Transcript of famous & widely-quoted 1986-03-07 lecture by Turing-Award mathematician Richard Hamming about how to do scientific research & development based on his life, antecedents of eminence, people he knew, the growing use of computers in science, navigating bureaucracy, maintaining creativity, and running Bell Labs.
- See Also
- Further Reading
- Introduction of Dr. Richard W. Hamming
The Talk: “You and Your Research”
- Greatness Origins
- Life-Cycle Effects
- Fame & Working Conditions
- The Importance of Importance
- Selling Science
- Success Summary
- Is Greatness Worth It?
- Causes of Failure
- Failure Summary
- Discussion—Questions & Answers
- Biographical Sketch of Richard Hamming
- External Links
Bell Communications Research Colloquium Seminar
7 March 1986
Bell Communications Research
445 South Street
Morristown, NJ 07962-1910
At a seminar in the Bell Communications Research Colloquia Series, Dr. Richard W. Hamming [1915–1998; MacTutor], 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, 1986.1
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 40 years of experience, 30 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.Reader-Mode To hide all links & apparatus and read the plaintext version of Hamming’s speech, you can use reader-mode: [toggle]
In order to make the information in the talk more widely available, the tape recording that was made of that talk was carefully transcribed [in 1986?]. 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 [Kaiser] 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.
Variants (cf. Wikiquote):
“You and Your Research: A Stroke Of Genius: Striving For Greatness In All You Do”, 1993 (abbreviated variant for IEEE Potentials periodical)
- 1991-02-28 video recording (proprietary)
- Advice for a Young Investigator, Santiago Ramón y Cajal1897
- Advice to a Young Scientist, Peter Medawar1979
- An Essay on the Psychology of Invention in the Mathematical Field, Jacques Hadamard1945
- “Cargo Cult Science”, 1974
- “10 Lessons I Wish I Had Been Taught”, Gian-Carlo Rota1996
- “Epigrams in Programming”, Alan Perlis1982
- “Practicing Western Science Outside the West: Personal Observations on the Indian Scene”, 1985
- “Sunset Salvo”, Tukey1986; “John W. Tukey: His Life and Professional Contributions”, Brillinger2002
- “Technology and Courage”, Ivan Sutherland1996; “Effects of World War II on education in science”, Lord Bowden1975
- “Work hard” & “A Close Call: How a Near Failure Propelled Me to Succeed”, Terence Tao2015/2020
- “Principles of Effective Research”, Michael Nielsen2004
- “Teach Yourself Programming in 10 Years”, Peter Norvig2001; The Mythical Man-Month, Fred Brooks1975
- “The 11 Laws Of Showrunning”, Javier Grillo-Marxuach2016
- “Good and Bad Procrastination”, Paul Graham2005; “How To Do Great Work”2003
- Why Greatness Cannot Be Planned review
- See Also: Log-normal pipelines, small groups, The Media Lab, ARPA, Bakewell & Invention of Breeding
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 [1927–], Vice President, Applied Research, Bell Communications Research.
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 known 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.4 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 7 books and of those 7 books which tell of various areas of mathematics and computers and coding and information theory, 3 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 10 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.
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.5
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.6
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.7 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.”8
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.9 Now that’s the necessary but not sufficient condition. All of these items I will talk about are both luck and not luck.
Brains vs Work. 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.
Pfann’s Progress. 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.10 Certainly he became much more articulate.
Clogston’s Contribution. And I can cite another person in the same way. I trust he isn’t in the audience, i.e. a fellow named [Albert M.] 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.11 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?12
That is the characteristic of great scientists; they have courage. They will go forward under incredible circumstances; they think and continue to think.13
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 3 winners [Shockley, Bardeen, & Brattain] 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.14 [cf. 2015, et al 2023 , et al 2023 .] 15
☞ 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.1617
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.18
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 [ie. not even assembly language]. 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 10 years with John Tukey at Bell Labs. He had tremendous drive. One day about 3 or 4 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.”19 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 10% 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.20 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.21 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.22
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.
What are the most important problems in your field, and why aren’t you working on them?
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.23 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.24 Let me warn you, ‘important problem’ must be phrased carefully. The 3 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.25
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 9⁄10 experiments were done in the lab and one in 10 on the computer. I made a remark to the vice presidents one time, that it would be reversed, i.e. 9⁄10 experiments would be done on the computer and one in 10 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 somewhere 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 closed26. 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.27 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 [Milne’s 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 days28, 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.”29 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 3 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. 3 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.30 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 [Sergei] 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 [the in-house journal Bell Labs Technical Journal] 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.31
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.”32
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 [MIT Lincoln Laboratory?], 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.”33 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.
