A SIMPLE ISSUE OBFUSCATED

The prerequisite of criticism is the ability to recognize plain incompat­ibility between one’s view and a putative counter-example. The critically- minded must recognize a counter-example when he sees one, and on occasion accept one and then change his view.

The prerequisite is not in universal terms. All critically-minded people cannot be required to recognize every incompatibility thrown at them - the exercise may require more mathematics than is at hand, or more leisure than one may wish to consume. Nor can we require that every counter-example which is reasonable be viewed as reasonable. We do not know what is reasonable. We know that reasonable reports of the mid- night-sun in antiquity and of elephants and castles in medieval Europe were quite reasonably dismissed as unreasonable. Similarly, as we know now, Wolfgang Pauli was in error in thinking it unreasonable to try to refute the law of conservation of parity, yet he was then not being un­reasonable. Finally, if we insist that reasonable counter-examples be ac­cepted forthwith, then we must declare Galileo, for example, un­reasonable.

How hard it is to notice all that may be involved in critical debates is illustrated by Galileo’s reversion to Aristotelian ideas after he had overthrown Aristotelianism to his own satisfaction; and Popper’s re­quiring immediate acceptance of observation reports and rejection of the hypotheses they contradict, while approving of Galileo’s admiration for Copernicus’s refusal to reject Copernicanism in the face of refutation from the observed variability of the brightness of Mars.

So much for the fact that critical people are not always critical - perhaps no one is. More needs to be said about critical-mindedness, as almost anybody accepts criticism sometimes, yet few are critically- minded. I shall not now enter this point, though I consider it important for a philosophy which follows Popper’s achievements yet rejects his tenets.

Let me begin with Michael Polanyi. His views on the matter are very simple to state but hard to develop. Briefly, he says that some criticism is acceptable, some not, this including observation reports. Which critic­ism is acceptable is a matter of personal knowledge, of intuition and of immediate feel; it is inarticulable, and subject to no criteria. The leader­ship of science may reject an observation report off-handedly and stick to a conflicting theory - just like that. They usually know what they are doing, or else they pay the price and lose their position at the top.

I do not like this theory, though on one point it seems fairly near the truth, simply by virtue of the fact that so many professional scientists today are less critically-minded than sheep. By Popper’s definition of science most scientists are not busy at scientific activity, since they offer neither (explanatory) hypotheses nor tests. Their minute contributions may be of some empirical and even intellectual value (measuring con­stants, calculating), but they are devoid of critical qualities.

Polanyi criticizes Popper by giving counter-examples to the equation of science with refutability. He does not offer examples from the sheepish behaviour of most scientists - since this would be question-begging. Rather, he gives cases of bona fide important scientific attainments which are either immune to empirical criticism or immunized for-the-time-being. Polanyi makes a good point, but errs in going on to claim that criticism, particularly empirical refutation, never takes place in science. Yet this wild-sounding idea is rather impressive: if criticism never has to be accepted as such, but only on certain conditions, then it is not criticism that causes changes of heart as much as the specific conditions which make for the acceptance of the criticism.

Impressive as it is, this idea is an obfuscation. It is true, yet it obscures the simple fact that when a situation is clear enough (there are conditions for clarity and these conditions may be involved) criticisms contradict given theories and force us to give them up. Further, such a development is a liberation. Popper’s detractors obfuscate this great idea of his: the overthrow of a theory as a result of observation is liberation achieved by empirical means. Thus, a refuting piece of evidence may be of a great theoretical import.

Hence, Polanyi’s criticism is answered: we can say, under certain con­ditions criticism is better accepted, yet stress the criticism, not the con­ditions. For the conditions are the clarity and the (hoped for) fruitfulness of the liberating effect of the criticism itself.

To see this, however, we have to see that criticism in general may be fruitful, including empirical refutation, of course. Yet one of the misunderstandings that plague Popper’s philosophy is the following idea which is often falsely ascribed to Popper: he allegedly does not see merit in refutations as such but only in their being instruments necessary for the proper corroboration of hypotheses. Popper has repeatedly said both that refutations are desirable and that there can be no corroboration except failed refutations. Now, this easily lends itself to the wrong reading that corroboration is desirable in itself and that refutations, though they should not be resisted, are not desirable in themselves but rather should be admitted as necessary occupation hazard. And this reading makes corroboration desirable though not easy to attain. But this reading is silly: if we hold false theories we may reasonably desire to refute them, not corroborate them. However, Popper’s lack of clarity on the role of corroboration makes it easy to read into his works the vulgar theory that corroboration is always good in itself, that every time a scientist cor­roborates a theory it calls for a celebration. In any case, my concern is less with Popper’s writings than with corroboration being an impediment, distracting an investigator from a more fruitful path.

