I R V I N E H. PA G E Cleveland, Ohio
Journal of Laboratory and Clinical Medicine (1971) 77, 357-360
With copyright permission from Mosby Inc.
Somebody must have said, never have so many been so certain they know so much about so much. Even in the management of research those who have never done an experiment blithely tell trained and experienced investigators how it should be done. One thing most researchers do agree on is that there is no single right way. Still, many errors in its conduct can be avoided, such as learning how to plan a research environment that encourages other than pedestrian research.
I suspect there is trouble ahead for research in cancer. People have become impatient with what they take to be lack of progress. Having seen what can be achieved by systems analysis, directed research, and great coordinated achievements such as the moon walk, they transfer the same thinking to the conquest of cancer all too readily.
Times are hard for all of us in research and many of us are not above taking the fullest advantage of the possibility to get more support for our particular field. Those of us in cardiovascular disease gave publicity a whirl a few years ago in the heart transplant and "artificial" heart episodes. Now cancer has taken the initiative, heralded by the appearance of Dr. Solomon Garb's book, Cure for Cancer. The American Cancer Society took a full page of the New York Times to tell the public that the cure for cancer was just around the corner if . . . and you know what the if means.
Quick to see the opportunity, Senator Ralph Yarborough and a bipartisan group of senators have sponsored some very far-reaching changes in research procedure, which if applied successfully to cancer may spread to many other fields.
The research community must know that the application of such a plan will have profound effects, whether for good or evil, or a little of both. As a long-time scientist, I have learned that prediction is a most hazardous undertaking -- the only safe ones to make should have the outcome dated after your own demise. The question, then, is whether so much of our research resources should be dedicated to "structured" or "targeted" research in one particular sector, no matter how important that sector may be. Few experienced researchers doubt that applied researching with the use of systems analysis is an orderly way to develop and apply important basic research leads. There are endless examples wherein key basic discoveries, which if developed might have led to an early discovery of a cure, have been overlooked and forgotten. The reasons for this are multiple, complicated, and need no elaboration now, except for one critical issue.
When most of the varied facts required for the solution of a problem are at hand, then is the time for systems analysis. The blank spots needing further research will be highlighted, hopefully filled, and an orderly plan developed to assemble the pieces without delay. By its very nature, however, such "structured" research does not foster innovation. The highly creative mind usually shuns participation in such projects. There is always the danger of confusing technicians with research scientists in large organizations. There are many other reasons for this: one is that these individualists avoid the anonymity inherent in large team approaches; nor do they enjoy sharing every new idea and having it "exploited" by others. Those who doubt this do not know creative research workers, as illustrated by the story of deoxyribonucleic acid (DNA) and ribonucleic acid (RNA).
One of the marks of genius in a research worker is his ability to select from among the myriad possible approaches to a problem the simplest and the one that has the greatest chance of success. There is no doubt that some great discoveries come by chance, aided by an inquisitive and patient mind; but the vast majority are the result of the careful building of a body of knowledge, derived from the painstaking analysis of the work of many. The genius sees the missing piece is the structure which makes it whole and then it is often ready to be developed and applied. We need his guidance throughout the development stage as well.
There are certainly times when "structured," "targeted" research pays handsomely. The serious difficulty, as I have said, is to decide when that time has come. Massive, short-term crash campaigns to conduct research , are risky as most creative researchers realize. They know the dangers of pressure to achieve and the dissipation of energy in paper work and endless committee meetings, the decisions of which they may find unacceptable. For these reasons, the better investigators may be unwilling to go along and as a result their work may lose support because it lies outside the main effort.
It is telltale that the full-time staff of the congressional commission concerned with the plan to formalize and direct the conquest of cancer is strongly biased toward managed research. It lends itself so much more easily to the ministration of committees, legmen, and paper organization plans. Further, it is so much easier to defend before Congressmen and laymen, simply because it is pat and orderly; none of these ifs, ands, and buts! It should be noted that of the $1 billion asked of Congress, $100 million would be spent on the experts to help them determine how to spend the money productively!
The experts who have the responsibility of mapping out the road to the cure of cancer are from a variety of professional and lay backgrounds Benno Schmidt, Dr. Sidney Farber, I. W. Abel, Elmer Bobst, Emerson Foote, G. Keith Funston, Dr. James Holland, Dr. Mathilde Krim, Dr. Joshua Lederberg, Dr. Jonathan Rhoads, Dr. Harold Rusch, Dr. William Hutchinson, Dr. Wendell Scott, Mrs. Anna Rosenberg Hoffman, Emil Mazey, Jubel Parten, Laurance Rockefeller, William Blair, Jr., Dr. Joseph Burchenal, Dr. Lee Clark, Dr. Paul Comely, Dr. Solomon Garb: full-time staff -- (1) Staff director Robert Sweek, former project manager on the fast-breeder nuclear reactor, program and ( 2 ) Deputy Director Carl Fixman, a former vice-president of New York Shipbuilding, who served the Atomic Energy Commission as plant engineer.
Experience teaches that the public is impatient, especially when promises are made, or seem to be made. Its original enthusiasm and willingness to finance the work chills and people turn to whatever other pipes pipe more engagingly if they do not receive a tangible benefit. In the past 2 decades, overpromise has been a besetting sin of the science community. This was not necessary in view of the altogether remarkable achievements which have been made. People have, for example, already forgotten who discovered penicillin and when it was discovered; nor are they aware of the extraordinary change in the practice of medicine as a result.