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!
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 [ie. the main Bell Labs facility] 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.
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 [Ian Ross?] 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 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.
Anger. 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.
Positivity. 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.
Arrogance. 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 innumerable 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 9 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.)
Alan 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.
Richard 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 we’re 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 [assistant vice-president] 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?
R. 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.
Q: 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?
RH: 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.34
It is true, and I can’t do anything about it; I cannot blame the present generation either. It’s just a fact.
Q: Is there something management could or should do?
H: 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!
Q: Is brainstorming a daily process?
H: 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!
- Q: What kind of tradeoffs did you make in allocating your time for reading and writing and actually doing research?
- H: 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.
Q: How much effort should go into library work?
H: 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.
Q: How do you get your name attached to things?
H: 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.
Q: Dick, would you care to comment on the relative effectiveness between giving talks, writing papers, and writing books?
H: 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.
Q: 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?
H: Some things you could do are the following.35 Somewhere around every 7 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 muckety-muck 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 [for MIT, which offered him tenure + a blank check], 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.36
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 7 years, but if you could, I would require a condition for doing research, being that you will change your field of research every 7 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.
Q: Would you compare research and management?
H: 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.
Q: 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?
H: 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.
Q: 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.
H: 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.)
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 30 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 $269584.33217613335$1300001996 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 President 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; 2nd 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; 2nd edition 1983; 3rd edition 1989; translated into several European languages.
- Coding and Information Theory, Prentice-Hall, 1980; 2nd 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 21 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.
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
This annotated web edition is (like the Paul Graham & Sam Altman versions) based on the HTML edition hosted by Gabriel Robins c. August 2002, which may have itself been based on an earlier Bell-originating digital edition given the line “Converted from TROFF to HTML by Chris Lott” (ex-Bell Labs) in some PDF versions (explaining the TeX-like backticks style), but the ultimate transcript was apparently transcribed by James Kaiser sometime before Hamming died 1998-01-07; it appears to have been printed in 1986 by “Bell Communications Research, Inc” (in addition to a 2009 reprint) & that may be the source of this transcription.
The 1986 transcript is the ‘canonical’ version in the sense that it is the most linked, read, & quoted version; having read the others, my opinion is that it is the best version—the other versions are more poorly structured, confusing, and leave out good parts seemingly at random (while, frustratingly for this editor, often throwing in additional historical details as Hamming apparently felt more at liberty to gossip post-1986), and fail to benefit from the 1986 Q&A.
I have updated the HTML typography to benefit from my website features like mobile & dark-mode, added annotated hyperlinks & section headers & anchors (particularly for Bell Labs insider jargon/references), inserted paragraph breaks, and made various minor corrections & changes. A manicule (☞) in the left-margin marks a passage from this talk which is frequently quoted (rather than italicize or bold large paragraphs).
- “Superintendent’s Guest Lecture (SGL)”, 4 April 1990
- Intro: “Learning to Learn”
- “Foundations of the Digital”
- “History of Computers—Hardware”, “Software”, “Applications”
- “Artificial Intelligence—Part I”, “II”, “III”
- “n-Dimensional Space”
- “Coding Theory—The Representation of Information, Part I”, “II”
- “Error-Correcting Codes”
- “Information Theory”
- “Digital Filters, Part I”, “II”, “III”, “IV”
- “Simulation, Part I”, “II”, “III”
- “Fiber Optics”
- “Computer Aided Instruction”
- “Quantum Mechanics”
- “Unreliable Data”
- “Systems Engineering”
- “You Get What You Measure”
- “How Do We Know What We Know”
- “You and Your Research”
Hamming defends his approach of focusing on success case-studies in the 1995 lecture:
There’s one very early problem I solved spectacularly not only from a computing point of view, but from a physics point of view. The value in the transistor research was extremely valuable. I meditated over why that was successful. I studied it over and over again and I believe this statement, “you should study your successes”.
You don’t study your failures. Study successes because when your time comes you will know how to succeed. If you study failures, you’ll know how to fail, so study success very closely. Not only yours, but other people’s. Why did Galileo do what he did? How did Newton do it? Try as best you can to study other people, how they succeed. What were the elements of their success? Which elements of that can you adapt to your personality?
