Money and Growth

Perry G Mehrling, Roger J Sandilands, Perry G Mehrling, Roger J Sandilands

• Publisher: Routledge
• Year: 1999
• ISBN:
  9781134653416
• Edition: 1
• Topic: Business
• Subtopic: Business generale
• Index: Business

Allyn Young is one of the central figures in the development of American economic thought, and is one of the originators of modern endogenous growth theory. This book allows full appreciation of the full extent of Young's work because many of his most significant contributions are buried in obscure journals and unsigned articles. This volume addres

Part I
The nature and scope of economics

1 Economics as a field of research

Quarterly Journal of Economics (1927) 42, 1 (November): 1–25. Read before the Institute for Research in the Social Sciences, of the University of Virginia, on May 20, 1927, as the second of a series of lectures dealing with the fundamental objectives and methods of research in the social sciences.

I. The social sciences differ from the physical in that the observer’s interest lies within them.—The contractual and the institutional views of society.—Corresponding types of investigation.—The genetic point of view.—II. Group research and its promise.—Induction and deduction.— Fruitful hypotheses essential.—Individual research; the constructive imagination.—Promising types of research.—The limitations and promise of research.

I

The social sciences, like the natural sciences, proceed upon the one great premise that the intricate flux of events can in some way be explained. What appear to be arbitrary or capricious happenings can be fitted into a scheme which has no room for anything but dependable uniformity and regularity. Such is the first article of the scientist’s creed. The second article of that creed is that the one way to come to a knowledge of these hidden uniformities is by means of those patient and methodical inquiries which we call research.

The social sciences, however have to be distinguished from the physical sciences, not only because the phenomena with which they deal are more complex, because their data are less exact, and because the experimental method which the more rigorous physical sciences employ is generally not available to them, but also because they encounter problems of orientation which are peculiar to them and from which the physical sciences are free. The physical scientist sets himself, as an impartial observer, outside of nature, inquires into nature’s processes, and tries to reduce them to simple general relations. He does not hope to be able to change nature, or even in any literal sense to gain “increased power over nature.” But he knows that as we come to understand nature’s processes better we are able to make better use of them—which means merely that in our ways of doing things we take account of our new knowledge. The data of the physical sciences are physical phenomena, but the problems which these sciences seek to solve are born of human interests, and so far as the knowledge which they yield has instrumental value, it serves human ends and leads to modifications of human arrangements.

The social scientist cannot, in any comparable way, put himself, as an impartial observer, outside of society, so as to get a view of social processes as a connected whole. His interests, his values, his ends, lie within that connected whole. Every occurrence in the contemporary life of a society enters into two separate sets of relations. In the first place, every such occurrence is a phenomenon, a scientific datum, which has to be fitted into the ordered scheme of social processes. In the second place, every such occurrence has its own immediate and concrete significance, and has to be accorded its due weight in any system of social values. We seek to understand the impersonal processes of nature and to take account of them, but we neither approve nor disapprove of them. We also seek to understand and to take account of social processes, but we reserve the right to approve or disapprove of them. We do not hope to change nature’s uniformities; but the processes of organized society, we believe, are in some degree plastic. So far as the knowledge which the social sciences yield has instrumental value, it serves social ends and leads to modifications of social arrangements. In any complete view the realm of the phenomena of organized society and the realm of ends are coterminous. The great first premise of the scientific method compels us to view these phenomena as rigidly determined and predictable, while the interests that prompt our scientific inquiries imply that they are in some measure amenable to control.

Upon the general philosophical aspects of the predicament in which the social scientist finds himself I do not propose to dwell. My present concern is with the practical devices by means of which men interested in social problems have been able to get something of value out of the scientific study of social processes. These devices all involve some particular orientation and some particular ordered scheme of abstraction. The traditional type of economic theory, for example, rests upon the common interest in increasing the production of wealth and securing its juster distribution. The data which it submits to scientific scrutiny (the pertinent aspects of the physical environment, along with other commonplace facts, being taken as given) are the reciprocal relations between certain types of human conduct that appear to be fairly stable and dependable in the mass, and the variations of such economic magnitudes as product, prices, wages, costs, profits, and interest rates. The economic processes of society are thus viewed as constituting an intricate but reliable mechanism, operating in an orderly and predictable way.

