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Philosophy of Science, 1950-2000

1. Introduction

The past century has assuredly been a turbulent time in the philosophy of science. The discipline itself has, of course, an ancient history, stretching back to Plato’s Republic and Aristotle’s Posterior Analytics. But as the sciences themselves have grown so rapidly in power and complexity over the last century, so has second-order reflection on these sciences, what we call philosophy of science, itself become a great deal more luxuriant-as well as more disputatious! The history of the philosophy of science has, in fact, emerged as a third-order discipline in its own right. The task of our symposium is primarily a historical one; we are asked to look at developments in the philosophy of science in the century just past and identify some of the milestones. Obviously, we have to be very selective.

I will restrict the scope of this paper in several ways. First, I will be concerned mainly with the second half of the century past. I began my graduate studies in philosophy of science at the University of Louvain in the Fall of 1950, so that mid-century seems a particularly appropriate starting-point for my review. Second, I will treat only philosophy of science and not the much more diverse set of fields loosely labelled the philosophy of the sciences. This latter treats philosophical issues raised by developments in particular sciences, like physics, biology, psychology, economics… These issues are usually specific to a given science; they are often issues that the practitioners of these sciences are themselves grappling with, like the entanglement issue in quantum physics or the altruism problem in evolutionary biology. Philosophy of science in the narrower sense of that term is a much less specialized enterprise. It deals with broadly epistemological problems common to the sciences or, at least, to large parts of the sciences. It is concerned with topics like validation, explanation, cause, and the like. Where philosophy of the sciences, with its distant origins in natural philosophy, is historically tied to individual sciences, philosophy of science has had much broader philosophical associations and has indeed had in recent centuries a strong influence on philosophy generally, most especially on epistemology, of which it constitutes a significant part. Its relationship to its own history is that of philosophy to its history; avenues explored in the past retain a relevance for the present. Indeed, as we shall see, philosophy of science may have an even more intimate relationship to its history than does philosophy itself.

One further restriction of scope might seem more problematic. I intend to limit my account to philosophy of science in the broadly “analytic” (effectively, the Anglo-American) tradition, leaving aside the substantial discussions of science in the “Continental” traditions of France and Germany. The divergence between the two that began with logical positivism and was hastened in the post-World War II years by the critical attitudes towards science favored by existentialist and broader moral and political concerns in Western Europe, has been, at least until recently, so deep that it would be difficult to do justice to both in the space of a short essay. Where one aimed at the explication of science more or less as a given, the other regarded science as a risky abstraction from the richer value-impregnated whole of human knowledge, hence the label: ‘critique of the sciences’ (Gutting, 1979). Where one valued linguistic clarity and rigor of argument, the other regarded these with a degree of distrust and tended to rely rather more on the resources of metaphor and linguistic invention.

I ought not, however, leave the gap seem quite so unbridgeable. Bachelard, in the ‘thirties, had already anticipated some of the main themes in later Anglo-American philosophy of science, notably the essentially historical character of science, the presence of breaks in the history of science, and the theory-ladenness of observation reports. More recent developments on both sides have also shown some obvious affinities of interest and have even, on occasion, led to some cautious dialogue (Bernstein, 1983; Gutting, 1998). Foucault’s reworking of the history of science, for example, where he makes a point of the “ruptures” he finds there, finds an obvious echo in Kuhn’s writings. Foucault and Hacking sometimes find common cause also in their approaches to scientific institutions. Habermas’ analysis of the cognitive interests governing scientific development could offer some pointers for the current debates on social construction on the anglophone side. Indeed, the gap between the two traditions is tending, if not to close, at least to lessen, as the sociology of scientific knowledge, in Britain particularly, pushes its challenge to philosophy of science, as this latter has been traditionally understood.

Looking back on the crowded history of the philosophy of science in the century just ending, which developments would be seen in retrospect as most significant? There would be fairly wide agreement, I suspect, on three that stand out: the transformation in the philosophy of science wrought by logical positivism in the second quarter of the century, next, the rapid decline of logical positivism and its virtual replacement by a very different set of concerns of a broadly historicist kind in the third quarter, and finally, after historicism had (not without a struggle) to some degree taken hold, the further recognition that history and contemporary practice testify to a larger and (some would say) a more constitutive role for social factors in scientific decision-making than has in the past been generally recognized. Debates about the merits (and the limits) of social constructivism have been perhaps the most notable, and certainly the most controversial, feature of philosophy of science in the closing quarter of the century. Postmodern critiques of scientific rationality of the sort that figure especially in literary journals have roused the ire of scientists even more than of philosophers of science; in the ensuing “science wars”, the two sides often appear to shoot past one another. I shall touch only briefly on this last development.

In this essay, I am going to focus mainly, then, on the historicist turn of the ‘sixties, its antecedents and its consequences. This will lead into the debate between defenders of scientific realism and their critics, among them the proponents of the more radical versions of social constructivism. It might not be too much to say, indeed, that these latter stand or fall with the fortunes of anti-realism. Those who have made the most sustained case for anti-realism have, as it happens, had little interest in social-constructionist initiatives. But it would, I think, be true that the limits of these initiatives are set more effectively by laying out the case for a carefully defined form of scientific realism than by tackling the more general issue of scientific rationality.

