Alec Nevala-Lee

Thoughts on art, creativity, and the writing life.

Posts Tagged ‘Peter Medawar

My ten creative books #1: On Growth and Form

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On Growth and Form

Note: For the next two weeks, I’ll be counting down ten books that have influenced the way that I think about the creative process, in order of the publication of their first editions. It’s a very personal list that reflects my own tastes and idiosyncrasies, and I’m always looking for new recommendations.

In my first semester in college, I won something called the Detur Prize, which presented undergraduates who had earned good grades with an enticing award: a copy of a book of their choice. When you’re eighteen years old and just starting to figure out who you are, a decision like this quickly becomes a declaration of intent: I felt obliged to pick a title that said something about what I hoped to accomplish. A quick glance at the spines of the books selected by my fellow students confirmed that I wasn’t alone in this—the most popular choices seemed to be The Yale Shakespeare and The Wealth of Nations, both of which were revealing in themselves. After a lot of thought, I settled on a book that surprised some of my friends: On Growth and Form by D’Arcy Wentworth Thompson. And though it took me the better part of the next decade to actually finish reading it, I knew from the start that it was the right choice, and my feelings still haven’t changed. Thompson’s weighty masterpiece is the best evidence yet presented that science and the humanities form a continuous whole, with the patterns in one sphere shedding light on the other, but only if channeled through the mind of an author qualified to draw those connections. And Thompson, who uniquely combined the strengths of a scientist, a classicist, and a mathematician, stands as one of the last of our truly comprehensive intelligences.

As its title implies, On Growth and Form covers a dazzling array of topics. Thompson offers up original research and insights on turtle shells, narwhal’s horns, horse’s teeth, soap bubbles, and honeycombs. He explains how a cell finds its shape, how leaves are arranged on a branch, how an insect wing is structured, how birds and fish move, and how human beings grow. And he does it with style. The Nobel laureate Peter Medawar once wrote:

I think that Growth and Form is beyond comparison the finest work of literature in all the annals of science that have been recorded in the English tongue. There is a combination here of elegance of style with perfect, absolutely unfailing clarity that has never to my knowledge been surpassed… Growth and Form will remain forever worth reading as a text in the exacting discipline of putting conceptions accurately into words.

And my lifetime of reading Thompson—or, more accurately, reading in Thompson—only confirms that verdict. If Thomas Young, in the words of his biographer Andrew Robinson, was the last man who knew everything, Thompson is the most recent figure who could mount a convincing challenge. That kind of universality is no longer feasible. But On Growth and Form stands as a permanent monument to the idea that such unification was not only possible, but essential. That’s why I chose it two decades ago. And it’s why it still fills me with awe today.

Written by nevalalee

July 30, 2018 at 9:00 am

The next three years

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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.

Written by nevalalee

March 2, 2018 at 8:44 am

Quote of the Day

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To be creative, scientists need libraries and laboratories and the company of other scientists; certainly a quiet and untroubled life is a help. A scientist’s work is in no way deepened or made more cogent by privation, anxiety, distress, or emotional harassment. To be sure, the private lives of scientists may be strangely and even comically mixed up, but not in ways that have any special bearing on the nature and quality of their work. If a scientist were to cut off an ear, no one would interpret such an action as evidence of an unhappy torment of creativity; nor will a scientist be excused any bizarrerie, however extravagant, on the grounds that he is a scientist, however brilliant.

Peter Medawar, Advice to a Young Scientist

Written by nevalalee

December 28, 2017 at 7:30 am

The Theater of Apollo

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In 1972, the physiologist Albert Szent-Györgyi, who won a Nobel Prize for his work on Vitamin C and the citric acid cycle, wrote a famous letter to the journal Science. He noted that scientists, like most creative types, can be roughly divided into two categories, variously known as the classical and the romantic, the systematic and the intuitive, or, as the physicist John R. Platt proposed, the Apollonian and the Dionysian. “In science,” Szent-Györgyi wrote, “the Apollonian tends to develop established lines to perfection, while the Dionysian rather relies on intuition and is more likely to open new, unexpected alleys for research.” After defining intuition as “a sort of subconscious reasoning, only the end result of which becomes conscious,” he continued:

These are not merely academic problems. They have most important corollaries and consequences. The future of mankind depends on the progress of science, and the progress of science depends on the support it can find. Support most takes the form of grants, and the present methods of distributing grants unduly favor the Apollonian. Applying for a grant begins with writing a project. The Apollonian clearly sees the future line of his research and has no difficulty writing a clear project. Not so the Dionysian, who knows only the direction in which he wants to go out into the unknown; he has no idea what he is going to find there and how he is going to find it. Defining the unknown or writing down the subconscious is a contradiction in absurdum. In his work, the Dionysian relies, to a great extent, on accidental observation…The Dionysian is often not only unable to tell what he is going to find, he may even be at a loss to tell how he made his discovery.