It is easy to criticize the present system of awarding federal grants for research. But the plan of independent review by study sections and councils is the best that anyone has so far devised. I personally can testify to their effectiveness, though like every other opinionated and selfish person, occasionally I wonder! But the concept that research priorities can be irrevocably set by a supercommittee has questionable appeal to me. I do not think it is in the best interest of research to direct it by consensus. In science, the right to have an opinion taken seriously should be won by achievement.
It is hard for me to understand why cancer must became the main target of American scientific interest. It is certainly by no means the largest killer and, so far as informed opinion can guess, probably no nearer to resolution than various kinds of heart disease, if I interpret the valuable report of the National Advisory Cancer Council, "Progress Against Cancer 1970," correctly. We should be under no illusion that money appropriated for one field will not in part be subtracted from another.
As in many fields of science there are exciting new developments. I appreciate the anticipation with which the solution of the problem of interferon will be greeted. Interferon seems to be one of a group of biologically active peptides which blocks an intracellular mechanism concerned with virus replication. There is evidence that it has antitumor activity. Then, the recent discovery of Howard Temin of the University of Wisconsin and David Baltimore of M.I.T. of an RNA-dependent DNA polymerase in RNA-containing viruses causing tumors has initiated an extraordinary research effort. Already Gallo, Yang, and Ting of the National Cancer Institute have announced the finding of an enzyme capable of making DNA from an RNA template in the lymphocytes of 3 patients with acute lymphocytic leukemia. None of this enzyme was found in the lymphocytes of normal people. This enzyme can be inhibited by N-dimethyl rifampicin, but as yet is not ready for clinical testing. This certainly supports the view that some tumors may be of an RNA-cancer-virus origin. It should be noted that these investigations are being done by men of great competence and as quickly as is reasonable. I am not sure that a massive systems analysis approach with infusion of large amounts of money would help. Perhaps so. There may well be a time for it, but that time is probably not now. Better to keep the paths to imagination uncluttered.
I end as I began with the statement that no one, including "blue ribbon committees," knows the future in research. A few researchers are better at picking the trends than most of us, but they usually will not make predictions in lieu of investigation. To doubt that the massive systems approach has great appeal to the business and legislative mind is stupid. The plan has great sales value and is understandable. The individual and small group research is at a great disadvantage in this sort of argument.
I may be very wrong in my guess as to the success of curing cancer by 1976 with the crisis approach, but I doubt it. I prefer to bet my tax dollar on the gifted individual who is given time, peace of mind, and an intellectually stimulating environment.
by Albert Szent-Gyorgyi
Biology and Medicine (1974) 18, 41-43
|This country owes its greatness equally to the wealth of its
natural resources as to the spirit of its pioneers. This pioneer spirit has penetrated
also its biomedical research and led to its wonderful successes. Research means going out
into the unknown, which demands a pioneering spirit. This spirit is now strangled by the
way in which the main federal biomedical granting agency, the National Institutes of
Health, distributes its grants.
The unknown is the unknown because one does not know what is there. If one knows what one will do and find in it, then it is not research any more and is not worth doing. The NIH wants detailed projects, wants the applicants to tell exactly what they will do and find during the tenure of their grants, which excludes unexpected discoveries on which progress depends. No doubt there are important problems which can be outlined in advance, as, for instance, the establishment of the sequence of amino acids in a protein, but the understanding of degenerative diseases, like cancer, muscular dystrophy, or schizophrenia, which is stagnant, waits for unexpected discoveries.
Scientific research is, in many ways, related to art. If one wants good music to be produced, one looks for a good musician and not for a project. Projects have no meaning and value anyway, because there are only two kinds of science: good and bad. Good science is made by good scientists, poor science by poor scientists, and the most brilliant project is worthless in the hands of a poor scientist, while, conversely, a good scientist has a good chance to come up with something valuable whatever he touches, because "die Welt rundet sich im Tautropfen" (Goethe), which could be translated by saying that all the great laws of nature are represented in a drop of dew. Pasteur went to Germany to study brewing beer and came home with the discovery of optical isomerism.
The objection can be raised that granting according to past achievement would cut out the young scientists who have had no chance yet to prove themselves. This is true, and special ways have to be found to discover them. There are ways to do so, but the need to find special methods for the case of beginning scientists is no excuse for torturing and paralyzing those who have already shown their worth.
Nobody can really judge the value of another fellow's project. Projects are nonsense. I don't think that any of the great discoveries were even made by projects. They were made by intuition. And who should judge, whom? This is a very difficult question, and I would like to point out its difficulty by a story. Many years ago I applied for a big grant from a private foundation. My request was granted. Some time later, one of the directors of that foundation told me the following:
"There was something queer about your application. Not being scientists, if such a great request is made, we ask opinions from a number of outside scientists, and mostly we get a uniform answer. In your case half of them answered, Give him everything he asks for. The other half advised, Not a penny! This was so striking that we inquired into the scientists who gave their opinion and found that the yes ones were all leading scientists, the nos were otherwise."
But even if committees were composed solely of top scientists, this would be no assurance of avoiding mistakes. Of the four major discoveries I made myself, two were immediately rejected by leading scientists of the field. It is natural that this should be so, because a discovery is a discovery because it is at variance with accepted knowledge.
