The philosophy of science is at present in a state of disarray. Numerous epistemic doctrines have been proposed and debated but none, as yet, has won a degree of acceptance comparable to that which positivism achieved. A full examination of the currently competing theories would require a large book in itself, so I must here be selective, and very brief. The theories noted in this section have some features of interest for the social scientist but, for various reasons, must be rejected as inadequate. In section 3 we will consider a theory that seems to me to be more satisfactory as a philosophy of social science, and perhaps defensible also in respect of the natural sciences.

In evaluating these epistemological theories we should keep in mind the basic agenda of the philosophy of science: (1) It should give a reasonably accurate generic account of the methodology that has been practised by sciences that may be considered to have achieved some measure of success in providing rational explanations of empirical phenomena. (2) It should, however, be able to accommodate the conception of scientific knowledge as tentative rather than final; that is, it should not demand that scientific propositions be judged as ‘true’ or ‘false’ in the absolute or dichotomous sense of these terms. (3) It should be able to explicate the relationship between theoretical hypotheses, which are imaginative mental constructs, and empirical data. (4) It should account for scientific progress in terms of the replacement of one explanatory hypothesis by a better one and by improvement in the techniques for obtaining empirical data. (5) It should provide a satisfactory account of the relationship between pure science and its practical applications. (6) It should explain the difference between scientific propositions and other beliefs.

(a) Predictive instrumentalism

We noted above that the Vienna Circle philosophers embraced the view that a scientific theory should only describe observable phenomena and not endeavour to explain them. To ‘explain’ means to assert a causal connection between phenomena and, in the view of the Circle, causality is a ‘metaphysical’ notion that must be rigorously excluded from scientific discourse. Predictive instrumentalism (often simply called ‘instrumentalism’ in the literature) takes the view that theories need not explain, nor indeed even describe, phenomena. All that is required of a theory is that it should be able to predict future events

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in the domain to which it is deemed to apply. According to this view, a theoretical hypothesis is a device for making forecasts. Neither its correspondence to the real world nor its explanatory power has anything necessarily to do with its scientific status. Science must be empirical, but the empirical tests must be applied to the conclusions generated by the theory, not to the premises upon which those conclusions are based. As we noted above, in it is logically possible to generate empirically true conclusions from empirically false premises. For the predictive instrumentalist this is of no concern whatever.

Causality is a difficult concept, still under debate, but most philosophers of science hold that causal explanation is a fundamental task of science. Predictive instrumentalism in effect construes science as a mysterious black box of propositions. They work, but we do not know why they work and we do not need to know. Predicting the onset of bad weather from a pain in one’s toe joint has the same scientific status a priori as the models used by meteorologists. Explaining that toe joint pain frequently precedes bad weather because people who suffer from osteoarthritis may experience such pain owing to a drop in ambient air pressure is totally irrelevant. According to predictive instrumentalism, science does not furnish knowledge about the way of the world, just a set of devices which, shrouded in a mystery which we have no need to penetrate, satisfies our desire to foretell the future. The predictive capacity of a theory is of course an essential consideration in all branches of applied science, but forecasting is intellectually unsatisfactory unless one has rational grounds for expecting the predicted event to occur.

In one of the social sciences - economics - this epistemic doctrine was, for a time, the centrepiece of methodological debate. Milton Friedman, the leading member of the Chicago school of economics, which emphasized empirical research as the foundation of the discipline’s claim to scientific status and the use of sophisticated statistical techniques, published an essay in 1953 entitled ‘The Methodology of Positive Economics’ (Essays in Positive Economics), which became the most widely read, discussed, translated, and reprinted paper on epistemological foundations in the history of economics. Friedman adopted the term ‘positive’ to represent the empirical orientation of what he regarded as scientific economics and to emphasize the distinction between this and the consideration of ‘normative’ issues. He was, apparently, unfamiliar with the philosophical literature and did not intend to state a position derived from the epistemological views of the Vienna Circle or its successors. In fact he advanced a strict predictive instrumentalism, arguing that the sole empirical test of an economic theory is the correctness of its forecasts. The assumptions employed by a theory to generate these forecasts are, he contended, of no account. They need not be supported by empirical evidence; they are necessarily unrealistic and, indeed, the more unrealistic the better. It took a while for economists to identify Friedman’s epistemology as ‘instrumentalist’ rather than ‘positivist’ (See Lawrence A. Boland, ‘A Critique of Friedman’s Critics’, Journal of Economic Literature, 1979), and to recognize its inadequacies, but

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the brief period of enthusiasm for it is now only an historical footnote in the debate over the philosophy of the social sciences.

(b) Conventionalism

This doctrine contends that a scientific theory is, like a descriptive language, a device for ordering and communicating information which works because the members of a community know the rules and obey them. Thus, for example, in a telephone book all names are arranged in order according to the rules of the alphabet. This is purely a matter of convention. Any other ordering system could work equally well if it were generally accepted. The concepts of science, according to this view, are, similarly, only conventions that scientists have created. They are used to order empirical data but they cannot be construed to satisfy the positivist insistence that concepts should be representations of the real world.