You can’t be everybody but you have to find your own method and studying success is a very good way of forming your own style.
1995 lecture: “But there’s lots of ways luck can hit you. For example, when I went to Bell Laboratories the first few months I was there, Shannon, Miss Sally Mead, and myself shared a very big room in the attic.”↩︎
This quote appears to be apocryphal. It does not sound at all like Isaac Newton, and I am unable to find any original.
This may be a distant descendant of more famous quotes about Newton’s approach to long-term concentration & visualization, eg. his description:
I keep the subject constantly before me, and wait ’till the first dawnings open slowly, by little and little, into a full and clear light.
His peculiar gift was the power of holding continuously in his mind a purely mental problem until he had seen straight through it. I fancy his pre-eminence is due to his muscles of intuition being the strongest and most enduring with which a man has ever been gifted…I believe that Newton could hold a problem in his head for hours and days and weeks until it surrendered to him its secret. Then being a supreme mathematical technician he could dress it up, how you will, for the purposes of exposition, but it was his intuition that was pre-eminently extraordinary.
Many times a discussion with a person who has just done something important will produce a description of how they were led, almost step by step, to the result. It is usually based on things they had done, or intensely thought about, years ago. You succeed because you have prepared yourself with the necessary background long ago, without, of course, knowing then that it would prove to be a necessary step to success.
…Thus, among other things, it was Feynman’s energy and his constantly trying new things that made one think he would succeed.
This trait must be coupled with emotional commitment. Perhaps the ablest mathematician I have watched up close seldom, if ever, seemed to care deeply about the problem he was working on. He has done great deal of first class work, but not of the highest quality. Deep emotional commitment seems to be necessary for success. The reason is obvious. The emotional commitment keeps you thinking about the problem morning, noon and night, and that tends to beat out mere ability.
While I was at Los Alamos after the war, I got to thinking about the famous Buffon needle problem where you can calculate the probability of a needle tossed at random of crossing one of a series of equally-spaced parallel lines. I asked myself if it was essential that the needle be a straight line segment (if I counted multiple crossing)? No. [the “noodle” variant] Need the parallel lines be straight? No. Need they be equally-spaced or is it only the average density of the lines on the plane? [Apparently the latter, see 1978 & 1981: crossing probability = (2×π) ✕ (needle length ∕ average density).]
Is it surprising that some years later at Bell Labs when I was asked by some metallurgists how to measure the amount of grain boundary on some micro photographs, I simply said, “Count the crossings of a random line of fixed length on the picture?”
I was led to it by the previous, careful thought about an interesting, and I thought important, result in probability. The result is not great, but illustrates the mechanisms of preparation and emotional involvement.
So I helped Bill Pfann, taught him how to use the computer, how to get numerical solutions to his problems, and let him have all the machine time he needed.
It turned out zone melting was just what we needed to purify materials for transistors, for example, and has proved to be essential in many areas of work. He ended up with all the prizes in the field, much more articulate as his confidence grew, and the other day I found his old lab is now a part of a National Monument!
Ability comes in many forms, and on the surface the variety is great; below the surface there are many common elements.
Even longer version in 1995 lecture:
He wanted to do Zone Melting. With zone melting you have a bar, and you have a coil round it which you heat by induction to melt the metal. You move it down slowly. If the impurities stay in solution you drag the impurities down. If impurities try to drop out, they’re pushed out the other side. Many, many passes removed the impurities from the middle of bar.
He had some equations. I put some algebra on it and some calculus and got some partial answers but I could see that he needed computing. I went around to his department and asked about him. They didn’t think much of them. I went back to my office. I thought he had a good idea. I had resolved to work with important people. I wanted to do important work, and work with important people. Here was my chance to contribute to a really good idea, if it were good, but his department didn’t think much of him.
…that success with Zone Melting was his one great idea, but it was what Bell Labs needed. We needed to be able to make germanium [silicon transistors came later] without very many impurities. Then we needed to be able to put as many [impurities] as we wanted in [to make semiconductors] because if you now take the same zone and drag it down, you can drag down impurities about the density you want in them. You have remarkable control with zone melting. You make a thousand passes or something—that’s why you can’t do it numerically other than with a computing machine because the thousand passes have end effects and they bounce around.
So, I was right that time. I guessed the man had something important. I worked with him and I was part of something important.
