McClintock

Eureka! Scientific discoveries, as everyone knows, are made by those flashes of insight in which the mind of a scientist perceives some previously hidden truth about nature. The deeper truth, occasionally alluded to but seldom pursued, is that scientists as individuals have little importance in scientific discovery.

The reason is simple. Scientists are fungible. Strike down any one scientist, even the most eminent, and all of his ‘firsts’ will be discovered sooner or later, usually sooner, by someone else. This is more true, not less, in particularly important fields, which also tend to be the most crowded. So hard does the throng of researchers bear down on nature’s secrets that the same discovery is often made by two or more different groups within a few weeks of each other.

In pre-modern science, before research was a profession or organised enterprise, individuals could and did make a significant difference. Without Newton, the foundations of physics perhaps wouldn’t have been laid for another fifty or a hundred years. Gauss’s unpublished notebooks anticipated the major mathematical discoveries to be made for a century after his death. But nowadays researchers are plentiful, and no longer constitute a constraint upon the unfolding of scientific progress.

If this seems surprising, it’s only because of the exaggerated attention paid by the public and by scientists themselves to the role of the individual researcher. Scientists, even more than journalists, are always heaping each other with honours, prizes and medals, all of them designed to accentuate individual achievement. Unlike general historians, who long ago abandoned the Great Man theory of history, historians of science still recount its progress as if it depended on the advances made by individual heroes of the test tube or cyclotron. The annual ceremony of investing the cardinals of science each year in Stockholm presupposes a model of science that was outmoded even in Nobel’s day. From all these sources the public receives the indelible impression that it’s men who make science, that it’s lone acting heroes who push back the frontiers of ignorance.

The more interesting truth is that science is a mighty juggernaut, dragged inexorably forward by the great government-funded research enterprises of Europe and the United States. No individual can significantly increase its historical pace. Discoveries are made in a reasonably logical progression, which is when the time is ripe for them. Proof lies in the exception: researchers who make discoveries too early, before the field is ready, are almost always ignored. Those who succeed in the essentially trivial feat of being first to try the right experiment at the right time earn the premium on which the scientific world places utmost importance: they gain the discoverer’s laurels.

The two books under review illustrate the rewards of working both against and in synchrony with the machine. Evelyn Keller’s A Feeling for the Organism is a biography of the American plant geneticist Barbara McClintock. Studying the inheritance of maize by conventional plant-breeding methods, McClintock figured out two major genetic mechanisms years before other biologists confirmed them at the molecular level. McClintock’s bad luck was to get out too far ahead of the juggernaut. Salvador Luria, on the other hand, caught the right wave at the right time, and rode it to a Nobel Prize. A Slot Machine, A Broken Test Tube is an autobiography which reflects a lifetime’s residence at science’s higher altitudes. Luria qualified as a physician in his native Turin and emigrated to the United States in 1940. He was influenced by Max Delbrück, a German physicist who decided to shape up biology by applying the methodology of physics to the simplest known forms of life, the phage viruses that prey on bacteria. As a member of Delbrück’s phage group, Luria made several interesting discoveries about the genetic mechanisms of bacteria.

Keller’s biography of McClintock poses two stimulating theses: that McClintock’s work was unreasonably ignored and ridiculed by her fellow biologists, and that as a woman she was a victim of discrimination. The book is based heavily on interviews with Keller’s subject, who presumably is in large measure the source of these views. On the evidence of the book, I believe both are at best partial truths.

McClintock has devoted her life to understanding the genetics of maize by the classical plant-breeder’s methods. After twenty years of close observation in the maize fields, she became uniquely adept at figuring out a plant’s genetics from its physical appearance. In the 1950s this had become an unfashionable approach. Baffled by the genetic complexity of higher organisms, biologists had turned to the simpler systems of phages and bacteria. In 1960 the French biologists Jacob and Monod produced evidence for a genetic control system in bacteria in which a gene that controls the function of other genes is switched on and off depending on the bacterium’s need for the products of those other genes. This was a milestone because it represented the first step in understanding how genes are controlled. Except that McClintock had made it ten years before.

Some remarkable analytical work led McClintock to infer the existence of the same mechanism operating in maize, where it was much harder to see. Her articles were also much harder to understand for all except specialists in the arcane subject of maize genetics. That was one reason why they made no impact at the time. More important, her findings didn’t explain the control mechanism in terms of its biochemistry. Jacob and Monod’s demonstration was compelling because it said: here are these enzymes which the bacteria need to break down a kind of sugar, here is the chemical signal that switches on the genes that make the enzymes, and here is the chemical that switches them off.

Once biologists had been persuaded by the details of Jacob and Monod’s experiments, they could see in retrospect what McClintock’s findings meant. With equal skill, McClintock also described another genetic mechanism, called transposition, the reality of which has been accepted only in the last few years. These are extraordinary feats of observation. They derive from McClintock’s distaste for the prevailing reductionism of molecular biology and her insistence on the opposite point of view: that organisms must be understood by studying them as a whole, not by breaking them into components. ‘I start with the [maize] seedling,’ she tells Keller, ‘and I don’t want to leave it. I don’t feel I really know the story unless I watch the plant all the way along. So I know every plant in the field. I know them intimately, and I find it a great pleasure to know them.’

