Scientists love to talk about how they do science. One product of this passion is the tendency to define with utmost precision all the terms we invoke in the doing of science, especially that magical incantation, "scientific theory." Recently Romer has written an article on how he tries to define this term to non-science students, ¹ which has drawn some critical comments from Brouwer.² I would carry the friendly debate one step further by suggesting that the exercise of defining "scientific theory" is simply not a worthwhile exercise for the physicist, either as a researcher or as a teacher, although it may be an enjoyable and even fruitful pastime for the philosopher.

Firstly, I would point out that a word or expression can be useful without possessing a precise definition. The word "big" is an excellent example. We all use it, although its definition is imprecise. It can be defined precisely, but to do so would be counter-productive; after all, there are more precise terms available ("tall," "heavy"), and yet "big" is a valuable word.

Secondly, precision does not imply accuracy. One of the most common ways of cheating in an argument is to look up some obsolete definition in a dictionary and flog one's opponent with it. A precise definition is accurate only if it agrees with usage, and an inaccurate definition can have serious consequences. Psychologists have learned this lesson the hard way. Most psychologists seem to agree that "intelligence" is simply a name for what intelligence tests measure, while we laymen use the word quite differently. Thus lay readers of psychological journals are often misled by their use of precise and inaccurate definitions, with serious social and political consequences.

A third important point is that scientists use the word theory in many different ways, and in most cases a theory might far better be defined as a model. Some of the most popular and universal approximate models in physics go by the names "single-particle theory," "continuum theory," "mean-field theory," "perturbation theory," "diffusion theory," and that grand old patriarch, "linearised theory." In some fields these constructs are merely computationally simpler forms of a more comprehensive theory; thus diffusion theory can be derived from the Boltzmann equation, classical physics follows by the correspondence principle from quantum mechanics, and linearised theories of course come from non-linear theories. In some fields, such as nuclear physics, a comprehensive theory cannot really be said to exist; different models are used for different calculations, and in fact different and quite contradictory theories may be used to calculate different parameters in the same calculation. Such usages might be referred to as "conditionally valid theories," and to use them one must know the conditions of validity as well as knowing the theory. For example, Newtonian mechanics is valid if all speeds are much less than c, and a = v²/r is valid if an object is undergoing uniform circular motion, etc.

A fourth point, not as directly related to Romer's article and Brouwer's comment, relates to the credibility of theories. Romer¹ observes that "... although the Ptolemaic theory was acknowledged to be a mathematical model, the early Copernicans looked on their theory as being not only successful but true." This is certainly debatable; the Tychonic system demonstrates that the greatest observational astronomer of the time felt that the Ptolemaic model was closer to "truth," while Copernicus' own caveats in the introduction to "De Revolutionibus," although perhaps not honest indications of his thinking, suggest that the comprehensiveness of his theory was important because of its practical utility, and not because it showed that it was closer to the truth. In fact, one of the most curious facts we have to offer our students is that scientists are quite ready to make use of theories they do not believe in. It can hardly be said that Einstein believed in the quantum theory, even though he was one of its greatest developers and practitioners. Most contemporary theorists agree that the relativistic field theory they use so heavily will be replaced by something better in the near future, and yet they continue to rely on it. The current controversy over whether evolution is a "scientific fact" or "merely a theory" points this up quite well. There is no real scientific content to the debate; even most creationists grant that evolution is a comprehensive and very successful theory.

I think that the prime criterion by which scientific theories are judged by scientists (not by philosophers or politicians!) is whether they are productive. I disagree with Romer's contention that the Copernican model replaced the Ptolemaic because it was more comprehensive; if so, it might well have been accepted when Aristarchus proposed it. Rather I think it was the impact of new discoveries in astronomy by Galileo and others that conflicted with the Ptolemaic model and demonstrated that the heliostatic theory correctly predicted what was in fact found. Theories become superseded (I reject Romer's use of the word rejected) because they are unproductive, not because they are wrong. For example, the Ptolemaic theory still provides the easiest way of finding planets with binoculars, and the caloric theory of heat is a good way to conceptualise thermal transport. If we really want our students to understand science, we should try to let them see how much mileage we can get out of the proper use of such rickety theoretical structures.

Some of the formal definitions that used to be invoked in discussions about scientific methodology appear to have faded from use, and we can well do without them; I am happy to say that it is a long time since I have been subjected to fastidious analysis of the progression of an idea from the status of "hypothesis" to that of "theory," culminating in its eventual enthronement as a "natural law." The word "hypothesis" rarely appears in current scientific literature, and the usage of "law" is more a matter of tradition than anything else; Bode's Law has no more profound status than the Special Theory of Relativity. A further semantic improvement might well be to down-play the word "theory," which we have such a compulsion to define, and rely more on the word "model," which perhaps far better conveys what we are really talking about. For example, Romer and Brouwer disagree on whether a theory should be inflexible. Perhaps it should, but if I have a useful model I don't want to lose it without a fight, so I want it to be flexible. The beauty of models is that they are less likely to be taken too seriously than are theories and laws.

Lest my remarks on Romer's paper, which I greatly enjoyed, seem unfair, I must point out that he does anticipate some of these points. Certainly his emphasis is on the desirability of comprehensiveness is well taken, and in fact many of the most popular models in physics, such as those based on linearised theories, have a universality that contributes much to the beauty of physics. He well recognises that "rejected" theories may not be discarded, as is beautifully stated in the last sentence of his article. But I would certainly agree with Brouwer that facts and inflexibility have rarely been as important to the scientist as to the philosopher, and it should be noted that Einstein, who was deeply concerned with the philosophical foundations of science, had an absolutely Aristotelian lack of concern for experiments that did not accord with his theoretical aesthetics.

Nor would I wish to convey the impression that it is not important to discuss scientific methodology with our students; indeed, I think that we have nothing more important to offer. But to do this honestly we must convey our true methodology, not an elegant abstraction. I personally feel that a precise definition of the term "scientific theory" is of no more value to a scientist than the definition of "colour" would be to an artist.

1. A. Romer, Am. J. Phys. 43, 947 (1973).
2. W. Brouwer, Am. J. Phys. 43, 184 (1975)

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