This is one more post on the Hamming series about how to select your research career topics.

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 were not even recognized as such!

The initial cost of tackling an important problem is high; if it is a hard, important problem, chances are that you will not solve it at the first go, and that publication will not happen as fast as tacking smaller, but more constrained, problems. Young researchers may think that this is the only way to start an academic career. And advisors would of course discourage their students if they propose a problem that is somehow ‘non-mainstream’ (Science is a social activity after all).

There are careers built on a single experimental effect. Not because it is particularly relevant, but because it is extremely solid and running more experiments demonstrating that it appears in different circumstances will produce more publications.

Hamming mentions how the first success often changes a socially-handicapped researcher with self-esteem problems into a courageous one. Maybe having a solid effect may act as a catalyst, but it is always important to see it as  a stepping stone, not a solid rock to build a home and not to move around much.

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.

Technorati Tags: philosophy – of – science, – planning, – sociology, – courage, – goals

Today my post will be a bit more high-level than usual. Most of us select scientific topics without paying much attention to overall strategy (i.e., which ones may produce the most benefit).

On this, the best piece of writing I have found is Richard Hamming’s famous essay “You and Your Research” (which is a transcription of a talk he gave at bell labs, e.g., here, and here), Richard Hamming suggests that you ask yourself three questions:

1. What are the most important problems in your field?
2. Are you working on one of them?
3. Why not?

“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.”

He also advocates that good research is not a matter of luck, and that hard work increases your chances of producing outstanding results. Again, this may seem obvious, but sometimes it is easy to attribute results to things other than work.

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.

Hamming worked in a place where everybody should have the resources (brain power, technical, free time, freedom of thought) to tackle the most important problems.  Considering that he worked at Bell Labs while people like Shannon and Tukey were there, I think the previous statement must be correct. Hamming started to eat at the Chemistry table:

[...] 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!

So it seems that not everybody who can tackle difficult, important problems that will make an impact in their field, does.

There are many nuggets on this talk. Concretely, I find useful his advice of reserving one day of the week to “Think big thoughts” -Although Fridays are particularly bad for me-. Since the material in his talk his very valuable, and hard to cover in one post, I’ll try to do a series on Hamming’s ideas. In any case, highly recommended read if you feel your motivation is dropping at some point.

Technorati Tags:philosophy – of – science, – science, – goals

Technorati Tags: science, strategy, productivity, goals, planning