Rethinking Hamming’s questions

Richard Hamming is a famous computer scientist. In his talk You and Your Research, Hamming recounts how asked researchers three questions which I paraphrase:

  1. What are the important problems of your field?
  2. What important problems are you working on?
  3. 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?

It is important to qualify what Hamming meant by “important problem”. He meant not only the result of the quest (curing cancer) but also the path taking you there (by using a new generation of antibiotics).

My thoughts on these questions:

  • In truth, hardly anyone knows what the important problems are. We typically know which methods are at our disposal, we know of many easy tasks, but we are effectively blind to any objective beyond that which has been done.

    We know something about our track record in this respect because, for example, researchers frequently make assessments about their fields and where it should go. It is not uncommon that when you read these assessments, years later, they appear hopelessly naive and misguided.

    Hamming believed that great scientists knew the important problems. I doubt it. I’d call it hubris.

  • To make matters worse, any popular answer is almost surely worthless to the individual. If an objective and a method are known to be promising, you can bet good money that people better than you have been working on it for some time already. In some sense, this almost ensures that whatever the great scientists tell us is the future, should be viewed with suspicion. It might be their future, but it much less likely to be your future.
  • Most importantly, I claim that most people do not care whether they work on important problems or not. My experience is that more than half of researchers are not even trying to produce something useful. They are trying to publish, to get jobs and promotions, to secure grants and so forth, but advancing science is a secondary concern. That’s why most people are not troubled by Hamming’s questions. And, of course, Hamming already observed that researchers who do not care for his questions tend not to go very far. He assumed that it is because they do not “know” the important problems, but I believe that a much more reasonable point of view is that they don’t care.

What we need, of course, is to filter out people who do not really care. I think that’s where informal settings help.

Tell smart people to work on what is important to them, but don’t tell them (ever) what exactly they must do. Do not reward any of them visibly for any repeatable action.

Soon enough, only the people who are will remain.