The Young Scientists' Network Digest
                  5 Jul 1994          Number 1549

     A news digest for discussion of issues involving the employment
      of scientists, especially those just beginning their careers

~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

                             DISCLAIMER

     Opinions and information appearing in this newsletter are those
       of their contributors, not of YSN's advisors and volunteers.

----------------------------------------------------------------------

Date: Sun, 3 Jul 94 23:48:54 -0400
To: ysn@ren.salk.edu
Subject: #1 YSN GL: Recipes for failure in grant writing

Alexander Scheeline has provided the YSN GL with the following
contribution which all new grant writers may want to consider
compulsory reading. Thanks Alex for lending a helping hand! 
Hopefully we may receive other valuable contributions of help
from 'YSN old-timers'.
Barry J Hardy


HOW TO WRITE A LOSING PROPOSAL

Alexander Scheeline
School of Chemical Sciences
University of Illinois at Urbana-Champaign
Urbana, IL  61801

Scheeline@c.scs.uiuc.edu


Note the title carefully.  I can not 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, "Why Research Grant Applications Are Turned Down,"
_BioScience_, V. 21, 1025-1026 (1971).

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.  


Antidote: propose something new.

2) Write a review article instead of a proposal.  13 pages 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.  Proposea 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.



This document may be freely distributed, provided attribution to the
original author is given, and any editorial changes by subsequent readers
are indicated by ellipsis (... for omissions) or brackets [insertions go
here].