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I am in Computer Science and currently in my proposal phase. For my problem statement, I want to come up with good research questions. However, at the moment I am struggling with the definition of "good" research questions. My professor usually comments that my current questions are not "why" questions, but instead are "yes/no" questions.

Any recommendations what make good research questions good?

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  • Do you want to know the answer? Really?

  • Do you realistically have a good shot at finding the answer, in a reasonable amount of time? Really?

  • Will lots of other people be happy to learn the answer (even if the question had never occurred to them before)? Really?

  • Are you sure nobody already knows the answer? Really?

If you can answer yes to all eight questions, it's a good research question.

(Unfortunately, some of these points may depend on what the actual answer is, which of course you don't know.)

  • Thx for your answer! You wrote, "If you can answer yes to all eight questions, it's a good research question.", however I only see four. Do you mean by eight question to question your question, by "really"? – Kare Dec 3 '14 at 7:32
  • Yes, I counted "Really?" – JeffE Dec 4 '14 at 2:22
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In my opinion, a good research problem has at least the following properties:

  1. It is a small piece of a big problem. In other words, it needs to be both small enough so that you can reasonably make progress on it, yet connect to a larger problem.
  2. It is possible to do a small "pilot" to sanity-check your approach and whether results are promising. Most research problems can take a lot of work to really tackle. It's good to have milestones along the way that can let you figure out if you are on the right track and whether the project is likely to be worth the full investment.
  3. Something can be learned from the work, whether or not it comes out the way that you hope. A large fraction of interesting research projects don't work out the way it was hoped: either the driving hypothesis was wrong, or turns out to be too hard, or something else shifts and things end up obsolete. A well formulated project will still contribute knowledge, whether or not it actually ends up advancing you toward the original goal.

Let me illustrate further with nice example that I saw recently: a group of undergrads at NCTU Formosa put together a project to modify E.coli to manufacture PBAN neuropeptides to stimulate pheromone production in the Heliothis virescens moth. This is a really specialized and esoteric-sounding goal, but relates to a much bigger idea: doing this could lead to a general approach to radically improved insect traps that could greatly reduce the need for industrial pesticide use. The narrowly scoped project they set for themselves thus connects to a much larger goal, but has a set of clearly delineated milestones along the way (e.g., create PBAN-expressing sequences, verify they work in E.coli, test the extract on female Heliothis virescens moths, verify the increase in trap efficacy, pilot tests with local organic farmers, etc.). Furthermore, even if it turns out the bigger vision can't be achieved, there still can be a lot of things learned about neuropeptide engineering, which may turn out to be relevant to a great many other questions, both foundational and applied.

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