klab
"What I cannot create, I do not understand." – R. Feynman
Jonas Kubilius

R. Hamming's tips on becoming a great scientist

This is an old talk so things may have changed since; however, I see a lot of sound advice that I myself found out to hold or at least vaguelly started understanding during my career. What follows are Hamming’s thoughts in a more structured manner.

Goal:

I have to get you to drop modesty and say to yourself, “Yes, I would like to do first-class work.”

Motivation:

(…) doing really first-class work, and knowing it, is as good as wine, women and song put together.

It’s not sheer luck:

I claim you have some, but not total, control over it [luck].

Personal traits

  • Courage: That is the characteristic of great scientists; they have courage. They will go forward under incredible circumstances; they think and continue to think.
  • Drive: 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.
  • Commitment: 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.
  • Coping with ambiguity: 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.

Work on important problems

  • Resolution: Instead of attacking isolated problems, I made the resolution that I would never again solve an isolated problem except as characteristic of a class.
  • Get good ideas: Great Thoughts Time
    • 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?”
    • 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?”
  • Go for the important problems
    • Most great scientists know many important problems. They have something between 10 and 20 important problems for which they are looking for an attack. And when they see a new idea come up, one hears them say “Well that bears on this problem.” They drop all the other things and get after it. (…) 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.
    • 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?

Work ethics

  • Learn to sell:
    • (…) 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.”
    • 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.
    • 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.
    • (…) you should spend at least as much time in the polish and presentation as you did in the original research.
  • Talk to people:
    • I used to go down to his [Ed Gilbert’s] office regularly and ask him questions and listen and come back stimulated.
    • 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.
  • You don’t need ideal 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. (…) What appears to be a fault, often, by a change of viewpoint, turns out to be one of the greatest assets you can have.
  • Educate your boss to let you do what you want: If you want to do something, don’t ask, do it. Present him [your boss] with an accomplished fact. Don’t give him a chance to tell you 'No'.

Fallacies

  • Fame:
    • 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.
    • You have to change. You get tired after a while; you use up your originality in one field. You need to get something nearby.
  • Fighting against the system:
    • 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.
    • (…) good [as opposed to great] scientists will fight the system rather than learn to work with the system and take advantage of all the system has to offer.
    • Which do you want to be? The person who changes the system or the person who does first-class science?
    • 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.
  • Ego assertion:
    • An enormous number of scientists feel they must assert their ego and do their thing their way.
    • If you chose to assert your ego in any number of ways, “I am going to do it my way,” you pay a small steady price throughout the whole of your professional career. And this, over a whole lifetime, adds up to an enormous amount of needless trouble.
  • Self-delusion: “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.