is the notion of ‘family continuity’, presented as a linear sequence of partially overlapping events. In the case of optical continuity, this can take us from an okapi (!) to a virus, such that any two adjacent objects in the sequence can be observed via the same mode of observation—the eye, the optical microscope, the electron microscope, and so on—and any one object can be identified as the same object via any two of these modes. Harré then claims that if any one member in such a sequence exists, then any other does too, from which he concludes that okapis and viruses exist, but electrons, the wave function, and the unconscious do not.

Here, of course, we have a foreshadowing of the later debate between the likes of Hacking, van Fraassen, and others over the use of instruments such as the microscope, and the observable–unobservable distinction in general. And Hesse ([1962]) raises some useful concerns in her review. As she points out, a plausible form of positivism will not be undermined by Harré’s argument, since family continuity does not extend across ontological classes. Instead, it only shows that new objects can be placed in the same class as ‘ordinary’ physical objects by means of a series of ‘ontological experiments’, namely, observations via anything from a magnifying glass through to an electron microscope. Thus, although this might be argued to undermine the kind of positivism that rules out observation via instruments such as microscopes, it leaves untouched what she considers to be a more plausible form that maintains that only one ontological kind of thing exists, taking us from okapi, say, to those things that can only be observed with instrumental aid, such as viruses.

The realist may have reason to be unhappy with Harré’s argument too, as it rules out electrons, for example. Hesse finds this to be very odd, since it would seem that there is another family continuity in this case, taking us from molecules to atoms to electrons; for Harré to deny this seems to imply no connection between electrons and observables, thereby undermining the former’s status as a kosher theoretical entity to begin with. Harré’s response is that only the effects of the electron are observed, not the thing itself. Hesse is dismissive: ‘What is this distinction between the effects of a thing and the thing itself? Might it not be said equally that the electron micrograph shows the effects of a virus, namely its deflections of fast electrons?’ ([1962], p. 238). Furthermore, it would seem that we can put electrons into the kind of sequence covered by ‘family continuity’ simply by taking into account any of the experiments by which we observe them and working our way ‘up’ to physical objects. But then, as she says, we may have proved too much, since this could be done for any theoretical entity in an acceptable theory. Although she admits that Harré might have been on to something here, it clearly stands in need of further development.

More interesting, perhaps, is Hesse’s point that Harré conflates the issue of what exists with that of what are objects, drawing on Strawson’s definition of an individual object as that for which well-defined identity conditions hold. But as she notes, arguably, such conditions do not hold for electrons and those of us who care about such things will recall her later use of the ‘money in the bank’ metaphor in this context: electrons are like money in a bank account; I can say that I have €300 in my current account, but I can’t go in, as it were, and point to a particular euro and say, ‘that’s mine’. In general, she argues, fundamental particles ‘are only just admitted as entities because of the short-term invariance of rest-mass, charge, and spin’ ([1962], p. 243). And she goes on to take a pop at Quine by insisting that it is useless to expect any light to be cast on this issue from the definition that an entity is one of the values over which variables of the theory range, ‘because it is precisely what this domain of values is that is often a matter of dispute within physics’ (p. 243). Indeed, she continues, the very act of axiomatizing a theory in order to answer the question ‘what are the values of its variables?’ implies the adoption of a certain interpretation, which in turn is equivalent to the decisions involved in answering the question ‘what are entities?’.

This critique of the received view continues in her pointed review ([1968a]) of Scheffler’s book, Science and Subjectivity ([1967]). Responding to the likes of Feyerabend, Hanson, and Kuhn, whom he viewed as advocating a pernicious form of subjectivism, Scheffler attempted to ground scientific objectivity in a Fregean analysis of meaning. Thus, we may grant that the sense of a theoretical term is determined by the relevant theoretical context and so, to use a hackneyed example, the meaning of ‘mass’ differs between Newtonian and relativistic mechanics but the reference may remain the same, and hence we can maintain that the theory of relativity represents an advance over Newton’s theory. However, Hesse ([1988a]) argues, sameness of reference is neither necessary nor sufficient for the comparability of two theories. It is not sufficient because scientific properties are intensional rather than extensional; and it is not necessary because two different theories may deploy different categorizations of objects—and here she gives the examples of Dalton’s and Cannizzaro’s theories of atoms. And yet we still want to say that statements of one theory imply or contradict those of the other. (Hesse ([1968b]) also went on to criticize Fine’s criterion of meaning change, but Leplin ([1969]) subsequently argued that it missed the mark.)

