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Critical Rationalism: A Restatement and Defence.

This volume is really two books stitched together, one on critical rationalism, the other on questions to do with probability theory and verisimilitude. The join occurs on p. 125, when the discussion switches to Bayesianism; after that it never really returns to critical rationalism. This second half is very different, in content and style, from the first, and I will begin with it.

Chapter 8 deploys chaos theory against the Bayesian claim that the posterior probabilities of subjects with very different priors will tend to converge as evidence accumulates. Its conclusion is that `agents who start off in almost complete (probabilistic) agreement may in special, perhaps unusual, circumstances come to diverge in their opinions more and more, despite being exposed to the same evidence' (p. 170).

Chapter 9, `Objective Probabilities', I found especially interesting. It reviews Popper's shift from a frequency to a propensity interpretation, examines an interesting objection to the latter, and proposes a revised frequency interpretation intended to combine the merits of these two predecessors. The propensity interpretation, as Miller understands it, construes `There is a probability of 1/6 of getting six-up with this die-throwing apparatus' as saying that this apparatus, given the present state of the universe, has a propensity of 1/6 to produce a six-up outcome. Thus it is restricted to indeterministic universes, and a main advantage of the classical frequency interpretation is that it remains applicable in deterministic universes. Its main disadvantage is that, unlike the propensity interpretation, it cannot handle single-case probabilities. Miller discusses the following difficulty for the propensity interpretation. Let p(alc) be the probability of outcome a on generating conditions c. If that is well defined, so too is p(c/a); but how, according to this interpretation, should this be understood? As the propensity of outcome a to produce conditions c? Surely not.

All the above-mentioned difficulties would be overcome by a revised version of the frequency interpretation that enables it to handle single-case probabilities; and this is what Miller goes on to provide. Consider a single throw of a die at time 0. According to an unrevised frequency interpretation, the probability of six-up is the limiting value of the frequency of this outcome in a hypothetical sequence of repetitions stretching to infinity, where the repetitions may be imagined as occurring at regular intervals. In place of that Miller imagines this throw as the last in a hypothetical sequence consisting of a denumerable infinity of repetitions at ever shorter intervals during the finite time interval (-1, 0), and also as the first in a converse sequence during the finite time interval (0, 1):

[ILLUSTRATION OMITTED]

The probability of getting six-up with a single throw at time 0 is the limiting value of the frequency (Miller actually writes `probability', but that is a slip) of this outcome `in shorter and shorter dense subintervals of (-1, 1) containing 0' (p. 192).

Chapters 10 and 11 are on the problem of verisimilitude and related issues. He shrewdly points out that Popper's critics paid scant attention to his concept of verisimilitude in its heyday; only after its collapse in 1974 did they start claiming that what had collapsed was a central plank of his philosophy. But it can be said in extenuation that their post-debacle evaluation reflected Popper's pre-debacle evaluation; he identified scientific progress with increasing verisimilitude and said, `we simply cannot do without this idea'. Only after the debacle did he play down its importance, saying that the idea of verisimilitude `is not an essential part of my theory' and that his main position was not `in the least shaken by this unfortunate mistaken definition'. (For references, see my [1984], pp. 281-2.)

Miller's own view is: an adequate definition of verisimilitude would be highly desirable; however, falsificationism can get along without this, which is just as well, since the prospects for it are bleak. He has a neat new way of obtaining his (and the late Pavel Tichy's) old 1974 result, together with a result arrived at independently by Keuth [1976] and by Vetter [1977]. Let `Cn(H)', `Ct(H)', and `Cf(H)' denote respectively the content, the truth-content, and the falsity-content of a theory H. Let f be an item in Cf(H) and now consider the bi-conditional f-iff-x, where x is any proposition. This bi-conditional is true when x is false and false when x is true. To every x in Ct(H) there will correspond an f-iff-x in Cf(H), and to every x in Cf(H) there will correspond an f-iff-x in Ct(H). This reproduces the Keuth-Vetter result that the number of a false theory's false consequences equals the number of its true consequences.

Miller's application of these ideas to verisimilitude-comparisons (p. 210) is rather terse, and I will try to present it in a more reader-friendly way. Popper's original requirement for theory K to have greater verisimilitude than theory H was: (1) Ct(H) [subset or equal to] Ct(K); (2) Cf(K) [subset or equal to] Cf(H); (3) at least one of these two containments is strict. That threefold requirement could of course be trivially met if H were true and strictly entailed by K; but Popper's whole object was to capture cases where at least one of the theories is false. If H were false and K true, condition (1) could not be met; for to an f in Cf(H) there would correspond an f-iff-x in Ct(H) that was not in Ct(K). So assume that H and K are false theories which satisfy (1) and (2). Can they satisfy (3)? Let f be in Cf(K) and hence, by (2), in Cf(H), and let x be any item in Cn(K). Suppose first that x is false. Then by (2) x is also in Cn(H). Now suppose that x is true. Then f-iff-x is in Cf(K) and hence, by (2), in Cf(H). But iff and f-iff-x are both in Cn(H), so is x. Hence every x, whether true or false, in Cn(K) is in Cn(H) and (3) is not met.

