The singer loves to sing. He asks society to allow him to do this. In exchange, he will make the sounds of the world more pleasant.
The scientist asks to be allowed to lift the skirts of the unknown. In exchange for this privilege, he might give many people some added years of life, or make their lives richer or more pleasant.
The key man in this business of cancer research is the scientist himself. There are many other people who are concerned with research, and if they are effective they keep the wheels turning smoothly. Administrators, technicians, and others can often make the difference between a job taking one year or ten years. But the key man in this enterprise is still the scientist. With out him there is no enterprise. Harold L. Stewart has pointed out that there is little that scientists have in common. The only common element that characterizes all of them is a basic enthusiasm for what they are doing.
It is important to remember that a scientist is a scientist only when he is working at it. When he comes home, if he's a family man, he assumes the role of husband, father, repairer of broken toys, taxpayer, and the many other roles that every individual is called upon to play. Even in his job there may be times when his role is not that of a scientist. He may assume the role of teacher, administrator, committee member, architect.
I would like to make this point again because I think it is important. Thc point is that a scientist is a scientist only when he is working at trying to solve a scientific problem. "Scientist" is an occupation like lawyer, plumber, or physician. It is not a title like "General" that follows a man to his grave. It is when "scientist" becomes a title that confusion arises. A man may start out as a scientist by receiving a Ph.D. (which is a title), work at being a scientist for a while, and then go into administration or into politics. While it is true that he is still capable of practicing the craft that he learned originally, this may not be what he is doing at all. If he realizes that what he is doing is administration or politics and not science, he can do his job reasonably well. If he is functioning in the administration or politics of science, then he knows enough to hire people who are actually engaged in doing science while he continues to perform his job.
The scientist may, in many ways, be in worse shape than the musician with regard to selling his products. The musician can point to a score, the artist to a painting, but the scientist's work, unless he is eminently successful, has no sale. In this sense, the picture of the creative scientist as a small man working in the corner of his laboratory, hoping that no one will notice him and take away his marbles, is not too far from wrong. This may be especially true of the exceptionally imaginative scientist who is far ahead of his time.
Fundamental research has no immediate utilitarian value. It comes out of the scientist as a work of art emerges from an artist. When his work becomes useful to the public, or popular as do works in the graphic arts or music, he will no longer have difficulty earning a living. But what does he do until that time comes? This poses no particular problem if, as the Prince of Monaco or the Emperor of Japan, he is born to the purple. If he is not independently wealthy, then there are several alternatives. He can work for a living and practice his art in his spare time. Universities offer this opportunity by paying a man to teach and allowing him the opportunity and the space to practice his art; which is research. Another alternative is to find a patron who will allow him to practice his art unimpeded by pecuniary considerations. But there are various kinds of patrons. The ideal patron is one who allows him to practice his art without interference. Such a patron might say to a composer, "Go and compose music. When you're done I'd like to hear it." For the scientist, such a patron was John D. Rockefeller and his institute, and the National Institutes of Health. There are other kinds of patrons. One type would hire a composer and tell him that "You can compose; but your compositions must be in the style of Beethoven." The dedicated creative artist will not be told how to practice his art, nor will the dedicated creative scientist. Failing to find a generous patron, he will probably turn to teaching for his livelihood, with research as his hobby. If he is a good teacher, then research's loss will be the teaching profession's gain. If he is a poor teacher, nobody gains. Some scientists, having little love for teaching, will accept the poor patron and turn out compositions in the style of Beethoven, while bootlegging their own art. Unfortunately, once corrupted, an artist has a slim chance of recapturing his integrity. He may even begin to enjoy the rewards that his hack work is producing, and will manage to convince himself that this work is real, and that his dreams are ethereal.
What is research, and why is it so unpredictable? Since scientists can put a man on the Moon, why not a cure for cancer?
It is difficult to explain to a lay audience what the odds are of making an important scientific discovery. There are millions of people who have a pretty good idea of what the odds are of getting a golf ball into a hole with a single stroke; or two or three or four. There are relatively few who understand how small the probability is of making an important scientific discovery. But the probability is different for different scientists. The highly skilled, perceptive investigator is more likely to make a discovery than the duffer. Everyone has heard of the beginning golfer who makes a hole in one; and the equivalent happens (rarely) in science. To the professional golfer, the hole in one is also quite improbable, but a hole in two or three is fairly frequent. This is not true of the duffer.
One crucial variable, which makes research different from golf, is that in research no one knows where the hole is. Therefore, the first problem is to find out where the hole is located; in other words, what is the problem that one has to solve? What some perceptive scientists do is to imagine the location of the hole (the problem) in their head and proceed to solve it. If you test it and the ball falls into the hole and the whole world cheers, you've done it. If the ball falls into the hole and no one cheers, you're never sure whether you've missed the boat (if I may mix metaphors) or have actually located the hole and sunk the ball, but the game isn't going to be played until next week.
There are as many different ways of doing research as there are of making music. Which way is correct? No one way is correct. All of the different approaches yield results of different kinds. All, in their own way, contribute to the advancement of our understanding. I should not say all, because some bits of research actually retard progress by cluttering up the literature with wrong information; which is considerably worse than no information at all.