When writing about the profound shift that occurred in the concerns of philosophers of science in the ‘sixties and ‘seventies, it is important not to make the transition sound altogether abrupt, a paradigm-shift in the classic Kuhnian sense. It was not abrupt; indeed, it was anticipated in significant ways long before the conventional marker of the change, Kuhn’s Structure of Scientific Revolutions, appeared in 1962. To introduce my topic, therefore, it seems appropriate to devote attention first to a brief appreciation of what might be called “anticipations”, various disagreements and developments that occurred even within the period of positivist dominance that, in retrospect at least, point forward to a very different philosophy of science than the rather stark one of Carnap’s Aufbau which in 1928 announced a radical new approach to the philosophy of science and, indeed, to philosophy generally.

2. Anticipations

Carnap’s project was to discover the logical syntax that should characterize the language of science. The logic here would be the newly-formulated extensional logic of the Principia Mathematica of Russell and Whitehead. For such a project to work there would have to be premises for the logic to work on; the science whose syntax is defined would have to have access to basic statements, “protocol sentences”, that would be warranted by experience directly, as befits a radically empiricist reconstruction. They would in that way provide “the firm basis to which all our cognitions owe whatever validity they possess”, as Schlick, the most committed defender of this founder ideal once put it (Schlick, 1959, 210). Neurath was, however, skeptical of this ideal from the beginning. Recalling the imprecision of the ordinary language that enters necessarily into basic statements about the physical world, he insisted that:

There is no way of taking conclusively-established pure protocol sentences as the starting-points of the sciences…. We are like sailors who must rebuild their ship on the open sea, never able to dismantle it in dry-dock and to reconstruct it there out of the best materials (Neurath, 1959, 201).

The force of Neurath’s argument eventually brought Carnap to agree with him, leading both of them to turn to a coherence account of truth, edging them away from the simpler foundationalist empiricism on which logical positivism had originally set its hopes. Meanwhile, doubt was being raised from a different quarter about the incorrigibility of the basic statements on which empirical science rests. For his attractive notion of falsifiability to function as the neat distinguishing characteristic of science, Popper needed something like protocol statements to function as his falsifiers. But were they, then, themselves to be held immune to test? Popper realized that this would lead to inconsistency. But how in that case was a destructive regress to be avoided? Popper’s response was to concede that at some point or other we must stop “and say that we are satisfied for the time being” (Popper, 1959, 104). This admittedly allowed entrance to an element of “decision or convention”, but he believed that the arbitrariness to which Neurath laid himself open could be avoided if a criterion could be specified, namely, ease in testing. He allowed, however, that this would sometimes leave room “not only for subjective convictions but even for subjective bias” (110) at the very foundations of theory-assessment in science but saw no way to avoid this entirely. It is not hard to discern in this gradual relaxation of the austere ahistorical foundationalist maxim some glimmerings of the historicism that lay ahead.

Another example of this softening would be Carnap’s gradual admission of the insufficiency of syntax for the philosophical analysis of the language of science; semantics would also be needed for a language with complex empirical application. This, in turn, led him to a fateful distinction between the “internal” and the “external” questions that might be posed regarding a linguistic framework (Carnap, 1956). A question, for example, about the existence of a particular class of entities, whether empirical or abstract, internal to, that is relative to, a given linguistic framework can be answered through a semantic analysis of the framework itself. But “external” questions about the entire class of entities associated with a given linguistic framework are really, he now claimed, covert questions about the utility of the framework itself and can be answered only by addressing pragmatic issues about the purposes of that language and how well these are being realized. A question about the existence of numbers which is unanswerable on simple empirical grounds, for example, reduces to an easily answerable question about the utility of number-language generally.

But this invoking of pragmatics has far-reaching consequences. On the face of it, it should apply to any theoretical framework, to any scientific theory, therefore, as Philipp Frank and Quine realized. A question about the existence of electrons might, then, reduce to the more tractable question of the practical utility of electron language (McMullin, 1983, 13). Frank argued that scientific theories ought not be regarded as “replicas of reality” for two reasons. First, they are “not unambiguously determined by the observed facts” (Frank, 1957, 355). But even more important, among the pragmatic reasons that ought to determine the acceptance of a particular theory is its “fitness to support desirable moral and political doctrines”. To those who would object that social factors of this sort ought not intrude into theory-assessment in science, Frank’s response was: the fact is that they do, and what is more, must do, since the traditional empiricist criteria of theory-assessment of themselves are insufficient to determine theory-choice. Further, “fitness to support desirable conduct on the part of citizens, or briefly, to support moral behavior, has served through the ages as a reason for the acceptance of theory” (Frank, 1957, 356, 354). It may be relevant to recall that Frank lectured at Harvard when Kuhn was a graduate student there. But it should also be noted that Kuhn never ventured as far in the historicist-constructivist direction as the one-time positivist quite clearly did.

Among others outside the positivist orbit who anticipated one element or another of the historicist turn and who influenced Kuhn more or less directly, we may recall four in particular. First among them was, of course, his Harvard colleague, Quine who rejected the two “dogmas” that he saw as implicit in the verificationist notion of meaning that underlay the entire positivist enterprise. Instead, he proposed a holistic theory of meaning in which “our statements about the external world face the tribunal of sense experience, not individually, but only as a corporate body” (Quine, 1953, 41). In this way, empiricism might still be saved but only at the cost of a much looser notion of empirical significance. A recalcitrant experience, far from immediately falsifying a theory, could in principle always be accommodated by making adjustments somewhere else in the web of statements constituting the theory. Such adjustments would be guided by such practical objectives as maximizing simplicity and inflicting as little disturbance on the network as possible. Whether such objectives would cohere with Quine’s overall instrumentalist goals for science was not so clear.

