PART C: Philosophical Theories of Problem Evaluation in Science
VIII.
I have classed problems into three broad logical types, according to whether they arise from inconsistencies, gaps or flaws in our knowledge system. I have introduced three kinds of factors which may contribute to our overall evaluation of a problem, namely, its expected impact on our knowledge, how much it will affect the actions we may wish to carry out, and the degree to which the problem is intrinsically puzzling. I have suggested that our choices of problems for inquiry are determined not only by our overall evaluation of the problem's importance, but also by our estimates of how likely it is that the problem can be solved at this time. Although there is a good deal of controversy about the extent to which decision theory correctly represents rational decision-making, my guess is that most philosophers of science would not object too strenuously to my classification of problems and the factors which enter into their evaluation.
What my framework deliberately does not provide are answers about how these factors should be weighted (should the epistemic value of a problem override its pragmatic value, or vice versa?). Neither does it tell us which types of problems seem to drive scientific inquiry. Do children evaluate problems differently than scientists do? Etc. What I will do now is use my framework in order to analyze and compare various philosophers' views about how knowledge grows.
Although most religions are quite Utopian in their images of the perfection to which people might aspire, they also are realistic enough to include within their theologies a quite robust concept of sin, which is regrettably admitted to be very much part of most mortals' lives. Traditional epistemologies are much less reality based. While admitting that belief systems in the past have contained serious mistakes, it is claimed that by the adoption of new scientific methods, error will be cast out forever. Both the empiricist Bacon and the rationalist Descartes believed that their respective methods would place scientific knowledge on new foundations - no belief would enter K unless it was certain to be true.
According to these optimistic justificationist epistemologies, there should be no occasion for problems arising from inconsistencies once science was properly underway. Not surprisingly, therefore, both Descartes and Bacon stress problems connected with filling in gaps. For Descartes, some of the gaps were deductive. Since the first principles were already known to us (obtained through Descartes' method of systematically doubting everything which was not clear and distinct), many propositions e.g., ones describing the movement of planets or the velocity of light, could be derived from them just as geometers could derive new theorems.
However, Descartes also realized there were explanatory gaps. In some cases, there were a variety of models which would explain the working of phenomena. If all of the models were consistent with the first principles, then experimentation would be needed to arbitrate between them. Descartes describes this situation succinctly using the example of a clock. We know immediately that it is powered by some mechanical device, but until we open it, we don't know exactly how the gears are arranged. All of Descartes' explanatory gaps are system bound - he never contemplated the possibility that the search for an explanation might lead us to break out of the received framework (e.g., that a clock might be powered by nuclear decay).
Bacon begins his account with an emphasis on the type of problem which I called filling in blanks. One has no theory, heuristic, no analogy which tells us what to expect. Thus, in the New Atlantis, half of the scientists are employed in passively collecting data. (The other half compile tables, try new experiments, interpret results, etc.)
When one looks at the details of Bacon's methodology, however, it emerges that all of this data-gathering is not totally random. First, one may pose a question (Bacon's example concerns the Nature of Heat) and collect instances related to it. And not all cases of heat are equally useful. Bacon has a rather detailed methodology of "prerogative" instances.
By focusing on one phenomenon (heat) and asking for the physically necessary and sufficient conditions for it, Bacon's methodology is really concerned with the search for explanations. Again, as was the case with Descartes, he does not anticipate that the inquiry may lead us outside of our present conceptual framework.
Thoroughgoing fallibilists, such as Popper, tend to stress the important role of inconsistencies in directing scientific inquiry. We always have problems arising out of violated expectations. And even when we do some deductive gap filling, one primary aim is to criticize existing theories, not just add to K. Popper also recognizes the search for deeper explanations of known regularities, but he mentions these less frequently.
Conventionalists, such as Duhem and Mach, placed great emphasis on the economy of thought provided by science. This would presumably make them very sensitive to problems arising from what I called systemic flaws. Some inconsistencies, such as the conflict between Copernican astronomy and Aristotelian physics need not trouble a conventionalist. If theories are really just convenient tools for categorizing and predicting, we can avoid conflict by judiciously restricting their scope of application.
Each of the philosophies sketched above picked a different logical type of problem as being of first importance in the rational development of science. If we look at historians of science, we find a similar variety of opinions about which evaluative factors have prevailed.
Marxist historians and some sociologists of knowledge emphasize the overriding effects of pragmatic factors on the problems which scientists choose to work on. Problems in navigation trigger inquiries into magnetic compasses and derivatively the general properties of magnets. Copernicus wanted to reform the calendar. Galileo discovered the phases of Venus while hoping to find more stars to name after the Medeci.
Note that this claim about social conditions affecting the choice of problems is much more plausible than the more radical sociology of knowledge thesis according to which the content of the solutions proposed is also strongly influenced by social and ideological factors.
Most historians of ideas on the other hand would see scientific problems being chosen because of their relationship to our knowledge system. Thus, a Burtt (Metaphysical Foundations of Modern Science), or a Koyre (Metaphysics and Measurement) see scientists responding overwhelmingly to the cognitive aspects of problems. Magnetism is fascinating because it appears to involve action at a distance. Although Galileo occasionally had to worry about money, his life's work has a beautiful coherence as he worked out systematic arguments and experiments concerning the Copernican theory, eventually developing a new science of motion. "Natural philosophy," as science used to be called, has its own internal standards for problem evaluation - these are almost completely independent of practical concerns.
