The problem I have given you is one of the simplest with which we have to deal. Conceive of the far greater complexity if we introduce an immune serum against the staphylococcus in such an experiment designed to increase the resistance of the rabbit to which it is given, and you will imagine where the real complexity of our science begins. Such a serum differs in its potency with the individual animal that has produced it, with its age after withdrawal from the animal body, and with the method by which it has been conserved; in other words, it introduces another variable factor. I may again define our mode of experimentation as differing from that of chemistry in requiring the introduction of simultaneous, external controls, the object of such controls being simply to define the effect of those conditions which we recognize as contributing to a given result.

Such differences as these, then, lead me to think that even great experience in one type of experiment will not fit one directly for experimentation of another sort. I do not mean to intimate that training in methods of precision is not of value, however different the conditions may be, but the best training for a given end lies in work and more work with the intrinsic materials involved, not so much as leading to greater technical accuracy as tending towards the establishment of an essentially specialized experimental viewpoint.

We come now to mention the value of multiple scientific experiences as fitting one for the larger synthesis or generalization in a given science. I have not reached that age where such generalizations as I mean appeal to me as the more important field in the experimental sciences, although I recognize that they are eventually necessary to present our work as a whole and in its practical aspects to the world at large. Such generalizations do, of course, imply

factual knowledge of the wider sort, and I must confess to being awed at times by the aptness of apparent analogies between the better-known conditions which exist in one science in explaining formative theories in another science. Personally, I also usually doubt the rigorous exactness of the conclusions drawn in respect to the significance of any one science by one who handles freely the data of several sciences. I suspect at once the reportorial viewpoint, the existence of second or third hand, and ever so slightly garbled information. I am inclined to trust the solution of my problems to a combination of specialists rather than to the superman. Here again I plead for collaboration.

In our great, vital and complex science of medicine we can see, I think, an illustration of the ultimate value of intensive specialization and of deliberate or chance collaboration. Out of indefinite, speculative, empirical, bedside methods of the practitioner, have emerged, through the stimulus of the exact sciences, a growing number of increasingly accurate and effective laboratory branches. These laboratory sciences have become of practical value in the diagnosis, prevention and cure of disease, precisely as they have become separate entities and have fallen into the hands of whole-souled and intensive specialists. I make no mention here of the intellectually satisfying value of a concrete body of similar facts which constitutes a science. The relatively rapid applicability of the data of laboratory medicine to human welfare is at once an enormous stimulus to accomplishment and also a potential danger, owing to the possibility of too rapid generalization and application to meet a practical need. There are many who are impatiently waiting with individual needs in mind to apply any method of apparent value we may devise, and it

requires at times no little self-restraint to withhold an apparent innovation for greater certainty. Over-enthusiasm greets the advent of every fact that has the least suggestion of practical value. We have ourselves lived through successive eras in medical progress when from each group of specialists was expected the last unraveling of the human mystery. Morphologist, physiologist, bacteriologist, and biochemist has each had his turn. The ultimate truth lies in all these sciences, and again in no one of them alone. The danger to sober advance is not in the successive enthusiasms with which each specialty has been received, but in the dabbling methods of a group of investigators who have attempted to "follow the ball"; investigating a given medical problem in successive years by the latest method in vogue, becoming rapidly in turn pathologist, physiologist, chemist.

The ultimate solution of each medical problem lies in the combined attack of a group of investigators converging from different points of the scientific compass, each trained in a separate method and employing it intensively. The problem of cancer, for example, is now being studied by the morphologist who describes hitherto undifferentiated structures in the malignant cell by special staining methods; by the immunologist who demonstrates the presence of reaction bodies in the serum of cancerous animals and human beings; by the chemist who shows that certain substances given parenterally inhibit or stimulate cell growth, or who produces similar results by the use of various diets; and by the expert in vital statistics who shows the actual increase or decrease in incidence of the disease; by the biologist who shows in Mendelian tables the heredity of the disease in animals; or, again, the effect of cross-breeding on transmission of the tumor; and by

the physicist who demonstrates the effect on the tumor growth of X-rays or radium. I have not exhausted the category, but merely wish to indicate that the significant advances in each of these methods of approach are made by specialists. Do not misunderstand me to mean that any one of these investigators may not be led by his work to assume seriously and purposefully the activities of any other type. Pasteur was a chemist who became a biologist and probably the greatest contributor to medicine, although without medical training, because he followed his problem to the bitter end into whatever field it led, with little regard for the fact that he was, technically speaking, unfit to encroach on medical territory. He rediscovered medicine from a new angle, untrammeled by any preconceived notions of how disease was regarded. Ignorance of veterinary medicine did not prevent him from isolating the causative agent of anthrax in cattle and from utilizing an attenuated virus in its prevention. Failure to have studied the central nervous system of man was no obstacle to the man who discovered the essential cause of hydrophobia and the means of preventing it. Imagine insisting that Pasteur's curriculum should have included medicine as a necessary prerequisite to the discovery of the fundamental principles of the infectious diseases.