The idea of ‘zone melting’, where one ‘squeezes out’ impurities—as if a big block of germanium or silicon were a toothpaste tube, and one just does it as many thousands of times as necessary—strikes me as a good example of “courage”.↩︎
NAS: “During his time in the electronics area Al acquired several patents on electronic devices, but his major contribution there was the “Clogston cable”, which had a laminated central conductor that much reduced microwave system losses. On the strength of this achievement Al was promoted to department head, and in 1953, in their search for managers knowledgeable in quantum physics, the Bell leadership appointed him department head in the burgeoning area of quantum solid-state physics.” (eg. 1953, 1952a/1952b)↩︎
The 1993 version includes another Shannon anecdote:
Courage is another attribute of those who do great things. Shannon is a good example. For some time he would come to work at about 10:00am, play chess until about 2:00pm and go home.
The important point is how he played chess. When attacked he seldom, if ever, defended his position, rather he attacked back. Such a method of playing soon produces a very interrelated board. He would then pause a bit, think and advance his queen saying, “I ain’t afraid of nothin’.” It took me a while to realize that of course that is why he was able to prove the existence of good coding methods. Who but Shannon would think to average over all random codes and expect to find that the average was close to ideal? I learned from him to say the same to myself when stuck, and on some occasions his approach enabled me to get significant results.
Without courage you are unlikely to attack important problems with any persistence, and hence not likely to do important things. Courage brings self-confidence, an essential feature of doing difficult things. However, it can border on over-confidence at time which is more of a hindrance than a help.
Now I’ll tell you another story. For about a year, he [Claude Shannon] came in about ten o’clock, played chess till about 2:00, and went home. At the end of year, the company gave him a salary raise. That’s all you could see he was doing, but at home he was creating information theory. The way he played chess, is the following…
When you get attacked in chess you could either defend yourself or you attack back. Shannon never defended himself. He attacked back. And the game would get tied up more, more, more, and more complex. Finally he would stop and think for a long while, grab his Queen, and say, “I ain’t scared nuthin”. Bing. The whole game would collapse then because he finally precipitated all pending operations and either won or lost. I learned that expression, “I ain’t scared of nothing.” I’ve used this several times on myself, when I was stuck and I didn’t know what on earth to do. I said it’s good for Shannon, it’s good enough for Hamming. “I ain’t scared of nothing, let’s go ahead and see what happens.” Sometimes by copying his style I came through to success. I deliberately copied his style.
And on Hamming himself (2011):
“I always remember, he would come into my office and try to solve a problem”, said [Bruce MacLennan, who was also a professor at NPS when Hamming was there]. “I had a very big blackboard, and he’d start on one side, write down some integral, say, ‘I ain’t afraid of nothin’’, and start working on it. So, now, when I start a big problem, I say, ‘I ain’t afraid of nothin’’, and dive into it.”
The desire for excellence is an essential feature for doing great work. Without such a goal you will tend to wander like a drunken sailor. The sailor takes one step in one direction and the next in some independent direction. As a result the steps tend to cancel each other, and the expected distance from the starting point is proportional to the square root of the number of steps taken. With a vision of excellence, and with the goal of doing significant work, there is tendency for the steps to go in the same direction and thus go a distance proportional to the number of steps taken, which in a lifetime is a large number indeed. As noted before, Chapter 1, the difference between having a vision and not having a vision, is almost everything, and doing excellent work provides a goal which is steady in this world of constant change.
The prior note:
It’s been pointed out that the October 1956 co-winner John Bardeen would win a Nobel Prize again for his research on superconductivity; on the gripping hand, however, the superconductivity research in question, BCS theory, was published in April 1957 & was completed before 18 February 1957. 5 years on, as Nobel laureate, He would signally misstep in trying to squash the Josephson effect (1973 Physics Nobel Prize).↩︎
You’ll have to get a wide feeling for what is going on and the supreme example of this [door] closure is the Institute for Advanced Study in Princeton. They take in people who’ve done something great, they give them the luxury of a beautiful office, a beautiful restaurant to dine in, wonderful grounds and everything else. They have adequate salary to live on. No cares, no worries, no nothing. You’re freed for life of anything at all. What happens? The bulk of them continue working on the problem they made that made them famous. They keep on elaborating on that. They’ve already made it famous. It doesn’t need to be added to. They got the thing going. Rarely do they change.
von Neumann was different. He was at the Institute and he did go out in reality. He turned up in Washington and in other places. He traveled widely and was receptive of new ideas. But the bulk of the people got to a point the Institute for Advanced Study don’t keep the door open on life as it were. They don’t do anything comparable to what they had done before. They are very able people but the Institute in my opinion sterilized them a great extent. So what you think are the ideal working conditions, are not.