The most influential critic of logical positivism in those years of its decline may have been Paul Feyerabend, who, like Quine, took his inspiration mainly from the philosophy of science but who, unlike Quine, relied heavily on illustrative references to the history of science. He was popularly regarded as the enfant terrible among the critics, though truth to tell, he was much more terrible later as an adulte than he ever had been as an enfant! Influenced by Popper and to a lesser extent by Wittgenstein, he set out in a series of discursive, insightful, though not always consistent, essays to underline what he saw as the problems facing empiricism, as that position had been interpreted by the Vienna Circle. His principal target was the notion of meaning invariance that he saw as its mainstay (Feyerabend, 1962, 31). In its stead, he proposed a “contextual” notion of meaning, holding that words obtain their meaning from what he called their “theoretical” context, understanding this to cover, as he put it, any general point of view concerning matters of fact (Preston, 1997, chap. 2). This holism of meaning led him to argue that meaning-change is a necessary feature of scientific theory-change, and even more controversially, to develop, partly in conversations with Kuhn, the view that successive theories may well be incommensurable with one another, leading to problems about their assessment relative to one another (Feyerabend, 1962, 58-9; Preston, 1997, chap. 6).

The opening chapters of Hanson’s book, Patterns of Discovery (1958) offered an accessible critique of the sense-datum construal of meaning, in the spirit of Wittgenstein’s Philosophical Investigations. Hanson argued that key elements in the empiricist account of science, observation and fact, are radically language-dependent. To observe is not just to see something; it is to see it as a particular kind of thing. Thus two people gazing at the same object may report very different observations: “an X-ray machine”, “a large metal object”, depending on their prior experience and their linguistic resources. His conclusion: observations are necessarily theory-laden, where the term ‘theory’ is taken to cover assumptions of any kind (Hanson, 1958, 19; Gutting, 1980, Part One). Duhem had made substantially the same point half a century before, relying mainly on a detailed analysis of scientific practice. Despite his constant reference to the history of science, Hanson relied here rather more on the analysis of ordinary language. His use of familiar diagrams drawn from gestalt psychology to make his point about the difference between seeing and seeing-as would find an echo later in Kuhn’s book. Hanson’s emphasis on human powers of pattern-perception was perhaps somewhat overdone since these play very little role in the reading of instrument dials and the like that constitute observation in much of modern science. And his reiterated claim that were Ptolemy and Kepler to look to the horizon at dawn they would observe, one the sun rising and the other the earth setting, carried his point about theory-ladenness a step too far. But his effort to extend the reach of philosophical concern to the topic of discovery in science, which had been deemed incapable of logical and hence philosophical analysis by the positivists, eventually bore fruit (Nickles, 1980a, 1980b). What his work may have lacked at times in logical rigor, it surely made up for in terms of imagination.

Another book made its appearance in the same year as did Hanson’s that excited little attention at first among philosophers of science but whose eventual impact was nonetheless considerable. Polanyi’s Personal Knowledge was one of those rare books, like Bacon’s New Organon or Wittgenstein’s Tractatus, that break into philosophy from the outside, as it were, drawing on resources remote from the prevailing philosophical tradition (Polanyi, 1958, 1961). Polanyi was an accomplished physical chemist who when he turned to philosophy found the logicist analyses of the Vienna Circle remote from the science he knew. Science was a complex learned activity, he argued, involving skill and even passion. What made for good science was, first and foremost, good scientists. And what made them good scientists could not be entirely reduced to rule, as though it could be learnt from a rule-book. Critics charged that the tacit dimension Polanyi introduced into scientific knowing would undermine the objectivity that could only be guaranteed by a testable adherence to norms or rules open to public scrutiny. Kuhn would encounter a very similar challenge.

3. The parting of the ways

We are now at a crucial point in our story. Both the empiricist notions of meaning and the logicist ideals of reduction that had defined the original logical positivist program for the philosophy of science had at this point been called into serious question, and this from within the positivist movement itself as well as from without. In retrospect, one might venture to say that what was now needed was a work that would bring to a focus those questionings and accomplish perhaps the paradigm-change that had been for some time in preparation.

That work would, of course, turn out to be Kuhn’s Structure of Scientific Revolutions whose impact on the philosophy of science, for better or for worse, can hardly be exaggerated. The best-selling philosophical work of the century, notable for its influence on fields far remote from science, notable too for its record of attracting critics and admirers in about equal measure, it presented a view of science that differed from the original positivist one, it might seem, in almost every essential detail. Where the positivist aim to subject science to rigorous philosophical analysis had required that it be stripped down to a timeless propositional framework in which only features like meaning, verification, explanation, would remain for discussion, Kuhn proposed to recover, so far as this was possible, the complexity of science as it has been actually carried on, extending the mode of analysis, therefore, from the narrowly logical to the broadly historical (Gutting, 1980; Hoyningen-Huene, 1993).

Kuhn’s construal of the history of science as long periods of what he called “normal science” punctuated by periodic abrupt paradigm-shifts, is so familiar that it presumably needs no elaboration. Rather, I want to stand back from it to ask: to what general features of science was Kuhn pointing? My suggestion is that they were three: one, science is a historical enterprise whose historical character has to be taken seriously; two, human subjectivity enters into the day-to-day operations of science at a deeper level than the positivist model could ever have accommodated; and three, science has an ineliminably social character that marks its operation in crucial ways. I plan to pursue these three threads in turn: historicity, subjectivity, and sociality. Much of the debate in philosophy of science from the early ‘sixties until today has been prompted by attempts to explore, and to determine the limits of, these three themes as they apply to our understanding of science.

