Monday, March 06, 2006

 

You and Your Research

From http://www.cs.virginia.edu/~robins/YouAndYourResearch.html

Richard Hamming
``You and Your Research''
Transcription of the
Bell Communications Research Colloquium Seminar
7 March 1986

J. F. Kaiser
Bell Communications Research
445 South Street
Morristown, NJ 07962-1910
jfk@bellcore.com

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 latter will more than twice outproduce the former. The more you know, the more you learn; the more you learn, the more you can do; the more you can do, the more the opportunity - it is very much like compound interest. I don't want to give you a rate, but it is a very high rate. Given two people with exactly the same ability, the one person who manages day in and day out to get in one more hour of thinking will be tremendously more productive over a lifetime. I took Bode's remark to heart; I spent a good deal more of my time for some years trying to work a bit harder and I found, in fact, I could get more work done. I don't like to say it in front of my wife, but I did sort of neglect her sometimes; I needed to study. You have to neglect things if you intend to get what you want done. There's no question about this.

On this matter of drive Edison says, ``Genius is 99% perspiration and 1% inspiration.'' He may have been exaggerating, but the idea is that solid work, steadily applied, gets you surprisingly far. The steady application of effort with a little bit more work, intelligently applied is what does it. That's the trouble; drive, misapplied, doesn't get you anywhere. I've often wondered why so many of my good friends at Bell Labs who worked as hard or harder than I did, didn't have so much to show for it. The misapplication of effort is a very serious matter. Just hard work is not enough - it must be applied sensibly.

There's another trait on the side which I want to talk about; that trait is ambiguity. It took me a while to discover its importance. Most people like to believe something is or is not true. Great scientists tolerate ambiguity very well. They believe the theory enough to go ahead; they doubt it enough to notice the errors and faults so they can step forward and create the new replacement theory. If you believe too much you'll never notice the flaws; if you doubt too much you won't get started. It requires a lovely balance. But most great scientists are well aware of why their theories are true and they are also well aware of some slight misfits which don't quite fit and they don't forget it. Darwin writes in his autobiography that he found it necessary to write down every piece of evidence which appeared to contradict his beliefs because otherwise they would disappear from his mind. When you find apparent flaws you've got to be sensitive and keep track of those things, and keep an eye out for how they can be explained or how the theory can be changed to fit them. Those are often the great contributions. Great contributions are rarely done by adding another decimal place. It comes down to an emotional commitment. Most great scientists are completely committed to their problem. Those who don't become committed seldom produce outstanding, first-class work.

Now again, emotional commitment is not enough. It is a necessary condition apparently. And I think I can tell you the reason why. Everybody who has studied creativity is driven finally to saying, ``creativity comes out of your subconscious.'' Somehow, suddenly, there it is. It just appears. Well, we know very little about the subconscious; but one thing you are pretty well aware of is that your dreams also come out of your subconscious. And you're aware your dreams are, to a fair extent, a reworking of the experiences of the day. If you are deeply immersed and committed to a topic, day after day after day, your subconscious has nothing to do but work on your problem. And so you wake up one morning, or on some afternoon, and there's the answer. For those who don't get committed to their current problem, the subconscious goofs off on other things and doesn't produce the big result. So the way to manage yourself is that when you have a real important problem you don't let anything else get the center of your attention - you keep your thoughts on the problem. Keep your subconscious starved so it has to work on your problem, so you can sleep peacefully and get the answer in the morning, free.

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 know quite know what problems are worth working on; all the hard work you do is sort of tangential in importance. He who works with the door open gets all kinds of interruptions, but he also occasionally gets clues as to what the world is and what might be important. Now I cannot prove the cause and effect sequence because you might say, ``The closed door is symbolic of a closed mind.'' I don't know. But I can say there is a pretty good correlation between those who work with the doors open and those who ultimately do important things, although people who work with doors closed often work harder. Somehow they seem to work on slightly the wrong thing - not much, but enough that they miss fame.

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 that those who have great skill and dabble in it, who work during the day and go home and do other things and come back and work the next day. They don't have the deep commitment that is apparently necessary for really first-class work. They turn out lots of good work, but we were talking, remember, about first-class work. There is a difference. Good people, very talented people, almost always turn out good work. We're talking about the outstanding work, the type of work that gets the Nobel Prize and gets recognition.

The second thing is, I think, the problem of personality defects. Now I'll cite a fellow whom I met out in Irvine. He had been the head of a computing center and he was temporarily on assignment as a special assistant to the president of the university. It was obvious he had a job with a great future. He took me into his office one time and showed me his method of getting letters done and how he took care of his correspondence. He pointed out how inefficient the secretary was. He kept all his letters stacked around there; he knew where everything was. And he would, on his word processor, get the letter out. He was bragging how marvelous it was and how he could get so much more work done without the secretary's interference. Well, behind his back, I talked to the secretary. The secretary said, ``Of course I can't help him; I don't get his mail. He won't give me the stuff to log in; I don't know where he puts it on the floor. Of course I can't help him.'' So I went to him and said, ``Look, if you adopt the present method and do what you can do single-handedly, you can go just that far and no farther than you can do single-handedly. If you will learn to work with the system, you can go as far as the system will support you.'' And, he never went any further. He had his personality defect of wanting total control and was not willing to recognize that you need the support of the system.

You find this happening again and again; good scientists will fight the system rather than learn to work with the system and take advantage of all the system has to offer. It has a lot, if you learn how to use it. It takes patience, but you can learn how to use the system pretty well, and you can learn how to get around it. After all, if you want a decision `No', you just go to your boss and get a `No' easy. If you want to do something, don't ask, do it. Present him with an accomplished fact. Don't give him a chance to tell you `No'. But if you want a `No', it's easy to get a `No'.

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 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

发信人: Black8 (⑧), 信区: Science
标 题: 做大事,成大业 YOU AND YOUR RESEARCH(zz)
发信站: 水木社区 (Thu Mar 23 10:52:09 2006), 站内

做大事,成大业 YOU AND YOUR RESEARCH
http://chn.blogbeta.com/124.html

March 23rd, 2006

这是大科学家Richard Hamming的著名讲演,于1986年在贝尔通讯研究中心给200多名Bellcore的科学家们所做。在google上一搜,还未见中文翻译。在享受到Hamming闪耀的智慧的同时,禁不住要把它译成中文,让更多的只学了法语、德语、和柬埔寨语还未来得及学英语的同胞可以分享。思维是独特的,任何人的翻译都加上了译者的“思想”。所以,要知道Hamming到底讲的什么,请看原文。要看我是如何听Hamming讲的,你可以继续了看这篇“翻译稿”了。尽管我本人从不是自然科学学者,其中的科学名人大多不熟悉,很多术语也不懂,但我仍作出努力。我的时间有限,抽空为大家效劳,恕我不字斟句酌了。不当之处,请您补上。而且Hamming是大家,我也没亲耳聆听过其教诲,我就不“直译” 了。遇到一时没译好的,希望后来者补我的缺,以免误人子弟。有明显的错误或需要的补缺,请大家贴到Comment里面。如若承蒙厚爱引用本译稿,敬请高抬贵手标明出处:中文翻译:老马 引自染缸。

演讲者介绍:Richard Hamming,前贝尔实验室著名计算机科学家,美国the Naval Postgraduate School in Monterey教授。1968年因其在“数值方法,自动编码系统,错误检测和纠错码”方面的贡献获得图灵奖。

我演讲的题目是“你和你的研究”。这不是有关研究管理方面的,而是关于你如何独自做研究的。我也可以作别的方面的专题演讲–但是不,今天是专门谈你。我不是谈什么平常的“车轱辘转”(run-of-mill)的研究,我是谈重大的研究。并且,为了描述重大的研究,我将时常要谈及相当诺贝尔奖那一类的“大事”。这和获奖不获奖无关,我指的是我们认为有重大价值的事情。如相对论,香农(Shannon) (信息理论之父,译者注)信息论,以及其他杰出的理论 —- 这就是我要讲的。

那么,我是怎样搞起这样的研究的呢?还在Los Alamos(美国洛斯阿拉莫斯国家实验室Los Alamos National Laboratory的所在地,1943年由能源部为研制原子弹而建立。译者注)的时候,我负责运行有关计算机方面的事,以便那些科学家们、物理学家们可以去干他们的(大)事了。我无非是个“跑龙套”的。尽管我在身体上与他们无异,但我还是与他们不同。说实话,我挺嫉妒的。我见过Feynman (1965年获诺贝尔物理学奖。译者注),我见过Fermi和Teller,我见过奥本海默,尤(里乌斯)·罗伯特(Oppenheimer)(1902 -1967美国原子物理学家, 原子弹计划主持人。译者注),我见过贝蒂(Hans Albrecht, 1906-, 美国物理学家, 曾获1967诺贝尔物理学奖。译者注)—他就是我的“老板”。我见过不少非常有才能的人,我于是有兴趣去了解自己与那些正在做事和已经成事的人之间的差别。(瞧瞧那龙套跑的,啧啧。译者注)