I hope you will not take my remarks as indicating anything but the highest appreciation of instruction in the sciences in general as the best training for the youthful mind, or as contributive to general culture. You will not accuse me of advocating early vocational training without a preliminary survey of the realm of knowledge. To be specific, you will not imagine that I discredit the now universal requirements that premedical students should acquire a modicum of chemistry, of physics, and of

biology as furnishing an intelligent, scientific viewpoint for their subsequent study of medicine. Such a survey is not only good, but very properly prescribed as necessary. My remarks have been directed at a very different level and type of intellectual development from this; we have been considering our own particular problems as investigators. What I have been interested in discrediting is the persistence of ideas of machine-made education into the productive years of scientific life; the idea that if we seek eventually to become effective we should take care to perfect ourselves laboriously in each of the branches that have been regarded as fundamental. There is a real danger that we may spend our lives preparing ourselves for an indefinite piece of work that we never even start. It is, of course, much easier to continue preparing ourselves, to keep our scientific judgment strictly symmetrical by endeavoring to fit in each contribution that others make into its proper place, rather than to insist that one particular piece of work must be done now and to the exclusion of everything else. This insistence, however, I consider to be the true raison d'être of specialization, the only basis of real productivity.

These remarks, to repeat, are not a recommendation for educational anarchy, but an explanation of how a somewhat one-sided development may not only not be inconsistent with, but indeed the very essence of highest accomplishment. This is not so much a recommended program as an explanation of how things really work out. It is intended to some extent as helping to dispel the discouragement that I believe has come to many of us when we cease to be mere recipients of information and in a position to think and to do for ourselves in a chosen profession. I must confess to many hours of doubt for more years than I care to admit, as to whether I should really

accomplish anything, owing to the fact that I had failed to become a good chemist en passant. It was always and increasingly too late to turn back and repair the errors or omissions of education, and as my problems finally gripped me instead of merely inviting me, I silently gave up the struggle to remodel my life. And in following some of these problems in certain of their ramifications, I found that although I could never hope to learn chemistry, I was curiously enough collaborating in investigations that utilized that very type of chemistry which my work required. I was absorbing in this intimate way certain very restricted forms of chemistry in the making.

Out of such experience has gradually formed a certain working philosophy, or, better, a philosophy of work which I have tried here to present to you. Those of you with less limitations may well question much that I have said, you may assert that breadth does not of necessity mean superficiality, and per contra, that digging a hole does not necessarily mean that it is deep, but in certain respects I am sure you will agree with me. Specialization in science, even in the narrowest sense, is essential to real accomplishment. Any extension of knowledge is dependent on an attentive consideration of a relatively small group of facts to the temporary exclusion of less related facts. To a great extent the smaller the group the greater the concentration possible, and the greater the resultant accomplishment. Each science is independent in so far as the individual investigator is concerned, and correlatively all sciences. can be learned with each specific scientific problem as a point of departure, at least so far as the needs of that problem demand. On the solution of problems depends the future of science.

FREDERICK P. GAY

UNIVERSITY OF CALIFORNIA

RESEARCH IN INDUSTRIAL LABORATORIES 1

Ar the second meeting of the Committee of One Hundred on Scientific Research of the American Association for the Advancement of Science, on December 28, 1914, the subcommittee on research in industrial laboratories was constituted to consist of Drs. R. F. Bacon (chairman), C. E. K. Mees, M. C. Whitaker, W. R. Whitney and W. H. Walker.

The following problems in the direction of industrial research have been considered by the subcommittee:

1. The organization of industrial research. 2. The selection and training of students for industrial research.

3. The factors involved in the promotion of cooperation between manufacturers and the universities, with particular attention to the depreciation of the policy of industrial secrecy.

4. The promotion of a better appreciation of research, with particular regard to the education of the public to the realizable functions of industrial research.

5. The establishment of stable relations between research institutions and the research departments of industrial plants.

6. Finally, the advisability of conducting a comparative study of the investigational activities, capacities and facilities of organizations devoted to or carrying on industrial research.

The conclusions arrived at by the subcommittee are presented in summary in the following report.

THE ORGANIZATION OF INDUSTRIAL RESEARCH

Principles involved in the organization of industrial scientific research have been discussed at length during the past year by Dr. C. E. K. Mees, a member of this subcommittee, in SCIENCE, N. S., 43, 763. The chairman of the subcommittee has also considered some principles in the administration of endowed industrial research laboratories in the Journal

1 Report of the Subcommittee on Research in Industrial Laboratories, presented by the chairman, Dr. Raymond F. Bacon, at the meeting of the Committee of One Hundred on Scientific Research, New York, December 26, 1916.

of the Society of Chemical Industry, 35 (1916), No. 1.

