July 20, 2004

Principles of Effective Research: Part IX

A longer post than usual today. We're now getting to the stuff that was in many ways the most fun to write, more concerned with the nitty-gritty of doing research. Today's post is concerned with different styles of doing research. In particular, I describe two idealizations, the "problem solver" and the "problem creator", and talk a little about how problem creators work. The next post will be about problem solvers.

The creative process

The problem-solver and the problem-creator

Different people have different styles of creative work. I want to discuss two different styles that I think are particularly useful in understanding the creative process. I call these the problem-solver and the problem-creator styles. They're not really disjoint or exclusive styles of working, but rather idealizations which are useful ways of thinking about how people go about creative work.

The problem-solver: This is the person who works intensively on well-posed technical problems, often problems known (and sometimes well-known) to the entire research community in which they work. The best problem-solvers are often extremely technically proficient and hard-working. Problem-solvers often attach great social cache to the level of difficulty of the problem they solve, without necessarily worrying so much about other indicators of the importance of the problem.

The problem-creator: This is a rarer working style. Problem-creators may often write papers that are technically rather simple, but ask an interesting new question, or pose an old problem in a new way, or demonstrate a simple but fruitful connection that no-one previously realized existed.

Of course, the problem-solver and the problem-creator are idealizations; all researchers exemplify both styles, to some extent. But they are also useful models to clarify our thinking about the creative process. One distinction between the two styles is how proactive one is in identifying problems, with the problem-solver being much more passive, while the problem-creator is extremely proactive. By contrast, the problem-solver needs to be much more proactive in developing their problem-solving skills. Both styles of research can be extremely successful.

Problem-solvers have numerous social advantages in research, and for that reason I believe they tend to be more common. In particular, it is relatively easy to recognize (and then reward) people who solve problems that are of medium or high levels of difficulty. This has rewards both in terms of the immediate esteem of one's peers - physicists love to trade legends about brilliant colleagues who immediately see through to the solution of some difficult problems or another - and also in the hunt for jobs and other tangible forms of recognition. It takes more time (and thus can be more difficult) to recognize people whose work is technically rather simple, but whose questions may eventually open up whole new lines of enquiry.

The advantage in being a problem-creator is that there is a sizeable comparative advantage in opening up an entirely new problem area, and thus being the first into that problem area. You can work hard to get a basic foundation in the skills needed in that problem area, and then clean up many of the fundamental problems.

The skills of the problem-creator

Our training as physicists focuses pretty heavily on becoming problem-solvers; we tend not to get much training as problem-creators. One reason I'm discussing these two working styles at some length is to dispel the common idea that creative research is necessarily primarily about problem-solving. It's true that many people have very successful research career as problem-solvers. But you can also consciously decide to invest more time and effort into developing as a problem-creator. I now describe some of the skills involved in problem-creation.

Developing a taste for what's important: What do you think are the characteristics of important science? What makes one area thrive, while another dies away? What sorts of unifying ideas are the most useful? What have been the most important developments in your field? Why are they important? What were the apparently promising ideas that didn't pan out? Why didn't they pan out? You need to be thinking constantly about these issues, both in concrete terms, and also in the abstract, developing both a general feeling for what is important (and what is not), and also some specific beliefs about what is important and what is not in your fields of interest. Richard Hamming describes setting aside time each week for "Great Thoughts'', time in which he would focus on and discuss with others only things that he believed were of the highest importance. Systematically setting aside time to think (and talk with colleagues) about where the important problems are is an excellent way of developing as a problem-creator.

On this topic, let me point out one myth that exerts a powerful influence (often subconsciously) on people: the idea that difficulty is a good indicator of the importance of a problem. It is true that an elegant solution to a difficult problem (even one not a priori important) often contains important ideas. However, I believe that most people consistently over rate the importance of difficulty. Often far more important is what your work enables, the connections that it makes apparent, the unifying themes uncovered, the new questions asked, and so on.

Internal and external standards for what is important: Some of the most thought-provoking advice on physics that I ever heard was at a colloquium given by eminent physicist Max Dresden. He advised young people in the audience not to work towards a Nobel Prize, but instead to aim their research in directions that they personally find fun and interesting. I thought his advice quite sound in some regards: for some people it is extremely tempting to regard external recognition as the be-all and end-all of research success, and the Nobel Prize is perhaps the highest form of external recognition in physics. Dresden is right, in the sense that working with a primary goal of winning a Nobel Prize would be pointless and degrading; far better to work in an area one personally finds enjoyable.

On the other hand, the Nobel Prizes are usually given for very good reasons: they reward some of the most interesting work in all of physics. There is, admittedly, a political element, with certain fields being favoured, and so on. Nonetheless, imagine a world in which one of these discoveries had not been awarded a Prize for some reason. Would you be proud to have your name associated with that discovery, even so, and regard the work on it as time well spent? In every case I can think of, that certainly is the case for me, and I suspect it's true for most other physicists.

I believe this highlights an interesting point about what makes something interesting and important. A person working toward a Nobel Prize or some other form of external recognition has, in some sense, decided to abdicate their personal decision about what is important and interesting. The external community of physicists (in this case, represented by the Nobel Committee) is what makes their decision: if it might win a Nobel, it's important.

Balancing this observation, this is not to say that your decision about what is interesting and important should be yours along. People who work in isolation rarely end up making contributions that are all that significant. Your decision about what is important should be informed by others: talk to your peers, find out what they think is important, look in the textbooks and history books and biographies, and, yes, look at what wins prizes (of all sorts).

