You and Your Research

本文包含三篇有关学术研究之方法与洞见。第一篇是大科学家Richard Hamming的著名演讲，于1986年在贝尔通讯研究中心给2000多名Bellcore的科学家们所做,此处可参看You and Your Research的中文译文。第二篇为著名数学家弗里曼·戴森的演讲译文——鸟和青蛙。第三篇为庞加莱关于数学发现的心理学的演讲。

You and Your research

Transcription of the
Bell Communicatios Research Colloquium Seminar
7 March 1986

At a seminar in the Bell Communications Research Colloquia Series, Dr. Richard W. Hamming, a Professor at the Naval Postgraduate School in Monterey, California and a retired Bell Labs scientist, gave a very interesting and stimulating talk, ‘You and Your Research’ to an overflow audience of some 200 Bellcore staff members and visitors at the Morris Research and Engineering Center on March 7, 1986. This talk centered on Hamming’s observations and research on the question “Why do so few scientists make significant contributions and so many are forgotten in the long run?” From his more than forty years of experience, thirty of which were at Bell Laboratories, he has made a number of direct observations, asked very pointed questions of scientists about what, how, and why they did things, studied the lives of great scientists and great contributions, and has done introspection and studied theories of creativity. The talk is about what he has learned in terms of the properties of the individual scientists, their abilities, traits, working habits, attitudes, and philosophy.

In order to make the information in the talk more widely available, the tape recording that was made of that talk was carefully transcribed. This transcription includes the discussions which followed in the question and answer period. As with any talk, the transcribed version suffers from translation as all the inflections of voice and the gestures of the speaker are lost; one must listen to the tape recording to recapture that part of the presentation. While the recording of Richard Hamming’s talk was completely intelligible, that of some of the questioner’s remarks were not. Where the tape recording was not intelligible I have added in parentheses my impression of the questioner’s remarks. Where there was a question and I could identify the questioner, I have checked with each to ensure the accuracy of my interpretation of their remarks.

INTRODUCTION OF DR. RICHARD W. HAMMING

As a speaker in the Bell Communications Research Colloquium Series, Dr. Richard W. Hamming of the Naval Postgraduate School in Monterey, California, was introduced by Alan G. Chynoweth, Vice President, Applied Research, Bell Communications Research.

Alan G. Chynoweth: Greetings colleagues, and also to many of our former colleagues from Bell Labs who, I understand, are here to be with us today on what I regard as a particularly felicitous occasion. It gives me very great pleasure indeed to introduce to you my old friend and colleague from many many years back, Richard Hamming, or Dick Hamming as he has always been know to all of us.

Dick is one of the all time greats in the mathematics and computer science arenas, as I’m sure the audience here does not need reminding. He received his early education at the Universities of Chicago and Nebraska, and got his Ph.D. at Illinois; he then joined the Los Alamos project during the war. Afterwards, in 1946, he joined Bell Labs. And that is, of course, where I met Dick - when I joined Bell Labs in their physics research organization. In those days, we were in the habit of lunching together as a physics group, and for some reason this strange fellow from mathematics was always pleased to join us. We were always happy to have him with us because he brought so many unorthodox ideas and views. Those lunches were stimulating, I can assure you.

While our professional paths have not been very close over the years, nevertheless I’ve always recognized Dick in the halls of Bell Labs and have always had tremendous admiration for what he was doing. I think the record speaks for itself. It is too long to go through all the details, but let me point out, for example, that he has written seven books and of those seven books which tell of various areas of mathematics and computers and coding and information theory, three are already well into their second edition. That is testimony indeed to the prolific output and the stature of Dick Hamming.

I think I last met him - it must have been about ten years ago - at a rather curious little conference in Dublin, Ireland where we were both speakers. As always, he was tremendously entertaining. Just one more example of the provocative thoughts that he comes up with: I remember him saying, “There are wavelengths that people cannot see, there are sounds that people cannot hear, and maybe computers have thoughts that people cannot think.” Well, with Dick Hamming around, we don’t need a computer. I think that we are in for an extremely entertaining talk.

THE TALK: "You and Your Research" by Dr. Richard W. Hamming

It’s a pleasure to be here. I doubt if I can live up to the Introduction. The title of my talk is, “You and Your Research.” It is not about managing research, it is about how you individually do your research. I could give a talk on the other subject - but it’s not, it’s about you. I’m not talking about ordinary run-of-the-mill research; I’m talking about great research. And for the sake of describing great research I’ll occasionally say Nobel-Prize type of work. It doesn’t have to gain the Nobel Prize, but I mean those kinds of things which we perceive are significant things. Relativity, if you want, Shannon’s information theory, any number of outstanding theories - that’s the kind of thing I’m talking about.

Now, how did I come to do this study? At Los Alamos I was brought in to run the computing machines which other people had got going, so those scientists and physicists could get back to business. I saw I was a stooge. I saw that although physically I was the same, they were different. And to put the thing bluntly, I was envious. I wanted to know why they were so different from me. I saw Feynman up close. I saw Fermi and Teller. I saw Oppenheimer. I saw Hans Bethe: he was my boss. I saw quite a few very capable people. I became very interested in the difference between those who do and those who might have done.

When I came to Bell Labs, I came into a very productive department. Bode was the department head at the time; Shannon was there, and there were other people. I continued examining the questions, “Why?” and “What is the difference?” I continued subsequently by reading biographies, autobiographies, asking people questions such as: “How did you come to do this?” I tried to find out what are the differences. And that’s what this talk is about.

Now, why is this talk important? I think it is important because, as far as I know, each of you has one life to live. Even if you believe in reincarnation it doesn’t do you any good from one life to the next! Why shouldn’t you do significant things in this one life, however you define significant? I’m not going to define it - you know what I mean. I will talk mainly about science because that is what I have studied. But so far as I know, and I’ve been told by others, much of what I say applies to many fields. Outstanding work is characterized very much the same way in most fields, but I will confine myself to science.

In order to get at you individually, I must talk in the first person. I have to get you to drop modesty and say to yourself, “Yes, I would like to do first-class work.” Our society frowns on people who set out to do really good work. You’re not supposed to; luck is supposed to descend on you and you do great things by chance. Well, that’s a kind of dumb thing to say. I say, why shouldn’t you set out to do something significant. You don’t have to tell other people, but shouldn’t you say to yourself, “Yes, I would like to do something significant.”

In order to get to the second stage, I have to drop modesty and talk in the first person about what I’ve seen, what I’ve done, and what I’ve heard. I’m going to talk about people, some of whom you know, and I trust that when we leave, you won’t quote me as saying some of the things I said.

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. Well, consider Einstein. Note how many different things he did that were good. Was it all luck? Wasn’t it a little too repetitive? Consider Shannon. He didn’t do just information theory. Several years before, he did some other good things and some which are still locked up in the security of cryptography. He did many good things.

You see again and again, that it is more than one thing from a good person. Once in a while a person does only one thing in his whole life, and we’ll talk about that later, but a lot of times there is repetition. I claim that luck will not cover everything. 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.

For example, when I came to Bell Labs, I shared an office for a while with Shannon. At the same time he was doing information theory, I was doing coding theory. It is suspicious that the two of us did it at the same place and at the same time - it was in the atmosphere. And you can say, “Yes, it was luck.” On the other hand you can say, “But why of all the people in Bell Labs then were those the two who did it?” Yes, it is partly luck, and partly it is the prepared mind; but ‘partly’ is the other thing I’m going to talk about. 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.”

One of the characteristics you see, and many people have it including great scientists, is that usually when they were young they had independent thoughts and had the courage to pursue them. For example, Einstein, somewhere around 12 or 14, asked himself the question, “What would a light wave look like if I went with the velocity of light to look at it?” Now he knew that electromagnetic theory says you cannot have a stationary local maximum. But if he moved along with the velocity of light, he would see a local maximum. He could see a contradiction at the age of 12, 14, or somewhere around there, that everything was not right and that the velocity of light had something peculiar. Is it luck that he finally created special relativity? Early on, he had laid down some of the pieces by thinking of the fragments. Now that’s the necessary but not sufficient condition. All of these items I will talk about are both luck and not luck.

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. On the other hand, in other fields it is something different. For example, Bill Pfann, the fellow who did zone melting, came into my office one day. He had this idea dimly in his mind about what he wanted and he had some equations. It was pretty clear to me that this man didn’t know much mathematics and he wasn’t really articulate. His problem seemed interesting so I took it home and did a little work. I finally showed him how to run computers so he could compute his own answers. I gave him the power to compute. He went ahead, with negligible recognition from his own department, but ultimately he has collected all the prizes in the field. Once he got well started, his shyness, his awkwardness, his inarticulateness, fell away and he became much more productive in many other ways. Certainly he became much more articulate.

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. Einstein did things very early, and all the quantum mechanic fellows were disgustingly young when they did their best work. Most mathematicians, theoretical physicists, and astrophysicists do what we consider their best work when they are young. It is not that they don’t do good work in their old age but what we value most is often what they did early. On the other hand, in music, politics and literature, often what we consider their best work was done late. I don’t know how whatever field you are in fits this scale, but age has some effect.

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. In fact I will give you my favorite quotation of many years. The Institute for Advanced Study in Princeton, in my opinion, has ruined more good scientists than any institution has created, judged by what they did before they came and judged by what they did after. Not that they weren’t good afterwards, but they were superb before they got there and were only good afterwards.

This brings up the subject, out of order perhaps, of working conditions. What most people think are the best working conditions, are not. Very clearly they are not because people are often most productive when working conditions are bad. One of the better times of the Cambridge Physical Laboratories was when they had practically shacks - they did some of the best physics ever.

I give you a story from my own private life. Early on it became evident to me that Bell Laboratories was not going to give me the conventional acre of programming people to program computing machines in absolute binary. It was clear they weren’t going to. But that was the way everybody did it. I could go to the West Coast and get a job with the airplane companies without any trouble, but the exciting people were at Bell Labs and the fellows out there in the airplane companies were not. I thought for a long while about, “Did I want to go or not?” and I wondered how I could get the best of two possible worlds. I finally said to myself, “Hamming, you think the machines can do practically everything. Why can’t you make them write programs?” What appeared at first to me as a defect forced me into automatic programming very early. What appears to be a fault, often, by a change of viewpoint, turns out to be one of the greatest assets you can have. But you are not likely to think that when you first look the thing and say, “Gee, I’m never going to get enough programmers, so how can I ever do any great programming?”

And there are many other stories of the same kind; Grace Hopper has similar ones. I think that if you look carefully you will see that often the great scientists, by turning the problem around a bit, changed a defect to an asset. For example, many scientists when they found they couldn’t do a problem finally began to study why not. They then turned it around the other way and said, “But of course, this is what it is.” and got an important result. So ideal working conditions are very strange. The ones you want aren’t always the best ones for you.

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 former will more than twice outproduce the latter. 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.

Now Alan Chynoweth mentioned that I used to eat at the physics table. I had been eating with the mathematicians and I found out that I already knew a fair amount of mathematics; in fact, I wasn’t learning much. The physics table was, as he said, an exciting place, but I think he exaggerated on how much I contributed. It was very interesting to listen to Shockley, Brattain, Bardeen, J. B. Johnson, Ken McKay and other people, and I was learning a lot. But unfortunately a Nobel Prize came, and a promotion came, and what was left was the dregs. Nobody wanted what was left. Well, there was no use eating with them!

Over on the other side of the dining hall was a chemistry table. I had worked with one of the fellows, Dave McCall; furthermore he was courting our secretary at the time. I went over and said, “Do you mind if I join you?” They can’t say no, so I started eating with them for a while. And I started asking, “What are the important problems of your field?” And after a week or so, “What important problems are you working on?” And after some more time I came in one day and said, “If what you are doing is not important, and if you don’t think it is going to lead to something important, why are you at Bell Labs working on it?” I wasn’t welcomed after that; I had to find somebody else to eat with! That was in the spring.

In the fall, Dave McCall stopped me in the hall and said, “Hamming, that remark of yours got underneath my skin. I thought about it all summer, i.e. what were the important problems in my field. I haven’t changed my research,” he says, “but I think it was well worthwhile.” And I said, “Thank you Dave.” and went on. I noticed a couple of months later he was made the head of the department. I noticed the other day he was a Member of the National Academy of Engineering. I noticed he has succeeded. I have never heard the names of any of the other fellows at that table mentioned in science and scientific circles. They were unable to ask themselves, “What are the important problems in my field?”

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 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.

I want to talk on another topic. It is based on the song which I think many of you know, “It ain’t what you do, it’s the way that you do it.” I’ll start with an example of my own. I was conned into doing on a digital computer, in the absolute binary days, a problem which the best analog computers couldn’t do. And I was getting an answer. When I thought carefully and said to myself, “You know, Hamming, you’re going to have to file a report on this military job; after you spend a lot of money you’re going to have to account for it and every analog installation is going to want the report to see if they can’t find flaws in it.” I was doing the required integration by a rather crummy method, to say the least, but I was getting the answer. And I realized that in truth the problem was not just to get the answer; it was to demonstrate for the first time, and beyond question, that I could beat the analog computer on its own ground with a digital machine. I reworked the method of solution, created a theory which was nice and elegant, and changed the way we computed the answer; the results were no different. The published report had an elegant method which was later known for years as “Hamming’s Method of Integrating Differential Equations.” It is somewhat obsolete now, but for a while it was a very good method. By changing the problem slightly, I did important work rather than trivial work.

