Letters to a Young Scientist (3 page)
As the young naturalist went from one part of the continent to another, he noticed something else: some kinds of living birds and other animals found in one locality were replaced by closely similar yet distinctly different kinds in another. What, he must have thought, is going on here? Today we know it was evolution, but that answer was not open to the young man. Anything that so openly contradicted holy scripture was considered heresy back home in England, and Darwin had trained for the ministry at the University of Cambridge.
When he finally accepted evolution, during the voyage back home, he soon began puzzling over the
cause
of evolution. Was it divine guidance? Not likely. The inheritance of changes caused directly by the environment, as suggested earlier by the French zoologist Jean-Baptiste Lamarck? Others had already rejected that theory. How about progressive change built into the heredity of organisms that unfolds from one generation to the next? That was hard to imagine, and in any case Darwin was soon figuring out another process, natural selection, in which varieties within a species—varieties that survive longer, reproduce more, or both—replace other, less successful varieties in the same species.
The idea and its supporting logic came in pieces to Darwin while walking around his rural home, riding in a carriage, or, in one important case, sitting in his garden staring at an anthill. Darwin admitted later that if he couldn’t explain how sterile ant workers passed on their worker anatomy and behavior to later generations of sterile ant workers, he might have to abandon his theory of evolution. He conceived the following solution: the worker traits are passed on through the mother queen; workers have the same heredity as the queen, but are reared in a different, stultifying environment. One day, during this lucubration, when a housemaid saw him staring at an anthill in the garden, she made reference to a famous prolific novelist living nearby when she said (it is reported), “What a pity Mr. Darwin doesn’t have a way to pass his time, like Mr. Thackeray.”
Everyone sometimes daydreams like a scientist at one level or another. Ramped up and disciplined, fantasies are the fountainhead of all creative thinking. Newton dreamed, Darwin dreamed, you dream. The images evoked are at first vague. They may shift in form and fade in and out. They grow a bit firmer when sketched as diagrams on pads of paper, and they take on life as real examples are sought and found.
Pioneers in science only rarely make discoveries by extracting ideas from pure mathematics. Most of the stereotypical photographs of scientists studying rows of equations written on blackboards are instructors explaining discoveries already made. Real progress comes in the field writing notes, at the office amid a litter of doodled paper, in the corridor struggling to explain something to a friend, at lunchtime, eating alone, or in a garden while walking. To have a eureka moment requires hard work. And focus. A distinguished researcher once commented to me that a real scientist is someone who can think about a subject while talking to his or her spouse about something else.
Ideas in science emerge most readily when some part of the world is studied for its own sake. They follow from thorough, well-organized knowledge of all that is known or can be imagined of real entities and processes within that fragment of existence. When something new is encountered, the follow-up steps will usually require the use of mathematical and statistical methods in order to move its analysis forward. If that step proves technically too difficult for the person who made the discovery, a mathematician or statistician can be added as a collaborator. As a researcher who has coauthored many papers with mathematicians and statisticians, I offer the following principle with confidence. Let’s call it Principle Number One:
It is far easier for scientists to acquire needed collaboration from mathematicians and statisticians than it is for mathematicians and statisticians to find scientists able to make use of their equations.
For example, when I sat down in the late 1970s with the mathematical theorist George Oster to work out the principles of caste and division of labor in the social insects, I supplied the details of what had been discovered in nature and in the laboratory. Oster then drew methods from his diverse toolkit to create theorems and hypotheses concerning this real world laid before him. Without such information Oster might have developed a general theory in abstract terms that covers all possible permutations of castes and division of labor in the universe, but there would have been no way of deducing which ones of these multitude options exist on Earth.
This imbalance in the role of observation and mathematics is especially the case in biology, where factors in a real-life phenomenon are often either misunderstood or never noticed in the first place. The annals of theoretical biology are clogged with mathematical models that either can be safely ignored or, that when tested, fail. Possibly no more than 10 percent have any lasting value. Only those linked solidly to knowledge of real living systems have much chance of being used.
If your level of mathematical competence is low, plan on raising it, but meanwhile know that you can do outstanding work with what you have. Such is markedly true in fields built largely upon the amassing of data, including, for example, taxonomy, ecology, biogeography, geology, and archaeology. At the same time, think twice about specializing in fields that require a close alternation of experiment and quantitative analysis. These include the greater part of physics and chemistry, as well as a few specialties within molecular biology. Learn the basics of improving your mathematical literacy as you go along, but if you remain weak in mathematics, seek happiness elsewhere among the vast array of scientific specialties. Conversely, if tinkering and mathematical analysis give you joy, but not the amassing of data for their own sake, stay away from taxonomy and the other more descriptive disciplines just listed.
