Every so often I enjoy looking at mathematician Doron Zeilberger’s page of opinions. (He also has some other nice stuff).
I enjoyed this recent opinion, especially the stuff about Gelfand’s approach to seminars – to constantly interrupt the seminar until every point is made as simply and clearly as possible.
Other opinions I particularly enjoyed: 1, on the value of publishing incomplete proofs, 2, on confessing dumb mistakes, and 3, on different types of creativity.
>From Richard Hamming, You and Your Research (with thanks to Julia Kempe):
Let me start not logically, but psychologically. I find that the major objection is that people think great science is done by luck. It’s all a matter of luck.
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And I will cite Pasteur who said, “Luck favors the prepared mind.” And I think that says it the way I believe it. There is indeed an element of luck, and no, there isn’t. The prepared mind sooner or later finds something important and does it. So yes, it is luck. The particular thing you do is luck, but that you do something is not.
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So, although I’ll come back several more times to luck, I want to dispose of this matter of luck as being the sole criterion whether you do great work or not. I claim you have some, but not total, control over it. And I will quote, finally, Newton on the matter. Newton said, “If others would think as hard as I did, then they would get similar results.”
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How about having lots of `brains?’ It sounds good. Most of you in this room probably have more than enough brains to do first-class work. But great work is something else than mere brains. Brains are measured in various ways. In mathematics, theoretical physics, astrophysics, typically brains correlates to a great extent with the ability to manipulate symbols. And so the typical IQ test is apt to score them fairly high.
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And I can cite another person in the same way. I trust he isn’t in the audience, i.e. a fellow named Clogston. I met him when I was working on a problem with John Pierce’s group and I didn’t think he had much. I asked my friends who had been with him at school, “Was he like that in graduate school?” “Yes,” they replied. Well I would have fired the fellow, but J. R. Pierce was smart and kept him on. Clogston finally did the Clogston cable. After that there was a steady stream of good ideas. One success brought him confidence and courage.
One of the characteristics of successful scientists is having courage. Once you get your courage up and believe that you can do important problems, then you can. If you think you can’t, almost surely you are not going to. Courage is one of the things that Shannon had supremely. You have only to think of his major theorem. He wants to create a method of coding, but he doesn’t know what to do so he makes a random code. Then he is stuck. And then he asks the impossible question, “What would the average random code do?” He then proves that the average code is arbitrarily good, and that therefore there must be at least one good code. Who but a man of infinite courage could have dared to think those thoughts? That is the characteristic of great scientists; they have courage. They will go forward under incredible circumstances; they think and continue to think.
Age is another factor which the physicists particularly worry about. They always are saying that you have got to do it when you are young or you will never do it.
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But let me say why age seems to have the effect it does. In the first place if you do some good work you will find yourself on all kinds of committees and unable to do any more work. You may find yourself as I saw Brattain when he got a Nobel Prize. The day the prize was announced we all assembled in Arnold Auditorium; all three winners got up and made speeches. The third one, Brattain, practically with tears in his eyes, said, “I know about this Nobel-Prize effect and I am not going to let it affect me; I am going to remain good old Walter Brattain.” Well I said to myself, “That is nice.” But in a few weeks I saw it was affecting him. Now he could only work on great problems.
When you are famous it is hard to work on small problems. This is what did Shannon in. After information theory, what do you do for an encore? The great scientists often make this error. They fail to continue to plant the little acorns from which the mighty oak trees grow. They try to get the big thing right off. And that isn’t the way things go. So that is another reason why you find that when you get early recognition it seems to sterilize you.
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Now for the matter of drive. You observe that most great scientists have tremendous drive. I worked for ten years with John Tukey at Bell Labs. He had tremendous drive. One day about three or four years after I joined, I discovered that John Tukey was slightly younger than I was. John was a genius and I clearly was not. Well I went storming into Bode’s office and said, “How can anybody my age know as much as John Tukey does?” He leaned back in his chair, put his hands behind his head, grinned slightly, and said, “You would be surprised Hamming, how much you would know if you worked as hard as he did that many years.” I simply slunk out of the office!
