Front Page Titles (by Subject) CHAPTER II: WHY INQUIRE? - The Selected Works of Gordon Tullock, vol. 3 The Organization of Inquiry
The Online Library of Liberty
A project of Liberty Fund, Inc.
Search this Title:
CHAPTER II: WHY INQUIRE? - Gordon Tullock, The Selected Works of Gordon Tullock, vol. 3 The Organization of Inquiry 
The Selected Works of Gordon Tullock, vol. 3 The Organization of Inquiry, ed. and with an Introduction by Charles K. Rowley (Indianapolis: Liberty Fund, 2005).
About Liberty Fund:
Liberty Fund, Inc. is a private, educational foundation established to encourage the study of the ideal of a society of free and responsible individuals.
The copyright to this edition, in both print and electronic forms, is held by Liberty Fund, Inc.
Fair use statement:
This material is put online to further the educational goals of Liberty Fund, Inc. Unless otherwise stated in the Copyright Information section above, this material may be used freely for educational and academic purposes. It may not be used in any way for profit.
“The scientific process has two motives; one is to understand the natural world, the other is to control it.”1 Putting the same thought in slightly more mundane language, we undertake investigations because we are curious, or because we hope to use the information obtained for some practical purpose. These two motives roughly correspond to the general fields of “pure” and “applied” research.2 The correspondence is not exact, partly because human motives are seldom completely unmixed, and partly because the terms “pure” and “applied” themselves are not clearly distinguished in common use. What is “pure” research to one scientist may appear “applied” to another. In the interests of clarity, I shall use the term “pure science” for research which is motivated primarily by curiosity and “applied science” for that which is motivated mainly by a desire to obtain practical objectives.
It is the general opinion that pure science is somehow superior to applied science. This feeling, paradoxically, is usually justified by claiming that the long-run results of pure research are apt to be of practical value. It will be pointed out that various practical inventions are the result of pure discoveries at some time in the past, and it will be implied that similar results will follow from further pure research. This argument sometimes seems to point toward the conclusion that pure research is really a superior form of applied research. In fact, the general argument rests on something like an optical illusion. If we take any present-day discovery, practical or in the field of the most abstract theory, it will normally be based on a great number of previous discoveries. Some of these discoveries will generally be from the field of applied science and some from the field of pure science. It is always possible to select one of these previous discoveries and say quite truthfully that the new discovery could not have been made if this older discovery had not been made first.
The argument for pure science in terms of its practical results generally takes advantage of this fact. Some recent practical development will be singled out, a bit of pure research in the past which was part of the basis for the new discovery will be pointed out, and the correct statement made that the new discovery could not have been made without the earlier bit of pure research. In a sort of logical leap, the argument will then simply generalize this correct bit of particular description. It will be implicitly or explicitly assumed that this is the way all practical improvements are made. The same system, of course, could be used to “prove” the importance of applied science to pure science; there is a Marxist school of thought which does just that. All of the early advances in bacteriology, for example, were dependent upon the practical improvements made by lens grinders who built progressively better microscopes.
Consider some area of science. At some time in the past a number of discoveries were made—some pure, some applied. On the figure below these are shown by the nodes at the top. With the progress of knowledge, further discoveries were made—designated by the nodes in the network—and eventually we arrive today at the discoveries at the bottom. The lines connecting the discoveries show interdependence; that is, each discovery is dependent upon all previous discoveries with which it is connected.
The normal practice is to put in only part of the diagram; thus discovery A′3 will be connected to P3 by the heavy line, or perhaps a tree, such as shown by the dotted lines, will be drawn connecting P3 with all of its “descendants.” From this partial diagram it may then be argued that pure science is really more important than applied science. It would make just as much sense to connect discovery P′1 to A1 and thus “prove” the superiority of applied science. In fact, the tree of knowledge may be drawn with almost any discovery as its root and can be used to “prove” that pure discoveries, applied discoveries, or discoveries made by men named Brown are more important than any others.
It is undeniably true that new discoveries are based on older discoveries. Further, if all previous discoveries of a certain class, whether that class be pure science, applied science, or discoveries made by men whose name begins with C, had not been made, then the absence of these discoveries would significantly reduce our present rate of progress. Transistors, for example, were originally invented and developed by applied scientists.3 In their work, of course, they utilized previous discoveries, both pure and applied. Once transistors were available, they rapidly became important components of innumerable laboratory devices. These devices, in turn, made it possible to make still further discoveries, both pure and applied. Any of these discoveries made through the use of transistorized laboratory or computing equipment can be traced back to either the invention of the transistor or to some preceding discovery, pure or applied. Tracing the ancestry of the discovery back to any one previous discovery, however, is essentially illegitimate. Any discovery is the heir of innumerable previous discoveries, many of them applied and many of them pure.
Furthermore, the importance of individual older discoveries is less than is sometimes thought. Many things which were hard to discover in 1900 would be easily discoverable today. A researcher who finds himself in need of some given bit of information will normally be pleased to find it in some old scientific journal, because simply looking it up is usually easier than working out the matter experimentally in the laboratory.4 On the other hand, our present equipment, both physical and theoretical, is so much superior to that of 1900 that a present-day graduate student may be able, in a few hours of work, to duplicate discoveries which were major scientific advances in 1900. Thus, if some bit of research which could have been undertaken in 1900 was, in fact, omitted, a modern researcher who needed the information in his work would be handicapped by the omission, but might well be able to overcome the problem with little difficulty.