Life styles in research are quite different. At one end of the spectrum is the scientist who directs a large operation involving many other scientists, massive numbers of technicians, large amounts of money, and who virtually runs his own publishing house. At the other end of the spectrum is the individual who is working alone, sometimes with a little bit of technical help, who spends more time thinking than he does experimenting, and publishes only when he feels that he has truly solved a problem. There is a whole spectrum In between. Many scientists experiment with different life styles and do things in different ways at different times.
I've heard creative scientists talk about doing two kinds of research: They say that they do "real" research and also have a "bread and butter" problem, which is the kind where you can see the end in sight and can therefore write a plausible project proposal in order to obtain money. You're also reasonably sure of a useful (?) publication at the end of the work. This "bread and butter" problem equips the laboratory, provides technicians, and so on. It also allows the scientist the time to do what most creative scientists consider to be the exciting stuff; the exploration of new and totally unpredictable frontiers. It allows him to do what Stewart calls "Sunday morning experiments," which are experiments that he's ashamed to do when anybody is watching. These are the long shot experiments which rarely pay off, but when they do, they pay off big.
The history of science is full of fortunate accidents falling upon the prepared mind. It is, in fact, the stuff that fine science is made of. Yet, for every one of these lucky accidents that turns out to be correct, there are thousands that end up in the waste basket, either because the observations are worthless, or because the tools to extract their meaning have not yet been discovered. The discovery by Gregor Mendel of the laws of heredity did not become truly meaningful until the role of the chromosomes was discovered. It was then that the brilliance of his observations became painfully evident. You can take ten scientists of equal ability and equal perceptiveness and, while all will produce work which is worthwhile, perhaps only one will make a startling discovery. It is much like walking through a maze. If the first turn that you take is wrong, and it is entirely accidental, someone else may have reached the goal ahead of you.
It would all be very nice if we could determine, in advance, who the creative scientists are going to be; and support them. There is no known way of doing this; any more than it is possible to determine from high school intelligence test scores, or grades, who is going to be the fine physician, architect, engineer, or war hero. We are forced to conclude that the man who is going to be successful is the one who becomes successful. It is necessary, therefore, to support a large number of scientists who will contribute relatively little in order to support the one who may contribute much. It is not too difficult for someone who understands the field, to pick out a promising scientist once he has started to make good some of the promise. It is virtually impossible to do this at any earlier time. It is also impossible to predict when a previously productive scientist will stop being scientifically productive and will start cluttering the literature with his undocumented personal opinions as a few Nobel Laureates have done.
It is the very rare scientist who sets out to make a particular discovery and does it Most discoveries are made by people who are trying to satisfy their curiosity about something, or by people who come upon something important by accident. More often than not, an individual goes into a particular branch of science because of some accident in his background (someone he loved died of cancer) or because some inspiring teacher "turned him on." Like that first critical turn In going through a maze, a good early choice is entirely accidental. The few people who have made outstanding discoveries in the process of performing the research for their doctoral thesis have done so because they were lucky enough to have a professor who pointed their nose in at least one fruitful direction. If not this, then it happened because they happened to be at a particularly good place at a particular time. This is not to say that brilliant people will not inevitably make some important discovery, but it might take them a considerably longer time; and they make it in an entirely different area. Pasteur did not set out to discover the cause of disease; he was interested in finding out what caused wine to sour. Jenner, the discoverer of smallpox vaccine, was perceptive enough to observe that milkmaids did not develop smallpox in the course of an epidemic. He associated the disease of cowpox with smallpox. Had he been in a different place, or in a different time, these fortuitous observations would not have been made. Even the well-known story of the discovery of the structure of DNA by Watson, Wilkins, and Crick could not have been made twenty years before the time it was made even if the same people had gathered together at the same place. Freud did not set out to discover psychoanalysis. He would have been a biologist, but for the accident that he had to earn a living; and he did it as a physician. It is interesting that all of these men would probably have made significant scientific discoveries, but they would not have been the ones that they are now famous for.
The deliberate discovery of the physical structure of DNA was possible because there was already a reasonably large body of existing information. Besides the equipment for x-ray crystallography (no mean accomplishment in itself), there was the finding of Erwin Chargaff in 1949 that there were fixed proportions of adenine, thymine, guanine, and cytosine. These so-called base ratios made the discovery of the structure of DNA possible. Chargaff did not know where his discoveries would ultimately lead when he started to study the chemistry of DNA. Friedrich Meischer, who discovered DNA in 1896 in Germany, had the idea that DNA might be the genetic material. Meischer might not have fared so well in today's research funding climate in obtaining money for an apparently useless quest.
I think that it is safe to say that there are now scientists working on problems that no one else is interested in, whose findings will some day excite the scientific world. It is also safe to say that there are scientific findings already published that no one is paying very much attention to, which may also someday excite the scientific community when it is ready for them.
A number of articles have pointed out that the public is impatient with the amount of time that scientists are taking. An excellent article by Christine Russell on "The Politics of Cancer" concludes with a statement that "It [the congressional battle about financing cancer research] should make clear to the public, on one hand, that it cannot expect instant cures to cancer, and that Congress anyway cannot legislate the remedies. On the other hand, it should serve as ample reminder to scientists that the public has a deep stake in their research, and that it will not tolerate for too long the ivory tower attitudes that sometimes do creep into their work. The scientists will have to give a convincing performance that they are, indeed, progressing toward practical payoffs." Attitudes like this, which insist on evidence of practical payoffs or convincing performance, will have the same effect on cancer research as telling the doctor who is trying to remove something from your eye to "Stop diddling around, and get the damn thing out."