Other criticisms include J. Robert Oppenheimer (letter to Frank Oppenheimer, 1935-01-11, pg 190–192 of Robert Oppenheimer: Letters and Recollections 1980):
I had a good day at Columbia, but was glad, after talking with him, that you were not committed to Dunning—not a bad egg, but you would not like him. [John R. Dunning was an instructor in physics at Columbia.] Bacher went down & back with me to Princeton, kept talking of the Picasso. Princeton is a madhouse: its solipsistic luminaries shining in separate & helpless desolation. Einstein is completely cuckoo; Dirac was still in Georgia [on vacation?]. I could be of absolutely no use at such a place, but it took a lot of conversation & arm waving to get Weyl to take a no.
…Asked years later to comment on the description of Princeton and its solipsistic luminaries, Frank Oppenheimer smiled. “It’s a kind of youthful cockiness”, he said, “and some of it stayed with my brother a little longer than it should have.” [interview with Frank Oppenheimer, April 14, 1976 [by Alice Kimball Smith & Charles Weiner]] Robert [Oppenheimer] expressed a more considered view in a 1939 radio talk celebrating Einstein’s 60th birthday, lauding his contributions to science and “those personal qualities that are the counterpart of great work: selflessness, humor, and a deep kindness.”38
Richard Feynman (his Surely You’re Joking, Mr. Feynman! draws its title from a stuffy Princeton don) where in “Part 4: From Cornell to Caltech, With a Touch of Brazil”, he writes (in part to explain why he turned down a second IAS offer):
The Dignified Professor: I don’t believe I can really do without teaching. The reason is, I have to have something so that when I don’t have any ideas and I’m not getting anywhere I can say to myself, “At least I’m living; at least I’m doing something; I’m making some contribution”–it’s just psychological.
When I was at Princeton in the 1940s I could see what happened to those great minds at the Institute for Advanced Study, who had been specially selected for their tremendous brains and were now given this opportunity to sit in this lovely house by the woods there, with no classes to teach, with no obligations whatsoever. These poor bastards could now sit and think clearly all by themselves, OK? So they don’t get any ideas for a while: They have every opportunity to do something, and they’re not getting any ideas. I believe that in a situation like this a kind of guilt or depression worms inside of you, and you begin to worry about not getting any ideas. And nothing happens. Still no ideas come.
Nothing happens because there’s not enough real activity and challenge: You’re not in contact with the experimental guys. You don’t have to think how to answer questions from the students. Nothing!…The questions of the students are often the source of new research.
With his lack of a PhD and his disdain for a system that forces both students and professors to spend years working on a problem, Dyson the frog clearly realized that he wasn’t suited to a conventional academic career. But it also made him reassess what his particular strengths were. His great accomplishment had given him an enviable lifetime appointment at the Institute for Advanced Study in Princeton; Robert Oppenheimer who was the director had himself sung Dyson’s praises.
For the next seven decades Dyson would become one of the most famous residents of the institute, but even his home institution was not spared from his contrarian take. He always thought the institute was too ivory tower and too much like an alien transplant in America—in contrast Ithaca and Cornell where he had lived before were the real American deal. He also disdained the tribalism among the institute’s mathematicians and their successful efforts to shut down John von Neumann’s computer project, a project which if it had been supported would have put the IAS on the map in the annals of modern computing.
This is much-quoted but I wonder if it is correct.
The IAS by design recruited the most eminent & famous scientists it could like Einstein or Godel—how much of this is just regression to the mean? And is this more about physics than other fields like math?↩︎
See also the MIT Radiation Laboratory, which was also infamously shack-like (but this has been credited as part of why it worked so well, in a version of How Buildings Learn—no one cared how they messed around with the building).↩︎
The 1995 lecture is more specific about the hard work:
…When I was home I thought, “Frankly I am not working really as hard as I could. I’ll never be able to work as hard as John does. I haven’t got the psychic energy, but I can work a hell of a lot harder than I have been. Let me reorganize my life. Let me quit spending my time and reading nonsense magazines and thumbing through newspapers. They’re not very important to my career; let’s spend my time studying things in my career.