The practical importance of research in previous periods is exaggerated by the process of tracing back the history of important present-day discoveries. Research in previous periods which did not lead to anything which turned out to be important is automatically excluded from the sample by this procedure. The correct test of the practical importance of research would be to examine all of the discoveries in a given field, say chemistry, in a given year, say 1900, and see what percentage have had important further discoveries as “heirs.” For a test of the importance of pure research in developing practically important discoveries, it would be necessary to confine the original sample to cases of pure research. The experiment has not been performed, but I suspect that the percentage of discoveries of pure science which have not been made use of in any practical way would be high.5
The percentage would, naturally, vary from field to field. Astronomy, which can fairly claim to be the oldest natural science, has had practically no applications from its earliest discovery to the present.6 Mathematics, rightly called the queen of science, also has had relatively little application.7 At first glance this statement may seem absurd, in view of the domination of much of science by mathematical equations, but this is looking at the matter backwards. Physics requires large amounts of mathematical manipulation, but it does not follow from this that any large part of the total research in mathematics is utilized in physics. In fact, of all the work done by mathematicians, applied science has used only a fraction. As an example, consider Euclid’s elegant proof that there is no largest prime number. This is now over two thousand years old, but no one has made a practical application of it, and it is hard to see how anyone ever will. In fact, considerably less than half of Euclid’s propositions have ever been used in practical applications.
It is, of course, always possible that a practical man trying to do something practical will find that a mathematical system worked out by a mathematician is of great use. Leibniz developed binary arithmetic because he thought it proved the existence of God. It continued to be thought of as an impractical curiosity until the development of computers made it of the utmost practical importance. History would appear to indicate, however, that the development of pure mathematics will proceed more or less independent of practical use and that only a small fraction of the work of the pure mathematicians will ever find such a use. We can easily point to other fields where little or nothing in the way of practical applications can be expected. Archaeology, physical anthropology, and paleobiology are all perfectly respectable sciences, yet they have few practical applications. Even in such apparently practical sciences as physics and chemistry, there are numerous areas where few practical applications have been made.
The arguments justifying pure science by its practical results are really very weak. It seems reasonable that a given amount of resources will have more practical effect if it is put into applied research rather than into pure research, although pure research is likely to have at least some practical results. This does not, however, indicate that pure research is undesirable. Curiosity is a legitimate motive. Personally, I am very curious about conditions on the moon and the various planets and would favor their exploration even if I were convinced (as I am not) that no single discovery capable of practical application would result. It should merely be kept in mind that pure research is an effort to learn more about the universe just because we want to know. It is not a superior way of obtaining practical results.
Nor is there any real justification for the general tendency to consider pure research as somehow higher and better than applied research. It is certainly more pleasant to engage in research in fields that strike you as interesting than to confine yourself to fields which are likely to be profitable, but there is no reason why the person choosing the more pleasant type of research should be considered more noble. It is probably true that there are some differences between the personalities of people engaging in pure research and those in the applied fields. Most scientists are interested both in their own living conditions and in their work. The relative weight given to those two considerations will vary from person to person. Those who put the greater emphasis on the material returns from research are likely to enter the applied field, while those more interested in the research as a thing in itself will likely engage in pure research. Persons who regard concern with things here below as somehow mean and earthy will thus tend to feel that pure researchers are superior. On the other hand, it can be argued that pure researchers are more egotistical, pointing their research toward satisfying their own curiosity rather than benefiting humanity. There is, in fact, no reason8 for feeling that either group is superior to the other. Einstein and Edison were both great men; let it go at that.
There is one sense, however, in which pure research is probably more productive than applied. In our present-day world very large amounts of resources are put into applied research, while pure research attracts considerably less money, particularly because a good deal of applied research is currently misclassified as pure. Granting that returns on research effort on a given subject at a given time are subject to diminishing returns, the marginal return on a given amount of effort in the pure field (in terms of discoveries, not in terms of monetary value) should be greater than in the applied field. It is probable that the pure fields of research are always a little behind the applied fields, and thus that progress is somewhat easier there. The spearheads of advance are probably normally in the applied fields rather than in pure science.
The popular belief that the reverse in the case is another example of one-sided reasoning. Both pure and applied researchers are normally working in fields which are separate. Both tend to use discoveries made in the other field some time ago. By pointing only to the indisputable fact that the pure scientist is engaged in research which is not being duplicated by applied researchers and the equally clear historic fact that applied scientists frequently make use of prior discoveries made by pure scientists, an apparent argument for the primacy of pure science can be made. But, since the applied researchers are also engaged in work which is not being duplicated by the pure sciences, and it is historically clear that pure scientists have frequently made use of discoveries by applied science, the reverse argument would be equally cogent. Reasoning from such sets of individual examples thus leads nowhere. It seems likely, however, that the marginal productivity of research effort in the two fields would vary inversely with the amount of effort in each. Thus, if we concentrated 99 44/100 per cent of our scientific effort in the field of pure science, the applied results of the remaining 56/100 per cent of the effort would probably be disproportionately great. Under present conditions, with the greatest efforts going into applied science, the reverse is probably true.
The simplest and clearest example of the dependence of pure science upon applied is the great boon which pure science has received from developments in the field of measuring devices.9 In addition, the production of laboratory equipment is now a major industry. The November 8, 1963, edition of Science, for example, contains over two hundred pages of advertisements of laboratory equipment. This is, of course, one of the periodic “Instrument Guide” issues of that journal, but the pages of almost any scientific periodical of good circulation will be filled with the advertisements of the equipment manufacturers who have engaged in applied research in the development of laboratory equipment. It ill becomes the pure physicist whose work is possible only because a group of engineers employed by High Voltage Engineering have developed and put into production a tandem Van de Graaff to deny his indebtedness to applied research.