当年我刚到贝尔实验室的时候,我进入到了一个硕果累累的部门。Bode是那时的部门头,香农(Shannon)也在那里。我一直问自己这样的问题:“为什么”和“差别是什么”。我于是去读有关的传记、自传,去问他们这样的问题:“你是怎么干起来这样的事的?” 我试着搞清差别是什么。这就是今天要谈的内容。

那么,为什么这样的话题重要呢?那是因为,就我所知,你一生只有一次生命。即使你相信来世,那也无助于你对待来世的“来世”!为什么你不在这次生命中就做一些意义重大的事呢,不管你是如何定义你的“意义重大”?我不会去定义它 —- 你懂我的意思。我将主要谈论科学,因为这是我研究的领域。尽管就我所知,别人也多次告诉我,我所讲的(道理)也适用于其他很多领域。尽管杰出的工作在很多不同的领域里都具有相同的特点,我还是将我自己限定在科学的领域。(他老人家的意思是说,他要去当总统或“政协委员”的话,实在是大材小用,驴头不对马嘴。译者注)

为了让你感觉到专门针对你个人的,我必须使用第一人称。我必须让你抛开谦逊并对自己说:“对,我想做一流的事。” 我们的社会会对那些着手去做像样的事的人皱起眉头,他们会怀疑:“你是那块料吗?运气会光顾你吗?或许你侥幸做成某件大事。” 好吧,随这些闲言碎语去吧。我要说的是:你为什么不现在就动手去做一点大事呢?!你不用告诉别人,但是你可以告诉你自己啊:“对,我就是喜欢做一些重要的事。”

为了达到第二个层次,我自己也得放下谦逊并以第一人称来谈我见识了什么,我做了什么,以及我听到什么。我会谈及一些人,其中一些你们认识,但我相信当我们离开的时候,你们不会把我的话当成“话柄”到处说事儿。

请让我从心理学的角度开始,而不是逻辑的。我主要不赞成人们认为重大科学成果是因运气而成。要说什么事情都和运气有关。但是,想想爱因斯坦,看看他做了多少不凡的事,那全都是运气使然吗?难道就没有一点可重复性?想想香农,他不仅仅搞了信息理论,多年以前他就做了一些别的有益的事,还有一些防卫密码系统。他可做了不少的好事。

你一次又一次地看到一个“好”人不只做一件“好”事。但有时一个人一生就做一件事,关于这一点我们一会儿再谈,只是更多时候是存在可重复性的。我坚持认为运气并不推及所有的事。我在此引用巴斯德(Louis Pasteur,19世纪法国化学家。译者注)的话:“运气只光顾有准备之士。” 他的话说出了我心里所想。的确有运气的因素,同时也有没有运气的成分。有准备之士早晚会找到重要的事并去做它。所以,的确,是有运气。你去做的那件特定的事是偶然,但是,你总归要做某事却并非偶然了(The particular thing you do is luck, but that you do something is not)。

举一个例子,我当初来到贝尔实验室,和香农共用一个办公室。他在那间办公室搞出了他的信息理论的同时,我也做出我的编码理论。真有点奇怪,我们两人居然在同一办公室、同一时刻做了这些“事”——在某种气氛中。你可以说:那是运气。另一方面你也可以问:“但是为什么那时所有在贝尔实验室的人只有我们两个做了这事呢?”是的,那里面部分是“运气”,部分是“有准备”。“部分”一概念也是我后面要谈到的另一问题。所以,尽管我会不时提及“运气”这个问题,但我不会把运气这东西看成与你的工作出色与否有没有关联的的唯一砝码(谢谢海涛帮我“掰斥”这句。译者注)我主张即使不是全部你也要对“运气”有部分掌控。最后我引用牛顿对此的原话:“如果别人也和我一样努力思考的话,那么他们也许会得出差不多的结论。”(译者注:问问自己,用一卡车苹果往你头上砸,直把你砸晕看能砸出个什么来。)

包括许多(大)科学家在内的很多人所具有的一个特质,如你所见,就是通常在他们年轻的时候,他们具有独立的思维并有勇气去追求。举一个例子,爱因斯坦,大概在他12或14岁的时候,他问自己:如果我有光速那么快,那么光波看起来是个什么样子?现在他知道了光电理论告诉你不可能有稳定的局部极大(local maximum),但是你随着光速移动,你就能看到局部极大(local maximum)。他能在12或14的时候就难能看到这样的“矛盾”——所有的事物在光速条件下看起来不一样。是运气使得他最后创造了相对论吗?(那是由于)他早就开始积累对此问题的思考。这,就是必要条件,而非充分条件。所有这些就是我要谈论的“运气”和“非运气”。

那么,把很多聪明的头脑都凑在一起会怎样?这主意听起来不错。这屋子里的听众们大概都具有从事一流工作还富余的头脑。“有头脑”可用不同的方式来衡量。在数学、物理、天体物理方面,一般来说,头脑在很大程度上与处理那些“信号”有关。因此标准的IQ测试足够给他们一个高分。但另一方面,在其他领域里有点不同。举个例子, Bill Pfann,此人发明了区域溶化(zome melting)理论,有一天走进我的办公室。他那时只是模模糊糊地有了一些想法和提出了一些问题。当时我非常清楚此人不太懂数学,而且有点“茶壶煮汤圆 ——有话说不明”的意思。但我觉得他的问题挺有意思的,于是我就把他的问题带回家琢磨了一下。我最后教他如何使用计算机以便帮他计算自己的答案。我给他提供了用数学计算的动力,他于是走了下去,悄无声息地在他自己的公寓里干了下去。终于他收获了在此领域里的全部声誉。只要他有了一个良好的开头,他的胆怯、他的不熟练、他的含糊不清都会消失。他会用用其他而更具成效的方式。当然,他变得更加融会贯通(articulate)。(译者注:也许你对 articulate会有不同翻译,对我,articulate就是“融会贯通”。其实翻译,即understanding + articulate,和做任何一件事一样,关键在于你融会贯通。)

我还要举另一个人的例子,希望他不在场。一个叫Clogson的家伙。我遇到他的时候正值我和他一起在John Pierce(贝尔实验室研究总监,在通信理论、电子光学和行波管研究方面有突出贡献。译者注。)小组一起攻克一个难题,我那时可没觉得他有肚里没有什么料(I didn’t think he had much)。我问那些和他一同上过学的同事们:“他在学校里就这德性吗?”“是的”,他们回答。那好,我还是把他辞退了吧。但是John Pierce明智地把他保了下来。Clogston最终做成了Clogston Cable (想想吧,能以他的名字命名东西的人是什么牛吧。译者注)。他并从此一发不可收拾,一次成功给他带来了自信和勇气。

成功科学家的重要品质之一就是勇气。一旦你鼓起了自己的勇气并相信自己能解决重要的问题,那么你就行。如果你觉得你不行,几乎肯定你不会去做。勇气就是香农(Shannon)所拥有的最重要的东西之一。想一想他的主要定理。他想建立一种编码方法,但是他并不清楚如何做,所以他搞了一个随机码(a random code)。然后他又卡了壳。然后他问了一个“不可能”的问题:“一个平均随机码(the average random code)会怎样?” 他于是去证明了平均码(average code)是arbitrarily good(随意性良好?),并且因而一定存在至少一个好的编码。除了一个拥有无限勇气的人,还有谁胆敢有如此勇气想此所想! 这就是伟大的科学家的品质——他们有勇气。他们不管周围境况,勇往直前;他们思考、思考、再思考。

年龄是另外一个自然科学家们(physicists)担心的因素。他们总是说你要做就得趁年轻,否则就别做。爱因斯坦做事就早,所有的量子理论的同仁们做他们的“事”的时候都早得吓人(disgustingly young)。大多数数学家、理论物理学家,以及天体物理学家都在他们的早年作出了我们公认的他们最好的成就。这并不是说他们岁数大了以后就不能做有益的工作,只是我们认为他们最有价值的事是他们年青的时候所为。在另一方面,在音乐、政治和文学方面,通常的情况是,那些我们仰慕的大作品往往出炉较晚。我不知道你的情况适合以上的哪种情况,但年龄总是有影响。

