What Makes a Good Project, or Not

This is one of the key questions in the career of a professional scientist. How do you come up with ideas? How do you choose which ones to pursue? A few people have impeccable taste for new projects and open up completely new research vistas more than once in their career: Andre Geim of graphene fame is one such example; Anthony Leggett, Pierre-Gilles De Gennes, and a two-time Nobel laureate John Bardeen (type-I superconductivity, transistor) also come to mind.

But let’s talk about us regular, mortal academics, who do good work and publish in reputable journals, and how we train our students to pick projects to work on once they are independent.

I have a couple of anecdotes from my advising past, and invite you to share your own in the comments.

Moving to a new field

Moving out of one’s comfort zone and into a new field can be intellectually invigorating and result in highly original and impactful work. As one colleague says, you have to read a lot, but not too much. You don’t want to read so much that you, too, get entrenched in the field’s cannons and lose the ability to think your own thoughts. But, there is such a thing as reading too little. It’s important to develop a real respect for the field, to learn about where the state of the art is and what the real open problems are.

Some time ago, a student who’d just started helping another former group member wrap up some papers came to my office full of ideas. The problem was, those ideas were clearly the first thing that popped into his mind and something that the field had dealt with decades ago. I tried to tell him as diplomatically as I could that those ideas were likely correct, so he was obviously getting what he was reading, but that the ideas were simply not novel enough or interesting enough to people right now, as the field had moved way past simple, quick-and-dirty models to much more sophisticated and accurate approaches and the cutting edge now lay elsewhere. He admitted that these were literally the first things that he thought of when he was only starting to read up.

Being a misunderstood genius… Or not

Each research group develops a specific style — not just in how they write and present their work but in how and why they choose the problems they tackle — and the style is strongly influenced by the group leader. I am not one who keeps students around for 8 years without a paper because I don’t want anything less than a Nature publication; far from it. Students in my group publish well, but there is definitely a bar to what I will agree is publishable with my name on it. There are colleagues in my general field who churn minimal publishable units that I never would, but I allow that it’s not just the question of their style or scientific taste; it may be an issue of external pressure related to salary, promotions, grants… Who knows? Basically, setting aside the stuff that I won’t work on because I think it’s misguided or wrong (hopefully nobody wants to work on that), there is also the stuff that I won’t work on because I think it’s too incremental, too boring (to me), or otherwise just not a good investment of effort and money (e.g., the field is moving too quickly for anyone without an army of postdocs).

Occasionally, I have a student who wants to do something that I don’t think is worth doing. We discuss the pros and cons and often the student agrees that something related but more “meaty” or otherwise clearly publishable would be a better use of their time. But, on occasion, a student  is quite enamored of an idea that I don’t approve of (not because it’s wrong, but because it’s too small potatoes, or not very novel, or yes — boring science) and thinks that I am standing in the way of their genius; the student might become relentless about trying to publish this work I don’t approve of.  This is when I do what I call, to myself and I suppose now to everyone who reads this blog, “polishing a turd for educational purposes” — give the student’s manuscript the best chance it’s got in terms of improving the text and layout and have the student submit the draft for publication in a venue that is suitable for the topic and type of work. I repeat until the end that I expect we will get creamed in review, as the work is just not complete enough or not novel enough, and sure enough, so far we’ve gotten creamed 100% of the time when I said that we would.  Polishing a turd for educational purposes is not the best use of my time (I could be polishing an actual publishable paper or a new proposal instead), but the educational part is quite important — sometimes, this seems to be the only way to get a strong-willed student to see that if I cannot be persuaded of the importance and novelty of the submitted work, and I have a vested interest in publishing the work of my students, then it’s very unlikely that other people can. The PhD advisor is usually the first line of defense against overblown results; I’m not saying it can’t happen that the PhD advisor is totally wrong and the student is indeed a genius, but it hasn’t happened to me yet, and probably doesn’t happen very often in general.

(To be continued…)

Please share your own thoughts/experiences about choosing well or poorly what to spend your scientific energy on.


  1. A related question: what do you do when certain things that you are not too excited to work on but close to your own work, are easily fundable? Would you go ahead and work on them?

    I totally sympathize with you on the strong-willed student. I have a senior student like this, who has been working on something extremely theoretical and uninteresting for the past year or so. I repeatedly told him that I don’t want to work on it — this is a paper people would have appreciated 10 years ago but now the field has moved on; but if he chooses, he can do it on his own time while he TAs but I will not be on the paper, so that’s what he’s been doing. Finally he submitted a paper on this work to the most theoretical venue in the field, and sure enough, it got resoundingly rejected, because guess what? too uninteresting. In the meantime, he has been ignoring problem after problem that I suggest to him. It’s a pity really, because he is a very good student and has academic ambitions; this is all just a gigantic waste of his time and potential — and if he put in the time and energy to the problems I suggested, we could have written some very nice papers. But at this point, I see no other way than to get him to graduate as soon as I can so that he can be out of my hair and I don’t have to deal with him anymore. Oh well.

  2. Hi n^6 :-), regarding going after the easily fundable grants for work that you are not too excited about: it depends on how flush you are, how important getting money (any money) is for your work (e.g., big experimental lab vs theory), who this “easy money” is from (is it from an agency where, after you get the money, you have lots of freedom in terms of what you do with it versus an agency that will expect detailed quarterly reports and exert a lot of oversight), how far it is from what you really want to do, and how easy it really is (in my experience, there is no really easy money for science).

