The practice of academic research is based on the production of formal documents that undergo formal reviewers by peers. We routinely evaluate academics for jobs and promotions based on their publication output. When asked about their contribution to science, many academics are happy to point at their papers. In some cases, they will also point at the grants that they have secured.
Back when I worked at NRC, a friend of mine, Martin Brooks gave a controversial talk entitled “user-based research”. It has been nearly 20 years, and I still remember this talk. His ideas were so upsetting that people left while he was talking. I stayed and listened. It took me years to own the ideas he expressed that day.
Martin complained that researchers mostly “threw research over the wall” expecting that other people (maybe industry) would pick up the research from the other side of the wall. While it certainly can happen that others will read your paper and apply it, you should not count on it. Nobody has to read and understand your work.
When I was a bit younger, a senior professor pointed out that some idea we were discussed had been described and tested by his team in some prestigious venue decades ago but that nobody ever did anything with it. Without thinking, I replied: it was your job to do something with it, don’t blame others. The room fell silent and there was a long pause.
I am not saying that if you find a way to cure cancer in mice, it is your job to get the therapy cleared for use with human beings and to open a hospital where the therapy is delivered. A single individual can only do so much.
What I am saying, however, is that publishing a research paper is not the goal of research. It is not the final output. It is only one element in a chain. And it is not even a requirement. You need to communicate your idea, but the peer reviewed journal article is just one such mean.
Your actual goal is “transfer”. That is, someone, somewhere, must put your ideas in practice beyond the publication of your paper. It does not mean “industrial applications” though it can be that. If your idea is worthwhile and you let it end with a research paper, you have failed.
And it does not merely mean collecting “citations” or other bibliometrics. People routinely cite papers without reading them. Few citations are influential.
But the academic incentives almost conspire to prevent impactful research. There is one specific criteria that academics like to apply that is destructive: novelty. For some piece of academic work to be judged worthwhile, it must be novel. I will say it again and again: originality is overrated.
Of course, people entering a new field tend to “rediscover known facts”. You have to push them back and tell them to go study some more. But there is a difference between naivité and lack of originality. You have to be aware of the history of your field, that is what scholarship is all about. But you also have to stick with ideas for the long run, until the fruits appear.
Instead of rewarding novelty, we should reward scholarship: we should ask people to show that they have studied and documented the past. We should never penalize someone who works on pushing a known idea by refining it, communicating it, validating it.
This idea that some venerable professor had 20 years ago that never went anywhere? Well, it might be entirely worthwhile to revisit it and make it go somewhere, even if it is not novel at all.
Further reading: Boote, D. N., & Beile, P. (2005). Scholars before researchers: On the centrality of the dissertation literature review in research preparation. Educational researcher, 34(6), 3-15.