In praise of boring projects

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” [0]. 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:

  • Few low impact papers are always better than no papers at all. This is really something that does not seem to resonate at all with some young scientists out there, who act as if gaps of two or three years in their publication records will be of no consequence. Granted, maybe a bunch of scarcely cited articles will raise some eyebrows among the members of the Tenure Committee, but as a tenure applicant I would rather have that than no articles — that is the almost surefire way of being turned down, at least at a research university.
  • It takes a great deal of self-assurance for anyone to believe that they can assess reliably the likely impact of a research project, much less the number of citations that the ensuing article will garner.
  • “Boring” projects can provide excellent training ground for undergraduate and beginning graduate students, or even for more experienced junior colleagues wanting to get their feet wet with an investigative tecique or methodology with which  they may not be familiar.
  • The most important reason for embarking on a project deemed  unlikely to lead to anything exceptional, which seems nothing more than mere duplication or confirmation of what others have done [1], is that Nature has a funny way of always being unpredictable. Something unexpected always seems to appear, which is why so many interesting results  are obtained in unlikely circumstances. 
  • 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. 

    Notes

    [0] 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…

    [1] 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…

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    One Response to “In praise of boring projects”

    1. GMP Says:

      I am totally with you here.

      We all want to be great. But great ideas don’t come about when you are eagerly waiting for them to. You have to go about doing your work, attacking problems that are interesting and that you can actually think of and are qualified to do, and then in the course of doing your work generally things come to place

      It’s sort of like waiting for inspiration to hit to start writing. That’s a recipe for disaster. You have to write crappy paragraphs anyway, look at references, read the references, edit crappy paragraphs, and then when the inspiration does hit, you milk it for all it’s worth. But even if it doesn’t, you will still have many meticulously edited paragraphs.

      I think there is a quote somewhere to the effect “You don’t wait for inspiration to start doing, you do to get inspiration.” (paraphrased)

      And I don’t think one can truly assess which papers will be well-liked and well-cited. I mean, yes, a paper in Nature/Science will be cited, but I have a Journal of Applied Physics (impact factor below 3) paper that gets as many citations per year as my Nature paper. It was simply a good, solid paper on a topic people cared about and appeared at the right time. It was one of the “boring” projects.

      And yes, no publications for years = professional suicide. I know people will forgive you for the first year on the tenure track, but not after that.

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