PH29A Is scientific method a myth?

The issue I want to examine now is encapsulated in the following remark by Larry Laudan:

virtually every major philosopher of science, from Aristotle to Carnap, has assumed that there is a set of rules for scientific method which are permanent and trans-temporal. By contrast, some historical research is suggesting that the rules constitutive of scientific rationality may change through time (1979, p. 45)

To determine an issue of this type, we need to be careful about how we identify elements of a method or methodology. Do something and then do something else, may, if inaction is allowed as doing something, cover every conceivable method but it is clearly useless as an account of anything. Appeal to authority is a somewhat more specific injunction, but there is a big difference between cases where the authority is a translation of the Bible or Virgil, a translation of Aristotle, or an article by Einstein.

To bring our question slighter more into focus, we can note that Popper, for instance, erected his methodological maxims on the basis of his appreciation of the deductive relations between universal theoretical claims and singular observational ones. These deductive relations are timeless, if anything is, so it is perhaps not surprising that Popperian methodology offers itself as applicable indifferently to many different historical epochs. Our question can be regarded as one specific instance of a wider question about the utility of stressing, on the one hand, formal universal logical matters, as against their specific exemplifications at a particular stage of enquiry in a discipline (a contrast frequently invoked in discussions of critical thinking, for instance).

But before starting in to the discussion, let us actually look at some proposed methodologies, or rather bits and pieces of methodology.

Examples of methodology:

• Descartes (à la Garber, (1989)) "reduce involved and obscure propositions step by step to simpler ones, and thus from an intuition of the simplest we try to ascend by those same steps to a knowledge of all the rest." One example starts from the question "what is the shape of a line (lens) that focuses parallel rays of light to the same point?", proceeeds to "what is the relation between angle of incidence and angle of refraction?", thence to "how is refraction caused by light passing from one medium to another?", to "how does a ray of light penetrate a transparent body?", to "what is light?" finally to "what is a natural power?" Descartes thinks he can answer that and then deduce the answers to his preceding questions.

Two comments for now: (1) Descartes' maxim can only be followed if you know a good deal already. His sequence of questions might well not occur to someone differently placed. (2) The procedure recommended is clearly of a piece with Descartes' approach to epistemology. It would seem to flow from (if not deductively follow from) his general assumptions about our cognitive predicament.

• Popper (à la Jarvie, (n.d.): I give several extracts from Jarvie's paper (most references to Popper are to his Logic of Scientific Discovery). "In the final section of Part I of The Logic of Scientific Discovery Popper discusses "methodological rules as conventions". He proposes a supreme or meta-rule which governs the later rules to be proposed. This reads:

  (SR) "the other rules of scientific procedure must be designed in such a way that they do not protect any statement in science against falsification" (LScD, p. 54).

  .... a methodology is not like the closed set of rules that constitute chess. Popper begins by proposing two examples, and we shall be able to extract others from later in the book. The first example is:

  (R1) "The game of science is, in principle, without end. He who decides one day that scientific statements do not call for any further test, and that they can be regarded as finally verified, retires from the game" (LScD, p. 53).

  The second example is:

  (R2) "Once a hypothesis has been proposed and tested, and has proved its mettle, it may not be allowed to drop out without 'good reason'" (LScD, p. 53-54).

  (R3) "[We] are not to abandon the search for universal laws and for a coherent theoretical system, nor ever give up our attempts to explain causally any kind of event we can describe" (LScD, p. 61).

  Proceeding through the book, the next time Popper brings up a methodological rule is when he is considering the problem of how to maintain the empirical character of an axiom system, to prevent it from becoming conventional. There is, he argues, no natural solution, only a methodological decision will do the job. Accordingly:

  (R4) "I shall...adopt a rule not to use undefined concepts as if they were implicitly defined" (LScD, p. 75).

  (R5) "[O]nly those [auxiliary hypotheses] are acceptable whose introduction does not diminish the degree of falsifiability or testability of the system in question but, on the contrary, increases it" (LScD, p. 83).

  (R6) "We shall forbid surreptitious alterations of usage" (LScD, p. 84.)

  (R7) "Inter-subjectively testable experiments are either to be accepted, or to be rejected in the light of counter-experiments" (LScD, p. 84).

  (R8) "The bare appeal to logical derivations to be discovered in future can be disregarded" (LScD, p. 84).

  (R9) "[A]fter having produced some criticism of a rival theory, we should always make a serious attempt to apply this criticism to our own theory" (LScD, p. 85n).

  (R10) "[W]e should not accept stray basic statements — i.e. logically disconnected ones — but ... we should accept basic statements in the course of testing theories; or raising searching questions about these theories, to be answered by the acceptance of basic statements" (LScD, p. 106).