What Bode was saying was this: “Knowledge and productivity are like compound interest.” Given two people of approximately the same ability and one person who works ten percent more than the other, the latter will more than twice outproduce the former. The more you know, the more you learn; the more you learn, the more you can do; the more you can do, the more the opportunity – it is very much like compound interest. I don’t want to give you a rate, but it is a very high rate. Given two people with exactly the same ability, the one person who manages day in and day out to get in one more hour of thinking will be tremendously more productive over a lifetime. I took Bode’s remark to heart; I spent a good deal more of my time for some years trying to work a bit harder and I found, in fact, I could get more work done. I don’t like to say it in front of my wife, but I did sort of neglect her sometimes; I needed to study. You have to neglect things if you intend to get what you want done. There’s no question about this.
On this matter of drive Edison says, “Genius is 99% perspiration and 1% inspiration.” He may have been exaggerating, but the idea is that solid work, steadily applied, gets you surprisingly far. The steady application of effort with a little bit more work, intelligently applied is what does it. That’s the trouble; drive, misapplied, doesn’t get you anywhere. I’ve often wondered why so many of my good friends at Bell Labs who worked as hard or harder than I did, didn’t have so much to show for it. The misapplication of effort is a very serious matter. Just hard work is not enough – it must be applied sensibly.
There’s another trait on the side which I want to talk about; that trait is ambiguity. It took me a while to discover its importance. Most people like to believe something is or is not true. Great scientists tolerate ambiguity very well. They believe the theory enough to go ahead; they doubt it enough to notice the errors and faults so they can step forward and create the new replacement theory. If you believe too much you’ll never notice the flaws; if you doubt too much you won’t get started. It requires a lovely balance. But most great scientists are well aware of why their theories are true and they are also well aware of some slight misfits which don’t quite fit and they don’t forget it. Darwin writes in his autobiography that he found it necessary to write down every piece of evidence which appeared to contradict his beliefs because otherwise they would disappear from his mind. When you find apparent flaws you’ve got to be sensitive and keep track of those things, and keep an eye out for how they can be explained or how the theory can be changed to fit them. Those are often the great contributions. Great contributions are rarely done by adding another decimal place. It comes down to an emotional commitment. Most great scientists are completely committed to their problem. Those who don’t become committed seldom produce outstanding, first-class work.
Now again, emotional commitment is not enough. It is a necessary condition apparently. And I think I can tell you the reason why. Everybody who has studied creativity is driven finally to saying, “creativity comes out of your subconscious.” Somehow, suddenly, there it is. It just appears. Well, we know very little about the subconscious; but one thing you are pretty well aware of is that your dreams also come out of your subconscious. And you’re aware your dreams are, to a fair extent, a reworking of the experiences of the day. If you are deeply immersed and committed to a topic, day after day after day, your subconscious has nothing to do but work on your problem. And so you wake up one morning, or on some afternoon, and there’s the answer. For those who don’t get committed to their current problem, the subconscious goofs off on other things and doesn’t produce the big result. So the way to manage yourself is that when you have a real important problem you don’t let anything else get the center of your attention – you keep your thoughts on the problem. Keep your subconscious starved so it has to work on your problem, so you can sleep peacefully and get the answer in the morning, free.
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If you do not work on an important problem, it’s unlikely you’ll do important work. It’s perfectly obvious. Great scientists have thought through, in a careful way, a number of important problems in their field, and they keep an eye on wondering how to attack them. Let me warn you, `important problem’ must be phrased carefully. The three outstanding problems in physics, in a certain sense, were never worked on while I was at Bell Labs. By important I mean guaranteed a Nobel Prize and any sum of money you want to mention. We didn’t work on (1) time travel, (2) teleportation, and (3) antigravity. They are not important problems because we do not have an attack. It’s not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important. When I say that most scientists don’t work on important problems, I mean it in that sense. The average scientist, so far as I can make out, spends almost all his time working on problems which he believes will not be important and he also doesn’t believe that they will lead to important problems.
