School of Chemical Sciences
University of Illinois at Urbana-Champaign
Urbana, IL 61801
Note the title carefully. I cannot tell anyone how to write a research proposal that will succeed in raising money for some particular project. I can, however, recommend ways to take a good idea and so present it that it can't be funded. Furthermore, if one avoids these traps, the chances of funding improve markedly. Most of this isn't new. An article to read is:
Donald J. Lisk. 1971. Why Research Grant Applications Are Turned Down. BioScience 21: 1025-1026.
I believe there was similar advice from a different author, published in 1968, but the manuscript escapes me at the moment. In any event, this advice isn't new. It appeared AT LEAST as long ago as the "Golden Age" of science funding, and it would not surprise me if someone found similar advice from the 19th century onwards.
Here are the 5 critical points; 5 ways to write a losing proposal:
1) Propose something that's already been done (or is only a minor extension of what's been done). If you propose to continue doing what you did in graduate school, or what you did during the last 3 years of your prior grant, you'll get a yawn from the reviewers and thumbs down from the agency.
[In other words, proposals that extend previous work to a limited degree, e.g., we know that individuals in many species of birds engage in extra-pair copulations but we don't know if they do in my species, or we know that individuals breeding in small forest fragments have lower nesting success than those in larger fragments but we don't know if they do in my state, are probably less likely to be funded than proposals that describe more original work.]
Antidote: propose something new.
2) Write a review article instead of a proposal. Thirteen pages of review followed by 2 pages of new ideas or 11 pages of review, 2 pages of preliminary results, and 2 pages of new ideas will not get you any money.
Antidote: write a review article and get it published. Refer to that article in the first few pages of your proposal, highlighting those points which lead you to your new problem. Then spend most of your time saying what you'll do, how you'll do it, why it matters, and why the taxpayers (or corporate sponsors or whoever) are better served by giving you money than using it themselves.
3) Have a solution looking for a problem. This is why method developers have trouble getting grants.
Antidote: find some REAL problem. Propose a viable solution to that
real problem. It may well be that developing a method will help solve that
problem. But, solving non-existent problems is not something many people
wish to spend their money on.
4) Find someone else's bandwagon and climb on board.
Antidote: find a sufficiently important problem that you'll establish
next year's bandwagon. Then you'll have other people chasing you (and your
grant) rather than the other way 'round.
5) Be blinded by subfield boundaries. Lines such as "to do this would require theory, and I'm an experimentalist." "I'm no biologist, so I'll develop this method in the hopes a biologist might find it useful some day." will do wonders to increase your number of declined proposals.
Antidote: find a co-investigator who can fill in those parts of the science for which you aren't qualified, or at least someone who can say they'll provide those small pieces of the project which require outside expertise. This also helps with 3) above. "But the only grants that count are ones on which I don't collaborate," you justifiably say. Funny -- if the particle physicists had said that between 1930 and 1993, there would be no Tevatron, SLAC, or CERN. "Small Science" hasn't caught on to this yet. Don't duck this tightrope -- learn the constraints you're working under and play by the rules. You can't change the rules 'til you've won under someone else's rules.
Related topic: choosing a research area is tricky. 1) above hints at the problem. Take a look, for example, at the Winter 1991 issue of American Heritage of Invention and Technology. There are articles on the transition from steam locomotives to diesels, and on the change in the late 1960's from ever-higher-performance aircraft to ever-more-economical aircraft. The connection: don't do research on mined out areas. Research on buggywhips in 1910, or human factors in the design of Morse telegraph keys in 1965, or on noise suppression in teletype assemblies today won't cut it. Note, however, that research on improvements in individual transportation, human factors in typing, and ergonomics of computer systems are all in the same areas as the Guaranteed Losers, but are more relevant to their respective times.
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