  (R11) "This makes our methodological rule that those theories should be given preference which can be most severely tested...equivalent to a rule favouring theories with the highest possible empirical content" (LScD, p. 121).

  (R12) "I propose that we take the methodological decision never to explain physical effects, i.e. reproducible regularities, as accumulations of accidents" (LScD, p. 199).

  (R13) "a rule...which might demand that the agreement between basic statements and the probability estimate should conform to some minimum standard. Thus the rule might draw some arbitrary line and decree that only reasonably representative segments (or reasonably 'fair samples') are 'permitted', while a-typical or non-representative segments are 'forbidden'" (LScD, p. 204).

  A final example from this context of probability statements and their confinement is:

  (R14) "[T]he rule that we should see whether we can simplify or generalise or unify our theories by employing explanatory hypotheses of the type mentioned (that is to say, hypotheses explaining observable effects as summations or integrations of micro events)" (LScD, p. 207).

  Jarvie concludes with a quotation from a later piece by Popper in which he contrasts what he sees as desirable in science with what the historian of science, T.S. Kuhn, described as "normal" science. Popper's methodology was in no sense a description of the social reality of the majority of scientists:

  'Normal' science, in Kuhn's sense, exists. It is the activity of the non-revolutionary, or more precisely, the not-too-critical professional: of the science student who accepts the ruling dogma of the day; who does not wish to challenge it; and who accepts a revolutionary theory only if almost everybody else is ready to accept it — if it becomes fashionable by a kind of bandwagon effect. To resist a new fashion needs perhaps as much courage as was needed to bring it about...
  I admit that this kind of attitude exists; and it exists not only among engineers, but among people trained as scientists. I can only say that I see a very great danger in it and in the possibility of its becoming normal (just as I see a great danger in the increase of specialisation, which also is an undeniable historical fact): a danger to science and, indeed, to our civilization (Popper 1968, pp. 52-53).

One commment we might make is the same as my second about Descartes. These recommendations flow from Popper's account of our cognitive situation. Regarding them as norms, and in line with the empiricist/positivist suspicion of any claim to truth for normative claims, Popper presents them as conventions, and thus invites the later criticism that we might as well choose to do things very differently. But my point about both methodologies is that they do not float free of the writer's wider beliefs about the universe, and in particular our cognitive situation. Popper may not want to countenance non-deductive relations of support, but if they exist, it is plausible to see cognitive facts thus supporting norms of his type.

Recent methodology

While definitely not universally endorsed, Popper can be regarded as exemplifying the traditional approach in scientific methodology. That approach, as Laudan said, assumed that basically things don't change as far as methodology goes, and that in science we have on the whole made regular and rationally recognisable progress. The situation was turned upside down by Kuhn's historical work, which contrasts "normal" with "revolutionary" science (see the last quotation from Popper) and gives an account of the latter, in terms of a Gestalt switch of "paradigms," that few could recognise as a matter of rationality. Partly in response, Lakatos proposed a historically more nuanced view in a Popperian mould, but that too was attacked by Feyerabend, who argued that it was impossible to find any methodological maxims implicit in what Popper and the tradition took to be exemplary science. (For a taste of Feyerabend, see these extracts from Against Method.) Laudan, whom we shall be looking at below, can be seen as attempting some sort of arbitration between the tradition and the Kuhn-Feyerabend radicals.

Some points made against the logical model

Style of theorizing: Shapere (1989) notes that the preferred type of physical theory started as mechanical (Newton's gravity didn't fit this but it was soon allowed in), and shifted to abstract with Maxwell's failure to give a mechanical interpetation of his theory of electromagnetism. Now the preferred manner is to use as mathematical structure a local gauge theory. He remarks that "the explanations offered are incompatible with the classical idea of explanation,.... the universe need not operate in those ways, need not be understandable in any of the senses extracted from, and designed to deal with, everyday experience" (p. 207). (Cushing (1990) also stresses the inevitable compromises of what we would like explanations to do when we are confronted with Quantum Mechanics.) A different point that Shapere also makes concerns the way these theories have been involved in narrative explanations in connection with Big Bang cosmology, thus closing the gap between physical and historical modes of explanation. But the point for now is that methodology regarding theory construction will vary with different periods.

Theory-ladenness 1: It is now pretty widely accepted that we cannot make a simple once-and-for-all division between items that are observational and those that are theoretical. Once upon a time genes were invoked as a theoretical explanation of patterns of inheritance; now we can chop and change them around. We can see sub-atomic particles in cloud chamber photographs. Shapere (1989) remarks "what counts as observational evidence is shaped by a background of other ideas, theoretical and non-theoretical" (p. 209), and so, again, methodological principles will recommend different things in different contexts.

