In a similar way, look at what Leonard Adleman (A in RSA, DNA computing, integer number factoring, etc) says in this interview (skip the chinese paragraphs): http://teacher.scu.edu.cn/ftp_teacher0/chjtang/teach/adleman...

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.

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