michael_nielsen

Most of my favourite papers are field finding.

Turing's paper on computing is field finding. So too are Feynman and Deutsch's papers on quantum computing.

By comparison, the early Sanger (et al) sequencing papers were field founding - they started a field - but not field finding, since it was obvious for many years prior that sequencing DNA (or RNA) was a good idea. Sanger et al were the first to really figure out how to do it.

Obviously, the distinction isn't black & white. Eg in Turing's case you can argue that the problem of developing a notion of effective computation was implicit in earlier work (eg Hilbert). But Turing understood the big picture problem superbly, & made it obvious this was a field

I've seen and heard lots of discussion of field founding, usually in a Sanger-like context: figuring out how to make progress on big problems that are more or less obvious to everyone.

But I've heard very, very little about field finding. And I believe field finders are (a) incredibly valuable for science; and (b) dramatically undervalued by existing institutions.

It's surprisingly hard to think of a field finding paper that was supported by a grant. It's a case where you by definition _can't_ make a strong prior argument for the work; in fact, the whole job is to figure out the basic concepts that will make such an argument even possible

Eg you can't motivate the founding paper of computer science by referring to some prior notion of how important computers are; you're actually trying to invent the notion of computers, & argue for its importance.