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From: Laws@KL.SRI.COM.UUCP
Newsgroups: comp.ai.digest
Subject: Gilding the Lemon
Message-ID: <12346288066.15.LAWS@KL.SRI.Com>
Date: Thu, 29-Oct-87 03:25:55 EST
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Posted: Thu Oct 29 03:25:55 1987
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Tom Dietterich suggests that AI students should consider doing
critical reviews and rational reconstructions of previous AI
systems.  [There, isn't a paraphrase better than a lengthy
quotation?]  I wouldn't discourage such activities for those
who relish them, but I disagree that this is the best way for
AI to proceed AT THE PRESENT TIME.

Rigorous critical analysis is necessary in a mature field where
deep understanding is needed to avoid the false paths explored
by previous researchers.  I don't claim that shallow understanding
is preferable in AI, but I do claim that it is adequate.

AI should not be compared to current Biology or Psychology, but
to the heyday of mechanical invention epitomized by Edison.  We
do need the cognitive scientists and logicians, but progress in
AI is driven by the hackers and the graduate students who "don't
know any better" than to attempt the unreasonable.

Progress also comes from applications -- very seldom from theory.
The "neats" have been worrying for years (centuries?) about temporal
logics, but there has been more payoff from GPSS and SIMSCRIPT (and
SPICE and other simulation systems) than from all the debates over
consistent point and interval representations.  The applied systems
are ultimately limited by their ontologies, but they are useful up to
a point.  A distant point.

Most Ph.D. projects have the same flavor.  A student studies the
latest AI proceedings to get a nifty idea, tries to solve all the
world's problems from his new viewpoint, and ultimately runs into
limitations.  He publishes the interesting behaviors he was able
to generate and then goes on the lecture circuit looking for his
next employment.  The published thesis illuminates a new corner of
mankind's search space, provided that the thesis advisor properly
steered the student away from previously explored territory.

An advisor who advocates duplicating prior work is cutting his
students' chances of fame and fortune from the discovery of the
one true path.  It is always true that the published works can
be improved upon, but the original developer has already gotten
80% of the benefit with 20% of the work.  Why should the student
butt his head against the same problems that stopped the original
work (be they theoretical or practical problems) when he could
attach his name to an entirely new approach?  

I am not suggesting that "artificial intelligence" will ever be
achieved through one graduate student project or by any amount
of hacking.  We do need scientific rigor.  I am suggesting that we
must build hand-crank phonographs before inventing information
theory and we must study the properties of atoms before debating
quarks and strings.  Only when we have exploited or reached impass
on all of the promising approaches will there be a high probability
that critical review of already explored research will advance the
field faster than will trying something new.


[Disclaimer:  The views expressed herein do not apply to my own
field of computer vision, where I'm highly suspicious of any youngster
trying to solve all our problems by ignoring the accumulated knowledge
of the last twenty years.  My own tendency is toward critical review
and selective integration of existing techniques.  But then, I'm not
looking for a hot new Ph.D. topic.]

					-- Ken Laws
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