Research Methodology

Hamming: After quite a while of thinking I decided, ``No, I should be in the mass production of a variable product. I should be concerned with all of next year's problems, not just the one in front of my face.'' By changing the question I still got the same kind of results or better, but I changed things and did important work. I attacked the major problem - How do I conquer machines and do all of next year's problems when I don't know what they are going to be? How do I prepare for it? How do I do this one so I'll be on top of it? How do I obey Newton's rule? He said, ``If I have seen further than others, it is because I've stood on the shoulders of giants.'' These days we stand on each other's feet!
You should do your job in such a fashion that others can build on top of it, so they will indeed say, ``Yes, I've stood on so and so's shoulders and I saw further.'' The essence of science is cumulative. By changing a problem slightly you can often do great work rather than merely good work. Instead of attacking isolated problems, I made the resolution that I would never again solve an isolated problem except as characteristic of a class.

Now if you are much of a mathematician you know that the effort to generalize often means that the solution is simple. Often by stopping and saying, ``This is the problem he wants but this is characteristic of so and so. Yes, I can attack the whole class with a far superior method than the particular one because I was earlier embedded in needless detail.'' The business of abstraction frequently makes things simple. Furthermore, I filed away the methods and prepared for the future problems.

To end this part, I'll remind you, ``It is a poor workman who blames his tools - the good man gets on with the job, given what he's got, and gets the best answer he can.'' And I suggest that by altering the problem, by looking at the thing differently, you can make a great deal of difference in your final productivity because you can either do it in such a fashion that people can indeed build on what you've done, or you can do it in such a fashion that the next person has to essentially duplicate again what you've done. It isn't just a matter of the job, it's the way you write the report, the way you write the paper, the whole attitude. It's just as easy to do a broad, general job as one very special case. And it's much more satisfying and rewarding!
Most good pieces of AI delicately balance several methodologies. For example, you must walk a fine line between too much theory, possibly irrelevant to any real problem, and voluminous implementation, which can represent an incoherent munging of ad-hoc solutions. You are constantly faced with research decisions that divide along a boundary between ``neat'' and ``scruffy.'' Should you take the time to formalize this problem to some extent (so that, for example, you can prove its intractability), or should you deal with it in its raw form, which ill-defined but closer to reality? Taking the former approach leads (when successful) to a clear, certain result that will usually be either boring or at least will not Address the Issues; the latter approach runs the risk of turning into a bunch of hacks. Any one piece of work, and any one person, should aim for a judicious balance, formalizing sub-problems that seem to cry for it while keeping honest to the Big Picture.
Some work is like science. You look at how people learn arithmetic, how the brain works, how kangaroos hop, and try to figure it out and make a testable theory. Some work is like engineering: you try to build a better problem solver or shape-from algorithm. Some work is like mathematics: you play with formalisms, try to understand their properties, hone them, prove things about them. Some work is example-driven, trying to explain specific phenomena. The best work combines all these and more.
Methods are tools. Use them; don't let them use you. Don't fall for slogans that raise one above the others: ``AI research needs to be put on firm foundations;'' ``Philosophers just talk. AI is about hacking;'' ``You have to know what's computed before you ask how.'' To succeed at AI, you have to be good at technical methods and you have to be suspicious of them. For instance, you should be able to prove theorems and you should harbor doubts about whether theorems prove anything.
Methodologies are social. Read how other people attacked similar problems, and talk to people about how they proceeded in specific cases.