In the same way, when using the machine up in the attic in the early days, I was solving one problem after another after another; a fair number were successful and there were a few failures. I went home one Friday after finishing a problem, and curiously enough I wasn’t happy; I was depressed. I could see life being a long sequence of one problem after another after another. After quite a while of thinking I decided, “No, I should be in the mass production of a variable product. I should be concerned with all of next year’s problems, not just the one in front of my face.” By changing the question I still got the same kind of results or better, but I changed things and did important work. I attacked the major problem - How do I conquer machines and do all of next year’s problems when I don’t know what they are going to be? How do I prepare for it? How do I do this one so I’ll be on top of it? How do I obey Newton’s rule? He said, “If I have seen further than others, it is because I’ve stood on the shoulders of giants.” These days we stand on each other’s feet!

You should do your job in such a fashion that others can build on top of it, so they will indeed say, “Yes, I’ve stood on so and so’s shoulders and I saw further.” The essence of science is cumulative. By changing a problem slightly you can often do great work rather than merely good work. Instead of attacking isolated problems, I made the resolution that I would never again solve an isolated problem except as characteristic of a class.

Now if you are much of a mathematician you know that the effort to generalize often means that the solution is simple. Often by stopping and saying, “This is the problem he wants but this is characteristic of so and so. Yes, I can attack the whole class with a far superior method than the particular one because I was earlier embedded in needless detail.” The business of abstraction frequently makes things simple. Furthermore, I filed away the methods and prepared for the future problems.

To end this part, I’ll remind you, “It is a poor workman who blames his tools - the good man gets on with the job, given what he’s got, and gets the best answer he can.” And I suggest that by altering the problem, by looking at the thing differently, you can make a great deal of difference in your final productivity because you can either do it in such a fashion that people can indeed build on what you’ve done, or you can do it in such a fashion that the next person has to essentially duplicate again what you’ve done. It isn’t just a matter of the job, it’s the way you write the report, the way you write the paper, the whole attitude. It’s just as easy to do a broad, general job as one very special case. And it’s much more satisfying and rewarding!

I have now come down to a topic which is very distasteful; it is not sufficient to do a job, you have to sell it. ‘Selling’ to a scientist is an awkward thing to do. It’s very ugly; you shouldn’t have to do it. The world is supposed to be waiting, and when you do something great, they should rush out and welcome it. But the fact is everyone is busy with their own work. You must present it so well that they will set aside what they are doing, look at what you’ve done, read it, and come back and say, “Yes, that was good.” I suggest that when you open a journal, as you turn the pages, you ask why you read some articles and not others. You had better write your report so when it is published in the Physical Review, or wherever else you want it, as the readers are turning the pages they won’t just turn your pages but they will stop and read yours. If they don’t stop and read it, you won’t get credit.

There are three things you have to do in selling. You have to learn to write clearly and well so that people will read it, you must learn to give reasonably formal talks, and you also must learn to give informal talks. We had a lot of so-called ‘back room scientists’. In a conference, they would keep quiet. Three weeks later after a decision was made they filed a report saying why you should do so and so. Well, it was too late. They would not stand up right in the middle of a hot conference, in the middle of activity, and say, “We should do this for these reasons.” You need to master that form of communication as well as prepared speeches.

When I first started, I got practically physically ill while giving a speech, and I was very, very nervous. I realized I either had to learn to give speeches smoothly or I would essentially partially cripple my whole career. The first time IBM asked me to give a speech in New York one evening, I decided I was going to give a really good speech, a speech that was wanted, not a technical one but a broad one, and at the end if they liked it, I’d quietly say, “Any time you want one I’ll come in and give you one.” As a result, I got a great deal of practice giving speeches to a limited audience and I got over being afraid. Furthermore, I could also then study what methods were effective and what were ineffective.

While going to meetings I had already been studying why some papers are remembered and most are not. The technical person wants to give a highly limited technical talk. Most of the time the audience wants a broad general talk and wants much more survey and background than the speaker is willing to give. As a result, many talks are ineffective. The speaker names a topic and suddenly plunges into the details he’s solved. Few people in the audience may follow. You should paint a general picture to say why it’s important, and then slowly give a sketch of what was done. Then a larger number of people will say, “Yes, Joe has done that.” or “Mary has done that; I really see where it is; yes, Mary really gave a good talk; I understand what Mary has done.” The tendency is to give a highly restricted, safe talk; this is usually ineffective. Furthermore, many talks are filled with far too much information. So I say this idea of selling is obvious.

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.

Now you might tell me you haven’t got control over what you have to work on. Well, when you first begin, you may not. But once you’re moderately successful, there are more people asking for results than you can deliver and you have some power of choice, but not completely. I’ll tell you a story about that, and it bears on the subject of educating your boss. I had a boss named Schelkunoff; he was, and still is, a very good friend of mine. Some military person came to me and demanded some answers by Friday. Well, I had already dedicated my computing resources to reducing data on the fly for a group of scientists; I was knee deep in short, small, important problems. This military person wanted me to solve his problem by the end of the day on Friday. I said, “No, I’ll give it to you Monday. I can work on it over the weekend. I’m not going to do it now.” He goes down to my boss, Schelkunoff, and Schelkunoff says, “You must run this for him; he’s got to have it by Friday.” I tell him, “Why do I?”; he says, “You have to.” I said, “Fine, Sergei, but you’re sitting in your office Friday afternoon catching the late bus home to watch as this fellow walks out that door.” I gave the military person the answers late Friday afternoon. I then went to Schelkunoff’s office and sat down; as the man goes out I say, “You see Schelkunoff, this fellow has nothing under his arm; but I gave him the answers.” On Monday morning Schelkunoff called him up and said, “Did you come in to work over the weekend?” I could hear, as it were, a pause as the fellow ran through his mind of what was going to happen; but he knew he would have had to sign in, and he’d better not say he had when he hadn’t, so he said he hadn’t. Ever after that Schelkunoff said, “You set your deadlines; you can change them.”

One lesson was sufficient to educate my boss as to why I didn’t want to do big jobs that displaced exploratory research and why I was justified in not doing crash jobs which absorb all the research computing facilities. I wanted instead to use the facilities to compute a large number of small problems. Again, in the early days, I was limited in computing capacity and it was clear, in my area, that a “mathematician had no use for machines.” But I needed more machine capacity. Every time I had to tell some scientist in some other area, “No I can’t; I haven’t the machine capacity,” he complained. I said “Go tell your Vice President that Hamming needs more computing capacity.” After a while I could see what was happening up there at the top; many people said to my Vice President, “Your man needs more computing capacity.” I got it!

I also did a second thing. When I loaned what little programming power we had to help in the early days of computing, I said, “We are not getting the recognition for our programmers that they deserve. When you publish a paper you will thank that programmer or you aren’t getting any more help from me. That programmer is going to be thanked by name; she’s worked hard.” I waited a couple of years. I then went through a year of BSTJ articles and counted what fraction thanked some programmer. I took it into the boss and said, “That’s the central role computing is playing in Bell Labs; if the BSTJ is important, that’s how important computing is.” He had to give in. You can educate your bosses. It’s a hard job. In this talk I’m only viewing from the bottom up; I’m not viewing from the top down. But I am telling you how you can get what you want in spite of top management. You have to sell your ideas there also.

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 than 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’.

Another personality defect is ego assertion and I’ll speak in this case of my own experience. I came from Los Alamos and in the early days I was using a machine in New York at 590 Madison Avenue where we merely rented time. I was still dressing in western clothes, big slash pockets, a bolo and all those things. I vaguely noticed that I was not getting as good service as other people. So I set out to measure. You came in and you waited for your turn; I felt I was not getting a fair deal. I said to myself, “Why? No Vice President at IBM said, ‘Give Hamming a bad time’. It is the secretaries at the bottom who are doing this. When a slot appears, they’ll rush to find someone to slip in, but they go out and find somebody else. Now, why? I haven’t mistreated them.” Answer, I wasn’t dressing the way they felt somebody in that situation should. It came down to just that - I wasn’t dressing properly. I had to make the decision - was I going to assert my ego and dress the way I wanted to and have it steadily drain my effort from my professional life, or was I going to appear to conform better? I decided I would make an effort to appear to conform properly. The moment I did, I got much better service. And now, as an old colorful character, I get better service than other people.

You should dress according to the expectations of the audience spoken to. If I am going to give an address at the MIT computer center, I dress with a bolo and an old corduroy jacket or something else. I know enough not to let my clothes, my appearance, my manners get in the way of what I care about. An enormous number of scientists feel they must assert their ego and do their thing their way. They have got to be able to do this, that, or the other thing, and they pay a steady price.

John Tukey almost always dressed very casually. He would go into an important office and it would take a long time before the other fellow realized that this is a first-class man and he had better listen. For a long time John has had to overcome this kind of hostility. It’s wasted effort! I didn’t say you should conform; I said “The appearance of conforming gets you a long way.” If you chose to assert your ego in any number of ways, “I am going to do it my way,” you pay a small steady price throughout the whole of your professional career. And this, over a whole lifetime, adds up to an enormous amount of needless trouble.

By taking the trouble to tell jokes to the secretaries and being a little friendly, I got superb secretarial help. For instance, one time for some idiot reason all the reproducing services at Murray Hill were tied up. Don’t ask me how, but they were. I wanted something done. My secretary called up somebody at Holmdel, hopped the company car, made the hour-long trip down and got it reproduced, and then came back. It was a payoff for the times I had made an effort to cheer her up, tell her jokes and be friendly; it was that little extra work that later paid off for me. By realizing you have to use the system and studying how to get the system to do your work, you learn how to adapt the system to your desires. Or you can fight it steadily, as a small undeclared war, for the whole of your life.

And I think John Tukey paid a terrible price needlessly. He was a genius anyhow, but I think it would have been far better, and far simpler, had he been willing to conform a little bit instead of ego asserting. He is going to dress the way he wants all of the time. It applies not only to dress but to a thousand other things; people will continue to fight the system. Not that you shouldn’t occasionally!

When they moved the library from the middle of Murray Hill to the far end, a friend of mine put in a request for a bicycle. Well, the organization was not dumb. They waited awhile and sent back a map of the grounds saying, “Will you please indicate on this map what paths you are going to take so we can get an insurance policy covering you.” A few more weeks went by. They then asked, “Where are you going to store the bicycle and how will it be locked so we can do so and so.” He finally realized that of course he was going to be red-taped to death so he gave in. He rose to be the President of Bell Laboratories.

Barney Oliver was a good man. He wrote a letter one time to the IEEE. At that time the official shelf space at Bell Labs was so much and the height of the IEEE Proceedings at that time was larger; and since you couldn’t change the size of the official shelf space he wrote this letter to the IEEE Publication person saying, “Since so many IEEE members were at Bell Labs and since the official space was so high the journal size should be changed.” He sent it for his boss’s signature. Back came a carbon with his signature, but he still doesn’t know whether the original was sent or not. I am not saying you shouldn’t make gestures of reform. I am saying that my study of able people is that they don’t get themselves committed to that kind of warfare. They play it a little bit and drop it and get on with their work.

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.

On the other hand, we can’t always give in. There are times when a certain amount of rebellion is sensible. I have observed almost all scientists enjoy a certain amount of twitting the system for the sheer love of it. What it comes down to basically is that you cannot be original in one area without having originality in others. Originality is being different. You can’t be an original scientist without having some other original characteristics. But many a scientist has let his quirks in other places make him pay a far higher price than is necessary for the ego satisfaction he or she gets. I’m not against all ego assertion; I’m against some.

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.

Now self-delusion in humans is very, very common. There are enumerable ways of you changing a thing and kidding yourself and making it look some other way. When you ask, “Why didn’t you do such and such,” the person has a thousand alibis. If you look at the history of science, usually these days there are 10 people right there ready, and we pay off for the person who is there first. The other nine fellows say, “Well, I had the idea but I didn’t do it and so on and so on.” There are so many alibis. Why weren’t you first? Why didn’t you do it right? Don’t try an alibi. Don’t try and kid yourself. You can tell other people all the alibis you want. I don’t mind. But to yourself try to be honest.

If you really want to be a first-class scientist you need to know yourself, your weaknesses, your strengths, and your bad faults, like my egotism. How can you convert a fault to an asset? How can you convert a situation where you haven’t got enough manpower to move into a direction when that’s exactly what you need to do? I say again that I have seen, as I studied the history, the successful scientist changed the viewpoint and what was a defect became an asset.

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!

(End of the formal part of the talk.)

DISCUSSION - QUESTIONS AND ANSWERS

A. G. Chynoweth: Well that was 50 minutes of concentrated wisdom and observations accumulated over a fantastic career; I lost track of all the observations that were striking home. Some of them are very very timely. One was the plea for more computer capacity; I was hearing nothing but that this morning from several people, over and over again. So that was right on the mark today even though here we are 20 - 30 years after when you were making similar remarks, Dick. I can think of all sorts of lessons that all of us can draw from your talk. And for one, as I walk around the halls in the future I hope I won’t see as many closed doors in Bellcore. That was one observation I thought was very intriguing.

