Hauke Hillebrandt

Mar 2021 · Summaries

You and Your Research

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Richard Hamming gave a talk once titled 'You and your research'. I've summarized the talk transcript, (actual talk on youtube). There's also a new more extensive book by Hamming: 'The Art of Doing Science and Engineering: Learning to Learn'

Tl;dr from Ten Simple Rules for Doing Your Best Research, According to Hamming:

Rule 1: Drop Modesty

Rule 2: Prepare Your Mind

Rule 3: Age Is Important

Rule 4: Brains Are Not Enough, You Also Need Courage

Rule 5: Make the Best of Your Working Conditions

Rule 6: Work Hard and Effectively

Rule 7: Believe and Doubt Your Hypothesis at the Same Time

Rule 8: Work on the Important Problems in Your Field

Rule 9: Be Committed to Your Problem

Rule 10: Leave Your Door Open

The title of this talk is 'You and your research' but it could also be called 'You and your engineering career'. This talk is about broad principles of career success.

This talk is not about managing research, it is about how you individually do your research.

I'm not talking about ordinary, but great, Nobel-Prize type of research (or at least things very significant research) like Shannon's information theory.

At Los Alamos and Bell Labs, I worked with famous, highly- capable scientists like I Feynman, Fermi, Teller, and Shannon. I wanted to find out why they were so good. I read biographies and asked researchers questions like: 'How did you come to do this?'' I tried to find out how they are different.

First, it's important you do significant things, because you only have one life. This applies to many fields.

You must drop modesty, defy societal norms and tell yourself 'I want to do something significant. I want to first-class work.'' Our society frowns on this. You're supposed to do great things by chance. But you should intentionally set out to do something significant.

People think great science is done by luck. But very many scientists, like Einstein and Shannon, have repeatedly done great science.

'Luck favors the prepared mind.'' There is indeed an element of luck, but the prepared mind sooner or later finds something important and does it. For example, when I came to Bell Labs, I was lucky to share an office with Shannon. Newton said, 'If others would think as hard as I did, then they would get similar results.''

Generally, great scientists have independent thoughts and the courage to pursue them. For example, a young Einstein asked himself 'What would a light wave look like if I went with the velocity of light to look at it?''. Is it luck that he finally created special relativity? No. Early on, he had laid down some of the pieces by thinking of the fragments. Now that's the necessary but not sufficient condition.

How about having a high IQ? It sounds plausible at first. Most physicists have a high IQ. But great work needs more than mere brains. For example, I helped one not very raw smart, but highly motivated non-physicist with the math of his problem and with a little help he did great work. I met another guy who initially didn't seem that smart but then he made a good invention, which gave him confidence and then he had a steady stream of good ideas.

You really need to have courage. Once you believe that you can do important problems, then you can. If you think you can't, almost surely you are not going to. Courage is one of the things that Shannon had supremely. You have only to think of his major theorem. He wants to create a method of coding, but he doesn't know what to do so he makes a random code. Then he is stuck. And then he asks the impossible question, 'What would the average random code do?'' He then proves that the average code is arbitrarily good, and that therefore there must be at least one good code. Who but a man of infinite courage could have dared to think those thoughts? That is the characteristic of great scientists; they have courage. They will go forward under incredible circumstances; they think and continue to think.

Age is another factor. Physicists often do their best work when they are young in their 20s. Perhaps it's because if academics do good work when younger, they're increasingly burdened with administrative work. In contrast, in the humanities, people usually do their best work at an older age.

When you are famous it is hard to work on small problems. This is what Shannon did. After information theory, what do you do for an encore? The great scientists often make this error. They fail to continue to plant the little acorns from which the mighty oak trees grow. They try to get the big thing right off. And that isn't the way things go. So that is another reason why you find that when you get early recognition it seems to sterilize you. In fact I will give you my favorite quotation of many years. The Institute for Advanced Study in Princeton, in my opinion, has ruined more good scientists than any institution has created, judged by what they did before they came and judged by what they did after. Not that they weren't good afterwards, but they were superb before they got there and were only good afterwards.

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

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

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

Now for the matter of drive. You observe that most great scientists have tremendous drive. I worked for ten years with John Tukey at Bell Labs. He had tremendous drive. One day about three or four years after I joined, I discovered that John Tukey was slightly younger than I was. John was a genius and I clearly was not. Well I went storming into Bode's office and said, 'How can anybody my age know as much as John Tukey does?'' He grinned slightly, and said, 'You would be surprised Hamming, how much you would know if you worked as hard as he did that many years.'' I simply slunk out of the office!

