SCIENCE CONSTRAINS ITSELF BY AUXILIARY HYPOTHESES

The constraints which I think science undertakes are often matters of calibration. I say undertakes because on occasion science may repeal or postpone this undertaking, as we shall see.

The constraint undertaken - and sometimes repealed - then, is related to calibration, both the successfully undertaken and the one skipped. The unsuccessful calibration, we remember, disqualifies the experiment before it is performed. Now, if the result of the experiment refutes a theory which one wishes to declare still unrefuted, one is always at liberty to recheck the calibration. This means that one tries to put the blame for a false prediction on some auxiliary hypothesis and then to show this by refuting it empirically - which is often easier said than done. Theoretical scientists throughout the history of modern science have questioned the results of observation and required rechecking - sometimes with detailed specifications, sometimes not - claiming that the results must accord with their views. In almost all such cases, rechecking was undertaken soon enough, either corroborating the theoretician’s a priori accusation, or forcing him to make a different move, or give up his position. If he does choose to make a different move which is again a challenge to the observer, some observer may take up his challenge and the story might develop accordingly; or the community of science may view him as a bore and a write-off.

Polanyi suggests that here the authority of the leadership of the com­munity of science comes into operation - when it declares that a theo­retician has gone far enough and now ought to desist: if he does not, he may be penalized and lose his status. In my view, however, it is a matter not of leadership but of democracy. As long as there are enough people interested in the theoretician’s struggles, I think, they may cooperate with him by checking what he suggests ought to be checked. It is very doubtful whether Planck could succeed in his venture without such close cooperation with experimenters. And he was both a high heretic and the secretary of the physical society to which he belonged. And he did not always accept the verdict of his experimental colleagues, of course, though he was not as stubborn as Newton was, for example. In particular, when a theoretician is his own experimentor, as Oersted or as Faraday was, a much higher latitude was allowed (by himself, and at his own risk).

Oersted, it is true, was somewhat penalized for his outlandish views, but he was also compensated (he failed to be appointed for the chair he felt was due to him, but as a consolation he received a stipend to build a private laboratory). Both Oersted and Faraday habitually blamed their instruments as too insensitive to detect effects which they were sure were present. This, to return to our problem, looks much too arbitrary: no matter what the missing effect is, we may always blame its elusiveness on the insensitivity of our instruments. This, surely, is easy enough! What is there to stop us from making such claims? Why, then, are such claims so seldom made? What was so special about Oersted or Faraday?

Take a modern effect: non-conservation of parity. What Lee and Yang felt was that the law of conservation of parity was rescued with great ease - too great - when a particle whose generation sometimes violated the law was declared to be two different particles (the so called tau-theta paradox).

It is not clear what would have happened if the two particles which Lee and Yang declared identical had shown a difference other than the known one, or if the experiment which they devised had ended in failure rather than in success. It is this kind of situation which, I think, ought to be examined more carefully.

What I wish to suggest, first, is that when a calibration is corroborated, its overruling has to be corroborated as well. Here is the requirement for corroboration based on prior corroboration of a contrary hypothesis in a manner hardly open to correlation with credence or credibility. Rather, the corroborated claim takes priority until its contrary is corroborated. It is simpler, we say, to take the corroborated thesis (as true) then to reject it in favour of its contrary, until the contrary be corroborated. But here simplicity may be synonymous with preferability. To make this rather ordinary and fuzzy presentation more cogent, let me put it thus. If one puts one’s view to empirical examination and another performs the examination and comes up with a result not congenial to one, if one can dismiss the uncongenial result by the mere guess that the other’s per­formance was not good enough, then a priori the other’s performance is useless because one’s excuse amounts to saying, there is no need for any

empirical examination of my views. That is to say, if one is a priori willing to discard as inaccurate any empirical evidence, then it is simpler not to start with the experiment in the first place.

To make simplicity signify more, we can say, in some circumstances the introduction of some contrary hypothesis introduces simplicity from some new direction and thus it may tip the balance. For example, it is simpler to say that we have not observed deviation from the law of con­servation of parity because the law holds than because our instruments are insensitive. But it is also simpler to say that two seemingly identical mesons are identical indeed, which entails that the law does not hold. For another example, it was simpler to declare the deviations from Gilbert’s theory of terrestrial magnetism to be due to local disturbances than to shift the magnetic poels from Earth’s geographic poles. But when evidence culminated the picture changed. After Ampere’s hypothesis concerning magnetism as due to currents, Earth’s magnetism was viewed as the re­sult of currents due to Earth’s charge and rotation. Consequently, the picture changed again and the magnetic poles found themselves imme­diately replaced in their original place at Earth’s geographic poles; and the observed magnetic poles had to be viewed as mere deviations from the true ones. This was a very big ad hoc adjustment; again we see how sometimes such adjustments thrust themselves upon us. Now these had to be corroborated. How? One cannot observe deviations of observed poles from the poles and so the theory as it stands thus far cannot possibly be either refuted or corroborated. In order to render it testable one needs further hypotheses! The history of the theory of Earth’s magnetism is very complex and not sufficiently studied; at least I am ignorant of it. Let me merely mention on that it includes another case of a revival of an old hypothesis - Hansteen’s revival of Halley’s hypothesis of two pairs of poles. Finally, it has been decreed that the Earth’s magnetism is not due to the diurnal rotation of the charged Earth but due to the rotation of Earth’s charged core which is due to, but not coincidental with, Earth’s diurnal motion. The terrific corroboration of this hypothesis came with the rise and corroboration of the hypothesis that Earth has altered its magnetic polarity a few times in its history, whereas, of course, nobody assumes that Earth has changed its diurnal rotation significantly ever since it came into orbit. (The corroborations of the changes of Earth’s magnetic polarity came from the analysis of the ages of some magnetic rocks. If our theory of radioactivity will change drastically these corro­borations may all wither away.)

It is difficult for me to decide how evident it is that all the developments of the kind discussed in the previous paragraph are bootstrap operations, that it is inconceivable that one hypothesis would be corroborated with­out taking another for granted and vice verca - always taking the most corroborated for granted to upset the other completely and replace it too. But I shall leave it as it stands for the time being.

VI.