This view of science has some merits. It emphasizes that science is a human creation and a social phenomenon, and it focuses on the utility of scientific concepts rather than their brute descriptive realism. But its defects greatly exceed its virtues. Like the contention that empirical observations are ‘theory-laden’, it considers only the nature of concepts, and neglects the role of explanatory hypotheses in scientific investigation. Moreover, according to the conventionalist view, the properties of the real world exercise no control over scientific concepts; they are purely arbitrary constructions, just as the alphabet is. In effect, science is simply the language that scientists have adopted in conversing with one another. Scientific propositions cannot be construed as even tentatively ‘true’. Scientific laws are like legislative laws, decreed by established authorities as normative rules of human behaviour. The philosophy of science undertakes to explain why scientists hold certain beliefs and why they change their beliefs. Conventionalism cannot address these questions satisfactorily.

(c) Rhetorical analysis

This resembles conventionalism in focusing on the language used in scientific discourse, but takes a different and even more extreme tack. Scientific language does not consist of neutral terms that are designed to arrange sense data and communicate information; its fundamental purpose is to persuade. The philosopher of science who truly wishes to understand what scientists do, so goes this argument, must devote his attention to the examination of the techniques of persuasion. He must therefore acquaint himself with ‘rhetoric’, that is, the analysis of the art of persuasive speech that the Greeks initiated centuries ago. Rhetorical analysis has been revived in modern times by disciplines that study speech and other media of communication and has become an important focus of interest in the academic, as well as the more

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immediately practical, aspects of journalism, political science, sociology, and business administration. (For a good discussion of this see the article on ‘Persuasion’ by Irving L. Janis in the International Encyclopedia of the Social Sciences.)

The proposition that rhetorical analysis is an epistemic doctrine and not merely an aspect of social science has recently been strongly argued by Donald N. McCloskey in his book The Rhetoric of Economics (1985). McCloskey develops and illustrates this thesis by reference to the literature of economics, but he makes it plain that he construes it to apply to all disciplines that claim to be objective empirical sciences. In essence, McCloskey contends that the claim is a sham; when one examines the literature closely one finds little empiricism and no objectivity. The typical scientific publication consists of the use of the various devices of rhetoric, such as metaphor, analogy, metonymy, etc., mobilized to persuade the reader to adopt the writer’s personal opinion. According to McCloskey, the methodological examination of scientific publications must take the form of literary criticism, for they are, essentially, exercises in imaginative literature.

This much may be granted: economists, and others, do try to persuade their colleagues, and they do use rhetorical devices in doing so. But this is not all they do. Scientists spend a great deal of time and effort in collecting data by surveys and experiments; they apply complex statistical and other computational procedures; and they take pains to see that their theoretical arguments conform to the canons of logical reasoning. At least sometimes, rhetorical devices such as metaphors and analogies are used by scientists, not simply to persuade, but to clarify and simplify a complex notion or argument in an effort to assist the reader to understand it. If McCloskey were right, all these efforts would have to be regarded as fakery, designed to dull the reader’s critical sense and enable the protagonist to insinuate his own views. The methodology of science would have to be regarded as a sophisticated form of the art of propaganda, which only the trained literary critic could unmask.

Admittedly, scientists sometimes behave in this fashion, especially when issues of public policy are at stake which engage ideological, religious, or other passionately held beliefs. There is bad science, and some of it is deliberate and subtly camouflaged. But scientists, including economists, have succeeded in discovering something about the world that can be construed as objective knowledge. McCloskey gives one no indication of the means by which this knowledge has been acquired. In effect, he contends that the only hard knowledge we have is knowledge of the techniques of persuasion. This, according to him, can be methodically investigated by means of rhetorical theory and the examination of texts, but it is, it would seem, exempt from the flaws it attributes to other disciplines. In effect, rhetorical practice is construed to be a unique empirical phenomenon in that it, and it alone, can be studied objectively! This is, of course, an insupportable contention.

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(d) Phenomenology

This approach to the philosophy of science is mainly associated with Edmund Husserl, a German philosopher who was strongly opposed to positivism, though he shared its view that the task of science is to produce apodictic propositions about the world. The early positivists felt that certainty is guaranteed by a methodology of investigation that relies solely upon empirical data. Phenomenology contends that what we know for certain consists of our internal mental impressions; it is as radical in its subjective view of knowledge as Vienna Circle positivism was in its objectivism. According to phenomenology, knowledge of the external world can be achieved because one can, through intense reflection upon one’s mental impressions, grasp the fundamental nature of worldly phenomena. Positivism restricted itself to the mere appearances of things; phenomenology focuses on their ‘essences’.

Phenomenology reflects a long tradition in philosophy that emphasizes the power of intuition. It has made no impact, so far as I can tell, on the natural sciences, and it is rarely discussed in the literature on the philosophy of science. I note it here mainly because, according to some commentators on the philosophy of social science, the doctrine of ‘methodological individualism’ which contends that social phenomena must be explained in terms of the intentional actions of individual persons, and Max Weber’s methodology of Verstehen, reflect a phenomenological epistemology. This seems to me rather far-fetched. The notion that one may obtain useful information about human behaviour by introspection, and that the social scientist should pay attention to mental entities such as purposes and preferences, is not the same as the claim that apodictic knowledge of the world maybe obtained by intuition and by it alone.

