On Criteria for the Economy of Science

A. K. Sukhotin

Science, however far it may go into the depths of abstraction, presents an aspect of human activity that has economic significance.

Of course, science owes much to society, but society owes no less to science. Researchers believe that up to 90% of the increase in the production of industrial output is a consequence of increased labor productivity; the latter, in turn, grows thanks to scientific and technological progress. According to world indicators of the effectiveness of scientific labor, the ratio of expenditures on science to the direct returns from the implementation of its results is 1:10. According to G. Kurakov’s calculations, for the Soviet Union one scientific worker (on average) contributes to an increase in output amounting to 50 thousand rubles per year. It is no accident that many West German, Japanese, and American firms have brought the share of capitalized profit invested in science up to 100%.

It would seem that, if science is so effective, it is more economical to invest funds in the development of science instead of expanding production itself (building new enterprises, increasing the number of workers, administrative and service personnel, etc.). However, the following becomes apparent. It turns out that the increase in the cost of scientific research is proportional to the growth of the square of the number of scientists participating in the research, while the growth of scientific output is proportional only to the fourth root of this number. Moreover, the volume of modern science has grown enormously, and it is deeply differentiated. Further, unlike ordinary production, in science it is difficult to foresee in advance the economic effect of its discoveries—or, in general, to commission a discovery—since science does not provide unambiguous answers concerning its future.

These and a number of other circumstances sharply raise the question of the “choice of science,” i.e., of the most promising branches, schools, and directions of research that carry the maximum economic effect. In connection with this, disciplines concerned with the science of science are developing rapidly: the economics and forecasting of scientific research. Attempts are being made to find criteria for the productivity and effectiveness of a scientist’s labor, so to speak, a coefficient of the usefulness of his output for society.

A quite natural approach seems to be the evaluation of the economy of a scientist’s labor by what his research gives to production¹.

However, along this path researchers encounter a number of difficulties. First of all, by no means all branches of science can be accounted for in terms of categories of productive efficiency. For example, purely theoretical sciences (mathematics, the field of fundamental physics, logic), the social sciences, the human sciences, and so forth. But this is not the only issue. Even within the limits of those sciences to which the criterion of productive efficiency is applicable, its use is made difficult by the circumstance that the economic effect is produced not directly by the scientific product itself (which is what we must evaluate), but only by the result of its technological applications. The introduction of science into production, however, does not depend on science. It is also necessary to take into account that a scientific discovery finds application in practice only after a certain (sometimes very considerable) time, whereas it must be evaluated, at the very least, when it is published (and still more desirably—at the moment of financing).

Taking this into account, researchers put forward, in evaluating the productivity of scientific labor, so-called “internal” criteria, which take into account not the effectiveness of science for production but certain characteristics of science itself. Such an approach seems legitimate to us. And the point, of course, should not be to oppose the “internal” criterion of science to the “external” one (its effectiveness in production), but rather to see them as complementary to one another. If a scientific product can be accounted for in terms of indicators of its significance for production, it should unquestionably be evaluated by that indicator. But at the same time the “internal” criterion should also be accepted.

Thus, we have two indicators of the effectiveness of a scientist’s labor. In both aspects the question concerns the economy of scientific research: in the first—in terms of the significance of science as a factor of economy in production; in the second—in terms of the search for the most economical paths of research, economical (from the standpoint of “internal” production and consumption) theories, laws and concepts, algorithms and operations.

The practice of selecting scientific workers by competition, the defense of candidate and doctoral dissertations, and the like, widely relies on such a criterion of the scientific significance of applicants as the number of publications. The productivity of a scientist’s labor is usually taken to be proportional to the quantity of his works. It is clear, however, that this criterion is in many respects inadequate, above all because it does not take into account the quality of the scientist’s output.

Apparently, while retaining the quantitative approach, this indicator should be supplemented by qualitative characteristics of scientific works. Such an attempt was once undertaken by S. G. Strumilin on the basis of the unit of value of scientific output he proposed: the sheet-point. This is one printed sheet evaluated in points: 1 point—for a satisfactory work, 2 points—for a good one, 3 points—for an outstanding one, 4 points—for a classic work. D. Price and others refine the criterion of qualitative assessment in terms of citation-frequency indicators; E. Weinberg—in terms of indicators of the influence of a discovery on adjacent branches of knowledge, and so on.