Note that this is not an argument for more resources for pure science. The decision as to how much we put into satisfying our curiosity and how much into improving our technology can be reached only on extrinsic grounds. If the American voter is actually not very curious and is interested only in the practical advantages of scientific advance (and the efforts to justify pure science on practical grounds might be taken as evidence that the advocates of pure science believe this is so), then we are investing too much of his resources in pure science. Decisions as to whether a given amount of resources should be put into pure or applied science can be solved only in terms of the ends which the persons making the decision wish to reach.
Turning, however, to the effects of these motives on research, applied research immediately confronts a major problem. Inquiry is, by definition, concerned with the unknown. A man instituting an inquiry can never know for certain what will result or even if anything will result. Thus, it might appear impossible for anyone to undertake research aimed at some given end, and hence that applied research is impossible. Actually, most economic actions are taken under conditions of imperfect knowledge and under circumstances where the outcome cannot be known with certainty.10 In this respect applied research does not differ from other forms of economic activity. Decisions on necessarily imperfect information must be made, and those who tend to make such decisions in such a way that they are successful will make large gains; those who tend to be wrong will have losses.11 The problem is simply that facing any person deciding how to expend resources. Whether a filling station on a given corner would be a wise investment and whether it will be feasible to produce a plastic with certain characteristics are questions of the same sort. Both involve some known and some unknown facts; both require guesses as to the unknown facts; and our historic experience would indicate that there are some people who are better than others in making such decisions. In this field the research director is, like any entrepreneur, simply a well-informed man making decisions without complete information. Certainly he will be wrong on occasion, but so will any other person who tries to decide on the best use of resources.12 In recent years a specialized type of entrepreneur who is good at guessing what can be invented and sold has developed, and whole companies, particularly in the electronics field, are built upon this type of entrepreneurship.
Of course, many practical inventions and improvements are made as a sort of by-product of the production process without any significant advanced planning or investment of resources. A workman will occasionally find an improved way of doing something or a way of making an improved product even if he does not invest any serious amount of time or effort in the search. More importantly, the management and supervisory personnel are likely to think of new ways of meeting their problems. Thus a continual, although slow, trickle of new techniques and devices can be seen throughout the whole history of the human race. This almost automatic process of invention, however, has been supplemented in recent centuries by the conscious process of directed research. Time and material resources are devoted solely to the process of making new inventions. Today this special form of “investment” takes up a significant part of our capital investments.13
This change, and it could be called a revolution, in the genesis of invention is largely the result of the development of the patent system. A patent is simply a legal monopoly granted by the state to the inventor of a new device. It has always disturbed economists because it has all of the disadvantages of an ordinary monopoly.14 The argument for it has always been that the advantage which it gives in rewarding invention much more than counterbalances the disadvantage inherent in monopolies. The issue is not easy, but most economists rather unhappily vote for the patent system while hoping that someone will invent a better social device. This is not, however, a book on economics, and I will leave this debate to the economic journals. For our purposes we need only note that patents exist and then turn to a discussion of their role in promoting applied research. It is a notable one.
Consider the situation prior to the development of patents (in the modern meaning of the term). Governments then normally approved inventions and technological improvements which resulted in new products. Sometimes the new product might be thought undesirable for some reason, but generally it was accepted with gratitude. On the other hand, inventions which simply eased the method of production of existing products were usually frowned upon. The fear that labor-saving inventions will result in widespread unemployment is as old as history. Its continuance today may be taken as one more indication that what we learn from history is that we do not learn from history. The Emperor Claudius’s rewarding an engineer who had developed some machines for reducing the manpower needed in construction and, at the same time, his prohibiting their use may be taken as a humane application of this fatuous policy. One of the great advantages of the modern patent system lies in its failure to distinguish between these two types of invention.
Without patents, a man considering investing time and money in some sort of economic enterprise would seldom consider applied research as a likely alternative.15 Any new product or process he discovered could be immediately copied by others. Thus the innovator would have spent his time and money in producing something which largely benefited others. Only if the new process was such that it could be kept secret (products, of course, could not be kept secret if they were to be sold; but a new product might involve a new process which could be kept secret) would research directed toward producing it be likely to be profitable. Under the circumstances research would be almost entirely devoted to the development of processes which could be kept secret. Only a small fraction of all possible inventions fall in this category. Consequently, there was little planned investment in research in the age before patents.
Even if some early entrepreneur did undertake research leading to the discovery of a process which could be kept secret, the necessity of keeping it secret would generally greatly reduce its utility. It could normally not be used on any great scale, because that would require letting too many workmen know how it was done.16 Normally, also, the process could not be dispersed to a number of geographically remote producing centers for the same reason. Thus the profit derived even from some process which could be kept secret would likely be less than the profit obtained from a patent on the same idea, and the incentive to undertake research would be proportionately less.
The disadvantage of the pre-patent system of keeping new inventions secret, however, has still not been fully pointed out. The advantages gained from any new invention can be divided into two categories: the direct advantage gained from its application and the indirect advantage gained from the increase in knowledge. The new device or process or one of its underlying principles is likely, in the long run, to have even greater effect through its intellectual descendants than through its direct application. Each discovery makes further discoveries just that much easier. If, however, the discoverer keeps his discovery secret, then no one else is able to use it in making other discoveries. Thus the simple act of keeping it secret deprives the human race of much of its advantage.