Thank you very, very much indeed Dick; that was a wonderful recollection. I’ll now open it up for questions. I’m sure there are many people who would like to take up on some of the points that Dick was making.

Hamming: First let me respond to Alan Chynoweth about computing. I had been computing in research and for 10 years I kept telling my management, “Get that !&@#% machine out of research. We are being forced to run problems all the time. We can’t do research because were too busy operating and running the computing machines.” Finally the message got through. They were going to move computing out of research to someplace else. I was persona non grata to say the least and I was surprised that people didn’t kick my shins because everybody was having their toy taken away from them. I went in to Ed David’s office and said, “Look Ed, you’ve got to give your researchers a machine. If you give them a great big machine, we’ll be back in the same trouble we were before, so busy keeping it going we can’t think. Give them the smallest machine you can because they are very able people. They will learn how to do things on a small machine instead of mass computing.” As far as I’m concerned, that’s how UNIX arose. We gave them a moderately small machine and they decided to make it do great things. They had to come up with a system to do it on. It is called UNIX!

A. G. Chynoweth: I just have to pick up on that one. In our present environment, Dick, while we wrestle with some of the red tape attributed to, or required by, the regulators, there is one quote that one exasperated AVP came up with and I’ve used it over and over again. He growled that, “UNIX was never a deliverable!”

Question: What about personal stress? Does that seem to make a difference?

Hamming: Yes, it does. If you don’t get emotionally involved, it doesn’t. I had incipient ulcers most of the years that I was at Bell Labs. I have since gone off to the Naval Postgraduate School and laid back somewhat, and now my health is much better. But if you want to be a great scientist you’re going to have to put up with stress. You can lead a nice life; you can be a nice guy or you can be a great scientist. But nice guys end last, is what Leo Durocher said. If you want to lead a nice happy life with a lot of recreation and everything else, you’ll lead a nice life.

Question: The remarks about having courage, no one could argue with; but those of us who have gray hairs or who are well established don’t have to worry too much. But what I sense among the young people these days is a real concern over the risk taking in a highly competitive environment. Do you have any words of wisdom on this?

Hamming: I’ll quote Ed David more. Ed David was concerned about the general loss of nerve in our society. It does seem to me that we’ve gone through various periods. Coming out of the war, coming out of Los Alamos where we built the bomb, coming out of building the radars and so on, there came into the mathematics department, and the research area, a group of people with a lot of guts. They’ve just seen things done; they’ve just won a war which was fantastic. We had reasons for having courage and therefore we did a great deal. I can’t arrange that situation to do it again. I cannot blame the present generation for not having it, but I agree with what you say; I just cannot attach blame to it. It doesn’t seem to me they have the desire for greatness; they lack the courage to do it. But we had, because we were in a favorable circumstance to have it; we just came through a tremendously successful war. In the war we were looking very, very bad for a long while; it was a very desperate struggle as you well know. And our success, I think, gave us courage and self confidence; that’s why you see, beginning in the late forties through the fifties, a tremendous productivity at the labs which was stimulated from the earlier times. Because many of us were earlier forced to learn other things - we were forced to learn the things we didn’t want to learn, we were forced to have an open door - and then we could exploit those things we learned. It is true, and I can’t do anything about it; I cannot blame the present generation either. It’s just a fact.

Question: Is there something management could or should do?

Hamming: Management can do very little. If you want to talk about managing research, that’s a totally different talk. I’d take another hour doing that. This talk is about how the individual gets very successful research done in spite of anything the management does or in spite of any other opposition. And how do you do it? Just as I observe people doing it. It’s just that simple and that hard!

Question: Is brainstorming a daily process?

Hamming: Once that was a very popular thing, but it seems not to have paid off. For myself I find it desirable to talk to other people; but a session of brainstorming is seldom worthwhile. I do go in to strictly talk to somebody and say, “Look, I think there has to be something here. Here’s what I think I see …” and then begin talking back and forth. But you want to pick capable people. To use another analogy, you know the idea called the ‘critical mass’. If you have enough stuff you have critical mass. There is also the idea I used to call ‘sound absorbers’. When you get too many sound absorbers, you give out an idea and they merely say, “Yes, yes, yes.” What you want to do is get that critical mass in action; “Yes, that reminds me of so and so.” or, “Have you thought about that or this?” When you talk to other people, you want to get rid of those sound absorbers who are nice people but merely say, “Oh yes.” and to find those who will stimulate you right back.

For example, you couldn’t talk to John Pierce without being stimulated very quickly. There were a group of other people I used to talk with. For example there was Ed Gilbert; I used to go down to his office regularly and ask him questions and listen and come back stimulated. I picked my people carefully with whom I did or whom I didn’t brainstorm because the sound absorbers are a curse. They are just nice guys; they fill the whole space and they contribute nothing except they absorb ideas and the new ideas just die away instead of echoing on. Yes, I find it necessary to talk to people. I think people with closed doors fail to do this so they fail to get their ideas sharpened, such as “Did you ever notice something over here?” I never knew anything about it - I can go over and look. Somebody points the way. On my visit here, I have already found several books that I must read when I get home. I talk to people and ask questions when I think they can answer me and give me clues that I do not know about. I go out and look!

Question: What kind of tradeoffs did you make in allocating your time for reading and writing and actually doing research?

Hamming: I believed, in my early days, that you should spend at least as much time in the polish and presentation as you did in the original research. Now at least 50% of the time must go for the presentation. It’s a big, big number.

Question: How much effort should go into library work?

Hamming: It depends upon the field. I will say this about it. There was a fellow at Bell Labs, a very, very, smart guy. He was always in the library; he read everything. If you wanted references, you went to him and he gave you all kinds of references. But in the middle of forming these theories, I formed a proposition: there would be no effect named after him in the long run. He is now retired from Bell Labs and is an Adjunct Professor. He was very valuable; I’m not questioning that. He wrote some very good Physical Review articles; but there’s no effect named after him because he read too much. If you read all the time what other people have done you will think the way they thought. If you want to think new thoughts that are different, then do what a lot of creative people do - get the problem reasonably clear and then refuse to look at any answers until you’ve thought the problem through carefully how you would do it, how you could slightly change the problem to be the correct one. So yes, you need to keep up. You need to keep up more to find out what the problems are than to read to find the solutions. The reading is necessary to know what is going on and what is possible. But reading to get the solutions does not seem to be the way to do great research. So I’ll give you two answers. You read; but it is not the amount, it is the way you read that counts.

Question: How do you get your name attached to things?

Hamming: By doing great work. I’ll tell you the hamming window one. I had given Tukey a hard time, quite a few times, and I got a phone call from him from Princeton to me at Murray Hill. I knew that he was writing up power spectra and he asked me if I would mind if he called a certain window a “Hamming window.” And I said to him, “Come on, John; you know perfectly well I did only a small part of the work but you also did a lot.” He said, “Yes, Hamming, but you contributed a lot of small things; you’re entitled to some credit.” So he called it the hamming window. Now, let me go on. I had twitted John frequently about true greatness. I said true greatness is when your name is like ampere, watt, and fourier - when it’s spelled with a lower case letter. That’s how the hamming window came about.

Question: Dick, would you care to comment on the relative effectiveness between giving talks, writing papers, and writing books?

Hamming: In the short-haul, papers are very important if you want to stimulate someone tomorrow. If you want to get recognition long-haul, it seems to me writing books is more contribution because most of us need orientation. In this day of practically infinite knowledge, we need orientation to find our way. Let me tell you what infinite knowledge is. Since from the time of Newton to now, we have come close to doubling knowledge every 17 years, more or less. And we cope with that, essentially, by specialization. In the next 340 years at that rate, there will be 20 doublings, i.e. a million, and there will be a million fields of specialty for every one field now. It isn’t going to happen. The present growth of knowledge will choke itself off until we get different tools. I believe that books which try to digest, coordinate, get rid of the duplication, get rid of the less fruitful methods and present the underlying ideas clearly of what we know now, will be the things the future generations will value. Public talks are necessary; private talks are necessary; written papers are necessary. But I am inclined to believe that, in the long-haul, books which leave out what’s not essential are more important than books which tell you everything because you don’t want to know everything. I don’t want to know that much about penguins is the usual reply. You just want to know the essence.

Question: You mentioned the problem of the Nobel Prize and the subsequent notoriety of what was done to some of the careers. Isn’t that kind of a much more broad problem of fame? What can one do?

Hamming: Some things you could do are the following. Somewhere around every seven years make a significant, if not complete, shift in your field. Thus, I shifted from numerical analysis, to hardware, to software, and so on, periodically, because you tend to use up your ideas. When you go to a new field, you have to start over as a baby. You are no longer the big mukity muk and you can start back there and you can start planting those acorns which will become the giant oaks. Shannon, I believe, ruined himself. In fact when he left Bell Labs, I said, “That’s the end of Shannon’s scientific career.” I received a lot of flak from my friends who said that Shannon was just as smart as ever. I said, “Yes, he’ll be just as smart, but that’s the end of his scientific career,” and I truly believe it was.

You have to change. You get tired after a while; you use up your originality in one field. You need to get something nearby. I’m not saying that you shift from music to theoretical physics to English literature; I mean within your field you should shift areas so that you don’t go stale. You couldn’t get away with forcing a change every seven years, but if you could, I would require a condition for doing research, being that you will change your field of research every seven years with a reasonable definition of what it means, or at the end of 10 years, management has the right to compel you to change. I would insist on a change because I’m serious. What happens to the old fellows is that they get a technique going; they keep on using it. They were marching in that direction which was right then, but the world changes. There’s the new direction; but the old fellows are still marching in their former direction.

You need to get into a new field to get new viewpoints, and before you use up all the old ones. You can do something about this, but it takes effort and energy. It takes courage to say, “Yes, I will give up my great reputation.” For example, when error correcting codes were well launched, having these theories, I said, “Hamming, you are going to quit reading papers in the field; you are going to ignore it completely; you are going to try and do something else other than coast on that.” I deliberately refused to go on in that field. I wouldn’t even read papers to try to force myself to have a chance to do something else. I managed myself, which is what I’m preaching in this whole talk. Knowing many of my own faults, I manage myself. I have a lot of faults, so I’ve got a lot of problems, i.e. a lot of possibilities of management.

Question: Would you compare research and management?

Hamming: If you want to be a great researcher, you won’t make it being president of the company. If you want to be president of the company, that’s another thing. I’m not against being president of the company. I just don’t want to be. I think Ian Ross does a good job as President of Bell Labs. I’m not against it; but you have to be clear on what you want. Furthermore, when you’re young, you may have picked wanting to be a great scientist, but as you live longer, you may change your mind. For instance, I went to my boss, Bode, one day and said, “Why did you ever become department head? Why didn’t you just be a good scientist?” He said, “Hamming, I had a vision of what mathematics should be in Bell Laboratories. And I saw if that vision was going to be realized, I had to make it happen; I had to be department head.” When your vision of what you want to do is what you can do single-handedly, then you should pursue it. The day your vision, what you think needs to be done, is bigger than what you can do single-handedly, then you have to move toward management. And the bigger the vision is, the farther in management you have to go. If you have a vision of what the whole laboratory should be, or the whole Bell System, you have to get there to make it happen. You can’t make it happen from the bottom very easily. It depends upon what goals and what desires you have. And as they change in life, you have to be prepared to change. I chose to avoid management because I preferred to do what I could do single-handedly. But that’s the choice that I made, and it is biased. Each person is entitled to their choice. Keep an open mind. But when you do choose a path, for heaven’s sake be aware of what you have done and the choice you have made. Don’t try to do both sides.

Question: How important is one’s own expectation or how important is it to be in a group or surrounded by people who expect great work from you?

Hamming: At Bell Labs everyone expected good work from me - it was a big help. Everybody expects you to do a good job, so you do, if you’ve got pride. I think it’s very valuable to have first-class people around. I sought out the best people. The moment that physics table lost the best people, I left. The moment I saw that the same was true of the chemistry table, I left. I tried to go with people who had great ability so I could learn from them and who would expect great results out of me. By deliberately managing myself, I think I did much better than laissez faire.

Question: You, at the outset of your talk, minimized or played down luck; but you seemed also to gloss over the circumstances that got you to Los Alamos, that got you to Chicago, that got you to Bell Laboratories.

Hamming: There was some luck. On the other hand I don’t know the alternate branches. Until you can say that the other branches would not have been equally or more successful, I can’t say. Is it luck the particular thing you do? For example, when I met Feynman at Los Alamos, I knew he was going to get a Nobel Prize. I didn’t know what for. But I knew darn well he was going to do great work. No matter what directions came up in the future, this man would do great work. And sure enough, he did do great work. It isn’t that you only do a little great work at this circumstance and that was luck, there are many opportunities sooner or later. There are a whole pail full of opportunities, of which, if you’re in this situation, you seize one and you’re great over there instead of over here. There is an element of luck, yes and no. Luck favors a prepared mind; luck favors a prepared person. It is not guaranteed; I don’t guarantee success as being absolutely certain. I’d say luck changes the odds, but there is some definite control on the part of the individual.