Theory-ladenness 2: Hooker (1989) makes the point that "rational inductive inference is context-dependent, the context being primarily fixed by theory" (p. 212, he uses Russell's chicken as a pertinent example: it is fed consistently each day for the whole year, until Christmas when, given our understanding of the cultural context, we expect it to be slaughtered for the table). "Method then is a function not only of logic but of substantive theory." Hooker says we should abandon the idea of eternal logical rules in favour of "complex control systems".

Laudan's account

Laudan's suggestion (1987, close to Hooker's own, I think) is that we should see methodology as a set of hypothetical imperatives: founded on claims about means-ends relations, the ends being our cognitive aims and the means being what we think will conduce to achieving them. As our aims change or our beliefs about what will achieve them change, so most likely the methodology will change to.

Our aims may change in relevant ways when we adopt different goals for explanation or constraints on explanation, or operate with different overall philosophical interpretations of a scientific theory (instrumentalist, realist, ...). They can also change in cognitively irrelevant ways.

But since all methodological rules will be founded upon means-ends connections, they will share whatever general logical constraints operate upon such things.

Sloep (1993) points out that in extracting methodological norms from a description of practice (the means actually found to bring about desired cognitive ends) we first have to choose the practice, and this looks set to prejudge the outcome. This is so particularly when a scientific controversy is primarily a matter of conceptual and inter-theoretic matters rather than what the facts are. Sloep's own position is that such apparently philosophical and unresolvable controversies often in fact depend upon participants' ignoring very simple and elementary methodological points, whose banality is not such as to lead to relativism. In the case he takes, claims about falsification get in the way of recognising what can be established when one is unable to reject a null hypothesis (specifically that the alternative has not thereby been falsified: "lack of a deviation from expectation may either reflect the lack of disturbing forces or the cancelling out of their effects" (p. 242)) There is a question in general about identifying cases of what we are interested in (science, in this case) and decisions could be made that prejudge certain questions by excluding possible exemplars. But speaking very roughly, there isn't much of a problem in general in identifying socially given categories. There may be odd cases at the boundaries where there is room for doubt (cf. the question about pseudo-science). (It is also worth noting that there are several boundaries in question — cultural, disciplinary, historical, etc.) Laudan makes the point that social institutions with a considerable history, like science, construct a canon of as it were permanent exemplars, and so if somebody proposes to do something utterly different from what the canon did, they wouldn't be counted as continuing the institution (conversely, the canon gives us a fair picture of what the institution consists in).

The Laudan/Worrall debate

Worrall's (1988) is a review of Laudan's Science and Values. Laudan claims that the modern rendition of traditional approaches to science works with a hierarchical model of three levels, factual, methodological, and axiological, in which disagreements at one level are resolved by appeal upwards. A problem here is what happens when there is disagreement at the top level (e.g., realist/instrumentalist; teleologists/anti-teleology; vitalism/reductonism,...). Recent history and sociology of science has emphasized a relativist holist model which features conversion, not rational change. Laudan offers his own 'reticulated' model as an alternative. Laudan's model has the same three levels but denies (against the holists) simultaneous change at all levels but allows (against the hierarchical models) upwards and downwards adjustments.

Worrall makes two main claims: the reticulated model fails to deliver and Laudan has mischaracterised the hierarchical model.

• Assume a possible shift from T₁, M₁, A₁ to T₂, M₂, A₂. Assume these really are the norms governing action (not merely what people say). But if M₁ ranked T₂ above T₁, how could acceptance of T₂ require a move to M₂? In the case he cites, it looks in fact that M₁ could not rank T₂ above T₁. Worrall takes one of Laudan's historical examples: Fresnel's theory accepted on Newtonian inductive principles; but if Fresnel postulates entities banned by Newtonian method, how could it have been rational to adopt Fresnel? (If all it shows is that scientists didn't actually use Newtonian methodology, it 's not a case of reticulated methodology.)
• Laudan takes a much wider view of method than hierarchical theorists; none of Laudan's principles would have counted as methodology for the hierarchical theory. The hierarchical model is an attempt to articulate the logic of science or scientific appraisal. Invalid arguments do not impugn deductive logic or suggest that its standards have shifted. Similarly, on the hierarchical view, axiology does not govern methodology since it doesn't accept methodological differences (or perhaps rather, if people disagree, at least one is wrong). Worrall claims that, for all their differences, different hierarchical theorists all produce the same ranking: Einstein, Newton, Aristotle. Worrall's diagnosis of Laudan goes by way of allowing that the hierarchical view tends to ignore the multi-level nature of science: types of theory, specific auxiliary theories, etc. General principles can be both substantive and heuristic (look for another theory of this type). So it is then easy for Laudan to take them as a matter of methodology, and thus as changing. Laudan makes much of the discovery of double-blind methodology in clinical trials, but for Worrall this is the application to an invariant principle (test a hypothesis against its plausible alternatives) of the substantive discovery of placebo effects.