They are, in fact, closely interlinked but in the end are distinct. They are also ambiguous, so it will be helpful to sharpen them somewhat first before entering into more detail on each. Let me begin with historicity and its associated “-ism”, historicism, which may, in the context of the philosophy of science, be the most ambiguous of the three (McMullin, 1979b). Kuhn invokes the theme of historicity in at least three distinct ways. First, there is historicity at the metalevel. Recall the familiar opening sentence of Structure:

History, if viewed as a repository for more than anecdote or chronology, could produce a decisive transformation in the image of science by which we are now possessed.

The implicit thesis here is that the appropriate warrant for the philosophy of science, in whole or in part, is the history and practice of science. This will later be called by an even more ambiguous term, epistemological naturalism.

A second way in which historicity makes its appearance in Kuhn’s work is the overwhelming emphasis he places on propositional science, the science of the research article and ultimately the textbook, as a historical phenomenon exhibiting discontinuous change. Of course, no one would ever have denied that science in this sense had a history. But what many readers of Kuhn’s book saw there in its emphasis on successive revolutions, each overthrowing the paradigm that had previously held sway, was a skeptical sort of historicism, which called in question the progressive character of science and the stability on which its claim to objectivity rested (Scheffler, 1967; Shapere, 1964).

The historical dimension of science could manifest itself in yet a third way when scientific rationality, that is, the norms that constitute science as science, themselves are viewed as subject to change, as dependent perhaps on historical context. The historicity of scientific rationality once again is a claim that no one would be likely to deny; what constitutes scientific reason today is obviously not the same as it would have been for Aristotle or even Galileo. But where deep disagreement can arise is in how far to push this claim, what its epistemological consequences are.

There is one further intrusion of the temporal dimension of science that Kuhn did not note but that would achieve some importance in later discussions of scientific realism. Many realists have argued that theory-assessment must take into account the temporal character of theory, its ability over time to predict novel outcomes or to deal with anomaly successfully. These are the features that were lost to sight (they would say) in the static propositional construal of theory favored by the positivists; yet these too are the features that count most in the decision to give a particular theory a realist interpretation (McMullin, 1996; Leplin, 1997).

How about the second theme, subjectivity? We saw already that Popper and Carnap had been forced to allow a subjective element in the decision to accept a particular observation-statement as properly basic. Popper spoke of it as conventional; Carnap allowed it to be pragmatic. The point was that a decision had to be made that was not simply rule-governed. Hanson and Kuhn would assert that observation statements are necessarily theory (or more properly assumption) laden; different scientists could bring different assumptions to the table, assumptions that reflected some degree of subjective choice. Even more significantly, theory-choice could not itself, Kuhn pointed out, be reduced to a matter of rule; rather, it involves maximizing values on whose character and relative weight scientists would be liable to disagree. Here too, then, subjective choice could enter into the ordinary workings of science. The fact that competent scientists routinely disagree as to which is the better theory, and that such controversy can be long-lasting is undeniable witness to this. Where philosophers may (and did) disagree is, of course, as to how much weight to put on this, and in particular how such subjectivity is in the long run to be constrained.

Finally, the third theme is sociality, the social character of scientific research, a theme already underlined in the seventeenth century, particularly by Bacon and Boyle. Kuhn stressed the role of the scientific community in shaping the education of the future scientist; he defined his notion of “normal” science in relation to that community. He pointed to the part played by the community in certifying observation claims and in resolving controversial theory choice. He believed, however, that the role of the broader social and political communities could be distortive and that the scientific community could and should distance itself from these broader social influences: “The practitioners of a mature science are effectively insulated from the cultural milieu in which they live their extraprofessional lives” (Kuhn, 1977, 119). Here, as we shall see in a moment, it was Kuhn who proved to be the conservative!

The enlargement of philosophical concern to dimensions of science that had been neglected or only reluctantly considered during the positivist era took in more than the three themes just listed. But these were the ones that would shape most of the debate in the years that followed. It is difficult to find a single term, a single “-ism”, to cover this era of diverse initiatives. A parting of the ways it has surely been. But apart from the bland and not very informative term, ‘post-positivism’, no label has as yet been agreed on by historians or by the protagonists themselves. Perhaps it is best to hold the historicist, the subjective, and the sociological initiatives separate, since apart from a rejection of positivist constraints, their implications for future discussion are worth keeping distinct.

So far I have been speaking in generalities. Now, some historical detail is needed, focussing on each of the three post-positivist enlargements of concern in turn. And first to the historicist challenges.

4. Historicist metamethodology

On what basis does philosophy of science, as a discipline, itself rest? If it is treated as a logic, the appeal is likely to be to intuition or the like, and the ensuing account will be regarded as normative, whether the logic be a deductive one, as with Aristotle or Descartes, or an inductive one, as with Mill or Carnap. But as far back as Kepler’s Apologia pro Tychone or Whewell’s Philosophy of the Inductive Sciences, there have been those who appealed to the history of scientific practice itself as proper warrant for a philosophy of science. Kuhn’s declaration would seem to ally him with these, and that is surely the sense in which his book has been taken. But some caution may be in order. His book is loaded with historical detail, to be sure, and this often serves to support the points he is making about paradigms, normal science, and the like. But on closer inspection, philosophy of language in the tradition of Quine and Feyerabend comes to seem almost equally important, and on at least one crucial issue, the incommensurability that supposedly afflicts paradigm-change, philosophy of language is clearly the main inspiration. Critics have questioned many of Kuhn’s claims on historical grounds, for example that crisis is a necessary condition for the appearance of a new paradigm, that paradigm shifts must occur “all at once”, or that the incommensurability between successive paradigm-shifts leads “inevitably” to difficulties of communication across the revolutionary divide (Kuhn, 1971, 77, 150, 149). And they have pointed to the general difficulty of deriving the warrant for a philosophy of science from the retelling of episodes from the history of science, since the retelling will inevitably involve interpretation in terms of the very philosophical framework that is in question. When, for example, Kuhn says that Priestley and Lavoisier saw different things when they looked at the same chemical phenomena, or, more generally, that the choice between competing paradigms has typically involved “a choice between competing modes of community life” (Kuhn, 1971, 120, 94), is history serving as warrant or as illustration of a philosophically-based thesis?