就让我说说为什么年龄产生那些影响。首先,如果你要做一些有益的工作,你必须要找到你全心身投入的状态,全力投入以至于不能再做更多的事了。你也许发现你就和我见到获诺贝尔奖时的布拉顿(Brattain, 美国物理学家, 曾获1956年诺贝尔物理学奖)差不多。颁奖的那天我们全都聚集Arnold大厅(Arnold Auditorium),三个获奖者都上台发表了演讲。第三个是布拉顿,他差不多噙着泪水说:“我知道这个诺贝尔奖的影响,但我不会让它影响我。我会继续保持做个好的老瓦尔特.布拉顿。” 我于是对自己说:“真带劲!”。但是仅仅几周的功夫我就看见(诺贝尔奖)对他产生影响。现在他只能对付那些“伟大的”的问题了。(译者注:既然如此的大牛科学家都为身外之物所累,我们又怎可幸免?所以,你没有做好“出名”的准备之前,不可妄自出名。名可不是什么人都可以出的。)

当你成名后再做一些“小”事就难了,香农(Shannon)也难逃此运。有了信息理论(information theory),你还能有什么“花招”呢?那些伟大的科学家也经常犯这样的“晕”。他们未能继续燃烧心中本可以燎原的星星之火(They fail to continue to plant the little acorns from which the mighty oak trees grow)。他们把“大”的事情给打发掉了。这并不是事情的本来面目。所以,这解释了为什么你明白一旦成名太早你就往往“废”了(sterilize you)。实际上我要给你我多年的最爱的例子:普林斯顿高级研修学院,比起其他的学院,在我看来,已经毁了无数好的科学家,你只要比比那些科学家去“普高”之前和之后的成就就可以分辨这点。他们进去之前可谓超级牛(superb),出来之后就变得一般牛了(only good)。

从这又引出工作条件的话题,也许有点次序颠倒。多数人想的是最好的工作条件。非常清楚,事实并非如此,因为人们常常在条件不好的时候富有成果。剑桥物理实验室有史以来最好的时期恰逢是他们实际上最简陋的时期——他们做出了有史以来最好的物理。

我给你一个我个人生活的故事。早些时候,对我来讲似乎表明贝尔实验室不像是常说的搞二进制的计算机程序的人聚集的地方。的确不是。但是每个人的确就是这样做出来的。(贝尔实验室自1925年成立至今,科学家们共获31000多项专利,他们中的11人获诺贝尔奖,他们中的其他人选择获得别的奖或其他的东西。译者注。)我本可以去西海岸找个什么飞机公司的差事也不是什么问题,但是贝尔实验室的人是些让人兴奋的人,而那些飞机公司的同仁不是。我想了好长一阵子,我去还是不去?我一直在想两全其美的是。最后我对自己说:“Hamming, 你一直想计算机能做任何事,为什么你不能让他们写程序?” 首先跳进我脑海的是“毛病”,并促使我非常糟的进入自动程序系统。所以,那些看起来像缺陷的东西,通过换位思考,常常变成你可能拥有的最有价值的财富。但你似 乎不太可能头一次看到它时就说:“哇塞,我不可能召集足够的程序员,那么我怎能搞成任何大事呢?”

这类的故事多的是。 Grace Hopper (Grace Murray Hopper 是共享代码库、编译器验证软件以及编译器标准的使用的早期倡导者。促进了计算机科学的发展,促成了COBOL的产生。译者注) 也有一个。我想只要你用点心你就能明白,伟大的科学家常常通过换一个角度看问题,就能把瑕疵变成财富。例如,许多科学家每当不能解决一个难题时,他们终究转而去研究为什么“不能”的问题。他们然后反过来看问题:“本来嘛,这才是问题所在。” 于是,就有了一个重要的结果。所以,理想的工作条件非常奇特——你想要的往往不是对你来说最好的。

现在来谈谈驱动力的问题。你观察到大多数伟大的科学家都有惊人的动力。我和John Tukey (1973年获得美国国家科学奖。在数学和统计学理论方面进行了深入的研究,并为统计学在物理学、社会科学和工程学方面的应用做出了突出贡献。译者注) 一起工作了10年,他一直动力十足。大约我加入三、四年后的一天,我突然发现John Tukey比我还稍年轻一些。John是个天才,我显然不是。我于是冲进Bode的办公室,对他说:“像我这‘把’年纪的人如何能和John Tukey了解得一样多?” 他向后靠在椅子上,把手放到脑后,咧嘴笑道:“如果你知道这些年像他一样努力的话你就能了解多少,你会大吃一惊的。”我无地自容般地(simply)逃出了他的办公室。

Bode实际上是这意思:知识和创造的成果就像利滚利(compound interest)。假设两个人拥有几乎一样的能力,其中一个人比另一个人多干十分之一的活,她将多产两倍。你知道得越多,就学得越多;你学得越多,就做得越多;你做得越多,机会就越多。这特别像“复利”。我不会给你一个“利率”,但是那是非常高的利率。假设两个人的能力一模一样,其中一个人设法日复一日每天都思考一个小时,那么他的一生的“产能”将是大大的提高。我把Bode的话记在心里。这些年我花了相当的功夫试着再努力一些,结果我发现,实际上我能做更多的工作。我本不愿在我太太面前说,但我得承认,我有时忽视了她。我得钻研。如果你一心想做成某件事,有时你不得不对另一些事视而不见。对此毫无疑问。

有关动力,爱迪生说:“天才是99%的汗水加1%的灵感”(听了老爱用中文说这话说了好几十年,今儿才搞清楚说的是“排汗”(perspiration)之类。译者注。)这也许有点夸张,意思却是说,“像样的‘活’比你想象的还要难干”,这一点放之四海而皆准。干成大事非的下功夫不可,而费脑力功夫使得 “活”难上加难。这就是症结,动力如果“使”不对的话,你便一事无成。我常思量我那么多在贝尔实验室的朋友们,工作努力的程度与我相比有过之无不及,为什么他们难成正果 (didn’t have so much to show for it)?有劲瞎使是个很严重的问题。玩命工作是不够的——好钢要用到刀刃上(it must be applied sendibly)。

我还得说说另一个性格方面的特点,那就是“似是而非”。我可是花了好一阵子才搞明白其重要性的。大多数人愿意相信世上万物非此即彼,是非分明。大科学家们却能很大程度地容忍“似是而非”。他们充分相信(自己的)预测,靠思想前行;他们有保持足够的警觉,随时挑出其中的错误和瑕疵,以便超越旧有理论,去创造新的、替代的学说。如果你过于相信,你将无暇留神其中的破绽;如果你过分怀疑,你甚至将无从起步。这需要一个良好的平衡。多数大科学家非常清楚为什么他们的理论是真知灼见,同时也知道哪里还有些小毛病,不敢忘怀。达尔文在他的自传里记载了他发现的每一处与他的信条相抵触的迹象,非如此,那些“证据”就会从他脑海里消失。每当你发现明显的毛病,你最好保持敏感并跟踪那些东西,紧紧盯住看看你能否解释或者调整你的理论去适应(这些“毛病”)。大成就大多如此。所谓大成就并不是指那些靠多加一位小数点搞成的东西,而是指那些投入感情的的事情。大多数大科学家们完全将他们自己融入课题之中,而不能完全投入的人鲜有做出杰出的、一流的成果的。

再者,感情投入还不够,这显然是一个必要条件。我能告诉你其中的理由。每一个研究了创造力的人都会认为“创造力从你的潜意识而来”。不知怎的,突然之间,灵光乍现(there it is!),说来就来。当然,我们对潜意识知之甚少。但是你非常清楚的是,你的梦也来自你的潜意识。并且你也意识到,在相当程度上你的梦是你白天的再现。如果你深深地痴迷并投入到一个问题中去,日复一日,你的潜意识除了除了干这活也不会干别的。然后,你在某个早晨,或某个下午(哈…,译者注)一觉醒来:有啦!(and there’s the answer.) 对于那些个不能投入到当前的事情上的人来说,他们的潜意识此时不知在哪儿磨蹭呢,凭何指望有什么好结果?所以,做事情的法子就是:如果你找到一件真正重要的事情,你就不要让任何别的事情成为你注意力的中心—-你思你所思(you keep your thoughts on the problem)。保持你饥饿的潜意识使它想你所想,然后你就可以安心地睡觉,静等天明,答案便不取自来。

现在聊聊Alan Chynoweth(演讲当天的主持人,好像是光纤通信大牛,译者注)提到我老是和搞物理的那帮人一起吃饭。我在此之前是和搞数学的人一块吃饭的,但我发现我已经了解了不少数学的东西,所以,事实上我所学甚少。物理学的饭桌那边,如他所说,的确是有点让人兴奋。但我认为他对我的贡献有点夸大其词了。听 Shockley (1956年诺贝尔物理学奖获得者)、Brattain (1956年诺贝尔物理学奖获得者)、Bardeen (1965、1972年两度物理学奖获得者)、J.B.Johnson (物理学家,噪声方面专家,发现热燥声,Johnson noice)、Ken Mckay (没找到背景的反正均为大牛科学家。译者注)还有其他人聊,我兴趣盎然,收获颇丰。但是可惜的是,诺贝尔奖、提升接踵而至,剩下我们这些“沉渣”而已。没人想要这些残渣剩饭,因此,和他们吃饭何益?