But this economic mechanism is something more than an object for scientific analysis and contemplation. It may be controlled, directed, or interfered with. It is a social instrument, to be used as our communal interests may dictate. Above the economic man stands the political man, free to limit and define the field of the economic man’s activity, to impose conditions upon him, to prevent him from doing certain things, to encourage him to do others. It is incorrect, therefore, to say that the traditional political economy implies a wholly mechanistic view of human society. All that it implies is a particular orientation, with one particular set of social processes viewed as a mechanism by free agents who want to understand the workings of the mechanism because they want to know how best to control it and use it. They want to know how far to control it and how far to leave it alone, and it is desirable that they should be able to predict the more remote as well as the immediate effects of particular measures of control. Agents, mechanism, instruments, and ends are thus all in the picture. Doubtless they are seen in a one-sided and partial way, and yet this view of things has proved itself to be practically serviceable, and the traditional political economy which embodied it was one of the great intellectual achievements of the nineteenth century.

Every social science has to be defined in terms of its problems, and accordingly includes agents, instruments, and ends, as well as a mechanism, among its postulates. But every social science has its own particular orientation. Thus for political science the behaviour of the political man may well be an object of scientific scrutiny, just as educational science may focus its attention upon the learner and criminology upon the law breaker. The same human activities which one science regards as sufficiently uniform and dependable in the mass to make scientific analysis of them profitable, appear in other social sciences as free or plastic. To the economist the citizen, the voter, may be a free agent; to the political scientist his conduct may be in some measure determinate; to the student of education he may be a bit of malleable human material.

There is no necessary conflict between these different views, for each is a partial view. Held to consistently, they would separate the different social sciences rather more narrowly and rigidly than is practically desirable. A worker in any part of the field of the social sciences needs to be aware of the importance for his own problems of more orientations than one. But I venture to hold that no complete scientific synthesis of all the different social sciences is possible, if only for the reason that, as I have said, the inquirer, with his interests, must stand somewhere within society and its processes.

There is another problem of orientation, which cuts across all the social sciences, for there are two different possible views of the general structure of society. Both views can be traced back as far as the Greeks, but sometimes one view and sometimes the other has been dominant. These two views, or ways of conceiving the structure of society, are the contractual and the institutional. In the contractual view social arrangements are deliberate contrivances resting upon voluntary agreements—instruments which men use in attaining their purposes. In the institutional view these same arrangements appear as social habits, the products of history, not really shaped by the rational prevision of men, but dominant factors, themselves, in determining what men’s purposes and values shall be, and establishing the patterns which human behavior follows. In the one view, the institutions which make up the structure of society are human expedients; in the other view, man himself, except for his endowment of native powers and propensities, is the product of life in society. These views are variously distinguished, as individualistic and social, rational and genetic, atomistic and universalistic, mechanistic and organic. Each pair of names conveys a particular emphasis, or invokes a particular analogy, but each expresses the same fundamental contrast or opposition.

I see no satisfactory ground for any other position than that both of these opposed views take account of necessary aspects of the structure and the processes of organized society, and that neither view, taken by itself, is adequate. Yet the opposition between these two views has at one time and another divided social scientists into two warring camps. We have had, and still have, too much of what Mill, in his essay on Coleridge called “the noisy conflict of half-truths, angrily denying one another.” Mill added these wise words: “All students of man and society who possess that first requisite for so difficult a study, a due sense of its difficulties, are aware that the besetting danger is not so much of embracing falsehood for truth, as of mistaking part of the truth for the whole.” These are words for all inquirers in the field of the social sciences to remember. Our work is retarded and our intellectual energies are dissipated in useless quarrels because of our intolerance of methods and points of view other than our own. There are only two things of which we have a right to be intolerant: first, positive errors of fact or of inference; second, intolerance itself.