The patent system is not, however, used in all fields of applied science. There are many areas where it is impossible to collect royalties from the users of new discoveries. In agriculture, for example, many discoveries simply take the form of improvements in such things as crop rotation, spacing and arrangement of plants, and proper mixture of fertilizers. It is not feasible for a man who has engaged in research and discovered that corn crops may be increased if fertilizers are mixed in a certain proportion under certain conditions of soil and climate to collect a royalty on the use of his idea. Individual farmers need merely order the various fertilizers from other dealers and put them on the crops in the desired proportions in order to get the full benefit of his idea without paying any royalties. Even if our patent laws permitted patents on such discoveries, the policing problem would be impossible.
The consequence is that private individuals who invest in research in such an area are not able to regain the costs of their research and therefore will not undertake it. Their situation is the same as that of any inventor without the protection of patents. The only way of obtaining new discoveries in this field is by some kind of collectively financed research paid for by all the farmers. As a rule, this means state-paid-for and -directed research. The fact that research in the agrarian field is largely governmental rather than private is perfectly logical.
It should be noted, however, that the dividing line between the areas where some kind of governmental research is necessary and the areas where private research may be relied upon does not exactly correspond with the division between agriculture and industry. Farm machinery, for example, has been largely developed by private inventors. Further, although most new and improved strains of crops or livestock come from government laboratories, there are occasional exceptions. Hybrid corn, for example, was certainly the most significant new “strain” of modern times, and it was developed entirely by private entrepreneurs. The difference is easily explained. Most improved seeds for a given crop will breed true. The farmer who has bought seed for one year is in a position to use his whole crop to compete with his original supplier in the second year.17 In the case of hybrid corn, however, this is not true. A farmer who was so foolish as to plant the crop he got from hybrid seed in the expectation that it would give equally good results would be sadly disappointed. The hybrid seed for each crop must be produced by a separate hybridization process, and the developers of hybrid corn, therefore, could and did make a large return on their investment in research. The profit was much less than would have resulted from a patent, however, since other breeders could duplicate their “strain.”
Outside agriculture, too, there are areas where applied research would appear to be called for but where the result would be unpatentable. Management techniques and sales methods provide examples. Under present conditions, relatively little serious research is devoted to these problems. Government-sponsored research does not provide an answer here, since the people who would initially benefit from the research do not have the political influence of the farmers and cannot hope to get large appropriations for this purpose. In these fields we are little better off than in the period before the invention of the patent. We do, of course, make progress, but we would make much more if some better way of rewarding the inventor could be developed.
A man interested in some particular bit of applied research may hire someone else to help him or even to do the whole thing. Under these circumstances very difficult problems of supervision may arise, but there is nothing which is particularly distinctive to research about them. A man desiring to accomplish anything who hires someone else to do it must remember that the other person is motivated not by a desire to carry out the project, but by a desire to earn his salary (in favorable cases, he may share the employer’s interest in the basic project). If he can continue to earn his salary while switching his work over to a field which interests him more or which will require less work, he is likely to do so. Some types of jobs, and research is among them, offer exceptional opportunities for this kind of thing, but all we can say is that supervision under such circumstances will be difficult and probably not wholly efficient. Scientific research does not differ from many occupations in this respect.
The major industrial laboratories, full of hired scientists doing various applied projects, are a major and important part of our scientific resources. Nevertheless, many of the scientists are dissatisfied and want to improve their social status by being pure scientists.18 The managers of the laboratories, interested in getting their research done at the least cost, may provide facilities for genuine pure science, if this permits them to hire scientists at a wage rate low enough that the savings will pay the cost of the pure projects. Sometimes, also, managements impressed by the propaganda about “social responsibility” will actually feel that pure research is their duty and undertake a little of it. Normally, however, the pressure of the stockholders, who want dividends, and competitors, who are continually coming out with new products or cutting prices, will force industrial laboratories to keep pretty close to research having direct practical applications. This pressure is weaker in companies having substantial monopoly powers; pure research is more likely in such areas.19
Another technique which has been frequently resorted to involves a slight change of definition which makes certain types of applied research “pure.” Thus, a laboratory trying to improve some device will find that further work requires information which is not now available—let us say a table of values of some physical constant. The compiling of this table, in spite of its eminently practical motivation, can be called pure research and thus may raise the social status of the men working on it.
Another type of applied research likely to be termed “pure” by people doing it involves the investigation of some particular field of research in hopes that something useful will be found. Thus DuPont, in the 1920’s, hired a distinguished chemist to go through a certain class of chemicals looking for something useful. Since he found nylon, this can be listed as one of the most spectacularly successful pieces of applied research in modern history. The whole process, however, was called pure research. It was called “pure” partly to raise the status of the researcher, who would probably have insisted on a higher salary if he had been told he was to do applied work, and partly because he was, in fact, given no very specific instructions. The management (and the chemist) felt that there were probably commercial products somewhere in the class of chemicals and were willing to pay for an investigation. If the chemist had found nothing useful, he would most certainly have been switched to another area (or fired), no matter how significant his discoveries were in terms of increasing our knowledge of the universe.
In 1958 Dr. John Grebe, director of nuclear and basic research for the Dow Chemical Company, presented a basic theory about the nature of the nucleus. The theory has attracted relatively little notice, probably because it turned out to be incorrect. For our purposes, however, it is interesting that he did his work on it at home on his own time.20 This was genuine pure research, inspired by his own dissatisfaction with the existing state of knowledge, and he realized that it was not the kind of thing which he could include in the company’s research budget.