For example, I got appointed very deliberately as a book review editor. There’s always a book on my coffee table waiting to be read and reviewed. When a review is written by me, I set it aside for about a week and ask myself afterwards, is that a good review? Does that really digest the book? If it doesn’t, you’re rereading the book or writing a better review.
This way I forced myself to get a lot wider acquaintance in computer science. Being a book review editor, I got to review the books I wanted. This was a device. Now it’s true I quit reading The New Yorker. I quit reading magazines. My wife complained occasionally that all I looked in at The New Yorker were the jokes. She was right. I didn’t have time to do everything. I wasn’t a first-class genius. I had to work hard. So I simply set aside other things and did that. It’s not hard to do. You just do it.
I had, also, during many years followed a golden rule, namely, that whenever a published fact, a new observation or thought came across me, which was opposed to my general results, to make a memorandum of it without fail and at once; for I had found by experience that such facts and thoughts were far more apt to escape from the memory than favourable ones. Owing to this habit, very few objections were raised against my views which I had not at least noticed and attempted to answer.
The later 1995 lecture offers a ruder account of “wasn’t learning much”:
Another example, I hope most [of these] people are dead, I guess they aren’t but they probably won’t hear this. I was in a math department and we used to go to lunch together. They played games, threw boomerangs, flew kites, and played this-and-that and they’d fiddle around.
I wanted to succeed, and I said to myself, “I can’t afford to waste lunch time”, so I went around to the physics table where I’d written a paper with one of the physicists [on nuclear magnetic resonance] and asked if I could join them.
When you’re learning things, I told you that you need to put hooks on ideas so they can be recovered widely. That was the thing that John Tukey could do and I couldn’t for so long. He could dredge up almost any kind of information. After he told me, I could see the what he said was true but I couldn’t think of it first. So I started doing what he did. When I got new piece of information, I turned it around many ways until it was connected with many pieces of information so that in various situations that idea would become available, and it has worked out fairly well.
You’re likely to saying to yourself, “you haven’t got the freedom to work.” I didn’t either when I began. I had to do more with less respect. When you hire a plumber to fix the plumbing, you expect them to be already trained. You expect them to be able. You don’t give a person a big lovely chance to do something great when they have not already demonstrated greatness. The onus is on you to demonstrate greatness and then you’ll get the opportunities. It’s not the other way around. It was beautifully put by an instructor when I was at Nebraska: the instructor went to the head of the Department and said “I want to be relieved of some teaching so I can do some research.” The Department head said, “when you’ve done the research, I’ll relieve you of the teaching.” You have to demonstrate your ability first and then you’ll have the freedom to do it. Otherwise, no—I had to do error correcting codes at home on my own time.
After I became more able, management left me alone. In fact, the management clearly had to believe the more we left Hamming alone the more he’d worry about what should be done, the more likely he’s going to do the right thing. That applied to a guy like Hamming who had a conscience and was worried. It doesn’t apply to some people. Some people, you give them freedom, they’ll do nothing. But I was compulsive and I was worried about doing a great job, so I did.
You are aware that frequently more than one person starts working on the same problem at about the same time. In biology, both Darwin and Wallace had the idea of evolution at about the same time. In the area of special relativity, many people besides Einstein were working on it, including Poincaré. However, Einstein worked on the idea in the right way.
The first person to produce definitive results generally gets all the credit. Those who come in second are soon forgotten. Thus working on the problem at the right time is essential. Einstein tried to find a unified theory, spent most of his later life on it, and died in a hospital still working on it with no significant results. Apparently, he attacked the problem too early, or perhaps it was the wrong problem.
There are a pair of errors that are often made when working on what you think is the right problem at the right time. One is to give up too soon, and the other is to persist and never get any results. The second is quite common. Obviously, if you start on a wrong problem and refuse to give up, you are automatically condemned to waste the rest of your life (see Einstein above). Knowing when you persist is not easy—if you are wrong then you are stubborn; but if you turn out to be right, then you are strong willed.
Another example is slightly different. When I was doing this 28 simultaneous [first order differential] equation I told you about the Navy intercept plane, I was solving it on a digital machine because the analog machine outside of Philadelphia couldn’t do the job. No analogue machine at that time could do it because they didn’t have the required accuracy.
