Good research: invent new problems or explain mysteries

It is a lot of work to grind through a research project and get an interesting paper out of it. Mostly, you have to be patient enough and work everyday at it. If you follow a sane process, it is difficult to fail entirely.

Picking the right research question is very important however: it is difficult to recover from a bad choice of topic. There are at least 3 types of good research questions: 1) explain with a theoretical model a (puzzling) experimental observation 2) improve by at least an order of magnitude an existing technique 3) make up a new problem and be the first to propose a solution (I call it Turney’s way).

I now believe that options 1 and 3 are far better than option 2. To illustrate my opinion, here is a little scenario:

  • read a paper;
  • think to yourself: I could improve this idea ten times over;
  • get excited, dream of fame, start crafting a paper;
  • late on Friday night, realize your contribution is tiny;
  • keep going (because you have invested so much);
  • months later, publish a weak paper.

So I submit to you Lemire’s first rule of good research: you must either be trying to explain puzzling experimental results, or be inventing new problems. In some sense, it amounts to discarding the “engineering way” which is to constantly perfect existing techniques.

Further reader: I have written much about how I think one can write a good paper and about my usual research process.

Published by

Daniel Lemire

A computer science professor at the Université du Québec (TELUQ).

7 thoughts on “Good research: invent new problems or explain mysteries”

  1. make up a new problem and be the first to propose a solution

    You’re giving away my secrets! Seriously, the world needs both inventors and refiners. Which you choose is probably more a personality thing than a strategic decision making thing.

  2. Making up a new problem and being the first to propose a solution has two advantages: you’re not trying to crack a nut that everyone else has been trying to crack for a long time, plus you have the biggest potential upside for novel contribution. The downside, however, is that you have a far bigger onus to prove that the new problem you’ve made up is worthwhile, since you don’t have the validation of others. I suspect it’s generally harder to publish results about a problem no one else has heard of. A cynical reviewer–or simply a rationally skeptical one–might suspect you of having made up a problem because you are unable to solve any of the ones already on the table.

  3. Coming up with good research problem which can sustain for ten years (in research community) is as difficult as solving a ten year old open problem. It’s not *easy*.

    Good research problems indeed means good research. Coming up with a new system is rather better and you get to solve the system in stages. But then you don’t remain a theory guy.

    It’s good to define a very big goal at the very beginning of your career and start solving all small problems towards that goal. In between you’ll find some *very good* problems. Either solve it on your own or collaborate it.

  4. at first when i read this i thought: yes, exactly! we need more (1) and (3) papers and fewer (2). but now i’m not so sure. the issue for me is that a lot of times i feel like the process of going through the “sludge” of (2) is what eventually leads to (1)s and (3)s. in fact, (1)s would almost be impossible without lots of people (maybe not me!) working on many many minor (2)s. i feel it’s also important for (3)s, too, because in order to do something new, you need to know what is possible already… at lot of times we have something that looks like a (2) only to find out a few years later that it actually has many qualities of a (3) that were simply lurking initially.

  5. make up a new problem and be the first to propose a solution

    I am rather attracted to this type of research, as well. However, having gone through the process a few time on a few (minor, but solid) research topics, I find that, because most of my initial work/effort is spent inventing a new problem, my initial proposed solutions are decent, but not great. When the new topic area finally catches on, it’s because some (2) has looked at my (3), and easily made an order-of-magnitude improvement on it.

    Thus, even though that (3) work was the first for a given area, the (2) work gets most of the perceptual credit.

    So I still believe that being able to open up new (3) areas is a very important research skill. But aside from personal satisfaction, isn’t it rather dangerous to be a “first mover”? Isn’t history replete with examples of the “second mover” getting most of the credit?

  6. LOL
    The early bird get the worm but the second mouse get the cheese…
    It’s true in industry too (even more so…)

  7. I think there is a connection between your ideas and Kuhn’s concepts of “normal science” and “revolutionary science”. http://en.wikipedia.org/wiki/The_Structure_of_Scientific_Revolutions#Coherence

    I think Peter is right, these kinds of work correspond to different personality types. From an impact standpoint, the mistake you don’t want to make is to do refinement work when the field is on the verge of a revolution. But I suppose that can be hard to guess.

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