Another related type of applied research which may sometimes be designated pure involves hiring some scientist who is believed to be particularly likely to make commercially useful discoveries and simply letting him do what he wants as long as the results are good. The Bell Telephone Laboratories seem to operate on this principal to a considerable extent.21 Excellent personnel are hired and very good facilities are provided. In theory, the scientists (or at least some of them) are free to investigate anything which strikes them as interesting. To read some of the descriptions of this laboratory, one might think that the fact that the overwhelming majority of the results have something to do with communications was purely coincidental. In fact, of course, the heads of the laboratory know that they must justify their budget appropriations in terms of output, and individual scientists know that they must make discoveries which are of enough use to pay their salaries. The whole thing is an exceptionally well-run applied-science laboratory.
Turning now to pure research, i.e., research undertaken to satisfy curiosity, we can distinguish two extreme cases. Robert Boyle, a wealthy man, equipped a laboratory and pursued highly important research as a sort of hobby. We may regard this as an example of pure curiosity research. At the other extreme, all universities have on their faculties people who do research and produce articles simply because that is the way they earn their living. They may actually have very little interest in the subject of their investigations and will abandon their researches without a single pang of regret if they are offered a better paying job doing something else. This is an example of induced curiosity. Most real-life pure research lies somewhere between these two extremes, of course, but we can simplify our discussion if we consider the two extreme cases separately. The intermediate situations which are commoner in the real world can then be thought of as varying mixtures of the two pure cases.
Induced research is a relatively recent development, and we can profitably follow the historic order and discuss pure curiosity research first. An investigation of the psychology of a selected list of eminent scientists resulted in the following description of their motivation:
Once it was fully understood that personal research was possible, once some research had actually been accomplished, there was never any question. This was it. . . . There has been no question since. From then on absorption in the vocation was so complete as seriously to limit all other activity. . . . Although a few of them have cut down on their hours of work as they have grown older, it is still the common pattern for them to work nights, Sundays, holidays, as they always have. Most of them are happiest when they are working. In all of these instances, other aspects—economic return, social and professional status—are of secondary importance.
Being curious plays a major role. . . . It is of crucial importance that these men set their own problem and investigate what interests them. No one tells them what to think about, or when, or how. Here they have almost perfect freedom.22
Most of these scientists, of course, were making their living by their scientific activity. For the truly curious, however, this is a relatively minor consideration. They have found an occupation in which they are paid for doing what they would do on their own if they happened to have inherited a fortune. In a sense they are hired to play. If we take the normal economic concept of opportunity costs, they may in fact be “paying” sizable amounts for the privilege of engaging in research. Some23 of them, certainly, could make considerably larger incomes by applying their abilities with equal diligence to some other line of work. Thus they actually do make a monetary sacrifice to engage in research, just as Robert Boyle reduced his expenditures on luxurious living in order to support the specially trained artisans who produced his equipment. Since they obviously enjoy their work, they are maximizing their utility, but not their income. Their basic motivation is curiosity, not making money.
We can divide the curiosity which motivates a pure researcher into two general types: general curiosity and particular curiosity. Most scientists will be found to be generally curious (at the least in the general field in which they operate, but more normally about the whole universe), but particularly curious about the solution of some problems upon which they are currently working. It is my belief that the particular curiosity which leads a scientist to undertake a given bit of research is always the outcome of his general curiosity. His general curiosity leads him to arrange to have a sizable information input, through reading journals, attending meetings, etc. This information input resolves some of his curiosity, but it will also occasionally suggest to him research which he could undertake which would further satisfy his curiosity. The result is the development of particular curiosity in a given problem and a specific research program. Thus the scientist’s curiosity is subject to social guidance. The information inputs from other scientists are important in shaping the problems which he will investigate. Similarly, he is normally interested in the approval of his peers and hence will usually consciously shape his research into a project which will pique other scientists’ curiosity as well as his own.
The situation can be readily explained with the aid of an economic analogy. A stock market speculator is, presumably, interested in making money through buying and selling stocks. He usually has little concern with which stocks. Nevertheless, opportunities for profit normally occur in various individual stocks, and the speculator must make his money out of such opportunities. He thus keeps well informed on conditions in the market and looks for opportunities to make money in individual stocks. His specific operations will always involve only a few stocks, but they arise naturally from his interest in using the whole market as a source of gain. Similarly, the man seeking to satisfy his curiosity will keep informed of developments in the whole field about which he is curious, but will undertake specific investigations only when he thinks he sees an opportunity for particularly fruitful discoveries. Like the stock market speculator, he may be wrong, but he generally receives a sort of consolation prize in the form of at least some new information.
This, it should be noted, is a major advantage the pure scientist has over the applied scientist. The applied scientist may fail. It may turn out that he cannot make the device or carry out the process toward which he aims, and that his effort, therefore, does not reach its goal. The pure scientist can hardly fail in this sense. His research will always lead to some result which satisfies his general curiosity even if it is completely unsuccessful from the standpoint of the particular curiosity which inspired the particular project. Thus, the famous Michelson-Morley experiment was an effort to discover certain characteristics of the movement of the earth with respect to the “ether.” The results simply did not make sense in terms of the physics of the day; they implied that the earth was stationary. The long-run effect of these completely unexpected results was the elimination of the “ether” from the “world view” of the physicist.24
Although particular curiosity comes from general curiosity, it may develop a life of its own. Thus a man who is curious about nature in general is likely to specialize his curiosity into some selected segment of the whole universe of potential knowledge. This segment itself will normally be pretty broad, although its width will vary from person to person. It may shift considerably during the life of any investigator. Within this segment, an ingenious and highly motivated investigator will see specific opportunities for increasing his knowledge and undertake corresponding specific investigations. This involves the particular curiosity which we have been discussing. In most cases, this particular curiosity is transitory, being readily replaced by something else if the investigation is successful or if it turns out to be a failure. Sometimes, however, the investigator becomes emotionally involved with a particular problem and subordinates all other interests to it. Usually, such involvement occurs only with difficult problems and, consequently, some of the most important advances in science have come from such a situation. Kepler’s work25 will do as an example. Simple problems can usually be solved quickly enough that the investigator does not have time to become obsessed. The more difficult problems usually take more time and are thus more likely to trap their investigators. Since the solution of such difficult problems is of greater importance than the solution of the easier ones, the emotional involvement of the researcher with his problem has, perhaps, received undue emphasis in accounts of the development of science. Not only have some important scientific advances occurred when the investigator was not deeply involved in the particular problem (the special theory of relativity, for example), but the bulk of the minor advances which make up so much of science have occurred without any deep emotional involvement between the scientist and his subject.