What Bode meant was: 'Knowledge and productivity are like compound interest.'' Given two people of approximately the same ability and one person who works ten percent more than the other, the latter will more than twice outproduce the former. The more you know, the more you learn; the more you learn, the more you can do; the more you can do, the more the opportunity- it is very much like compound interest. I don't want to give you a rate, but it is a very high rate. Given two people with exactly the same ability, the one person who manages day in and day out to get in one more hour of thinking will be tremendously more productive over a lifetime. I took Bode's remark to heart; I spent a good deal more of my time for some years trying to work a bit harder and found I could get more work done. I neglected my private life sometimes; I needed to study. You definitely have to neglect things if you intend to get what you want done.

'Genius is 99% perspiration and 1% inspiration.'' This might be exaggerated, 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 that he needed to write down every piece of evidence that contradicted his beliefs or else he'd forget them. When you find apparent flaws you have to be sensitive, keep track of them, and watch 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.

You need commitment, but it's not enough. Why? Those who have studied creativity say that it suddenly appears out of your subconscious. We know little about the subconscious; but we know that your dreams come from it, which rework the experiences of the day. If you are deeply immersed and committed to a topic, day after day, your subconscious will work on it. And so you wake up one morning, and there's the answer. If you're not committed to your current problem, the subconscious goofs off on other things and doesn't deliver. To manage yourself, don't let anything but your important problem get the center of your attention- keep your thoughts on the problem. Starve your subconscious so it has to work on your problem, and get the answer after a good night's sleep for free.

I used to eat lunch with mathematicians, but I already knew a lot of mathematics and so I wasn't learning much. I then switched and ate at the physics table, which was an exciting place, but I didn't contribute much, but I was learning a lot listening to great physicists. But when they became famous and won Nobels, there was no use eating with them.

So I started eating with the chemists.

There I started asking the 'Hamming questions':

I wasn't welcomed after that and had to find somebody else to eat with. But later one of them said 'Your questions got under my skin and I thought a lot about them. I haven't changed my research but it was well worthwhile.'' This person became very successful, unlike others at that table, who couldn't ask themselves those questions.

If you don't work on an important problem, it's unlikely you'll do important work. Great scientists have carefully thought through many important problems in their field, and how to attack them. By important I mean guaranteed a Nobel and any sum of money. The three outstanding problems in physics, we didn't work on were time travel, teleportation, and antigravity. They are not important problems because we do not have an attack. It's not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important. When I say that most scientists don't work on important problems, I mean it in that sense. The average scientist spends almost all their time working on problems which they themself believe won't be important and they also don't believe that they will lead to important problems.

You need to plant acorns to grow oaks. 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. If you want to do great work, you clearly must work on important problems, and you should have an idea.

I've adopted what I called 'Great Thoughts Time.'' After Friday noon, I only discuss great thoughts like: 'What will be the role of computers in all of AT&T?'', 'How will computers change science?'' For example, I came up with the observation at that time that nine out of ten experiments were done in the lab and one in ten on the computer. I thought that it would be reversed, i.e. most experiments would be done on the computer. People thought I was a crazy out of touch mathematician. But I knew they were wrong and they've been proved wrong. They built labs when they didn't need them. I saw that computers were transforming science because I kept 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 that more than one-half of the people at Bell Labs will be interacting closely with computers soon. 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.

Most great scientists know many important problems. They have something between 10 and 20 important problems for which they are looking for an attack. And when they see a new idea come up, they say 'Well that bears on this problem.'' They drop everything and get after it. I once talked to a friend from Los Alamos about how it was lucky that the fission experiment occurred in Europe when it did because that got the US working on the atomic bomb. 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 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. Often it doesn't work out, but you don't have to hit many of them to do some great science. One of the chief tricks is to live long!

Another important and subtle trait. Some people work with the door open or the door closed. If you close your door, you get more done today, and are more productive than most. But in the long-run, you don't quite know what problems are worth working on; all the hard work you do is sort of tangential in importance. If you work with the door open, you get all kinds of interruptions, but also occasionally you get clues as to what the world is and what might be important. Maybe this is effect is correlational and those who close the door are more closed minded. But the correlation is strong 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.