Szent-Györgyi, who clearly identified as a Dionysian, went on to state that writing grant proposals was always an “agony” for him, and that while he always tried to live up to Leo Szilard’s commandment “Do not lie without need,” he often had no alternative: “I filled up pages with words and plans I knew I would not follow. When I go home from my laboratory in the late afternoon, I often do not know what I am going to do the next day. I expect to think that up during the night. How could I tell, then, what I would do a year hence?” He added that while his “fake projects” were always accepted, his attempts to write down honestly what he thought he would do were invariably rejected:

This seems quite logical to me; sitting in an easy chair I can cook up any time a project which must seem quite attractive, clear, and logical. But if I go out into nature, into the unknown, to the fringes of knowledge, everything seems mixed up and contradictory, illogical, and incoherent. This is what research does; it smooths out contradiction and makes things simple, logical, and coherent. So when I bring reality into my projects, they become hazy and are rejected. The reviewer, feeling responsible for “the taxpayer’s money,” justly hesitates to give money for research, the lines of which are not clear to the applicant himself.

Szent-Györgyi concluded by saying that in his lifetime, he made two important discoveries, both of which “were rejected offhand by the popes of the field,” and that he had no doubt that they both would have been bounced with equal dispatch if he had tried to describe them in a grant application. And he left the problem without any real solution, except the suggestion that proposals for future research should either take into account the scientist’s earlier work or consider “the vouching of an elder researcher” who can attest to the applicant’s ability.

I’ve never had to apply for a grant, and I’d be curious to hear the perspectives of readers of this blog who have. But I’ve written book proposals, which presented me with a milder version of the dilemma that Szent-Györgyi described. (It’s milder, in part, because writers often work on spec, which means that the submission process in commercial publishing isn’t subject to the same pressures that you see in academia.) A proposal is a kind of map or miniature version of the finished work, whether it’s six pages long or seventy, and the author usually prepares it in a relatively short period of time, before the research or writing process has even begun. As a result, it can’t capture the information that the writer has to discover en route, as Ted Kooser puts it. It can only hint at what the author hopes to do or find, which, depending on your point of view, amounts to either a strong inference or a lie. It’s a system set up to reward or accommodate writers whose style lends itself to that kind of presentation, or who have the skills to fake it, and there are undoubtedly gifted people whom it excludes or discourages. Like grant writing, it exists primarily for the convenience of institutions, not individuals, and it creates a parallel world of obstacles that have to be navigated to get to the real challenge of doing interesting work. You could call it a necessary evil, or, if you’re feeling generous, you could argue that it’s a proxy for kinds of talent that can’t be measured directly. If you can handle the artificial, even ritualized strictures of the grant or proposal process, it’s a sign that you can tackle more important problems. Like an audition or a job interview, it takes on aspects of a game, and we’d like to believe that the test it provides will be predictive of good results later on.

It isn’t hard to find the flaws in this argument. (Among other things, until recently, I would have argued that the organizational demands of a successful political campaign serve as a similar audition for holding high office, and we’ve all seen how that turned out.) The greatest danger is the trap presented by all rituals of admission, which is that they ultimately measure nothing but the ability to pass the test. Just as college entrance exams and whiteboard interviews have inspired a cottage industry of books, tutors, and classes designed to coach applicants who can afford to pay for it, grant writing has mutated into grantsmanship, with its own rules, experts, and infrastructure. And the risks, as Szent-Györgyi said more than forty years ago, are very real. It’s a system that rewards researchers who are content, as Peter Medawar once put it, to figure out why thirty-six percent of sea urchin eggs have a tiny little black spot, simply because it’s the kind of project that can get funding. The grant application process may also play a role in the replication crisis in the social sciences, since it encourages applicants to project an unwarranted certainty that can be hard to relinquish when the data isn’t there. Perhaps worst of all, it penalizes whole groups of people, not just our hypothetical Dionysian geniuses, but also women and minorities who can’t always afford to play the game—and Szent-Györgyi’s otherwise reasonable suggestion that weight be granted to “the vouching of an elder researcher” only compounds the problem. If an Apollonian system resulted in a society of Apollos, we might be inclined to forgive it, but that isn’t the case. To the extent that it works, it’s because the division between Apollonian and Dionysian isn’t an absolute one, and most people learn to draw on each side at different times. Those who succeed have to be less like Apollo or Dionysus than, perhaps, like Hermes, the trickster who can change in response to the demands that the situation presents. And as flawed as the current system may be, we’ll have reason to miss it if it disappears.

