By Gordon Rugg
If a problem’s still a problem three years after its discovery, then the answer probably isn’t in the obvious place.
When you’re a new researcher tacklling a hot, newly-identified problem, there’s a strong temptation either to follow a hunch (a really bad idea, since the odds are heavily stacked against you) or to do much the same as everyone else is doing, so you can hide in the crowd. If the research community is making steady progress on a problem, then hiding in the crowd is a pretty safe strategy for new researchers, while they learn their skills. At worst, they’ll end up with some dull results that they’ll manage to publish somewhere; at best, they might happen to get lucky, and find something interesting.
However, if the research community still isn’t making progress on a problem after three years, then it’s worth considering a sideways move to a different problem, or a change in how you’re tackling the problem.
Phrased that way, it looks self-evident, which it is. But why three years, rather than two, or four? Here’s the reason.
Imagine that a new problem suddenly appears. Here’s what happens, step by step.
Bright, ambitious researchers apply for grants to tackle the problem in a sensible (and obvious) way. Anyone trying to tackle it in a non-obvious way probably won’t get funding, on the sensible grounds that it makes better sense to try the obvious solution first. By the time they’ve written the bid, waited for the bid to be reviewed, waited for the money to arrive after a successful bid, advertised for the research assistant who will do the work, appointed the successful research assistant, and waited for the research assistant to work off their notice at their previous job, it’s getting close to the end of the first year.
The research assistant gets up to speed on the topic, does some hands-on research, and analyses the results. By this point, it’s near the end of the second year.
If there’s a promising result, then the research team rush out a conference paper so they can establish priority of publication, while they work on the more heavyweight journal article. They’ll go for a conference because you can get an article into a conference within months or even weeks, whereas a journal article might take a couple of years to appear in print. That will get them into print within the third year.
That’s why the key figure is about three years. It’s a simple, useful way of spotting problems that are likely to require a different approach.
How do you choose a sensible different approach? There are two main methods.
One is to look at the deep structure of the problem, and then see if there are any well-established approaches in other fields that are good at handling problems with that same deep structure. This requires a fair amount of experience and knowledge of more than one field.
The other is the old familiar favourite of having a cup of coffee with someone wise and knowledgeable, who can listen to your description of the problem, and then suggest some approaches that might do the job. This is usually a fast, simple solution, and only requires knowing someone wise and knowledgeable, plus being willing to listen to suggestions.
So, that’s the three year principle. We’ve described a variety of research approaches in previous articles, and we’ll be describing more approaches in future articles; we hope that you’ll find some useful solutions among them.