Another thing: 'It ain't what you do, it's the way that you do it.'' For instance, I was once conned into doing on a digital computer, a problem which analog computers couldn't do. And I was getting an answer. But I knew I had to file a report on this military job; after I spent a lot of money on it and I have to account for it and every analog installation will try to find flaws in the report. I was using a poor method, but I was getting the answer. But the problem was not just to get the answer; it was to prove that the digital computer could beat the analog computer. So I reworked the method, created an elegant theory, and changed how we computed the answer; the results were no different. The published report had an elegant method which was later known for years, and so by changing the problem slightly, I did important rather than trivial work.

Similarly, when I first started using the digital computer, I solved one problem after another after another, I had many successes and few failures. But I was still dissatisfied. I could see life being a endless sequence of problems. I concluded that 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 me.' 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: '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 so that others can build on top of it, so they will indeed say, 'Yes, I've stood on so and so's shoulders and I saw further.'' The essence of science is cumulative. By changing a problem slightly you can often do great work rather than merely good work. Instead of attacking isolated problems, I resolved to never again solve an isolated problem except as characteristic of a class.

Mathematicians 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.

Finally: '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 so that people can indeed build on what you've done, or so 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 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!

Unfortunately, it is not sufficient to do a job, you have to sell it. Scientist find 'selling' awkward and ugly. The world is supposed to be waiting, and when you do something great, they should rush out and welcome it. But everyone is busy. You must present it so well that they read and appreciate it. When browsing, why do you read some articles and not others? You had better write your report so when it is published in journal or elsewhere, readers will stop and read yours, or you won't get credit.

There are three things you have to do in selling:

  1. Learn to write clearly and well so that people will read it
  2. Learn to give reasonably formal talks
  3. Learn to give informal talks (There are many 'back room scientists'' who keep quiet during discussions. They file reports arguing with a decision after it's already been made, but that's too late. They would not stand up during heated discussion and join the debate and state their reasons. You need to master that form of communication as well as prepared speeches.)

I was very nervous when I first had to give speeches. I realized I either had to learn to give speeches smoothly or partially cripple my career. The first time IBM asked me to give a speech, I decided 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, and I offered to give more. As a result, I got more 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.

Why are only a few presentations remembered? The technical person wants to give a highly limited technical talk. But generally, the audience wants a broad general talk, more survey and background than the speaker is willing to give. And so, many talks are ineffective. Speakers often get lost in the details, and most of the audience can't follow. You should paint a general picture to say why the topic is important, and then slowly give a sketch of what was done. Then more people will know and understand what you've done. People tend to give a highly restricted, safe talk; this is usually ineffective. Furthermore, many talks are filled with far too much information.

Let me summarize:

When you start out you might not have much control over what work on. But once you're moderately successful, there are more people asking for results than you can deliver and you have choice, but not completely.

Educate your boss. I once had someone from the military demand some answers by Friday. But I already had other urgent important tasks and commitments. I said 'No, I can't do it now, but I'll do it over the weekend. '' The military guy complains to my boss who then tells me to prioritize it. I said, fine but the military guy is lazy and won't work over the weekend anyway and so he doesn't need it by Friday afternoon. When this turned out to be true, from then on, my boss let me set my own deadlines.

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 compute. I wanted instead to use compute for a large number of small problems. Back then, we had limited compute and the dogma was 'mathematicians don't need compute.'' But I needed more compute. So every time scientists complained because I rejected their requests for lack of compute, I told 'Go tell your manager that I need more compute.'' After a while I could see what was happening up there at the top: other managers told my boss 'Your man needs more compute.'' I got it!

Secondly, when I loaned what little compute we had then, I stipulated that when you publish, you must acknowledge the hard work of our programmers. After a couple of years, I then went through a year of all articles published at Bells and counted what fraction thanked some programmer. I took it to my 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.

Is the effort to be a great scientist worth it? When you ask people this and get beyond their modesty, most will say that it is as good as wine, love and art 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. It's worth the struggle to try and do great work because, the value is in the struggle more than it is in the result. The struggle to make something of yourself is worthwhile in itself. Success and fame are sort of dividends.

I've told you how to do it. If it's is so easy, why do so many talented people fail? For example, many mathematicians were far more able and better endowed than I, but didn't produce as much. Some of them did produce more than I did; and some others produced a lot, but I was highly productive against a lot of others who were better equipped. Why? What happened to them? Why do so many of the people who have great promise, fail?

Well, one of the reasons is drive and commitment. The people who do great work with less ability but who are committed to it, get more done than those who have great skill and dabble in it, who work during the day and go home and do other things and come back and work the next day. They don't have the deep commitment that is apparently necessary for really first-class work. Good, very talented people, almost always turn out good work. But not first-class, Nobel calibre type work, which is different.