Since the two views of which I have spoken are really supplementary, one to the other, it follows that in the social sciences we must make room for two different general classes or types of investigation. In the first type we concern ourselves with certain aspects of the nature and the operations of a complicated social mechanism. We search for uniform and dependable relations that will help to explain the degree of order that is apparent in our social environment. In the second type of inquiries we seek to get an understanding, not of those general and dependable relations among things which we call “laws,” but of specific events, particular institutions, and unique situations. We look for explanations of differences, of the new forms which our institutions and our activities assume from time to time.

What am I trying to emphasize is the distinction between the field of “science,” in a narrow and strict sense, and the field of “history”—a distinction which many philosophers have recognized, but which has been curiously neglected in current American discussions of the problems and methods of the social sciences. Because both the natural and the social sciences, as commonly defined, extend over both fields, I prefer to follow Cournot in distinguishing, not between science and history, but between the abstract sciences and the historical sciences, between the sciences which have to do with those dependable abstract general relations which we call laws, and the sciences which deal with given situations or particular events in terms of their specific relations to situations and events which have preceded them.

Now it is a capital error to hold (with Thorstein Veblen and some of his followers) that the explanation of things in terms of their historical antecedents is in some special sense a scientific mode of explanation; that, as Veblen puts it, modern sciences are characteristically “evolutionary sciences,” and concern themselves primarily with “unfolding sequences” and “cumulative causation.” The truth is, of course, that the goal towards which the natural sciences are always pressing—even though it may be an unattainable goal—is the explanation of this world of changing and evolving forms and types of organization in terms of some simple and stable mechanism. Mathematical physics has not abdicated to descriptive genetics its place as the perfect type of science, and in a manner the ultimate type.

It is far from my purpose to belittle the importance of historical and genetic inquiries for the social sciences. I am merely trying to correct what seem to me to be prevalent misconceptions respecting the part they play in increasing our knowledge. I shall not even attempt to support the thesis that the unique and special character of historical events make “historical laws” impossible—for that thesis seems to depend partly on the way in which we define “history,” and partly on what we mean by “law.” There can be no doubt, however, that the sort of knowledge that we get from those historical inquiries which assume the institutional view of the structure of society, is not the sort of knowledge that we get from those inquiries into abstract general relations which assume a mechanistic or contractual view of the structure of society.

The mechanistic or contractual view of society is of necessity an instrumental view. The knowledge we get from researches into the nature of the general form of the economic relations that obtain in such a society is practical working knowledge, and can be formulated in working rules. It tells us what the general character of effects of a particular measure of control will be, what will happen if we pull a particular lever. Historical and genetic inquiries do not lead to working rules. They extend the range of our experience, they give us a better understanding of ourselves and of our possibilities and our limitations, they lead to new appraisals of our social arrangements, but they tell us little or nothing about means. At their best they add to our wisdom, to our judgment respecting what things are worth accomplishing, but they add little to the technical equipment required for successful accomplishment.

Researches into the “unfolding sequence” of institutional forms encounter the difficulty that the results they give are never scientifically verifiable. Wholly different interpretations of the course of history may have equally good credentials. A countless number of threads of continuity ramify backward into the past, and are woven together into what Maitland called the seamless web of history. Selection among them has to be made on the ground of present interests, and there is always the danger that it will be made on the ground of present predilections or present prejudices. Every account of the origins and the development of any of our contemporary institutions involves a revaluation of the past as well as of the present. (Consider, for example, the contrast between Alfred Marshall’s summary account of what he calls “the growth of free industry and enterprise,” and any one of the various socialistic accounts of the origins of what the socialists prefer to call “modern capitalism.”)

Of course, the worker in this field cannot give free rein to his imagination, for he is controlled and limited by the facts. But his task is not merely to ascertain the facts: he has to select them, evaluate them, and relate them so that they will tell their story. His task is not merely one of research, but of esthetic construction as well. What he sees and reproduces will depend not only upon what there is to be seen, but upon what he looks for, and that will depend upon himself, his training, and his interests.