There is, however, a feature of phenomenology that merits more serious consideration. Immanuel Kant made a celebrated distinction between ‘phenomena’ and ‘noumena’, that is, between the information about external things that emerges from the interaction between sensations and our cognitive apparatus, and the things ‘in themselves’. Phenomenology emphasizes this distinction. Sensations do not provide direct knowledge of noumena; they only generate electrical impulses in our nerve fibres, which must be processed by the brain before one has an intelligible perception. What we call ‘empirical information’ is therefore not immediate, but some steps removed from the object it is taken to represent. This is especially so in science, where most empirical data are yielded by indirect observational procedures. For example, the physician who is looking at an X-ray plate is not perceiving a fractured bone. Photons impact upon the retinas of his eyes, generating electrical impulses in nerve fibres which are delivered to certain centres of his brain, where, together with stored information from previous experience, they create his mental impression of a fractured bone. The import of this is that it is naive to treat empirical data as unproblematic equivalents of real things. This does not mean

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that empiricism must be abandoned, as phenomenologists claim; it calls rather for an appraisal of the role that empirical ‘facts’ play in scientific inquiry which is more sophisticated than the notion that facts sit in judgement on theoretical hypotheses. We shall return to this point below.

(e) Evolutionary epistemology

Some philosophers take the view that epistemology is a ‘meta-science’, that is, the object of its investigation is science, but it is not itself an empirical science on the same plane as physics, biology, economics, etc. The propositions of epistemology refer to empirical phenomena, but they lie on a different plane of discourse, which constitutes a higher level of abstraction than that of the sciences. Others reject this view, contending that the task of epistemology is to explain science and its development in the same way that scientists explain other phenomena. Philosophers must descend from their transcendent height and give a ‘naturalistic’ account of science. We now go on to examine four theories that adopt this stance, starting with the notion that the development of science can be explained in terms of the operation of a mechanism analogous to Darwin’s theory of natural selection.

Herbert Spencer, as we noted above (Chapter 15 A 4) held the view that evolution is not merely the process by which the earth has been populated by a medley of organic species; it is a cosmic principle that pervades the whole realm of existence. Following this metaphysical conception, we ought to be able to account for the development of scientific knowledge, like all other phenomena, in terms of the operation of the laws of evolution. Spencer suggested such a notion, but it was more explicitly advanced by Georg Simmel, one of the founders of German sociology, in a paper published in 1895 (‘On a Relationship between the Theory of Selection and Epistemology’, reprinted in H. C. Plotkin, ed., Learning Development, and Culture: Essays in Evolutionary Epistemology, 1982). According to Simmel, organisms use ‘concepts’ in dealing with the problems they confront and ‘a true concept for an animal is that which makes it behave in a way most fitting its circumstances’. In the process of selecting among variations in organic structures, including the organs of ‘knowing,’ the mechanism of evolution selects progressively more efficient ‘psychogenic concepts’. The survival of the fittest organisms means also the survival of the most ‘life-promoting’ concepts. Man’s knowledge, according to Simmel, results from this selection process. Accordingly, the relation between the truth of man’s knowledge and its practical utility is that ‘knowing is not first true and then useful, rather it is first useful and then referred to as true’.

Karl Popper espoused an evolutionary view in his theory of the development of knowledge, but shifted the focus significantly, construing human knowledge as growing by means of cultural, not organic, evolution. According to Popper, the entities that compete for survival, at least in civilized societies, are not

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people but scientific theories. When a conflict of beliefs is decided by physical combat, there is no guarantee that the victors entertain beliefs that are more objectively true than those of the vanquished but, in Popper’s view, progressive growth in objective knowledge is assured if the beliefs themselves compete in a contest of verisimilitude where nature is the judge.

There are numerous variants on the theme of evolutionary epistemology (see Michael Bradie, ‘Assessing Evolutionary Epistemology’, Biology and Philosophy, 1986). Some follow Simmel in treating the philosophy of science as a branch of biology, that is, ‘sociobiology’. Others maintain, as Popper does, that epistemology is an autonomous discipline and contend that the evolutionary process at work in the development of science is not literally Darwinian, but only analogous to it. Stephen E. Toulmin does not advocate the reduction of the philosophy of science to biology, but he maintains that a Darwinian theory of the development of science is not merely a suggestive metaphor or analogy, but provides an explanation of the phenomenon (‘The Evolutionary Development of Natural Science’, American Scientist, 1967; Toulmin maintains the same view in his Human Understanding, 1972). Michael Ruse, on the other hand, is a strong supporter of the sociobiological research programme in general and, in respect of epistemology, he claims that the Darwinian mechanism solves such fundamental problems as the nature of induction and causality, but he regards evolutionary epistemology as proceeding by analogical argument and points out important respects in which the theory of organic evolution by natural selection fails to have counterparts in the evolution of science (Taking Darwin Seriously: a Naturalistic Approach to Philosophy, 1986). I note Toulmin and Ruse here in order to illustrate briefly the wide variety of views held by advocates of evolutionary biology. The matter is still under debate and no systematic doctrine has so far emerged as the consentient view.