The issue of meaning change crops up again in her analysis of the problem of ‘grue’ (Hesse [1969]). As we all recall, Goodman posed the following problem: Consider the predicate ‘grue’, which applies to all things examined before time t just in case they are green and all things after t just in case they are blue. The two hypotheses that ‘all emeralds are green’ and ‘all emeralds are grue’ are thus supported by the same evidence before t but make different predictions after t, and intuitively we prefer the former to the latter. How then to capture that intuition, articulated in Goodman’s characterization of ‘green’ being more projectible than ‘grue’? Goodman himself argued for a pragmatic account, according to which the predicate ‘green’ is historically more entrenched in our language than ‘grue’. While agreeing that this is correct in principle, Hesse argues that in most actual cases, certain relevant asymmetries other than entrenchment can always be found to justify our choice over the competing predictions. First, she insists that any satisfactory solution of the puzzle must adhere to the following principles: (A) ‘the language describing the present evidence must not be merely verbally different, but must yield predictions which are both genuinely different, and different in respects which the “green” and “grue” speakers (who will be called “Green” and “Grue” respectively) can explain to each other and agree to be different’ ([1969], p. 14); (B) ‘the problem should be shown to be soluble in its strongest form, and that since the solution is to be sought by finding asymmetries in the predictions of Green and Grue, it should not be set up in such a way as to introduce needless asymmetries into the definition or interpretation of the problematic predicates’ (p. 15).

Considering what Green and Grue understand each other to be asserting in their respective predictions, principle (B) rules out such obvious suggestions as, ‘Green understands Grue to be predicting that emeralds will change colour at time t’. In that case, symmetry would clearly be violated, but this can’t be a viable solution. But if both Green and Grue are committed to emeralds remaining the same colour, how can principle (A) be satisfied? The asymmetry must be sought elsewhere, in some ‘real difference’ between Green and Grue. One option would be to shift away from what objects look like and focus on some ‘objective’ property such as wavelength. To illustrate what's involved, Hesse presents a nice piece of dialogue between Green and Grue. Green insists that his prediction does not predict a change in wavelength while Grue’s does, and hence his (Green’s) is simpler, thus establishing the relevant asymmetry. Grue then responds by introducing further grue-like predicates at this more fundamental level in terms of which the symmetry is restored. That is, symmetry can be restored by substantially modifying the relevant theory held by Green, but that, Hesse maintains, would ultimately involve the construction of a new theory entirely—one that is entirely different from currently accepted physics. It is then the absence of the latter that accounts for our inductive expectation that ‘all emeralds are green’ will continue to hold after t. In other words, once we pay attention to the relevant network of laws in terms of which we understand predicates such as ‘wavelength’ or ‘green’, we can see that non-trivial cases of the puzzle are going to be few and far between.

Of course, as she then concludes, genuine examples might be found in the context of the debate regarding meaning variance. Whether there are any theories that are symmetrical in the requisite manner is a question for the historians, but as she says, ‘What Goodman has shown, and it is a fundamentally important insight, is that if there were such pairs of conflicting theories, they would be confirmationally incommensurable’ ([1969], p. 23). Thus, in this confirmational respect at least, Hesse takes Kuhnian incommensurability to be identical with the non-trivial form of Goodman’s paradox (of course, it goes beyond this). In that regard, then, the puzzle is insoluble, but Hesse insists that in practice we rarely encounter such fundamentally conflicting theories (and even more so, theories that are appropriately symmetrical). And so focusing on entrenchment is misleading, since paying due attention to the history of science will show that in all cases, other considerations are always given priority, generating the asymmetry that is needed to break the paradox.

This paper then formed a chapter in her highly regarded book on scientific inference (Hesse [1974]), praised by Bloor ([1975]) as ‘an important and challenging book [that] deserves the closest study not only by philosophers of science, but also by historians and sociologists of science’. Here she brings together the various components of her rejection of the received view and offers instead her ‘network model’ of scientific knowledge (sometimes called the ‘Hesse-net’), touched on above, according to which all scientific predicates are to be understood in the context of a law-informed network (and here, of course, one can find certain commonalities with Quine’s ‘web of belief’). As a result, the circumstances under which an ‘observation’ predicate may be correctly applied may change as these laws change, and hence there is no fundamental distinction between theoretical and observational languages. The structure of the network is then best described via Bayesian probability theory. I’ve chosen to include Dorling’s critical review of this aspect of the book, which focuses on the core problem of how we can be justified in taking the evidence for some theory as increasing the probability that other predictions of that theory will also be confirmed.

