Filed under: Uncategorized | Tags: Byzantine agreement, distributed computing, grants, theory
The process of grant writing was completely opaque to me when I was a grad student. As a faculty member, I now take the position that grant writing is intrinsically important, and that all grad students should learn something about it in order to get insight into the long-term planning process for doing research. For this reason, it’d be nice to see more examples of funded grants publicly available.
Last January, I posted a one page project summary for one of my funded NSF proposals. This year again I was lucky enough to have a proposal funded and I’m posting the one page summary below. I hope that some readers find it useful.
Great post today on the Tomorrows-Professor Mailing list – the advice is clearly applicable to any mathematical or scientific discipline. It took me surprisingly many years to realize this secret, but now it is the first thing I think about in my research. I’m including the post below in its entirety.
The Astonishing Secret to Getting Jobs, Grants, Papers, and Happiness in Biomedical Research
I didn’t notice at the time, but there was a point in my life when I more-or-less stopped asking successful scientists how they did it, and someone asked me. And while I offer neither evidence nor assertion that I am successful (indeed, I think I have a great way to go), the fact that I somehow can continue to do this, and occasionally be asked about it, might be regarded as a kind of success. There are some of us who mark success by tenure (a concept that serves as high comedy among my friends who are in business), “impact factor” (ditto), or the recognition of our peers (which is a wonderful thing, but not why I embarked on this career). But I’m going to go with the first definition: getting to do this thing we do, biomedical research, for now and for the foreseeable future.
But like many of my closest colleagues, for a long time I felt like the farm boy Wesley, who was kidnapped by the Dread Pirate Roberts from the movie “The Princess Bride” (which, if you haven’t seen, will be far more useful for your scientific career than anything I can offer here). Every day, Roberts would say “Goodnight, Wesley, I’ll probably kill you in the morning.” Wesley studied hard at swordsmanship and other piracy skills, and one day, when his captor retired, Wesley was given the ship and the title, and became the Dread Pirate Roberts himself. More or less, this is what happened to me, without the pirate part, and my mandate here is to try to tell those of you who may be looking for some success yourselves how you might do this, too.
So here goes. If you are committed to this path, and want papers, grants, and employment for now and tomorrow, I can sum up in two words what it is that is asked of you, and really, everyone who works in science: Astonish us. That’s it. (There is a maxim that says, “If it fits on a bumper sticker, it isn’t true.” While I generally ascribe to this, it does not apply in this particular case. That said, no, I do not have this on my car’s bumper. It might encourage the wrong sort of driver.)
Really. Look at it this way: When I have a great stack of grants to review, I know that only one in ten or so will likely be “F’ed”. (On U.S. study sections, we are not allowed to say the word “Funded.” Somewhat foolishly, we say “F’ed,” and we know what it means. Such is the way of government. It also lightens the mood when we are reviewing grants. Of course, most proposals will be “F’ed,” which in this context means “Not Funded.”) But if in an astonishing proposal the data look compelling, if the approaches are sound, and if the experiments will most likely work, and in so doing possibly change my thinking about the universe (okay, my little corner of the universe) then it will move to the top of the stack. It has to. I have to do whatever I can to make sure it gets done.
I hear a line of advice all the time that I can confidently tell you is nonsense. It goes like this: “In order to get your grant supported, it has to be letter perfect, with absolutely no mistakes, and every experiment you propose has to already be done.” Don’t believe this, it just ain’t so. We get this advice from folks who don’t get their grants supported (and hey, I’ve been there), who see nit-picky reviews that point out every little problem, no matter how trivial. Hence the advice. But this misses the subtext. A favored application has astonished the reviewers, who can be very forgiving about mistakes, chancy experiments, and the occasional missing control if they are convinced that the work has a real chance of affecting how we think about something important.
So okay, you have to astonish us. And if you do this with what you propose, and if you follow through, great papers and a promising career will come in time. But how can you do this? Most likely, nothing in your training has ever prepared you for this challenge. Indeed, it sounds impossible. But here’s the thing: Most of you, reading this, already know the answer.
Sometime in your past, you read, saw, or heard something about the universe that astonished you, so much so that you simply needed to know more about it. And the more you learned, the more astonished you became. And this approach to knowing something amazing, which could not have been known by reason or belief or any other method, convinced you that however astonishing it all is, it is as close to “true” as we can get, in a way that satisfied you. Many people love to be astonished by all sorts of means, but this path to astonishment worked for you, and hopefully still does. It’s why you became a scientist.
The rest is relatively easy. The trick is for us to remember to apply this to our own research: Which avenues of investigation will lead us, not only to information that may be useful, but to something remarkable? Sure, much of what we do is not surprising, amazing, or astonishing, but has to be done anyway. But go beyond the drudgery? Why do we need to spend time, energy, and resources to answer a question? Somewhere at the end of the Yellow Brick Road of your efforts there must be something wondrous you can envision. If not, follow another road.