Go forth, then, and do great work!

(End of the General Research Colloquium Talk.)

BIOGRAPHICAL SKETCH OF RICHARD HAMMING

Richard W. Hamming was born February 11, 1915, in Chicago, Illinois. His formal education was marked by the following degrees (all in mathematics): B.S. 1937, University of Chicago; M.A. 1939, University of Nebraska; and Ph.D. 1942, University of Illinois. His early experience was obtained at Los Alamos 1945-1946, i.e. at the close of World War II, where he managed the computers used in building the first atomic bomb. From there he went directly to Bell Laboratories where he spent thirty years in various aspects of computing, numerical analysis, and management of computing, i.e. 1946-1976. On July 23, 1976 he ‘moved his office’ to the Naval Postgraduate School in Monterey, California where he taught, supervised research, and wrote books.

While at Bell Laboratories, he took time to teach in Universities, sometimes locally and sometimes on a full sabbatical leave; these activities included visiting professorships at New York University, Princeton University (Statistics), City College of New York, Stanford University, 1960-61, Stevens Institute of Technology (Mathematics), and the University of California, Irvine, 1970-71.

Richard Hamming has received a number of awards which include: Fellow, IEEE, 1968; the ACM Turing Prize, 1968; the IEEE Emanuel R. Piore Award, 1979; Member, National Academy of Engineering, 1980; and the Harold Pender Award, U. Penn., 1981. In 1987 a major IEEE award was named after him, namely the Richard W. Hamming Medal, “For exceptional contributions to information sciences and systems”; fittingly, he was also the first recipient of this award, 1988. In 1996 in Munich he received the prestigious $130,000 Eduard Rhein Award for Achievement in Technology for his work on error correcting codes. He was both a Founder and Past President of ACM, and a Vice Pres. of the AAAS Mathematics Section.

He is probably best known for his pioneering work on error-correcting codes, his work on integrating differential equations, and the spectral window which bears his name. His extensive writing has included a number of important, pioneering, and highly regarded books. These are:

• Numerical Methods for Scientists and Engineers, McGraw-Hill, 1962; Second edition 1973; Reprinted by Dover 1985; Translated into Russian.
• Calculus and the Computer Revolution, Houghton-Mifflin, 1968.
• Introduction to Applied Numerical Analysis, McGraw-Hill, 1971.
• Computers and Society, McGraw-Hill, 1972.
• Digital Filters, Prentice-Hall, 1977; Second edition 1983; Third edition 1989; translated into several European languages.
• Coding and Information Theory, Prentice-Hall, 1980; Second edition 1986.
• Methods of Mathematics Applied to Calculus, Probability and Statistics, Prentice-Hall, 1985.
• The Art of Probability for Scientists and Engineers, Addison-Wesley, 1991.
• The Art of Doing Science and Engineering: Learning to Learn, Gordon and Breach, 1997.

He continued a very active life as Adjunct Professor, teaching and writing in the Mathematics and Computer Science Departments at the Naval Postgraduate School, Monterey, California for another twenty-one years before he retired to become Professor Emeritus in 1997. He was still teaching a course in the fall of 1997. He passed away unexpectedly on January 7, 1998.

ACKNOWLEDGEMENT

I would like to acknowledge the professional efforts of Donna Paradise of the Word Processing Center who did the initial transcription of the talk from the tape recording. She made my job of editing much easier. The errors of sentence parsing and punctuation are mine and mine alone. Finally I would like to express my sincere appreciation to Richard Hamming and Alan Chynoweth for all of their help in bringing this transcription to its present readable state.

J. F. Kaiser

鸟和青蛙

弗里曼•戴森(Freeman Dyson)1923年12月15日出生，美籍英裔数学物理学家，普林斯顿高等研究院自然科学学院荣誉退休教授。

戴森早年在剑桥大学追随著名的数学家G.H.哈代研究数学，二战结束后来到美国康奈尔大学，跟随汉斯•贝特教授。他证明了施温格和朝永振一郎发展的变分法方法和费曼的路径积分法的等价性，为量子电动力学的建立做出了决定性的贡献。1951年他任康奈尔大学教授，1953年后一直任普林斯顿高等研究院教授。

《鸟和青蛙》(Birds and Frogs)是戴森应邀为美国数学会爱因斯坦讲座所起草的一篇演讲稿，该演讲计划于2008年10月举行，但因故被取消。这篇文章全文发表于2009年2月出版的《美国数学会志》(NOTICES OF THE AMS, VOLUME56, Number 2)。

经美国数学会和戴森授权，科学时报记者王丹红全文翻译并在科学网上发布这篇文章。

有些数学家是鸟，其他的则是青蛙。鸟翱翔在高高的天空，俯瞰延伸至遥远地平线的广袤的数学远景。他们喜欢那些统一我们思想、并将不同领域的诸多问题整合起来的概念。青蛙生活在天空下的泥地里，只看到周围生长的花儿。他们乐于探索特定问题的细节，一次只解决一个问题。我碰巧是一只青蛙，但我的许多最好朋友都是鸟。

  这就是我今晚演讲的主题。数学既需要鸟也需要青蛙。数学丰富又美丽，因为鸟赋予它辽阔壮观的远景，青蛙则澄清了它错综复杂的细节。数学既是伟大的艺术，也是重要的科学，因为它将普遍的概念与深邃的结构融合在一起。如果声称鸟比青蛙更好，因为它们看得更遥远，或者青蛙比鸟更好，因为它们更加深刻，那么这些都是愚蠢的见解。数学的世界既辽阔又深刻，我们需要鸟们和青蛙们协同努力来探索。

  这个演讲被称为爱因斯坦讲座，应美国数学会之邀来这里演讲以纪念阿尔伯特•爱因斯坦，我深感荣幸。爱因斯坦不是一位数学家，而是一位融合了数学感觉的物理学家。一方面，他对数学描述自然界运作的力量极为尊重，他对数学之美有一种直觉，引导他进入发现自然规律的正确轨道；另一方面，他对纯数学没有兴趣，他缺乏数学家的技能。晚年时，他聘请一位年轻同事以助手身份帮助他做数学计算。他的思考方式是物理而非数学。他是物理学界的至高者，是一只比其他鸟瞭望得更远的鸟。但今晚我不准备谈爱因斯坦，因为乏善可陈。

弗兰西斯•培根和勒奈•笛卡尔

  17世纪初，两位伟大的哲学家，英国的弗兰西斯•培根(Francis Bacon)和法国的勒奈•笛卡尔(Rene Descartes)，正式宣告了现代科学的诞生。笛卡尔是一只鸟，培根是一只青蛙。两人分别描述了对未来的远景，但观点大相径庭。培根说：“一切均基于眼睛所见自然之确凿事实。”笛卡尔说：“我思，故我在。”

  按照培根的观点，科学家需要周游地球收集事实，直到所积累的事实能揭示出自然的运动方式。科学家们从这些事实中推导出自然运作所遵循的法则。根据笛卡尔的观点，科学家只需要呆在家里，通过纯粹的思考推导出自然规律。为了推导出正确的自然规律，科学家们只需要逻辑规则和上帝存在的知识。

  在开路先锋培根和迪卡尔的领导之下，400多年来，科学同时沿着这两条途径全速前进。然而，解开自然奥秘的力量既不是培根的经验主义，也不是笛卡尔的教条主义，而是二者成功合作的神奇之作。400多年来，英国科学家倾向于培根哲学，法国科学家倾向于笛卡尔哲学。法拉弟、达尔文和卢瑟福是培根学派；帕斯卡、拉普拉斯和庞加莱是迪卡尔学派。因为这两种对比鲜明的文化的交叉渗透，科学被极大地丰富了。这两种文化一直在这两个国家发挥作用。牛顿在本质上是笛卡尔学派，他用了笛卡尔主义的纯粹思考，并用这种思考推翻了涡流的笛卡尔教条。玛丽•居里在本质上是一位培根学派，她熬沸了几吨的沥青铀矿渣，推翻了原子不可毁性之教条。

  在20世纪的数学历史中，有两起决定性事件，一个属于培根学派传统，另一个属于笛卡尔学派传统。第一起事件发生于1900年在巴黎召开的国际数学家大会上，希尔伯特(Hilbert)作大会主题演讲，提出了23个未解决的著名问题，绘制了即将来临的一个世纪的数学航道。希尔伯特本身是一只鸟，高高飞翔在整个数学领地的上空，但他声称，他的问题是给在同一时间只解决一个问题的青蛙们。第二起决定性事件发生在20世纪30年代，数学之鸟——布尔巴基学派(Bourbaki)在法国成立，他们致力于出版一系列能将全部数学框架统一起来的教科书。

  在引导数学研究步入硕果累累的方向上，希尔伯特问题取得了巨大成功。部分问题被解决了，部分问题仍悬而未决，但所有这些问题都刺激了数学新思想和新领域的成长。布尔巴基纲领有同等影响，通过带入以前并不存在的逻辑连贯性、推动从具体实例到抽象共性的发展，这个项目改变了下一个50年的数学风格。在布尔巴基学派的格局中，数学是包含在布尔巴基教科书中的抽象结构。教科书之外均不是数学。自从在教科书中消失后，具体实例就不再是数学。布尔巴基纲领是笛卡尔风格的极端表现。通过排除培根学派旅行者们在路旁可能采集到的鲜花，他们缩小了数学的规模。

自然的玩笑

  我是一个培根学派的信徒。对我而言，布尔巴基纲领的一个主要不足是错失了一种惊喜元素。布尔巴基纲领努力让数学更有逻辑。当我回顾数学的历史时，我看见不断有非逻辑的跳跃、难以置信的巧合和自然的玩笑。大自然所开的最深刻玩笑之一是负1的平方根，1926年，物理学家埃尔文•薛定谔(Erwin Schrodinger)在发明波动力学时，将这个数放入他的波动方程。

  当薛定谔开始思考如何将光学和力学统一时，他就是一只鸟。早在100多年前，借助于描述光学射线和经典粒子轨迹的相同数学，汉密尔顿统一了射线光学和经典力学。薛定谔也希望用同样的方式来统一波动光学和波动力学。当时，波动光学已经存在，但波动力学尚未出现。薛定谔不得不发明波动力学来完成这一统一。开始时，他将波动光学作为一个模型，写下机械粒子的微分方程，但这个方程没有任何意义。这个方程看起来像连续介质中的热传导方程。热传导与粒子力学之间没有可见的相关性。薛定谔的想法看起来没有任何意义。然而，奇迹出现了。薛定谔将负1的平方根放入机械粒子的微分方程，突然间，它就有意义了。突然间，它成为波动方程而不是热传导方程。薛定谔高兴地发现，这个方程的解与玻尔原子模型中的量化轨道相吻合。

  结果，薛定谔方程准确描述了我们今天所知原子的每一种行为。这是整个化学和绝大部分物理学的基础。负1的平方根意味着大自然是以复数而不是实数的方式运行。这一发现让薛定谔和其他所有人耳目一新。薛定谔记得，当时，他14岁大的“女朋友”伊萨•荣格尔(Itha Junger)曾对他说：“嗨，开始时，你从来没想过会出现这么多有意义的结果吧？”

  在整个19世纪，从阿贝尔(Abel)、黎曼(Riemann)到维尔斯特拉斯(Weierstrass)，数学家们一直在创建一个宏大的复变函数理论。他们发现，一旦从实数推进到复数，函数论就变得更深刻更强大。但是，他们一直将复数看作是人造结构，是数学家们从真实生活中发明的一种有用、优雅的抽象概念。他们未曾料到，他们发明的这个人工数字事实上是原子运行的基础。他们从未想象过，这个数字最初是出现在自然界。

  大自然所开的第二个玩笑是量子力学的精确线性。事实上，物理对象的各种可能状态构成了一个线性空间。在量子力学被发明之前，经典物理总是非线性的，线性模式只是近似有效。在量子力学之后，大自然本身突然变成了线性。这对数学产生了深刻的影响。19世纪，索菲斯•李(Sophus Lie)发展了他关于连续群的精致理论(elaborate theory)，以期弄清楚经典力学系统的行为。当时的数学家和物理学家对李群几乎没有任何兴趣。李群的非线性理论对数学家来说过于复杂，对物理学家来说又过于晦涩。索菲斯•李在失望中离开了人世。50年后，人们发现大自然本身就是线性的，李代数的线性表示竟然是粒子物理的自然语言。作为20世纪数学的中心主题之一，李群和李代数获得了新生。

  大自然的第三个玩笑是拟晶体(Quasi-crystals)的存在。19世纪，对晶体的研究导致了对欧几里德空间中可能存在的离散对称群种类的完整列举。人们已经证明:在三维欧几里德空间中，所有离散对称群仅包含3级、4级或6级的旋转。之后，1984年，拟晶体被发现了，从液体金属阵列中长出的真正固体物显示了包含5重旋转的二十面体的对称性。与此同时，数学家罗杰•彭罗斯(Roger Penrose)发现了平面“彭罗斯拼砖法”。拟晶阵列是二维彭罗斯拼砖法的三维模拟。在这些发现之后，数学家不得不扩大晶体群理论，将合金拟晶体包含其中。这是还在发展中的一个重要研究项目。