This difficulty became even more pronounced in later appeals to history of science in order to support a particular philosophy of science. Lakatos made this historicist metamethology a keystone of his methodology of scientific research programs. But he had to allow that a degree of what he called “rational reconstruction” of history would necessarily be involved, even to the extent of allowing that, on occasion, the actual practice of science did not conform to the model that his MSRP would require (Lakatos, 1971; McMulliln, 1978). Calling on history as warrant would, then, at the very least, involve a decision as to which of the rival accounts needed the least amount of “rational reconstruction” to fit the historical record. Even more troublesome was the old challenge to inductivism that Lakatos’ mentor, Popper, had pushed so hard: how is one to avoid bias in the selection of historical case-studies to support one’s supposedly inductively-based claim? In the end, the appeal of Lakatos’ scientific method in terms of progressive and degenerating problem-shifts, hard-core and protective belts of premises, and the rest, derived at least as much from a commonsense prior rationality, as from a supposed fit with history.

In his book, Progress and Its Problems, Laudan proposed a model of scientific rationality which would make it dependent on an appeal to some “archetypal” developments in the history of science that would be certified in advance as rational by what he called “pre-analytic intuitions” on the philosopher-historian’s part (Laudan, 1977). And they would, apparently, be deemed “rational” because of their success in what he defined as “problem-solving.” The task of the philosopher of science would then be to construct an account of scientific rationality that would fit as many of these intuitions as possible. But surely there is a threat of circularity here: do we not already need to have a definite notion of rationality or alternatively, of successful problem-solving in mind in order to pick out the needed archetypes (McMullin, 1979)? Laudan struggled with this and other related objections to this sort of historicist, or has it also been called, “naturalist”, metamethodology in later writings, and organized a large-scale testing of his account of scientific rationality against a set of specially-written historical case-studies (Donovan et al., 1992). But objections persisted to this sort of inductivist approach. It seems clear by now that the basic philosophy of science can neither disregard the historical practice of science nor take this practice as a sufficient norm, prior to any decision as to how the history of science itself is to be reconstructed. The project of extracting a form of rationality from episodes in the past history of science of which the participants themselves may have been unaware evidently requires a pretty delicate touch!

5. Rationality and theory-change

So much, then, for history of science as warrant. But this was by no means the principal message that the first readers of Kuhn’s work took away with them. They saw the book as historicist in a far more controversial way, as indeed challenging the very rationality of science itself on historicist grounds. The major theme of the book was, after all, the discontinuity of paradigm-change and the consequences thereof. Later stages of theory-development cannot properly be said to be any nearer the truth than earlier stages were. The metaphors of religious conversion and gestalt shift, the stress on incommensurability, caught immediate attention. All in all, the book seemed designed to challenge the rationality, the reason-giving, that had defined natural science since its earliest phases.

In a postscript to the second edition of Structure and in a number of essays in his later work, The Essential Tension, Kuhn labored to show that the implications of his account of paradigm-change for the rationality of that change were far less radical than his critics were assuming them to be. His disavowals were not entirely successful; his critics continued to use terms like ‘irrationalist’ or ‘relativist’, ‘subjectivist’, to describe his message. The rhetoric of the first edition of Structure evidently lingered in people’s minds. I would argue, however, that if his writings be taken as a whole, it seems fair to say in retrospect that he was trying to redefine the rationality of paradigm-change in science rather than to undermine it fatally (McMullin, 1993).

First, he always emphasized that there are “good reasons” for paradigm-change (Kuhn, 1971, 199), notably the perception of anomaly and the recognition of an alternative to the ruling paradigm. What he wanted to bring out was that these reasons are not coercive; they cannot compel assent and there is no precise point at which defense of the older paradigm becomes illogical. Second, though he emphasized that the factors governing theory-choice in science function as values to be maximized rather than as logical rules to be mechanically followed, he also maintained in his later work that these values or shared criteria carry through paradigm-change; they are, he boldly asserts, “permanent attributes of science” (Kuhn, 1977, 335), available to guide paradigm-choice. No matter how deep the incommensurability between two successive paradigm-languages may run, the values governing theory-choice are there to serve as criteria applicable to each paradigm alike. Proponents of the two paradigms, Kuhn goes on, will disagree as to the relative weight to be given to the criteria, but the fact is that they will have a stock of perfectly good, though admittedly not compelling, reasons to call in support of their own paradigms. Third, the challenge of incommensurability, which had seemed almost insurmountable in the first edition of Structure, seemed to dwindle in his later work, notably in his last treatment of that topic, in the final essay of the Festschrift in his honor, World Changes (Horwich, 1993), where he makes it clearer than he had originally done that to call two paradigms incommensurable is not to imply that they cannot be rationally compared. Since it is perfectly obvious that even in the case of the most profound paradigm-shift in the history of natural sciences, the Galilean one, Galileo himself could compare the Aristotelian paradigm of his own early work to the new one he was proposing for mechanics, this clarification on Kuhn’s part was welcome.

