Letters to a Young Scientist

I recently finished reading Letters to a Young Scientist by Edward Wilson, which is a collection of letters written by the distinguished biologist as advice for a budding researcher. I thought the book was a great read, not just due to the gems of advice scattered throughout the text, but also due to the author’s candid prose. Books of this nature can often become overly preaching, but the friendliness of the author’s tone exemplifies the message and provides a genuine glimpse into a working scientist’s creative process. If you’re short on time (or don’t have the patience to read a book in its’ entirety), then hopefully these highlights provide you with a gist of the content. I’d highly recommend reading it in the original though, since:

I think highlights provide a lossy transmission of the content, often missing important contextual information from surrounding paragraphs.
Reading only highlights can result in a wildly different interpretation from the original (resulting from the sampling bias of only seeing selected highlights).

Regardless, I hope you’re able to enjoy the message as much as I did (and a glimpse of these highlights convinces you to take the leap and read the original). Onwards!

I’ve told you my Pushmataha-to-Harvard story not to recommend my kind of eccentricity (although in the right circumstances it could be of advantage); and I disavow my casual approach to early formal education. I grew up in a different age. You, in contrast, are well into a different era, where opportunity is broader but more demanding.

Put passion ahead of training. Feel out in any way you can what you most want to do in science, or technology, or some other science-related profession. Obey that passion as long as it lasts. Feed it with the knowledge the mind needs to grow.
Sample other subjects, acquire a general education in science, and be smart enough to switch to a greater love if one appears. But don’t just drift through courses in science hoping that love will come to you. Maybe it will, but don’t take the chance. As in other big choices in your life, there is too much at stake. Decision and hard work based on enduring passion will never fail you.
A strong mathematical background does not—I repeat, does not—guarantee success in science. If, on the other hand, you are a bit short in mathematical training, even very short, relax. You are far from alone in the community of scientists, and here is a professional secret to encourage you: many of the most successful scientists in the world today are mathematically no more than semiliterate.
I finally got around to calculus as a thirty-two-year-old tenured professor at Harvard, where I sat uncomfortably in classes with undergraduate students only a bit more than half my age
Mathematics is convenient in that it can be achieved by self-instruction.
Exceptional mathematical fluency is required in only a few disciplines. Particle physics, astrophysics, and information theory come to mind. Far more important throughout the rest of science and its applications, however, is the ability to form concepts, during which the researcher conjures images and processes in visual images by intuition.
Stay as Newton a moment longer. Notice as he did how light passing through curved glass sometimes comes out as a rainbow of colors, always ranging from red to yellow to green to blue to violet. Newton thought that white light is just a mix of the colored lights. He proved it by passing the same array of colors back through a prism, turning the mix back into white light.
As a young man in the 1830s, he (Charles Darwin) made a five-year voyage on a British government vessel, the HMS Beagle, around the coast of South America. He took that long period to explore and think broadly and deeply about the natural world.
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.
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.
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.
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.
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.
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.
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.)
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.
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.
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.
A generalization of this kind, widely applied, with at least a few facts here and there and some logical reasoning behind it, is a theory.
What, then, in broadest terms is the scientific method? The method starts with the discovery of a phenomenon, such as a mysterious ant behavior, or a previously unknown class of organic compounds, or a newly discovered genus of plants, or a mysterious water current in the ocean’s abyss. The scientist asks: What is the full nature of this phenomenon? What are its causes, its origin, its consequence?
It is wise at the outset to figure out as many different solutions as seem possible, then test the whole, either one at a time or in bunches, eliminating all but one. This is called the method of multiple competing hypotheses.
So scientists shuffle along as best they can, intuiting, guessing, tinkering, gaining more information along the way. They persist until solid explanations can be put together and a consensus emerges, sometimes quickly but at other times only after a long period.
That is why many theories, even if they fail, are said to be “heuristic”—they are good for the promotion of discovery. Incidentally, the source of the word eureka—“I have found it!”—
When earlier I said you can surely succeed, I also assumed that you are able to daydream. But be prepared mentally for some amount of chaos and failure. Waste and frustration often attend the earliest stages. When a workable idea emerges, the research becomes more routine, and also much easier to think about and explain to others.
Since so much of good science—and perhaps all of great science—has its roots in fantasy, I suggest that you yourself engage in a bit right now.
Make it a practice to indulge in fantasy about science. Make it more than just an occasional exercise. Daydream a lot. Make talking to yourself silently a relaxing pastime. Give lectures to yourself about important topics that you need to understand. Talk with others of like mind. By their dreams you shall know them.
The ideal scientist thinks like a poet and only later works like a bookkeeper.