  大自然开的第四个玩笑是拟晶和黎曼ζ函數零点(zeros of the Riemann Zeta function)在行为上的相似性。黎曼ζ函數零点令数学家们着迷，因为所有的零点都落在一条直线上，没有人知道这是为什么。著名的黎曼猜想是指：除了平凡的例外，黎曼ζ函数零点都在一条直线上。100多年来，证明黎曼猜想一直是年轻数学家们的梦想。我现在大胆提议：也许可以用拟晶体来证明黎曼猜想。你们中的部分数学家也许认为这个建议无关紧要。那些不是数学家的人可能对这个建议不感兴趣。然而，我将这个问题放到你们面前，希望你们严肃思考。年轻时的物理学家里奥•齐拉特(Leo Szilard)不满意摩西的十条诫命，写了新十诫来替换它们。齐拉特的第二条诫律说：“行动起来，向有价值的目标前进，不问这些目标是否能达到：行动是模范和例子，而不是终结。” 齐拉特践行了他的理论。他是第一个想象出核武器的物理学家，也是第一个积极以行动反对核武器使用的物理学家。他的第二条诫律也适用于这里。黎曼猜想的证明是一个值得为之的目标，我们不应该问这个目标是否能实现。我将给你们一些这个目标可以实现的暗示。我将给数学家们一些建议，这是我在50年前成为一名物理学家之前获得的忠告。我先谈黎曼猜想，再谈拟晶体。

  直到最近，纯数学领域还有两个未解决的超级问题：费马大定理的证明和黎曼猜想的证明。12年前，我在普林斯顿的同事安德鲁•怀尔斯(Andrew Wiles)证明了费马大定理，如今，只剩下黎曼猜想有待证明。怀尔斯对费马大定理的证明不只是一个技术绝技，它的证明需要发明和探索数学思想的新领域，这比费马大定理本身更辽阔更重要。正因如此，对黎曼猜想的证明也将导致对数学甚至物理学诸多不同领域的深刻认识。黎曼ζ函數和其他ζ函數也类似，它们在数论、动力系统、几何学、函数论和物理学中普遍存在。ζ函數仿佛是通向各方路径的交叉结合点。对黎曼猜想的证明将阐明所有这些关联。就像每一位纯数学领域里严肃的学生一样，我年轻时的梦想是证明黎曼猜想。我有一些模糊不清的想法，认为可以引导自己证明这个猜想。最近几年，在拟晶体被发现后，我的想法不再模糊。我在这里把它们呈现给有雄心壮志赢得菲尔茨奖的年轻数学家们。

  拟晶体存在于一维、二维和三维空间。从物理学的角度看，三维拟晶体最为有趣，因为它们栖息于我们的三维世界，可以通过实验加以研究。从数学家的角度来看，一维拟晶体比二维和三维拟晶体更为有趣，因为它们种类繁多。数学家这样定义拟晶体：一个拟晶体是离散点群的分布，它们的傅立叶变换是离散点频率。或简而言之，一个拟晶体是一个有纯点谱的纯点分布。这个定义包括了作为特例的普通晶体，它们是拥有周期谱的周期分布。

  将普通晶体排除在外，三维中的拟晶体只有极为有限的变形，它们均与二十面体有关。二维拟晶体数目众多，粗略地讲，一个独特的类型与平面上每个正多边形都相关联。含五边形对称的二维拟晶体是著名的平面彭罗斯拼砖。最后，一维拟晶体有更为丰富的结构，因为它们不受制于任何旋转对称。就我所知，目前还没有对一维拟晶体存在情况的全数调查。现已知，一种独特拟晶体的存在与每个皮索特-维贡伊拉卡文数(pisot Vijayaraghavan number)或PV数对应。一个PV数是一个实代数整数，是整系数(integer coefficients)多项式方程绝对值大于1的根。全部PV数的集合是无限的，并有非凡的拓扑结构。所有一维拟晶体的集合都有一种结构，其丰富程度可与所有的PV数集合相比，甚至更丰富。我们并不确切地知道，一个由与PV数没有关联的一维拟晶体构成的大世界正等待探索。

  现在谈一维准晶体与黎曼猜想的联系。如果黎曼猜想是正确的，那么根据定义，ζ函數零点就会形成一个一维拟晶体。它们在一条直线上构成了点质量(point masses)的一个分布，它们的傅利叶变化同样也是一个点质量分布，前者的点质量位于每个素数的对数处，其傅里叶变换点质量位于每个素数的幂的对数处。我的朋友安德鲁•奥德泽科(Andrew Odlyzko)发表了一个漂亮的ζ函數零点的傅利叶变换的计算机运算。这个运算精确地显示了傅利叶变换的预期结构，在每一个素数或素数的幂的对数上有明显的间断性。

  我的推测如下。假设我们并不知道黎曼猜想是否正确。我们从另一个角度来解决问题。我们努力获得一维拟晶体的一个全数调查和分类。这就是说，我们列举和分类拥有离散点谱的所有点分布。对新对象的收集和分类是典型的培根归纳活动。这也是适合于青蛙型数学家的活动。然后，我们发现众所周知的与PV数相关的拟晶体，以及其它已知或未知的拟晶体世界。在其它众多的拟晶体中，我们寻找一个与黎曼ζ函數相对应的拟晶体，寻找一个与其它类似黎曼ζ函數的每个ζ函數相对应的拟晶体。假设我们在拟晶体细目表中找到了一个拟晶体，其性质等同于黎曼ζ函數零点。然后，我们证明了黎曼猜想，等待宣布菲尔茨奖的电话。

  这是一种妄想。对一维准晶体进行分类极其困难，其困难程度不亚于安德鲁•怀尔斯花7年时间所解决的问题。但是，如果我们以培根主义者的观点来看，数学的历史就是骇人听闻的困难问题被初生牛犊不怕虎的年轻人干掉的历史。对拟晶体分类是一个值得为之的目标，甚至是可以实现的目标。这个问题的困难程度不是像我这样的老人能解决的，我将这个问题作一个练习留给听众中的年轻青蛙们。

艾布拉姆•伯西柯维奇和赫尔曼•外尔

  现在，我介绍我所知道的几位著名的鸟和青蛙。

  1941年，我作为一名学生来到英国剑桥大学，极其幸运地受教于俄罗斯数学家艾伯拉姆•萨莫罗维奇•伯西柯维奇(Abram Samoilovich Besicovitch)。时值第二次世界大战，剑桥只有很少的学生，几乎没有研究生。尽管当时我只有17岁，而伯西柯维奇已是一位著名教授，但是，他给了我相当多的时间和关注，我们成为终身朋友。在我开始从事和思考数学时，他塑造了我的性格。他在测量理论和积分方面上了许多精彩的课程，在我们因他大胆地滥用英语而哈哈大笑时，他只是亲切地笑笑。我记得仅有一次，他被我们之间的玩笑惹怒。在沉默了一会后，他说:“先生们，有5000万英国人讲你们所讲的英文。有1.5亿俄罗斯人讲我所讲的英文。”

  伯西柯维奇是一只青蛙，年轻时，因解决一个名为挂谷问题(Kakeya Problem)的初等平面几何问题而出名。挂谷问题是这样描述的：让一条长度为1的线段按360度的角度在一个平面上自由转动，这条线扫过的最小面积是多少？日本数学家挂谷宗一(Soichi Kakeya)在1917年提出这个问题，并成为之后十年内未解决的著名问题。当时，美国数学界领袖乔治•伯克霍夫(George Birkhoff)公开声称，挂谷问题和四色问题是最著名的未解决问题。数学家们普遍相信，最小的面积应该是π/8,即棒在三尖点内摆线的面积(three-cusped hypocycloid)。三尖点内摆线是一条优美的三尖点曲线，它是一个半径为四分之一的小圆圈在一个半径为四分之三的定圆内滑动时，动圆圆周上的一个点所绘制的轨迹。长度为1的线段在旋转时始终与内摆线相切，它的两端也在内摆线上。一条线段在旋转时与内摆线的三个点相切，这是一幅多么优美的画，绝大多数人相信它一定给出了最小面积。然后，伯西柯维奇给了大家一个惊喜：他证明，对任何正ε(positive ε)来说，这一线段在旋转时所扫过的面积小于ε。

  实际上，在挂谷问题成为著名问题之前，伯西柯维奇已经在1920年解决了这个问题，但在当时，伯西柯维奇本人甚至不知道挂谷提出了这个问题。1920年，他将解决方案用俄文发表在《彼尔姆物理和数学学会期刊》(Journal of the Perm Physics and Mathematics Society)上，这是一份不被广泛阅读的期刊。彼尔姆大学位于距离莫斯科东面1100公里的彼尔姆城，在俄罗斯革命之后，这个城市成为许多著名数学家的短暂避难所。他们出版了两期《彼尔姆物理和数学学会期刊》，之后,期刊便在革命和内战的混乱中停刊了。在俄罗斯之外，这份期刊不仅不为人知，而且不可获取。1925年，伯西柯维奇离开俄罗斯，来到哥本哈根，并在这里获知到他已经在5年前解决的著名挂谷问题。他将解决方案重新出版，这一次，论文用英文发表在德国著名的《数学期刊》(Mathematische Zeitschrift)上。正如伯西柯维奇所说，挂谷问题是一个典型的青蛙问题，一个与数学的其它方面没有太多联系的具体问题。伯西柯维奇给出了一个优雅、深刻的解决方案，揭示出它与平面中点集结构的一般定理之间的联系。

  伯西柯维奇的风格体现在他的三篇最好的经典文章中，这些文章的标题是:“平面点集之线性可测量的基本几何性质”(On the fundamental geometric properties)，它们分别发表在1928年、1938年和1939年的《数学年鉴》(Mathematische Annalen)上。在这些论文中，他证明：平面上的每个线性可测量集可被分解为有规则和无规则的分支，规则分支在每个地方几乎都有一个切线，而无规律分支都有一个零测量投射向几乎所有方向。简而言之，规则分支看起来像连续曲线，而无规则分支看起来不像连续曲线。无规则分支的存在和性质与挂谷问题的伯西柯维奇解有联系。他给我的工作之一是，在高维空间中将可测量集分为规则分支组件和无规则分支。虽然我在这个问题上一事无成，却永远被烙上了伯西柯维奇风格。伯西柯维奇风格是建筑学风格。他用简单元素建造出精美、复杂的建筑结构，通常情况下有层次计划；当大厦建成时，通过简单的论证就可从完整结构中推导出意外的结论。伯西柯维奇的每项工作都是一件艺术品，像巴赫的赋格曲一样精心构成。

  在跟随伯西柯维奇做了几年的学生后，我来到美国普林斯顿，认识了赫尔曼•外尔(Hermann Weyl)。外尔是一只典型的鸟，正如伯西柯维奇是一只典型的青蛙。幸运的是，在外尔退休回到位于苏黎世的老家之前，我在普林斯顿高等研究所与他有一年的相处时间。他喜欢我，因为在这一年间，我在《数学年鉴》(Annals of Mathematics)上发表了有关数论的论文，在《物理评论》(Physics Review)上发表了量子辐射理论的论文。他是当时活在世上的少数几位同时精通这两领域的专家之一。他欢迎我到普林斯顿研究所，希望我像他一样成为一只鸟。他失望了，我始终是一只固执的青蛙。尽管我总是在各种各样的泥洞附近闲逛，我一次只能关注一个问题，没有寻找问题之间的联系。对我而言，数论和量子理论是拥有各自美丽的两个世界。我不像外尔一样去发现构建大设计的线索。

  外尔对量子辐射理论的伟大贡献是他发明了规范场。规范场的想法有一段奇特历史。1918年，在他统一广义相对论和电磁学的理论中，他作为古典场论发明了它们，并称之为“规范场”，因为它们关系到长度测量的不可积分性。他的统一理论立即遭到爱因斯坦的公开拒绝，经历了这个来自高层的霹雳之后，外尔并没有放弃他的理论，只是进入别的领域。这个的理论没有可验证的实验结果。1929年，在量子理论被其他人发现后，外尔意识到与经典世界相比，他的规范场论更适合于量子世界，而他将经典场论转化为量子场论所做的事，就是将实数转化为复数。在量子力学中，每个电荷的量子伴随一个有相位的复杂波函数，并且规范场涉及相位测量的不可积分性有关。规范场可以精确地与电磁势等同，电荷守恒定律成为局部规范不变性理论的推论。

  从普林斯顿回到苏黎世4年后，外尔去世了，我应《自然》之邀为他撰写讣告。“在20世纪开始从事其数学生涯的所有活着的数学家中，”我写道，“赫尔曼•怀尔是在最多的不同领域做出了重大贡献的人物之一。他堪与19世纪最伟大的全能数学家希尔伯特和庞加莱相提并论。活着的时候，他生动地体现了纯数学与理论物理前沿的联系。现在，他去世了，这种联系中断了，我们期望直接借助于创造性的数学想象来理解物质世界的时代结束了。”我哀伤于他的逝世，但我并不希望追随他的梦想。我高兴地看到纯数学和物理学在向截然相反的方向前进。