In Chapter 11 Miller reworks a disquieting result which he first published in 1975. He takes off from the following numerical example (with acknowledgements to Popper). Let the true values of the quantities [phi] and [psi] be respectively 0 and 1. Theory K gets [phi] nearly right and [psi] exactly right; theory H does worse on both counts. We now define two further quantities, [eta] and [xi] as follows: [eta] = [psi] - 2[phi] and [xi] = 2[psi] - 3[[phi]. So the truth is [eta] = 1 and [xi] = 2. This time, theory H gets [eta] nearly right and [xi] exactly right; theory K now does worse on both counts. For a critic who protests that these latter values are unnatural artefacts Miller has ready to hand the riposte that we might equally have started with [eta] and [xi] and gone on to define [phi] and [psi] as: [phi] = [xi] - 2[eta] and [psi] = 2[xi] - 3[eta].

This chapter, and with it the book, ends on a dispirited note:

there seems to be the strongest possible methodological demand

for our being able to make sense in some way of the degree to

which some hypothesis, in answer to some problem, approaches

what might be thought to be the true answer to that problem. I am

no less sorry than I was 20 years ago that I still seem unable to do

much at all to satisfy that demand.

I now turn to the first half of the book. First, a quick word about Chapter 4, which is a tribute to the late Bill Bartley by way of a rehabilitation of his Comprehensively Critical Rationalism against criticisms levelled at it by John Post and myself. I am not sure whether it is successful, but it certainly is very nicely done. Now to the main business, the `restatement' of critical rationalism. In Chapter 1 the aim of science is declared to be simply to classify statements as true or false. (If this means classifying them correctly, then science has had little success in fulfilling this aim, since `scientific knowledge is most often not true', p. 54.) It pursues its aim by means of an open admission policy combined with a rigorous expulsion policy. The only requirement on hypotheses for admission to science is that they be empirically falsifiable. (This gets a little qualified; the hypothesis should make some attempt, `however feeble', to solve a scientific problem; and unfalsifiable metaphysical hypotheses are allowed in, though only on the coat-tails of falsifiable hypotheses, and must go with them if the latter are expelled.) Once admitted, falsifiable hypotheses must be tested as rigorously as possible, in the hope that the false ones among them will be falsified. No credit accrues to a hypothesis from passing tests--`this makes not a jot of difference' (p. 7). But failing a test makes a decisive difference.

Chapter 2, `Popper's Solution of the Problem of Induction', has a section entitled `Enumeration of Objections' followed by one entitled `Elimination of Objections'. Since objections raised in my [1984] are among those he purports to eliminate, I was disappointed that he takes no account of one I directed (with no claim to originality) specifically against him. In his [1982] Miller had summarized a long quotation from Popper about `relying' in our actions on scientific theories as follows: `In other words, in the lucky event that we have an unrefuted hypothesis relevant to our practical problem we shall normally plan our actions on the assumption that this hypothesis is true.' On this I commented: `his sentence ought to have begun: "in the all too likely event that we have a plethora of unrefuted and mutually conflicting hypotheses relevant to our practical problem..." But how should this sentence now continue?' ([1984], p. 342). In his present book that 1982 passage is reproduced unchanged (pp. 8-9), and this very obvious objection is not addressed. I do not understand what Miller now says about reliability. He writes: `If you want to act appropriately to a situation, then true predictions of the effects of the competing proposals are all that you need. There is nothing to be gained from predictions that are reliable as well' (p. 45); again: `our aim is to make true predictions, not reliable ones' (p. 28). But predictions that are true are reliable as well. A true prediction that we do not know to be true is still reliable (it won't let us down), though we do not know that it is. If, as he says, the demand for reliability cannot be met, then nor can the demand for truth.

This pseudo-opposition between reliability and truth is symptomatic of a false antithesis that crops up all too frequently in this book. For instance, Miller asks: `Which ticket would you prefer to draw in a sweepstake: the one bearing the favourite's name, or the one bearing the winner's?' (p. 66, his italics). Suppose that the race has not yet been run, or at least that its result is not yet known, and that I have drawn the ticket bearing the favourite's name. I would of course gladly swap it for the one bearing the winner's name if I knew which one that is; but since I don't, I won't. Miller writes: `if our goal is simply to sort out what is true, the detour through probability or confirmation, or support [or, he should have added, Popper-style corroboration]... is plainly gratuitous' (p. 5). If we could know which (if any) of the competing hypotheses before us is the true one, we could indeed go straight to it without bothering to ask which one (if any) is best corroborated. But if truth in science is not manifest but `hidden in the deep', what Miller calls a gratuitous detour is the only way.

