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I gave a presentation on my PhD research at university last week, and it was criticised for lacking practical significance. A different comment suggested the presentation was not placed in context. Could somebody provide some advice on how to place research in context and convey its practical significance? How can I effectively assess who/what/where/when will see the benefits of my research?

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    <rant>It is annoying that (in general in academia) you are forced to say that your research is significant. So it is... (which is hard to tell before) or you make it up.</rant> – Piotr Migdal Jul 4 '13 at 7:17
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    @Piotr Migdal: I disagree with you. What I find annoying is two things: that there seems to be little place for fondamental research, and that in response fondamental researchers lie about their motivations to make it look more applied than it is. But one should be able to explain at least why she is interested in the question she worked out for years, and this has to be related to some sort of significance. – Benoît Kloeckner Jul 4 '13 at 7:45
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    @BenoîtKloeckner Actually, I agree with you. The question "Why do you consider this topic worth investigating?" is crucial (and when it is a PhD student is is usually not yet possible to judge significance, without story-telling). But when it comes to "practical significance"... well, for fundamental research (as opposed to applied, or - engineering) it almost certainly not cure cancer, solve environmental problems and create a quantum computer (and again, Roentgen didn't work on "saving millions of lives with better diagnostics" - he was just working on a potentially fruitful thing). – Piotr Migdal Jul 4 '13 at 12:17
  • I have similar issue but with my advisor. He always asks me for applications (applied scenarios) for my research ideas. I believe its out there but I do not know what's the name of it. I either come up with application from my little head or the whole paper will be screwed. – seteropere Jul 5 '13 at 4:34
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Ask yourself a number of questions:

  • Why am I doing the research?
  • What problem am I solving?
  • Why should anyone else by interested in this research?
  • How can my results help solve someone else's problem?

The first two questions will help you understand what you are doing from your own personal perspective, as well as establishing the context of the work. The latter two will help you establish why someone else would be interested in your work.

In short, ask What? and So what? about your work.

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    I think that for many PhD students the answer to the first question is "because my supervisor picked this project for me"... Of course, the real reason is never stated publicly... – Nick S Oct 20 '16 at 0:49
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Definitely, your advisor is the person who should help you most with this question, so make sure you talk to her.

With this disclaimer, I would like to distinguish two things: the good and the bad way to justify the significance of your research. To be clear, good and bad are personal (but motivated) judgments and are not related with what will please people asking you that question, but with what is sane argument.

Let's start with the bad way:

  1. this is the most important thing and most others are specialization of it: giving false but vaguely plausible reasons to study what you studied, hopping to reach other's expectations,

  2. claiming applications that are often claimed in the area, or vaguely related but at best very long term applications (e.g. "my study of cell migration is crucial for understanding metastases, so it will help cure Cancer"; this works with any fondamental research in cell biology),

  3. name-dropping (e.g. "Nobel Prize Trucmuche has studied this 20 years ago, so surely that must be interesting"),

  4. generalization for the sake of generalization -applies maybe mostly to maths, but applies a lot there- (e.g. "Finsler geometry is a generalization of Riemannian geometry, so surely it is interesting").

  5. lacking any clue (e.g. "My advisor told me to do it, so I did"). If you don't know why you are doing what you do, at some point you should find out or change subject.

Note that 1. is very, very often seen in grant application, and it might be impossible in some cases to apply successfully without resorting to this kind of argument. This does not make it a good argument; we should be as thorough in assessing the relevance of our research than we are in assessing our research result.

Now the good way:

  1. this is the most important thing and all others are specialization of it: explaining the reasons why you where interested in the project, why you find it fascinating or interesting,

  2. giving perspective applications that sincerely did motivate your work, either from start or that you realized during the research process. This may not exist, which is not (rather, should not be) an issue, at least in fondamental research,

  3. placing your research in context: how it relates to what has been done before, to which previously raised question it answers, which previously held beliefs it contradicts,

  4. explaining how it generalizes previous work to meaningful, existing examples (e.g. "My theorem on Finsler geometry explains such and such features of Hilbert geometry"),

  5. explain the perspectives opened by your work (e.g. "if we believe this principle applies even more generally, then we can hope to use my methods to understand such and such important phenomenons"),

  6. explain why it is fun (e.g. "look at this dancing corn starch: weird, huh?")

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Without knowing your actual field of research, here are some general pointers (by no means, is this an exhaustive list):

  • Research and find other papers based on or is similar to your work, this will give a bit of a basis for the practical context.

  • From reading of papers, try and define a gap where your research may help with.

  • Ask your supervisor/advisor for advice in this, employ their help in defining the context.

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    "From reading of papers, try and define a gap where your research may help with." This seems to go backward: you do research because you noticed a gap in what we know, not the other way round. – Benoît Kloeckner Jul 4 '13 at 7:46
  • Doesn't hurt to find further evidence for this, particularly in a practical sense. – user7130 Jul 4 '13 at 7:59
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    @Benoit: Maybe in an ideal sense, but I think many PhD students start marching down their research path because their advisor has noticed that gap; I don't know how many students find that gap on their own. That's why I like the third suggestion here the most. – J.R. Jul 4 '13 at 10:37
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    @J.R.: sure, but then the advisor can point out the gap, and at some point the graduate student must understand the motivation by herself. – Benoît Kloeckner Jul 4 '13 at 14:23

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