In this connection it seems possible to raise the question of criteria for the economy of science, proceeding from the considerations that in it there are ideas and solutions whose advancement and discovery have a fruitful influence on its development, promote the progress of science, and in this sense make these ideas and solutions economical, yielding a great cognitive effect, which in the final analysis also has an influence on the development of production. Perhaps it makes sense to reserve the concept of the economy of science for characterizing its “internal” cri-

theory, and in assessing its role for the development of production to apply the concept of the economic efficiency of science.

Thus, speaking of the efficiency of science, let us try to outline criteria for evaluating the significance of its products for the development of science itself.

This problem was posed by positivism. E. Mach took as the criterion of economy the minimum of mental energy expended on the construction of science. Neopositivism, having subjected to criticism the biologico-psychological interpretation of logical economy, adopted it in the sense of a minimum of logical and sign units within the body of knowledge. In defining the criteria for the economy of science, positivism of both tendencies commits a fundamental error by refusing to pose the problem gnoseologically. This leads to an incorrect understanding both of the criterion of economy itself and of its relation to the requirements of truth. The standpoint of materialism rests on the recognition of the ontological determination of the characteristics of economy and simplicity of knowledge—in particular, by such factors as the unity of nature, the invariance of its processes and phenomena, their symmetry, and their commonality.

We proceed from the view that the economy of science must be assessed not by how much effort has been spent on its construction (there are tasks and problems in solving which no expenditure proves excessive or superfluous), nor by how many logical and sign units (concepts, laws, assumptions) are used, but by taking as the criterion above all the very content of the knowledge obtained.

Practice and the theory of knowledge suggest that the most effective for the development of science are ideas and theories that carry general knowledge, that advance general methods and techniques for the solution of cognitive tasks.

It turns out, for example, that particular problems can be solved if they have been formulated as general ones and solved on the basis of general methods. In general, a concrete problem, when expressed in a general form, is solved more easily than by way of particular approaches. There is the so-called “inventor’s paradox”: it is easier to prove a stronger theorem than a weaker one. (Here, if proposition B follows from A, but A does not follow from B, then proposition A is considered stronger than B.)

Thus, for example, while solving the concrete problem of determining the composition of the crown (in order to ascertain whether it contained an admixture of silver to the gold), Archimedes formulated it as a general one (finding the specific weight of a substance of any kind) and solved it by discovering his famous law of specific weight. In analogous fashion, the problem of determining the distance from the Earth to the Moon was solved, formulated as the general problem of determining distances to inaccessible objects—and so were many other problems. In general, science often uses the following procedure: when an investigation reaches a dead end, an attempt is made to comprehend the concrete problem as a general one, to discover the condition for a general approach to it, and to formulate a general theory.

But what are the reasons why a general idea, a general solution, is more effective? First of all, a general formulation of the problem makes it possible to draw upon a broader range of ideas and methods—complex methods born in the border areas of the sciences—and to carry out deep analogies. Further, a general formulation of the problem results in its simplification (liberation from details and particulars that obscure the meaning). A well-known role here is played by the circumstance that an abstractly simplified formulation of a problem makes it possible to express it by means of a drawing; in other words, it helps to translate the conditions of the problem into a visual image. The point is that the objects of thought are apparently represented in the psyche in visual images, i.e., as researchers suppose (Newell,

Simon and Shaw), not only visual information, but also abstract information in general (arriving in abstract form) is processed in the brain thanks, so to speak, to an internal “mental eye,” i.e., according to the algorithms of the visual system. Moreover, it is known that vision is the sense organ with the greatest throughput capacity of its channels (in comparison with, for example, the ear–brain system, 33.5 times greater). Consequently, the transition to visual coding makes it possible, in solving a problem, to “actualize” enormous stores of visual information and thereby bring into action powerful additional resources from the stock of knowledge. This helps, in particular, to approach the problem from different sides, to modify it, and in general to comprehend it from the standpoint of a broader approach.

A general proposition proves economical because on its basis an entire class of problems is solved, within which the original problem turns out to be only one of the elements, and its solution no more than a consequence of the general approach. Thus, the discovery of a general method makes it possible to solve, “in one stroke,” a whole range of problems, for each of which—were there no general method—it would be necessary to find its own special solution.