Newton, for example, invented calculus in order to give substance to his imagination. Darwin by his own admission had little or no mathematical ability, but was able with masses of information he had accumulated to conceive a process to which mathematics was later applied. An important step for you to take is to find a subject congenial to your level of mathematical competence that also interests you deeply, and focus on it. In so doing, keep in mind Principle Number Two:
For every scientist, whether researcher, technologist, or teacher, of whatever competence in mathematics, there exists a discipline in science for which that level of mathematical competence is enough to achieve excellence.
A relativistic jet formed as gas and stars fall into a black hole; artist’s conception. Modified from painting by Dana Berry of the Space Telescope Science Institute (STScI). http://hubblesite.org/newscenter/archive/releases/1990/29/image/a/warn/.
T
HE PURPOSE OF THIS LETTER
is to help orient you among your colleagues.
When I was a sixteen-year-old senior in high school, I decided the time had come to choose a group of animals on which to specialize when I entered college the coming fall. I thought about spear-winged flies of the taxonomic family Dolichopodidae, whose tiny bodies sparkle like animated gemstones in the sun. But I couldn’t get the right equipment or literature to study them. So I turned to ants. By sheer luck, it was the right choice.
Arriving at the University of Alabama at Tuscaloosa, with my well-prepared and identified beginner’s collection of ants, I reported to the biology faculty to begin my freshman year of research. Perhaps charmed by my naïveté, or perhaps recognizing an embryonic academic when they saw one, or both, I was welcomed by the faculty and given a stage microscope and personal laboratory space. This support, on top of my earlier success as nature counselor at Camp Pushmataha, buoyed my confidence that I had the right subject and the right university.
My good fortune came from an entirely different source, however. It was choosing ants in the first place. These little six-legged warriors are the most abundant of all insects. As such, they play major roles in land environments around the world. Of equal importance for science, ants, along with termites and honeybees, have the most advanced social systems of all animals. Yet, surprisingly, at the time I entered college only about a dozen scientists around the world were engaged full-time in the study of ants. I had struck gold before the rush began. Almost every research project I began thereafter, no matter how unsophisticated (and all were unsophisticated), yielded discoveries publishable in scientific journals.
What does my story mean to you? A great deal. I believe that other experienced scientists would agree with me that when you are selecting a domain of knowledge in which to conduct original research, it is wise to look for one that is sparsely inhabited. Judge opportunity by how few there are of other students and researchers in one field versus another. This is not to deny the essential requirement of broad training, or the value of apprenticing yourself to researchers and programs of high quality. Or that it also helps to make a lot of friends and colleagues of your age in science for mutual support.
Nonetheless, through it all, I advise you to look for a chance to break away, to find a subject you can make your own. That is where the quickest advances are likely to occur, as measured by discoveries per investigator per year. Therein you have the best chance to become a leader and, as time passes, to gain growing freedom to set your own course.
If a subject is already receiving a great deal of attention, if it has a glamorous aura, if its practitioners are prizewinners who receive large grants, stay away from that subject. Listen to the news coming from the current hubbub, learn how and why the subject became prominent, but in making your own long-term plans be aware it is already crowded with talented people. You would be a newcomer, a private amid bemedaled first sergeants and generals. Take a subject instead that interests you and looks promising, and where established experts are not yet conspicuously competing with one another, where few if any prizes and academy memberships have been given, and where the annals of research are not yet layered with superfluous data and mathematical models. You may feel lonely and insecure in your first endeavors, but, all other things being equal, your best chance to make your mark and to experience the thrill of discovery will be there.
You may have heard the military rule for the summoning of troops to a battlefield: “March to the sound of the guns.” In science the opposite is the one for you, as expressed in Principle Number Three:
March away from the sound of the guns. Observe the fray from a distance, and while you are at it, consider making your own fray.
Once you have settled upon a subject you can love, your potential to succeed will be greatly enhanced if you study it enough to become a world-class expert. This goal is not as difficult as it may seem, even for a graduate student. It is not overly ambitious. There are thousands of subjects in science, sprinkled through physics and chemistry, biology and the social sciences, where it is possible in a short time to attain the status of an authority. If the subject is still thinly populated, you can with diligence and hard work even become
the
world authority at a young age. Society needs this level of expertise, and it rewards the kind of people willing to acquire it.
The already existing information, and what you yourself will discover, may at first be skimpy and difficult to connect to other bodies of knowledge. If this proves to be the case, that’s very good. Why should the path to a scientific frontier usually be hard rather than easy? The answer is stated as Principle Number Four:
In the search for scientific discoveries, every problem is an opportunity. The more difficult the problem, the greater the likely importance of its solution.
The truth of this guidebook dictum can be most clearly seen in extreme cases. The sequencing of the human genome, the search for life on Mars, and the finding of the Higgs boson were each of profound importance for medicine, biology, and physics, respectively. Each required the work of thousands, and cost billions. Each was worth all the trouble and expense. But on a far smaller scale, in fields and subjects less advanced, a small squad of researchers, even a single individual, can with effort devise an important experiment at relatively low cost.
