The memory of persistence

In Origins of Genius, which is one of my favorite books on creativity, the psychologist Dean Simonton makes an argument that I’ve tried to bear in mind ever since I first read it. While discussing the problem of creative productivity, Simonton states emphatically: “If the number of influential works is directly proportional to the total number of works produced, then the creators with the most masterpieces will be those with the most ignored and neglected products! Even the most supreme creative genius must have their careers punctuated with wasted efforts.” After quoting W.H. Auden, who observes that a major poet will tend to write more bad poems than a minor one, he continues:

If the creative genius is generating failures as well as successes, this seems to support the assumption that the creative process is to a certain extent blind. Even the greatest creators possess no direct and secure path to truth or beauty. They cannot guarantee that every published idea will survive further evaluation and testing at the hands of audiences or colleagues. The best the creative genius can do is to be as prolific as possible in generating products in the hope that at least some subset will survive the test of time.

This still ranks as one of the most significant insights into the creative process that I’ve ever seen, and Simonton sums it up elsewhere, like a true poet, in a form that can be easily remembered: “Quality is a probabilistic function of quantity.”

Simonton has a new book out this week, The Genius Checklist, with a long excerpt available on Nautilus. In the article, he focuses on the problem of intelligence tests, and in particular on two cases that point to the limitations of defining genius simply as the possession of a high IQ. One revolves around Lewis M. Terman, the creator of the modern intelligence scale, who had the notion of testing thousands of students and tracking the top performers over time. The result was an ongoing study of about 1,500 men and women, known as the “Termites,” some of whom are still alive today. As Simonton notes, the results didn’t exactly support Terman’s implicit assumptions:

None of [the Termites] grew up to become what many people would consider unambiguous exemplars of genius. Their extraordinary intelligence was channeled into somewhat more ordinary endeavors as professors, doctors, lawyers, scientists, engineers, and other professionals…Furthermore, many Termites failed to become highly successful in any intellectual capacity. These comparative failures were far less likely to graduate from college or to attain professional or graduate degrees, and far more likely to enter occupations that required no higher education whatsoever…Whatever their differences, intelligence was not a determining factor in those who made it and those who didn’t.

Terman also tested two future Nobel laureates—Luis Alvarez and William Shockley—who were rejected because they didn’t score highly enough. And Simonton notes that neither James Watson nor Richard Feynman, whose biography is actually called Genius, did well enough on such tests to qualify for Mensa.

Even if you’re a fan of Marilyn vos Savant, this isn’t particularly surprising. But I was even more interested in Simonton’s account of the work of Catharine Cox, Terman’s colleague, who decided to tackle the problem from the opposite direction—by starting with a list of known luminaries in all fields and trying to figure out what their tested IQs would have been, based solely on biographical information. This approach has obvious problems as well, of course, but her conclusion, which appears in her book The Early Mental Traits of Three Hundred Geniuses, seems reasonable enough: “High but not the highest intelligence, combined with the greatest degree of persistence, will achieve greater eminence than the highest degree of intelligence with somewhat less persistence.” And in her discussion of qualities that seem predictive of success, persistence is prominently mentioned:

We may conclude that the following traits and trait elements appearing in childhood and youth are diagnostic of future achievement: an unusual degree of persistence—tendency not to be changeable, tenacity of purpose, and perseverance in the face of obstacles—combined with intellective energy—mental work bestowed on special interests, profoundness of apprehension, and originality of ideas—and the vigorous ambition expressed by the possession to the highest degree of desire to excel.

Cox concludes: “Achievements…are not the accidents of a day. They are the natural outgrowth in individuals of superior general powers of persistent interest and great zeal combined with rare special talents.”

