Hamming's talk

Richard W. Hamming completed his PhD in mathematics in 1942. He was hired by the Manhattan Project in Los Alamos to take over the computing facilities that the physicists had set up. Hamming felt "a stooge", was envious, as he worked with people such as Bethe, Teller, Feynman. He wondered what made these people what they were, what set apart "those who did from those who might have done". As a result, he made the conscious decision: "Yes, I want to do first-class work". Later in the talk, he refers to this also as "significant work" or "important work". The talk had as title "You and Your Research" and was given at the Morris Research Center of Bellcore on March 7, 1986.

My source is a transcript with abstract and introduction by J.F. Kaiser. The transcript not only covers Hamming's talk, but also the introduction by Alan G. Chynoweth. My copy does say whether it was published.

"You and Your Research" can be organised by collecting together (see the points below) the observations about what makes the difference between "those who did and those who might have done".

• Luck
  Hamming admits that luck plays a part. But I get the impression that he considers it a minor part. Quotes Pasteur: "Luck favours the prepared mind". And Newton who believed that he had thought harder about his problems than anybody else.
• Courage
  It takes courage to think about important unsolved problems. (Excepting of course the officially canonized problems, such as Hilbert's, Fermat's Last Theorem, P = NP, ...). But the solutions that made a difference were to problems that not were recognized as such and those who worked on them usually did not get encouragement. The first success often changes a fumbling, diffident researcher into a courageous one. Hamming reflects about the lack of courage he perceives in the generation after him, compared to that of his own. He ascribes the greater amount of courage to the enormous confidence gained from the experience of emerging from a tight spot in the second world war to a glorious victory, and working hard at it. He doesn't blame the present generation, though, and acknowledges that their experience is very different.
• Age
  Here is one reason why people switch off after the first big success: after that it is hard to work on small problems. Einstein in his later years is an example: there was no way he could have had success in unified field theory. Hamming submits that Shannon suffered the same fate. In Hamming's opinion, the Institute of Advanced Study in Princeton has ruined a lot of careers. (Feynman has a similar opinion.) Because of this effect, the false impression is created that one can only do great things when young. Hamming advocates change of field at least every ten years. Even though he made a great contribution in error-correcting codes, he stopped reading papers in this area after a time. He acknowledges the difficulty in starting as a nobody in a new field. But of course the new field should be sufficiently closely related scientifically. Sociologically it will be disjoint.
• Working conditions
  Poor working conditions can be used creatively to lead to original solutions. Hamming mentions as an example that Bell Labs did not have acres of programmers. This prevented some projects and forced others, more worthwhile ones, into existence.
• Drive
  Mentions the "compound interest effect": if one person works ten percent more than another, the difference accumulates compounded because, if you know more, then you learn more. Hamming does not mention brains as what distinguishes the great scientists, but does believe that it is Drive. A brighter worker who only dabbles in a topic does not get anywhere; a less bright one who is committed is often successful. It helps to corner yourself by making commitments public. Hamming attributes a lot of good work to the drive exhibited by a cornered rat.
• Ambiguity
  You should believe a theory enough to benefit from it. You should be aware of its deficiencies at the same time, so you are ready to come up with a better one when the opportunity presents itself. This is the kind of ambiguity necessary for good scientific work that a lot of people fail to cultivate.
• Subconscious
  It happens that someone wakes up in the morning and suddenly has the solution to a problem. The unconscious has done the work while sleeping. This only happens if the unconscious has nothing else to work on. Hence, Hamming says, "keep your unconscious starved". Another form of Drive or Commitment.
• Important Problems
  If you don't choose an Important Problem, then you can't do Important Work. Too few people take the time to determine what problems are important. Hamming has for many years devoted Friday afternoons to "Great Thoughts Time". Samples: What will the role of computers be in all of AT&T? How will computers change science? The trick is to find the right kind of Important Problems. Time travel, teleportation and antigravity are important in some sense, but not the right kind.
• Open doors
  Hamming feels that people keeping the door to their offices closed may get more work done in the short run, but in the long run don't get as far as they might because they tend to misapply their effort as a result of not being in touch.
• The way in which you do it
  Hamming had a service job: to do computations for the scientists at Bell Labs. By paying attention to the way in which he did the jobs he did significant scientific work. This often involved re-doing the job, getting the same figures, but in a cleaner way. One of the cleaner ways became Hamming's Method for the integration of differential equations.
• Selling the work
  The work not only has to be done, but it also has to be published. It not only has to be published, but also has to be read. Most papers pay too much attention to the technical details of the contribution itself. Potential readers can't follow it. The papers that get read pay more attention to background and less to the contribution itself. Making sure that people pay attention is called "selling the work" by Hamming. To do this you have to learn to write clearly, give good formal talks, and to give good informal talks. Hamming estimates that about as much work should be spent on polish and presentation as on the work itself.
• Educate your boss
  Sometimes you should. Sometimes you can.
• Use the system
  The "system" being secretaries, technicians, bureaucrats, etc. A lot of scientists fight it. Using it can give great results, but requires some effort or other measures that are distasteful to many scientists.
• Is it worth it?
  The required drive and commitment comes at the expense of other things. Hamming thinks it's worth it, although the "other things" included in his case his health.
• Stimulation
  Seek out the Greats and be stimulated by them. Avoid "sound absorbers": people who may absorb ideas, but do not stimulate in return.
• Library work
  Those who do too little don't get anywhere. Those who do too much don't get anywhere either.
• Research or management?
  That depends on your vision. If you have a vision about, say, the role of mathematics in Bell Labs, then the only way to make it happen is to become the head of the mathematics department. Hamming never went into a management position.

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