  讣告以外尔为人的概述结束：“外尔的性格是一种审美感，这主导了他对所有问题的思考。有一次，他曾半开玩笑地对我说，‘我的工作总是努力将真与美统一起来；但是，如果只能选择其中之一，那么我选择美。’这段话是对他个性的完美概括，表明他对自然终极和谐的深刻信念，自然的规律必将以数学美的形式呈现出来。这表明他对人类弱点的认识，他的幽默总会让他不至于显得傲慢自大。他在普林斯顿的朋友还记得我最后一次见他的模样：那是去年四月在普林斯顿高等研究院举行的春之舞会上：一个高大、和蔼、快乐的人，尽情地自我享受，他明朗的身架和轻快的步伐让人一点看不出他已经69岁。”

  外尔逝世后的五十年是实验物理和观察天文学的黄金时代，也是培根学派旅行者收集事实、青蛙们在我们生存的小片沼泽地上探索的黄金时代。在这50年中，青蛙们积累了大量的有关宇宙结构、众多粒子和其间相互作用的详尽知识。在持续探索新领域的同时，宇宙变得越来越复杂。不再是展现外尔数学简洁和美丽的大设计 ，探索者发现了夸克和伽玛射线爆等奇异事件，以及超对称和多重宇宙等新奇概念。与此同时，在持续探索混沌和许多被电子计算机打开的新领域时，数学在变得越来越复杂。数学家发现了可计算性的中心谜团，这个猜想表示为P不等于NP。这个猜想声称：存在这样的数学问题，它的个案可以被很快解决，但没有适用于所有情形的快速算法可解决所有问题。这个问题中最著名的例子是旅行销售员问题，即在知道每两个城市之间距离的前提下，寻找这位销售员在这一系列城市间旅行的最短路径。所有的专家都相信这个猜想是正确的，旅行销售员的问题是P不等于NP的实际问题。但没有人知道证明这一问题的一点线索。在赫尔曼•外尔19世纪的数学世界中，这个谜团甚至还没有形成。

杨振宁和尤里•曼宁

  对鸟们来说，最近五十年是艰难时光。然而，即使在艰难时代，也有事情等着鸟们去做，他们勇敢地去解决这些事情。在赫尔曼•外尔离开普林斯顿后不久，杨振宁(Frank Yang)从芝加哥来到普林斯顿，搬进了外尔的旧居，在我这一代的物理学家中，他接替外尔的位置成为一只领头鸟。在外尔还活着时，杨振宁和他的学生罗伯特•米尔斯(Robert Mills)发现了非阿贝尔规范场(non-Abelian gauge fields)的杨—米尔斯理论，这是外尔规范场思想的一个漂亮外推。外尔的规范场是一个经典数量，满足了乘法交换定律。杨-米尔斯理论有一个不交换的三重规范场(triplet of gauge fields)。它们满足量子力学自旋三分量的交换法则，这是最简单的非阿贝尔躺代数A2(non-abelian lie algebra A2)的生成子。这个理论后来如此普遍，以至规范场论成为任何有限元李代数的生成子。有了这种普遍性，杨—米尔斯规范场理论为所有已知粒子和其相互作用提供了一个模型框架，这个模型就是今天粒子物理学的标准模型。通过证明爱因斯坦的重力场论适合于同样的框架，以克里斯托夫三指标符号规取代范场的作用，杨振宁为这个理论上写下点睛之笔。

  在他1918年一篇论文的附录里，加上1955年为庆祝他70岁生日而出版的论文选集中，外尔阐述了他对规范场理论的最后想法(这是我的翻译)：“对我的理论最强有力的辩护应该是：规范场不变性与电荷守恒相关，正如坐标不变性与能量动量守恒的相关性。”30年后，杨振宁来到瑞士苏黎世，参加外尔百岁诞辰庆典。杨振宁在演讲中引用这段话，作为外尔提出将规范场不变性作为物理学统一原理的思想证据。杨振宁继续说：“通过理论和实验的发展，今天我们已经认识到：对称性、李群和规范场不变性在确定物质世界的基本作用力中发挥了至关重要的作用。我将之称为对称支配相互作用基本原理。”对称支配相互作用的观点，是杨振宁对外尔言论的概括。外尔发现规范场不变性与物质守恒定律有密切关系。但他只能走这一步，不能走得太远，因为他只知道可交换为阿贝尔域的规范场不变性。借助于非阿贝尔规范场产生的非平凡李代数，场之间形成的相互作用变得独特，因此，对称性支配相互作用。这是杨振宁对物理学的伟大贡献。这是一只鸟的贡献，它高高地飞翔在诸多小问题构成的热带雨林之上，我们中的绝大多数在这些小问题耗尽了一生的时光。

  我深深敬重的另一只鸟是俄罗斯数学家尤里•曼宁(Yuri Manin)，他最近出版了一本名为《数学如隐喻》(Mathematics as Metaphor)的随笔。这本书以俄文在莫斯科出版，美国数学协会将之译为英文出版。我为英文版书作序。在这里，我简单引用我的序言:“对鸟们来说，《数学如隐喻》是一个好口号。它意味着数学中最深刻的概念是将一个世界的思想与另一个世界的思想联系起来。在17世纪，笛卡尔用他的坐标概念将彼此不相干的代数学和几何学联系起来；牛顿用他的流数(fluxions)概念将几何学和力学的世界联系起，今天，我们将这种方法称为微积分学。19世纪，布尔(Boole)用他的符号逻辑(symbolic logic)概念将逻辑与代数联系起来；黎曼用他的黎曼曲面概念将几何和分析的世界联系起来。坐标、流数、符号逻辑和黎曼曲面，都是隐喻，将词的意义从熟悉的语境拓展到陌生的语境。曼宁将数学的未来看成是对可见但仍不可知的隐喻的一个探索。最深刻的一个隐喻是数论和物理学之间在结构上的相似性。在这两个领域中，他看到并行概念诱人的一暼，对称性将连续与离散联结起来。他期待一种名为数学量化(quantization of mathematics)的统一。”

  “曼宁不认可培根主义者的故事。1900年，希尔伯特在巴黎的国际数学家大会上提出著名的23个问题，规划了20世纪的数学议程。根据曼宁的观点，希尔伯特的问题是对数学中心议题的一种干扰。曼宁认为数学的重要进展来自纲领，而非问题。通常情况下，问题是通过采用老想法的新方法而得以解决。研究纲领是诞生新想法的苗圃。他认为，以一种更抽象语言重写了整个数学的布尔巴基纲领是20世纪许多新思想的源泉。他将统一了数论和几何学的朗兰兹纲领视为21世纪新思想的希望之泉。解决了著名未解决问题的人会赢得大奖，但只有提出新纲领的人才是真正的先锋。”

  俄文版的《数学如隐喻》中有十个篇章在英文版中被删除了。美国数学学会认为，英文读者不会对这些篇章产生兴趣。这种删除是双重不幸。第一，作为一位非凡的数学家，曼宁广博的兴趣远远超越了数学，但英文版读者只能看见观点被拦截的曼宁；第二，我们看见的是观点被截断的俄罗斯文化，相比较于英语言文化，俄罗斯文化没有那么多的分门别类，它让数学家与历史学家、艺术家和诗人有更密切的接触。

约翰•冯•诺伊曼

  约翰•冯•诺伊曼(John von Neumann)是20世纪数学中另一位重要人物。冯•诺伊曼是一只青蛙，他用自己惊人的技术技能解决了数学和物理学众多分支领域中的问题。从创立数学的基础开始，他发现了集合论的第一个令人满意的公理集，避免了康托尔(Cantor)在试图解决无穷集和无穷数时遇到的逻辑悖论。几年后，冯•诺伊曼的鸟类朋友库特•哥德尔(Kurt Godel)用他的公理集证明了数学中的不可判定性命题。

  哥德尔的定理让鸟们对数学有了新看法。哥德尔之后，数学不再是与独特真理概念捆绑在一起的单一结构，而是带有不同公理集和不同真理概念的结构群岛。哥德尔证明数学不可穷尽。无论选择怎样的公理集作为基础，鸟们总能找到这些公理不能回答的问题。

  冯•诺伊曼从数学基础的奠定迈向了量子力学基础的奠定。为了给量子力学一个坚实的数学基础，他创立了一个宏大的算子环理论(theory of rings of operator)。每个可观察量都可以由一个线性算子来代表，量子行为的特殊性可由算术代数忠实地代表。正如牛顿发明了描述经典力学的微积分，冯•诺伊曼发明了描述量子力学的算子环理论。

  冯•诺伊曼在几个领域做出了奠基性贡献，特别是从博弈论到数字计算机的设计。在他生命的最后十年里，他深深陷入到计算机里。他对计算机的兴趣如此强烈，以至决定不仅要研究它们的设计，而且还要用真正的硬件和软件构建一台可做科学研究的计算机。我对冯•诺伊曼在普林斯顿高等研究所的早期计算机有生动清晰的记忆。那时，他有两个主要的科学兴趣：氢弹和气象学。夜晚，他用计算机做氢弹问题，白天，则做气象学问题。白天，游荡在计算机大楼里的许多人都是气象学家，他们的领导者是朱尔•查耐(Jule Charney)。查耐是一位真正的气象学家，妥善谦卑地讨论天气变幻莫测的神秘，怀疑计算机解决这个神秘的能力。我听过冯•诺伊曼以这个问题为主题的一次演讲。如往常一样，他充满自信地说：“计算机将使我们能够在任何时刻将大气划分为稳定域和不稳定域。我们可以预测稳定域，我们能够控制不稳定域。”

  冯•诺伊曼相信，任何不稳定域都可以通过明智而审慎的小扰动来推动，推动它向任何所期望的方向移动。小扰动可以通过携带烟雾发生器的飞机舰队来实施，在扰动效果最佳的地方吸收太阳光，提高或降低局部温度。特别是，通过尽早确定不稳定域，我们能在飓风之初将之停止，然后在该区域气温上升并形成漩涡之前，降低其气温。冯•诺伊曼在1950年指出，只需用十年的时间就能建造足以精确诊断大气中稳定和不稳定区域的强大计算机。一旦能够精确诊断，我们就能在短时间内实施天气控制。他期望能在20世纪60年代的十年中，对天气的实际控制成为常规操作。

  冯•诺伊曼当然错了。他错在不知道混沌(chaos)。我们现在明白，当大气运动局部不稳定时，实际上常常是发生了混沌。“混沌”意味着刚开始聚拢在一起运动会随着时间推进而呈指数般离散。当运动成为混沌时，它就不可预测，小扰动不可能将之推向可预测的稳定运动。小扰动通常是将之推向另一种同样不可预测的混沌运动。所以，冯•诺伊曼控制天气的战略思想破产了。最终，他是一位伟大的数学家，但也是一位中庸的气象学家。

  1963年，在冯•诺伊曼逝世6年后，爱德华•劳伦兹发现气象方程的解总是混沌。劳伦兹是一位气象学家，通常也被认为是混沌的发现者。他在气象学的背景中发现了混沌现象，并赋予它们一个现代化的名字。事实上，早在1943年在剑桥的一次演讲中，我已听数学家玛丽•卡特赖特描述了同样的现象，比劳伦兹早20年。卡特赖特1998年以97岁高龄逝世，她以不同的名称称呼这种现象，但他们讲述的是同一现象。她是在描述一种非线性放大器振动的范德波尔方程的解中发现了这些现象。范德波尔方程在第二次世界大战中变得重要，因为在早期的雷达系统，非线性放大器要为发报机提供动力。发报机工作不规则时，空军就会责备制造商生产了有缺陷的放大器。玛丽•卡特赖特被请来寻找问题。她发现问题出在在范德波尔方程。她指出，范德波尔方程的解有精确的混沌行为，这正在空军所抱怨的。在我听冯•诺伊曼谈论天气控制之前7年，我已经从玛丽•卡特赖特处得知所有的混沌问题，但我没有远见卓识足以将二者联系起来。我从来不曾想到：范德波尔方程所描述的不规则行为可用于天气预报的研究。如果我是一只鸟而不是一只青蛙，我也许能看出其中的联系，也许就能帮助冯•诺伊曼解决许多麻烦。如果他在1950年就知道混沌，那么他会深入地思考这个问题，并会在1954年就混沌问题谈一些重要的见解。

  在走向生命尽头之时，冯•诺伊曼陷入了麻烦。因为他是一只真正的青蛙，但每个人都期望他是一只飞翔的鸟。1954年，国际数学家大会在荷兰阿姆斯特丹举行。国际数学家大会每四年举办一次，应邀在大会开幕式上作演讲是一个崇高的荣誉。阿姆斯特丹大会的组织者邀请冯•诺伊曼作大会主题演讲，希望能再现希尔伯特1990年在巴黎大会上的盛况。正如希尔伯特提出的未解决问题指引了20世纪前半叶的数学发展，冯•诺伊曼应邀为20世纪后半叶的数学指点江山。冯•诺伊曼演讲的题目已经在大会纲要中公布了。它是：《数学中未解决的问题——大会组委会邀请演讲》。然而，会议结束后，包含所有演讲内容的完整会议记录出版了，除了冯•诺伊曼的这篇演讲之外。会议记录中有一空白页，上面只写着冯•诺伊曼的名字和演讲题目，下面写着：“演讲文稿尚未获取。”