Once he has made a discovery, the scientist who is primarily motivated by curiosity is rather apt to want to tell people about it. He is probably proud of the discovery, and like the rest of us, he enjoys the approval of others. The successful investigator will normally discuss his discovery with all whom he can get to listen and may carry his enthusiasm to the point of acute boredom for most of his listeners. In most cases the circle of people who will be interested is quite narrow, but this narrow circle is composed of the people best qualified to judge the discovery.26 From the standpoint of the development of our knowledge of the universe, this is of great importance. It is highly important that new discoveries be circulated rapidly. Further, the desire of the scientist for the approval of his peers provides a slight but real social control over his choice of problems. Unless the discovery he makes is of interest to at least the specialist, he will find it hard to get people to listen and approve his results. Sometimes this element of social control is unfortunate. Gregor Mendel was surely one of the greatest scientists of the nineteenth century. He is famous for only one set of experiments, however, his discovery of the foundations of modern genetics. After making these truly epoch-making discoveries, he gradually moved out of science and became abbot of a small monastery. Surely his complete inability to interest the biologists of his day in his discoveries27 was one of the major factors in this shift in his activities.
A man engaged in satisfying his curiosity may hire assistance just like anyone else. We may distinguish two cases. In the first, the employee is hired to engage in specific research. Thus a junior scientist may be expected to make various minor investigations which his senior directs. The situation does not differ very much from that found in many industrial laboratories. The ultimate end aimed at, the increase of knowledge for its own sake, is different, but the means and the relations between the participants are the same. Another method of getting people to do specific research in return for monetary rewards is simply to offer a prize. The most famous example of this technique was the prize offered by the British Admiralty for an accurate chronometer after the destruction of Sir Cloudesley Shovell’s fleet off the Scilly Isles.28 This was an example of applied research, but the same technique could as well be used in the pure field. Occasionally someone interested in some specific problem does offer a prize for its solution.
The use of monetary rewards to get scientists to investigate specific problems which the provider of the money is curious about, however, is of no great significance in modern pure science. More commonly, an effort is made to stimulate the curiosity of the hired researcher. Since this technique is so important to the organization of modern science, I will give it a special name—“induced curiosity.” There are two general methods to use. The first, and less important, is simply to offer a prize for the best work in some field. Thus there is an annual prize for the best paper concerned with gravity, and the Journal of Political Economy used to offer a prize for the best published article each year. The Nobel prizes, in a sense, are examples of this technique. It is important to distinguish this from the offering of prizes for specific discoveries. I am particularly curious, let us say, about the chemistry of silicon. As a way of satisfying my curiosity, I offer a series of prizes for the synthesizing of certain designated possible compounds of silicon. This is using the prize system to obtain research in specific fields which I have selected. The alternative would be to offer the same prizes for the “best” research in silicon chemistry. In the second case, I do not designate the specific research to be carried out. The researcher hoping to win a prize must not only carry out research, he must first decide what research is most likely to be important. Thus I have “induced” curiosity in him and hope to benefit from it in having my own curiosity satisfied.
Unfortunately, this method of inducing curiosity is relatively little used. The more common method consists of hiring an investigator and making his continued employment contingent upon his obtaining significant discoveries.29 As compared with the prize system, this device has disadvantages. The curious person who has decided to spend funds in satisfying his curiosity must choose his investigator. Thus his efficiency as a personnel manager and the various chance factors which always affect the hiring of individuals will be reflected in the results. Advertising a prize and letting anyone who wishes make investigations in that field will normally lead to a sort of self-selection by a very wide group of people, and only those who think themselves30 specially qualified will make the attempt.
In practice the system has become entangled with the educational system, which has its disadvantages. Before discussing this, however, it is necessary to turn to a special situation which does not depend upon induced curiosity, but which appears to. Let us suppose that a wealthy man (or institution) is curious about colloids. He (or it) finds a poor man who is also much interested in colloids. The wealthy man (or institution) gives him an honorarium so that he can devote his full time to satisfying his curiosity. Under these circumstances, which may be considered ideal for research, there is no induced curiosity because the curiosity was already there. It is a case where both parties are permitted to do as they wish and find that, through accidents, their wishes coincide.
In many cases of induced curiosity, an effort is made to pretend that the above situation exists. It will be maintained with every appearance of sincerity that research workers work because of their interest in the problems with which they deal and that they are employed not simply for that end. Doubtless most scientific workers, like most workers in other fields, are in fact interested in their work. Most men act out of a series of overlapping motives, but that the dominant one in this case is the system we have described as induced curiosity can be readily seen by examining the real situation. In the first place, the people who hire academic personnel in scientific fields where research is turned out make no bones about using research results as a major criterion in hiring and deciding whether to continue the employment of their subordinates. The faculty members themselves seem convinced that academic success is highly correlated with “publication”31 and will usually explain promotions and demotions largely in these terms.