Laudan's reply (1989)

• It is not admitting that standards change that leads to relativism but our inability to justify the standards. Typical hierarchical theorists did not offer such a justification (Popper said it was a matter of convention, Reichenbach a matter of choices).
• Worrall is committed to implausibly frequent false consciousness on the part of scientists.
• Worrall is committed to some purely procedural principles. But his example (test against plausible alternatives) fails for some possible worlds (small, finite). Nor was it always used: Laudan refers to some early physics which was a matter of showing how to solve certain problems but in which no tests were reported. Laudan says the principle is almost vacuous: it tells us nothing about when a test really tests.

Worrall's reply (1989)

• Yes we have learnt to do science better. But to say our methods are better we need a fixed core: deductive logic and weighing of evidence. (He says when statistics first became central to science they were evaluated by reference to the same fixed principles, but has to admit that there is still much strife over which principles are appropriate.)
• We cannot justify our position against a resolute sceptic. Deductive logic too must be adopted dogmatically. He thinks the serious worry does arise from the idea of standards changing: why ignore "creation science" if one day its standards might be accepted?
• Worrall claims that, when carefully examined, the historical record does not require him to suppose as much false consciousness as Laudan claims.
• He admits that Laudan is right about more general principles being infected with some assumptions about the world. So the contrast is not substantive/formal but more or less substantive. This means that Worrall's methodological principles are fallible but not necessarily (and not likely to be) corrigible.
• He rejects some of the specific criticism of his testing principle, however: it says test against rivals, if there are any so Laudan's finite case is irrelevant. Nor does it claim that such testing is the only way to argue for a theory, so the physics history Laudan notes is, even if correct, irrelevant.

By way of summing up, it seems that one general comment is to endorse Worrall's claim about the level at which methodological principles are being analysed. Cushing (1990) argues that there are no atemporal constraints beyond "normal, commonsense demands placed on everyday argument" (p. 178). Worrall is concerned to insist on the latter; Laudan and his supporters stress the interesting derivative principles. A problem for Worrall is that his unchanging principles turn out to be very uninteresting (deductive logic is important, but in this context not exactly news) or elusive, as he admits about those governing the acceptance of statistical theories.

I don't want to go too far into Laudan's means-end claim, except to say that I would prefer to stick with the perhaps sketchier notion I adumbrated earlier, of methodological recommendations flowing from one's view of our cognitive predicament. Sometimes that view is sufficiently tight to permit straightforward means-end reasoning (as perhaps in the case of double-blind clinical tests); other times the links are looser.

Works cited:

• Cushing, J.T. [1990] Is scientific methodology interestingly atemporal? British Journal for the Philosophy of Science, 41: 177-194
• Garber, D. [1989] Descartes and method in 1637 PSA 1988 Vol. 2, 225-236
• Hooker, C.A. [1989] From logical formalism to control structure: the evolution of methodological understanding, PSA 1988 Vol. 2, 211-221
• Laudan, L. [1979] Historical methodologies: an overview and manifesto, in P.D. Asquith and H.E. Kyburg, Jr. (eds.) Current Research in Philosophy of Science (Philosophy of Science Association).
• Laudan, L. [1987] Methodology's prospects, PSA 1986, Vol. 2 347-354
• Laudan, L. [1989] If it ain't broke, don't fix it, British Journal for the Philosophy of Science, 40: 369-375
• Shapere, D. [1989] Modern physics and the philosophy of science, in A. Fine and J. Leplin (eds.), PSA 1988, Vol. 2, 201-210.
• Sloep, P. [1993] Methodology revitalized? British Journal for the Philosophy of Science, 44: 231-249
• Worrall, J. [1988] The value of a fixed methodology (review article of L. Laudan, Science and Values), British Journal for the Philosophy of Science, 39: 263-275
• Worrall, J. [1989] Fix it and be damned: a reply to Laudan, British Journal for the Philosophy of Science, 40: 376-388

A few others:

• Ginev, D. [1993] Do we need fixed methodological principles? British Journal for the Philosophy of Science, 44: 329-334
• Grobler, A. [1990] Between rationalism and relativism: on Larry Laudan's model of scientific rationality, British Journal for the Philosophy of Science, 41: 493-507
• Schmaus, W. [1996] The empirical character of methodological rules, PSA 1996 S98-S106
• Shapere, D. [1985] Objectivity, rationality, and scientific change, in P. Asquith and P. Kitcher (eds.), PSA 1984, Vol. 2, 637-663.
• Siegel, H. [1996] Instrumental rationality, PSA 1996 S116-S124
• Worrall, J. [1985] The Background to the Forefront, in P. Asquith and P. Kitcher (eds.), PSA 1984, Vol. 2, 672-682.

E.P. Brandon, last revised 31 October 2001.

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