  究竟发生了什么事？我知道所发生的事情，因为1954年9月2日，星期四，下午3:00，我正坐在阿姆斯特丹音乐厅的听众席上。大厅里挤满了数学家，所有人都期望在这样一个历史时刻聆听一个精彩绝伦的演讲。演讲结果却是令人非常失望。冯•诺伊曼可能在几年前就接受邀请做这样一个演讲，然后将之忘到九宵云外。诸事缠身，他忽略了准备演讲之事。然后，在最一刻，他想起来他将旅行到阿姆斯特丹，谈一些有关数学的事；他拉开一个抽屉，从中抽出一份20世纪30年代的老演讲稿，弹掉上面灰尘。 这是一个有关算子环的演讲，在30年代是一个全新、时髦的话题。没有谈任何未解决的问题，没有谈任何未来的问题。没有谈任何计算机，我们知道这是冯•诺伊曼心中最亲爱的话题，他至少应该谈一些有关计算机的新的、激动人心的事。音乐厅里的听众开始变得焦躁不安。有人用全音乐厅里的人都能听见的声音大声说：“Aufgewarmte suppe”，这是一句德国，意思是“先将汤加热(warmed-up soup)”。1954年，绝大多数数学家都懂德语，他们明白这句玩笑的意思。冯•诺伊曼陷入深深的尴尬，匆匆结束演讲，没有等待任何提问就离开了音乐厅。

弱混沌

  如果冯•诺伊曼在阿姆斯特丹演讲时对混沌略有了解，那么他可能提出的未解决问题之一应该是弱混沌。50多年后的今天，弱混沌依然是尚未解决的问题。这个问题是要明白为什么混沌运动常常受到边界约束，不会引发任何猛烈的动荡。弱混沌的一个好例子是太阳系中行星和卫星的轨道运动。科学家们最近发现，这些运动是弱混沌。这是一个令人震惊的发现，颠覆了太阳系作为有序稳定运动最好例证的传统概念。200年前，法国天文学家、数学家拉普拉斯(Laplace)认为，他已经证明了太阳系是稳定的。现在看来拉普拉斯错了。轨道的精确数值积分清楚地显示，相邻轨道呈现指数级偏离。在经典力学的世界里，弱混沌似乎无处不在。

  在长期积分(long-term integration)做出来之前，人们从未想象过太阳系中的混沌行为，因为这种混沌是弱的。弱混沌意味着相邻轨道呈指数级离散，却不会离散得太远。这种离散开始时以指数级速度增长，但随后就维持在边界处。因为行星运动的离散是弱的，所以太阳系能在40亿多年的时光里得以生存。尽管这种运动是混沌的，但行星从来不会在远离它们所熟悉的地区漫游，因此，太阳系作为一个整体从来不曾分崩离析。尽管混沌无处不在，但拉普拉斯将太阳系当作像时钟运动一样完美的观点离事实并不遥远。

  在气象学领域，我们看到了相同的弱混沌现象。尽管新泽西的天气糟糕地混沌，但这种混沌严格有限。夏天和冬天有着不可预测的温和或严厉，我们却能可靠地预测：气温绝对不会升至45摄氏度或低到零下30摄氏度，这是经常出现在印度和明尼苏达的极端情况。物理学中没有守恒定律禁止新泽西的气温不可以升至印度一样的温度，或禁止新泽西的气温不能降低到明尼苏达的气温。混沌的弱点成为这个星球上生命长期生存的关键。弱混沌在赋予我们各种挑战性天气的能力的同时，也保护我们不致遭受危及我们生存的剧烈温差波动。我们还不能理解混沌保持这种仁慈之弱的原因。这是今天在座的年轻青蛙们可以带回家的另一个未解决问题。我挑战你们弄明白这个问题：为什么在各种动力系统中观察到的混沌均是普遍微弱。

  混沌的特征已被众多的数据和无止境的美丽图片所勾勒，但却缺少严格理论。严谨理论赋予一个课题以智力的深度和精确。在你能证明一个严格理论之前，你不可能全面理解你所关注的概念的意义。在混沌领域，我知道只有一个严格理论在1975年被李天岩(Tien-Yien Li)和吉姆• 约克(Jim Yorke)所证明，这篇短论文的题目是：《周期三蕴含混沌》(Period Three Implies Chaos)。李-约克论文是数学文献中不朽的珍宝。他们的理论将非线性地图的区间扩展至它本身。当被当作是一个经典粒子的轨道时，点位置的连续性就能重复。如果一个点在N次映像之后又回到它原始的位置，那么这个轨道就有N个周期。由此而论，如果一个轨道从所有的周期轨道中离散，那么这个轨道就被定义为混沌。这个理论表明，如果单个轨道拥有三个存在周期，那么混沌轨道就是存在的。这个证明简洁、短小。在我的印象里，这个理论和它的证明投向混沌基本特征的光芒胜过几千张美丽图片。它解释了混沌为什么在这个世界里普遍存在，但没有解释混沌为什么总是这样弱，这是留给未来的一个任务。我相信，在证明有关弱混沌的严谨定理之前，我们是不会从根本上理解弱混沌。

弦理论家

  我想在弦理论上讲几句。只讲几句，是因为我对弦理论知之甚少。我从来没有劳心费神地学习这个理论，或自己花功夫去研究它。但是，当我在普林斯顿研究所有一个家时，我周围环绕着弦理论专家，我有时能听到他们之间的谈话。偶尔，我也能明白一点点他们谈话的内容。有三件事情是显而易见：第一，他们正在做第一流的数学，从而让迈克尔•阿蒂亚(Michael Atiyah)、伊萨多•辛格(Isadore Singer)这样的领袖级纯数学家也爱上弦理论，它开启了一个有新想法和新问题的全新数学分枝，最不寻常的是，它赋予数学一种解决老问题的新方法，这些老问题以前是不能解决的；第二，这些弦理论学家认为自己是物理学家而非数学家。他们相信自己的理论描述了物质世界的一些真实东西；第三，还没有任何证明显示这个理论与物理学相关。这个理论至今尚未被实验所证明。这个理论还在它自己的世界里，远离物理学。弦理论学家们付出艰苦努力，试图演绎这个可能在真实世界里被检验的理论的结果，但至今尚未成功。

  我的同事爱德华•威腾(Ed Witten)、胡安•马尔达西那(Juan Maldacena)和其他创建弦理论的人，都是鸟，他们飞翔在高高的天空，俯览远隔千里的众山全貌。在世界各地的大学里，几千名在弦理论上埋头苦干的谦卑实践者是青蛙，他们探索那些鸟们在地平线上第一次看到的数学结构的细节。我对弦理论的忧虑是从社会学角度而不是科学角度。成为发现新联系和探求新方法的第一批几千名弦理论学家之一，这是一个光荣的事；但成为第二批或万名弦理论学家之一，则不是一件光荣的事。今天，世界各地分布着上万名弦理论学家。对第1万名或第2000名科学家来说，情形是危险的。不可预测事情可能会发生，比如形势变化，弦理论不再时髦。这样的事情也可能发生：9000名弦理论学家可能会失业。他们在一个狭窄的领域接受训练，在其它科学领域可能无法被聘用。

  为什么如此之多的年轻人被弦理论所吸引？这种吸引部分可能是智力因素。弦理论如此大胆、在数学上如此高贵。但这种吸引也可能是社会因素。弦理论吸引人的原因是它能提供职位。那么，为什么弦理论领域能提供这么多的职位呢？因为弦理论是廉价的。如果你是某个偏远地方的大学物理学主任，没有多少钱，你无法承担建造一个做物理实验的现代化实验室，但你有能力聘请几位弦理论学家，因此，你提供了几个弦理论的职位，这样，你就拥有了一个现代化的物理系。对提供职位的系主任而言、对接受这些职位的年轻人而言，这是多么大的吸引力！然而，对年轻人和科学的未来而言，这是危险有害的情形。我并不是说我们应该在年轻人发现弦理论激动人心时劝阻他们不要从事这项研究。我的意思是我们应该给他们可替代的选择，让他们不致于因经济需求而被迫进入弦理论。

  最后，我想谈谈我对弦理论未来的推测。我的推测可能是错的。我从来没有幻想过我能预测未来。我告诉你们我的推测，只是想给你们一些思考的问题。我认为，弦理论不可能完全成功或完全无用。所谓完全成功，我的意思是它是一种完全(完整？)的物理理论，解释了粒子和其间相互作用的所有细节。所谓完全的无用，我的意思是它保留了一种纯数学的美丽。我的推测是，弦理论将在完全成功与完全失败之间的某一处终结。我认为它应该类似于李群，这是索菲斯•李(Sophus Lie)在19世纪为经典物理创建的一个数学框架。所以，只要物理学保持其经典性，李群就是一个失败。它们是一个寻找问题的解决方案。但另一方面，五十年后，量子革命改变了物理学，李代数找到用武之地：成为认识量子世界对称性中心作用的关键。我期望今后五十年或一百年中，物理学的另一场革命会引入我们今天一无所知的新概念，这些新概念将赋予弦理论一种全新的意义。在此之后，弦理论会突然发现自己在宇宙中应有的位置，提出对真实世界可经测试的陈述。我警告你们：这个有关未来的猜测可能是错的，它本身具有证伪性的美德，(科学哲学大师)卡尔•波普尔(karl Popper)说，这正是科学命题的特点。 明天，它可能会被来自大型强子对撞机的新发现所推翻。

再谈曼宁

  在结束这个演讲之际，我再回到曼宁和他的书《数学如隐喻》。这本书主要谈数学，但它也许会让西方读者感到吃惊，因为作者用同样的文才描述了其它主题，比如集体无意识、人类语言的起源、孤独症心理学、魔术师在诸多神话文化里的作用。对他的俄罗斯的同胞来说，如此丰富的兴趣专长并不令人惊讶。俄罗斯知识分子保持了老俄罗斯知识阶层的骄傲传统，科学家、诗人、艺术家和音乐家属于一个独立阶层。今天依然如此，我们在契诃夫的戏剧中看见他们：一群理想主义者因疏远迷信的社会和反复无常的政府而联结在一起。在俄罗斯，数学家、作曲家和电影制片人倾心交谈，一同走在冬夜的雪地里，围坐在一瓶酒的周围，分享着彼此的思想。

  曼宁是一只鸟，他的视野超越了数学疆界进入了更广阔的人类文化地貌。他的兴趣爱好之一是瑞士心理学家卡尔•荣格(C.G荣格1875年7月26日——1961年6月6日，瑞士著名的心理学家和分析心理学的创始人。)发明的原型理论。荣格认为，原型是一种根植于一种我们共同分享的集体无意识之中的精神意象。原型所拥有的这种强烈感情是已经丢失的集体悲欢喜乐记忆的遗迹。曼宁说，为了寻找这种理论的启发性，我们不必将荣格的理论作为一种真理来接受。

  三十多年前，歌手莫尼克•莫瑞利(Monique Morelli)录制了一盘皮埃尔•迈克奥兰(Pierre Macorlan)作词的唱片。其中一首歌是《死城》(La ville Morte)，萦绕于心的旋律切合着莫瑞利深沉的低音，随着歌声的对位，一个具有强烈冲击力的死城形象生动地出现了。歌声并没有特殊之处：

  每次聆听这首歌，我的情感都极为强烈。我常常问自己：为什么这首歌的简单歌词似乎与一些深厚的无意识记忆产生了共鸣？那些死亡的灵魂似乎通过莫瑞利的歌声在述说。现在，意料之外，我在曼宁的书中找到了答案。在“空城原型”一章中，曼宁描述了从古至今，从人类聚集在城市开始，从人类聚集成军队去蹂躏它们开始，死城原型如何在建筑学、文学、艺术和电影的创作中反复出现。在迈克奥兰歌词中，一位述说主角是一位占领军中的老兵，当他与妻子穿过那座尘埃满布的死城时，他听到了更多：

  迈克奥兰的歌词和莫瑞斯的歌声好像唤醒了来自我们集体无意识的一个梦，一位在死城中穿越的老兵的梦。像死城的概念一样，集体无意识的概念可能就是一个神话。曼宁的篇章描绘了这两个可能的神秘概念投向彼此的隐晦之光。他将集体无意识描述为一种无理性力量，这种强大的力量将我们拉向死亡和毁灭。死亡之城的原型是自从城市和抢劫军队出现后，几百座真正被毁灭的城市的痛苦的升华。我们逃离疯狂的集体无意识的唯一方法是基于希望和理性的理智集体意识。我们今天文明面临的伟大任务是创建这样一个集体意识。(完)

Poincaré’s Philosophy of Mathematics

Mathematical Creation

How is mathematics made? What sort of brain is it that can compose the propositions and systems of mathematics? How do the mental processes of the geometer or algebraist compare with those of the musician, the poet, the painter, the chess player? In mathematical creation which are the key elements? Intuition? An exquisite sense of space and time? The precision of a calculating machine? A powerful memory? Formidable skill in following complex logical sequences? A supreme capacity for concentration?