Secondly, there is the problem of personality defects.

  1. Wanting total control. Here's a lesson from someone with a promising career who was head of a computing center and he was temporarily on assignment as a special assistant to the president of the university.

But he showed me how he managed his mail and pointed out how inefficient the secretary was. He wrote mail himself and bragged how he could get so much more work done without the secretary's interference. But the secretary said he didn't delegate properly and didn't have a good system that would allow her to help him. If you don't delegate and do everything yourself, you can go just that far and no farther. If you learn to work with the system, you can go as far as the system will support you. And, he never went any further, because he had his personality defect of wanting total control, unwilling to recognize that you need the support of the system.

This is common. Good scientists fight the system rather than learn to work within it 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', just go to your boss and get a 'No'. If you want to do something, don't ask, do it. Present your boss with an accomplished fact. Don't give your boss a chance to tell you 'No'

  1. Ego assertion. When I moved to Los Alamos Labs from New York at IBM, I was treated unfairly in terms of getting compute. It came down simply to being overdressed. I had to decide whether to assert my ego and dress the way I wanted and have it negatively affect my professional life, or to conform. I made an effort to conform and dress properly, and was treated fairly as a result. Dress according to the expectations. If I go back to the east coast to give a talk at MIT, I dress more formally. I know enough not to let my clothes, my appearance, my manners get in the way of what I care about. Many 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.

Even if you're really good, if you dress too casually, others will take a longer to realize this and you have to overcome this kind of hostility. It's wasted effort! I didn't say you should conform; I said 'The appearance of conforming gets you a long way.'' If you assert your ego in any number of ways and always do it your way, you pay a small steady price throughout your career, which adds up to an enormous amount of needless trouble. John Tukey paid a terrible price needlessly. He was a genius anyhow, but would have been far better, and far simpler, had he been willing to conform a little bit instead of ego asserting. He always dressed how he wanted and never conformed. People will continue to fight the system. Not that you shouldn't occasionally!

Take time to be nice and friendly to superordinates, and it'll pay off. By realizing you have to use the system and studying how to get it 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 your whole life. Successful people often know when to give in and not fight red-tape. I am not saying you shouldn't make gestures of reform, but able people 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. Don't expend energy in a foolish project. Yes, somebody has to change the system. But who do you want to be: The person who changes the system or the person who does first-class science? When you fight the system, be clear what you are doing, how far to go out of amusement, and how much to waste your effort fighting the system. Let somebody else do it and 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. Sometimes a certain amount of rebellion is sensible. 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 their quirks in other places make them pay a far higher price than is necessary for the ego satisfaction they get. I'm not against all ego assertion; I'm against some.

  1. 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.

Look for the positive side of things instead of the negative. For example, I am egotistical. 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! I'd have been ashamed to come back without it! I used my ego to make myself behave the way I wanted to. I bragged about something so I'd have to perform. I found out many times, like a cornered rat in a real trap, I was surprisingly capable. I have found that it paid to say, 'Oh yes, I'll get the answer for you Tuesday,'' not having any idea how to do it. By Sunday night I was really hard thinking on how I was going to deliver by Tuesday. I often put my pride on the line and sometimes I failed, I'm surprised how often I did a good job. Learn to use yourself. Know how to convert a situation from one view to another which would increase the chance of success.

Self-delusion is very common. There are enumerable ways of you changing a thing and kidding yourself and making it look some other way. Why didn't you do X? There are a thousand alibis. If you look at the history of science, usually nowadays there are 10 people close to an important discovery, but the first gets all the glory. The other nine say they had the same idea but didn't do and make excuses. Don't try and kid yourself. You can tell other people all the alibis you want. 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. 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 sum, some of the reasons why so many people who have greatness within their grasp don't succeed are:

  1. They don't work on important problems
  2. They don't become emotionally involved
  3. They don't try and change what is difficult to some other situation which is easily done but is still important
  4. They keep giving themselves alibis why they don't.
  5. 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!

Unedited: DISCUSSION- QUESTIONS AND ANSWERS

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

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

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

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

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

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

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

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

Question: Is there something management could or should do?

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

Question: Is brainstorming a daily process?

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

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

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

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

Question: How much effort should go into library work?

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

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

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

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

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

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

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

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

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

Question: Would you compare research and management?

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

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

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

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

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