Re:What Problems to Solve
by robotresearcher on Monday July 14, 2014 @02:03PM
(#8032259)
I'm having trouble reconciling Feynman and Adleman's advice. Adelman would rather read a novel than work on anything but the most important problems whose time has come. Feynman got his mojo back by understanding spinning plates, and famously loved to goof around with physics problems. Hamming would probably agree with Adleman here.
Perhaps they would agree that one should have some ambition and do what's important, but Feynman would have you sneak up on it from behind, while keeping the juices flowing with playfulness. I'll go with that.
Re:What Problems to Solve
by ambulancechaser on Monday July 14, 2014 @02:57PM
(#8032550)
Well, there's no reason to reconcile them. They can have differing opinions on how to approach problems. But don't think that Feynman was working nonstop on spinning plates and those diagrams he invented. He liked working in strip clubs, started drawing a bunch, and randomly learned Portuguese when he followed a pretty woman onto a plan to Brazil. There he joined a street band and learned to play instruments while continuing his drawing. This seems pretty comparable to the idea of reading a book for a break.
Regardless, you can find people's ways of focusing to differ and not have to reconcile every smart person's personal way to study and research.
To me, Feynman's example of the plates is something that you do in addition to Adleman/Hamming's advice.
Of all the problems to work on, work on those that have have a reasonable angle of attack (Adleman/Hamming), that you have the ability to solve (Feynman). And in addition, make sure you plant little seeds instead of just working on big problems after you've succeeded (Hamming in 'You and your research'), which amounts to being able to play with spinning plate problems (Feynman)
NW = The interviewer
LA = Leonard Adleman
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NW: They say the most creative and challenging part of research is finding the right question to ask. Do you agree with that?
LA: I wouldn't characterize it as the most challenging thing, but it's of critical importance. Sometimes it's not hard to find the "right question'. For example the mathematics literature is full of very important unanswered questions. In this case, the real issue is: Has that question's time come? Have we reached a point where developments in the appropriate area of science give us some chance of breaking the problem? For example, I worked on a famous centuries old math problem called "Fermat's Last Theorem". I was not 'strong' enough to solve it, but I find some solace in the fact that my intuition that its 'time had come' was right. The problem was finally solved two years ago by Andrew Wiles of Princeton. It was one of the major events in the history of mathematics.
The other side is to generate new questions. That's a funny process. The way I seek to generate new questions is to start to look at whole new fields, like biology, immunology or physics. Since I come from a different field, mathematics, I bring an unusual point-of-view that sometimes allows me to generate questions different from the classical questions in those areas. Like the question of DNA computing.
For the young scientist, this question of choosing the right question to spend your valuable limited intellectual resources on is critical. I often sit for months and do no productive work that anybody can see, because I don't feel I have a good enough question to work on. Rather than take on some lesser question, I would prefer to read a mystery novel. The point is, sometimes it's important to lie fallow for a time waiting for the 'right question' to appear, rather than to engage in uninspiring work and miss the important opportunity when in comes.
But in the end, the real challenge of science is to make progress - to succeed, to contribute knowledge.
NW: Of course, in an academic setting, there's that drive to publish or perish...
LA: Yes, that's a problem, because you have to feed your family. But I always tell my students and junior faculty that they are better off following their inspiration and their hearts in what research they do, that they should always try to take on the most interesting and important problems, that they should not waste their time on little problems just to make another line on a vitae.
My philosophy is that it's important, in a curious way, for scientists to be courageous. Not physically courageous, but courageous in an intellectual way. I believe that by working on extremely hard problems, by being courageous, you may succeed. But even if you fail, you fail gloriously. And you will have learned immense amounts, you will have extended the envelope of what you can do. As a byproduct of failing on a great problem, I have always found that I could solve some lesser but still interesting problems - which then fill your vitae.
"""