It was not always as it is today. When I applied for the first time for a grant from the NIH and asked one of the directors how to go about it, he said, "Write something, and then forget it. You know, there are always nosy congressmen, and we must be covered by a piece of paper." This was sound philosophy which brought two Nobel Prizes to the NIH.
The spirit emanating from the White House under President Nixon is not improving things. The very capable director of the NIH was fired, and since President Nixon took office I have been, myself, unable to secure a grant and am unable to believe that the thousands of applicants who got grants were all that much better scientists. I am not applying any more, having made it a rule to take no more than three kicks in the pants by anyone. I do not think that the rejection of scientists who have contributed to science is a great encouragement to young scientists. I also want to remain free to turn in whatever direction my research demands.
During the fascist rule in Hungary I was told by a leading author,
The present way of granting may do the greatest harm to science by making researchers avoid problems which do not make good projects.
I would like to finish with an anecdote which might be worth preserving. Langmuir, one of the greatest American physicists, told me that when he was a young man he was invited [to take a temporary position] by General Electric, where they gave him a room. At the end of the first year, unexpectedly, Steinmetz came into his room and asked, "What have you achieved all this time?" "I achieved nothing," answered Langmuir, "but had enormous fun," whereupon Steinmetz offered him a job with tenure. This is a method of finding good young ones: to see whether they can have fun in a laboratory locked up alone.
|IN PRAISE OF SMALLNESS -
HOW CAN WE RETURN TO SMALL SCIENCE?
Perspectives in Biology and Medicine
(1980) 23, 37
We all know that what is cannot be otherwise. The existence of anything weights the scales most unfairly against everything else that could have been in its place but is not. The only change that we accept benevolently is growth: a bigger gross national product, an expanding trade deficit, more murders in the New York subway, etc. An overgrowing scientific establishment, therefore, seems quite in order. We are imbued with certain false equations but reject others. More scientists: more useful discoveries -- that is accepted. More physicians: more sick people -- that is rejected.(Recently, when making one of those impermissible remarks, I was rebuked as a cynic. Since I have sometimes referred to myself as a stoic or a skeptic, I seem to be making the round of non-Platonian Greek philosophy, although I am still studying to be an Epicurean.)
Those who are below me in age, that is, the vast majority, will probably not even know what I am talking about; a fate, willingly borne, which has accompanied me during my life. They will not understand what I mean when I say that we ought to find ways of reforming our system of scientific investigation, of going back, in part, to the conditions of research that I myself experienced during the early days of my activity.
"There is no return," they will say, "and those were bad times anyway; and besides he [meaning me] has not moved in 30 years -- so what does he complain about?"
Granted, times were bad, they were, in fact, beastly; they have always been beastly. Only now they are a little worse. Still, however, the climate of research was more agreeable, and there was more fresh air for the individual mind to develop, to find his bearings, and to proceed at his own innate speed. There was more freedom in every sense, because everybody, including the competition, was equally indigent. "That is a funny argument," I hear, "Divest ourselves of our riches, eh? Turn into hermits or coenobites?"
Nothing of the sort is contemplated. When Schumacher wrote his much-discussed and little-followed book , he did not expect to put General Motors out of business. He was looking, he was looking desperately, for an alternative to social and economic conditions that many people consider intolerable. His book was received with some approval and much derision. [I remember seeing, some time ago, an answer to one of those imbecilic inquiries in which Schumacher's book was listed as one of the worst books that the keen thinker had read during the year.] It is disheartening to notice that mankind, purple or blue from suffocation, looks with the utmost scorn upon the few who try to open a window.
My purpose in writing these lines is, of course, more modest, and the proposals I shall submit are more limited in scope. The only legitimacy I can claim is that I have been some sort of scientist for quite a while and that I have watched, with increasing dismay and even hopelessness, the ever more rapidly changing scenery of scientific research and also the change in the type of actors who are overcrowding the stage. I have described my position in several earlier publications (e.g., in a recent book  and also in an article that appeared in this journal ), and I need not restate it here.
After a few more or less random remarks about science, and about biology in particular, I shall first briefly review the present scene and then outline my suggestions for a remedy. Readers familiar with my opinion of experts or specialists (see, e.g., ), will not be surprised if these lines do not sound like the professional product of a think tank.
Nowadays, when every school of little fishes carries its name and number, we have even ethicists or ethicians, people who supposedly confer ethics, just as the beautician confers beauty. We have, I believe, even scientific ethicists, about whom I cannot make up my mind whether their task is to make the scientist more ethical or to lament his lack of this desirable quality. Less astonishing is the existence of several flourishing schools of the philosophy of science. Not being qualified to judge their achievements, I can only say that even ardent nonreaders of Sir Karl Popper or Mr. Thomas Kuhn are now surfeited with such slogans as "falsifiability" or "paradigm." The more I look into these things, the less I know what "science" is; and still I once thought I knew it quite well. (Saint Augustine experienced, I believe, a similar difficulty before the meaning of "time.")
What bothers me about this, I hope inspiriting, philosophical discipline is the singular in its designation: "science." When I hear such a title as "the nature of man," I know that I shall not learn anything about anybody in particular. Still, one could claim that all of humanity does find itself in one and the same leaky boat. But is this true of the sciences? Is not each in its own leaky boat, although they may all be rocked by the same ocean or supplied by the same chandler? To my possibly shortsighted view it appears that what all sciences have in common are comparatively few things -- mostly trivial bookkeeping matters, as it were -- and that the plural, "the sciences," ought not to be understressed.