Connected with this is the fact that general theories and ideas exert a profound influence on the development of science, stimulating the emergence of new directions and branches, and powerfully affecting adjacent fields of knowledge. Natural scientists long ago noticed the connection between the generalizing power of thought and its effectiveness. Thus, J. C. Maxwell, for example, regarded as most fruitful, as bringing real scientific success, that path of research which is connected with the putting forward of general hypotheses and ideas. A sufficiently general supposition, justified with respect to certain phenomena, may, he wrote, be confidently applicable also to the region of phenomena that interest us.^2

The more general an idea is, the more influential is its effect, and the more economical it is in its significance as a factor increasing the rate of progress of science. G. M. Dobrov (The Science of Science), investigating the rates at which chemical elements were discovered (as an indicator of the development of chemistry), notes that the discovery of elements proceeded especially rapidly in the 1870s of the nineteenth century and in the 1940s of the twentieth century, whereas in other years there was a slowing of the rate. This is connected, as the author emphasizes, with Mendeleev’s discovery of the periodic law of the elements at the end of the nineteenth century and with the development of new conceptions of the structure of matter in the 1940s of our century.

Thus, in solving a scientific problem, more than one variant is possible. But from among those that lead to the goal (and are equally true), it is reasonable to choose the most economical one, the one that brings the greatest cognitive success. This, however, is not the path associated with the smallest amount of mental expenditure, the shortest path leading directly to the goal, but the one that leads to the construction of a general theory capable of dynamism and expansion into neighboring fields of knowledge. The economical path is the one on which one is able to formulate a concrete scientific problem \((p)\) as \((P)\), so that for its solution it proves possible to find a method \(M\) such that \(M \to m\), where \(m\) is the method of solving the original problem; and \(P \to p\) (read, respectively: if \(M\), then \(m\), and if \(P\), then \(p\)).

Among the techniques of a general approach and a general solution to a problem are such as the “method of principles,” the “principle of the common cause,” the “method of causal necessity,” the “rule of variation,” and so on.

Thus, for example, the “method of principles” consists in the ability, when formulating a new theory, first to advance a minimum of general propositions, and then to try to show how properties and relations follow from them—

^2 See J. C. Maxwell, Matter and Motion. St. Petersburg, 1885, pp. 155–156.

of the objects of the subject area under investigation. General principles are introduced inductively, but not as empirical generalizations; rather, they are introduced as bolder assumptions. Newton already used this method; later it was developed in systems of hypothetico-deductive constructions of the sciences. Moreover, the broader the subject area (the more general the theory is), the more strongly the role of the “method of principles” increases.

In scientific cognition, so-called “approximate methods” of solving problems are widely used. The essence of these methods is that, in considering limiting cases, one abstracts from certain quantities of objects in order to obtain general values. Approximate methods are effective when an exact calculation entails a complication of the mathematical apparatus and is associated with great mental costs. At the same time, it is characteristic that an approximate (general) approach to physical reality itself underlies an approximate method, and this is reflected in the formulation of general physical concepts and a general theory. For example, in general the state of any physical system changes with time; nevertheless, if we abstract from this circumstance, we obtain the concept of the so-called stationary state, on the basis of which it becomes possible to apply approximate methods to solve a number of problems that are difficult to solve on the basis of an exact theory.

In the book The Direction of Time, H. Reichenbach proposes, in solving certain cognitive situations, to be guided by the so-called “principle of the common cause,” which may be regarded as a methodological rule connected with the requirement not to admit superfluous entities. The case of the concurrence of improbable events is analyzed. When it occurs, its probability proves to be greater than the probability of a chance concurrence. Then, to explain it, one must invoke the “principle of the common cause,” the essence of which is that “for improbable coincidences there must exist a common cause.”² For example, a lightning strike started a flame, and the fire is spread by the wind. The coincidence of fire and wind is improbable. Therefore, says Reichenbach, we seek a common cause—that is, a factor on the basis of which the simultaneous actions of fire and wind no longer prove improbable. In the given case such a common cause is the thunderstorm. One may say that here we have “economized” on hypotheses, explaining two phenomena on the basis of a single cause instead of postulating two.

In distinguishing two criteria of the economy of science—the “internal” criterion (an indicator of the generality of ideas) and the “external” criterion (the significance of science for practice, an indicator of the economic effectiveness of science)—we would like to draw attention to the fact that, in a certain respect, these criteria converge. In fact, theories that are economical in the sense of the generality of the proposed solutions and ideas prove to be economical (economically effective) also in the sense of their usefulness for the development of production, since they bring about profound changes in science and thereby also influence the development of applied research, stimulating the emergence of new technical branches and technological solutions. As Thomson observed, inventions bring about reforms in production, while scientific discoveries bring about revolutions.

1. See, for example, Proceedings of the Leningrad Polytechnic Institute, 1963, No. 227, pp. 187–192. ↩

2. H. Reichenbach, The Direction of Time. Moscow, Foreign Literature Publishing House, 1962, p. 214. ↩