I am in Computer Science. I read a survey today. The author gave such a good result by the end of the article that I think the research question can be called "closed": the result performance is ideal and I think the problem is not worth researching any more; future developers can simply use the algorithms proposed and things should be fine. However, the author of the survey did not say so -- they did not say that the problem is solved, nor did they said anything about future work.

I believe (in this specific case), that the problem is solved:

  1. The research goal is to reduce network latency. By the time the survey was written (year 2008), the result latency was 100ms. With such latency, human users won't notice a network delay, because that only happens when the latency exceeds 150ms.
  2. The authors of the survey did not publish any paper on optimizing the algorithms after that survey.

Does these mean that the problem is safely closed? If so, why didn't the survey authors say that? If not, why didn't they continue working on it? How would I know whether a research question is solved or not?

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    In your example, there is still room for improvement until the latency is equal to the distance between the two endpoints, divided by the speed of light. The difference might not be noticible for humans, but for other purposes it may matter. High-frequency trading comes to mind. – Pieter Naaijkens Jan 6 '13 at 14:44
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    they did not say that the problem is solved, nor did they said anything about future work. — Bad survey author. No biscuit. – JeffE Jan 6 '13 at 15:29

I don't think a research question is every “closed”, as you say, though it's of course a matter of vocabulary. In the example you mention, it seems clearly that there is no current incentive to design better solutions, but unless it is actually proven that there can be none, it's not a solved-and-closed question, it's a “we don't actually need to do better” question. This makes all the difference in the world.

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    Some research questions can be closed, by the method you describe, proving that there is no better solution. This has indeed happened many times for mathematical research questions, such as the optimal close-packing of equal spheres. – Peter Olson Jan 6 '13 at 18:17
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    @PeterOlson yeah, mathematics is one field were you might say such things. I thought about writing an additional paragraph about that, but it's not my field so I was worried to say stupid things. Here goes anyway: In mathematics, you can indeed prove a theorem, but it's rarely ends up all work on a give “question” in the broader sense: what happens with less strict hypothesis? can a shorter proof be found? is there proof that doesn't rely on a given axiom? what happens in neighboring situations? In your example of sphere packing, I believe the question is still open for larger dimensions… – F'x Jan 7 '13 at 8:36
  • @F'x: but in an applied field, how much should we care about a solution we don't need? – Blaisorblade Oct 12 '13 at 0:29

I'd like to expand on Pieter Naaijkens's answer, because your question and his answer bear on a more general problem: when is a problem worth solving? Or viceversa, should one care about a paper solving this problem? I'll present the answer I've grown up with (as a PhD student), though I've seen wildly different opinions on this, so I don't think there's a fully objective view (though characterizing the spectrum of opinions is what matters here).

I've learned that it's up to the author to motivate the reader to care about the paper ("sell one's research"), though others might disagree; nowadays this is necessary because of the research-literature overload we live in. In applied fields, a common motivation is a set of (possibly indirect) applications. Different kind of motivations exist, but I'll conjecture that even good theoretical work should matter to other theoretical work to be good, and then leave other motivation out of scope.

Would you accept a paper (1) solving this latency problem for websites interacting with users? By your reasoning, I wouldn't (at least, not at a top venue). But let's assume that again Pieter Naaijkens submits a paper (2) on the topic. It first convinces readers that better latency matters by describing some application (say high-frequency trading, assuming this actually applies). Then, paper (2) solves the problem exactly like paper (1) above. The second paper could get past the same reviewers. I might even argue that with that motivation (assuming it's good), he might create a research question. And in some cases, simply motivating well a research question might be enough for a paper.

To demonstrate that wildly different opinions exist, I'll offer two opposite examples.

  • I've seen a reviewer explain that a paper was good research but he wasn't sure whether it addressed any relevant problem; the reviewer concluded with a strong accept judgement. (Of course I won't share details).
  • On the other hand, Tanenbaum's Modern Operating Systems book explains that some research had the only point of keeping otherwise unemployed graph theorists off the streets, because (it is hinted) the problem lacked actual applications.

Other examples of researchers questioning the motivation of other research abound, but I won't add further anecdotical evidence.

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