Were a biochemist, a biologist, or a medical scientist to look for help and enlightenment in the books dealing with the philosophy of science, I do not think that he would find much of use. He would, perhaps, notice with disappointment that the discussion was limited to physics, especially theoretical physics, to astronomy and mathematics, and that the main thing, LIFE -- Hegel had called it "the inconceivable mystery" -- was not a suitable matter for the deliberations of philosophizing grown-ups which -- to plagiarize my ancient self  -- "while telling us all about everything, tell us nothing about anything particular."
If the baffled seeker after philosophical uplift succeeds in penetrating the hard shell of arrogant reductionism, inside he will find very little indeed. Even before getting into science, he probably knew that it is the systematic search for the orderly truth of nature; but whether, after many years of cohabitation with what scientists call nature, he is willing to concede that the order of the solar system and the order of the cell nucleus are brought about by identical forces, will depend more upon his character than into science have little relevance to his own praxis, that is, to the use of his own mind in his own investigations.
I should, however, state in fairness that I have come across one study of the epistemology of science in which the straitjacket is loosened. In his book with the refreshing title Against Method, Feyerabend writes [6, p. 202]: "Science is split into numerous disciplines, each of which may adopt a different attitude towards a given theory and single disciplines are further split into schools. The basic value judgements of an experimentalist will differ from those of a theoretician. . . , a biologist will look at a theory differently from a cosmologist."
In other words, vive la difference! It still remains, however, unfortunate that I can get no support from the specialists of generalism when I try to explain the term "small science" employed in the subtitle of this article. I shall, therefore, have to be content with the statement that in speaking of "science" I am thinking of the research pursued by an individual, perhaps together with one or two others, and that I leave out of consideration "centers of excellence," "institutes," "workshops," "study groups," and all other pinnacles of spurious togetherness. And when I speak of "small," I mean small.
I shall jot down here, topsy-turvy, a few considerations which have guided me in my thinking, if "thinking" is the mot juste:
1. Men are first human beings and only then scientists, bank tellers, etc.
2. Science is not a religion, although it may be a child, perhaps an illegitimate child, of philosophy. One can, therefore, not "believe" in science; but one can trust or distrust the scientific methods or the results of scientific research.
3. Science is a profession or a conglomerate of professions, not a way of life. But the methods that science has developed and applied successfully -- for example, the evaluation of the significance of observations -- may guide one in one's life; and this is not limited to practicing scientists.
4. Science is the application of reason, and mainly of logic, to the study of the phenomena of nature.
5. Therefore, the most important scientific tool is the human brain.
6. Each brain sits in its own head. Hence, the all-important unit in research is the individual scientist.
7. Out of the labor of individual brains, there may develop a consensus which may be either right or wrong. (Peculiarly enough, this consensus is very much subject to the prevailing fashions of the time.)
8. Despite the power of logic, true premises may lead to false conclusions, for in science we can almost never be sure that we have assembled all the premises that are required.
9. It is, therefore, often only one, ostensibly tiny, item that may bring about an explosive change of consensus. If this occurs, there will be a few dissidents who, as shown later, will sometimes be wrong and sometimes right.
10. Science -- and here I mean natural science -- is good for the scientist; whether also for the rest of humanity is arguable.
11. The natural sciences, as they grew in the last 100 or 200 years, have relied much more on inductive than on deductive reasoning. Whether this was entirely to their benefit, I do not know.
12. The so-called advance of science rests, in most cases, on two kinds of observation: predictable and unpredictable. The major part is of the first kind, predictable; it grows out of the accumulated body of accepted knowledge, and these observations can very well be made by teams or at least by several people in collaboration. The much rarer kind, the unpredictable observations, are the only ones deserving the name of discovery, and they are always due to a single person.
13. Very seldom it happens that great progress is made because of an intuition, sometimes of a nearly dreamlike character. This can certainly be achieved only by an individual, never by a group. Such intuitions are usually later verified experimentally and sometimes still later disproved by another set of experiments. As in most sciences the boundary between imagination and rational perception often is obscure, an intuition will sometimes be concealed by him who had it, being supplied ad hoc with an experimental underpinning out of which the inspiration will be claimed to have grown. Poets and scientists are ashamed of different things.
14. Science, as an activity of the intellect, operates on no recognizable schedule, similar in this respect to poetry or music. Some people work fast, others slowly; in any event, there never is any hurry.
In a recent book , I have tried to describe the educational and scientific climate at the time when I began. In that period, science still was thinly populated and transparent. The present-day opacity, due to overcrowding and to the pullulation of multidisciplinary busyness, had not yet set in. Coming to the United States in 1928, I found a scientifically underdeveloped country dominated by an unhurried, good-natured second-rateness. European scientists who visited the country at that time were attracted by the feeling of freedom generated by the wide open spaces and even more by the then very pleasant aroma of the dollar.
Looking back on the growth, the not entirely benign growth, of the scientific establishment, I discern five periods. What I say, is, of course, the opinion of an individual, wholly unanointed with the oil of expertism. In any event, every scientist is 90 percent layman, and in my case another 5 percent should perhaps be added. The periods that I distinguish are:
Period I was a time of small science, in a fairly stable equilibrium and with a quite shallow growth rate. Research grants were extremely rare and amounted mostly to only a few thousand dollars per year. Graduate students often lived with their families; if they received something from the department, it was pocket money. Faculty salaries were very low. One felt a little in a backwater; but in my field, biochemistry, ripples began to be noticeable, foremost in the use of stable and radioactive isotopes.