I spoke earlier about planting acorns so that oaks will grow. You can’t always know exactly where to be, but you can keep active in places where something might happen. And even if you believe that great science is a matter of luck, you can stand on a mountain top where lightning strikes; you don’t have to hide in the valley where you’re safe. But the average scientist does routine safe work almost all the time and so he (or she) doesn’t produce much. It’s that simple. If you want to do great work, you clearly must work on important problems, and you should have an idea.
Along those lines at some urging from John Tukey and others, I finally adopted what I called “Great Thoughts Time.” When I went to lunch Friday noon, I would only discuss great thoughts after that. By great thoughts I mean ones like: “What will be the role of computers in all of AT&T?”, “How will computers change science?” For example, I came up with the observation at that time that nine out of ten experiments were done in the lab and one in ten on the computer. I made a remark to the vice presidents one time, that it would be reversed, i.e. nine out of ten experiments would be done on the computer and one in ten in the lab. They knew I was a crazy mathematician and had no sense of reality. I knew they were wrong and they’ve been proved wrong while I have been proved right. They built laboratories when they didn’t need them. I saw that computers were transforming science because I spent a lot of time asking “What will be the impact of computers on science and how can I change it?” I asked myself, “How is it going to change Bell Labs?” I remarked one time, in the same address, that more than one-half of the people at Bell Labs will be interacting closely with computing machines before I leave. Well, you all have terminals now. I thought hard about where was my field going, where were the opportunities, and what were the important things to do. Let me go there so there is a chance I can do important things.
Most great scientists know many important problems. They have something between 10 and 20 important problems for which they are looking for an attack. And when they see a new idea come up, one hears them say “Well that bears on this problem.” They drop all the other things and get after it. Now I can tell you a horror story that was told to me but I can’t vouch for the truth of it. I was sitting in an airport talking to a friend of mine from Los Alamos about how it was lucky that the fission experiment occurred over in Europe when it did because that got us working on the atomic bomb here in the US. He said “No; at Berkeley we had gathered a bunch of data; we didn’t get around to reducing it because we were building some more equipment, but if we had reduced that data we would have found fission.” They had it in their hands and they didn’t pursue it. They came in second!
The great scientists, when an opportunity opens up, get after it and they pursue it. They drop all other things. They get rid of other things and they get after an idea because they had already thought the thing through. Their minds are prepared; they see the opportunity and they go after it. Now of course lots of times it doesn’t work out, but you don’t have to hit many of them to do some great science. It’s kind of easy. One of the chief tricks is to live a long time!
Another trait, it took me a while to notice. I noticed the following facts about people who work with the door open or the door closed. I notice that if you have the door to your office closed, you get more work done today and tomorrow, and you are more productive than most. But 10 years later somehow you don’t know quite know what problems are worth working on; all the hard work you do is sort of tangential in importance. He who works with the door open gets all kinds of interruptions, but he also occasionally gets clues as to what the world is and what might be important. Now I cannot prove the cause and effect sequence because you might say, “The closed door is symbolic of a closed mind.” I don’t know. But I can say there is a pretty good correlation between those who work with the doors open and those who ultimately do important things, although people who work with doors closed often work harder. Somehow they seem to work on slightly the wrong thing – not much, but enough that they miss fame.
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Let me summarize. You’ve got to work on important problems. I deny that it is all luck, but I admit there is a fair element of luck. I subscribe to Pasteur’s “Luck favors the prepared mind.” I favor heavily what I did. Friday afternoons for years – great thoughts only – means that I committed 10% of my time trying to understand the bigger problems in the field, i.e. what was and what was not important. I found in the early days I had believed `this’ and yet had spent all week marching in `that’ direction. It was kind of foolish. If I really believe the action is over there, why do I march in this direction? I either had to change my goal or change what I did. So I changed something I did and I marched in the direction I thought was important. It’s that easy.