Written by nevalalee

March 23, 2017 at 9:30 am

The spot on the sea urchin’s egg

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Peter Medawar

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.

As an example of research work not worth doing, Lord Zuckerman invented the cruelly apt but not ridiculously farfetched example of a young zoology graduate who has decided to try to find out why thirty-six percent of sea urchin eggs have a tiny little black spot on them. This is not an important problem; such a graduate student will be lucky if his work commands the attention or interest of anyone except perhaps the poor fellow next door who is trying to find out why sixty-four percent of sea urchin eggs do not have a little black spot on them. Such a student has committed a kind of scientific suicide, and his supervisors are very much to blame. The example is purely imaginary, of course, for Lord Zuckerman knows very well that no sea urchin eggs are spotted.

Peter Medawar, Advice to a Young Scientist

Written by nevalalee

October 22, 2016 at 7:30 am

My great books #2: On Growth and Form

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On Growth and Form

Note: I’m counting down my ten favorite works of nonfiction, in order of the publication dates of their first editions, and with an emphasis on books that deserve a wider readership. You can find the earlier installments here.

In my first semester in college, I won something called the Detur Prize, which honored undergraduates who had achieved high grades with an enticing award: a copy of a book of their choice. When you’re eighteen years old and just starting to figure out who you are, a decision like this becomes a statement of intention: I felt obliged to pick a title that said something about what I hoped to accomplish. A quick glance at the spines of the books selected by my fellow students confirmed that I wasn’t alone in this—the most popular choices seemed to be The Yale Shakespeare and The Wealth of Nations, both of which were revealing in themselves. After a lot of thought, I settled on a book that surprised some of my friends: On Growth and Form by D’Arcy Wentworth Thompson. And though it took me the better part of the next decade to actually finish reading it, I knew from the start that it was the right choice, and I haven’t wavered in that certainty since. Thompson’s masterpiece is the best evidence yet presented that science and the humanities form a continuous whole, and that the patterns that you find in one sphere can shed light on the other, but only if channeled through the mind of an author qualified to draw those connections. And Thompson, who uniquely combined the strengths of a scientist, a classicist, and a mathematician, stands as one of the last truly comprehensive intelligences that the world ever produced.

As its title implies, On Growth and Form covers a dazzling array of topics: Thompson offers up original research and insights on turtle shells, narwhal’s horns, horse’s teeth, soap bubbles, and honeycombs. He explains how a cell finds its shape, how leaves are arranged on a branch, how an insect wing is structured, how birds and fish move, and how human beings grow. And he does it with style. The Nobel laureate Peter Medawar once wrote:

I think that Growth and Form is beyond comparison the finest work of literature in all the annals of science that have been recorded in the English tongue. There is a combination here of elegance of style with perfect, absolutely unfailing clarity that has never to my knowledge been surpassed… Growth and Form will remain forever worth reading as a text in the exacting discipline of putting conceptions accurately into words.

And my lifetime of reading Thompson—or, more accurately, reading in Thompson—only confirms that verdict. If Thomas Young, in the words of his biographer Andrew Robinson, was the last man who knew everything, Thompson is the most recent figure who could mount a convincing challenge. That kind of universality is no longer feasible. But On Growth and Form stands as a permanent monument to the idea that such unification was not only possible, but essential. That’s why I chose it two decades ago. And it’s why it still fills me with awe today.

