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I have attended a decent number of TCS conferences. It is good that researchers solve difficult problems. However, I am often interested in the reason why a problem is interesting in the first place. So, I often ask the presenters about some real life application of the problem that they have solved.

For example: If somebody has studied the Independent set problem on planar graphs of degree at most 4. Then, I ask why a planar graph of degree 4 is an interesting use case. Note that I am aware of why the independent set problem is interesting in general graphs.

However, the presenters usually do not answer such types of questions properly.

The following are the replies that I often receive:

  1. They do not give the answer and simply say that it is an established problem. It makes me feel dumb.

  2. Some people admit that they do not know about it and they are only studying the theoretical side of the problem.

  3. Some presenters enthusiastically answer the question and give more details than I expected.

Should I avoid asking such types of questions?. Should I simply believe that the problem will have some application in the future, if not now? Then, how can we know if some problem is more interesting than the other, if we do know its usecase yet?

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    $\begingroup$ I think you should distinguish between "is it right to ask this question" and "is it right to ask this question at the end of the talk". The answer to the former is certainly "yes"; i.e., there are appropriate contexts to ask it in. For the latter, it is understandable if a speaker doesn't want to get into the general discussion of why established problems are important to work on. $\endgroup$ Sep 21 '21 at 6:58
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    $\begingroup$ This is not at all about whether the question is appropriate, but whether your behavior and the manner of communication is appropriate. That is, it is a question about social norms, not about theoretical computer science. $\endgroup$ Sep 21 '21 at 7:06
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    $\begingroup$ @AndrejBauer "That is, it is a question about social norms, not about theoretical computer science." Really? I see three questions asked. The first is about social norms and the other two are about theoretical computer science. $\endgroup$ Sep 21 '21 at 15:41
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    $\begingroup$ My 2 cents: Asking a TCS researcher "what are the real-world applications of your research?" is akin to trolling. TCS is closest to math in this sense - real-world application is not usually a motivation for the work. Indeed, most (including the best) TCS researchers generally don't have much tie to, say, applications in industry or elsewhere. (To be clear, I think this is not a bad thing. TCS and math are still well-motivated.) $\endgroup$
    – Neal Young
    Sep 21 '21 at 16:08
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    $\begingroup$ By "well-motivated" do you mean "has known real-world applications"? If so I don't think this is the standard TCS interpretation of "well-motivated". In the standard interpretation, well-motivated is more subtle, and I would say a good part of it is something like an aesthetic judgement, which is probably not easy to explain clearly to someone who doesn't share it. For example, consider the concept of probabilistically checkable proofs. This concept has, a-priori, no direct practical application. Exploring such creative ideas is one of the cornerstones of TCS. See also "Turing machine". $\endgroup$
    – Neal Young
    Sep 21 '21 at 16:27
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(Personal opinion: I personally think asking such questions is good for you, good for the speaker, and good for the community. It helps keep us at least a little bit grounded.)

(Slightly more objective answer:) If they say it is an established problem, you should not feel stupid, it was still a legitimate question. Why is it an established problem? The honest answer is usually one of a few types:

  1. originally someone had a use case for it, they asked some theorists, and theorists started working on it but then most of them don't know the original use case, or

  2. this problem itself is not interesting in applications, except in that we hope it gives us some insight into a more general problem that we don't yet know how to solve, but which might be better-motivated from the viewpoint of applications.

  3. This problem is not interesting in applications nor for anything connected to applications as far as we know, it is just fun/interesting/beautiful to work on.

(I suspect (2) may be part of the answer for your example of planar independent set in graphs of degree at most 4.)

As to your last question, having a use case is not the only thing that makes a problem interesting.

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    $\begingroup$ Thanks! It clarifies a lot. The third point is making me a bit uncomfortable. How can we quantify: "fun/interesting/beautiful to work on"? Anything I think about is beautiful in some sense. Even a water droplet is stupendously beautiful. How to find the right direction among infinite set of problems? $\endgroup$ Sep 21 '21 at 6:52
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    $\begingroup$ Finding a good research direction is it's own problem :), which I think there have been several questions about on this site, and which I think does not really lend itself well to quantification (only qualitative analyses). If you find many things beautiful enough to work on, then you will have lots of choices. $\endgroup$ Sep 21 '21 at 7:02
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    $\begingroup$ What is "interesting" has a sociological aspect. Popularity of problems/areas is often not based on applicability, and interest in them can go up and down based on many factors. It is helpful to develop one's own taste in problems. Most researchers in TCS are balancing several factors in choosing problems. $\endgroup$ Sep 21 '21 at 14:02
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    $\begingroup$ How much public funding (tax-payer money) should be spent on pure theoretical research? Tricky issue for universities and governments.. If the economy is in bad shape, they are going to cut down funding for research in pure theory.. (They might say "Since you love theory so much, do it on the weekends, in your own time".) $\endgroup$ Sep 23 '21 at 3:13
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If a theory problem has some practical application, it is certainly a good thing. But often just the mere hardness of a problem can make it interesting, even exciting, without any real-life use case.

A well-known example is the 4-color problem (the vertices of every planar graph can be colored with at most 4 colors, such that adjacent vertices have different colors). Although it can be motivated by map coloring, but real-life cartography does not use it, because real maps typically use more than 4 colors, anyway, see the example below.

On the other hand, the hardness of the problem makes it interesting on its own right, regardless of any application. The problem was open for more than a century, and motivated a lot of research in graph theory. Eventually solved in the 1970s, but, as far as I know, still no classical proof is known that does not require computer assistance.

Responding to the comment of Lieuwe Vinkhuijzen: overall, I would encourage asking researchers about the real-life application of their work, for example, at conferences. Such applications are likely to increase the value of the work, and the collective wisdom of a discussion may help identifying potential applications. On the other hand, I also find it perfectly acceptable if the researcher answers: I was merely motivated by the inherent beauty and hardness of the problem, without having any real-life use case in mind.

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I'll expand on mathworker's intial comment in that while I think it's generally good to ask these questions, at a presentation during the short Q&A period following the talk may not be a good time.

If the presenter didn't put the answer to this question in their talk, I'd guess they probably (a) have no answer, (b) have a pretty generic answer along the lines you mentioned, and/or (c) think the answer is well-known to much of the audience. In these cases, this question and answer might not be that useful to the room. So you might decide to ask it in a one-on-one instead.

On the other hand, I bet sometimes one would get really good and interesting responses.

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