If we really want to identify the geniuses of the future, it seems, we should look for persistence as well as intelligence, and we might even be tempted to develop a test that would gauge a student’s “tenacity of purpose.” The ability to remain focused in the face of failures and setbacks is clearly related to Simonton’s rule about quality and quantity, which implies that a genius, to borrow John Gardner’s definition of the true writer, is someone who doesn’t quit. But there’s an even more important point to be made here. As I noted just the other day, it’s easier to fail repeatedly when you occupy a social position that protects you to some extent from the consequences. It can be hard to be “as prolific as possible in generating products” when even one mistake might end your creative journey forever. And our culture has been far more forgiving of some categories of people than of others. (In discussing Terman’s results, Simonton makes the hard decision to omit women from the group entirely: “We’re talking only of the males here, too. It would be unfair to consider the females who were born at a time in which all women were expected to become homemakers, no matter how bright.” And he might also have cited the cultural pressures that discourage a woman from taking risks that are granted to a man.) When you look at lists of canonical geniuses, like the authors of the great books, they can start to seem maddeningly alike—and if we define privilege in part as the freedom to make repeated mistakes, it’s no wonder. Over time, this also reduces the diversity of the ideas that are available for cultural selection, which can lead to a crisis in itself. The only solution is to increase the range of voices, and it isn’t easy. In the absence of such advantages, even the individuals who beat the odds must have been confronted at every turn by excellent reasons to give up. But nevertheless, they persisted.

The next three years

No matter what your field might be, the most important factor in doing interesting work is often the selection of problems to tackle. We don’t always get to decide how we spend our time from one day to the next, but we occasionally arrive at decision points that will determine what we’ll be doing for years to come. Such moments tend to happen when we aren’t fully prepared for them, like when we have to pick a college major, and even as adults, we frequently fall back on instinct—and if some people have greater success than others, it might just be because they have better hunches. But we don’t always make such choices with the seriousness that they deserve. This might appear to go against the principle that ideas are cheap and execution is what really counts, but they aren’t as inconsistent as they seem. It’s true that there’s a big difference between having a bright idea and actually seeing it through, and that you should worry less about people stealing your ideas than about successfully bringing projects to completion. The world is full of good ideas, and if you lose out on one, there’s always another. But not every idea is equally suited for what you bring to it, and if you choose poorly, it can take you in the wrong direction for years. And it’s often the ideas that seem the most exciting at first that turn out to be the most misleading. (If I seem particularly interested in the subject right now, it’s because I’m about to deliver what I expect will effectively be the final draft of my book Astounding. The next few months will be taken up by the practical side of book publication, and I really need a break. But at some point, I’m going to have to figure out what to do next. And I’m writing this post to set down some guidelines for my future self about where to look.)

Not surprisingly, this issue gets a lot of attention in science and technology, which are fields in which the choice of subject can be crucial. In Advice for a Young Scientist, Peter Medawar has an entire chapter titled “What Should I Research?”, and he offers a good place to start:

It can be said with complete confidence that any scientist of any age who wants to make important discoveries must study important problems. Dull or piffling problems yield dull or piffling answers. It is not enough that a problem be “interesting”—almost any problem is interesting if it is studied in sufficient depth…In choosing topics for research and departments to enlist in, a young scientist must beware of following fashion. It is one thing to fall into step with a great concerted movement of thought such as molecular genetics or cellular immunology, but quite another merely to fall in love with prevailing fashion for, say, some new histochemical procedure or chemical gimmick.

In his fascinating, sometimes infuriating memoir Avoid Boring People, James D. Watson makes a similar point: “Mopping up the details after a major discovery has been made by others will not likely make you out as an important scientist. Better to leapfrog ahead of your peers by pursuing an important objective that most others feel is not for the current moment.” But he also qualifies this in a way that seems worth remembering:

I feel comfortable taking on a problem only when I believe meaningful results can come over a three-to-five-year interval. Risking your career on problems when you have any a tiny chance to see a finish line is not advisable. But if you have reason to believe you have a thirty percent chance of solving over the next two or three years a problem that most others feel is not for this decade, that’s a shot worth taking.