挨着物理学的饭桌的是化学那帮人的饭桌。我曾和其中一个家伙一起干过,Dave McCall (多牛?译者注),那时他正和我们的秘书眉来眼去的呢。我走过去对他说:“我能加入你们吗?”他们还能说不吗。所以我就和他们那帮人吃了一阵子饭。我开始发问了:“什么是你们哪个领域的重要的事呢?” 一个多星期以后,另一个问题:“你们正在搞什么重要的课题呢?” 有过了一段时间后:“如果你们干的事情不那么重要,如果你们不认为那将导致重大的结果,那你们还在贝尔实验室搞它干嘛呢?”我于是从此不再受欢迎。我得再找别的人去吃饭了了!那还是在春天。

到了秋天,Dave McCall在饭厅堵住我对我说:“Hamming,你的话一直让我记着。我想了一个夏天,比如,什么是我的领域里重要的问题。我并没有改变我的研究,但是,这思考是值得的。” 我然后说:“谢谢你,Dave。”转身走了。我注意到几个月以后他成了他们部门的头,我注意到有一天他成了国家工程院的院士(member)。我注意到他成功了。我可没听说过他们那个饭桌上的还有其他人在科学和圈子里被提起过。他们没能问自己:什么是我这个领域里的重要问题?

如果你不去搞那些重大的问题,你就没法干那些重要的活。十分显而易见,大科学家细细地从头到尾考虑过在他们那个领域里的诸多重要难题,并且随时留神考虑如何攻克那些难题。我得提醒你,说“重要/大问题”得留神。在一定的意义上,当我在贝尔尔实验室的时候,那三个在物理方面的突出难题,从未被好好研究过。所说重要,是指可以获得诺贝尔奖以及你能谈及的任何金钱的程度。我们未曾搞过(1)时间旅行;(2)遥距传递(teleportation);(3)反引力 (antigravity)。我们不去攻克他们就不显重要。不是结果导致一个问题的重要性,是你找到合理的攻克手段(使它重要)(It’s not the consequence that makes a problem important, it is that you have reasonable attack)。当我说多数科学家没有做那些重要的工作,我是指这个意思。

我前面说到过“星星之火,可以燎原 (planting acorns so that oaks will grow)”之类。又不可能总能清楚结果在哪,但你却能在那些可能“有戏”的地方充满活力。甚至即使你相信大的科学就是一些运气什么的,你仍要站到电闪雷鸣的山顶, 而不必藏在你感觉安全的峡谷。话虽如此,众多科学工作者毕生仍只例行公事般地从事“安全”的工作,所以他/她“产出”有限。就这么简单:如果你要干大事,你必须毫不迟疑地(clearly)去干重大难题,而且你得有个想法。

顺着John Tukey和其他人主张的思路,我最终采用了我称作“重大思考时间”“制度”。当我周五去吃午饭,我此后只会讨论重大思考。所谓重大思考,我是指那些诸如 “计算机对整个AT&T会成为什么角色”,“计算机怎样改变科学界”的问题。举个例子,我那时注意到十分之九的实验是在实验室做的,但只有十分之一是在计算机上做的。我有次专门跟一个副总裁谈了我的看法:事情得反过来。比如十分之九的的试验应该在计算机上做,剩下十分之一留给实验室。他们早知道我是数学狂缺乏现实观。我知道他们错了,并且随着越来越证明我对,他们自然就越来越错了。他们在不需要的时候建起了各种实验室。我发现计算机正改变着自然科学,因为我花了很多时间问自己:“计算机会给科学什么影响,我能怎样改变(影响)?”我再问:“这如何影响贝尔实验室呢?”我有一次发表高见,用同样的方式,指出一半以上的贝尔试验的人在我离开之前将会离不开计算机或相关。现在你们已经看到结局了。我发奋思考:我的领域向何处去,机会在哪里,什么是重要的事情值得做。让我继续下去,就会有机会做点大事。

多数大科学家牢记很多重大问题。他们约有一二十个大问题想方设法去攻克。每当他们发现一个新想法出现的时候,你就会听到他们说:“唔,这个与该问题有关。”他们于是抛开其他一切,全攻此问题。现在我要说一个可怕的故事,我听来的,不担保其真实性。我当时坐在机场候机厅正和一个在Los Alamos的朋友谈论关于在欧洲发生的裂变实验在当时多幸运,因为这使得我们在美国这儿能搞原子弹。他说:“不。在伯克利(Berkeley)我们已经收集的不少的数据。我们之所以没能推导出来,是因为我们正在建造更多的机器设备,如果我们推导出来那些数据的话,我们就能发现裂变。”他们让到手的鸭子飞了。机会稍纵即逝!

伟大的科学家们,一旦机会来临,他们便紧追其后并且决不言弃。他们放下其他一切。他们摆脱掉其他事情,紧追一个想法不放手,因为他们已经有了通盘的考虑。他们的思想是时刻准备着的,看见机会就紧跟其后。当然,很多时候也不能奏效,但是你并不需要如此“鞍打”多次就能做一些大的科学。就这么简单。一个主要的诀窍就是活得长一点。

另一个性格特点,我一开始并没注意到。我注意到以下这些事实:有人“闭门造车”,有人“开门迎客” (people who work with the door open or the door close)。我观察到,如果你把办公室的门关起来,你今儿或明儿就能多干点,你也会比别人多出不少的活。但是,10年以后就未必了。你不知道干了点什么值得干的事儿。那些把门敞开的人的确是受了很多的打扰,但他也不时地获得些线索,了解这世界是什么或什么更重要。好了,我是无法证明何为因何为果,因为你会说:“关门造车”意味着“封闭心灵。”我可不知道。只是我可以说,那些敞开了门干活的人和最终成就了大事的人之间,存在千丝万缕的联系,即使你关上门多使劲地干也无济于事。反而,他们看起来干得有点不对劲——也不是太不对劲,但足以不成气候。

我想谈谈另一个话题,那是从大家都知道的歌词里来:“你做什么无关紧要,你怎样做才紧要。”我从自己的一个例子说起。当年正值关注二进制的日子里,我着迷似的搞着数字电脑(digital computer),其中一个问题最好的模拟运算装置(analog computer)也无能为力。(天哪,我头一回才听说电脑分数字的和模拟的,我犯错了吗?我以小人之见斗胆将“analog computer翻成“模拟运算装置”。大家瞧着办。五、六十年代的“大家伙”到底都什么样呢?译者注)。后来我得到了一个结果。我仔细考量了之后对自己说:“嗨,Hamming,你知道你得就这个军事方面的活向上打个报告。你花了那么多的钱可得能说明问题在哪啊,每一个模拟装置都等着看你的报告以便确实找不到毛病了。” 老实说,我是用对付一个相当简单的(crummy)的方法去做这要求的大集成的,但我居然也得到了答案。我终于明白了事实上这问题不在于就是找到了答案,关键在于首先证明了它,在此之上,我能用一个数字电脑战胜“模拟电脑”(又来啦,analog computer,就是它啦。译者注),而且在它自己的“地盘”(哪个地盘?明白的就明白了,糊涂就糊涂吧。反正咱也不可能搞懂所有的事儿。译者注)。我然后修改了那个解决方案的法子,创立了一个相当一流的理论。那个公布出来的报告就有一个后来好多年以后公认的“Hamming’s method Integrating Differential Equiations(“哈明XXXX法”, 哈哈,谁愿意怎么翻就怎么翻吧。译者注)这个现在说起来可能有点陈康烂谷子了,但是当时可火了一阵子。就是稍微改变了问题本身,我把无关紧要的活干成了一个大活。

同理,当早年在顶楼用机器(再次提及的“机器”均指计算机。那个年代,计算机不是我们看到的样子。译者注)的时候,我在攻克一个又一个难题,成功的居多失败的少。周五弄完了一个问题回到家里,却奇怪我并不快活——我很沮丧。我看到生活就是一个问题接着一个问题又接着另一个问题。想了相当长一阵子后,我决定:不,我得对各种“产品”进行“批量生产”,我得考虑所有“下一步的问题”,而不是仅仅眼前的问题。通过改变提问,我仍得到了同样甚至更好的结果。我去着手主要问题:我如何才能在我不知问题是什么的时候攻克机器(计算机。译者注)并做些“未来的问题”?我要如何为此做准备?我要怎样做才能站到计算机之巅?我要如何遵从牛顿的法则?他说:“如果我能比别人看得远,那是因为我站在巨人的肩旁上。” 而现如今,我们(仅)站在相互的脚面上!

