I’ve been reading E. O. Wilson’s new book, Letters to a Young Scientist. It’s the latest addition to the list of “advice from older famous scientists” books, which also includes Peter Medawar’s similarly titled Advice To A Young Scientist and what is probably the grandfather of the entire genre, Ramón y Cajal’s Advice for a Young Investigator. A definite personal point of view comes across in this one, since its author is famously unafraid to express his strongly held opinions. There’s some 100-proof Wilson in this book as well:
. . .Science is the wellspring of modern civilization. It is not just “another way of knowing”, to be equated with religion or transcendental meditation. It takes nothing away from the genius of the humanities, including the creative arts. Instead it offers ways to add to their content. The scientific method has been consistent better than religious beliefs in explaining the origin and meaning of humanity. The creation stories of organized religions, like science, propose to explain the origin of the world, the content of the celestial sphere, and even the nature of time and space. These mythic accounts, based mostly on the dreams and epiphanies of ancient prophets, vary from one religion’s belief to another. Colorful they are, and comforting to the minds of believers, but each contradicts all the others. And when tested in the real world they have so far proved wrong, always wrong.
And that brings up something else about all the books of this type: they’re partly what their titles imply, guides for younger scientists. They’re partly memoirs of their authors’ lives (Francis Crick’s What Mad Pursuit is in this category, although it has a lot of useful advice itself). And they’re all attempts to explain what science really is and how it really works, especially to readers who may well not be scientists themselves.
Wilson does some of all three here, although he uses examples from his own life and research mainly as examples of the advice he’s giving. And that advice, I think, is almost always on target. He has sections on how to pick areas of research, methods to use for discovery, how to best spend your time as a scientist, and so on. The book is absolutely, explicitly aimed at those who want to make their mark by discovering new things, not at those who would wish to climb other sorts of ladders. (For example, he tells academic scientists “Avoid department-level administration beyond thesis committee chairmanships if at all fair and possible. Make excuses, dodge, plead, trade.” If your ambition is to become chairman of the department or a VP of this or that, this is not the book to turn to.
But I’ve relentlessly avoided being put onto the managerial track myself, so I can relate to a lot of what this book has to say. Wilson spent his life at Harvard, so much of his advice has an academic slant, but the general principles of it come through very clearly. Here’s how to pick an area to concentrate on:
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. . .I advise you to look for a chance to break away, to find a subject you can make your own. . .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.
One of the most interesting parts of the book for me is its take on two abilities that most lay readers would take as prerequisites for a successful scientist: mathematical ability and sheer intelligence in general. The first is addressed very early in the book, in what may well become a famous section:
. . .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.
He recommends making up this deficiency, as much as you find it feasible to do so, but he’s right. The topic has come up around here – I can tell you for certain that the math needed to do medicinal chemistry is not advanced, and mostly consists of being able to render (and understand) data in a variety of graphical forms. If you can see why a log/log plot tends to give you straightened-out lines, you’ve probably got enough math to do med-chem. You’ll also need to understand something about statistics, but (again) mostly in how to interpret it so you aren’t fooled by data. Pharmacokinetics gets a bit more mathematical, and (naturally) molecular modeling itself is as math-heavy as anyone could want, but the chemistry end of things is not.
As for intelligence, see what you think about this:
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. . .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 in an intermediate degree: bright enough to see what can be done but not so bright as to become bored doing it.
By “entrepreneurship”, he doesn’t mean forming companies. That’s Wilson’s term for opportunistic science – setting up some quick and dirty experiments around a new idea to see what might happen, and being open to odd results as indicators of a new direction to take your work. I completely endorse that, in case anyone cares. As for the intelligence part, you have to keep in mind that this is E. O. Wilson telling you that you don’t need to be fearsomely intelligent to be successful, and that his scale for evaluating this quality might be calibrated a bit differently from the usual. As Tom Wolfe put it in his essay in Hooking Up, one of Wilson’s defining characteristics has been that you could put him down almost anywhere on Earth and he’d be the smartest person in the room. (I should note that Wolfe’s essay overall is not exactly a paean, but he knows not to underestimate the guy).
I think that intelligence falls under the “necessary but not sufficient” heading. And I probably haven’t seen that many people operate whom the likes of E. O. Wilson would consider extremely smart, so I can’t comment much on what happens at that end of the scale. But the phenomenon of people who score very highly on attempted measures of intelligence, but never seem to make much of themselves, is so common as to be a cliché. You cannot be dumb and make a success of yourself as a research scientist. But being smart guarantees nothing.
As an alternative to mathematical ability and (very) high intelligence, Wilson offers the prescription of hard work. “Scientists don’t take vacations”, he says, they take field trips. That might work out better if you’re a field biologist, but not so well for (say) organic chemistry. And actually, I think that clearing your head with some time off actually can help out a great deal when you’re bogged down in some topic. But having some part of your brain always on the case really is important. Breaks aside, long-term sustained attention to a problem is worth a lot, and not everyone is capable of it.
Here’s more on the opportunistic side of things:
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.
I know exactly what he’s talking about here, and I think he’s completely right. Many, many big discoveries have their beginnings in just this sort of thing. Isaac Asimov was on target when he said that the real sound of a breakthrough was not the cry of “Eureka!” but a puzzled voice saying “Hmm. That’s funny. . .”
Well, the book has much more where all this comes from. It’s short, which tempts a person to read through it quickly. I did, and found that this slighted some of the points it tries to make. It improved on a second pass, in my case, so you may want to keep this in mind.