When writing a grant proposal, do you first think of the topic? The experiments? The preliminary data? Something else?

Recently, a friend who was working on a grant proposal asked if I have the specific experiments in mind first and then come up with the framing from there, or if I have the big picture framing in mind and develop the specific experiments from there. I was a little stumped at first, then realized that was because I don’t really use either of those approaches. Instead, my initial motivation is usually preliminary data that I’m excited about and where it’s clear more work needs to be done to figure out what is really going on.

Here’s an example: As a graduate student, I carried out a study on a population where I tracked a parasite outbreak and host population dynamics and, at the same time, assayed the susceptibility of the population to that parasite at three time points. The results of the susceptibility assays were not at all what I expected at the start of the experiment:

three panels: top showing a normal distribution of susceptibility, the bottom two showing a bimodal distribution(Figure 2 from Duffy et al. 2008 BMC Evolutionary Biology)

The best explanation was that there was disruptive selection on susceptibility during the epidemic, with more resistant and more susceptible clones having higher fitness during the epidemic. There’s plenty of theory that predicts parasite-mediated disruptive selection (especially if there’s a tradeoff associated with resistance; we now know there is, but we hadn’t measured one at the time), but, at the same time, it was not what I predicted. There was also the intriguing bit shown in the bottom panel: the offspring that were produced sexually at the end of the epidemic seemed to show the same bimodal distribution that the population did at the end of the epidemic. That was even more unexpected.

These results led to so many questions: when should we expect to see directional selection for increased resistance vs. disruptive selection? And theory predicts scenarios where we would expect directional selection for increased susceptibility, even during a disease outbreak—does that happen? Does it relate to tradeoffs associated with resistance? Do those vary across environments? And what is the effect of sexual reproduction and hatching from the egg bank on the distribution of susceptibility the following spring—does it go back to a normal distribution? Do we see resistance phenotypes from prior years? And what happens between when things hatch in the spring and when disease outbreaks happen in late summer and autumn? What about predators—do they alter tradeoffs and selection?

So, when I started my faculty position, it was clear to me that this was what my first grant proposal should be on. The figure above was the central motivation for that proposal.

Things have been similar for many future proposals: There’s often a particular result that makes me think “Huh, what is going on with that?!?” That suggests a general theme for the proposal, and often there are some obvious follow up experiments, and from there it’s sort of a jumble of working on framing and experiments at the same time, all motivated by an intriguing pattern I’m hoping to understand.

It’s interesting to me that I hadn’t really thought carefully about how I approach proposals before my friend asked, and it also makes me wonder what others do. Do you tend to start with a question/topic? A set of experiments? An intriguing observation? Something else?

 

* At first, I considered titling this post, “What motivates your grant proposals?” But the honest answer to that would be “needing money to support the people in my lab and do research”, not any of the things discussed above!

** My mentors drummed into my head that we write proposals, not grants. If we wrote grants, we’d be in great shape!

7 thoughts on “When writing a grant proposal, do you first think of the topic? The experiments? The preliminary data? Something else?

  1. This is super-interesting!

    One thing that strikes me is how difficult it is to back out someone’s underlying grant development process from the papers arising from the grant (or even from the grant itself?). Reading your papers, I wouldn’t have guessed that this is your grant development process.

    Which probably just says something about me. My own grant development process is very different than yours (I’m very question-first), so what you do looks like magic to me! To the part of my brain that writes my grants, your grant development process looks haphazard, almost like waiting around hoping to get lucky and stumble across something. Which of course just shows that that part of my brain doesn’t understand your process. You know your study system well; you’ve built up a ton of background information about it over the years. Which allows you to make informed choices about what to measure next, and allows you to follow up in a productive way when your measurements reveal a surprise. It’s like you’re assembling a puzzle. You have an idea of what piece you’re looking for when you go looking in the box for the next piece. And if the piece you grab turns out not to fit, or you happen to see an interesting-looking piece very different from the one you went looking for, well, that’s fine because you can still fit those pieces in elsewhere.

    • Yes, I think that, to use your puzzle analogy, I look for the piece that seems most intriguing to me, then build the puzzle around that!

      • But of course, what you find intriguing will reflect your deep knowledge of the system, and of ecology and evolutionary biology more broadly. You’re not going to be intrigued by just *any* unexpected result. At least, not equally intrigued by any unexpected result. For some unexpected results, you’d probably go “Oh huh, that result just makes no sense. Weird. I’m going to file it away and not bother following it up in my next grant.” Like how someone solving a puzzle won’t just start building the puzzle around any ol’ randomly chosen piece, because some pieces seem like better ones to build around than others.

        Though of course, different puzzle solvers probably prefer to build around different sorts of pieces. I’m a “find the corners and edges first” person myself. And if I get intrigued by a random piece I happen to spot, it’s always a piece from some quite-distinctive part of the puzzle, thereby making it easy for me to build around. I avoid stuff like swathes of (say) blue sky until the end, and I’m terribly slow at completing them. But I can imagine that there are puzzle solvers out there who are more sensitive than I am to subtle differences in shape and coloration, who would be happy to build around a piece of blue sky if that’s what they happened to pick out of the box.

        The analogy to different types of scientists is left as an exercise to the interested reader. 🙂

        This convo now has me thinking back to philosopher Susan Haack’s work. She analogized doing science to solving a crossword. But I think my puzzle analogy is good too. 🙂

  2. Cool post! I think I do a hybrid approach–I have a set of general questions I’m interested in. As I explore promising natural systems, I look for evidence that a particular experiment might offer insight into one of my general questions…

  3. In my only successful grant – I thought of the [mathematical/simulation] experiment first, then backed out what the interesting question was behind the experiment. But the experiment answers a very obvious question, so maybe it isn’t all that different.

  4. Great questions. I wonder if the answer is relative to career stage? My first grant apps as a PhD student were more frame-based. Now, I find that I start with specific experimental designs/pilot data that I’ve developed through my work.

    • Excellent point! Yes, when I was a grad student, I think my applications were driven more at first by the big picture question I was interested in.

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