你应该以这样的方式去干你的活:甘为人梯!于是别人就会说:“看哪,我站在他的肩膀之上,我看得更远了。” 科学的本质是积累!通过稍微改变一下问题,你就能常常作出非常好的的活,而不是一般好的活。我不去做相互孤立的问题,除非看到一类相同的本质。我决不再去解决单一的问题。

现在,如果你是个不错的数学家,你就知道努力的归纳意味着简单的结论。“那是他要的问题,但是这是问题如此这般的特征。对啊,我能用高明得多的方法攻克整个这一类难题,因为我尚未被那些细节所困扰。” 这个抽象的“买卖”真值,常让事情变得简单。更者,我丢掉(file away)细枝末节,只准备将来的问题。

为了结束这部分,我要提醒你:“好工匠不怨家伙式——一个有用之才与其工作的问题相处融洽,无论他得到什么,并且尽力而为争取最好的解决结果。” 我还要建议,通过改变问题,通过从不同的角度看事物,在你的最终成果中,你总能成就相当程度的不同寻常,因为,你要不然能以此方式做事——让人们确实在你的成果的基础上有所建树;要不然只能以彼方法干活——下一个人不得不把你干的活从头再来复制一遍。这不是仅仅一个作业的方法,这是你写报告的方法,你写论文的方法,以及整个态度。做更广泛的、一般的工作就像做一个个案一样容易,并且会更加有惊人满意的结果和有价值!

我现在得来聊聊一个非常讨厌的话题——你做完一件事情还不够,你还得把它“贩卖”出去。对于一个科学家而言,推销是一件棘手的事。这非常讨厌,你本不该做这事,这世界就该等着,当你做成某件大事时,他们就该赶快出来主动迎接。但是,事与愿违的是每个人都很忙着他们自己的活。你必须很好地主动介绍,使得他们能把手头的活放在一边,过来瞧瞧你的东西,理解它,然后回过头来说:“是,那玩意不错。” 我建议当你打开一本刊物,翻页的时候,你问问为什么你读其中一些文章,不读另外一些。你最好在写报告的时候也想想:当它发表在《物理评论》或其它什么刊物上的时候,别让读者们把你的文章翻过去,而是停下来读一读你的文章。如果他们不停下来读它,你就会竹篮打水一场空(you won’t get credit)。

一共有三件事你得去推销。你得学会写好写清楚以便人们愿意看;你必须学会发表相当正式的发言;你还必须学会作出非正式的谈话。我们有不少所谓的“后排科学家”。在一个会议上,他们更愿意闭口不谈。三星期后,决定也做完了,然后他们提交了一份报告,说了一通为什么你该如此这般一番。哎,太晚了。他们不愿站在一个炙手可热的会议的中央,在大庭广众之下说:“我们应该做这件事,为了这些原因…”你必须掌控这种形式的交流以及准备发表演说。

当我刚开始做演讲的时候,我几乎是一种生理上的病态,我非常非常紧张。我意识到或者我得学习作演讲,或者我的整个职业生涯就得缺一条腿。头一次在纽约IBM要我做一个演讲,我决定要做一个非常好的演讲,一个真正符合听众需要的演讲,不是一个专业上的,而是更广泛的;一个如听众喜欢,我可以在演讲结束时轻轻地说“只要你们想听,我任何时候愿意效劳”的演讲。其结果,我通过给有限的听众做演讲获得了大量的锻炼。最终我战胜了害怕,而且,我也能学到什么方法有效,什么方法没效。

通过参加会议我搞清楚了为什么有的论文能够被记住而有的却不能。专业人员就愿谈论非常限定的专业问题,但大多数情况下听众只想要一个宽泛的发言,并且希望比发言者说得更多的调查和背景介绍。其结果是,很多发言毫无效果而言。发言者说了个题目,然后一猛子扎进了他解决的细节中去,听众席上的极少人能够跟进。你应当勾勒一个大致的图画去说明为什么重要,然后慢慢地给出纲要,说明做了什么。那样更多的人就会说:“对,乔做了这个或马莉做了那个。我知道了怎么回事。是呀,马莉讲得不错,我明白了马莉做了什么。”我们的倾向是做一个高度限定的、安全的发言。但那往往是没有成效的。而且,太多的发言充斥了太多的信息。所以我说“推销”的方法显而易见。

让我总结一下。你得去干那些重要的问题。我反对全部是运气,但是我承认是有不少运气的成分。我赞成巴斯德的“运气光顾有准备之士”的说法。我极力主张我过去所为,如多年以来坚持的星期五下午“大想法时间”,只有大想法—-意思是我投入10%的时间试图去搞懂本领域更大的问题,比如什么重要和什么不重要。我早些时候发现我相信“此”却一整周时间都奔着“彼”方向忙乎。这的确有点滑稽。如果我真正相信作用点在“这”,为什么我往“那”去?我要不就的改变我的目标,要不 就的调整行动。所以,我改变我做的事并且向认为重要的方向迈进。就这么简单。

现在你也许要告诉我,你还未能支配那些你干的事。当然,当你刚开始的时候是有点难。但一旦你获得了适当的成功,就会有更多的人前来要求结果,比你能提供的要多的时候,你就有了一些选择的权力了,但不是全部。我来告诉你相关的一个故事,这还与“开导”你的老板的主题有关。我有一个老板,叫Schelkunff,它过去和现在都是我的好朋友。有军队的人来求助我,要求周五出答案。嗯,我已经决定把我的计算机资源为一组科学家所用,用于精炼数据。我正沉浸于短的、小的、重要的问题。这个军队的人却要我在周五提交结果。我说: “不行。我会在星期一给你结果。” 他就跑到我的老板Schelkunoff那里。Schelkunoff说:“你必须给他干这活。他必须周五要结果。” 我问他:“为什么我也得如此呢?” 他说:“你必须!” 我说:“行。Sergei,但是你得坐在你的办公室一直到周五最后一班班车,盯着那伙计,看着他走出门去。” 我在周五下午很晚拿出了结果,给了那军队的人。我然后走到Schelkunoff的办公室坐下。当那人出门的时候,我说:“你看, Schelkunoff,这伙计手里什么也没拿。我可是把结果给他了啊。” 星期一一早Schelkunoff把他叫来,对他说:“你周末过来干活了吗?” 我能听到好像磨磨唧唧的,那伙计试图搞清楚到底怎么发生了什么。他知道他本该周末到,没有最好别说有。所以他说他没来。从那以后 Schelkunoff总说:“你设定了你的最后期限,但那也没准(you can change them)。”

一次教训就足以开导我的老板明白为什么我不愿把探索性的研究放在一边儿去搞什么华而不实的事,为什么我能判断不去做那些抢占所有设施的没劲的事。我宁肯用这希望设备去为一个小事进行大运算。再说一遍,早年我的“运算”能力受到限制,因为在我的领域里,“数学家对机器无用处”的结论显而易见。每次我都得告诉其他领域里的科学家们,当他们抱怨:“我没法干,我没有计算机(mechine)。” 我跟他们说:“去告诉你们的副总裁:Hamming需要更多的计算机(computing capacity)。”

我还干了一件事。当在计算领域早些时候我产生了(loaned)一点编程的能力时,我说:“我们没有给与我们的程序员足够的认可。当你发表一篇论文时,你应该谢谢程序员,否则你就别再从我这指望更多的帮助了。程序员应该被个别地致谢,因为他们付出了努力。” 我等了好多年,然后我翻了翻某一年全年的BSTJ(The Bell System Technical Journal. 译者注)文章,数数有哪些专门感谢了那些程序员。我把这拿到老板那里,对他说:“这反映计算机在贝尔实验室的中心地位——如果BSTJ是重要的,那么,计算机怎么重要就一目了然了。” 他只好让步。你也能开导你的老板,这并不容易。在此,我是自下而上的角度,而不是自上而下。但我告诉你是怎样才能得到你所需要的,不管头头们怎么想。你得把想法“推销”给他们。

好了,我现在谈下一个话题:“努力去做一个大科学家值得吗?”要回答这个问题,你必须问问周围的牛人。如果你能让他们放下谦虚,他们往往会说:“是的,做真正一流的事情,并且掌握(knowing)它,就如同将美 酒、美女、和美曲(wine, women, and song)放到一起一样美妙。如果你再看看老板们,他们往往都重又回来,或者提出项目要求,试图重去体验新发现的时刻。他们总是这样。所以很显然,做过的人还想再做。但是这种体验是有限的。我从不敢出去问那些没干过大事的人他们怎么想这个问题。这难免有失偏颇,但我还是觉得值得一试。我想,十分肯定地值得一试那些一流的工作,因为事实是,价值体现在奋斗过程中而非结果上。为自己的事情奋斗本身就值得。成功和名誉只是附带的孳息而已。

我已经告诉你如何做。那么既然如此容易,为什么那么多聪明人还是失败了呢?比如,在我看来如今贝尔实验室数学部门有不少人比我有才华和能力,但他们却没能做的和我一样多。确有一部分比我做的要多,香农(Shannon)就比我多,还有别的一些人。但我的确比很多资质高的同事要多产。为什么这样?他们怎么啦?为什么这么多的有很好前景的人都失败了?