Nevertheless, it is not premature to note that the basic approach of evolutionary epistemology has defects which would seem to render it ineligible for general acceptance. The most conspicuous of these is that it treats the notion of ‘progress’ as inapplicable to the history of science or, if it is, as equivalent to survival. Even Darwin pointed out that the survival of an organism is merely indicative of its adaptation to the environment, not a certificate of merit. In the domain of ideas one perhaps has little reason to be more sanguine. Astrology, for example, has not been driven from the field of competition. It flourishes, along with belief in magic, folklore medicine, and a score of old and new mysticisms, even on university campuses in ‘enlightened’ societies. For a quarter of a century in the Soviet Union, belief in the Lamarckian theory of inheritance had much more survival value than Mendelian genetics, yet one would hardly say that it constituted a step in the progress of scientific knowledge. In the domain of economics, neoclassical theory demonstrates that competition generates progress - in certain limited respects and under certain specific conditions. But evolutionary epistemologists have advanced no comparable theory to sustain their contentions. They have a naive faith in

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competition, assuming that, whatever the conditions, the surviving beliefs are better than the failing ones.

Some evolutionary epistemologists reject the notion that beliefs can be compared in such terms, contending that all we can say about surviving beliefs is that they have survived. This is either an empty truism or makes evolutionary epistemology into a biologicized version of the epistemological theory examined above under the heading of ‘conventionalism’. Karl Popper avoided this by insisting that a scientific belief about the way of the world must be compatible with empirical data. It is not a question of the popularity of a belief, or its acceptability to established authorities; it is the warrant one has for holding it that distinguishes science from non-science. Evolutionary epistemology does not seem capable of addressing the issue of the warrantability of belief. It either construes survival as equivalent to progress, or it contends that the notion of progress is inapplicable to our knowledge of the world. Nevertheless, the emphasis of evolutionary epistemology on the competition of ideas is salutary. Though not an adequate epistemology, it calls attention to another important, but quite different, subject, the social organization of scientific research.

(f) Kuhn’s paradigm model

One of the notable features of evolutionary epistemology is that, when viewed in terms of cultural rather than biological evolution, it directs attention to the fact that science is a social enterprise. In recent years, historians and philosophers of science have paid increased and growing attention to the social context of science, a field previously cultivated only by a few sociologists. (A pioneering scholar in this field was Robert K. Merton; a collection of his papers has been reprinted as The Sociology of Science: Theoretical and Empirical Investigations, 1973.) This line of thought was greatly stimulated by Thomas S. Kuhn’s The Structure of Scientific Revolutions (1962), which, interestingly, and perhaps ironically, was published as a volume in the ‘International Encyclopedia of Unified Science’ series, which Otto Neurath had initiated in order to promote the positivist philosophy. During the past twenty years or so no theory of the nature of science has received more attention than Kuhn’s, by natural and social scientists as well as by professional historians and philosophers of science.

Kuhn takes the view that the philosophy of science must be empirical, drawing its conclusions from an examination of the historical record of science. One must also pay attention to the fact that scientists working in a particular field constitute a cultural community whose members, like those of other social groups, share certain enculturated ideas, since the fate of any new scientific theory depends critically upon the response of the established peer group of scientists. Kuhn’s Structure was a bold attempt to unite the history of science, the philosophy of science, and the sociology of science into a comprehensive theory of scientific development. It is comparable in its aim to Comte’s ‘law of

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the three stages’ as a theory of mental evolution, and Marx’s ‘dialectical’ view of historical change.

Kuhn’s basic thesis is that the history of any science reveals two alternating phases, a period of ‘normal science’ and a period of ‘revolution’. During the first of these scientists proceed with their work within the frame of the established basic conceptions or ‘paradigm’ of the peer group. But, as scientific investigation proceeds, bits of empirical information come forward that are not consistent with the accepted paradigm. Initially, scientists do not worry about such apparent falsifications of the basic conceptual framework with which they are working, but as the ‘anomalies’ accumulate the established paradigm becomes increasingly untenable. Eventually, it is cast out by a ‘revolution’ in scientific thinking, a new paradigm is adopted, and the ‘normal’ work of science resumes. Though Kuhn does not note the point, his theory closely resembles Karl Marx’s thesis that each stage in man’s socioeconomic history is characterized by the accumulation of endogenously generated ‘contradictions’ which, eventually, can no longer be contained, and the ‘social integument’ ‘bursts asunder’ in a revolutionary transformation.