The great and sinister Talleyrand is quoted as having said that nobody who had not lived before 1789 (i.e., before the French Revolution) knew how sweet life could be. I could say something similar, namely, that nobody who had not been at least a graduate student before 1940 or 1942 could know how happy small science can be.
Period II was essentially the time of World War II. For the first time, the government engaged on a large scale in certain fields of research. The Manhattan Project and the Office of Scientific Research and Development (OSRD) recruited large numbers of scientists. The OSRD was a relatively leisurely institution; how much it accomplished, I am not in a position to judge. In some respects, it strikes me as an early version of the National Science Foundation (NSF).
The Manhattan Project, on the other hand, was something very different. It got scientists used to working in teams, the size and quality of which could not have been thought possible earlier. It certainly accomplished a lot -- too much, if I may say so -- and to some people it may have appeared as a huge scientific concentration camp. It had a far-reaching influence on the further development of scientific research, for it seemed to demonstrate that everything can be solved, if enough people are put to work on it. That this assumption is fallacious anyone considering the difference between basic and applied research will understand easily. But such thinking is becoming rare.
Because the United States were far from the theatres of war, the period also was of great importance for biological research. It permitted the country to make a tremendous leap forward, and it propelled American science -- by default, as it were -- to the forefront in nearly all fields. For some time after, science became preponderantly American science.
Period III, the first 12 years after the end of the war, was a time of more rapid, but not yet exorbitant, growth. Its beginning was marked by the return of war veterans to the universities: the best crop of graduate students the country has ever seen. With the exception of a few specialized foundations, most of the large private foundations, which had been the backbone of basic research, relinquished the field. Instead, the huge government agencies began operating, such as NIH, NSF, the Atomic Energy Commission, the Office of Naval Research, etc. In other words, the universities first curtailed and then stopped their support of scientific research, and the government took over. Although this momentous shift marked the end of free basic research, I do not believe that even I, with all my Cassandrian inclinations, recognized the seriousness of the changeover. Besides, the fledgling agencies stepped cautiously at first, and the number of researchers still was small in comparison with the enormous amounts of money available. All considered, it was a good time for science, although the seeds of the future had begun to sprout.
Period IV, roughly 1957-67, was, at least in the beginning, the time of the Sputnik which, as has often been remarked, signaled the onset of scientific megalomania. The force-feeding of research became fashionable, to which purpose the universities were encouraged, by all sorts of head and overhead money, to take in more students, expand their faculties, build more laboratories, etc. Secretaries of study sections of NIH traveled throughout the country, soliciting new and more grant applications. That required more bureaucracy on the part of the universities, and pyramids of uselessness were erected everywhere. A great deal was spent to control the flow of funds, in order to prevent the investigator from buying a hot dog on his grant. On the other hand, the weirdest types of symposia and congresses were financed, and travel money could be had easily.
Because science was being sold to the people, as if it were a new lipstick, it is not astonishing that many of those attracted and recruited did not really belong there. Inasmuch as scientific research is an activity in which the controlling effects of supply and demand are concealed, selection as to motive and talent had always been performed in a different way: through the operation of a pledge of poverty, as it were. This filtration effect people, subject to the laws of the marketplace for which their education had, however, equipped them particularly poorly. It was during that time that I noticed the disappearance of happy faces from laboratory and classroom. Grimness and tension had set in.
This brings me to Period V, since roughly 1967, that is, the present. As is to be expected of any historical process, many of the obnoxious features had gradually become apparent earlier, others were brought about suddenly. To begin with, that product of enlightened liberalism, the unspeakable Vietnam War, brought in its wake the crash of the dollar, inflation, and a feeling of nagging and questioning unrest. The revolt of the young people, vomiting at what they were told and taught, was doubtless worldwide; but I experienced it here and can only speak of what I saw myself. Many of them turned against the universities, quite a few against science. This is often described as "anti-intellectualism," in my opinion wrongly. There is so much to be against in this crazy world of ours, that I am particularly careful about sticking labels on anybody or anything.
As in every decaying commonwealth, also in science, the financial powers and the means of production, that is, the laboratories, etc., have become concentrated in ever fewer hands. We are sailing straight into a managerial dictatorship in which the individual scientist can no longer have a voice. In other words, science has become thoroughly politicized, a playball of power networks in which such expressions as "the search for truth" or "the benefit of humanity" must sound unconvincing, and even ridiculous, since everybody knows what and who are behind them. The distance between an Einstein or an Avery and a Vice-President in Charge of Research is very far indeed. They may use the same words, but they mean different things. In my opinion, there is no denying that the face of science has changed more in the last 15 years than it did during all its previous history.
One consequence of sudden bigness, of the abrupt swelling of science, has been the enormous increase in the number of publications. Many new journals arose, mostly serving special interests. As the brain of man has changed much less than his habitat, a form of scientific neurosis has come about which no longer permits the individual scientist to stand firmly on the ground; he floats, weightless as it were, in a wide space, buffeted by forces he does not understand anymore. The production of scientific knowledge on the assembly line has diminished or abolished the value of knowledge itself. Just as our powers of perception are geared to a definite rhythm at which sensations can be apprehended, an increase in the speed with which scientific knowledge is produced can only cause dizziness or, alternatively, a protective encapsulation of the individual. These changes have led to a tremendous fragmentation of all scientific disciplines into a host of mutually unintelligible cliques.