其中一个原因是动力和投入。做大事的人中,能力差一点但全力投入的人,比起能力很强但有点花里胡哨——那些白天上班干活晚上回家干别的第二天再来干活的人,要多有成就些。他们缺乏一流工作所需的必要的投入。他们是赶出了不少得不错的事,但别忘了,我们说的可是一流的工作。这是完全不同的。不错的人,聪明的人,总是出些不错的活。但我们说的是非同平常的活,是可以获得诺贝尔奖和真正荣誉的活。

第二个原因我觉得是个性的缺陷。我要举一个我在Irvine(美国加州大学 Irvine分晓。译者注)熟识的一位同事的例子。他是计算机中心的头并且那阵子是校长的特别助理。显然他有一个光明的前途。有一次他带我到他的办公室向我介绍她处理信件的方法,以及如何处理回信。他告诉我他的秘书如何的为有效率。他把信件一垛一垛分放好,并且知道哪是哪。而且它会自己用打字机一一回信。他向我吹嘘有多么多么了不起,它是如何不用秘书的帮忙把这些事都干了。我于是背着她问他的秘书。那秘书说: “我当然没法帮他,他根本不让我拿到他的信件。他不让我进入他的网络系统,我也不知道东西放在地板的哪块。我当然没法帮他。”然后我回去对他说:“你看,如果你用现在的方法,单枪匹马地干,你就只能原地踏步了,不会有长进了。如果你能学会利用整个系统来工作,你就能走得更远,能走多远就多远。” 结果是他再没有什么长进了。他缺失的个性使得他总想控制一切,而不是意识到你需要整个系统的支持。

你会发现这种情况屡见不鲜。普通的科学家会与系统为帝,而不是学会和系统相处并利用系统所提供的帮助。系统的支持其实很多,如果你能学会如何用的话。如果你有耐心的话,你就能学会很好地使用系统,而且,你总就会学会如何绕过它。因为(after all),如果你需要一个拒绝,你就到你的老板那里,轻易就能得到一个拒绝。如果你想做什么事,别去请求,做就是了,然后交给他一个既定的事实。别个他一个拒绝你的机会。但如果你就想要“不”,那很容易得到那个“不”。

另一个个性缺陷是自负的坚持己见。我要说说我自己的事。我刚从 Los Alamos来时在在纽约麦迪逊大街590号,那时用着台计算机。我仍按西部的打扮,大斜杠口袋,一个bolo(bolo=bolo tie ,翻译成饰扣领带可能更好,译者注)以及所有那些玩艺。我隐隐约约地注意到我好像没有得到和别的人一样的服务。所以我开始估量估量。你来了等着轮到你。但我觉得我没得到公正的待遇。我对自己说:“咋回事?并没有IBM哪个副总裁说过‘得跟Hamming过不去’。只是那些底下的秘书们这样做。当一个裂缝出现的时候,他们抢着过来看看谁跌进去了,让后再去找别的人(瞧热闹。译者注)。可是,为什么?我可没得罪他们。”答案:我没有按照他们认为的此次此地应有的打扮穿衣着服。原来如此—-我没穿合适!我得做个决定——我是坚持我的自负,想穿什么就穿什么,从此耗干我职业生涯的努力;还是顺应环境?我最后决定还是作出努力顺应环境。真是一蹴而就,我于是马上得到更好的服务了。而现在,作为一个老怪物(old colorful character),我得到比其他人还好的服务。

你应当根据你演讲听众的期望来穿衣打扮。如果我要在麻省理工学院计算机中心做个演讲,我就穿个有bolo和旧款灯芯绒外套或别的什么。我十分清楚别让我的衣着、外表和举止影响我在意的事。不在少数的科学家觉得他们必须坚持他们的自我,按他们的方式做他们的事。他们不得不着这个、那个,还有其他的事,并且为此付出相当的代价。

John Tukey几乎总是穿着随意。他走进一个重要的办公室,人们往往要花一些时间才能这是一个一流的人人后才能听他说。有相当一阵子John不得不对付这类的麻烦(hostility)。真是浪费功夫!我不是说你应该顺从,我说“顺从的样子给你一条畅通之道”。如果你选择某些方面坚持自负,“我要按我的法子做这个”,你在你整个的职业是生涯中付出一定的代价。这样,在你的一生中,累积起来就会形成巨大量的不必要的麻烦。

通过“受累”更秘书们讲讲笑话和友好些,我从秘书那里获得了极大的帮助。例如,一次因为一些愚蠢的原因所有在Murray Hill的复制的服务都关门了。别问我怎么回事,他们就会这样。我有一些事必须要他们完成。我得秘书给Holmdel的什么人打电话,希望公司的车花1个小时来此地并且把复制的活完成,然后再回去。那可真是我长期努力鼓励她,给她讲笑话,以及对她友善的很好的回报。这就是投之桃李,报之琼瑶。通过认识你必须使用系统并研究如何让系统为你工作,你学会如何让系统为你的想法做调整。或者你可以直愣愣地与之为敌,如同一个未经宣战的小战争,更他较一辈子劲。

我觉得John Tukey付出了相当大的不必要的代价。不管怎的,他是个天才。但我认为他本可以更好,好很多,更简单,如果他愿意顺应一点点,而不是自负的坚持。他就是想任何时候想怎么穿就怎么穿。则不仅仅对穿着适用,也适用于其他千万件事情。人们会继续与系统为敌,你可以有时不这么干 (Not that you shouldn’t occasionally)!

当他们把图书馆从Murray Hill搬到远的那头时,我的一个好朋友提出要一辆自行车的申请。哈,机构也不是傻瓜,他们等了一整子送回来一张地图,并且说:“你可以在图上指名要走哪条路以便我们可以给你买个保险。”过了几个星期,他们又问:“你要把自行车放到哪里以及你准备怎么锁它以便我们如此这般。”他终于明白了他终究会被官样文章逼死,于是他举手投降。他后来升至贝尔实验室总裁。

Barney Oliver(天文学家,以SETI外星球智能探索研究著称。前HP实验室负责人。译者注)是个好人。有一次他给IEEE (Institute of Electrical and Electronics Engineers 美国电气及电子工程师学会。译者注)写信。那会儿贝尔实验室的正式的职位挺多,IEEE的“道”也挺深。既然你无法改变正式机构的规模,他就给IEEE出版方面的人,说:“既然有这么多IEEE会员都在贝尔实验室,并且官方机构如此之大,所以杂志的规模也得改变。” 他去争取他老板的签字,回来的还是他自己签字的那份的复印件,但他还是没搞清他的那份原件到底送出没有。我不是说你不该持改革的姿态,我是说我所了解的能人总是避免让自己惹上冲突的麻烦。他们游戏其中,然后丢开,投入到工作中。

许多二流的伙计常被系统逮着戏弄一番,然后带入纷争。他把他的精力花费在愚蠢的“项目”上。然后,你会告诉我总有人得去改变系统。我同意,的确有人得去干,你愿意去干哪样呢:一个是去改变系统,另一个是去做一流的事?到底哪一个角色是以想要的?必须十分清楚,当你与系统抗争的时候,你在干什么?多久这“笑话”能完?得费你多少功夫与之斗争?我的忠告是让别的什么人去干,你还是去成为一流科学家算了。你们中几乎没有人有能力即能改良系统又能成为一流的科学家。

另一方面,我们不能老是屈服。时常有相当数量的反抗是合理的。我注意到几乎所有科学家凭着单纯的感觉喜欢嘲弄一下系统。其结果基本上就是,你在其他领域没有创新你也无法在本领域获得原创力。原创力是与众不同!你如果不具备其他的创新的特质,你不可能成为一个有创造力的科学家。但是许多科学家为了满足他/她的自我,让他在其他方面的怪癖为他支付了不必要的高昂的代价。我不是反对所有的对自我的维护,我反对其中一部分。

另一个毛病时发怒。一个科学家经常变得狂躁,这根本无法办事。愉悦,好;生气,不好。发怒完全不对路子。你应该跟随和合作,而不是老跟系统过不去。

另一方面你应该看到一个事情得积极的一面,而不是消极的一面。我已经给了你好些例子,还有更多。我在某种情况下,通过改变对事情的看法,是如何将一个明显的缺点转化成优点的呢?我给你讲另一个例子。我是个任性的人,对此不用怀疑。我知道多数在休假期间写书的人不能按时完工。所以,我离开之前我就会告诉所有的朋友,当我(休假,译者注)回来的时候我的书就会完工。是的,我就要它完工——如果我没能写完它,我得为之感到羞愧!我用我的自负去帮助实现我想达到的举止。我夸下海口于是我不得不去实现。我很多次发现,就像耗子急了了也咬人(a cornered rat in a real trap),我不可思议地能力非凡。我认为完全值得一说:“好啊,我会在星期二把答案给你。” 即使还不知道怎样去做。星期天的晚上我还在想如何才能在星期二交差。我常常把我的自尊悬于一线,当然有时仍不成。但是如我所说,如同逼急了的老鼠,我常出人意料地干出很多出色的活。我觉得你需要学会利用自己,我觉得你应知道如何将一个局面从一个角度转换到另一个角度,以提高成功的机会。