Keep in mind that innovators in both literature and science are basically dreamers and storytellers. In the early stages of the creation of both literature and science, everything in the mind is a story. There is an imagined ending, and usually an imagined beginning, and a selection of bits and pieces that might fit in between. In works of literature and science alike, any part can be changed, causing a ripple among the other parts, some of which are discarded and new ones added. The surviving fragments are variously joined and separated, and moved about as the story forms. One scenario emerges, then another. The scenarios, whether literary or scientific in nature, compete with one another. Some overlap. Words and sentences (or equations or experiments) are tried to make sense of the whole thing. Early on, an end to all the imagining is conceived. It arrives at a wondrous denouement (or scientific breakthrough). But is it the best, is it true? To bring the end safely home is the goal of the creative mind. Whatever that might be, wherever located, however expressed, it begins as a phantom that rises, gains detail, then at the last moment either fades to be replaced, or, like the mythical giant Antaeus touching Mother Earth, gains strength. Inexpressible thoughts throughout flit along the edges. As the best fragments solidify, they are put in place and moved about, and the story grows until it reaches an inspired end.
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.
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.
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.
Entrepreneurship is enhanced by performing lots of quick, easily performed experiments. Yes, that’s what I just said: experiments quick and easily performed.
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. Use but don’t love technology. If you need it but find it at all forbiddingly difficult, recruit a better-prepared collaborator. Put the project first and, by any available and honorable means, complete and publish the results.
But is groupthink the best way to create really new science? Risking heresy, I hereby dissent. I believe the creative process usually unfolds in a very different way. It arises and for a while germinates in a solitary brain. It commences as an idea and, equally important, the ambition of a single person who is prepared and strongly motivated to make discoveries in one domain of science or another.
Innovator, creative collaborator, or facilitator: in the course of your successful career, you may well fill each of these roles at one time or another.
I’ve gone into this boyhood story to make a point that may be relevant to your own career trajectory. I have never changed.
THE BETTER EMOTIONS of our nature are felt and examined and understood more deeply during maturity, but they are born and rage in full intensity during childhood and adolescence. Thereafter they endure through the rest of life, serving as the wellsprings of creative work.
THE JOURNEY TO AN UNEXPLORED LAND. This yearning takes a variety of forms: to search for an unknown island; to climb a distant mountain and look beyond; to journey up an unexplored river; to contact a tribe rumored to live there; to discover lost worlds; to find Shangri-la; to land on another planet; to settle and start life anew in a distant country.
SEARCH FOR THE GRAIL. The grail exists in many forms: the powerful formula (or talisman) known to the ancients but lost or kept secret;
Courage in science born of self-confidence (without arrogance!), a willingness to take a risk but with resilience, a lack of fear of authority, a set of mind that prepares you to take a new direction if thwarted, are of great value—win or lose.
One of my favorite maxims is from Floyd Patterson, the light heavyweight boxer who defeated heavier men to win and for a while hold the heavyweight championship. “You try the impossible to achieve the unusual.”
TO MAKE DISCOVERIES in science, both small and important, you must be an expert on the topics addressed. To be an expert innovator requires commitment. Commitment to a subject implies sustained hard work.
To learn more of the details of the great invasive threat, and to find solutions before it has reached catastrophic levels, will require far more science and science-based technology than we now possess. Humanity needs more experts who have the passion and breadth of knowledge to know what to look for in the first place.
Similar wonders await your attention. The universal nature of scientific knowledge yet to be revealed includes a near-infinitude of surprises.
TO MAKE IMPORTANT DISCOVERIES anywhere in science, it is necessary not only to acquire a broad knowledge of the subject that interests you, but also the ability to spot blank spaces in that knowledge. Deep ignorance, when properly handled, is also superb opportunity. The right question is intellectually superior to finding the right answer.
That is the way to create truly original science. Therefore, look especially for oddities, small deviations, and phenomena that seem trivial at first but on closer examination might prove important. Build scenarios in your head when scanning information available to you. Make use of puzzlement.
Even if our intellect were somehow limited to the biosphere alone, scientific research would still be an endless adventure of exploration.
We need a larger scientific effort, and many more scientists in all disciplines. Now I’ll repeat what I’ve said when I began these letters: you are needed.
As factual information grows about any subject—in this case chemical communication—we dream about what it all means. We make propositions about how the phenomena we discovered work and how they came into existence. We find a way to test these various hypotheses. We look for a pattern that emerges when we put the parts together, like a jigsaw puzzle. If we find such a pattern, it becomes the working theory—we use it to think up new kinds of investigation, in order to move the whole subject forward. If this extension doesn’t work very well and now facts appear that contradict the theory, we adjust it. When things get bad enough, we junk the theory and create a new one. With each such step, science moves closer to the truth—sometimes rapidly, sometimes slowly. But always closer.
When biologists see a number go up following a disturbance and then fall back to the original level, whether body temperature, density of bacteria in a flask, or biological diversity on a continent, they suspect that an equilibrium exists in the system.
In science every answer raises more questions.
Successful research doesn’t depend on mathematical skill, or even the deep understanding of theory. It depends to a large degree on choosing an important problem and finding a way to solve it, even if imperfectly at first. Very often ambition and entrepreneurial drive, in combination, beat brilliance.