We’re all fairly good at problem solving. That’s the skill we were taught and on which we were endlessly drilled at school. Once we have a problem, we know how to turn the crank and get a solution.
Ah, but finding a problem – there’s the rub. Everyone knows that finding a good problem is the key to research, yet no one teaches us how to do that. Engineering education is based on the presumption that there exists a pre-defined problem worthy of a solution. If it were only so!
After many years of doing and managing research, I’m still not sure how to find good problems. Often I discovered that good problems were only obvious in retrospect, and even then I was sometimes proven wrong years later. Nonetheless, I did observe that there were some people who regularly found good problems, while others never seemed to be working along fruitful paths. So there must be something to be said about ways to go about this.
I recently received an article from an Internet pioneer, Craig Partridge, containing a list of open research problems in communications and networking, as well as a set of criteria for what constitutes a good problem. In his list and others that I have seen, there are sensible guidelines for choosing research problems, such as having a reasonable expectation of results, believing that someone will care about your results and that others will be able to build upon them, and ensuring that the problem is indeed open and understudied.
All of this is easier said than done, however. Given any prospective problem, an Internet search may reveal a plethora of previous work, much of which (unfortunately!) will be hard to access. On the other hand, if there is little or no previous work, maybe there is a reason no one is interested in this problem. You need something in between. Moreover, even in defining the problem you need to see a way in, the germ of some solution, and a possible escape path to a lesser result, like the runaway truck lanes sometimes available on steep downhill highways.
Timing is critical also. There is a definite early-bird phenomenon. Once a good problem area is opened up, everyone rushes in and soon there are diminishing returns. But this same effect can lead to a herd behavior on unimportant problems when a large number of papers appear on a subject of little practical significance in a self-approving circle. Such problems often admit of many small variations whose cumulative effect is not in proportion to the deluge of publications. On the other hand, real progress usually comes from a succession of incremental and progressive results, as opposed to those that only feature variations on a theme.
The work habits of a researcher also have a lot to do with success in problem choice. Richard Hamming used to divide researchers into two groups: those who worked behind closed doors and those whose doors were always open. The closed door people were more focused and worked harder to produce good immediate results, but failed in the long term. Today in a networked world I think we can take the open or closed door as a metaphor for researchers who are actively connected and those who are not. And just as there may be a right amount of networking, there may also be a right amount of reading, as opposed to writing. Hamming observed that some people spent all of their time in the library, but never produced any original results, while others wrote furiously, but were relatively ignorant of the relevant literature.
Hamming, who shared an office with Claude Shannon and personally knew many famous scientists and engineers, also remarked on what he saw as a “Nobel Prize effect,” where once having achieved a famous result, a researcher felt that he or she could only subsequently work on great problems. As a consequence, that researcher never did great work again. Much of good research starts instead with small problems, just as they say great trees grow from small acorns.
Like a lot of things in life, in order to latch onto a good research problem it helps to be in the right place at the right time and to be prepared to take advantage of your good fortune. Sometimes all the good and well-intentioned advice in the world won’t help you avoid working on a dead end problem. I know; I’ve been there, done that.