Kuhn’s scenario of scientific development is appealing, especially since we have become accustomed to identifying certain prominent events in the history of science as ‘revolutionary’. The literature freely refers to the ‘Copernican revolution’, the ‘Einsteinian revolution’, the ‘Keynesian revolution’, and so on. But this locution, though sometimes convenient, raises more problems than it solves. For example, the reader of I. Bernard Cohen’s recent book, Revolution in Science (1985) is introduced to so many revolutions identified by the author that there would seem to be hardly any domain left for ‘normal science’ to occupy. Kuhn himself, in a postscript to the second edition of Structure (1970), accommodated his critics by loosening his notion of revolution to such an extent that it cannot serve effectively as a differentiating concept. Historians of science have on the whole been very critical of the empirical value of Kuhn’s central notions of paradigm and revolution, and are disinclined to accept his model as a satisfactory depiction of the actual history of science. In effect, Kuhn was attempting to state a universal ‘law of history’, and his thesis, like other similar general propositions about history, is more speculative than empirical. Philosophers of science have been equally critical of Kuhn (see, for example, Stephen Toulmin, Human Understanding, 1982, pp. 98-130; Israel Scheffler, Science and Subjectivity, 1982; and Ian Hacking, Representing and Intervening, 1983).

In the initial formulation of his thesis Kuhn construed the paradigm of a science to be a primary metaphysical postulate. It is the ontological conception shared by the peer group of established scientists which guides their work. A paradigm shift is like a mass religious conversion; the scientists, so to say, are born again and look at the world through new eyes. Different paradigms are incommensurable. There are no general criteria that can be used to determine whether one paradigm is better than another and, therefore, there can be no

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question of progress in scientific knowledge, or indeed of differentiating scientific from non-scientific propositions. Kuhn’s argument, like evolutionary epistemology, is really an extension of conventionalism. Good science is simply that which is in accord with the paradigm convention of the peer group; when that convention changes, it becomes bad science.

Kuhn, apparently, did not anticipate the storm of protest that this brought down upon him from philosophers, who pointed out that his conception would deprive science of any claim to be an empirically controlled method of objective inquiry, or even one that is rational. In subsequent statements Kuhn significantly modified his original position, saying that he did not intend to argue that a scientific paradigm is such an autonomous ontological conception that it is totally immune from empirical and other tests of the sort that scientists routinely apply to lesser propositions. Paradigms are not absolutely incommensurable and the usual epistemic criteria of theory choice (such as degree of observable verisimilitude, scope, simplicity, fruitfulness, etc.) come into play in persuading scientists to shift from one paradigm to another. With such admissions, however, Kuhn’s theory of science falls to the ground. A ‘paradigm’ becomes merely a theoretical hypothesis, perhaps one that is more central to a field of science than others, but not differing from them in any fundamental way. A ‘revolution’ in science becomes simply a period of exceptionally rapid advance, initiated by discoveries that prove to be unusually fruitful in the investigation of old problems or in opening up new lines of scientific inquiry.

The extraordinary enthusiasm that some social scientists have shown for Kuhn’s model partly reflects the power of language. For a decade or so it was avant-garde to talk in terms of ‘paradigms’ and ‘revolutions’. But there is more to it than that: first, though Kuhn did not succeed in sustaining his ontological view of paradigmatic propositions, there are, in some fields of science, certain ‘core’ propositions that are more important to the whole field than others, and scientists are loath to abandon them when there is contradicting evidence. In economics, for example, the conception of consumers and producers as rational agents has been maintained despite conflicting empirical experience and the psychological theories of Freud and others which deal with the non-rational substrate of human mentation. Secondly, while Kuhn did not do anything that can properly be described as sociological analysis, he did call attention to the social nature of science, and especially to the role of peer groups as established authorities. The first of these issues was addressed by Imre Lakatos in advancing his ‘methodology of scientific research programmes’ (MSRP); the second by the Edinburgh school’s ‘strong programme in the sociology of science’.

(g) Lakatos’s methodology of scientific research programmes

By the late 1960’s a great deal of the debate on the philosophy of science had come to focus on the difference between Kuhn’s approach and Karl Popper’s

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revision of positivism. Imre Lakatos, whose earlier work on the philosophical foundations of mathematics was highly regarded, entered this debate with the intention of combating Kuhn and supporting Popper. I mention this point because the reader of this literature will find that, though Lakatos’s theory resembles Kuhn’s much more than it does Popper’s, he expresses his opposition to Kuhn in strong, sometimes indeed abusive, terms, and is by contrast civil and even deferential to Popper. Lakatos died young, without developing a book-length treatment of his philosophy of science. His MSRP approach is contained in a few papers published between 1968 and 1971.

Lakatos defends Popper against the charge of ‘naive falsificationism’, that is, the notion that a theoretical hypothesis is immediately shown to be false if there is any evidence that is inconsistent with it. He makes two main points in this connection: first, that specific scientific hypotheses are part of a general complex or ‘series’ of theories which together constitute a coherent ‘research programme’; and secondly, that such a programme is not abandoned when specific empirical anomalies are disclosed unless another, superior, programme is available. Popper is correct in stressing that empirical evidence can only falsify a theory, not verify it, but science, says Lakatos, progresses by means of ‘sophisticated falsification’, which focuses on the comparative evaluation of whole research programmes. (‘Falsification and Methodology of Scientific Research Programs’, Imre Lakatos and Alan Musgrave, eds, Criticism and the Growth of Knowledge, 1970). So far, Lakatos’s epistemic theory appears to be equivalent to Kuhn’s in substance, if not in terminology. The difference between them appears when one examines his explication of the notion of a ‘research programme’.