But at the end of the day you've got to form your own independent standards for what is interesting and important and worth doing, and make judgments about where you should be making a contribution, based on those standards. I think better advice from Dresden would have been to aim to produce work of the highest possible caliber, but according to what you have come to believe is important.

Exploring for problems: Obviously, all researchers do some of this. For the problem-solver, the process of exploring for problems often works along the following lines: keep moving around, looking for problems that you consider (a) well-posed, or able to be well-posed after some work on your part, (b) likely to fall within a reasonable time to the arsenal of tools at your disposal (perhaps with some small expansion of that arsenal), and (c) below some minimum thresholds of interest and difficulty. Once you've found a problem of this sort, you work hard on the problem, solve it, and publish.

Problem-creators may be rather more systematic about exploring for problems. For example, they may occasionally set time aside to survey the landscape of a field, looking not just for problems, but trying to identify larger patterns. What types of questions do people in the field tend to ask? Can we abstract away patterns in those questions? What other fields might there be links to? What are the few most important problems in the field? Problem-creators set aside time for doing this kind of systematic exploration, and do it in a disciplined way, often with feedback from others.

Surveying the landscape can be particularly revealing. A lot of people work in fashionable subfields of a larger field primarily because there are lots of other people working in that subfield. The problems they work on may be technically complicated, especially after a few years, when the most basic questions have been answered. This is compensated by the fact that it's extremely comforting to work within a field where there is a standard narrative explaining the importance of the field, some canonical models for what problems are interesting, and a willing audience of people ready to appreciate your work. In addition, working in such subfields gives younger people a chance to show off their technical prowess (sometimes, not unlike elk spoiling for a fight) to peers in a position to recommend them for valuable faculty positions.

Getting ahead of the game: There are many important problems, and sometimes an entire field comes to some agreement about what is important: proving the Riemann Hypothesis, or understanding high temperature superconductivity. Sometimes, however, there is a problem either not appreciated at all, or only dimly appreciated, that is equal in importance to such gems. Consider the creation of the scanning tunneling microscope - the basic idea had been around for years, yet nobody had ever seriously tried to build the device. The inventors put it together on a shoestring, and created one of the major tools of modern physics. Or consider David Deutsch and Richard Feynman's creation of the field of quantum computing, by framing the right questions ("What would a quantum mechanical computer be capable of?'' and "Would it be faster than a classical computer?''). One of the big ways you can get ahead as a researcher is by identifying and then solving problems that are important, but perhaps not terribly difficult, ahead of everyone else.

Identify the messes: In a nice article about how he does research, physicist Steven Weinberg emphasized the importance of identifying the messes. What areas of physics appear to be a state of mess? Funnily enough, one of the signs of this can be that it's very hard to understand. For a long time - and to some extent this persists today - physics texts on general relativity were very difficult to understand. The tensor calculus in them was often confusing and difficult to understand. There was a good reason for this: the basic definitions in the subject of differential geometry, although laid down in the 19th century, didn't really reach their modern form until the mid part of the twentieth century, and then took considerable time to migrate to physics. The reason a lot of the discussion of tensor calculus in physics texts is confusing is because, very often, it is confused, being written by people who don't have quite the right definitions (meaning, in this case, simplest, most elegant and natural) in mind.

When you identify such a mess, the natural inclination of many people is to shy away, to find something that is easier to understand. But a field that is a mess is really an opportunity. Chances are good that there are deep unifying and simplifying concepts still waiting to be understood and developed by someone - perhaps you.

Posted by Michael Nielsen at July 20, 2004 09:07 PM

A very nice article... I was pointed to a related article by Tim Gowers that talks about 'two cultures' along the same lines. you might find it interesting...


Posted by: Suresh at July 21, 2004 03:45 AM

If you liked the link from Suresh, you might also want to look for a copy of Gian-Carlo Rota's book _Indiscrete Thoughts_. He has several essays on the world of mathematics, including one that discusses the difference between theory builders and problem solvers. It is less technical than the Gowers article, but amusing and thought-provoking nontheless.

Incidentally, the Gowers article doesn't mention one of my favorite results: the Matrix-Tree Theorem. This is a wonderful result that connects the theory of #P problems, combinatorics, and linear algebra. You can find one proof at


but the collection of _Proofs from The Book_ contains several others, including a clever double-counting argument. Babai and Frankl have a book on _Linear Algebra Methods in Combinatorics_ that's been in preparation nearly forever that has oodles of results like this, along with applications.

Anyway, as for training problem-creators, the Stanford CS department once gave "why do some areas of research flourish and others not" as a question on the Operating Systems qualifying exam. Talk about pressure!

Posted by: DavidM at July 22, 2004 04:19 PM

David: I greatly enjoyed the Rota book, and some of the book reviews, in particular, stay in my mind. Coincidentally, I quoted one of them to a colleage today, and saw your comment an hour or so later!

I'll look into the matrix-tree theorem. I'm a physicist, but I have a project at the moment where #P problems arise naturally, so it's on my mind.

As for the Stanford problem, it sounds like an interesting experiment. I'd be tempted to try using questions like that as the basis for assignments in undergrad and grad courses.

Posted by: Michael Nielsen at July 22, 2004 10:00 PM

A somewhat related division of mathematicians, from Grothendieck's "autobiography" (translated into english):


Posted by: Anonymous at July 23, 2004 07:14 PM