If we look at the history of mathematics we will find many examples of problems which seem to have been chosen primarily for their interest as technical puzzles. As far as I can tell, the three famous problems of antiquity (trisecting the angle, squaring the circle, and doubling the cube) were of absolutely no practical value and very little fundamental conceptual importance. (Examples of practical math problems are the computation of complicated odds in gambling games or deriving the formula of the shape of a log chain whose ends are supported at different heights. Examples of conceptual problems include attempts to derive the 5th Euclidean postulate from more intuitive claims or 18th Century concerns about the status of infinitesimals.)
In principle, one can approach disputes about the relative frequency of problems of each type and the manner in which the various factors are weighted through empirical investigation. A few such studies have been done: for example, see Nick Mullins' flow chart of the contributions of pure vs. mission-oriented research in the development of the birth control pill. Not surprisingly, we find a continuous interaction between both kinds of endeavor, although the R&D aspects predominate at the end. I wouldn't expect any very interesting patterns to emerge, partly because the really good problem areas in science involve both the search for explanation and the removal of inconsistencies and are important for a variety of reasons, both pragmatic and epistemological.
Consider as an example, the problem of ballistics. Galileo was the first to describe the parabolic path of a projectile. This result was of immense importance in the pure science of mechanics because it involved a mathematical combination of the law of falling bodies and the principle of inertia. But it was also of practical importance to gunners. Tables based on Galileo's law were drawn up showing the angle above the horizon a gun should be pointed in order for the cannon ball to land a certain distance away.
We now ask what kind of research led up to Galileo's discovery, pure or applied? Interest in projectile motion goes back at least to Aristotle, but let us arbitrarily begin the story with Tartaglia, a 16th Century scientist-technician. Tartaglia was the first to discover a special case of the law of projectile motion, namely that the maximum horizontal distance was achieved when the cannon was pointed 45o above the horizon. (It is interesting to note that Tartaglia thought that his discovery would make warfare too dangerous, and so he burnt his notebooks. Later when the Turks were threatening Vienna, he revealed his military secret to the Duke.)
Although Tartaglia began his study of mechanics with a practical problem presented to him by a professional artilleryman, he solved it by using a variant of the medieval theory of impetus. Although he derived his result about maximum distance from an erroneous theory, experiments by gunners showed that his result was roughly correct (deviations were attributed to air resistance).
So the story goes roughly as follows: Tartaglia began with a practical problem (How can we make our cannon balls go farthest?), but used theory from pure science to obtain a result of practical importance. Galileo began with pure theoretical problems (What is the general description of projectile motion of which Tartaglia's law is a special case, and how is it related to both horizontal inertial motion and the vertical motion of falling bodies?) and arrived at a result of both pure and practical interest.
In this case, it seems pretty hopeless to try to apportion credit between the pure and practical motivations for scientific inquiry. Tartaglia started with a practical problem which turned out to be theoretically interesting. Galileo started with a theoretical problem which turned out to have practical import. Of course, it is possible that more extended historical research might tip the balance of one side or the other.
What are the implications of this science policy and the allotment of funds? First, there can be no platonic formula for the optimal allocation of funds between pure and applied research or between gap filling and horizon expanding inquiry. Each has played an important role at various junctures in the history of science and technology. It is best to pursue a mixed strategy, funding a variety of approaches to a variety of problems.
The framework laid down above gives us a description of the factors which should enter into policy decisions. The ideal problems would have far-reaching import for society's knowledge system (high K-value), have enormous positive practical implications (high A-value) and appear to be ripe for solution (high S-potential).
Estimating these factors can never be done with much reliability/accuracy. The K-value depends both on the details of the solution (which is not yet in hand) and its logical connections with the rest of our system, some of which may not be at all obvious.
The A-value is even harder to estimate, long-term practical consequences are notoriously difficult (and in some cases even impossible) to foresee (Cf. the problems in technology assessment). And before a solution is in hand, who can really say for sure how solvable the problem is?
Nevertheless, we can and do make judgments on these matters which are probably better than chance. Certainly there would be no excuse for concentrating public monies on boring useless problems just because they appear to be ripe for solution. It is just as silly to concentrate funds on urgent, important problems which we have reason to believe cannot be solved, at least at the present.
The extreme fallibility and variability of these judgments indicate the wisdom of having a plurality of funding agencies. And there should always be some "mad money" around for projects which receive eccentric or idiosyncratically high appraisals from generally reliable evaluators. In our discussion of science policy, we have been referring to community-based evaluations: How important is the problem for the knowledge and actions of society? But often individual scientists also have a personal stake in certain problems. During the Manhattan Project refuge physicists worked with special enthusiasm. Once he had been condemned by the Inquisition for his belief in the Copernican theory, Galileo was especially motivated to develop a new physics which would be consistent with the new astronomy. Convinced that his theory of mechanics and matter was correct and determined to overwhelm his continental critics, Newton worked with special zeal to derive a host of new predictions from this theory. Many medical researchers pick a disease because it has affected a family member. Dewey emphasized the importance of personal involvement for efficient inquiry. However, there are also dangers if the researcher has a high personal involvement in a particular solution to the problem. Thus, historians have argued that Galileo was blinded to flaws in his theory of the tides because of his pressing need to find a proof that the earth moved. And Newton's burning desire to predict parameters such as the speed of sound to the last decimal led him to fudge his calculations. (See Westfall's "Newton and the Fudge Factor.") The causes of self-deception and cheating in science are complex, but they are often related to some of the same values which also lead to heroic research efforts.