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I have heard from academics in various fields that the usefulness of their research is not always immediately clear, but sometimes, a piece of research will inadvertently become important at some point in the future.

If this is true, i.e. if the usefulness of a research idea is not immediately clear, how could one write a convincing research proposal when a research proposal is supposed to address the importance of the idea? Does one resort to generic lines such as "to expand our understanding of x, y, and z"?

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This has a lot of possible answers. One wants to say, as many answers as there are research proposals.

In mathematics, some things matter just for the pure beauty of it. The same may be true in other fields. Probably true in the arts as well.

In CS one can often search for improvements on current best practice - faster, more secure, smaller, simpler.

Some problems matter because the search for answers has been long and unfruitful. Some things in physics are like that.

Some things matter because they provide synergy between existing ideas thought to be distinct. Drug research, pedagogical research.

Some things are useful. And, as you say, one can hope that other things become useful in the future. Very fresh pure math may have few current uses. But potentially future uses.

Think about why you want to do the research. Think about how it will complete something from the past. Think about how it might foreshadow the future.

I'm sure you can come up with something. And it need not matter to everyone. Sometimes it will only "matter" to a small group of specialists. Math can be like that too.

And they aren't mutually exclusive. Quite a few of these were manifest in my own doctoral research.

  • This is going to partly depend on the funding source. For example, for at least some of the UK research councils at present, proposals must explain the "Economic, societal or environmental impact" of the work, with clear pathways predicting how that impact will be delivered. – Flyto Jan 16 at 10:08
  • Does 'very fresh pure math' refer to anything less than 100 years old? I would claim that the vast majority of advances in pure math in the last 100 years have no applications outside of pure math and maybe theoretical physics today. This might change in the future though ... – quarague Jan 16 at 12:09
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Nearly all of the time, all you can know is the very near use that could be made of your research. Just as one example: The idea of making a laser was originally quite "out there." When Einstein did his work on the idea in 1917 it would have been very difficult to predict the very many uses we now put it to. And since it was more than 40 years before one was constructed, it clearly remained difficult for many years.

So it's doubly a challenge. It's a challenge for you to try to predict where it might go. And even if you do predict correctly, it's a challenge to try to get your reviewers to agree.

But never mind. Predicting the future is a task at which nearly everybody is affected severely by the Dunning-Kruger effect. People think they know all about it and can confidently predict exactly what will happen for all of their lives. In reality, nearly nobody can predict more than trivial things, and even those at most a few days in advance. At 2 days out, weather forecasts are about 50% accurate where "it will be the same as today" is 60% accurate.

It also depends on the nature of the proposal and the process to follow. In many cases, the ultimate motivation of the people approving a proposal is some variation on prestige for the granting agency or profit for some company.

So bring in some cynicism. Figure out how you can leverage the self interest of the granting body. Don't actually lie. But present things so that the "shiny" parts of your work will reflect positive light on the granting body. They do a lot of medical research? Your research will contribute to the process of finding a cure for a particular disease. They fund a lot of research for aircraft safety? Your research will contribute to improving aircraft safety. You get the idea.

Then it's a question of choosing a granting body that has a suitable lever for you to pull. If your research really does contribute to curing a particular disease, you should get yourself in front of a granting body that funds such things. If you really have a way to invent a better flight computer for commercial aircraft, then you need to tell an aviation company's granting department about it. Again, you get the idea.

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Skipping over the case where the usefulness is already clear.

Experience and knowledge of the field helps. For a new student it is very hard to know what kind of research would make a valuable addition. But a researcher who's been around for a while has a wider view:

  • What kind of research has been happening recently, and what new vistas it opens up?
  • What are people talking about on conferences that they'd want to investigate?
  • What grants exist? What kind of research do they exist to fund? Which particular projects have they been funding recently?
  • What are big hairy problems in the field, and what are bite-size portions of it that a junior scientist could try to do something with?
  • What kind of new techniques, sources, resources have recently been discovered or acquired, that allow new types of research?
  • What's been happening in society, relating to this field? Are there ethical worries? Is there excitement about a new device?
  • What kind of problems in industry could be tackled if a particular technique was developed? (Much easier to answer if you've been involved with industry than as a pure cloistered academic.)
  • What kinds of problems in other academic disciplines could be attacked if your field develops a new technology for them? (for example, what can Deep Learning do for the study of historical texts?)

Those points are useful to narrow down where to look for promising ideas to research. But what if you already have an idea, and need to convince people to fund it?

The same points can be helpful. If you know what kind of research other people would recognize as valuable, you have a starting point to relate your novel idea to those desires of theirs.

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