Kaiser, J. F. “Richard Hamming: You and your research.” Simula Research Laboratory (2010): 37-60.

This talk was given by Dr. Richard W. Hamming at Morris Research and Engineering Center on March 7, 1986 as a part of the Bell Communications Research Colloquium Series. The talk is also available here.

Synopsis

This talk is not about managing research, it is about how we individually do our (ground breaking) research such as, Relativity or Shannon’s information theory. After the war (WWII) Hamming went on to work at Bell Labs. He was also a member of the Manhattan Project at Los Alamos where he worked up close with Feynman, Fermi, Teller, Oppenheimer and Bethe (his boss) and observed the difference between “people who do and those who might have done”.

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. Before Relativity and Information Theory, both Einstein and Shannon did many great works, which are still looked into. Greatness wasn’t luck, rather there is a repetition pattern.

The prepared mind sooner or later finds something important and does it. It is luck that the mind landed on a particular topic to work, but that the person was able to accomplish something in that topic is not luck. 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. The ground work is laid down initially by curiosity, thinking hard and thinking of the fragment, which lays down the ground work. This is a necessary but not a sufficient condition. 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?.”

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. They will go forward under incredible circumstances; they think and continue to think.

Age is another factor which the physicists particularly worry about. They always are saying that you have got to do it when you are young or you will never do it (which is aparantly true for most physicists, mathematicians etc.) but the reason is that after doing great work they will find themselves on all kinds of committees and would be unable to do any more work. Like, Walter Brattain, after winning the Nobel Prize was practically with tears in his eyes, and he 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.” But in a few weeks it was affecting him. And now he could only work on great problems.

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. ~ Hamming.

Good 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. Adversitives would allow you to think differently and innovatively - new ideas are born and often just by change of viewpoint, turns out to be one of the greatest assets you can have.

One of the better times of the Cambridge Physical Laboratories was when they had practically shacks - they did some of the best physics ever.

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. The ones (problems) you want aren’t always the best ones for you.

John (Tukey) was a genius and I (Hamming) clearly was not. Well I went storming into Bode’s office and said, “How can anybody my age know as much as John Tukey does?” He leaned back in his chair, put his hands behind his head, grinned slightly, and said, “You would be surprised Hamming, how much you would know if you worked as hard as he did that many years.” I simply slunk out of the office!

Bode said, “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.” You have to neglect things if you intend to get what you want done. There’s no question about this.

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. 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. It comes down to an emotional commitment.

On Creativity They say, “creativity comes out of your subconscious.” Somehow, suddenly, there it is. It just appears. 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. Keep your subconscious starved so it has to work on your problem, so you can sleep peacefully and get the answer in the morning, for free!.

Many a times, people fail to ask themselves or maybe they are unable to, “What are the important problems in my field?” 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 working on it?. 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.

Which problem is important? 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. In physics, Anti-gravity, Teleportation and Time-travel are outstanding problems, but they are not important because there is no attack on them. How to identify them? You can’t always know exactly where to be, but you can keep active in places where something might happen. It begins by thinking hard about where was your field is going, and where are the opportunities, and what were the important things to do. You should say, “Let me go there so there is a chance I can do important things”. If you want to do great work, you clearly must work on important problems, and you should have an idea.

Too early/Too Late?

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.

Open Door/Closed Door policy: In Hamming’s opinion, 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. 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.

Mundane Work: Sometimes, a rather mundane task may fall upon your lap which would require you to do uninspiring work. But think about it like this, you will have to do the work, would have to file report and follow the due process. But think about the origin of the problem and try to question it’s relevance: by changing the problem slightly, you can do important work rather than trivial work. That was the case with Hamming who’s mundane work, but changing this thought point led to his significant work “Hamming’s Method of Integrating Differential Equations”.

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

“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.

