I doubt if I can offer any deeper insight or more pointed advice to a tenure track assistant professor in the sciences, than what anyone can find on a number of reputable science blogs.
Often times, however, as I go through posts describing the “dos and donts” of young scholars wanting to maximize their changes of eventually landing tenure, while I find myself in agreement with the general ideas expounded (we are not really talking secrets, anyway), I also feel that some of the most common recommendations could be taken too far, or interpreted too rigidly, ultimately doing the probationary faculty more harm than good.
The purpose of my post is to warn against adopting too literal an interpretation of one of the most commonly heard recommendations; as usual, when talking about an intrinsically imperfect exercise, such as that of evaluating the scholarly work of a tenure applicant, no “rule” can be regarded as cast in stone .
Independent and original
Taking into account the disclaimer of note , if you look through the guidelines of any institution of higher learning, at which the expectation exists that faculty engage in some scholarly research (and where consequently the academic performance of any one of them is assessed also through an evaluation of his/her research output), you will read somewhere wording to the effect that the research program of a successful tenure applicant should show evidence of independence and originality. What does this mean ?
In this particular context, “independent” and “original” are closely related. Of course, all research work should be generically “original”, i.e., not consisting of a mere duplication (or, very modest extension) of work of others.
What is specifically meant, when assessing the merit of a tenure application, is that a research program that should appear largely as the expected, obvious continuation of the work carried out by the applicant during her graduate and postdoctoral training, work presumably inspired by the applicant’s supervisors , will generally raise eyebrows, and leave evaluators concerned. This will be especially the case if the majority, or at any rate a significant fraction of the research articles published during the applicant’s probationary period, are co-authored by her former mentors.
There are reasons for this basic criterion to be in place. An effective academic faculty must be able to think of research projects and ideas of sufficient originality, as well as scientific breadth and depth, to constitute the core of the research work of (under)graduate students and postdocs supervised. These individuals will eventually compete for jobs with their peers at other institutions, and in order for them to have a fighting chance, their work should not be seen as “ordinary”, but should rather stand out.
While this obviously depends for the most part on their own ability, there is no question that the initial choice of project, and of the investigative approach followed, will crucially affect the fortunes of the trainees — and usually the supervising faculty plays a major role in the choice. Junior investigators too closely dependent on input from others, will generally lack the imagination and creativity required to generate the type of research projects that advisees need, in order to make a name for themselves. To me, this is the most important reason for expecting a junior faculty to demonstrate independence and originality.
There are other potentially negative long-term consequences from one’s inability to work independently, affecting especially one’s likelihood of securing extramural research funding, ability to supervise students on a regular basis, and generally of maintaining an active research program later on in the career.
This is why most graduate and postdoctoral supervisors will recommend their former advisees, having landed their first tenure-track appointment, against collaborating with them for a few years. The purpose is exactly for the junior scientists to establish their own independent research records, in the eyes of the greater community. It is the same advice that many senior scientists and science bloggers offer to probationary faculty reading their blogs.
And, please, do not get me wrong, it is sensible advice, but one that should be taken with a grain of salt. In particular, one ought not forget that so-so is always better than no.
Productivity comes first
The most damning thing by far, for the record of a probationary faculty, is too little, of anything. No credible case can be built on a bunch of hypotheticals, in defense of someone’s meager publication list. Very few department chairs or Science deans, will take seriously the contention that the applicant’s limited productivity only reflects the difficulty and ambition of her research objectives. In the absence of any published preliminary results, intermediate achievements, high profile speaking invitation, something to differentiate temporary lacks of success from inactivity, most of us will be more inclined to believe the latter .
Thus, even though of course one should pick potentially very rewarding and challenging projects, one had better make sure that there be every year something to show for. And, in order to cover that base, it is a wise idea not to put all one’s eggs in one basket, but rather allow for one’s own research program to include different projects of varying scope and difficulty. It is not necessary that each project consist of the quest for some “holy grail”.
Boring can be beautiful
Brilliant ideas, the kind of which no one has thought yet, are hard to come by. But the good news is, there is a lot to be said for “boring” research projects, i.e., ones that may not have much breadth (or, to use our favorite lingo, yield only “incremental information”) and will likely not alter the conventional wisdom and/or result in glamorous, high profile publications. Yes, they still serve a number of very legitimate purposes, which make them worth pursuing, especially at times of limited inspiration.
First of all, there is a very important educational aspect to the scholarly research that one pursues in academia. It is not all about making landmark discoveries, it is also (in fact, some say mostly) about the hands-on training that it offers students, training which many of us deem valuable, no matter what the future professional paths of the students might be.