According to Lakatos, every scientific research programme has a ‘hard core’, a set of propositions that are immune from empirical test because it is surrounded by a ‘protective belt’ of assumptions, conditions, etc., which can be invoked to deflect the impact of any contradictory evidence. Outside the hard core lie theoretical hypotheses that can be tested, and abandoned if the evidence so indicates, without calling the hard core of the programme into question. Some commentators interpret Lakatos’s ‘hard core’ as equivalent to Kuhn’s ‘paradigm’, that is, an ontological postulate. But Lakatos rejects the notion that it consists of such metaphysical-level assumptions. For example, he identifies the hard core of the Newtonian programme as Newton’s three laws of motion and his principle of universal gravitation. Even with such an example, however, it is not easy to understand what Lakatos means by the hard core of a programme, and to apply the notion to other fields of science. It is more definite than Kuhn’s paradigm, but not a great deal more. Nevertheless, one may agree that in every science there are some propositions that play a more fundamental role than others, and that the scientists working in the field are more inclined to employ stratagems that save them when contradictory evidence appears than to abandon them forthwith.

The history of science, says Lakatos, shows that scientific knowledge

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progresses, most notably when one research programme is replaced by another. This is not, as Kuhn implied, a ‘mystical conversion’ to a new ontology, but results from a rational appraisal of the relative capacities of the two programmes as general frameworks of scientific inquiry. A new programme will be adopted when it is shown that it can explain everything that the previous programme could, and more besides. With the adoption of a new programme, not only are many of the empirical anomalies of the old one eliminated but a ‘problem-shift’ often occurs, that is, new areas of inquiry are opened that were hitherto unrecognized by scientists or beyond their reach. The history of science is basically an account of how research programmes gradually ‘degenerate’ and finally give way to ‘progressive’ ones. In Kuhn’s view, says Lakatos, the choice between competing paradigms is a matter of ‘mob psychology’, while in his own epistemic theory the preference of scientists for one programme over another is rational. Lakatos, in effect, postulates that the scientist has what economists call a ‘utility function’, in which his scientific goals are the arguments. His behaviour in choosing between programmes is rational action to maximize this function, subject to the constraints which are imposed on it by the state of development of his science (see Richard J. Hall, ‘Can we use the History of Science to Decide between Competing Methodologies?’ in Roger C. Buck and Robert S. Cohen, eds, Boston Studies in the Philosophy of Science, VII, 1971). In Lakatos’s view we should not regard scientists who in former times held theories now discarded as irrational or even misguided. The adherents of the phlogiston theory of combustion, for example, were as sensible as modern scientists are; they chose the best research programme that was available to them at the time (Lakatos, ‘History of Science and its Rational Reconstructions’, ibid.). This is, in my view, a significant point of merit in Lakatos’s epistemic stance. The MSRP model allows the possibility of gaining knowledge by using theories that are subsequently regarded as, in the absolute sense, false. The history of science is largely a record of progress made with such ‘false’ theories. If one takes the view that a theory is either categorically true or false it is impossible to explain how progress can have occurred. But Lakatos’s epistemic model does not explain it, either, it only allows that it is possible.

We might pursue this issue a bit further, since it reveals a serious weakness, not only in Lakatos’s MSRP but in all epistemological theories that claim to be empirical in the same way that physics, biology, and the other scientific disciplines are. According to this conception the empirical data that can be used to test an epistemological theory are provided by the history of science. Such a contention rests upon a false analogy: that these historical data are homologous to the data the scientist obtains by observation of the real world. This is clearly incorrect. The real world provides the chemist, say, with data about the process of combustion; the history of chemistry provides data about theories of combustion. It is indeed a fact that Joseph Priestley believed combustion to be a process in which a substance, ‘phlogiston’, is given off by the burning material. But his belief was wrong; the existence of phlogiston is a

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non-fact. The history of science is largely a record of erroneous theories. The non-facts postulated by erroneous theories cannot serve to test an epistemic proposition empirically, any more than erroneous laboratory observations can test a scientific proposition. Unlike the scientist, the philosopher has no reliable data. If indeed he did have access to ‘correct’ data, he would have no work to do but record them. There would be no problem for him to address. The problem he does address has to do, not with the beliefs of scientists, but with the warrantability of their beliefs. The philosophy of science is a normative enterprise, not an empirical one.

Lakatos’s MSRP has not survived criticism better than Kuhn’s paradigm model of science. Like most philosophers of science, Lakatos seems to have physics exclusively in mind when speaking of ‘science’. Other natural sciences cannot as easily be accommodated to the Procrustean bed of the MSRP. In the social sciences only economics appears to offer the possibility of an easy fit, and there have been a number of efforts to reconstruct the history of economics in Lakatosian terms, but they have not been convincing (see Douglas W. Hands, ‘Second Thoughts on Lakatos’, History of Political Economy, 1985). This does not mean, as some have strongly argued, that the philosophy of social science must be fundamentally different from that of the natural sciences; its import is that, as a model for the history of science, the Lakatosian MSRP fails to meet the empirical test of general applicability.