It is generally conceded by those engaged in the direction of industrial research that, in order to be efficient, research laboratories of this type should be as thoroughly equipped as possible. In the case of industrial concerns having a number of plants and in the case of organizations of manufacturers, the tendency of organization should undoubtedly be towards concentration and cooperation in the maintenance of one large well-equipped research laboratory, rather than towards the erection and support of a number of smaller separated laboratories. It is, of course, necessary, especially in the case of chemical plants, that the analytical and control work be carried out in situ, but experience indicates that it is much better practise to centralize the research work.

Since the policy which insures adequate guidance to a research organization must be based upon the accumulation of facts, method in laboratory administration should provide for facilities for securing detailed information on a vast field, and for competent counsel from those who have a store of specialized knowledge. When the laboratory executive's work has passed the one-man stage, a division of labor comes about and it is here that he must see to it that he surrounds himself with men who are capable of effective effort-alert, original investigators of initiative and leadership.

An organized research administrative staff should not only result in effective division of labor, but also in efficient expenditure of executive energy, more effective plans, and general stabilization. This can come about if there is a pervading organization type of mind, which "is common to those drilled in systematic thinking and long immersed in the materials of their particular vocation. Such a mind sees details, but only as parts of a whole; reaches generalizations, but by the inductive route."

With regard to the investigatory staff, while the individual can exert only a very small influence except as a member of an organization or institution, yet a research institution never gains note or influence except through the

attainments and achievements of its individual members. The research department of a large industrial concern will be great because it has investigators on its staff who possess great originality and ability and because its director is wise and far-sighted. It is generally conceded that the personal factor is always paramount in industrial research, and that, as in every other organization, the control of men is the real problem in laboratory administration.

A brief consideration of the conditions favorable to both pure and industrial research is pertinent in connection with any discussion of the personal organization.

It is particularly adverse to progress to regard able investigators as abnormal men; for successful research demands neither any peculiar conformity nor any peculiar deformity of mind, but it requires, rather, peculiar normality and unusual industry and patience. It is little less inimical to expect productive work from those who are absorbingly preoccupied with other affairs than research; for fruitful scientific inquiry entails, in general, prolonged and arduous, if not exhausting, labor, for which all of the researcher's time is none too much. This is the experience of the Carnegie Institution and all other research organizations. It is only to be expected, therefore, that those most likely to produce important results in research are those who have qualified for the responsibilities thereof by the completion and publication of several worthy investigations, and who are at the same time able to devote the bulk of their energies thereto. The productive researchers in our universities are those who are devoting their whole time, or practically their whole time, to investigatory work.2

Research should never be allowed to fall into the rut of prosaic routine. The personnel of the investigatory staff should be maintained at 2 As a rule, the head professors of chemistry in the larger universities are not giving more than three to five hours of lectures during the week, the rest of their time being devoted to research, while a number of them have one or more private research assistants, besides the candidates for advanced degrees, doing research work.

the very highest standard and all administrative plans should be carried out with enthusiasm and earnestness.

In the research laboratories of manufacturing plants the personal cooperation of the research staff with the members of other branches of the organization always proves an important aid in maintaining interest in the work and is, in addition, mutually educating.3 In particular, the research department should have an esprit de corps that keeps things moving and should lead the way so strikingly as to be apparent to all other departments of the corporation. In consequence, mediocrity

should never be tolerated. It should be borne in mind, however, that the research man can only accomplish efficient work when he is free from restraint and petty annoyances.

Cooperation is always contributory to success in a research laboratory, and, other conditions being equal, the valuable men are the ones who can and will cooperate with one another. another. As in business, men succeed only as they utilize the ideas and services of other men. It follows, therefore, that the strength of an investigatory staff, properly operated, should increase more rapidly than the increase of its numbers, and that a fraternal spirit will play an important rôle in the productiveness of any research department.

The experience in several of our most successful industrial research laboratories has clearly shown that cooperation between the different departments thereof can be adequately and completely obtained by wellplanned weekly conferences on the subjects under study. While some directors of industrial research hesitate to spend the time which these conferences entail, it is the opinion of the subcommittee that conferences of this na

8 In several of our largest corporations, the plant superintendents make monthly reports to the research departments, including all ideas of their own or of their assistants which may in any way warrant investigation. Then, too, the salesmen report regularly to the research department regarding the various ways in which the company's products are used and what substitutes are employed for the company's products. Such plans stimulate closer thought and observation.