Hesse’s response is to draw on the notion of analogy once again, and to argue that such an analogy holds between the relevant instances of prediction, such that we are justified in inferring from the presence of the relevant properties in one such observed instance to their presence in the unobserved ones. This is formally accommodated by requiring that the relevant a priori probabilities satisfy a ‘clustering’ rule, according to which properties that go together in one case stay together in other cases. As Dorling notes, Hesse takes this rule to lie at the heart of scientific inference. Unfortunately, he goes on to argue, it fails in the context of actual historical examples of rival theories—such as Tycho’s and Copernicus’s, or Einstein’s and Ritz’s—which agree on some predictions but not on others. Take the latter example: Here we have agreement on the prediction of the null result in the Michelson–Morley experiment but disagreement over the observed velocity of light emitted from a source moving relative to the observer. Einstein understood both of his predictions as following from the law that the velocity of light is constant relative to any observer, whereas Ritz took both of his to follow from the law that the velocity of light is constant relative to the light source. In this example, Dorling ([1975]) insists, it is difficult to see how Hesse could find a significant analogy in the one case but not the other, yet we cannot have transitivity of confirmation in both cases without contradiction.

This criticism draws on earlier work (Dorling [1974]), and Hesse’s ([1975]) response is illustrative: First, she maintains that she does not assume that we are always justified in making the inference above; rather, she is interested in establishing when we are and when we are not justified. And second, there are different criteria for confirmation in play here. Indeed, at the end of his BJPS review, Dorling accuses her of being closer to a neo-Carnapian than a true Bayesian personalist, which—Life of Brian resonances aside—perhaps makes her account even more interesting from today’s perspective!

Finally, returning to an earlier stage of her career, I’ve also included her papers on Gilbert’s De Magnete (Hesse [1960a], [1960b]) because they serve as a reminder of not only the close ties the BSPS had, at its inception, with the BSHS, but also Hesse’s own historical interests. As noted above, these interests nicely mesh with today’s revival of an ‘integrated’ approach to HPS, at both the national and international levels. In this work, Hesse considers the different views of historians of science regarding Gilbert’s work. Some took him to be one of the first Baconians in his emphasis on experimental work; others focused on his metaphysical predilections. Hesse articulates a third view by bringing De Magnete under the lens of the (then) recently published English translation of Logic of Scientific Discovery. In particular, she suggests that ‘Popper's thesis, namely, that there are no privileged observation statements upon which scientific theory can be inductively based, is amply illustrated by the details of Gilbert's work’ ([1960b], p. 130). More generally, from the Popperian perspective, Hesse argues that the above distinction drawn by historians should be replaced by another: between Gilbert the experimental scientist, who adopts a form of ‘conjectures and refutations’, and Gilbert the metaphysician, who proposes views that are unfalsifiable but heuristically suggestive. Interestingly, in the context of a detailed analysis of Gilbert’s research into the nature of electricity and magnetism, and in particular the sense in which his notion of a magnetic ‘form’ might be viewed as a cause of the relevant phenomena, she makes the distinction between what is now known as the deductive-nomological account of explanation and the alternative view of explanation as ‘making plain’, in the sense of capturing some puzzling phenomenon via a familiar model. Here again the role of analogy is crucial, and Hesse clearly sets out the positive and negative analogies that Gilbert draws between magnetism and the soul, thereby adding further nuance to his animism. And of course, from the Popperian perspective, this analogy is metaphysical and unfalsifiable.

The paper ends with Hesse’s reflections on Bacon’s dismissal of Gilbert’s work, in which she suggests that the ‘subsequent practice of science’ ([1960a], p. 141) justifies the latter’s approach rather than the former’s, in that although Gilbert also used a method of ‘crucial experiment then elimination’, what was being eliminated were entire prior theories rather than mere ‘qualities’. (Hesse ([1966]) went on to consider Bacon’s method, as refracted through the work of Hooke.) And, she argues, this elimination does not proceed with the aim of showing there can be only one theory, but rather ‘merely replaces a few refuted theories with another’, thereby following a method that is ‘nearer the pattern of later physics’ ([1960b], p. 142).

One might object to the details of her historical analysis of Gilbert’s work (cited in Freudenthal [1983]), and one certainly could balk at this early imposition of a Popperian framework upon it. But what is of lasting significance in this paper is her view, as expressed in another of her books, that ‘In writing the history of science there will always be present, either implicitly or explicitly, some philosophical view of the nature of science’ (Hesse [1961]). This integrative attitude runs throughout her work, from these early papers to her later forays into the sociology of scientific knowledge (Arbib and Hesse [1986]; Hesse [1980]). But as indicated at the beginning of this introductory essay, her importance for the history and philosophy of science as a whole goes beyond this academic work, to embrace her active roles in professional organizations on both sides of the Atlantic and, not least, her editorship of this journal. The papers reproduced here are only a small sample of her extensive and varied output over many years, but hopefully they are indicative of both the range of her interests and her philosophical insight.

*With thanks to Wendy Parker for helpful amendments.