I think you're forgetting the problem of incentives. Whatever standard procedures for evaluating/predicting usefulness you come up with, if they're actually used to allocate resources and status in practice, people will have the incentive to hack them by designing and presenting their own work to come off as better than it really is. And since people who do research are usually very smart, you'll be faced with a host of extremely smart people trying to outsmart and cheat your metrics, in which many will surely be successful. Goodhart's law, and all that.

This, of course, is not even considering whether the influential people whom you'd have to win over to establish such practices have the incentive to submit their past and present work to such evaluation. Unfortunately, although the problems you point out are very real, there is no straightforward solution for them; almost any attempt at fixing institution is likely to run into difficult and unpredictable problems with perverse incentives.

My hypothesis is that what we find interesting is largely the result of subconscious, heuristic (i.e., intuitive) optimization for status, and so interesting problems are useful to the extent that such intuitions are accurate, and the extent that we as a society reward the discoverers of useful ideas with status.

From an individual perspective, part of this problem is an instance of the more general problem of how to improve our intuitions and when to override (or combine) them with explicit reasoning, which I think is a very interesting (and useful!) one. (The post takes a more social perspective, which of course is also very interesting.)

At least in math, one common indication of of interestingness is how much something is connected to other things or shows up in different forms. Thus for example groups are very interesting in the abstract because they show up in many different mathematical contexts. This is a good metric for also determining usefulness since the more things something is connected to in the abstract the more likely it is that one of those connections will be practical.

It sounds like a good first step is to develop a reliable way of recognizing in retrospect what was in fact useful, and classifying research projects/publications that way.

Of course, this works better for short-term projects. A fifty-year longitudinal study on heritability of disease risk factors is hard to measure the usefulness of in less than fifty years.

Two properties of interesting problems seemingly overlooked by the above:

1) Interesting problems are Fun

2) Interesting problems motivate, which is closer to the topic of this post. I would not underestimate this motivation, after reading one of the participants on the Manhattan project say something to the extent that "we had to work on the bomb because it was so cool"

In the biological sciences, one often finds claims of interestingness or usefulness in the abstracts, introductions, and conclusion sections of research papers. Research may claim to overthrow existing paradigms, for example, or lead to disease cures. Presumably one also finds these claims or promises in research proposals. But I'm not sure how one evaluates research papers and programs for how much interestingness and usefulness they actually deliver.

Some kind of citation metric, presumably. But how do we distinguish between being cited for being interesting vs being cited for being useful?

I'm somewhat skeptical of the claim that researcher's level of interest in a given subject is very strongly correlated with the maximum possible benefit to society that could come out of an intensive study of the topic. It may be true, but I think that the primary motivation is just that the problem presents an interesting challenge.

That being said, I do think that scientists and researchers work harder and more efficiently when they enjoy what they're doing. If, as I suspect, interesting-ness is uncorrelated to potential benefits, we should still ensure that interesting projects are funded.

Imagine, in a hypothetical scenario, that there are two different areas of study that, if researched, would produce innovations of equal value to society. This fact, however, is not known to the individual running the research budget. Let's suppose (just for the sake of numbers) that a scientist who is actively curious about a problem will work 20% faster on that problem than an uninterested scientist. In this case, funding the interesting project will be more efficient than funding the uninteresting one. Obviously, we should pursue lots of areas of research, because the uninteresting problem will give us benefits too. However, we should make sure that we don't defund interesting projects in order to pursue lines of inquiry that will not yield results as efficiently.

If researchers are more likely to work on problems they find interesting, we will automatically find that most of the useful research was done by people who found it interesting. We will also find that there is a lot of useless research being done.

I think this is obviously the case, and the data therefore does not give evidence to the hypothesis that interestingness is a good heuristic for usefulness.

I think good research is useful, and bad research is non-useful. Research that the researcher doesn't find interesting is unlikely to be good. Therefore, it is unlikely that research that the researcher doesn't find interesting is going to be useful.

I don't think that interesting research is likely to be useful because researchers are more likely to be interested in useful things. Most of what mathematicians study, for instance, has little obvious practical value.