Letters to a Young Scientist (6 page)
A fire ant laying an odor trail. Drawing by Thomas Prentiss. Modified from “Pheromones,” by Edward O. Wilson,
Scientific American
208(5): 100–114 (May 1968).
I
F YOU CHOOSE
a career in science, and particularly in original research, nothing less than an enduring passion for your subject will last the remainder of your career, and life. Too many Ph.D.s are creatively stillborn, with their personal research ending more or less with their doctoral dissertations. It is you who aim to stay at the creative center whom I will now specifically address. You will commit your career, some good part of it, to being an explorer. Each advance in research you achieve will be measured, as scientists constantly do among themselves, by completing one or more of the following sentences:
“He [or she] discovered that . . .”
“He [or she] helped to develop the successful theory of . . .”
“He [or she] created the synthesis that first tied together the disciplines of . . .”
Original discoveries cannot be made casually, not by anyone at any time or anywhere. The frontier of scientific knowledge, often referred to as the cutting edge, is reached with maps drawn by earlier investigators. As Louis Pasteur said in 1854, “Fortune favors only the prepared mind.” Since he wrote this, the roads to the frontier have greatly lengthened, and there is an enormously larger population of scientists who travel to get there. There is a compensation for you in your journey, however. The frontier is also vastly wider now, and it grows more so constantly. Long stretches along it remain sparsely populated, in every discipline, from physics to anthropology, and somewhere in these vast unexplored regions you should settle.
But, you may well ask, isn’t the cutting edge a place only for geniuses? No, fortunately. Work accomplished on the frontier defines genius, not just getting there. In fact, both accomplishments along the frontier and the final eureka moment are achieved more by entrepreneurship and hard work than by native intelligence. This is so much the case that in most fields most of the time, extreme brightness may be a detriment. It has occurred to me, after meeting so many successful researchers in so many disciplines, that the ideal scientist is smart only to an intermediate degree: bright enough to see what can be done but not so bright as to become bored doing it. Two of the most original and influential Nobel Prize winners for whom I have such information, one a molecular biologist and the other a theoretical physicist, scored IQs in the low 120s at the start of their careers. (I personally made do with an underwhelming 123.) Darwin is thought to have had an IQ of about 130.
What, then, of certified geniuses whose IQs exceed 140, and are as high as 180 or more? Aren’t they the ones who produce the new groundbreaking ideas? I’m sure some do very well in science, but let me suggest that perhaps, instead, many of the IQ-brightest join societies like MENSA and work as auditors and tax consultants. Why should the rule of optimum medium brightness hold? (And I admit this perception of mine is only speculative.) One reason could be that IQ-geniuses have it too easy in their early training. They don’t have to sweat the science courses they take in college. They find little reward in the necessarily tedious chores of data-gathering and analysis. They choose not to take the hard roads to the frontier, over which the rest of us, the lesser intellectual toilers, must travel.
Being bright, then, is just not enough for those who dream of success in scientific research. Mathematical fluency is not enough. To reach and stay at the frontier, a strong work ethic is absolutely essential. There must be an ability to pass long hours in study and research with pleasure even though some of the effort will inevitably lead to dead ends. Such is the price of admission to the first rank of research scientists.
They are like treasure hunters of older times in an uncharted land, these elite men and women. If you choose to join them, the adventure is the quest, and discoveries are your silver and gold. How long should you keep at it? As long as it gives you personal fulfillment. In time you will acquire world-class expertise and with certainty make discoveries. Maybe big ones. If you are at all like me (and almost all the scientists I know are, in this regard), you will find friends among your fellow enthusiasts and experts. Daily satisfaction from what you are doing will be one of your rewards, but of equal importance is the esteem of people you respect. Yet another is the recognition that what you find will uniquely benefit humanity. That alone is enough to kindle creativity, though it cannot alone sustain it.
How hard will this be? I’ll pull no punches about that part. At Harvard I advised mostly graduate students who planned for academic careers. They chose to combine research with teaching in a research university or liberal arts college. I posited the following time for success in this combination: at the start, forty hours a week for teaching and administration; up to ten hours for continued study in your specialty and related fields; and at least ten hours in research—presumably in the same field as your Ph.D. or postdoctoral work, or close enough to draw on the experience from your student years. Sixty hours a week total can be daunting, I know. So seize every opportunity to take sabbaticals and other paid leaves that allow you stretches of full-time research. Avoid department-level administration beyond thesis committee chairmanships if at all fair and possible. Make excuses, dodge, plead, trade. Spend extra time with students who show talent and interest in your field of research, then employ them as assistants for your benefit and theirs. Take weekends off for rest and diversion, but no vacations. Real scientists do not take vacations. They take field trips or temporary research fellowships in other institutions. Consider carefully job offers from other universities or research institutions that include more research time and fewer teaching and administrative responsibilities.
Don’t feel guilty about following this advice. University faculties consist of both “inside professors,” who enjoy work that involves close social interactions with other faculty members and take justifiable pride in their service to the institution, and “outside professors,” whose social interactions are primarily with fellow researchers. Outside professors are light on committee work but earn their keep another way: they bring in a flow of new ideas and talent and they add prestige and income proportionate to the amount and quality of their discoveries.
