Abstract: A series of confusions, setting in around the time of Imre Lakatos and Thomas Kuhn, has caused philosophers to think that history is evidence for testing methodology. This confusion has continued in the work of Larry Laudan, Ronald Giere, and Philip Kitcher (The Advancement Of Science)

   The works of some methodologists display no confusion. J.S.Mill, for example, was explicitly a descriptive methodologist. He developed his system not only by reading the work of other philosophers, but also by careful study of what physicists had done, in investigations regarded by the current consensus of physicists as rational. But once he had completed his system, the historical behaviour was used as illustrations of the proposed methods, rather than as evidence for them.  The idea that the examples of actual behaviour of past working physicists not only instantiated say, Bacon-Herschel-Mill's methods of Similarity, Difference, and Concomitant Variation, but also tested whether they were correct, would have been regarded as an odd reversal of the intended situation.  Physicists doubtless did all kinds of things, some rational, some not - it did not matter. The methods proposed in Mill's System of Logic summarised the current best practice, whatever physicists had done in the past.

   Karl Popper was always clear on the role of history for methodology.  He warned Lakatos not to lose sight of the purpose of methodology, which is the 'Logic Of Scientific Discovery', in a welter of historical detail.

   Present confusion, if it exists, has arisen perhaps because some philosophers, such as Imre Lakatos, blocked by insoluble specialist methodological difficulties, abandoned descriptive methodology. This was particularly if, unlike Mill:
(i) they were complete-justification methodologists
(ii) they were focussed methodologists, persistently tackling the one situation in which methods are exceptionally difficult to justify - high-level theory-choice.
   Lakatos proposed, for high-level theory-choice, methods M - which had been widely agreed by physicists for at least a century. He showed that physicists had incomplete justification for M; but this lack of an indubitable justification was also widely agreed. So far, so good.
   As a descriptive methodologist, he could have then worked on the justification of M; or he could have continued to devise the rest of a descriptive methodological system. He did neither of these things. He felt that M must be better justified, though he could not see how. And he felt that his chosen situation was the only one of interest. So he was stuck. What should he do next?  He ignored Popper's warning, and the confusion arose.
   He began to do quite detailed historical investigation, intending, it seems, to prove that real physicists, in real situations, had been primarily motivated in their decisions by M.  If (a) these episodes were agreed by everyone, or by the consensus of current physicists, to display typically rational actions and if (b) the physicists involved historically were primarily, or solely, motivated by M, then he thought that everyone would have to agree that M were typically rational, whether they could justify them any better, or not.
   But this historical research was pointless and doomed: 'pointless' because, on the one hand, M were accepted as typically rational by current physicists already; finding further labelled illustrations of their use in history was irrelevant.  On the other hand, critical philosophers, such as complete-justification methodologists, were hardly going to be persuaded by historical episodes. 'Doomed', because no complete historical episode can ever be conclusively labelled as internal, only certain strands in it; real historical behaviour is the result of many interacting causal factors, only some of which are internal - and deciding which is primary is impossible; there may well be no historical episode in which M are uniquely visible as the causal factor, because in fact M underdetermine the decision.
   Lakatos' M had not thereby failed some kind of valid historical test; they passed the only indirect test that aspects of such episodes can provide - that some causal threads in the physicist's behaviour, which accord with M , are labelled 'rational' by current physics consensus - or by its ghostly counterpart, intuition. The historical episodes had no further relevance to his methodology.
   Ironically he overestimated the rationality of episodes which may well have displayed the use of his methods, but only as one causal strand amongst many. It is infamously impossible to locate one factor as decisive in historical episodes. Thus his claim that his factors would be decisive was inevitably - gleefully - disproved by historians.
   He had taken a wrong turning. If he could identify some methods that were rational to use in a certain abstracted situation, and if current physicists agreed that these were rational methods, and if he could find historical cases which the physicists intuitively agreed displayed, amongst other things, the influence of this factor - operating more as an illustration than as evidence, than that was sufficient. He did not need to try to prove that the factors were, in historical fact, decisive - and indeed they may not have been. This would have been the project neither of descriptive nor normative methodology; it would have been the attempt to prove that physicists were, in these historical situations, acting internally. This has nothing to do with the descriptive or normative methodology; it is a question in the area of history, or perhaps of the assessment of activities for the purpose of demarcation.
   His resort to rational reconstructions was understandably regarded by historians with bemusement, though they were a sensible attempt to back-track, viewing historical episodes - as they should be - as just blurred illustrations of methodological principles. They are altering history to give versions of how it might have looked if the physicists involved had only taken internal factors into account in their behaviour. This is potentially interesting to methodologists and to historians; for example, they can be used to identify internally underdetermined decisions, which could not have been made, without an input from an external factor. With clarity of purpose, they can be revived.
   Lakatos had reduced justification for his methods to footnotes, almost to invisibility.  But his attempt to obtain respectability for them through history was doomed.  Thus his useful re-identification of Duhem's unit of assessment (the research programme) and the two factors (progress and degeneration by novel fact prediction and ad hoc adjustment) widely currently regarded by physicists as rational, - rightly or wrongly, as the normative methodologist would say - became lost in confusion.
   The more detailed his history became, and the more historians objected to his still over-simplified hijacking of history for partisan ends, the clearer became the full tangle of causal threads influencing behaviour, and required to explain it; but by this stage the mistaken idea of using the full complexity of historical episodes as some kind of vital evidence for methodology had been planted in some philosophers' minds - and the mistaken idea that history had a vital rôle in methodology in some historian's minds.