自我错觉对于人类是非常非常平常的事。数不胜数的可能性是:你改变了一件事然后骗你自己让它看起来像别的样子。当你问:“为什么你没这样这样做?” 那个被问的人有一千个托辞。如果你看看科学史,通常是有10个人都差不多了,但是我们只注意到那个首先做出来的人,那剩下的9个人说:“哎,我想到了,但是我就是没这么做。如此这般。” 有太多的借口。为什么你不是那第一个?为什么你没能做好?别去辩解,别试图愚弄自己。你想跟给别人说什么借口就说什么吧,我不在乎。就是对自己要诚实。

如果你确实想成为一名一流的科学家,你的了解你自己,你的弱点,你的强项,即以你的坏毛病,比如我的自尊自大。怎样才能将一个缺点转化成一个优点?怎样才能将弹尽粮绝的境遇转化成你多需要的情形?我再说一次,如我所见,据我研究历史,成功的科学家改变视角,一个瑕疵也能变成了一块美玉(what was a defect became an asset)。

简而言之,我认为那些本已胜券在握的科学家最后未能成功的原因是:他们没做重要的问题;他们没能投入感情;他们没有试图改变对于看起来容易但仍重要的,尽管在别的情形下较困难的事情。还有,他们老是给自己各种借口为什么没做成。他们老是归结为运气使然。我已经告诉你事情有多容易,更我已经告诉你如何去改进。所以,动手吧,你们就会成为伟大的科学家。

————回答提问————

G.Chynoweth (主持人):这是充满智慧和洞察力的50分钟,这是从多年精彩的职业生涯积累而成。我自己就失去了这些足以令我们成功的洞察。这其中一些是非常非常及时的。其中之一就是要更多的计算机。今天上午我除了这个可没听到大家都在反复议论什么别的。所以,尽管我们可能比你早年就想到的迟了20-30年,Dick (同事对Hamming的称呼。译者注),但现在来的还是挺是时候的。Dick,我能想到的所有我们能从你的谈话中获得的智慧,其中一个就是:以后我在这个大厅里四处走走时,不再希望看到还有像Bellcore那样到处关着的门。这就是今天吸引我的观察之一。

由衷地谢谢你,Dick,这真是一次出色的大思考。现在我们接受提问。我可以肯定有不少人愿意继续下去Dick所论及的有关观点。

Hamming: 首先让我回应Alan Chynoweth提到的计算机的话题。我在研究中使用计算机多年,在过去的10年中我一直跟上面的头头脑脑说:“把那些(该死的)计算机从研究中拿开,我们总是被迫搞这些事。因为老得忙着应付那些计算机,我们都没法研究了。” 最后这话传上去了。他们打算把计算机搬到别的地方去。少说我是一个不受欢迎的“扫帚星”,可我奇怪人们并没有因他们的玩意被搬走了而对我嗤之以鼻。我跑到 Ed David的办公室对他说:“我说Ed,你得给你的研究人员一台机器。如果你给他们一台大家伙,我们就又回到和以前一样的麻烦中去了,于是我们又忙于机器而无暇思考了。所以,就给他们一台最小的机器,因为他们都是能人。他们会学会用小计算机做研究,代替大的计算机。” 想我所想,Unix出现了。我们给他们一个比较小的机器,他们决定让它做大的事情。我们得有一个系统来做,这就是Unix!

G.Chynoweth:我刚好也想说这事儿。在我们当前的环境下,Dick,虽然我们与那些处心积虑的官僚体系较劲,有一句是一个被激怒的AVP(?)说的话我老挂在嘴边。他使劲嚷嚷道:“Unis从未交付使用。”

问题:个人的压力会怎样?那会让事情不同吗?

Hamming:会的。但如果你不能投入感情,就不会。我在贝尔实验室这些年来一直有早期的溃疡病症(有研究声称溃疡病与压力有关。译者注),我到海军研究生院 (Naval Postgraduate Schoo)后病症就消失了,也放松了不少,现在我的健康状况好多了。但是如果你要想成为一个大科学家,你就得忍受压力。你也许会有一个优雅的一生,你也许会成为一个优雅的人,另外或者也许你会成为一个伟大的科学家。你要过只想有娱乐伴随、事事占全的优雅美满生活的话,你就会开始“优雅”的一生。

问题:你谈到的关于勇气的内容无人反对,像我们这些头发花白的人或已有建树的人已没有那么多担忧。但我感觉到在年轻人当中,他们当前的担心是在高度竞争环境下的抗风险能力。你对此有何高见?

Hamming:我还要举更多Ed David的例子,Ed David担忧我们社会中总体勇气的缺失。我们是走过了不同时期的人。我们走过了战争(二战。译者注),走过了建造了原子弹的Los Alamos,走过建设雷达的时期(此话背景不明,应是和二战有关。译者注),诸如此类,然后来到了(贝尔的)数学部门,一个研究的领域,以及一群充满勇气的人。我们目睹事情的经过,我们刚刚赢得了一场战争,美妙之极。我们有理由充满勇气以便完成更多的使命。所有这一切我都无法再重新“安排”重现一次。我也不能埋怨当今一代没有这样的勇气。但我同意你说的,我只是不能加上抱怨。就我看来,当今一代有伟大的理想,只是缺乏勇气去实现。但是我们有啊,因为我们因环境而拥有——我们刚刚经历了一场极成功的战争。在战争中,我们也曾长时间地绝望,如你所知,那是拼死的抗争。但是我们的胜利给了我们勇气和自信,这就是为什么你看到的40年代后期及整个50年代,各个科学实验室在早先的基础上产生了一系列的成果。因为我们中的许多人被过去的日子逼迫学习别的东西——我们被迫学习我们不想学习的东西,我们被迫打开那扇门——于是我们可以得益于我们学到的东西。的确,我对(当今一代的勇气)无能为力,我也无权指责年轻一代。这就是现实。

问题:有什么是管理层可以或应该做的吗?

Hamming:管理层做不了什么事!如果你所说的是研发管理,那是另一回事,我得再花一个小时来讲。这次演讲是关于个人如何成功地进行研究,与管理层能做什么无关,也与其他的任何障碍无关。那么你怎样做呢?就像我观察别人如何做的一样。就那么容易,也就那么难。(牛人说牛话啊。译者注)

问题:“自由讨论(头脑风暴)”应成为日常的必经程式码?

Hamming:以前这是个问题,但看起来没有什么“回报”。对于我自己来说,我内心有和别人交谈的愿望,但是一个头脑风暴的会议不是太有价值。我的确去和人认真地谈,对他说:“嗨,我认为是有这么回事,我是这样想,这样看的……”然后翻来覆去地谈来谈去。但是你必须挑选有能力的人谈。用其他的比喻,比如你知道的“临界质 (critical mass)”。如果你肚里有足够的料,你就拥有了临界质。再者就是我以前称呼的“不间断吸收器(sound absorbers 即国人所说的“吸功大法”。译者注)。 如果你有了“吸功大法”,你就能出新点子,然后他们只会说:“是,是,是。” 你需要做的就是行动起来去取得足够的临界质,“是呀,这提醒了我这样,这样,” 或者“你想过这样或那样吗?” 当你和别人谈话的时候,对那些只会点头称是的“好”人,你可拿开你的“吸功大法”了。去找那些能马上启发你的人谈吧。

例如,你一和 John Pierce谈话就会很快被激起情绪。以前有一帮子人我常和他们谈,比如Ed Gilbert,我常去他的办公室向他请教问题,听他讲,回来时信心百倍。我仔细挑选可以头脑风暴的人和不可以头脑风暴的人,因为“吸功大法”是祸根。他们只是一些好人,他们填满了整个空间但除了抽取你的思想,他们什么也不贡献,而且那些被抽取的新想法很快就寿终正寝了,而不是有个回音。是的,我发觉有必要和别人交谈。我想那些闭门造车的人未能这样做,导致了他们未能让他们的想法更锋利,比如“你注意到这里有什么事吗”。我从不知道有这样的事 ——我过去看个究竟就行了。有人指了条路,我看来,我已发现了一堆书我回家必须读。我去问那些我认定能回答我并给我尚不知道线索的人问题,然后我走出去,自己看个究竟。

问题:你在给阅读、写论文、和实际做研究各自分配时间上是如何取舍的?