The system, however, is in other ways badly designed to get the best out of inducing curiosity. In the first place, the research is subsidized as a sort of by-product of education. Instead of hiring people who are thought to be good investigators to do research, they are nominally hired to teach and are required to devote a good deal of time to that end. The organization of the researchers and the number employed are entirely controlled by the needs of the university system. Thus the national balance between investigators in economics and physics is heavily influenced by the number of students who elect to enroll in courses in these two fields. The geographical distribution of various types of physicists is also controlled by the needs of the educational system. They are spread across the country in a pattern determined by the needs of universities rather than the needs of research, and men in the same branch of work may see each other only at the yearly meetings of the societies to which they belong.
Furthermore, the people who hire them are not directly interested in their work. The number and length of published papers are highly important, but the authorities responsible for hiring and firing are frequently not sufficiently interested in the subject covered to even bother to read them.32 The whole responsibility for evaluating research, in essence, is left to the editors of the learned journals. If research is good enough to be published in a respected journal, it is assumed to be valuable on that evidence alone. This delegation of authority by the real employers to editors, who, to say the least, are of widely varying abilities, would appear to be unlikely to lead to good results.
The present university administrators themselves, however, would be rather poor people to put in charge of deciding what research is important. Most are little interested in the results of research, although they feel that good research is necessary to maintain the prestige of the university, and many have the common man’s attitude of respectful admiration for “science.” If the administrator has come up from the research side, he may retain his interest in his particular field but is unlikely to be much more concerned with increasing knowledge on the interrelation of American Indian languages than is the average man. His real interests are administrative, particularly getting more money (he may be able to develop great enthusiasm for “science” if he thinks that this will increase his take). All of this is not to denigrate such men. They are necessary for the advancement of science, and their continual concern for getting more funds is of the utmost importance for the advancement of research. It is simply to say that the present scheme under which they do not have much to say in determining the relative merits of various investigators is not as irrational as it might appear.
Who then does decide? At first glance, it would appear that the editors of journals fulfil this function. In fact, although they are important, they fill a subordinate role. I could not turn myself into a power in chemistry by the simple expedient of starting a journal. The ultimate control lies in the hands of the readers. Every scientist who is really curious about his field reads a good deal of material in it. Although he probably does not read any one journal from cover to cover, he reads in a good many. Thus, although he may not have read any individual piece of research by a given other investigator, he can tell something about his ability by noting what journals have published his work.
The scheme works in somewhat the same manner as the market economy.33 The individual scientists are both producers and consumers of research, producing on a specialized basis the results of their particular curiosity and consuming results of others’ particular curiosity in order to satisfy their general curiosity. Each one, by subscribing himself, or influencing institutions to subscribe, to journals and by making the type of statements which build or demolish reputations, contributes his mite to the importance of each journal. The editors of the journals are thus motivated to do their best to select the best articles from among the contributions they receive. Since the most prestigious journals usually get first choice of articles, a sort of hierarchy of excellence is established, and the general scientific worth of a man can be, in fact, approximated by simply counting the number of publications he has had in various journals.
This chapter started with the assertion that we inquire to satisfy our curiosity or to obtain useful information. I should like to point out that the two motives are not mutually exclusive. A man can be motivated to the same investigation by considerations of both types. The relative weight of the two motives obviously varies vastly from case to case. Further, though these two motives are the characteristically scientific ones, most investigators have also been motivated by various other subordinate considerations. Some of the early scientists were under the impression that they had been directly ordered by God to undertake their investigations. More importantly, a good many researchers get a good deal of amusement out of their investigations. The aesthetic side of science should not be ignored. Mathematicians in particular seem to be heavily motivated by the beauty of their work, but most scientists get at least some aesthetic satisfaction from their subjects. All of this is to say that man is a complicated animal and his motives are many and varied. The two motives of curiosity and a desire to make practical application of new knowledge, however, will be found to be more intense among scientists than among the rest of the population and may therefore be used to distinguish science from other activities.
[1. ]Charles Snow, “The Two Cultures: A Second Look,” Times Literary Supplement, October 25, 1963, pp. 834–44, at p. 840. Lord Snow does not, of course, claim any originality for this thought. He is simply presenting the orthodox doctrine in his usual lucid English.
[2. ]Sir George Thomson, “Two Aspects of Science,” Science, 14 (October, 1960), 996–1000.
[3. ]See note 21 below.
[4. ]The so-called “data explosion” has made it sometimes very difficult to get information out of the “literature.” The time taken to search through the library for some bit of knowledge may be less than the time taken in rediscovery. This problem will be discussed in Chapter IV.
[5. ]Professor B. R. Williams, in a paper read to the economics section of the British Association on September 4, 1956 (“Science and Industrial Innovation”), estimated that even among those scientific ideas which “are adjudged worthy of industrial research ten or less will be proved worthy of industrial application.”
[6. ]In a sense, astronomy was, from the first, used for practical matters in the form of astrology. More significantly, navigation and timekeeping have used minor parts of astronomy, and astrogation may shortly use more. Chemistry and nuclear physics have also owed minor debts to astronomy. Nevertheless, only a tiny bit of the work of the astronomers has had any effect on human affairs.
[7. ]See Michael Polanyi, Personal Knowledge, p. 186, and G. H. Hardy, A Mathematician’s Apology (Cambridge: Cambridge University Press, 1940), pp. 71–83.