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Well I now come down to the topic, “Is the effort to be a great scientist worth it?” To answer this, you must ask people. When you get beyond their modesty, most people will say, “Yes, doing really first-class work, and knowing it, is as good as wine, women and song put together,” or if it’s a woman she says, “It is as good as wine, men and song put together.” And if you look at the bosses, they tend to come back or ask for reports, trying to participate in those moments of discovery. They’re always in the way. So evidently those who have done it, want to do it again. But it is a limited survey. I have never dared to go out and ask those who didn’t do great work how they felt about the matter. It’s a biased sample, but I still think it is worth the struggle. I think it is very definitely worth the struggle to try and do first-class work because the truth is, the value is in the struggle more than it is in the result. The struggle to make something of yourself seems to be worthwhile in itself. The success and fame are sort of dividends, in my opinion.
I’ve told you how to do it. It is so easy, so why do so many people, with all their talents, fail? For example, my opinion, to this day, is that there are in the mathematics department at Bell Labs quite a few people far more able and far better endowed than I, but they didn’t produce as much. Some of them did produce more than I did; Shannon produced more than I did, and some others produced a lot, but I was highly productive against a lot of other fellows who were better equipped. Why is it so? What happened to them? Why do so many of the people who have great promise, fail?
Well, one of the reasons is drive and commitment. The people who do great work with less ability but who are committed to it, get more done that those who have great skill and dabble in it, who work during the day and go home and do other things and come back and work the next day. They don’t have the deep commitment that is apparently necessary for really first-class work. They turn out lots of good work, but we were talking, remember, about first-class work. There is a difference. Good people, very talented people, almost always turn out good work. We’re talking about the outstanding work, the type of work that gets the Nobel Prize and gets recognition.
The second thing is, I think, the problem of personality defects. Now I’ll cite a fellow whom I met out in Irvine. He had been the head of a computing center and he was temporarily on assignment as a special assistant to the president of the university. It was obvious he had a job with a great future. He took me into his office one time and showed me his method of getting letters done and how he took care of his correspondence. He pointed out how inefficient the secretary was. He kept all his letters stacked around there; he knew where everything was. And he would, on his word processor, get the letter out. He was bragging how marvelous it was and how he could get so much more work done without the secretary’s interference. Well, behind his back, I talked to the secretary. The secretary said, “Of course I can’t help him; I don’t get his mail. He won’t give me the stuff to log in; I don’t know where he puts it on the floor. Of course I can’t help him.” So I went to him and said, “Look, if you adopt the present method and do what you can do single-handedly, you can go just that far and no farther than you can do single-handedly. If you will learn to work with the system, you can go as far as the system will support you.” And, he never went any further. He had his personality defect of wanting total control and was not willing to recognize that you need the support of the system.
You find this happening again and again; good scientists will fight the system rather than learn to work with the system and take advantage of all the system has to offer. It has a lot, if you learn how to use it. It takes patience, but you can learn how to use the system pretty well, and you can learn how to get around it. After all, if you want a decision `No’, you just go to your boss and get a `No’ easy. If you want to do something, don’t ask, do it. Present him with an accomplished fact. Don’t give him a chance to tell you `No’. But if you want a `No’, it’s easy to get a `No’.
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Many a second-rate fellow gets caught up in some little twitting of the system, and carries it through to warfare. He expends his energy in a foolish project. Now you are going to tell me that somebody has to change the system. I agree; somebody’s has to. Which do you want to be? The person who changes the system or the person who does first-class science? Which person is it that you want to be? Be clear, when you fight the system and struggle with it, what you are doing, how far to go out of amusement, and how much to waste your effort fighting the system. My advice is to let somebody else do it and you get on with becoming a first-class scientist. Very few of you have the ability to both reform the system and become a first-class scientist.
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Another fault is anger. Often a scientist becomes angry, and this is no way to handle things. Amusement, yes, anger, no. Anger is misdirected. You should follow and cooperate rather than struggle against the system all the time.