Hamming:我坚信,在我的早年,我认为要花和原始研究一样多的时间用来修改和表达。现在我认为要花50%的时间用来表达,这是一个非常大的数字。

问题:应该花多少精力在图书馆里面?

Hamming:那要取决于什么领域。举个例子:在贝尔实验室有个同事,一个非常非常聪明的家伙。他老在图书馆里呆着,读所有的东西。如果你想要参考资料,你到他那里去,他就会告诉你所有的参考资料。但我在提出以上那些看法的同时,下这个结论:长此以往他不会有任何以他命名的成果。他现在已退休,成为了一个副教授。他是很有价值,我对此没有疑问。他写了一些不错的文章登在《物理评论》上,但他没有以他命名的成果,因为他读得太多。如果你成天研究别人怎么做的,你就会按别人的老路子思考。如果你想要有不同的新思维,你就得按那些创新的人的路子——先把问题搞得相当清楚,然后不去想任何答案,直到你已经仔细地把如何做的过程考虑清楚,以及如何你只要稍微调整以下问题的角度。所以,是的,你需要保持状态,保持状态去搞清问题,而不是成天靠读书去找答案。阅读是搞清“怎么回事”以及“可能性”的必要手段,但靠阅读去寻找答案不是可取的有意义的研究的方法。所以,我给你两个答案:你阅读;但不是靠读的量,而是靠读的方式起作用。

问题:你是如何让事情以你的名字命名的?

Hamming:靠做大事!我告诉你一个“Hamming window”的事。我以前老“难为”Tukey。后来一天我接到他从普林斯顿打来的电话。我知道他在搞power spectra(不敢乱译,字面为“能量频谱”之类。译者注),他问我是否介意他把某个window命名为“Hamming window”。我对他说:“算了吧,John,你知道我只做了很小的一部分,主要是你做的。” 他说:“对,Hamming,但你贡献了不少的‘小事’, 你理应得到这些荣誉。” 所以他就叫那为“Hamming window”。让我继续。我常搅合John的大事。我说的大事就是把你的名字变成“安培 ampere”、“瓦特 watt”、“傅立叶 fourier”的时候 ——但你的名字被拼成小写(西方人名以大写开头,小写即是以人命名某物。译者注)。这就是“Hamming window”的来历。

问题:你能谈谈演讲、写论文和写书之间各自的效果吗?

Hamming:短期来看,论文是非常重要的,如果你明天就要去激励某人。如果你想要一个长期的认可,写书的作用更大,因为我们大多数人需要方向。现今的知识几乎是无穷的,我们需要方向寻找自己的方向。让我告诉你什么是无穷的知识。从牛顿时代开始至今,我们差不多每17年就增加一倍的知识量。我们基本上通过“专业化”来应付。在下一个 340年,按此增长规律,会使原本的只是增加20次方,如一百万,并且现在的一个领域届时就会有一百万个专业领域。这不会发生。直到我们找到不同的工具,现在知识的增长就会窒息而停止。我确信那些帮助我们融会贯通的、协作的、抛开重复的、丢掉干瘪的方法,(从而代表重要思想的书)会成为未来后代所珍视。公开演讲也是必要的,私下谈话也是必要的,写论文也是必要的。但我倾向于认为,长期看,那些只写至关重要内容的书比起什么都谈的书要重要,因为你并不需要知道所有的事。我并不要了解那么多关于企鹅的事就是一个通常最好的回答。你只需要知道精髓。

问题:你提到在某个事业中获得诺贝尔奖的事以及随之而来的名声远扬。这就是有关名声更广泛的问题吗?一个人能为此做什么呢?

Hamming:你能做以下的事情:大约每7年做一个重大的专业领域调换,如果不是全部的。所以,我从数值分析到硬件,到软件,等等。周期性地,因为你想要用到你所有的想法。当你到了一个新的领域,你就像一个婴儿一样重新开始。你不再是一个mukity muk (不是英语单词。“权威/大人物”之类,完全瞎猜。译者注),你可以从头再来,你可以播洒那些种子以期长成参天大树。香农,我相信他毁了他自己。事实上,当他离开贝尔实验室的时候我就说:“香农的科学生涯结束了。” 我受到不少朋友的“炮击”,他们认为香农和以往一样聪明。我说:“是的,他仍聪明,但他的科学生涯就此结束。” 我确信事实如此。你的改变,一阵子之后你就会疲倦,你用光了在一个领域的创造力,你需要找到相近的事。我不是说要你从音乐换到理论物理再换到文学。我是说,在你的领域里你需要更换不会令你厌烦的区域。你不可避免地被迫每七年变动一次。如果你可以的话,我会要求一个做研究的条件,做到此,你得每七年改变一次研究的区域,伴随以合理的解释,或者到第十年的头上,管理层有权强制你改变。我坚持改变因为我是当真的。老的领域会发生什么呢?会有一些成熟的方法在那起作用,大家一直用着。他们在当初正确的方向上继续前行。但世界变化着,现在有新的方向。但老伙计们还在老路子上迈着步子。

你需要走进一个新的领域以求新的视角。你能为此做些事,但那要费神和费力。要有点勇气才能说出:“是的,我要放弃我的响亮名声。” 比如,当校正错码成功发布的时候,有了这些理论,我对自己说:“Hamming,你要停止看该领域的论文了,你要完全忽略它,你要试着做点别的事了,别老吃老本。” 我有意拒绝继续在此领域。我甚至不去读有关的文章以强迫自己去做别的一些事情。我操控着我自己,这就是我在整个谈话里反复宣讲的内容。了解我的缺点,我操控着自己。我有很多缺点,所以我有很多的问题,比如,有很多可操控的可能性。

问题:你能比较一下研究和管理吗?

Hamming:如果你想成为一名伟大的研究者,你就不要成为一个公司的总裁。如果你就是想成为公司的总裁,那是另一件事。我不反对成为公司总裁的想法,只是我不想。我认为Ian Ross在贝尔实验室总裁的位置上干得不错,我不唱反调。但是你得清楚你要什么。进一步说,当你还年轻,你也许希望挑选去成为一名伟大的科学家。如果你活得较长,你也许会改变你的想法。比如,一天,我到我的老板Bode那里,对他说:“为什么你要当这个部门的头呢?为什么你不去当一名大科学家呢?” 他说:“Hamming, 我有远见,知道贝尔实验室的数学部分要怎样,如果要让这个“远见”得到共识,我就得当上部门的头。” 当你觉得你想干什么的远见正好在你游刃有余的能力范围内,你就应努力获取它。如果有一天你的远见大大超过了你轻松应付的能力时,你就应该去做管理工作。而且,“远见”越大,你就应做越大的“管理”。如果你拥有一个关于整个实验室应该向何处去,或者有关整个贝尔系统,你就得到该去的位子让它实现。你从底层是无法轻易让它实现的。这取决于你的目标和对目标的渴望,而且这些都随生活而改变,你得准备这些变化。我选择回避管理工作因为我更希望做我容易应付的事。但这是我的选择,只对我起作用。每个人有权做出自己的选择,保持一个开放的心态。但是一旦你选择了一条道路,看在上天的份上,明确你做过什么以及你做了什么选择。别试着两样都占。

问题:一个人对自己的期望重要呢,还是置身于你所在的那个期望你做出大事的群体重要?

Hamming:在贝尔实验室,每一个人期望我干出大活—-这可是帮了我大忙。每个人期望你做出好的活,所以你就去做,如果你有自尊心的话。我想让你的周围聚集一流的人非常重要。我寻找最好的人群。当物理饭桌失去了最好的人时,我就离开。在化学饭桌同样情况发生时,我也离开。我总是跟着那些有能力的人,因此我能从他们那里学习,他们也期望我做出成绩来。通过有意操控自己,我觉得我做出了比放任自流好得多的事情。

问题:你在一开头弱化运气的成分,但你好像模糊了那些致使你到Los Alamos,使你到芝加哥、使你到贝尔实验室的特定事件。

Hamming:是有一些运气。另一方面我不知道其他的可替代的路。除非你能说其他的路原本就不会机会均等或比我现在更成功,我也无从得知。你做某件特定的事是因为运气吗?举个例子,当我在Los Alamos遇到Feynman时,我就知道他能获得诺贝尔奖。我不知道他为什么,但我就是知道他会从事伟大的工作。不论未来走哪个方向,这个人都会干大事。而且,显而易见,他做了。不是说你在这种特定条件下稍做一点点大事就是所谓“运气”,早晚有各种各样的机会。有大把大把的机会,如果你身在其中,你逮着一个,你早晚会成功,非此即彼。事事都有个运气的成分,“是”或者“不是”。运气关照有准备的头脑,运气宠爱有准备的人。当然,这不是什么担保。我不担保任何特定情况下的成功。我说:运气的确改变概率,但是对一个个人来说,在他身上总有一部分是绝对可由自身掌控的。

往前走,去做大事!



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