When I was young, one afternoon a week was enough to inform me about all that was published in chemistry and biochemistry. Now, more time than that is needed just to go through the list of titles in Current Contents. It is not recognized sufficiently that there can be an inflation of scientific facts: the more are being produced, the less the value of each. The knowledge industry is no less absurd than other industries appeared to Charlie Chaplin in the film Modern Times.
To one curious consequence of the pathological distension of science I have drawn attention before, namely, the complete break in tradition. This can be demonstrated easily by a comparison of the bibliographies of older papers with those of present ones. Almost nothing discovered or observed earlier than in the last 3 or 5 years appears to deserve mention.
This complete loss of perspective has changed the climate of research to an extent that is difficult to describe. Conceptionally, we live in science mostly on those things that are no longer quoted in the references; what is quoted has a half-life of 3 or 4 years; but we never run out of this kind of stuff.
I seem to be alone in concerning myself with what could be called the sociopathology of science; even that does not make me an expert. I have had, however, much occasion to compare the scientific careers of my generation with the problems facing a young scientist under the present conditions; and I must say, we had it much better, despite the beastliness of depressions, wars, and horrors through which we had to live.
Our entire system of teaching and research is based on the exploitation of the young: graduate students, postdocs, assistant professors. In some respects, this has always been so, but it has become much worse owing to the incomparably larger number of careers that are affected now. It ought to be investigated in detail to what extent an insane financing policy on the part of the government agencies and the greed on the part of the teaching and research institutions are responsible, but I have no time for that here.
In any event, I have come across too many sad stories of young scientists setting out on their weary climb: several postdoc years, first full of hope and then full of despair; and then, after 250 or 500 letters of application, the first job somewhere as assistant professor, mostly in an awful somewhere. Then, the desperate attempt to get the first research grant; the shorter the hopes, the longer become the applications. Some write whole books which nobody reads. If they succeed in getting a little money, then there begins the struggle of inserting their own meager self into the dense thicket of abundant recent information, of finding and holding their own research problem. Half-hearted attempts at the publication of half-finished masterpieces are followed by the notice from the department that they cannot count on receiving tenure. They are thrown out, and a new assistant professor, 5 years younger, is taken on. The system thrives, the individuals perish.
When I hold those stories of woe against the sumptuously funded "institutes," "centers of excellence," "clinical and diagnostic centers," etc., I can see that the trend is all toward the creation of very large scientific conglomerates in which, under the leadership of men with managerial qualifications, the predictable will be discovered in ton lots.
It is not difficult to illustrate the malignant deformation of scientific research by choosing, at random, a few figures from an official publication. I have taken two universities, one eastern and one western, that received about the same total of support from NIH, and I have indicated the distribution of funds in tables I and 2. The figures for research grants apply to fiscal 1976 ; those for research contracts, to fiscal 1975 . As can be seen in table 1, two persons received more than 23 percent of the money given, almost $7.75 million. In table 2, the bounty is distributed slightly more widely, but one grantee (1 W) brought home considerably more than $4 million, 11 percent of the entire funds. Besides, I have not even investigated how much additional support one or the other of these people may have gathered simultaneously from other public or private foundations. In addition, it is certainly not insignificant that in both instances the large grants, which comprised only 6 percent of the total number of grants, amounted to nearly one-half of the entire funds. Had I widened my search, the results would doubtless have been similar. In any case, what I found serves to confirm the validity of Robert Merton's well-known Saint Matthew principle: our system makes the rich richer.
So far as I can judge, the scientists listed in my two tables are of average quality, certainly no geniuses, and not 250 times better than the little fellows who received little grants. It is, however, quite obvious that the champions knew something that the others had never learned. If science has become a spectator sport and you like to sit and watch the matador, then this is the way to do it; but not if you consider scientific research as a significant activity of the human mind. It would be no solution to say, as some might do, that the money should go directly to the university, for in that case I would predict, knowing some of those concerned, that, instead of getting one-quarter of the total, they would get three-quarters.
The frightening waste of resources will become evident to anybody who considers how little of value the orgy of goal directedness has actually produced. One could, in fact, argue that our scheme of research support has much more harmed than helped the scientific growth of the individual. As it is well known that, wherever money is abundant, charlatans are brought forth by spontaneous generation, this interesting natural phenomenon has not been entirely absent from American "biomedical research."
I have often asked myself how we can escape the dehumanization to which our way of life and, therefore, our way of doing science condemn us. Is there a way out? As for correcting our way of life, I know very well that I can offer no remedy, for profounder minds than mine have not succeeded. But even within our miserable system, can one not think of an arrangement that could bring back some of the spirit of both dignity and high adventure that scientific research offered to my generation and to those who preceded us?
Before undertaking my little Sunday excursion to Utopia, I should like to state my objectives:
A few additional comments are in order. In the course of the last 20 years, and to an ever-increasing scientific research has been made to carry all sort of house- and bookkeeping expedients designed to rescue the faltering universities and colleges. To give one example: in the program of just one institute, the National Heart, Lung and Blood Institutes, the "indirect cost" rose from 17.4 percent of the "direct cost" in 1966 to 35.6 percent in 1976 [9, p. 62]. This means, incidentally, that during these 11 years the recipient institutions received no less than $273 million alone in "overhead." Now, it is quite clear that there are numerous universities, colleges, institutes, and so on, worth being rescued by the nation, but this ought to be done by way of the front door. One could think of something on the order of the British Universities Grant Committee, whose permanent contributions would defray not only the costs of overhead, etc., but also the salaries of the senior research officers. In other words, I should like to see the research grants awarded to individual scientists reserved for only one purpose: the furtherance of their own scientific endeavors.