At one time Imre Lakatos forged a compromise between Popper and Polanyi. According to his collaborator Alan Musgrave, the major idea of Lakatos is that certain ideas comprise the hard core of our research activities, the guiding ideas or regulative ideas of our researches, and for a time at least we protect them against refutations. This is both historically questionable and obfuscating. It assumes that only hard cores are protected, it assumes that all researchers in a field share the same guiding ideas, it assumes that refuted ideas cannot be guiding. There is empirical evidence against each of these assumptions, but if they constitute the hard core of Lakatos’s own researches, he may well protect them. This is, then, obfuscation.

The reluctance to admit refutations, which is now shown by Lakatos, a former disciple of Popper, is the first motive behind the earliest re­sponses to Popper’s views. Moritz Schlick, the father of the Vienna Circle, called it masochistic. This is not much of an argument, to be sure, as it does not indicate any over-eagerness to take the bitter medicine, let alone to show that it is bitter. The suggestion of overeagerness can be found in two versions, one which plainly violates the thesis of asymmetry and one which is more puzzling and may violate even the law of con­tradiction.

The first view is that of Hempel, of the symmetry between verification and refutation: both are impossible and must be replaced by the weaker confirmation and disconfirmation. (The word ‘disconfirmation’ is a neologism.) In order to render a refutation into a mere disconfirmation, however, we must raise doubts as to the truth of some observation reports, whereas in order to render a verification a confirmation we do anything else but raise such doubts.

The second view is that of A. J. Ayer. Ayer suggested, in a very famous passage of his, that maybe a hypothesis is refuted only once, like having the measles; if so, he added, then it would be a mistake to reject it on the basis of one measly refutation. Taken literally, this seems to be nothing short of quarrelling with logic - and logic seems to me to be as haughty and adamant as ever in declaring a universal statement contradicted by even one true existential statement to be false - irrevocably so. But what Ayer had in mind was perhaps a rule expounded by Newton at the end of his Opticks: when an exception to a generalization is discovered, the generalization should be modified to exclude the exception and the modified generalization retained. This, at least, is not against logic. Popper would object only that many qualifications may accrue in this manner and the generalization thus repeatedly qualified may lose its testability, content, and interest. Hence Ayer’s objection, when put in a logical manner, is less of an objection than it seems: Popper does not oppose the tactic Ayer seems to suggest except when it is over-used: when the measles becomes more than a mere childhood disease.

But all this is needling. The chief issue at hand seems to amount to the question, do we want finality in science, if not finality in the ac­ceptance of a thesis, at least in its rejection? If not, will it not be faintly ludicrous to reject a thesis and then reject the rejection and re-endorse the thesis? I think this is the root of the trouble. But since examples of resur­rected hypotheses are easy to find, the trouble is one which scientists handle, and so philosophers should acknowledge its existence.

There is more to Ayer’s objection to Popper than meets the eye, but unfortunately Ayer does not go into much detail. Suppose there is only one non-white swan in the whole universe. In a definite sense, then, the observation of this unique specimen is unrepeatable.

The argument I develop from Ayer prima facie looks reasonable enough to be problematic if not disturbing. So it may be advisable to go over the ground carefully, familiar or unfamiliar as it may be, and see how much is presupposed in even the simplest experimental reports. It is not necessary to decide whether a scientist’s presuppositions are right, but merely what presuppositions are involved.

Let me close this discussion with an example in which we do not doubt that scientists were right yet which is a challenge to the philosopher concerning the presuppositions of empirical evidence. There is a story which may be false - for all I know it is true - yet which is very thought­provoking. In one laboratory, so the story goes, measurements of proper­ties of metals, strength, elasticity, etc., seemed clearly to correlate to days of the week! The evidence was declared in some sense impossible, though it was admitted to be true. It was later found that the pieces of metal suf­fered from fatigue which disappeared on weekends, when they were allowed to rest. Metal fatigue is now considered an observed fact. So when should we ignore evidence in favour of a hypothesis?

IV.