A crucial question towards the beginning of any research project is, why should my group succeed in elucidating an answer to a question where others may have tried and failed?
Here's how I'm going about dividing the possible worlds, but I'm interested to see if anyone has any other strategies. First, the whole question is conditional on nobody having already answered the particular question you're interested in. So, you first need an exhaustive lit review, that should scale in intensity based on how much effort you expect to actually expend on the project. Still nothing? These are the remaining possibilities:
1) Nobody else has ever thought of your question, even though all of the pieces of knowledge needed to formulate it have been known for years. If the field has many people involved, the probability of this is vanishingly small and you should systematically disabuse yourself of your fantasies if you think like this often. Still... if true, the prognosis: a good sign.
2) Nobody else has ever thought of your question, because it wouldn't have been ask-able without pieces of knowledge that were discovered just recently. This is common in fast-paced fields and it's why they can be especially exciting. The prognosis: a good sign, but work quickly!
3) Others have thought of your question, but didn't think it was interesting enough to devote serious attention to. We should take this seriously, as how informed others choose to allocate their attention is one of our better approximations to real prediction markets. So, the prognosis: bad sign. Figure out whether you can not only answer your question but validate its usefulness / importance, too.
4) Others have thought of your question, thought it was interesting, but have never tried to answer it because of resource or tech restraints, which you do not face. Prognosis: probably the best-case scenario.
5) Others have thought of your question and run the relevant tests, but failed to get any consistent / reliable results. It'd be nice if there were no publication bias but of course there is--people are much more likely to publish statistically significant, positive results. Due to this bias, it is sometimes hard to tell precisely how many dead skeletons and dismembered brains line your path, and because of this uncertainty you must assign this possibility a non-zero probability. The prognosis: a bad sign, but do you feel lucky?
6) Others have thought of your question, run the relevant tests, and failed to get consistent / reliable results, but used a different method than the one you will use. Your new tech might clear up some of the murkiness, but it's important here to be precise about which specific issues your method solves and which it doesn't. The prognosis: all things equal, a good sign.
These are the considerations we make when we decide whether to pursue a given topic. But even if you do choose to pursue the question, some of these possibilities have policy recommendations for how to proceed. For example, using new tech, even if it's not necessarily demonstrably better in all cases, seems like a good idea given the possibility of #6.