But if Kuhn’s views on the rationality of paradigm-change were in the end less radical than at first they seemed to be, he never retreated from the more radical claim that the history of science shows that science cannot be construed as converging on truth about the natural world; the discontinuities in the historical record are compatible with a modified notion of scientific rationality but not (he claimed) with the traditional view of science as progressing towards an ever-deeper grasp of real structure. There was no progression in that ontological sense from Aristotle to Newton to Einstein, only an improvement in problem-solving, in the accuracy and scope of prediction. In a famous sentence, he declared: “The notion of a match between the ontology of a theory and its ‘real’ counterpart in nature now seems to me illusive in principle” (Kuhn, 1971, 206). Though he made it clear that his motivation for this strongly anti-realist view of theory came in the first instance from the philosophy of language, he claimed that it was confirmed by his reading of history. He allowed that this would seem a relativist position to many, but insisted that this was as far as the history of science allowed one to go.

I will return in a moment to this challenge to the traditional realism of the sciences and the influence it has exerted in the intervening years. But first, a further possible intrusion of historicity into the one-time atemporal logic of science must be noted.

6. Historicity and rationality

Kuhn, as we just saw, responded to the charge of irrationalism lodged against him by claiming that he was perfectly prepared to allow on historical grounds that paradigm-change and, more broadly, theory-assessment in general are shaped by criteria that remain relatively unchanged over time. Later writers have tended to question this restriction of the historicist thesis, arguing that the criteria of theory-assessment, as for the acceptance of an observation-claim, have themselves changed substantially over the years. Shapere and Laudan, for example, have developed somewhat different accounts of how and why such change has taken place (Shapere, 1984; Laudan, 1984a). Like Kuhn himself, they are anxious to maintain the overall rationality of theory-assessment in science, and believe that this can be done by providing a second-order account of how the criteria themselves might alter, on grounds that can themselves be described without circularity as rational.

The key to this is to show, on historical or on logical grounds, how the chosen criteria are fitted to serve the long-range goals of science. Of course, this raises the further historicist query: might not the goals themselves alter, and would this change still count as rational? Laudan developed what he called a “reticulated” model of scientific inquiry, involving aims, methods for achieving these aims, and at the bottom level, factual claims. Each of these three elements, he argued, calibrates the others, allowing any one of them to change but keeping the whole in a sort of meta-rational balance. It seems clear that the goals of science have, in fact, changed over the course of history: Aristotle’s goal of demonstration, worthy though it was, proved impracticable, as did the seventeenth-century goal of universal mechanical explanation as that goal was then understood. The challenge, then, is to reconcile this story of maturing goals with the claim to a complex form of rationality, in which accuracy of prediction is likely to serve a key role at the meta-level (McMullin, 1989, Introduction).

7. Subjectivity

I have spent a good deal of time at what I think to be the most characteristic emphasis in the philosophy of science of the last half-century, namely, the emphasis on historicity in one form or another. But other themes impose themselves too. In the logicist picture of science, the individual subject was almost invisible; the stress was on rule, universally applicable. Already among the positivists themselves, as we saw, there was a growing realization that human decision entered in at many of the key moments in scientific inquiry. When and how was an observation to be certified as basic? Which of two fairly effective theories was to be preferred? There was room for legitimate disagreement in response to questions like these. Popper and Carnap used the slippery term ‘convention’; others spoke of “decisional” elements. Of course, the notion that scientific claims are routinely underdetermined by the data offered in their support was in no sense new. It was a commonplace already in the seventeenth century, though somewhat obscured in the later Newtonian era.

We have already seen how Kuhn urged that the criteria involved in theory-assessment ought to be regarded as values to be maximized rather than as rules to be followed. Different scientists will understand values like coherence, simplicity, and so forth, differently and also weight their importance differently. In this way, the prevalence of controversy at the growing points of science becomes intelligible, a feature of science that resisted explanation in the hard-and-fast terms favored by strict positivism (Engelhardt and Caplan, 1987). One of the liveliest issues in post-positivist philosophy of science has been the propriety of allowing metaphysical considerations to affect theory-assessment. It is clear that they do, in fact, do so, sometimes in dramatic ways, as, for example, in the famous disagreement between Bohr and Einstein regarding the merits of the new quantum theory. But should they do so? Metaphysics, after all, is not outside the range of rational argument; it ought not reduce to a matter of taste or the contingency of personal background, as its positivist critics charged it did. There are, of course, difficult issues here, issues that are in no way new but that present themselves here in a new guise. It seems fair to say that they are not likely to be resolved soon!

8. The realism debate

The thrust of philosophy of science in recent decades has been, as we have seen, to call in question many of the idealizations on which the logical-empiricist program depended. Restoring the historical dimension to science, recognizing how far from simple rule are many of the decisions that scientists must make in the course of their work, led from logicism to what has at times amounted almost to an anti-logicism, seen in its most extreme form in Feyerabend’s later writings. No one has been inclined to deny the progressive character of science if it be regarded merely as an instrument of prediction, a set of problem-solving devices. It would surely be difficult in our technology-driven society, even for a philosopher, to query the fast-accelerating power of the natural sciences to mold the earth to human desires. Where question arises is in regard to ontology, to the ability of the sciences to reveal the underlying structures of the natural world. That the sciences can do this would seem beyond question to most people, scientists and non-scientists alike. How, then, explain the rise of anti-realism among philosophers of science in the ‘sixties and ‘seventies? Was it just the professional perversity of philosophers showing itself, their irrepressible inclination to call in question the obvious? Or was it the sort of consequence one might have anticipated from the decline of positivism?