This is not salesmanship, branding, or trickery; it is not “grantsmanship.” This is at the most fundamental core of what we do, as humans, following our evolutionarily selected impulses to explore our world, in this case with the technical and conceptual tools available to us as scientists. And there is a bonus as well. When we actually achieve our own moments of astonishment in our own research, however fleeting, these represent our real success. The sort of success we got into this to attain. The other kinds will follow, and we may not even notice.
* Douglas R. Green studies cell death and survival at the Department of Immunology, St. Jude Children’s Research Hospital, Memphis, TN. He recently wrote “Stress in biomedical research: Six impossible things,” Mol Cell, 40:176-178, 2010. He is also the author of Means to an End: Apoptosis and Other Cell Death Mechanisms, available from Cold Spring Harbor Press. He is a member of the Faculty of Cell Biology at F1000. For his latest evaluations, click here.
Filed under: Uncategorized | Tags: funding, game theory, grants, security, theory
Dear blog, please forgive me for my neglect these many, long weeks!
About this time last year, I blogged about some tips that I found useful for writing NSF proposals. It turns out that the NSF proposal I submitted last year was funded! Let’s hope that things go as well again this year. I sometimes get requests for full proposals I’ve submitted that have been funded, and like many researchers, I’m a bit uncomfortable posting an entire proposal. However, this time, in the spirit of recommitting myself to interesting and reasonably frequent blogging, I’m going to post the one page project summary for my funded proposal, and I will post it right here. I hope that some readers will find it useful.
I haven’t been posting in a while because I’ve been busy with preparing NSF grant proposals (which have shifted their deadlines this year from spring to December). In the interest of getting out a post (and procrastinating), I’m going to write today about my great passion as a researcher: grant writing. Seriously, I do sometimes enjoy the opportunity to plan out a research agenda for the next 3-5 years, and always the proposals I write do inform the research I will do in the future. Also, so far I’ve also been really lucky with grants, with a hit rate of about 60% (we’ll see how it goes this year now that we have a toddler around the house). When your grants are funded, the grant writing process is much more fun!
Here are some of the tricks that I’ve learned for good grants. Mostly these are from my experiences with NSF grants but they have been useful for other agencies. I’d love to hear about some other ideas in the comments section.
- Nail Motivation: Start with the problem you are trying to solve. Show that solving this problem has big implications, hopefully outside your own narrow area of work; and that your research will take significant steps towards solving the problem
- Nail Novelty: What is it about your approach that will cause you to succeed where others have failed? What unique ideas/tools/techniques do you bring to the problem?
- Expose a gap: As early as possible in the proposal, describe a gap in current research
- Don’t repeat: Don’t repeat text from the grant summary in the intro of your grant! This risks starting a bad precedent of the reader skipping over parts of your grant.
- Pull in the reader. Write a first sentence for both the summary and intro that is controversial, asks an interesting question, evokes strong emotions (hopefully not disgust :), etc.
- Less is More: Don’t tack on ideas or problems that you don’t really understand. The reviewers will uncover your ignorance and your grant will be skewered. The main constraint on conveying ideas is not the page length, but rather reviewers time. Expect a reviewer to spend about 30 minutes on your grant. You can really only get across a couple of clear ideas in this time. I know this from experience – whole sections of my grants have been misunderstood by reviewers in the past because I tried to cram too much in. Make it clear what the grant will not cover as well as what it will cover.
- Pictures are crucial: Spend as much time putting in 2-3 useful figures as you would writing a section of the grant
- Related Work is crucial: You’re proposal should be like an exciting conversation with the research community. Thread related work throughout your proposal – be generous with praise for great ideas, and make it clear how your efforts fit into the broader scheme. If you make the related work look exciting, your own research will look more exciting. Don’t miss anything that is remotely relevant to your work. A common way to have a grant shot down is a review like: “This proposal ignores results from the work of researcher X”.
- Technical depth: a portion of your proposal (maybe a third?) can and should be addressed to the experts. This is the place to include proofs, equations and enough technical details to convince the experts you have a good idea.
- Try to give something to the reader: teach the reader something new, include an interesting story or analogy, describe a cool problem. The reader will appreciate anything that breaks the monotony of reading grant proposals.
Some ideas about the process:
- Give a talk: I have found it useful to give a talk on preliminary results and future ideas as part of the proposal writing process. It works well to do this for both an expert audience and a non-expert audience. See what questions and ideas you get and use these to improve the proposal.
- Become your own worse enemy: you absolutely need to anticipate the 2 or 3 most devastating criticisms of your grant and then address those in the proposal
- Get feedback: Get an expert and a non-expert to spend half an hour with the grant and give quick feedback,
- Be intellectually mature: Don’t pretend you’ll solve every problem. Give credit where it is due. Be realistic about the research time line and the limitations of your technique.
- Try to write an hour a day on the grant to keep up momentum.
- Develop a style: I like to use a sort of dialect style where I describe problems and then solutions, or questions and then answers. This usually determines the broad outline of my proposal. However, there are many different writing styles and you should figure out what works best for you.