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C00002 00002	%lighth[w90,jmc]		Lighthill after almost 20 years
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%lighth[w90,jmc]		Lighthill after almost 20 years
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\title{Lessons from the Lighthill Flap}


	Martin Lam gives us a British civil servant's view of
the Lighthill report and subsequent developments.  My
comments concern some limitations of this view that may be related
to the bureaucratic background of the author---or maybe they're
just a scientist's prejudices about officials.

	Lam accepts Lighthill's eccentric partition of AI
research into Advanced Automation, Computer-based Studies of the
Central Nervous System and Bridges in between.  This
classification wasn't accepted then and didn't become accepted
since, because it almost entirely omits the scientific basis of
AI.

	AI didn't develop as a branch of biology, based on either
neurophysiological or psychological observation, experiment and theory.
It also isn't primarily engineering, although an engineering
offshoot has recently developed.
Instead it has developed as a branch of applied mathematics and
computer science.  It has studied the problem of systems that
solve problems and achieve goals in complex informatic situations,
especially the {\it common sense informatic situation}.  Its experiments
and theories involve the identification of the intellectual mechanisms,
the kinds of information and  the kinds of reasoning required to achieve
goals using the information and computing abilities available
in the common sense world.  Sometimes this study divides up
neatly into heuristics and epistemology, and sometimes it
doesn't.  Even connectionism, originating in a neurophsyiological
metaphor, bases its learning schemes on mathematical considerations
and not on physiological observation.

	Lam's inattention, following Lighthill, to the scientific
character, goals and accomplishments of AI goes with a narrow
emphasis on short range engineering objectives.  Maybe this is
normal for British civil servants.  Nor is Lighthill the only
example of a physical scientist taking an excessively applied
view of scientific areas with which he is unfamiliar and finds
uncongenial.

	The Lighthill Report argued that if the AI activities he
classified as Bridge were any good they would have had more
applied success by then.  In the 1974 Royal Institution debate on
AI, I attempted to counter by pointing out that hydrodynamic
turbulence had been studied for 100 years without full
understanding.  I was completely floored when Lighthill replied
that it was time to give up on turbulence.  Lighthill's fellow
hydrodynamicists didn't give up and have made considerable
advances since then.  I was disappointed when BBC left that
exchange out of the telecast, since it might have calibrated
Lighthill's criteria for giving up on a science.

	My own opinion is that AI is a very difficult scientific
study, and understanding intelligence well enough to reach
human performance in all domains may take a long time---between
5 years and 500 years.  There are fundamental conceptual problems
to be identified and solved.

	Many of these problems involve the expression of common
sense knowledge and reasoning in mathematical logic.  Progress
here has historically been slow.  It was 150 years from Leibniz
to Boole and another 40 years to Frege.  Each advance seemed
obvious once it had been made, but apparently we earthmen
are not very good at understanding our own conscious mental
processes.

	An important scientific advance was made in the late
1970s and the 1980s.  This was the formalization of nonmonotonic
logical reasoning.  See (Ginsberg 1987).  Not mentioning it in
discussing the last 20 years of AI is like not mentioning quarks
in discussing the last 30 years of physics, perhaps on the
grounds that one can build nuclear bombs and reactors in
ignorance of quarks.  Logic needs further improvements to handle
common sense properly, but no one knows what they are.

	The Mansfield Amendment (early 1970s and later omitted
from defense appropriation acts) requiring the U.S.  Defense
Department to support only research with direct military
relevance led to an emphasis on short range projects.  While the
pre-Mansfield projects of one major U.S. institution are still
much referred to, their post-Mansfield projects have sunk
without a trace.  I don't suppose the Lighthill Report did much
harm except to the British competitive position.

	Government officials today tend to ignore science in
planning the pursuit of competitive technological advantage.
Both the Alvey and the Esprit projects exemplify this; DARPA has
been somewhat more enlightened from time to time.  It's hard to
tell about ICOT, but they have been getting better recently.
Some of the goals they set for themselves in 1980 to accomplish
by 1992 require conceptual advances in AI that couldn't be
scheduled with any amount of money.  My 1983 paper ``Some Expert
Systems Need Common Sense'' discussed this.

	At present there is a limited but useful AI technology
good enough for carefully selected applications, but many of the
technological objectives people have set themselves even in the
short range require further conceptual advances.  I'll bet that
the expert systems of 2010 will owe little to the applied
projects of the 1980s and 1990s.

\noindent References:

\noindent
{\bf Ginsberg, M. (ed.) (1987)}: {\it Readings in Nonmonotonic Reasoning},
Morgan-Kaufmann, Los Altos, CA, 481 p.

\noindent {\bf McCarthy, John (1983)}: ``Some Expert Systems Need Common Sense'',
in {\it Computer Culture: The Scientific, Intellectual and Social Impact
of the Computer}, Heinz Pagels, ed.
 vol. 426, Annals of the New York Academy of Sciences.
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