That’s an attractive approach, and science needs McClintocks as well as reductionists. But should biologists have embraced McClintock’s ideas at the time she proposed them? I suspect not, and Keller offers no evidence to make the reader suppose otherwise. Keller hasn’t interviewed other biologists to ask why they dismissed her, but McClintock’s approach could not have been as persuasive as that of Jacob and Monod. Also, her presentation seems to have left much to be desired. Luria describes listening to her lecture at Cold Spring Harbor: ‘There was Barbara McClintock, a tiny but formidable scientist, speaking as fast as anyone I knew and packing years of work into a one-hour lecture.’

Keller’s attempt to make something of a martyr of McClintock is flatly unconvincing. It’s true that universities discriminated against women for many years. But McClintock seems to have suffered far less than many. She managed to keep working at her research through the 1930s, when academic jobs were not plentiful. She was elected to the National Academy of Sciences in 1944, becoming the third woman member in its history, and was made president of her professional society, the Genetics Society of America, in 1945. Academy membership is the second highest national honour to which American scientists aspire. The highest is the National Medal of Science. McClintock received that in 1970. Since the book was written she’s received the Nobel Prize. What are she and her biographer complaining about? What further recognition can they expect? The grievance seems to be that there is still resistance to her wider genetic theory, which holds that organisms can genetically reprogramme themselves in response to changes in the environment. That’s close to Lamarckism, which is reason enough for scepticism. Like her other discoveries, it must await a molecular underpinning before biologists can be expected to give it serious attention. McClintock’s problem has not been lack of recognition but a lag in recognition. That reflects both the torpor of the scientific juggernaut and her misfortune in leaping ahead of it by an unfashionable method. Keller’s biography is an absorbing portrait, but the reader should keep the same distance from her thesis as she should have kept from her subject.

Luria opens his autobiography with the perilous confession that he finds ‘most biographies of scientists remarkably uninteresting and their autobiographies even more so’. His own comes close to falling into the same category: in part, through no fault of his own – he has lived the blameless and uneventful life of a scholar – and in part because of a certain lack of awareness both of himself and of his profession. If a man is not on oath in lapidary inscriptions, presumably he is not obliged in autobiography to pretend to a modesty he doesn’t feel. Luria chooses to portray himself as aglow with self-satisfaction. Of a teacher who advised him not to go into research, he comments: ‘Perfectly true, but as useless as telling Gauguin not to paint.’ His colleagues ‘all tell me that I am a good [laboratory] director, sensitive but no pushover.’ ‘It still surprises me that I should have been, and still continue to be, a rather good teacher.’ When a chemical company sought Luria’s aid in setting up a research programme, they got ‘a good one, probably the best in the country’. Despite which, Luria seems to have limited insight into how companies work. ‘More disturbing, I have seen managers deciding on purely commercial grounds whether scientific projects of great merit should be continued or terminated.’ One wonders how such insensitive klutzes manage to stay in business.

Luria is more perceptive on the subject of the juggernaut phenomenon.

If a discovery is not made by X it will be made by Y. In fact, many discoveries have been made almost simultaneously by two or three scientists ... If Watson and Crick had not discovered the double helix structure for DNA it would probably have been discovered by someone else within a few weeks or months ... Likewise, if I had not discovered restriction and modification of bacteriophage they would have been discovered elsewhere within a few months.

If individuals are not the limiting factors in the juggernaut’s progress, what are? Technique, for one.

Techniques determine the bounds of the terrain that can be explored, and the juggernaut moves steadily ahead, restrained only when it exhausts one field of inquiry and waits for a new technique to open up another. Techniques are of course invented by individuals, but the reward system of science gives relatively little acknowledgment to their inventors. Glory goes to the theorists and experimenters. The next decade in molecular biology will be spent in exploring the limits of two techniques, the gene-splicing technique invented by Stanley Cohen and Herbert Boyer in 1973, and the hybridoma technique created by Georges Köhler and Cesar Milstein in 1975. None has won the share of Nobel’s dynamite money that for some curious reason is accepted as the supreme accolade among scientists.

Do scientists such as Luria and McClintock get too much glory? I suspect they do. Historians of science, who might be expected to provide the necessary perspective for such judgments, are strangely reluctant to trespass into modern times. Remarkable as it may seem, the only broad-sweep history of molecular biology is by a journalist, Horace Judson. His Eighth Day of Creation (1979) gives a vivid sense of molecular biology as a community of researchers, each feeding ideas into a common pool and drawing sustenance from it. This is a select crowd, but only one individual really stands out from it – its grand theoretician and driving force, Francis Crick. The phage group – Luria, Delbrück, and Alfred Hershey – played a vital minor role. Luria’s book is nicely written but it gives little sense of the wider community of which he was a part.

McClintock’s story is interesting for just the opposite reason: she wasn’t part of the community, even though she works at Cold Spring Harbor, the summer gathering-place of molecular biologists. As an outsider, she had essentially no influence on the community. What is extraordinary is that she managed to get so far on her own, that she anticipated the pack by a decade or more, and that she did so by pushing to its very limits an approach that everyone else had abandoned. Her individual achievement aside, science would be no further behind without her, since like Cassandra’s her importance has been recognised only after the event.

The Luria and McClintock books hold interesting implications for the funding of basic scientific research. When, as Luria describes, two or three scientists make the same discovery independently, that field of science is clearly overpopulated; scientists and resources could be switched to some other field with no deceleration in the juggernaut’s pace. But to which field? The McClintock case holds the answer. A subject in which a critical and provocative finding has never been closely investigated or repeated is clearly underpopulated, and a prime candidate for receiving new resources.