Chapter 3 propounds the extraordinary thesis that `there are no such things as good reasons; that is, sufficient or even partly sufficient (or positive) reasons for accepting a hypothesis rather than rejecting it, or for implementing a policy, or for not doing so' (p. 52). Can he really mean this? If, to borrow an example from Hume, I believe that I shall tread on someone's gouty toe unless I make a slight detour, don't I have at least a partly sufficient reason for implementing a detour-policy? In my [1984] I used `rationality-scepticism' as a label for the thesis that `we never have any good cognitive reason to adopt a hypothesis about the external world'; I regarded this as the sceptical ne plus ultra and took for granted that it is anathema to rationalists of whatever stripe; but in his examination of my book Miller commends rationality-scepticism (p. 120).

As we saw, his view of science combines easy admission with harsh expulsion; but if there are never good reasons for acceptance, can there be good reasons for rejection? Wouldn't a reason to reject hypothesis h as false be a reason to accept not-in as true? Miller calls this, with good reason, `the tricky bit' (p. 67). There are, he says, two responses open to the critical rationalist, one `specious and superficial' (we may pass this over), the other `simple and satisfying'. Well, it is indeed simple: `critical rationalism need have no more truck with negative reasons than it does with positive reasons. There are no negative reasons either' (p. 70). What now becomes of Popper's `hypothetico-destructivism', as Miller calls it? As he rightly says, `Many will fear that this abnegation of negative reasons as well [as positive reasons] will void science of its last vestiges of rationality and leave it at the whim of entirely arbitrary decision' (p. 70). Although he doesn't acknowledge it, Miller is obviously in a dilemma here. If he came up with a good reason for repelling this fear, which he doesn't, he would have refuted the very thesis he is championing.

I find it rather irritating that he presents this defeatist philosophy of science with a chirpy optimism. By the illicit use of success-words incompatible with his rationality-scepticism, he makes it sound as though capturing the truth is a straightforward business. Thus he says that the business of science is the discovery of truth-values (p. 11, my italics) and the aim of science is to identify truths (p. 208, my italics); again, `science proceeds not by getting near to separating true and false statements but by actually separating them' (p. 3, my italics). Sometimes he tries to cancel the success-element; for instance, after `... by actually separating them' he adds `(correctly or incorrectly)' which is like saying that the Duke of Wellington did not get near to winning battles but actually won them (successfully or unsuccessfully).

Since an unwary reader of this book may gain the impression from its many acknowledgements and salutations to Popper that it is essentially a restatement of Popper's philosophy, I may point out that it is very unPopperian in important ways. (1) Popper did not endorse a policy of waving in any old rivals to a currently prevailing theory, provided only that they are falsifiable. He rightly considered it an important feature of his methodology that it enables us to say what kind of theory would be better than the prevailing one, provided it passes tests ([1963], pp. 217, 240f.). (2) A main component of Popper's methodology was his theory of corroboration (see the concluding chapter and appendix (*)ix of his [1959]); corroborations are what ultimately govern the rational acceptance of theories. This disappears without trace in Miller's `restatement'. In his index there are six entries against `corroboration', five of which refer to places where an author is being quoted or reported. The sixth comes in the course of an examination of my [1984]. I had tried to give a fresh answer to the question, `Why do corroborations matter?' Miller writes: `The answer is that corroboration doesn't matter' (p. 120). (3) Popper had a horror of anything like rationality-scepticism. He insisted that a theory's being currently the best corroborated, while not justifying the theory, does justify a preference for it over its rivals. He may not have kept these two kinds of justification as separate as he should have done, but his philosophy allows there to be sufficient reasons for accepting one theory as better than its rivals at the present time. Of course, Miller is free to make what changes he likes; but in a book which purports to present `a sounder and less blinkered appreciation of Popper's work than it has previously enjoyed' (p. x), I don't think he should silently ditch large chunks of it.

The book has its quota of Millerisms (`Pyrrhonic victory', `wistful thinking', `Expected Futility', etc.). I liked `I wish to keep an empty mind on the subject'. A more accurate title for the book would have been: `What Remains of Critical Rationalism when the Rationalism is Dropped'.

References

Keuth, Herbert [1976]: `Verisimilitude or the Approach to the Whole Truth', Philosophy of Science, 43, pp. 311 36

Miller, David [1982]: `Conjectural Knowledge: Popper's Solution of the Problem of Induction' in Paul Levinson (ed), In Pursuit of Truth Essays in Honour of Karl Popper's 80th Birthday, Hassocks, Harvester, pp. 17-49

Popper, Karl R. [1959]: The Logic of Scientific Discovery, London, Hutchinson.

Popper, Karl R. [1963]: Conjectures and Refutations, London, Routledge & Kegan Paul.

Vetter, Herman [1977]: `A New Concept of Verisimilitude', Theory and Decision, 8, pp. 369-75.

Watkins, John [1984]: Science and Scepticism, Princeton, Princeton University Press and London, Hutchinson.
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Author:Watkins, John
Publication:The British Journal for the Philosophy of Science
Article Type:Book Review
Date:Dec 1, 1995
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