An interesting post at DrugMonkey discusses the research statement that tenure-track science faculty candidates are required to include in their application packages. Having been involved in several such searches in physics, I can offer an opinion as to what search committee members typically look for, when going through one of them.
Disclaimer: A faculty search is a highly non-linear process, in which objectivity is often lost in the mire of departmental politicking and maneuvering, jealousy among faculty colleagues, individual agendas, etc. No matter how impressive a candidate and well thought out his/her application, there is always the chance that none of that will matter in the end, as some puzzling decision will be made (including that of forgoing the hire altogether, even in the presence of more than one seemingly qualified applicant). Still, that is no reason not to put one’s best foot forward; even though one’s bid may not be successful, leaving a good impression always bodes well for one’s professional future.
The fundamental difference between a Research Plan and a Research Summary seems to confuse many a candidate. The latter describes past research accomplishments; such information is clearly valuable and relevant, in many respects provides support and credibility to one’s research plan, and therefore should be included somewhere in the application package. However, a research plan is not about what has been done, but rather about what will be done.
I remember discussing my own research plan with my then postdoctoral advisor, at the beginning of my job search over a decade ago, asking him more or less “What the heck am I supposed to write here ? Do they want to know what projects I shall tackle next ? What NSF program I shall seek funding from ?”.
I thought I had decent, credible answers to all those questions, and I really thought (hoped) that he would say, yeah, just write all that down in good English. Alas, he said to me something along the lines of “Well… If a graduate student walked into your office at this very moment, and asked you for a research project possibly leading to a doctoral dissertation, would you have something for him/her ?”.
That caught me off guard. I started thinking… Would I ? No, not really. Sure, plenty of small, short-term projects popped into my mind, the type of projects one thinks of as a graduate student or postdoc; but… nothing really “dissertation worthy”.
It was not anymore about finding a numerical trick to carry out that specific calculation, for that particular quantity, for that well-defined, known mathematical model of a physical system on which scores of people had been working over the past two decades. That was the type of stuff on which I had been focusing until then; that had been my only mode of operation. But all of a sudden, things were different.
Which original, broad fundamental issues would my future research program address ? That was the question for which, for the first time in my life, I had to think of an answer. It was a difficult, and very humbling process, because it occurred to me that it had ramifications in almost every aspect of my (hopefully) future profession. I found myself thinking back of the time when I first decided to study physics; what problems were most interesting to me ? Which seminars was I most likely to attend ? And, also, which parts of the research profession did I enjoy the most ? To which people did I like talking the best, among those whom I knew in my professional field ? And, how much physics did I know, really ?
It can be quite intimidating, but, the great thing about science is: all you need is a starting point — thereafter, things take a life of their own, and you stumble into interesting problems without even looking. A research statement must make this very point and none other, i.e., that the candidate has a starting point.
Yup, in the end that’s all there is to it. Of course, the plan must be credible, well articulated and realistic, and obviously the candidate must be able to defend it scientifically, on paper and during the interview– after all, research grant proposals will be based upon it — but basically this is the whole point.
(In case the reader is wondering “Wait a minute… are you saying that there are newly hired tenure-track assistant professors who do not even know where to start ?” — yes, that is exactly what I am saying. I know many of them. I think that very often these are capable and bright people, who simply were not ready for a faculty job when they were hired, and I really do not think that they were done a favor by being hired).
A research statement which I (as well as many of my colleagues) regard favorably, will convey a clear impression that the candidate has gone through the exercise described above. There will be an introductory sentence describing the broad scientific issues that the person plans to address, a general definition of the strategy (experimental or theoretical) that (s)he is proposing to adopt, and the progress that (s)he will attempt to make. And then there will be a description of few, representative research projects of various degree of difficulty, on which students could be engaged. These projects will be placed in the broader context described above, namely of the scientific question(s) that the future faculty will be asking through his/her program.
Now, because it is all about having a starting point, it is important to get one thing straight: none of this is binding. Whether the candidate, if hired, sticks to that plan or not is immaterial — nobody will ever take to task a faculty going up for tenure for not having followed the originally advertised research plan (the only thing that matters at that point, is whether the person’s actual research record is successful or not — I have witnessed cases of scientists who decided to do very different things than what they originally had planned, and this was just never an issue ).
Too many research statements read like “these are the projects on which I am currently working — I plan to finish them”, or, more generally, “I plan to keep doing what I have done so far — if it has carried me to this point, it must be good”. What is the problem with that ? First of all, the person ‘s work has been supervised, albeit to different degrees. Naturally, many postdocs are capable of working independently, but the typical committee member will generally not know a given applicant in person (and letters of reference are not always trustworthy — see my thoughts on this subject here), and it is difficult to assess someone’s scientific contribution, let alone leadership, to the work done up to that point. A research plan must give a sense of one’s ability to continue on on his/her own, and in order to show independence of thought it is a good idea to impart a noticeable change of focus, differentiating the future work from that done under supervision.
But there is a more important problem with a statement that reads as suggested above: It lacks originality. At some point the research vein that a candidate has exploited as a graduate student or a postdoc will simply dry out, for a number of reasons (funding, loss of interest on the part of the community, etc.). When that happens, the person must be capable of finding something else to work on. This is why it is a good idea for a candidate to try and convince a search committee, that (s)he is ready to branch out on his/her own, at hiring time.
 As usual, things must be done within reason. Too quick or abrupt a switch of research field may raise eyebrows, especially if the person ends up drifting toward an area of research that is perceived as too far removed from the scientific mission of the department of affiliation. Still, I have seen a lot of people get away with stuff like that — of course, they were very successful in their research endeavor, by all accepted academic measures (publications, funding, invitations to speak, awards, etc.).