How many scientific discoveries have been made by investigators carrying out studies that, in principle, should have merely reproduced known results and/or confirmed the conventional wisdom ? I do not have numbers but I suspect many. Serendipity plays much more important a role than many a scientist would care to admit.
Of course, a posteriori we are all geniuses. Once someone smarter than us does us the favor of explaining to us what it is that we have just observed, why it is not what we originally thought (in fact, why what we originally thought can actually not be observed at all in that way), and maybe even educates us on its significance, then we can have fun making up all sort of awe-inducing stories, for the purpose of impressing people with our brilliance.
“The key idea came to me while I was lazily chewing on a pretzel at the mall… Suddenly I could not take my eyes off the tantalizing pattern printed on the paper napkin… My mind went to that elusive magnetic phase I had been unsuccessfully trying to observe in my computer simulations… Now it all seemed crystal clear in my mind — that was how spins would arrange themselves !…”
Don’t get me wrong, it may well be that nonsense such as that described by the fictitious condensed matter physicist quoted above happens, sometimes… But the fact is, we would never know if that is really how thing went, or whether maybe the person luckily stumbled upon something interesting unexpectedly, possibly even as a result of an experimental or theoretical error, while looking for something unrelated, pursuing a dead-end project which no one with a single functioning neuron would even consider… Well, Mother Nature has a way of displaying its kindness toward scientists by throwing gems at them, perhaps out of pity. And, we should only be thankful for that, for science would not be nearly as much fun as it is, were it not for its unpredictability.
If there is one lesson that I have learned in 25 years in science, is that there is a lot to be said for seemingly boring projects, and for the so-called “Nike approach” — just do it . Of course, I agree with the notion that one should always “think big”, seek to achieve important results on problems of fundamental, broad interest among one’s community, as opposed to making it all about producing tables of numbers; I agree that one should try to follow a plan, have at least one basic guiding idea, as opposed to shooting in the dark, leapfrogging from one calculation or experiment to the next, hoping to stumble upon something spectacular. That is precisely why funding agencies ask applicants to submit proposals.
At the same time, I think that there is a greater risk, especially for junior scientists, and I am mostly thinking of tenure track faculty here, and it is that of perennially waiting for inspiration, for some “killer idea”. Of late, i seem to be having this argument a lot with younger colleagues, including some who seem to be struggling to get their research program off the ground, but at the same time tend to shot down rather quickly any suggestion of possible research project that, in their view, is either too complicated, or not likely to lead to anything “Earth shattering”.
Their contention is generally that their future hinges on accomplishing something noteworthy, and for that they need to find the “right project” . They claim that carrying to fruition a research project that, even in the best scenario, will have “low impact in the field”, is just as bad as not doing anything, so it’s not worth their time and effort.
“Something like that has been done already”… “No one will care”…. “How many cites can I possibly get”…. “this will not end up in [insert favorite unapproachable high impact journal here]”, are the things that I most commonly hear.
I have several problems with that attitude, and in part I have already expounded them in other posts, but let me rehash them here:
In conclusion, while I obviously support the general notion that scientists, especially junior ones, should try going after important results and pursue potentially significant and original projects, there are also very good reasons to work on a few “boring” ones, concurrently. I don’t think it is anything of which one should be ashamed — I am not, anyway.
 My understanding is that the “right project” is one for which they are uniquely positioned to make a major contribution in a very short time, thereby making a name for themselves and consequently securing a future in science. I am not saying that that scenario is impossible, I am just thinking that it is very, very unlikely, and that banking a career on it is risky; a contingency plan seems like a good idea. It is often also unclear to me whether, in their mind, such brilliant projects, of high potential significance but doable “quickly”, should be handed to them by someone else (who ? And why would that someone else give the projects to them?), or they are just waiting for the idea to come to them…
 There used to be a time when independent duplication and confirmation of someone else’s original results was regarded as an important, no, crucial contribution to scientific progress. Now things are different… One will not publish in Nature or Science, simply for confirming previously published results, much less for disproving some fascinating but incorrect findings, and apparently anything that is not published in Science or Nature is worthless…