This brings me to the ways in which scientific problems are found and discoveries made. Scientists, mathematicians among them, follow one of two pathways. First, early in the research a problem is identified, and then a solution is sought. The problem may be relatively small (for example, what is the average life span of a Nile crocodile?) or large (what is the role of dark matter in the universe?). As an answer emerges, other phenomena are typically discovered, and other questions raised. The second strategy is to study a subject broadly, while searching for any previously unknown or even unimagined phenomena. The two strategies of original scientific research are stated as Principle Number Five:
For every problem in a given discipline of science, there exists a species or other entity or phenomenon ideal for its solution. (Example: a kind of mollusk, the sea hare
Aplysia
, proved ideal for exploring the cellular base of memory.)
Conversely, for every species or other entity or phenomenon, there exist important problems for the solution of which it is ideally suited. (Example: bats were logical for the discovery of sonar.)
Obviously, both strategies can be followed, together or in sequence, but by and large scientists who use the first strategy are instinctive problem solvers. They are prone by taste and talent to select a particular kind of organism, or chemical compound, or elementary particle, or physical process, to answer questions about its properties and roles in nature. Such is the predominant research activity in the physical sciences and molecular biology.
The following example is a fictitious scenario of the first strategy, but, I promise you, is close to true dramas that occur in laboratories:
Think of a small group of white-coated men and women in a laboratory—early one afternoon, let us say—watching the readout on a digital monitor. That morning, before setting up the experiment, they were in a nearby conference room, conferring, occasionally taking turns at the blackboard to make an argument. With coffee break, lunch, a few jokes, they decide to try this or that. If the data in the readout are as expected, that will be very interesting, a real lead. “It would be what we’re looking for,” the team leader says. And it is! The object of the search is the role of a new hormone in the mammalian body. First, though, the team leader says, “Let’s break out some champagne. Tonight, we’ll all have dinner at a decent restaurant and start talking about what comes next.”
In biology, the first, problem-oriented strategy (for every problem, an ideal organism) has resulted in a heavy emphasis on several dozen “model species.” When in your studies you take up the molecular basis of heredity you will learn a great deal that came from a bacterium living in the human gut,
E. coli
(condensed from its full scientific name,
Escherichia coli
). For the organization of cells in the nervous system, there is inspiration from the roundworm
C. elegans
(
Caenorhabditis elegans
). And for genetics and embryonic development, you will become familiar with fruitflies of the iconic genus
Drosophila
. This is, of course, as it should be. Better to know one thing in depth rather than a dozen things at their surface only.
Still, keep in mind that during the next few decades there will be at most only a few hundred model species, out of close to two million other species known to science by scarcely more than a brief diagnosis and a Latinized name. Although the latter multitude tend to possess most of the same basic processes discovered in the model species, they further display among them an immense array of idiosyncratic traits in anatomy, physiology, and behavior. Think, in one sweep of your mind, first of a smallpox virus, then of all you know about it. Then the same for an amoeba, and then on to a maple tree, blue whale, monarch butterfly, tiger shark, and human being. The point is that each such species is a world unto itself, with a unique biology and place in an ecosystem, and, not least, an evolutionary history thousands to millions of years old.
When a biologist studies a group of species, ranging anywhere from, say, elephants with three living species to ants with fourteen thousand species, he or she typically aims to learn everything possible over a wide range of biological phenomena. Most researchers working this way, following the second strategy of research, are properly called scientific naturalists. They love the organisms they study for their own sake. They enjoy studying creatures in the field, under natural conditions. They will tell you, correctly, that there is infinite detail and beauty even in those that people at first find least attractive—slime molds, for example, dung beetles, cobweb spiders, and pit vipers. Their joy is in finding something new, the more surprising the better. They are the ecologists, taxonomists, and biogeographers. Here is a scenario of a kind I have personally experienced many times:
Think of two biologists hunting in a rain forest, packing heavy collecting equipment, with an online field guide waiting back at camp and DNA analysis at the home laboratory. “Good God, what is that?” one says, pointing to a small, strangely shaped, brilliantly colored animal plastered onto the underside of a palm leaf. “I think it’s a hylid frog,” his companion replies. “No, no, wait, I’ve never seen anything like it. It’s got to be something new. What the hell is it? Listen, get close, and be careful, don’t lose it. There, got it. We’re not going to preserve it yet. You never know, it might be an endangered species. Let’s take it back alive to camp and see what we can find on the Encyclopedia of Life website. There’s that guy at Cornell, he knows all the amphibians like this one pretty well, I think. We might check in with him. First, though, we ought to look around for more specimens, get all the information we can.” The pair arrive back at camp and start pulling up information. What they find is astonishing. The frog appears to be a new genus, unrelated to any other previously known. Scarcely believing, the pair go online to spread news of the discovery to other specialists around the world.
The potential paths you can follow with a scientific career are vast in number. Your choice may take you into one of the scenarios I’ve described, or not. The subject for you, as in any true love, is one in which you are interested and that stirs passion and promises pleasure from a lifetime of devotion.