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Humanist Archives: Nov. 10, 2018, 8:26 a.m. Humanist 32.176 - releasing the hares

                  Humanist Discussion Group, Vol. 32, No. 176.
            Department of Digital Humanities, King's College London
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        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" [1], 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

[1] http://www.cs.virginia.edu/~robins/YouAndYourResearch.html (and 

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.

[2] 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

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