Another thing you should look for is the positive side of things instead of the negative. I have already given you several examples, and there are many, many more; how, given the situation, by changing the way I looked at it, I converted what was apparently a defect to an asset. I’ll give you another example. I am an egotistical person; there is no doubt about it. I knew that most people who took a sabbatical to write a book, didn’t finish it on time. So before I left, I told all my friends that when I come back, that book was going to be done! Yes, I would have it done – I’d have been ashamed to come back without it! I used my ego to make myself behave the way I wanted to. I bragged about something so I’d have to perform. I found out many times, like a cornered rat in a real trap, I was surprisingly capable. I have found that it paid to say, “Oh yes, I’ll get the answer for you Tuesday,” not having any idea how to do it. By Sunday night I was really hard thinking on how I was going to deliver by Tuesday. I often put my pride on the line and sometimes I failed, but as I said, like a cornered rat I’m surprised how often I did a good job. I think you need to learn to use yourself. I think you need to know how to convert a situation from one view to another which would increase the chance of success.
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In summary, I claim that some of the reasons why so many people who have greatness within their grasp don’t succeed are: they don’t work on important problems, they don’t become emotionally involved, they don’t try and change what is difficult to some other situation which is easily done but is still important, and they keep giving themselves alibis why they don’t. They keep saying that it is a matter of luck. I’ve told you how easy it is; furthermore I’ve told you how to reform. Therefore, go forth and become great scientists!
Following up on the previous post, something that has been bugging me is that it was not clear to me how the actions of San Francisco Mayor Newsom differed from those of Justice Roy Moore, who caused a huge ruckus with a public monument to the Ten Commandments.
Were Newsom and Moore acting solely in their role as private citizens, I’d have no trouble: I approve of Newsom’s stance, and disagree with Moore’s. But when both men are committed to upholding the rule of law, its a little more murky.
Conservative Law Professor Eugene Volokh has a thoughtful post on exactly this question, pointing out a number of key differences between the two positions.
I’ve always wondered what it’d be like to see a huge social change happening in my own back yard – I have only hazy memories of the big battles about equal rights for women in Australia in the 1970s and early 1980s.
I’m now hoping we’ll see such a change again, and soon. Wedding pictures don’t usually make me all that sentimental, but I find myself moved by these.
You can send flowers.
(Via Patrick Nielsen Hayden.)
In 2001 Judith Rich Harris published “The Nurture Assumption”, which, from the many favourable mentions I’ve seen in a variety of contexts, seems to have had a considerable influence on our thinking about how human beings develop.
I haven’t yet been able to get a hold of Harris’ book, but I did just find an essay by her in a collection of essays put together by John Brockman, “The Next 50 Years”.
The argument Harris makes in the essay can be summarized as follows:
(a) Genetic factors play a large (though far from exclusive) role in controlling human development.
(b) Most studies in developmental psychology assume that it is the environment that determines human behaviour.
(c) Those studies therefore fail to control for genetic effects.
(d) Those studies are therefore essentially useless.
It’s a fascinating argument: simple, yet if correct, devastating for an entire academic field.
(To avoid any confusion in attribution, I should say that I don’t know who originated this argument, although it is clear that Harris is but one of many contributors.)
Everyone knows, at some level, that correlation does not imply causation, but it is difficult to avoid the fallacies that can result when one is not mindful of this.
It occurred to me when talking with my partner, Jen, this evening that I don’t have a nice vivid example of this point ready at hand. So we made one up that I think illustrates the point memorably.
Suppose one observes top basketball players, and notices that they all tend to wear very expensive basketball shoes. Is one justified in assuming that more expensive basketball shoes cause someone to be a better basketball player?
In some small measure, the answer is yes. But it doesn’t matter what you put on my feet, I’m never going to jump like Michael Jordan.
Indeed, marketing in general seems to be based largely on the fact that, at some level, in many cases subconscious, we easily confuse correlation with causation.
Crooked Timber has a nice piece about the mass resignation of the editorial board at the Journal of Algorithms, in response to price gouging by the publisher, Elsevier. Many interesting links, thoughtful discussion of how best to distribute scientific information, and interesting thoughts about the future of scientific communication.
What follows is a long post that’s not the slightest bit academic. It’s personal (possibly to the point of self-absorption) with a few general observations throw in.