Selling your work: Your report should reflect the ingeneuiness so that as the readers are turning the pages of the journal, 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. 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. You should not be the back room scientists who keep quiet in the conference, they should be prepared and have to master this form of communication. Practice giving talks, if you don’t, it could essentially affect your career.

Why some papers are remembered and most are not? Technical person is trained to give a technical talk whilst most of the time the audience wants a broad general talk and wants much more survey and background than the speaker is willing to give. As a result, many talks are ineffective. You should paint a general picture to say why it’s important, and then slowly give a sketch of what was done while holding the hand of your audience.

How to choose? There comes a time when you have to choose: you can either change your goal or change what you do. There is a solution, (from Hamming’s experience) He changed something he did and he marched in the direction he thought was important. It’s that easy. When you first begin, you may not have choice. But once you’re moderately successful, you do, not completely but upto some extent.

Making the best use of resources: With large resources, it gets troubling at times to focus on what problems to solve. You have the resources to tackle large problems but hamming wanted to use the facilities to compute a large number of small problems, instead, which in hindsight is a more efficient approach.

You can educate your bosses. It’s a hard job. But you can get what you want in spite of top management. You have to sell your ideas there also.

Is the effort to become a great scientist worth it? 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.

Why so few make it? 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.

Other thing is the problem of personality defect: The personality defect of wanting total control and was not willing to recognize that you need the support of the system. You should be able to find the necessary means in the system to be able to go further. Having complete control is not the best way. If you will learn to work with the system, you can go as far as the system will support you. 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. Or you can fight it steadily, as a small undeclared war, for the whole of your life. For instance, you could just go to your boss and get a “No” easily. 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”.

Another personality defect is ego assertion. You should dress according to the expectations of the audience spoken to. You should know enough not to let your clothes, your appearance, your manners get in the way of what you really 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. Hamming didn’t say you should conform; he said “The appearance of conforming gets you a long way.”

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.

Another fault is anger. Another thing you should look for is the positive side of things instead of the negative.

There is also a good ego. Sometimes, there are situations when you should make a commitment to deliver something when often you don’t have a clue how to do things. This can help you think harder and by hard thinking you often put your pride on the line and sometimes you will fail, but, like a cornered rat you’d surprised how often you will do a good job.

If you really want to be a first-class scientist you need to know yourself, your weaknesses, your strengths, and your bad faults. And think about how you can convert a fault to an asset?

Strengths

Weaknesses

Thoughts

Takeaways

Favourite bits

• There are wavelengths that people cannot see, there are sounds that people cannot hear, and maybe computers have thoughts that people cannot think.

• You don’t have to tell other people, but shouldn’t you say to yourself, “Yes, I would like to do something significant.” (to do: link my my article)

• Newton said, “If others would think as hard as I did, then they would get similar results.”

• When you are famous it is hard to work on small problems. 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.

• You would be surprised Hamming, how much you would know if you worked as hard as he did that many years.

• The steady application of effort with a little bit more work, intelligently applied is what does it. (In Bell Labs, many who worked as hard or harder than I (Hamming) did, didn’t have so much to show for it. Why? The misapplication of effort is a very serious matter. Just hard work is not enough - it must be applied sensibly.)

• “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?”

• “Great Thoughts Time.” ~ When I (Hamming) went to lunch Friday noon, I (Hamming) would only discuss great thoughts after that.

• 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 set your deadlines; you can change them.

• By taking the trouble to tell jokes to the secretaries and being a little friendly, I got superb secretarial help.

• 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.

Suggested Reading (optional)

Case study (optional)

A fellow named Clogston: Hamming met him when he was working on a problem with John Pierce’s group and he didn’t think Clogston had much. He asked his friends who had been with him at school, “Was he like that in graduate school?” “Yes,” they replied. Richard may very well would have fired the fellow, but J. R. Pierce was smart and kept him on. Clogston finally did the Clogston cable. And after that there was a steady stream of good ideas. One success brought him confidence and courage.

References