Philosophers too have found the MSRP wanting. Lakatos observes that scientists do make comparative evaluations of alternative research programmes, and he insists that these are based on ‘rational’ considerations, but he fails to elucidate the criteria that are employed. The justification of programme choice is not addressed. Like Kuhn, Lakatos attempts to deduce the methodology of science from empirical evidence offered by the history of science instead of evaluating scientific practice in terms of normative philosophic principles. If the MSRP is a law of scientific development it is, at best, an empirical generalization, an example of the ‘inductivism’ that Lakatos himself rejects. We may take it for granted that science is an effective cognitive enterprise. The MSRP undertakes to describe how science works, but it fails to provide an explanation of why it works. Responding to his critics at a symposium on the MSRP (‘Replies to Critics’, in Buck and Cohen, eds, Boston Studies), Lakatos admitted that some normative epistemic principle is required to save his theory from degenerating into inductivism on the one hand or conventionalism on the other. In defending his theory, however, he shifted ground significantly:

My critics... seem to have missed my thoroughgoing methodological instrumentalism. In my view all hard cores of scientific research programs are likely to be false and therefore serve only as powerful imaginative devices to increase our knowledge of the universe. This brand of instrumentalism is consistent with realism…’ (Lakatos’s emphasis)

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This remark, however, points to a different line of epistemological theory, which has little resemblance to the MSRP model.

(h) The ‘strong programme’ in the sociology of science

When Lakatos speaks of abandoning one research programme for another on the basis of an evaluation of their relative merits he assumes that the factors entering into the ‘rational’ choice between them are only those that are relevant to the goal of obtaining objective knowledge of the world. He rejects the notion that external factors such as the political, social, or economic environment have anything to do with the fate of particular scientific theories or the choice of general research programmes. The ‘externalist thesis’, which argues the contrary - that such factors do indeed play a significant role in science - has a long history, especially with respect to the social sciences. The ‘Edinburgh school’, whose leading figures are David Bloor and Barry Barnes, carry it a giant step further. They take the stance that all scientists are dominated by their cultural ambience in all aspects of their work and thought; it determines not only their choices of problems to investigate, but their so-called philosophical conception of the nature of science and the criteria of warrantability that they use in evaluating beliefs. All beliefs, according to this view, are epistemically ‘symmetrical’, whether they are beliefs about observable phenomena, or beliefs about philosophical principles, or beliefs about the efficacy of witchcraft or the power of deities. Science, and the philosophy of science, which are just sets of beliefs like any other, should be deprived of their pretensions to rational detachment and construed purely as empirical social phenomena. Some evolutionary epistemologists wish to make the philosophy of science a branch of biology; the Edinburgh school argues that it is properly a branch of sociology, which they describe as the ‘strong programme’ in the sociology of science. (The central theses of the strong programme were first clearly formulated by David Bloor in his Knowledge and Social Imagery, 1976. For a good discussion of the programme the reader is referred to a series of papers on it in Philosophy of the Social Sciences, 1981. Chapters 7 and 8 of Paul A. Roth, Meaning and Method in the Social Sciences, 1987, also contain a good exposition and critique.)

The strong programme view of science has some close affinities to two notions we have aleady encountered: the argument advanced by Russell Hanson and others that science cannot be objective because empirical observations are ‘theory-laden’ (see the discussion above of the version of this that construes observations as laden with ‘culture-specific ontologies’); and W. V. O. Quine’s ‘underdetermination thesis’, which contends that, even if objective empirical observations could be made, ambiguity concerning their causes would persist because it is always possible to postulate more than one theory to account for observed phenomena. We have already considered the reasons why these are not compelling arguments against scientific objectivity and need not repeat the considerations here, but it is worth taking a moment to

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note the inference that the advocates of the strong programme draw from the underdetermination thesis.

If observation facts do not enable us to choose between alternative theories, how do we choose? The strong programme contends that the choices of scientists in this ubiquitous state of affairs are determined by sociological factors. Critics of the programme point out that this is itself a theoretical hypothesis, not a hard fact (see Larry Laudan, ‘The Pseudo-science of Science?’ Philosophy of the Social Sciences, 1981). There are other criteria of theory choice, such as simplicity, scope, practical applicability, etc. The defender of the strong programme might reply that all these criteria are no more than social conventions that scientists have been enculturated to accept, but this reduces the programme to little more than the assertion, which no one would want to quarrel with, that scientists are human beings who belong to a social community. It does not demonstrate that the Newtonian theory of the planetary system is merely a social convention of Western-educated astronomers. As Laudan points out, the contention that beliefs have causes does not mean that all beliefs have the same causes, much less that ‘social factors’ are the only causes that operate in the domain of human mentation.