Watson knows what he’s talking about, but his own claim to fame—the discovery of the structure of DNA—was also due in part to luck and good timing. As Max Perutz, who won a Nobel Prize for his work on hemoglobin, recalled:

I sometimes envied Jim. My own problem took thousands of hours of hard work, measurements, calculations. I often thought that there must be some way to cut through it—that there must be, if only I could see it, an elegant solution. There wasn’t any. For Jim’s there was an elegant solution, which is what I admired. He found it partly because he never made the mistake of confusing hard work with hard thinking; he always refused to substitute one for the other.

Success, in other words, doesn’t just depend on choosing an important subject, but finding one in which you might hold an advantage. As Herbert A. Simon put it so memorably:

I advise my graduate students to pick a research problem that is important (so that it will matter if it is solved), but one for which they have a secret weapon that gives some prospect of success. Why a secret weapon? Because if the problem is important, other researchers as intelligent as my students will be trying to solve it; my students are likely to come in first only by having access to some knowledge or research methods the others do not have…In reviewing the record, I observe that I have always been pretty careful in setting the odds, and have usually behaved like an honest professional gambler…It is not unfair to have the experiences or to be at the places that provide one with a secret weapon.

Such weapons aren’t always obvious, and recognizing them can require a genius of its own. (For example, Simon writes that one of his secret weapons in the fifties was “a digital computer, and an idea—derived from contact with computers—that it would be used as a general processor of symbols,” which is hardly a trivial insight.) I’ve said elsewhere that I like to focus on areas where information is “available, but obscure,” and I often find myself thinking of an anonymous comment on a thread on Hacker News:

Find an unsexy domain that you have more access to than the average person. Start to build domain expertise in that area as quickly as you can (people are surprisingly willing to talk when you don’t want to sell them something, but just learn about how they do things)…Loop back with the people in the unsexy industry to get feedback. Remember, not all industries are bombarded with technology—you’ll need to strike a balance between showing them something sufficiently “fancy” to pique interest, and abstracting away your technology so they focus on a problem it solves…Build things in a low-cost way and use that to identify tangentially related problems until you think you’ve found a big enough pain point.

That’s basically how I wrote my book, and I’ve since come to realize how lucky I was to choose a subject that was neglected enough for me to do something useful and new, while also interesting enough to open doors. Frankly, I’m not sure if I’ll ever be able to do it again, although I’ll be thinking hard about how. I’ll make the best choice that I can. And I’ll know whether or not I was right in about three years.

Our fearful symmetry

Yesterday, I spent an hour fixing my garage door, which got stuck halfway up and refused to budge. I went about it in the way I usually approach such household tasks: I took a flashlight and a pair of vise-grips and stared at it for a while. In this case, for once, it worked, even if I’m only postponing the inevitable service call. But it wouldn’t have occurred to me to tackle it myself in the first place—when I probably wouldn’t have tried to fix, say, my own car by trial and error—if it hadn’t been for two factors. The first is that the workings were all pretty visible. On each side, there’s basically just a torsion spring, a steel cable, and two pulleys, all of it exposed to plain sight. The second point, which was even more crucial, is that a garage door is symmetrical, and only one side was giving me trouble. Whenever I wasn’t sure how the result should look, I just had to look at the other half and mentally reflect it to its mirror image. It reminded me of how useful symmetry can be in addressing many problems, as George Pólya notes in How to Solve It:

Symmetry, in a general sense, is important for our subject. If a problem is symmetric in some ways we may derive some profit from noticing its interchangeable parts and it often pays to treat those parts which play the same role in the same fashion…Symmetry may also be useful in checking results.

And if I hadn’t been able to check my work along the way using the other side of the door, I doubt I would have attempted to fix it at all.