I do not mean to suggest that within the limits set by the facts the historical or genetic interpretation of our existing economic order depends solely upon the personal equation of the investigator. If he is an honest workman he will be controlled by the circumstance that all of the knowledge he gets, by whatever methods of inquiry, must fit together so as to be a consistent whole. In practice the lines between different views of the structure of economic society and different methods of inquiry cannot be drawn so sharply as I may have seemed to suggest. The economic theorist does not “deduce” his results from a few simple premises. Even when he controls his findings by using statistics, he works in the midst of a context of experience, and the system of general relations which constitutes his theory is empty of meaning unless it is consistent with that body of experience, and explains and organizes some part of it. Similarly, whatever new views of the structure of economic society we get by looking backward to its development must supplement and be consistent with that abstract and general view of economic relations which we call economic theory. Every economic theorist ought to be something of an historian, and every student of the development of economic institutions ought to be something of a theorist.

It may be that I have dwelt overlong on these preliminaries, but this has seemed to me to be an appropriate occasion for entering a protest against the fruitless quarrels of the methodological sects, against their intolerance, and against their pretensions to exclusive possession of the only right points of view and the only effective methods of research. We ought to welcome sound work in the field of economics—work that really contributes to our understanding of economic problems,—whatever its orientation and whatever method or technique it employs. The prerequisite to this degree of tolerance is the recognition of the fact that no one orientation can possibly lay bare the whole field of the economist’s interests.

II

I hesitate to try to say towards what particular economic problems research could most profitably be directed just now. The difficulty is partly in the necessity of fitting research problems to the interests and equipment of the individual investigator and to the resources available to him, and partly in the rich diversity of important problems. Much depends, moreover, upon whether group research or individual research is contemplated.

Group research is an important and promising new development. It involves a common attack upon a particular problem or set of problems, by an organized body of investigators who apportion their work so as to get some of the advantages of the division of labor, and who may be able to turn over routine parts of their tasks to a corps of clerical assistants. This sort of organized research undoubtedly has advantages when what is wanted is a definite answer to a definite question, and when the question is one of fact. The task then is one of assembling materials and of putting them through appropriate technical processes so as to get a finished product. The form, though not the precise content, of the product is known in advance. The product must always be got by assembling facts in a particular way, or by relating them in a particular way. Doubtless research of this kind, directed toward a definite objective, will often yield important by-products; and doubtless, also, individual investigators who are engaged in this kind of research, will often hit upon new methods of dealing with their materials, or will find that new explanations and possible new inquiries come into their minds. But the specific goal of such research, as I have said, is a definite answer to a definite question of fact.

We have made hardly more than a beginning in organized group research in economics, and I look for a considerable increase in the number and importance of such undertakings. There are many important tasks which are beyond the powers and the resources of the individual investigator and which call for the cooperation of a number of investigators, with different capacities and different training. The advantages of this kind of organized cooperation are so obvious that I need not enlarge upon them. Its limitations are, or ought to be, equally obvious. These limitations are bound up with the fact that effective research is more than mere routine, more than a manufacturing process. The multiplication of research activities and the increase of endowments for research will not of themselves afford any assurance that there will be a corresponding increase of our understanding of the economic life of society. The assembling and systematic ordering of historical documents and statistical data is not enough. Willingness and industry are not enough. A perfected scientific technique is not enough. The really important thing is that research be directed towards the answering of significant questions, and it is hard to frame significant questions except in the light of definite hypotheses. Formulating questions and hypotheses is the first and most important task of the investigator.

Just because we can make a formal logical distinction between deduction and induction, we are prone to exaggerate the difference between deductive and inductive methods of inquiry. In the practical work of getting knowledge, we pass from a generalization to the facts and from the facts back to new generalizations in a way that blends deduction and induction. We begin, let us say, with a hypothesis—a tentative generalization. We then look into the facts, knowing that if the hypothesis is sound the facts we find within a certain range will not be inconsistent with it, and we determine our field of inquiry accordingly. This much is deduction. If the facts prove to be consistent with the hypothesis, our tentative deduction is transformed into an induction (or, as we say when we are testing some existing theorem, into a “verification”). If the facts are inconsistent with the hypothesis we cast about for a new hypothesis, for a generalization that brings the facts into some sort of orderly relation. In any really creative research, however modest in scale, there is this process of continuous give and take between the search for general relations and the scrutiny o...