Written by nevalalee

November 3, 2015 at 9:00 am

The availability factor

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Theobald Smith

Whenever I do a reading from The Icon Thief, I like to joke that I wrote a novel about the Rosicrucians mostly because they were available. Other conspiracy thrillers had already sucked most of the pulp out of the likes of the Freemasons, the Illuminati, and the Priory of Sion, and although the Rosicrucian novel was a genre of its own as late as the nineteenth century, there hadn’t been any examples of it in a long time. There was also a huge amount of material—not all of it particularly interesting—on Rosicrucianism and its relationship to later occult and artistic movements, so I knew early on that I’d have my choice of sources. And I suspect that if I’d done some digging and discovered that there wasn’t much there, I would have chosen a different subject entirely. The shape of that novel, in short, was largely determined by the access I had to the resources I needed: I knew before I even began laying out the plot that I wouldn’t suffer for lack of background. The same is true of many of my short stories, the majority of which were inspired by an existing book or article that offered up an abundance of useful, concrete ideas. In many cases, the plot was explicitly tailored around the facts that I had at my disposal, and if I ended up focusing on one area rather than others, it was because of the tools I happened to have at hand.

The question of availability—or, more specifically, of whether or not you have a reasonable expectation of finding the materials you need—governs a surprising amount of creative work, both in the arts and in other fields. In The Art of Scientific Investigation, W.I.B. Beveridge tells us: “The great American bacteriologist Theobald Smith said that he always took up the problem that lay before him, chiefly because of the easy access of material, without which research is crippled.” It’s a strategy that has affinities with bricolage, or the art of making do with whatever is lying around, and it also reflects the sifting and filtering process required to distill any body of information into a readable form. (“The output an ounce, the labor a year,” as Mayakovsky says, and it only works if you have plenty of ore in the first place.) There seems to be a critical mass you need to reach before you can start serious work on any project, and although much of it has to be spun out of the creator’s own substance, like Whitman’s noiseless patient spider, it doesn’t hurt to have a ready reservoir of ideas from the outside world. Making anything worthwhile is hard enough as it is, so it helps to know from the start that you have access to a decent body of material. And this can come from the details of your own life as much as from anything else: “Write what you know” is less an admonition from up on high than a practical guideline for ensuring that you have enough with which to proceed.

Robert Scott Root-Bernstein

Of course, there are risks to this approach, since it can lead to an excessive focus on the obvious. In his valuable book Discovering, Robert Scott Root-Bernstein writes:

Where does one find problems? Not where answers already exist. There is an old story about a drunk who loses his key in a dark alley. A policeman wandering by later finds the drunk on his hands and knees under the street lamp at the corner. “Hey! What are you doing there?” “Looking for my key.” “Where’d ya lose it?” “In the alley.” “Then why are you looking under the lamp?” “It’s too dark to see in the alley.” Like the drunk, too many scientists choose their research projects within the sphere of existing light. They are scared to be ignorant, scared to founder. They are what Peter Medawar calls “philagnoists”—lovers of their own ignorance. Not so the best scientists, who seek out the unknown. Peter Carruthers, head of theoretical physics at Los Alamos, speaks for many when he says: “There’s a special tension to people who are constantly in the position of making new knowledge. You’re always out of equilibrium. When I was young, I was deeply troubled by this. Finally, I realized that if I understood too clearly what I was doing, where I was going, then I probably wasn’t working on anything very interesting.” Don’t be paranoid of the void.

Later on, Root-Bernstein adds: “There will be a crowd searching under the light. If you assume that keys to understanding nature are fairly randomly spread about, your chances of finding one are much better out in the dark because you’re likely to be the only one searching there.” The problem, then, is how to reconcile this with the availability factor, and as with most aspects of the creative process, the key lies in striking a balance: the excursions we make into the unknown are most likely to succeed if we’ve tethered ourself to a stable body of known facts, particularly if it happens to border an area of darkness. And such islands of material are more common than you might think. As a writer, I’ve learned to focus on information that is available but obscure: the world is full of ideas or subjects that have been explored up to a point and then abandoned, or relegated to a forgotten corner of intellectual history. It’s why I’ve made a point of seeking out the books that nobody reads anymore, or using a single idea as a wedge to pry my way into a body of knowledge that I wouldn’t have found if I hadn’t been looking for it. Again and again, I’ve been amazed to find ideas that were neglected, or known only to specialists, that provided a foundation for fascinating stories. It’s a big world out there, and not every lamp has a crowd beneath it. If half of being a writer is knowing where the lamps are, and being able to recognize one when you see it, the other half lies in pushing past that circle of illumination into the shadows. And you’ll have better luck if you move from the light into the dark, or the other way around, than if you focus solely on one or the other.

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