A preliminary comment: Anti-realism, in its instrumentalist form, has been a recurrent feature of the history of science. It has usually been local, that is, affecting only a particular science or set of sciences, rather than global, that is, affecting theoretical natural science generally. Thus, an instrumentalist construal of mathematical astronomy was more or less standard in medieval and Renaissance times; a similar approach to atomic physics was not uncommon in the nineteenth century. There were specific reasons in each case for this sort of reservation in regard to a particular domain of science. Their empiricist account of meaning led the logical positivists, especially in their earlier stricter period, to be wary about theoretical language and to question, in consequence, the ontologies that go with it. Thus, there was an anti-realist cast to their thinking, this time of a global sort, that regarded the explanatory success of physical theory as inadequate testimony of the existence of the entities postulated by the theory. In an influential essay “The theoretician’s dilemma”, Hempel called this ontological skepticism in question and went on himself later to defend a strong form of realism (Hempel, 1958; 1966).

But Kuhn, as we have seen, defended anti-realism as a direct consequence of his account of meaning and of paradigm-change. Since each paradigm tends to sweep away its predecessor, there can, he claimed, be no confidence in the permanence of the theoretical entities associated with any particular paradigm, no matter how well-supported that paradigm may appear. Later writers, like Laudan, Rorty, and Fine, picked up on this historicist theme, Laudan in particular developing an effective polemic against what he called convergent realism (Laudan, 1984b). Global anti-realism of this sweeping sort has one nasty consequence: it calls into question any sort of reality-claim for entities the warrant for whose existence would be the explanatory success of the theories in which they appear. This would include, then, all historical theories, cosmology, evolutionary biology, palaeontology, all attempts to establish the sequence of events in the distant past as well as the sorts of entities that populated the universe long ago, or for that matter, not so long ago. Quod nimis probat, nihil probat; the medieval adage “what proves too much, proves nothing”, comes immediately to mind (McMullin, 1984).

Global forms of anti-realism, inspired by accounts of theoretical meaning or of theory-change, by attacks on the misnamed “inference to best explanation”, or by the more extreme forms of social constructivism, are all vulnerable to this kind of commonsense objection. Among anti-realisms, much more viable are local or selective anti-realisms directed at specific sciences for reasons peculiar to that science. It is no accident that the most effective critics of scientific realism in recent decades are philosophers of quantum physics, like van Fraassen, who are motivated primarily by the ontological puzzles of their own field (van Fraassen, 1980). Indeed, van Fraassen’s notion of empirical adequacy would implicitly commit him to some sort of realism for entities other than the sorts of unobservables with which quantum physics deals. It would be quite consistent to hesitate to assign ontological status to the categorically remote sorts of quantum and field entities invoked by the theoretical physicist and yet to maintain a realist approach more generally. Finding a persuasive philosophical warrant for scientific realism in the face of arguments from the historical instability of theory or from the apparent circularity of arguments relying on the best explanation of the explanatory success of specific theories, is at the heart of the current debate. Hacking, for example, in his Representing and Intervening has argued for a form of realism that does not rely on an appeal to the explanatory virtues of theory (Hacking, 1983). The anti-realist case seems often, indeed, to reduce to a critique of the arguments currently advanced for realism rather than providing a defence for, and a clarification of the practical implications of, anti-realism in its own right. I would argue that paying special attention to the diachronic criteria of theory, that is, to those that track specific theories over the course of time, criteria like fertility, for example, affords the most effective positive argument in support of a qualified form of realism (McMullin, 1996b). But to pursue this would lead too far afield.

9. The social turn

I have left till last what has been perhaps the most spectacular new development in the philosophy of science of the last thirty years: the rapid rise and diversification in, social approaches to the understanding of science (Mendelsohn et al., 1977; Barnes and Edge, 1982; Brown, 1984; McMullin, 1992). This key development has taken two very different forms. In keeping with Kuhn’s directing of attention to the practice of science in the broadest sense, there has been a transformation of the historiography of science to include topics and approaches that would previously have been thought marginal to the pursuit of “real” history of science, that is, to the history of scientific ideas and their validation. Merton and his students had been applying the techniques of sociology to the community of scientists ever since the ‘thirties, treating that community, as Kuhn would later do, as in principle a relatively insulated one. But this reverential attitude was not to last. The combined efforts of historians, sociologists, ethnographers, anthropologists, from the ‘seventies onwards began to present a much more complex picture of the actual practice of science, both contemporary and historical.

The topic of experiment, overly idealized in earlier philosophy of science, came in for particularly intensive and illuminating analysis (Franklin, 1986; Galison, 1987; Gooding, 1989). The different “styles” of different laboratories, for example, seemed to be a topic worthy of the sort of scrutiny that anthropologists have long given different tribal cultures (Traweek, 1988). In consequence of this continuing research, we now have a far fuller grasp of the complex reality of the natural sciences as involving quite different sorts of practices.