Parenthetically, a "Universities and Colleges Grant Authority" (UCGA) would have a much wider task than the indirect support of scientific activities. I have always viewed it as a very unhealthy development that teaching institutions were forced to rely on research for their rehabilitation. In my order of national priorities, education is vastly more important than research. A country that neglects the education of its young people suffers irremediable damage; it will consist solely of barbarians with special skills.
And finally, two introductory remarks.
1. My proposals deal principally with "pure" research in the exact and semiexact sciences, such as chemistry, physics, biochemistry, parts ofbiology, etc., and not with the applied sciences, such as most medical and technical research. They have in mind the kind of work that can be undertaken by an individual or a small group, say, three or four, and do not, therefore, apply to the construction of accelerators, telescopes, etc.
2. I say it most hesitantly, but no return to small science can be contemplated without some form of restriction of the number of newly created scientists. In what manner educational contraception can be practiced, I cannot discuss here; but I hope that it will be less cruel than the present method which, with its sudden termination of training grants and withdrawal of predoctoral fellowships, I would describe as "abortion in the fifth year of pregnancy." Science cannot be a mass occupation, any more than the composing of music or the painting of pictures.
Here, then, is the mixture of proposals and comments that I should like to offer.
1. The support of individual, basic research should be taken away entirely from the NIH. I should like to see the NIH return to their intramural occupations, which could be described approximately as applied clinical research. If the extramural organization of NIH is to be maintained, it ought to be concerned exclusively with large program and center grants -- provided they make any sense, which I doubt -- and it should deal with institutions, not with individual scientists. The present tangle of enormous and tiny research grants, as it appears in the published lists, may wrongly be taken as a sign of democracy. But to me it always looked as embarrassing as if a janitor were listed by mistake in the Social Register where only his employer has a right to figure. [On one page of a recent list I see, for the same institution, one grant of $8.5 million and one of $4,000. The scales of justice could hardly have used the same pans for weighing those two.]
2. An agency should be created which, for the purposes of the present discussion, I shall call the Basic Research Organization (BRO). Until a few years ago, before it became bloated, the National Science Foundation could have fulfilled this function, but now it would have to undergo both restriction and expansion in order to serve the purpose. Besides, it is an old academic experience that a declining university department cannot be rehabilitated except by creating a new department with a somewhat different name and letting the decrepit one die by attrition. I believe the same applies to government agencies.
3. There would be only one BRO grant per individual scientist, and it would have an upper limit. This I should be inclined to set, at the moment, at $100,000. The present accelerating inflation renders, however, exact estimates impossible. Inasmuch as this country refuses to learn from the effects of the disastrous inflation that infested central Europe in the early twenties, it is too much to hope that some form of indexing could apply to the research grants.
4. Grants would be given for 5 years, unless a shorter period is requested. They would be terminated immediately if a grantee accepts support from another public or private agency.
5. The grants would be used exclusively for salaries of collaborators, equipment, and materials. The present hodgepodge, in which even faculty salaries are being paid, entirely or in part, out of the individual research grants, must end. As I pointed out in Section VI of this essay, expenditures by the universities ought to be handled by direct and permanent bulk grants from what I have called here the UCGA: an acronym signifying, unexpectedly, the "Universities and Colleges Grant Authority" and not the tetranucleotide composition of RNA. These bulk grants would also have to take care of overhead, travel expenses, publication costs, subscriptions, etc., so that individual research grants would be used only for research.
6. No applications longer than five pages would be accepted. Research objectives would be stated with the utmost brevity, and the researchers would be encouraged to change them without permission. It would be made clear to them that there are no preferred topics and that they are free to roam within the limits of their own conscience. The deleterious effects of convulsively changing scientific fashions, which I have tried to describe in a previous article , ought to be avoided as far as it is possible.
7. Although a budget outline would form part of the initial application, it ought to be made easy for the grantees to redistribute the budget after notification: Money saved in 1 year could be carried over to the next.
8. It would be stated as a principle that the grants are given to the individuals and not to the institutions, and that they can be taken along if the researcher moves away.
9. I should like to see some kind of provision stating that the BRO will not permit the purchase, from its funds, of any instrument for which the manufacturer does not guarantee service facilities and parts for 10 years. All equipment bought on a grant remains the property of the BRO and is lent to the researcher, who is responsible for its upkeep.
10. I should like to find a way of discouraging unnecessary publications, but I have not found a solution, save the radical one which I proposed some years ago that all scientific papers be published anonymously. Besides, who can decide what is necessary? I may find a paper to be rubbish, but the poor devil who wrote it may consider it his only means of achieving tenure.
11. It might be wise to think of a tri- or quadripartite division of the BRO according to geographic regions. This would have the advantage of diminishing the preponderant weight of a few institutions, so noticeable in the present distribution of funds.
