Humanist Discussion Group, Vol. 32, No. 176. Department of Digital Humanities, King's College London Hosted by King's Digital Lab www.dhhumanist.org Submit to: firstname.lastname@example.org Date: 2018-11-10 07:57:35+00:00 From: C. M. Sperberg-McQueen
Subject: starting hares and catching hares [Apologies for mis-filing the following in my baby-stepping with the new interface. So you're getting this clutch of meta-hares twice! --WM] Subject: starting hares and catching hares Date: Fri, 9 Nov 2018 11:14:42 -0700 From: C. M. Sperberg-McQueen To: Willard McCarty CC: C. M. Sperberg-McQueen You pose an interesting question and have elicited some interesting responses on the list. I seem to be in a minority, possibly a minority of one, on the subject -- possibily a symptom of incipient curmudgeonhood, or possibly just chronic out-of-step-ism. Starting hares does not in itself and without further qualification seem as valuable to me as it appears to seem to those who have responded so far on Humanist. For one thing, it is easy enough to start hares, or to ask questions no one knows how to go about answering; it is harder to start hares that are worth anyone's chasing, and harder still to start hares that anyone will know how to chase usefully. I heard once of a manager who told his people "please rid yourself of the notion that it's enough to come to me with a good idea -- good ideas are cheap, and I already have more good ideas than I have time to pursue. We need ideas that we know how to implement, and which will return our investment quickly enough to make them worth investing in." Those outside of commercial enterprises are not bound to seek quick financial return, but that doesn't mean the concept of return on investment is irrelevant, only that the measurements work differently. As Richard Hamming points out in a talk he apparently gave many times under the title "You and Your Research" , the interest of a problem or the potential utility of its solution is not a sufficient reason to work on it -- important problems are those for which a solution will be interesting or useful and for which we see some way forward. In Hamming's words: If you do not work on an important problem, it's unlikely you'll do important work. It's perfectly obvious. Great scientists have thought through, in a careful way, a number of important problems in their field, and they keep an eye on wondering how to attack them. Let me warn you, `important problem' must be phrased carefully. The three outstanding problems in physics, in a certain sense, were never worked on while I was at Bell Labs. By important I mean guaranteed a Nobel Prize and any sum of money you want to mention. We didn't work on (1) time travel, (2) teleportation, and (3) antigravity. They are not important problems because we do not have an attack. It's not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important.  http://www.cs.virginia.edu/~robins/YouAndYourResearch.html (and elsewhere) Douglas Lenat phrases what I think is a similar point in different terms . Ed Feigenbaum's influence on me: you figure that as a researcher you will have on the order of three decade-sized bets to make in your life. So you might as well make each one count.  Quoted (apparently from interview) in Dennis Shasha and Cathy Lazere, Out of their minds (New York: Copernicus, 1995), p. 234. To be sure, some hares have led us a merry chase for decades and centuries before being caught. And as Piet Hein put it, "Problems worthy of attack / prove their worth by fighting back." But though Fermat's last theorem (for example) eluded proof for a long time, it did not look unapproachable; the number of failed attempts to prove it testifies to just how approachable it looked. Popular accounts of the Wiles/Taylor proof say that the work involved a huge amount of new mathematics; I suspect that some of the failed attempts also produced important new work but cannot point to examples. I give these mathematical examples because successful proofs in mathematics do pretty much end any discussion of whether the proposition in question is or is not a theorem. In the humanities, there are plenty of hares which seem to be blessed with eternal life; take any proposition from Plato or Descartes or ..., other than those concerning physics, and you can probably start a good argument in any faculty club in the world. On a smaller scale -- Joseph Bedier's statistical argument against stemmatic textual criticism waited sixty-odd years for its definitive answer by M. P. Weitzmann (Bedier's gut feelings about the probability of two- and three-branched stemmata turn out to be wrong, and his argument collapses as a result). For another -- perhaps I'm unusual in this, but if I want interesting unanswered questions to think about and work on, it's not as though I am dependent on anyone else to suggest topics. I have "Someday" files with scores or hundreds of questions and projects, enough to fill two or three professional lifetimes, I suspect, even for someone who works faster than I do. I have the impression that open questions are useful and important in many disciplines, and that due credit is paid to those who posed them. Even after the hare is caught, they may be remembered: Fermat's name will remain attached to Fermat's Last Theorem. But I also note that whether a hare someone starts is taken seriously as identifying an open question seems to depend a lot on who started the hare. A question posed by somone who has done important work and a question posed by a talkative undergraduate will seldom have the same weight or urgency. Fermat would be known as a great mathematician even if the volume with his famous marginal note had been lost. Christian Goldbach may be remembered today only for Goldbach's conjecture, but he was a reasonably serious mathematician. The problems Hilbert listed in Paris in 1900 were taken seriously in part because Hilbert was already recognized as one of the world's great mathematicians. Many of Hilbert's problems have in fact been solved: they were problems for which attacks existed, or were found. Neither relativity nor quantum theory would have led to successful revolutions in physics if their predictions had not agreed with those of Newton to eight or ten significant figures -- essentialy to the limits of measurement -- for everyday problems involving non-relativistic speeds and non-quantum distances. Einstein asked himself what a lightwave would look like if one kept pace while running alongside it, but his contribution to physics was not just in formulating the question but in working out the ferociously difficult answer. The notes Galois made the night before he died started a lot of hares, but he also caught many of the hares he started, which partly explains why other mathematicians were interested in chasing the others. It is for this reason, or something like it, that I take what Ronald Haentjens Dekker or David Birnbaum says about data structures for the representation of text seriously, but not what some other scholars say about that topic. Jerome McGann has suggested indirectly that his rejection of SGML and XML is analogous to quantum theory's rejection of Newtonian physics. But I have sought in vain in his work for any alternative suggestion concrete enough to implement (let alone one that works better for scholarly computing than SGML and XML). I fear that from where I sit, McGann's attitude towards SGML and XML looks much more like the Flat Earth Society's rejection of Newtonian physics, or creation scientsts' rejection of geology, than like quantum physics. Starting hares is sometimes a useful service, as is sowing seed to the wind. But it is catching hares, or bringing in the wheat, that makes the harvest feast possible. ******************************************** C. M. Sperberg-McQueen Black Mesa Technologies LLC email@example.com http://www.blackmesatech.com ******************************************** _______________________________________________ Unsubscribe at: http://dhhumanist.org/Restricted List posts to: firstname.lastname@example.org List info and archives at at: http://dhhumanist.org Listmember interface at: http://dhhumanist.org/Restricted/ Subscribe at: http://dhhumanist.org/membership_form.php
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