    I will say this: I have had some “easy money” as part of a center for the work we really weren’t particularly interested in or had much expertise in, and it turned out that the work was quite complicated to do (not helped by lack of interest or expertise) and it took us a long time to get results as the learning curve was quite steep. Other people (some of my well-funded contemporaries) report thinking initially that going after the easy pots of money was the way to go even though they lacked genuine interest, and then it turned out that they were stuck having to do the stuff they never wanted to do… Which is certainly better than closing up shop if you need money and there is no other source, but definitely not what you want to spend your time on if you also have funded projects that you truly enjoy working on.

    I don’t know. We can’t be snobs and turn our noses up and away from funding whenever it isn’t specifically tailored to our heart’s desires. On the other hand, we’re not hired guns who will do whatever is needed in exchange for money; sometimes the rationale behind a funding call is misguided. I’d say if you can envision doing at least something you’d really enjoy under the project umbrella, then go for it. Otherwise, don’t. If you are too far removed in terms of expertise (and not really excited to develop said expertise) or just not interested in these types of projects, I don’t think it’s worth it, and the lack of genuine interest sometimes — often? — comes across in proposal writing.

  3. I’ve had a really successful collaboration for the past four years that has allowed me to delve into a field that is a couple steps removed from my own. The good news is that this field seems to be much more fundable than my own, which is a huge plus. I’m not sure what I actually bring to the collaboration, since I started out not knowing the field at all, but for whatever reason it seems to work. Your point about bringing an outsider’s perspective resonates with me in this case – I think my minimal knowledge has allowed me to simplify questions and help the group develop questions/papers that are broader reaching than they might have otherwise been.

  4. I struggle the most with technique-driven projects where the internal logic is, “No one in the literature can do X. Let’s do X, and see what happens.” These can be very frustrating to trainees, especially relative to a project like “What’s the minimal model to explain Y?” Of course, there is always some motivation for why X is worthwhile to the field – but the immediate application to an experiment is less clear. That can make it difficult for trainees to make choices about relevant approximations, etc.

    I got so irritated with this sort of problem as a graduate student – even though I eventually got some nice work out of them- but now as a mentor I end up suggesting these sorts of projects, and see trainees get frustrated too! Have you had this experience?

  5. Rheophile, in my field it is very, very hard to get funding for projects that focus on methods. Very hard, almost impossible, except under special grant calls. However, we do develop techniques, but they are always in the context of trying (at least nominally) to solve a clear and compelling outstanding problem, with some well-articulated goalposts along the way that are also interesting in their own right. This has served my group well, in that it enabled me to undertake these broad and long-term technique developments that span multiple students, where every couple of years we are able to solve a cool specific problem with what we’ve developed thus far. To me, this development of a technique sort of as an afterthought (of course it’s not, to me that has always been where the fun is) and really bringing out the specific uses in the shorter and medium term has been helpful both for getting funding (we’ll solve this problem for you if you give us money!) and for student satisfaction (they get papers along the way).

    Did this address your question somewhat or am I off?

  6. xyk – thanks! I agree, that does sound ideal – a good link of methods and applications. It seems either that your field has very different funding tendencies (worrisome, since I don’t think we’re that far apart – hard condmat vs bio-soft?) – or my advisors have been not great about communicating their intended purpose to their trainees! I guess I’ll find out which is true when I start submitting my own grants this next round.

  7. “He admitted that these were literally the first things that he thought of when he was only starting to read up.”

    Embarrassed to say that I discovered I did something close to this as a young PI entering a new field. To be a bit too charitable to me, the field’s version wasn’t very rigorous and was couched in the oddest language that kept the relevant papers from turning up in my searches. Nonetheless, I felt like a dumba$$ when others pointed out how much had already been done after one of my talks. It was also a learning experience because I had had a postdoc working in this area and had expected him to scour the literature more deeply too, but he had read even less than me (though he knew it was new for both of us) and was doubly disappointed. Basically kvetched about it for a year instead of focusing on the good questions and techniques we could still bring to the field.

    The experience has made me very humble. I now make it clear to all trainees that they are responsible for the lit review. I of course try to read everything also, but it can become too much. (Curious how other PIs negotiate this sort of responsibility–I am in a more biological subfield, so maybe the volume is highe rthan in the physical sciences.)

  8. Tired prof, one of the hardest parts of the job is learning to what degree to trust the work done by graduate students. I find that, by the end of their PhD, most have a pretty strong grasp of the literature in their field; however, while they are getting there, it’s a struggle. And I would say that, for most students and during most of their PhD studies, if I do a deep literature dive (as I do when I write grants), I always find important papers that they missed. I would say that only a minority of students show an aptitude to quickly and accurately map out the state of the art in a new field — I say it’s an aptitude because no one taught me how do it, and while I try to teach my students, most rely too much on automatic searches; that’s simply not enough; you have to follow citation trails and map out quickly which group are the most important ones and then see the threads that emerge from their work… Basically you have to look, really look at a lot of papers, and a successful mapping of the literature involves all this: which journals are good, which papers are highly cited, which threads came from those highly cited papers, who are the key contributors, what are the open problems that the field agrees are worth solving… The best students are able to grasp how to do this early on, so when I check their work/literature surveys, I find very few important things they missed. For most students, however, I think it may be a combination of not wanting to put in the time/thinking it’s boring/why bother if I will clean up after them anyway and not really seeing how this all fits together.

    I agree it’s quite tiring to follow disparate bodies of literature. In my group, there are presently about four nearly nonoverlapping projects. I have made peace with the fact that there is no such thing as being fully caught up (it’s only a fleeting state); I do deep literature dives when it’s time to write a proposal or a paper, and in the meantime I assume the students are doing a passable job that I will eventually have to check; I also get table-of-contents alerts from a number of journals, so I can at least scan the titles. I accept that I might miss something, but it’s usually not something major and not for very long. We do what we can.

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