The essay below, delivered in the first years of this century as a lecture before the Psychological Society in Paris, is the most celebrated of the attempts to describe what goes on in the mathematician’s brain. Its author, Henri Poincaré, cousin of Raymond, the politician, was peculiarly fitted to undertake the task. One of the foremost mathematicians of all time, unrivaled as an analyst and mathematical physicist, Poincaré was known also as a brilliantly lucid expositor of the philosophy of science. These writings are of the first importance as professional treatises for scientists and are at the same time accessible, in large part, to the understanding of the thoughtful layman.

Poincaré on Mathematical Creation

The genesis of mathematical creation is a problem which should intensely interest the psychologist. It is the activity in which the human mind seems to take least from the outside world, in which it acts or seems to act only of itself and on itself, so that in studying the procedure of geometric thought we may hope to reach what is most essential in man’s mind…

A first fact should surprise us, or rather would surprise us if we were not so used to it. How does it happen there are people who do not understand mathematics? If mathematics invokes only the rules of logic, such as are accepted by all normal minds; if its evidence is based on principles common to all men, and that none could deny without being mad, how does it come about that so many persons are here refractory?

That not every one can invent is nowise mysterious. That not every one can retain a demonstration once learned may also pass. But that not every one can understand mathematical reasoning when explained appears very surprising when we think of it. And yet those who can follow this reasoning only with difficulty are in the majority; that is undeniable, and will surely not be gainsaid by the experience of secondary-school teachers.

And further: how is error possible in mathematics? A sane mind should not be guilty of a logical fallacy, and yet there are very fine minds who do not trip in brief reasoning such as occurs in the ordinary doings of life, and who are incapable of following or repeating without error the mathematical demonstrations which are longer, but which after all are only an accumulation of brief reasonings wholly analogous to those they make so easily. Need we add that mathematicians themselves are not infallible?…

As for myself, I must confess, I am absolutely incapable even of adding without mistakes… My memory is not bad, but it would be insufficient to make me a good chess-player. Why then does it not fail me in a difficult piece of mathematical reasoning where most chess-players would lose themselves? Evidently because it is guided by the general march of the reasoning. A mathematical demonstration is not a simple juxtaposition of syllogisms, it is syllogisms placed in a certain order, and the order in which these elements are placed is much more important than the elements themselves. If I have the feeling, the intuition, so to speak, of this order, so as to perceive at a glance the reasoning as a whole, I need no longer fear lest I forget one of the elements, for each of them will take its allotted place in the array, and that without any effort of memory on my part.

We know that this feeling, this intuition of mathematical order, that makes us divine hidden harmonies and relations, cannot be possessed by every one. Some will not have either this delicate feeling so difficult to define, or a strength of memory and attention beyond the ordinary, and then they will be absolutely incapable of understanding higher mathematics. Such are the majority. Others will have this feeling only in a slight degree, but they will be gifted with an uncommon memory and a great power of attention. They will learn by heart the details one after another; they can understand mathematics and sometimes make applications, but they cannot create. Others, finally, will possess in a less or greater degree the special intuition referred to, and then not only can they understand mathematics even if their memory is nothing extraordinary, but they may become creators and try to invent with more or less success according as this intuition is more or less developed in them.

In fact, what is mathematical creation? It does not consist in making new combinations with mathematical entities already known. Anyone could do that, but the combinations so made would be infinite in number and most of them absolutely without interest. To create consists precisely in not making useless combinations and in making those which are useful and which are only a small minority. Invention is discernment, choice.

It is time to penetrate deeper and to see what goes on in the very soul of the mathematician. For this, I believe, I can do best by recalling memories of my own. But I shall limit myself to telling how I wrote my first memoir on Fuchsian functions. I beg the reader’s pardon; I am about to use some technical expressions, but they need not frighten him, for he is not obliged to understand them. I shall say, for example, that I have found the demonstration of such a theorem under such circumstances. This theorem will have a barbarous name, unfamiliar to many, but that is unimportant; what is of interest for the psychologist is not the theorem but the circumstances.

For fifteen days I strove to prove that there could not be any functions like those I have since called Fuchsian functions. I was then very ignorant; every day I seated myself at my work table, stayed an hour or two, tried a great number of combinations and reached no results. One evening, contrary to my custom, I drank black coffee and could not sleep. Ideas rose in crowds; I felt them collide until pairs interlocked, so to speak, making a stable combination. By the next morning I had established the existence of a class of Fuchsian functions, those which come from the hypergeometric series; I had only to write out the results, which took but a few hours.

Then I wanted to represent these functions by the quotient of two series; this idea was perfectly conscious and deliberate, the analogy with elliptic functions guided me. I asked myself what properties these series must have if they existed, and I succeeded without difficulty in forming the series I have called theta-Fuchsian.

Just at this time I left Caen, where I was then living, to go on a geologic excursion under the auspices of the school of mines. The changes of travel made me forget my mathematical work. Having reached Coutances, we entered an omnibus to go some place or other. At the moment when I put my foot on the step the idea came to me, without anything in my former thoughts seeming to have paved the way for it, that the transformations I had used to define the Fuchsian functions were identical with those of non-Euclidean geometry. I did not verify the idea; I should not have had time, as, upon taking my seat in the omnibus, I went on with a conversation already commenced, but I felt a perfect certainty. On my return to Caen, for conscience’s sake I verified the result at my leisure.

Then I turned my attention to the study of some arithmetical questions apparently without much success and without a suspicion of any connection with my preceding researches. Disgusted with my failure, I went to spend a few days at the seaside, and thought of something else. One morning, walking on the bluff, the idea came to me, with just the same characteristics of brevity, suddenness and immediate certainty that the arithmetic transformations of indeterminate ternary quadratic forms were identical with those of non-Euclidean geometry.

Returned to Caen, I meditated on this result and deduced the consequences. The example of quadratic forms showed me that there were Fuchsian groups other than those corresponding to the hypergeometric series; I saw that I could apply to them the theory of theta-Fuchsian series and that consequently there existed Fuchsian functions other than those from the hypergeometric series, the ones I then knew. Naturally I set myself to form all these functions. I made a systematic attack upon them and carried all the outworks, one after another. There was one, however, that still held out, whose fall would involve that of the whole place. But all my efforts only served at first the better to show me the difficulty, which indeed was something. All this work was perfectly conscious.

Thereupon I left for Mont-Valérien, where I was to go through my military service; so I was very differently occupied. One day, going along the street, the solution of the difficulty which had stopped me suddenly appeared to me. I did not try to go deep into it immediately, and only after my service did I again take up the question. I had all the elements and had only to arrange them and put them together. So I wrote out my final memoir at a single stroke and without difficulty.

I shall limit myself to this single example; it is useless to multiply them…

Most striking at first is this appearance of sudden illumination, a manifest sign of long, unconscious prior work. The role of this unconscious work in mathematical invention appears to me incontestable, and traces of it would be found in other cases where it is less evident. Often when one works at a hard question, nothing good is accomplished at the first attack. Then one takes a rest, longer or shorter, and sits down anew to the work. During the first half-hour, as before, nothing is found, and then all of a sudden the decisive idea presents itself to the mind…

There is another remark to be made about the conditions of this unconscious work; it is possible, and of a certainty it is only fruitful, if it is on the one hand preceded and on the other hand followed by a period of conscious work. These sudden inspirations (and the examples already cited prove this) never happen except after some days of voluntary effort which has appeared absolutely fruitless and whence nothing good seems to have come, where the way taken seems totally astray. These efforts then have not been as sterile as one thinks; they have set agoing the unconscious machine and without them it would not have moved and would have produced nothing…

Such are the realities; now for the thoughts they force upon us. The unconscious, or, as we say, the subliminal self plays an important role in mathematical creation; this follows from what we have said. But usually the subliminal self is considered as purely automatic. Now we have seen that mathematical work is not simply mechanical, that it could not be done by a machine, however perfect. It is not merely a question of applying rules, of making the most combinations possible according to certain fixed laws. The combinations so obtained would be exceedingly numerous, useless and cumbersome. The true work of the inventor consists in choosing among these combinations so as to eliminate the useless ones or rather to avoid the trouble of making them, and the rules which must guide this choice are extremely fine and delicate. It is almost impossible to state them precisely; they are felt rather than formulated. Under these conditions, how imagine a sieve capable of applying them mechanically?

A first hypothesis now presents itself; the subliminal self is in no way inferior to the conscious self; it is not purely automatic; it is capable of discernment; it has tact, delicacy; it knows how to choose, to divine. What do I say? It knows better how to divine than the conscious self, since it succeeds where that has failed. In a word, is not the subliminal self superior to the conscious self? You recognize the full importance of this question…

Is this affirmative answer forced upon us by the facts I have just given? I confess that, for my part, I should hate to accept it. Re-examine the facts then and see if they are not compatible with another explanation.

It is certain that the combinations which present themselves to the mind in a sort of sudden illumination, after an unconscious working somewhat prolonged, are generally useful and fertile combinations, which seem the result of a first impression. Does it follow that the subliminal self, having divined by a delicate intuition that these combinations would be useful, has formed only these, or has it rather formed many others which were lacking in interest and have remained unconscious?

In this second way of looking at it, all the combinations would be formed in consequence of the automatism of the subliminal self, but only the interesting ones would break into the domain of consciousness. And this is still very mysterious. What is the cause that, among the thousand products of our unconscious activity, some are called to pass the threshold, while others remain below? Is it a simple chance which confers this privilege? Evidently not; among all the stimuli of our senses, for example, only the most intense fix our attention, unless it has been drawn to them by other causes. More generally the privileged unconscious phenomena, those susceptible of becoming conscious, are those which, directly or indirectly, affect most profoundly our emotional sensibility.

It may be surprising to see emotional sensibility invoked à propos of mathematical demonstrations which, it would seem, can interest only the intellect. This would be to forget the feeling of mathematical beauty, of the harmony of numbers and forms, of geometric elegance. This is a true esthetic feeling that all real mathematicians know, and surely it belongs to emotional sensibility.

Now, what are the mathematic entities to which we attribute this character of beauty and elegance, and which are capable of developing in us a sort of esthetic emotion? They are those whose elements are harmoniously disposed so that the mind without effort can embrace their totality while realizing the details. This harmony is at once a satisfaction of our esthetic needs and an aid to the mind, sustaining and guiding. And at the same time, in putting under our eyes a well-ordered whole, it makes us foresee a mathematical law… Thus it is this special esthetic sensibility which plays the role of the delicate sieve of which I spoke, and that sufficiently explains why the one lacking it will never be a real creator.

Yet all the difficulties have not disappeared. The conscious self is narrowly limited, and as for the subliminal self we know not its limitations, and this is why we are not too reluctant in supposing that it has been able in a short time to make more different combinations than the whole life of a conscious being could encompass. Yet these limitations exist. Is it likely that it is able to form all the possible combinations, whose number would frighten the imagination? Nevertheless that would seem necessary, because if it produces only a small part of these combinations, and if it makes them at random, there would be small chance that the good, the one we should choose, would be found among them.

Perhaps we ought to seek the explanation in that preliminary period of conscious work which always precedes all fruitful unconscious labor. Permit me a rough comparison. Figure the future elements of our combinations as something like the hooked atoms of Epicurus. During the complete repose of the mind, these atoms are motionless, they are, so to speak, hooked to the wall…

On the other hand, during a period of apparent rest and unconscious work, certain of them are detached from the wall and put in motion. They flash in every direction through the space (I was about to say the room) where they are enclosed, as would, for example, a swarm of gnats or, if you prefer a more learned comparison, like the molecules of gas in the kinematic theory of gases. Then their mutual impacts may produce new combinations.

What is the role of the preliminary conscious work? It is evidently to mobilize certain of these atoms, to unhook them from the wall and put them in swing. We think we have done no good, because we have moved these elements a thousand different ways in seeking to assemble them, and have found no satisfactory aggregate. But, after this shaking up imposed upon them by our will, these atoms do not return to their primitive rest. They freely continue their dance.

Now, our will did not choose them at random; it pursued a perfectly determined aim. The mobilized atoms are therefore not any atoms whatsoever; they are those from which we might reasonably expect the desired solution. Then the mobilized atoms undergo impacts which make them enter into combinations among themselves or with other atoms at rest which they struck against in their course. Again I beg pardon, my comparison is very rough, but I scarcely know how otherwise to make my thought understood.

However it may be, the only combinations that have a chance of forming are those where at least one of the elements is one of those atoms freely chosen by our will. Now, it is evidently among these that is found what I called the good combination. Perhaps this is a way of lessening the paradoxical in the original hypothesis…

I shall make a last remark: when above I made certain personal observations, I spoke of a night of excitement when I worked in spite of myself. Such cases are frequent, and it is not necessary that the abnormal cerebral activity be caused by a physical excitant as in that I mentioned. It seems, in such cases, that one is present at his own unconscious work, made partially perceptible to the over-excited consciousness, yet without having changed its nature. Then we vaguely comprehend what distinguishes the two mechanisms or, if you wish, the working methods of the two egos. And the psychologic observations I have been able thus to make seem to me to confirm in their general outlines the views I have given.

Surely they have need of [confirmation], for they are and remain in spite of all very hypothetical: the interest of the questions is so great that I do not repent of having submitted them to the reader.