12. I have left for the end the question of screening the applications. I wish that we could return to the patriarchal benevolence with which, as described in my recent book , I received my first support. But I fear that cannot happen, and there must be some sort of selection process, but not the one employed now. I consider the so-called peer review, as it is handled presently, as one of the worst features of the current system. It worked well as long as there was more money than takers. Priorities with two decimals, discredited even in beauty contests, are no solution. I should like, on the one hand, to expand the roster of reviewers very considerably and, on the other hand, to make sure that the same panel is not likely to handle more than one application.
In my opinion, we have been overdoing the notion of the expert or the specialist. In fact, the more a person believes to know about a narrow subject, the less open he will be to originality. Five biochemists ought to be able to pass on a biochemical application, and five botanists on a botanical one. For this purpose, I would establish very large lists of potential reviewers in the different fields, perhaps all members of such professional societies as the Federation of Biological Societies. From these rosters five names would be pulled by lottery for the mail review of each request. One could argue that the opinions of the panels ought to be only advisory and that the final decision should rest with the BRO itself. I do not know whether the type of organization envisioned here would receive a very large or a relatively small number of applications. If it can be done, it would be advisable to schedule personal interviews with the applicants. In any event, there must be some provision for appeal in case of rejection.
These are my basic proposals, and, of course, they are quite incomplete. Many things for which I have no space remain to be worked out, for example, the type of criteria by which applications are to be evaluated, or the way in which non-medical big science is to be supported. But I should like to mention two categories of support that are a little outside of the normal program considered here. I shall refer to them as "senior scientists' grants" and "innovation grants."
13. Just as the New York subway, which I use every day, carries at least two pitch-black cars in each train -- for the repose of the muggers between work, I suppose -- an organization designed to support small science must consider the special case of the retired scientist who may want to continue his research activity. The stupidly arrogant manner in which the elderly are treated had struck me long before I reached their unenviable ranks; and the elderly scientist is at a double handicap: he has no "peers," for the beavers who judge him are not only inordinately eager, but also excessively young; and, besides, he often has lost the ability to swallow his pride and to suffer fools with the gladness required by our time. (I have seen letters of refusal whose tone adds no page of glory to the annals of American science.) In my opinion, a sufficient number of special grants ought to be reserved for retired scientists who sometimes are, in fact, much better than their louder-mouthed nonpeers who sit in judgment. Therefore, these "golden age" applications ought to be screened by special panels if such can be found. My reason for suggesting this special category is that I expect the regular BRO grants to be of most use to comparatively young scientists.
14. There is a need for swiftly obtainable small grants, which I refer to as "innovation grants." These awards, perhaps with an upper limit of $10,000, should be accessible on relatively short notice to all scientists, regardless of whether they are recipients of other help. They could be used for investigating a new idea, before a formal application can be submitted, for writing a book or some other scholarly work, etc., but not for travel or attendance at a congress.
If wisdom could be bought with money, the many hundreds, yes, thousands of millions expended on the essentially fruitless study of the great scourges of present-day humanity -- heart disease, cancer, and so on -- would have had more success. But what money principally does is to produce takers. These I certainly do not wish to blame, for they have been saddled with an impossible task. If the syndic of Florence had stepped out on the balcony and had thrown loads of ducats to the crowd below, in the hope that Lorenzo Ghiberti would be among them and that it would be he who would collect the bounty, the paradise door of the Baptistery would never have been made. This also holds for fundamental science in which the unpredictable happens when it is least expected. But for it to happen, there must exist the possibility of a very large number of unforeseeable free associations, of entirely unplanned collisions. The freer, the less trammeled the scientist, the greater the chance of new principles being found.
I have little expectation that my scheme, or a better one, will be adopted. For that, an enormous upheaval, comparable with the great Cultural Revolution of China, would be required. But we live in a middle kingdom in which nothing ever happens except by default.
Nevertheless, I should be happy if my suggestions -- and there are many possible variations on the theme -- were taken seriously, at least to the extent of being discussed; but this is more than I can hope. There will be numerous objections, because many will consider such a scheme as damaging to them and, therefore, to science. But I should like to ask them whether they believe that when the people set out to support science they really had in mind the creation of a class of scientific impresarios. Whoever attempts to think the problem through will, I believe, come to the conclusion that a more equitable and less goal-conscious distribution of the available funds cannot but be to the advantage of real science. It may even, as an additional benefit, help us to reach some of the goals that drab and blind goal directedness has failed to achieve.
1. E. F. SCHUMACHER. Small is beautiful. New York: Harper & Row, 1973.
2. E. CHARGAFF. Heraclitean fire. New York: Rockefeller Univ. Press, 1978.
3. E. CHARGAFF. Perspect. Biol. Med., 18: 251, 313, 1975.
4. E. CHARGAFF. Scheidewege, 8: 460, 1978.
5. E. CHARGAFF. Adv. Protein Chem., 1: 1, 1944.
6. P. FEYERABEND. Against method. Verso ed. London: New Left Books,1978.
7. National Institutes of Health. Research grants, fiscal year 1976. DHEW Publication No. (NIH) 77-1042.
8. National Institutes of Health. Research and development contracts, fiscal year 1975. DHEW Publication No. (NIH) 76-1044.
9. National Heart, Lung and Blood Institutes. Fact book for fiscal year 1976. DREW Publication No. (NIH) 77-1172, p. 62.
10. E. CHARGAFF. Perspect. Biol. Med., 19: 324, 1976.
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Last edited on 17 Nov 2003 by Donald Forsdyke