David Bloor refers to case studies conducted by adherents of the strong programme, citing one that, according to him, conclusively showed that Pasteur’s famous experiment demonstrating that life forms could not arise from non-living matter was accepted by the scientific establishment because it harmonized with the political and social conditions and the theological beliefs of nineteenth-century France (‘The Strengths of the Strong Programme’, ibid.). He does not note that scientists in other countries then, and since, have accepted Pasteur’s theory, and does not consider that they have done so because they regard the empirical evidence as warranting its acceptance as a true proposition about the world. Reference to external reality does not enter the ambit of the strong programme. According to Barry Barnes, some ‘over-enthusiastic’ devotees of it may have given the impression ‘that reality has nothing to do with what is socially constructed’ but, nevertheless, he comes within a hair’s breadth of this contention himself: the notion of ‘truth’, he declares, is like ‘good’ - ‘an institutionalized label used in sifting belief or action according to socially established criteria’ (Scientific Knowledge and Sociological Theory, 1974, pp. vii, 22; Barnes’s emphasis).

As epistemology the strong programme fails, but we might note before we leave it that it does not stand up well as sociology, either. The assertion that undefined ‘social factors’ account for our scientific beliefs is not a sociological theory. These factors must be specified, and the way in which they operate must be indicated, in order to make even a beginning at the construction of a sociological theory of science. The adherents of the strong programme do not do this. When pressed, they resort to the ‘interests’ of scientists, thus throwing the issue into the domain of the economist. In principle, the analytical apparatus of microeconomic theory could be applied to this matter, since

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scientists may be construed as making choices between alternative theories on the basis of their ‘utility functions’, just as consumers are construed as choosing what commodities to buy in order to maximize their satisfaction. Recently, economists have devoted some attention to the ‘knowledge industries’, but have not attempted to argue that this line of investigation can replace the philosophy of science. Lawrence A. Boland has, indeed, convincingly shown that there are technical reasons why the economic analysis of rational choice cannot be extended to provide an acceptable account of theory choice by scientists (‘Methodology as an Exercise in Economic Analysis’, Philosophy of Science, 1971). One may glibly say that scientists, like other humans, are motivated by their ‘interests’, but translating this into an epistemological theory, as the Edinburgh school seeks to do, does not appear to offer much prospect of success.

The sociology of science is an important subject, especially in a world where science has become professionalized and so much scientific work is conducted within the administrative and policy framework of social institutions such as business firms and governmental agencies, and where university science must be financed by grants derived from public funds and foundations. But the sociology of science is not the philosophy of science, and unsupported sociological assertions will not assist us to understand the place of science in the modern world.

We have now almost finished our survey of the epistemological theories that have emerged as successors to positivism. Since none of them appears to be a winning candidate, the philosophy of science is said to be ‘in crisis’, a state of affairs that does not seem to concern scientists, who pursue their craft with undiminished enthusiasm and confidence. Some commentators on the current state of epistemology suggest that, since no epistemological theory has won general acceptance, we should adopt a ‘pluralist’ stance (e.g. Bruce Caldwell, Beyond Positivism: Economic Methodology in the Twentieth Century, 1982, chapter 13, and Paul A. Roth, Meaning and Method in the Social Sciences: the Case for Methodological Pluralism, 1987). But it is not clear what this means. Is a particular science, such as economics, to be epistemically construed as being a compound of predictive instrumentalism, Lakatosian MSRP, and other items from our smorgasbord? Or is one science to be regarded as wholly Kuhnian and another wholly conventionalist? Paul Feyerabend advocates the ultimate pluralism: since no epistemological theory is acceptable, then all methods of obtaining knowledge that human ingenuity can imagine are equally meritorious, and none should be condemned as invalid; philosophers of science should shut up shop and seek other, more productive, occupations (Against Method Outline of an Anarchistic Theory of Knowledge, 1975). This distressing counsel is unlikely to be heeded, and it need not be. The so-called ‘crisis’ in epistemology is greatly overblown; it stems from the original positivist notion that scientific theories must be demonstrated to be ‘true’ in the sense of

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isomorphic correspondence to reality, and the reactions against this which, in effect, declare that science is simply what scientists do, and truth is what scientists believe, without any reference to the rationality of their actions and the warrantability of their beliefs. It is not necessary to adopt either of these positions. Scientists themselves do not, nor do the standard textbooks that are used in university courses to introduce students to the nature of modern science. The dominant view one finds at these levels is that scientific theories are instruments of inquiry which are employed in the discovery of truth, not true or false in themselves. The controversy between the ‘instrumentalist’ and ‘realist’ view of theories is an old one. ‘It is a matter of historical record,’ says Ernest Nagel:

that, while many distinguished figures in both science and philosophy have adopted as uniquely adequate the characterization of theories as true or false statements, a no less distinguished group of other scientists and philosophers has made a similar claim for the description of theories as instruments of inquiry. (The Structure of Science, 1961, p. 141)

This controversy is not merely semantic, as Nagel believes. It revolves around the central issue of how we can be said to ‘know’ something about the world when our theories are incomplete and provisional and, moreover, will most likely be shown in the future to be false. This issue is important for all the sciences, but especially so for the social sciences, which deal with a world that is itself in flux. We go on now to examine the epistemology of instrumentalism or, in order to distinguish it from the ‘predictive instrumentalism’ discussed above, ‘cognitive instrumentalism’.

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