But it also points at a subtle bias in the way we pick our problems. There’s no question that symmetry plays an important role in the world around us, and it provides a solid foundation for the notion that we can use beauty or elegance as an investigative tool. “It seems that if one is working from the point of view of getting beauty in one’s equations, and if one has a really sound insight, one is on a sure line of progress,” Paul Dirac famously said, and Murray Gell-Mann gave the best explanation I’ve ever found of why this might be true:

There’s a quotation from Newton, I don’t remember the exact words but lots of other physicists have made the same remark since—that nature seems to have a remarkable property of self-similarity. The laws—the fundamental laws—at different levels seem to resemble one another. And that’s probably what accounts for the possibility of using elegance as a criterion [in science]. We develop a mathematical formula, say, for describing something at a particular level, and then we go to a deeper level and find that in terms of mathematics, the equations at the deeper level are beautifully equivalent. Which means that we’ve found an appropriate formula.

Gell-Mann concludes: “And that takes the human being, human judgment, out of it a little. You might object that after all we are the ones who say what elegance is. But I don’t think that’s the point.”

He’s right, of course, and there are plenty of fields in which symmetry and self-similarity are valuable criteria. Yet there’s also a sense in which we’re drawn to problems in which such structures appear, while neglecting those that aren’t as amenable to symmetrical thinking. Just as I was willing to take apart my garage door when I wouldn’t have done the same with my car—which, after all, has a perfectly logical design—it’s natural for us to prefer problems that are obviously symmetrical or that hold out the promise of elegance, much as we’re attracted to the same qualities in the human face. But there are plenty of important questions that aren’t elegant at all. I’m reminded of what Max Perutz, who described the structure of hemoglobin, said about the work of his more famous colleague James Watson:

I sometimes envied Jim. My own problem took thousands of hours of hard work, measurements, calculations. I often thought that there must be some way to cut through it—that there must be, if only I could see it, an elegant solution. There wasn’t any. For Jim’s there was an elegant solution, which is what I admired. He found it partly because he never made the mistake of confusing hard work with hard thinking; he always refused to substitute one for the other.

In The Eighth Day of Creation, Horace Freehand Judson calls this “the most exact yet generous compliment I have ever heard from one scientist to another.” But there’s also a wistful acknowledgement of the luck of the draw. Both Perutz and Watson were working on problems of enormous importance, but only one of them had an elegant solution, and there was no way of knowing in advance which one it would be.

Given the choice, I suspect that most of us would prefer to work on problems that exhibit some degree of symmetry: they’re elegant, intuitive, and satisfying. In the absence of that kind of order, we’re left with what Perutz calls “thousands of hours of hard work, measurements, calculations,” and it isn’t pretty. (As Donald Knuth says in a somewhat different context: “Without any underlying symmetry properties, the job of proving interesting results becomes extremely unpleasant.”) When we extrapolate this preference to the culture as a whole, it leads to two troubling tendencies. One is to prioritize problems that lend themselves to this sort of attack, while overlooking whole fields of messier, asymmetrical phenomena that resist elegant analysis—to the point where we might even deny that they’re worth studying at all. The other is to invent a symmetry that isn’t there. You can see both impulses at work in the social sciences, which tend to deal with problems that can’t be reduced to a series of equations, and they’re particularly insidious in economics, which is uniquely vulnerable to elegant models that confirm what existing interest groups want to hear. From there, it’s only a small step to more frightening forms of fake symmetry, as Borges writes in “Tlön, Uqbar, Orbis Tertius”: “Any symmetry with a resemblance of order—dialectical materialism, anti-Semitism, Nazism—was sufficient to entrance the minds of men.” And the first habit has a way of leading to the second. The more we seek out problems with symmetry while passing over those that lack it, the more likely we become to attribute false symmetries to the world around us. Symmetry, by definition, is a beautiful thing. But it can also turn us into suckers for a pretty face.

Tennis and girls at Cambridge

They say all [James Watson] did in Cambridge was play tennis and chase girls. But there was a serious point to that. I sometimes envied Jim. My own problem took thousands of hours of hard work, measurements, calculations. I often thought that there must be some way to cut through it—that there must be, if only I could see it, an elegant solution. There wasn’t any. For Jim’s there was an elegant solution, which is what I admired. He found it partly because he never made the mistake of confusing hard work with hard thinking; he always refused to substitute one for the other. Of course, he had time for tennis and girls.

—Max Perutz