I was using a variation of Milne’s method which was pretty crummy. I’d found Milne’s method was unstable and had patched it up a little bit. One day I realized I was going to have to fill in a report of what I did because government contracts always require reports. Everybody who had analog computers was going to try and pick flaws and what I did because I was really showing that a digital machine could beat the analog on his own home ground. That’s really what I was doing, not getting the answer a problem. I was really demonstrating something much more important.
I promptly started deriving a better method of integrating the differential equations. I finally used a method which for some years was known as “Hamming’s method”. I don’t recommend it now but it was very suitable for the machines as they were.
So I had the girl programmer change a few of the instructions, run a trajectory once more to check the new program got the same as the old answers, and then went ahead. Thus, this report has a very jazzy method of solving differential equation instead of a very crummy method. Both are equally effective, but one was defensible and one was not.
I changed the nature of the problem. I saw that the problem although originally was, “Get the answers of these trajectories.” In fact, it was something else. It was proving that a digital machine could beat the analog machine on its own home ground of differential equations. I redefined the problem and made it a success.
I would not have found the Hamming method if I had not realized that the method I was using which was adequate for me and we were all going to see if we’re getting right answer, but it was not nice. It was not clean and as simple. It was rather ugly. So I changed the problem.
…Bell Labs believed that time-shared computing was the future. A project was initiated to create a time-shared computer facility with terminals in laboratories. It was believed that IBM was not up to the challenge, and therefore a project, named MULTICS (Multiplexed Information and Computing Service), was initiated, with GE to supply the computer hardware (GE 645), MIT the system software, and BTL [Bell Telephone Laboratories] the systems integration. The MULTICS project was initiated around 1964. Although GE had not up-to-then made a large mainframe machine, it did deliver its GE-645 to Bell Labs as a replacement for the IBM 7094.
It became apparent that the system overhead for time-shared computing was substantial, and the project seemed doomed to failure. BTL abandoned its involvement around 1969. IBM then supplied its IBM-360 mainframe computer to BTL to replace the GE machine. The failure of MULTICS ultimately led to Unix and C. I recall the software researchers working in the attic of Building 2 on what would become the Unix operating system—from failure came a great success. The Executive Director of computing research was Edward E. David Junior In 1970, he left BTL to become Science Advisor to President Nixon. I would leave Bell Labs to join his staff in mid-1971.
My department head, Peter B. Denes, wisely doubted that a single central computer would be able to serve hundreds of research labs. Around 1965, he therefore obtained his own dedicated laboratory computer; initially a DDP-124 that was then upgraded to a DDP-224 (initially made by the Computer Control Company and later Honeywell). The computer system was primarily used for speech research, but was also used for computer music by Max V. Mathews and various visiting composers, such as Emmanuel Ghent and Laurie Spiegel. The lab in which it was used had a raised floor for all the cables. There was a large hard disk drive with removable disk packs; a head crash was a disaster, destroying the disks and generating a horrible screech and odor.
Again, you should do your job in such a fashion others can build on top of it. Do not in the process try to make yourself indispensable; if you do then you cannot be promoted because you will be the only one who can do what you are now doing! I have seen a number of times where this clinging to the exclusive rights to the idea has in the long run done much harm to the individual and to the organization. If you are to get recognition then others must use your results, adopt, adapt, extend, and elaborate them, and in the process give you credit for it. I have long held the attitude of telling every one freely of my ideas, and in my long career I have had only one important idea “stolen” by another person. I have found people are remarkably honest if you are in your turn.
1995 lecture expansion:
Well, let me come down now to a saying of Socrates, who lived about 470–399 BC and in Greece. He said, “the unexamined life is not worth living.” I heard it while I was crossed first time I heard while crossing the campus at Yale behind a professor and a student, before we could turn, the student again said “the unexamined life is not worth living.”, and before we crossed the whole quad, he recited three times “the unexamined life is not worth living”.
You should examine your life. You’ve only got one life to lead as far as any of us know. Why shouldn’t it be the life you want to have instead of whatever happens to you? To come down the back end and say, “Well, I didn’t do any harm, I had an enjoyable life”—is that what you want to say your old age? You just had a good time in life? Or do you want to say, you know, “I did something was important at least something that I thought was important.”
That’s your problem therefore, to pick these things up and do it, if you want to have a happy life in the back end.
Cf. Simonton and meta-science on adjacent field switches for late-career productivity.↩︎
I agree: Shannon did his best work when forced to publish, and tenure simply freed him to not publish anything (even though he had a great deal of interesting things he could’ve published, and some trickled out anyway).↩︎