[8. ]The publisher’s reader put a note on the margin here: “There are many strong reasons on both sides.” Perhaps that is a better way of putting it.
[9. ]For a discussion of the early development of scientific instruments see Charles Joseph Singer, ed., A History of Technology (Oxford: Clarendon Press, 1957), vol. 3, pp. 582–646.
[10. ]See Frank Knight, Risk, Uncertainty and Profit (Boston, 1921).
[11. ]This would be true in a planned or governmentally controlled economy as well as in a free economy. Only in this case, the decision-making unit might be very large so that the rewards and losses would not be apportioned to the individuals responsible.
[12. ]W. I. B. Beveridge, The Art of Scientific Investigation (New York: Norton, 1950), is largely written from the standpoint of an applied researcher, specifically, from the standpoint of an investigator of the diseases of animals. Clearly Beveridge did make errors, but equally clearly the lines of investigation which he decided to pursue tended to be the right ones.
[13. ]In bookkeeping terms this is not true. Under the tax laws most research expenditures can be treated as current expenses and are so handled in most accounting systems. Although I do not question the tax advantages to be obtained by this procedure, the expenditures are actually investments.
[14. ]The patent monopoly has another disturbing feature, the almost comic confusion of the laws in this field. Leonard Lockhard put these complexities in fictional form in four most amusing stories published in Astounding Science-Fiction: “Improbable Profession,” September, 1952; “That Professional Look,” January, 1954; “The Curious Profession,” April, 1956; and “The Professional Touch,” February, 1959. For a careful statement of the problem from an economist’s viewpoint see Fritz Machlup, “Patents and Inventive Effort,” Science, 133 (May 12, 1961), 1463–66. The economic literature prior to 1959 was carefully surveyed by Richard R. Nelson in “The Economics of Invention,” Journal of Business, 32 (April, 1959), 101–27.
[15. ]Prescriptions, Drugs and the Public Health, “a digest of the presentation of the Pharmaceutical Manufacturers Association before the Senate Subcommittee on Antitrust and Monopoly,” presents the businessman’s view on this problem. See also “Patents as a Research Tool,” a speech by Robert L. Hershey, vice president, E. I. du Pont de Nemours & Co., before the ninth annual conference of the Patent, Trademark, and Copyright Research Institute of George Washington University, given June 17, 1965.
[16. ]Venetian glass was produced on a considerable scale for quite a while before the secret leaked out, but the normal entrepreneur could not expect to have the dread Committee of Ten to help him keep his process secret.
[17. ]Sometimes, even when the strain will breed true, the precautions necessary to prevent accidental contamination of the breeding stock may be costly. In these circumstances, specialized breeders may develop, but the price they receive for their seed reflects the difficulty of raising it, not the cost of the developmental research.
[18. ]Similar considerations may lead to publishing data rather than keeping it secret. “The big company . . . has to publish enough to make itself attractive to the scientific community, whence will come its future strength. Yet the old sense of property, the basis of the firm’s very existence, inhibits it from tossing to the four winds those few nuggets of practical information for which gold has been traded.” Kodak reports, Science, 148 (May 14, 1965), 890.
[19. ]Sometimes morale may be raised by simply announcing that a branch of the laboratory which has been devoted to improvements in gadgets will, from now on, carry out pure research (in the development of gadgets). This type of thing will achieve maximum effectiveness if it coincides in time with one of the periodic reorganizations of the laboratory.
[20. ]New York Times, March 12, 1959, p. 3.
[21. ]Richard R. Nelson, The Link Between Science and Invention (RAND Corporation, P-1854-RC, December 15, 1959), gives an account of the most important single discovery of the Bell Laboratories, the transistor, and makes it quite clear that the researchers had practical applications in mind at all times.
[22. ]Anne Roe, “A Psychological Study of Eminent Psychologists and Anthropologists, and a Comparison with Biological and Physical Scientists,” Psychological Monographs, 67, No. 2 (February, 1953), 49. These remarks refer to all of the scientists, not just the psychologists.
[23. ]To offer a subjective guess, considerably more than half.
[24. ]The experiment was carefully discussed by Dr. A. Grünbaum in his vice-presidential address to the history and philosophy section of the AAAS on December 29, 1963, at the Cleveland meeting. The speech was published under the title “The Bearing of Philosophy on the History of Science” in Science, 143 (March 27, 1964), 1406–12.
[25. ]Charles Joseph Singer, ed., A Short History of Scientific Ideas to 1900 (Oxford: Oxford University Press, 1959), pp. 236–41.
[26. ]A mechanical method of approximating the circulation of a new idea has been developed in the “citation count.” By counting the number of times a given article is footnoted in other articles, an idea of its importance can be obtained. For a sample of the method, see J. H. Westbrook, “Identifying Significant Research,” Science, 132 (October 28, 1960), 1229–34.
[27. ]Singer, A Short History of Scientific Ideas to 1900, pp. 485–90.
[28. ]Singer, A History of Technology, vol. 4, pp. 410–12.
[29. ]See Norman W. Storer, “The Coming Changes in American Science,” Science, 142 (October 25, 1963), 464–67, for a discussion of the changes which have come about in science as a result of the rapid growth of this type of research.
[30. ]And they necessarily know more about themselves than any employer.
[31. ]See Theodore Caplow and Reece J. McGee, The Academic Marketplace (New York: Basic Books, 1958), for a detailed discussion of the part research papers play in the hiring of academic employees.
[32. ]This is brought out particularly clearly on pages 126–31 of The Academic Marketplace.
[33. ]For an account of the strictly commercial side of the process, together with some examples, see Time, January 12, 1962, p. 36.