Everything else being equal, picking the right problems is the key factor determining your success as a researcher (no matter how you define success). In a previous post, I proposed three categories of research problems:
- explain a previously unexplained observation;
- perfect an existing technique;
- invent a new problem.
It appears that all 3 categories are equally valid. Which technique you prefer is a matter of style.
Today, I would like to propose a new, orthogonal, categorization in terms of the depth of the problem you tackle. Some problems
- are narrow and well-defined, you can complete them in a few months;
- form a set of narrow and well-defined problems, likely to keep you busy for years.
I have tended myself toward the first category (see “my research process“). The benefit of a focused burst of research producing a distinct result should not be underestimated. The most obvious benefit is that you can quickly move on and thus, you can afford to try your hand at random problems. It is the equivalent of a hit-and-run. If you are the curious sort, it allows you to learn about a new topic, without investing your career in it. However, it makes applying for grants more difficult. You are also less likely to achieve some recognition because the depth of your contribution might be less.
The second category means that you must find yourself a niche and work over it for years. Indeed, preferably, not too many people in the world must be aware of these problems you have identified. The catch is: how can you know, ahead of time, that the topic and the problems you see now, will still be interesting in two or three years? Are you investing in vain? Presumably, if you can follow this strategy, grant applications and recognition may come more easily. But what happens if you get bored?
The two categories relate to how you read papers. If you read papers thinking “maybe I could build on their work”, then you will naturally tend to the first category. Reading a lot of papers on different topics favors random hit-and-run research projects. Are you reading the list of accepted papers looking for clues as to what you will work on next? Are you attending talks to pick up random new ideas?
However, if you tend to “pull” research papers out of the (virtual) library based on your own ideas, then you will more likely gravitate toward the deeper research projects. In this case, your mental filters are much stronger: you tend to filter out everything that does not directly relate to your goals. You may still attend many conferences, and read lists of accepted papers, but your brain will filter most of the data out.