But right from the beginning there was another more ambitious project of a rather different character under way under the capacious banner of the “social”. Though it went under the name of sociology, its aims were overtly philosophical in character. How, its proponents asked, are we to understand the nature of “scientific” knowledge itself in the light of this new emphasis on the social aspects of science as a practice and not just as a disembodied set of propositions? The earliest exponents of what they called the “sociology of scientific knowledge” were associated with the University of Edinburgh and their so-called “strong program” was intended, not just to amend, but to replace philosophy of science as it had been practiced from Aristotle’s day up to our own. The traditional focus on the propositional would be replaced with a new and broader concern with the social, in all that elastic term’s many applications.

Bloor and Barnes, when announcing their vision for a new field, SSK, that in their view would be more sociology than philosophy, relied on the claim that social factors, particularly what they called “interests”, social, political, personal, played a significant role at every step in the sciences, notably in the shaping of experimental “data” and in the final stages of theory-assessment (Bloor, 1976; Barnes, 1976). So far, this might not seem so different from the doctrine of the Idols in Bacon’s New Organon, or the notion of “convention” we have seen in the work of Popper and Carnap. Where it diverges is that the proponents of SSK see these social influences as constitutive and as ineliminable, as a necessary part of scientific decision-making, which (they claim) is radically underdetermined from the side of the physical world. Scientific theories are, then, to a significant extent social constructions imposed upon reality. The question of their truth is thus beside the point. The entities they postulate lack a credible claim on reality; they are, in effect, no more than aids in prediction. Here social constructionist versions of anti-realism meet those that derive from historical accounts of theory-change.

Not all of the socially-inspired philosophies of science are so emphatic in their challenge to traditional objectivist commitments. And some, indeed, are more extreme in that regard (e.g. Woolgar, 1988). There is a fair amount of disagreement between the more philosophically-inclined exponents of SSK and the more descriptively-oriented defenders of ethnomethodological approaches. And there is little agreement about how best to respond to the reflexivity challenge (must not the claims of SSK themselves to be taken to be socially-constructed and thus to have, at best, no more than a tenuous hold on truth?) (Ashmore, 1989).

The social-constructionist challenge to the objectivity of scientific judgement faces one question, in particular (McMullin, 1984b). If theory-choice is as heavily influenced by socio-political and other, on the face of it non-epistemic, factors, why should it yield theories that continue to improve dramatically in the crucial matter of accurate prediction? One response has been to reject outright the distinction between epistemic and non-epistemic. Another has been to claim that certain sorts of social factor can also be epistemic, that is, truth-yielding. Some feminist philosophers of science, among them Helen Longino, argue that feminist values can lead to a more holistic approach to such areas as neuro-physiology, an approach that is more likely in the long run to yield good science (Longino, 1990). This is an interesting proposal, one that could in principle be tested. There is obviously a better chance that a philosophical world-view might turn out to be a properly epistemic factor in scientific theory-choice than, say, class-interest or the rivalry between competing research groups.

What is at issue in all this is not whether or not social, political, and personal interests play a role in purportedly cognitive decision-making in science. They obviously do, as case-studies of scientific controversy make clear (Englehardt and Caplan, 1987), and as is in any case evident from even the smallest familiarity with scientific research. Where the disagreement lies between the more subjectivist social accounts and the more traditional philosophies of science is as to whether the role of particular non-epistemic factors tends to be progressively limited by the normal operations of science over the course of time, and whether in consequence it can possibly be correct to claim that long-tested theory is more social construction than a fair representation of real extra-social structures in the natural world.

10. Conclusion

In this all-too-rapid review, I have tried to pick out the themes that have most actively engaged philosophers of science over the course of the last half-century. Inevitably much has gone without mention. I have emphasized the historicist turn of the ‘sixties and ‘seventies. But the pages of the main U.S. journal, Philosophy of Science, or the British Journal for the Philosophy of Science, remind one also of how much has remained the same. Many authors are still struggling with the same logical issues-reduction, probability theory, inductive validation…-as those that preoccupied the philosophers of science of the ‘thirties. Many more are turning to novel issues in the philosophy of the sciences, notably in the areas of evolutionary biology and quantum mechanics. The newest generation of philosophers of science appear to be attracted most to these latter fields, perhaps in part, at least, because the intellectual excitement generated by the historicist turn of nearly forty years ago has to some extent subsided.

Perhaps the most striking development of the last half-century, however, has been the growth of philosophy of science as a professional discipline. The first-ever LMPS Congress, which was held at Stanford University in the U.S. in 1960, was a small affair compared to the LMPS Congresses of more recent years. At the first-ever biennial meeting of the U.S. Philosophy of Science Association in Pittsburgh in 1968, a small meeting-room was more than sufficient for our numbers. Now there are hundreds of academic philosophers of science spread over many countries, and dozens of journals and conference-proceedings devoted to the field. I rather doubt that we have as many towering figures in the field as we had in those extraordinarily productive mid-century decades. But the quantity of really high-quality work is far greater today than before. And one feature of the historicist turn I have been chronicling is the impressive research that has been appearing in case-studies from the history of science as well as in the history of philosophy of science itself, published in consistently appealing new journals: Studies in the History and Philosophy of Science, Perspectives on Science, Science in Context. We understand a field best, whether it be science or the philosophy of science, they are saying by implication, by studying it not just as an atemporal propositional form but also as a living and changing organism.

It is this realization that has been the principal achievement of the tumultuous ‘sixties and ‘seventies. The excesses of those years and the years since are evident. But these should not blind us to the importance of the insights that were then gained, as well as of the issues that were then raised, many of them still only partially resolved. They will carry us well into the new millennium.


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