I know some people like blogs to have fairly clean cut themes, and so far mine has been mostly academic in flavour. However, I’m still experimenting to figure out what I want this blog to be about.
What I’m saying is, if you’re not interested in non-academic blogging, you may wish to skip this!
I’ve lost a fair bit of weight over the past four months – about 8 kilos. I’d like to lose about the same again, at which point I think I’ll qualify as “fully fit”.
To some extent, I’ve been inspired in my weight loss by the “Fitness blogging” of Jim Henley. In that spirit, I’ll offer a few observations.
(Following Jim Henley, I’ll record that I’m 185 cms, and was 97.6 kg last October. I’m now down to about 89kg. Anything under 85kg will be reasonably fit, and 82kg would be great.)
My amazing super secret to weight loss is to combine increased exercise with an improved diet! Who’d have thought?
Something I hear people discuss quite frequently is the question “What’s the big result of the last year or two in field X?”
My current answer to this question, in the field of quantum information science, is Raussendorf and Briegel’s cluster-state model of quantum computation.
This model tells you that, in order to quantum compute, it suffices to prepare a single quantum state (the “cluster state”), and then do local (i.e., single-qubit) measurements on that state.
Such measurements suffice to write in the initial state of the computation, the dynamical operations performed, and to read out the results of the computation!
In Debbie Leung’s memorable metaphor (memorable if you’re a Unix nut, anyway!), you simply “ping” Nature, and she computes. No “dynamics”, in the usual sense of the word, just ask questions of a suitably correlated state! Those questions don’t even have to be nonlocal; all the nonlocality is carried in a single, universal state.
Whatsmore, if you believe the Church-Turing-Deutsch thesis, you can efficiently simulate an arbitrary physical system this way.
I’ve spent most of the last two months thinking about this model, and the better I understand it, the more interesting and beautiful it seems.
(Disclaimer: I guess I should say that I’ve got a bit of a personal interest in advertising this work, since I’ve done some related work.)
Lance Fortnow, commenting on a post by guest blogger Scott Aaronson, has some sensible advice for aspiring researchers:
Your success in academics, like any professional endeavor, depends in part on how much effort you put into it with the relationship far more than linear. But by no means is social life and a productive research career incompatible. Most academics eventually find a life partner and many of us have children. We have many non-academic hobbies and activities even as graduate students. The trick is to find the right balance between your academic and non-academic activities, a difficult task but far from impossible. I truly admire the massive works of Paul Erdös, but I would never trade my life for the one he led.
I think the usual result of working as hard as Erdos – who was reputed to work up to 18 hour days – is depression. Besides the inherent tragedy, that’s no good for your creative work! I’ve seen formerly successful researchers work incredibly hard, yet make no progress, simply because they were overdoing it.
My opinion is that successful creative thought requires really intense concentration, and that for most people a few hours a day of such concentration is the most that can be sustained. Otherwise, leave plenty of time for the little daily chores of life, rest, relaxation, aned enjoying yourself!
Examples of people that I’ve heard follow this kind of pattern include G. H. Hardy, who apparently worked four hours a day at his research, like clockwork, and Poincare, who did two hours intense work in the morning, two in the afternoon.
I’m currently about two thirds of the way through the audio version of James Gleick’s book “Isaac Newton”.
What I’m enjoying most about the biography is hearing about the goings-on at the Royal Society, newly formed in Newton’s day. What emerges from the book, in my opinion, is that the innovation in forming such a society was at least as important as Newton’s discoveries. You can see in the Society’s activities the beginning of peer review, of the journal system, of the need to do experiments reproducing others’ results, and of the need to cite others’ work appropriately.
It’s very interesting to read about the little intrigues that went on. Someone would publish a new result; Hooke, or Newton, or some other eminence would then claim “Oh, I obtained those results many years ago”. That’s all very well, but if someone obtains a result, and then puts the only record in their filing cabinet, Science does not advance. Only through publication in archived, widely accessible journals does Science advance. Many early members of the Royal Society seemed to understanding this instinctively, and they moved toward an institutional system in which work is not done until it is published.