Boring projects they can be excellent ways to introduce to professional research undergraduate or Summer students, as well as beginning graduate students, whose background may not enable them to tackle cutting edge problems. They need to learn how to do calculations, or to carry out experiments, how to organize coherently their data, come up with an overall coherent interpretation and picture, give talks, write scientific articles. In fact, often times such “safe” research projects, which can be completed relatively quickly and lead to a concrete, definitive results, are preferable for training purposes.
Secondly, one out not forget that there is no such thing as a “simple” research project. Nature has a way of surprising us all the time, unveiling unexpected, hidden facets even in apparently mundane systems. So, even if it looks like a “boring” project, even if one is redoing something that has already been done, even of it looks like, in the best case, one will merely confirm what is already known, it is a good idea to do it anyway, if there is nothing at hand clearly more worthwhile. Something will be learned by someone, in any case.
Make no mistake, I am not trying to promote irrelevant research here. I strongly believe that scientists, especially young ones, should think big and go after big things. The research portfolio of a tenure applicant should not consist mostly, or exclusively of boring or at any rate scarcely significant projects, there is no question about that. All I am saying is, anything is preferable to noticeable gaps in one’s publication record.
How original do I need to be ?
OK, so, let us cut the crap and be realistic. The research program of a tenure-track assistant professor will almost always be the continuation of what the person did as a graduate student and/or postdoc, at least to some extent. And it makes perfect sense.
After all, why abandon the well-established, successful research program that has landed the person the job to begin with, one that is likely to produce more interesting results ? Why venture out on something entirely new, requiring that one become familiar with new science, possibly learn new methodologies, compete in a field where one is not as well known ? Why risk bringing to a halt one’s research output for a number of years, receive only lukewarm review on grant proposals from skeptical reviewers unfamiliar with the applicant’s work and ability, instead of riding the wave of support arising from one’s solid postdoctoral work ? I would never recommend any of my advisees to do anything like this. If anything, I would suggest that they develop in parallel a new line of research, while exploiting their existing one to its full extent .
And, while publishing more articles with former mentors may not be the optimal thing to do, it still beats the hell out of not publishing anything. Thus, a tenure-track faculty going through an unexpected dry spell, unable to generate a reasonable stream of publication for a period of time approaching or exceeding one year, should consider seeking the collaboration of former mentors.
If that means getting out of a slump and back on track, in the process regaining confidence and enthusiasm, I think it would be foolish not to do it.
Again, I think that hitting the ground running and ensuring a reasonably consistent scientific output is the most important thing. In time there will be plenty of opportunities to differentiate one’s own research program from whatever one “inherited” as a trainee, by thinking of new directions and/or extensions, giving it a different spin or flavour, and so on.
 This post is not really about that, but I am still going to make the following observation, based on my 15-year experience as a faculty in North America: the same, identical tenure application will be evaluated in vastly different ways, depending on a number of factors. These include, and are not limited to, the type of institution (research intensive versus mostly teaching), its reputation, the prestige enjoyed by the department of affiliation of the applicant (both within the institution itself, as well as vis-a-vis departments at comparable institutions), and also the historical context and the particular moment in time at which the application is put forward. In fact, I have seen tenure bids which I regarded as comparably strong, being received vey differently, at my own institution, within a few years of one another.
 There is obviously a considerable degree of unfairness in all that, for the assumption that anything that someone did as a graduate student or as a postdoc, must have been to a significant extent inspired, directed and even carried out by his/her supervisor(s), can frequently be erroneous. Still, it is an assumption that people will almost invariably make, mostly because it is generally quite difficult to disentangle the original contribution of any individual participant to a collaborative research project.
 After all, every probationary faculty, no matter how unproductive, could be granted tenure based on argument that “they are not quite there yet, because they are working on something earth shattering — when they do succeed, they will bring prestige to our institution”. It is objectively difficult to take this kind of rhetoric seriously. At that rate, why have tenure review at all ?
 Yes, I suppose that means that, for a few years, I shall be “competing” with my former students or postdocs, so to speak, because they will be continuing on with the same science on which they did their graduate or postdoctoral work in collaboration with me, and there is a pretty decent chance that I (and my subsequent students) will keep working in the same area as well. I do not believe that there is any obligation on the part of either one to avoid “stepping on the other’s toes”, nor should there be any expectation of that. Scientific problems do not “belong” to any one, and fair competition is always a good thing, both for science and for the scientists involved (one word: citations).