   The work of Kuhn compounded the confusion, mixing fragments of methodology (such as the justification of normal science, already understood in, for example, Popper's work) with sections of history presented as evidence.
   We omit reference to incommensurability, the most exciting aspect of Kuhn's work, since he later abandoned it (as did Feyerabend).
(i) He presented historical data that some physicists, some of the time, seemed to settle into routine work, puzzle-solving, on the assumption that various grand theories (paradigms) were not to be questioned (normal science), even when experiments seemed to give results in conflict with them, or when there were inconsistencies in the theories. At other times there were revolutions in which one of the grand theories was changed.
   He proposed, see below, that he was not just suggesting that because this happened, it should happen.  He implied that it was a justified method, and one not widely recognised.
Methodologists recognised aspects of Lakatos' methods in Kuhn's work; Lakatos' methods made some strands of behaviour in 'normal science' situations rational which were not rational on some interpretations of Popper's methodology.  Since Popper later made clear that he saw the value of normal science, this is now of little interest.
(ii) Kuhn also insisted that important physical decisions were often underdetermined by rational methods, and made on grounds involving other factors, for example of a social kind.
   Popper, Lakatos, and other philosophers, whatever impression they may have given, never thought that they were 'giving a complete account of historical physics'.  We doubt if they would have valued this task at all, or considered it as feasible.  They realised that historical physics behaviour was by no means entirely rational.  They realised that the rational strand, as a causal factor in historical decisions, was only one among many; Lakatos, at least, also realised that the internal factors did not, even ceteris paribus, fully determine behaviour - other factors were not only accidentally present in decisions, but also necessary for them. The detailed historical behaviour of physicists, combining their behaviour qua internal investigator with their behaviour qua normal member of society, was not interesting or relevant to the methodologist. This extent of agreement explains the feeling, repeatedly referred to in Criticism And The Growth Of Knowledge, that the arguments were at cross-purposes.
   Popper and Lakatos, as methodologists, may have said that their aim was to give an account of physics, but what they were actually aiming to do was to give an account of just those strands of reasoning, just those causal factors, which are justifiable. Kuhn, we think, shared this aim; he did not want to describe the whole sweep of scientific history - he wanted "a philosophy of science" (p.207).  Kuhn, in the 1969 Postscript, accepts that a weakness in his 1962 essay is that he pays so little attention to traditional internal factors - not mentioning that, by so doing, he greatly increased the dramatic quality of the original essay.  He accepts that there are factors in theory choice - the agreed battle-ground situation - such as whether a theory makes quantitative, precise, predictions, which turn out to be accurate, whether it is simple, whether it is self-consistent, and whether it is consistent with other accepted theories. However, he pays little attention to them. Kuhn insists that he is not just doing descriptive history; his "theory has consequences for the way in which scientists should behave if their enterprise is to succeed" (p.208).  He has obtained "descriptive generalisations" from the history of physicists' behaviour, looking at cases involving physicists "whose methods have been developed and selected for their success" (p.208).  He hopes to show that these cases are not "anomalous behaviour", by showing that they can be derived from a rational theory, by showing that physicists "do in fact behave as the theory says they should".  He knows there is danger of circularity in this claim, and he is implicitly suggesting that justification for the theory can be obtained independent of history, but that the history of cases pre-labelled, perhaps intuitively as typically successful, should then fit with his theory.
   Suppose we try presenting his theory as descriptive methodology - since he was uneasy about the question of history as evidence, and explicitly wanted his theory to be normative:
(i) Physicists should not always be working on the basis that all their hypotheses are questionable, and any could be adjusted at any time (at the extreme, revolutionary mode). Sometimes they should work in another mode on the solution to puzzles, based on the presumption that certain theories (paradigms) are true (at the extreme, revolutionary mode); these puzzles include situations where the hypothetical structure is inconsistent, for example because of an experiment. Justification: the full implications of theories can only be worked out by such intensive and extended study; continual, widespread, concern about all the hypotheses of physics, increasing at the higher levels, is counterproductive. This is an empirical claim, supported partly by logical consideration of the structure of higher-level hypotheses, and partly by generalised evidence from history - indicating that valuable progress has often been made during phases of normal science.  Note that this is an important role for detailed history of physics, genuinely providing evidence for methodology (though not, we repeat, for metamethodology).
(ii) Many factors are involved in the revolutionary change of a higher-level hypothesis; those which are internal - rational given the specially valued aim - such as successful novel fact prediction, and simplicity (linked to anomalies), and internal and external consistency, should be given due emphasis. If these factors underdetermine the change, then the partially conventional, non-rationally determined, character of the new hypothesis should be explicitly stated.
Justification: the internal factors are supposed justified, but no justification is attempted.
   These proposals fit neatly into descriptive methodology, and should be accepted.  Popper and Lakatos accepted them. Kuhn thought that the discovery of normal science as a justifiable method was important; Popper and Lakatos thought it was obvious and unimportant.  But falsifiability, successful novel fact prediction, and complicating ad-hoc adjustments, are fairly obvious as well.  In fact, all of descriptive methodology should be obvious, in the sense that someone familiar with the current intuitive methodology of physicists should find all the methods and assessments systematised in it intuitively obvious. (Perhaps it is this slightly depressing fact which has caused philosophers to exaggerate the extent of their achievements, and insist on the imperceptible differences between their view and others)
   Kuhn was reacting against some notions current at that time, such as that, perhaps, a rational physicist can never justifiably accept a set of high-level hypotheses as working hypotheses, but should be always working to disprove (falsify) them; that progress, perhaps, only consisted of such falsifications; that a theory can only justifiably supersede another one if it includes all the true content of its predecessor.  His study of historical episodes, intuitively labelled by him - and via him the current physics consensus - as rational, indicated that "those notions did not at all fit the enterprise that historical study displayed".  This also is a sensible use of history, tentatively, as hints towards the correct set of methods to describe the present consensus.
 

   The story is not over. Some people (Giere's 'Naturalised Philosophy of Science'?) have shifted to a different task: to find a total set of hypotheses from which the detailed behaviour of historical physicists follows as a consequence - regardless of which factors are internal and which are not; to explain the behaviour of physicists as a whole.  This enterprise is of no interest to the methodologist.

   Philip Kitcher, in his 'The Advancement Of Science', begins with a long section of history of evolution.  He then regards describing and explaining the behaviour of physicists as his primary aim - as is made clear by, for example, his use of a model of the mind/brain of the physicist, which he uses to help him to explain why a physicist might make a particular decision in a particular situation.

   Overall this is a disappointing episode in the history of the philosophy of science.  We propose that methodologists should explicitly cut themselves off from history; they should persuade themselves that it does not provide the evidence for their meta-investigation - merely illustrations.  They should follow the example of Mill.  The only role that historical events play is as illustration for some particular methods (see Methods of Physics - Historical Evidence).

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