Wherever your research career takes you, whether into academia or otherwise, stay restless. If you are in an institution that encourages original research and rewards you for it, stay there. But continue to move about intellectually in search of new problems and new opportunities. Granted that happiness awaits those who can find pleasure while working on the same subject all their careers, and they assuredly have a good chance of making breakthrough advances while doing so. Polymer chemistry, computer programs of biological processes, butterflies of the Amazon, galactic maps, and Neolithic sites in Turkey are the kinds of subjects worthy of a lifetime of devotion. Once deeply engaged, a steady stream of small discoveries is guaranteed. But stay alert for the main chance that lies to the side. There will always be the possibility of a major strike, some wholly unexpected find, some little detail that catches your peripheral attention that might very well, if followed, enlarge or even transform the subject you have chosen. If you sense such a possibility, seize it. In science, gold fever is a good thing.
To make such success more likely, there is another quality in which you might or might not be well endowed but if not should at least try to cultivate. It is entrepreneurship, the willingness to try something daunting you’ve imagined doing and no one else has thought or dared. It could be, for example, starting a project in a part of the world neither you nor your colleagues have yet visited; or finding a way to try an already available instrument or technique not yet used in your field; or, even more bravely, applying your knowledge to another discipline not yet exposed to it.
Entrepreneurship is enhanced by performing lots of quick, easily performed experiments. Yes, that’s what I just said: experiments quick and easily performed. I know that the popular image of science is one of uncompromising precision, with each step carefully recorded in a notebook, along with periodic statistical tests on data made at regular intervals. Such is indeed absolutely necessary when the experiment is very expensive or time-consuming. It is equally demanded when a preliminary result is to be replicated and confirmed by you and others in order to bring a study to conclusion. But otherwise it is certainly all right and potentially very productive just to mess around. Quick uncontrolled experiments are very productive. They are performed just to see if you can make something interesting happen. Disturb Nature and see if she reveals a secret. To show you my own devotion to the quick and sloppy, I’ll give you several examples from my own initially crude efforts. These are from memory; I didn’t keep notes, careful or otherwise.
• I put a powerful magnet over a column of running ants to see if I could turn their direction or at least disrupt them, and hence detect whether ants have a magnetic sense. Time consumed: two hours. Result: failed. The ants couldn’t care less.
• I sealed off the metapleural glands of ants in a laboratory colony. These tiny organs are clusters of cells found on each side of the middle part of the body. I then let the operated ants run over the screened roof of a culture of soil bacteria, and also over other cultures with ants not so treated, in order to see if the metapleural glands shed airborne antibiotic substances. Time consumed: two weeks. Result: failed. (I should have continued the effort, becoming more persistent and using different methods. The substances are there, as subsequent researchers showed.)
• I tried to create mixed colonies of two species of fire ants by chilling them and switching their queens. Time consumed: two hours. Result: success! I used the method to prove (with careful experiments and neat notes this time) that the traits distinguishing the two species are due to different genes. Chilling and mixing is now a standard technique for several lines of research.
• In the 1950s, it was thought that ants probably communicate with chemical signals (later called pheromones). But the possibility was still open that they use instead coded tappings and strokings with their antennae. A drumbeat of antennae on the body of a nestmate, for example, might be an alarm signal. I decided to see if I could locate the gland that produces odor trails. If successful, I thought, that could be the first step in working out the ant pheromone code. I dissected out all the main organs in the abdomen of worker fire ants and laid artificial trails made from them, patiently slicing and picking under the microscope with the finest surgical forceps. Time consumed: one week. Result: there was no response to any of the first organs tried, but then to my surprise came a powerful response to the Dufour’s gland, an almost invisible finger-shaped organ located at the base of the sting. A major success this time. Not only did the fire ants follow the trail, they rushed out of the nest to get onto and follow it. The Dufour’s secretions, it seemed, are both guides and stimulants: this was a new concept in pheromone studies. Other scientists and I went on during the following years to work out the dozen or so pheromone signals that compose most of the ant vocabulary.
Performing small, informal experiments is an exciting sport, and the risk in lost time is small. However, if a preliminary procedure proves necessarily time-consuming or expensive or both, the cost in time and money can become quickly prohibitive. If the effort fails, entrepreneurship requires the character and the means to start over—just as it does in business and other careers outside of science.
I will close this letter with one further piece of relevant practical advice to offer you if you are already a graduate student or young professional. Unless your training and research commit you to a major research facility, for example a supercollider, space telescope, or stem-cell laboratory, do not linger too long with any one technology. When a new instrument is at the cutting edge, it may open new horizons of research quickly, but it is also at first usually expensive and difficult to operate. As a result, there will be a temptation for a young scientist to build a career in the new technology itself rather than to make original studies that can be performed with it. In biochemistry and cell biology, for example, the centrifuge has long been essential for spinning apart different kinds of molecules and by this means making them available for physical and chemical analysis. In this way the trees can be separated from the forest, so to speak, and by this means can make the whole forest more understandable. At the beginning, centrifuges required a room of their own and a trained technician to manage them. As their engineering was streamlined, however, any researcher could, with a few instructions, run the machines alone. Then centrifuges came out of their personal laboratories in the form of smaller, less expensive units. Today, graduate students in many fields of biology accept them as a routine part of their tabletop armamentarium. The same progression, from technology worthy of a discipline of its own to a routine part of every well-equipped laboratory, also occurred in the evolution of scanning electron microscopy, electrophoresis, computers, DNA sequencing, and inferential statistics software.