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Comments on "The State of Technology in Artificial Intelligence" by
Duda, Nilsson, and Raphael

	As a summary of the state of research in artificial intelligence,
this paper reminds me of a scene in a Western novel in which the bad
guys are making their victim dance by shooting at his feet.  Each
one-paragraph capsuled accomplishment represents one leap in the air
in response to a demand for a list of the breakthroughs accomplished in
the last fiscal year.  The style has evolved by survival of the fittest
in an atmosphere of competition for bureaucratic favor.  As such it allows
the recipient to read the article between telephone calls at thirty
seconds per paragraph.  At the end he can't decide whether it is a total
fake, great work or somewhere in between, but he knows he has to make
up his mind in a few months on whether to fund it but also knows he
can't or won't spend more than another hour in understanding it better.
What he %2can%1 do is point to the seventeenth accomplishment and ask his
underlings, "Tell me more about that one" or "What are we doing now
different from what my predecessor was supporting three years ago?".

	Different styles of presentation have been tried but haven't shown
themselves fit to survive.  The trouble with a general %2Scientific American%1
style essay on artificial intelligence is that if honestly done, this
year's essay reads very much like last year's; I'm still getting royalties
for the book version of a %2Scientific American%1 article I wrote eleven
years ago.  The trouble with concentrating the explanations
on a single topic is that it's
very risky; whole programs get shot down if a Congressional staffer or
an other official isn't turned on.  Once upon a time, DoD supported
research in on a less hectic basis, remembering that rare breakthroughs
sometimes produce decisive military advantages - like radar, code breaking,
the jet engine, or the atomic bomb.  Now three breakthroughs per year per
project is the norm.

	The authors of this report have a wide acquaintance with AI
work, and there is good evidence they have read all the works to which
they refer.  Nevertheless, though I have read less, I cannot accept their
picture of the field or its history.

	As they correctly report, much AI research consists of a sequence
of pilot projects.  The project need not have a directly applicable goal,
but it must show a capability analogous to something that would be
applicable.  Projects, whether theoretical or experimental, aimed only at
discovering facts are difficult to support except as a sideline.

	I don't agree with the history of artificial intelligence
presented in the paper.  The phases depicted arose partly as fads
and were amplified by the need to write a new general picture
for the sponsors every two years.  At the risk of being out-of-date,
I will claim:

	1. We have not learned all we can from some of the problems
which were attacked experimentally in the late fifties.  There is
still more to be learned from chess, from theorem proving,
and learning, for example.

	2. The tendency for each research project to build a complete
system with a "natural language" front end, a collection of domain
dependent experts, and an "explainer" leads to superficial work -
even if it does make for better demonstrations.

	3. It is important for artificial intelligence to isolate
technical problems within the subject for separate treatment.  For
example, the separation of the AI problem into epistemological
and heuristic parts is necessary.

	4. The field is now 95α% experimental and 5α% theoretical
if one excludes theoretical work that isn't really about AI at all.
It should be about 20α% theoretical.

	5. The field requires a renewed concentration on basic
research.

	6. The connections of AI with philosophical logic will
make a large contribution to both fields.

The file is AI[W77,JMC] at SU-AI and this draft was PUBbed on {date}.