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C00002 00002	presid.1[f83,jmc]	First AAAI presidential message
C00007 00003	  The exceptions that come to mind are (1) Barbara
C00008 00004	What follows is the President's message.  I'll shorten  it if there
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presid.1[f83,jmc]	First AAAI presidential message
see e83.in[let,jmc]/355p

	Artificial intelligence research in America and the rest of the
world is unbalanced.  There is too little basic research in relation
to the amount of applied research.  The ratio of basic to applied
research seems to be smaller than in the older sciences.

	Even people entirely motivated by applications and not at all
by scientific curiosity should be concerned that
the present state of AI as a science won't support all the
expected applications.

	I see two reasons for this situation.

	1. Government agencies, especially in the early seventies,
were excessively biased towards applications.  The largest
supporter of AI research has been DARPA, and the Mansfield Amendment
in 1970 required the Defense Department to justify all supported
research as having a direct military application.  Often this
was interpreted fairly liberally, but nevertheless suppport of
basic research in AI was drastically reduced.

	About the same time NSF also developed a strong applied
bias.  This was less harmful in the more established sciences where
there were elder statesmen in a position to defend basic research.

	2. However, the main reason seems to me to be internal to
AI itself.  Basic research in AI has been very difficult.
It is not clear what is the appropriate theory, and it has been
difficult to design experiments that were genuinely informative except
perhaps negatively.  When a program fails to achieve its goals for
other reasons than bugs, we conclude that our understanding of the
intellectual mechanisms required for the task is inadequate.
We shall elaborate these points.

	I have argued elsewhere for dividing the theory of AI into
epistemology and heuristics.  Epistemology concerns the facts about
the world, how this information can be represented in a computer,
and what are the appropriate modes of reasoning.  Heuristics concerns
how to do the necessary pattern matching and search in a sufficiently
efficient way.

	Basic research in AI should involve problem domains chosen
for the scientific knowledge they will give rather than immediate
application.  Geneticists experiment with fruit flies and bacteria
not because they wish to improve fruit flies or bacteria but because
their genetic mechanisms are most accessible to experiment.
The Moscow computer scientist
A. S. Kronrod called chess the Drosophila of artificial intelligence.
Already about 1950 Turing pointed out the advantages of chess as
a domain for AI.  It admits many kinds of heuristics, and it permits
direct comparison with human performance.
Nevertheless, the use of chess as a scientific domain was discouraged
as frivolous, and programming chess turned mainly into a sport with
a few exceptions.

	To prove my point about the neglect of basic research in AI
I should say what the main problems are and recount how little activity
is taking place.  I'll try, but one of the reasons why the fundamental
problems aren't worked on more is that no-one can say precisely what
they are.
  The exceptions that come to mind are (1) Barbara
Liskov's thesis on expressing the information in chess books about
how to win certain endgames as a partial ordering between positions.
(The chess books certainly don't give programs)
(2) David Wilkins

	The identification and programming of the intellectual mechanisms
required to achieve human-level intellectual performance or to behave
intelligently in specific problem domains.

What is a pattern?

1. quote Doyle

2. the mathematical and empiricist deviations

What follows is the President's message.  I'll shorten  it if there
is a space problem.  Note that the formulas  n↑2  and  n log n
need to be printed properly.  I would be glad to look at the TEX version
and possibly tinker a bit more.

Here is the harangue that will appear in AI Magazine; hope it helps.
	AI NEEDS MORE EMPHASIS ON BASIC RESEARCH

	Too few people are doing basic research in AI relative to the
number working on applications.  The ratio basic/applied is less in
AI than in the older sciences and than in computer science generally.
This is unfortunate, because reaching human level artificial intelligence
will require fundamental conceptual advances.  Even the applied goals
proposed by various groups in the U.S., Europe and Japan
for the next ten years are not just engineering extrapolations from
the present state of science.  Their realization will require more basic
research than is now being done.

	Jon Doyle put it this way in a recent net message. "... tentative,
but disturbing conclusion: that the students interested in AI are not
very interested in fundamental questions, open problems, and long term
research, but instead are eager to get in on big, build-it-now
projects in expert systems and natural language interfaces."  He
was definite about CMU, but he conjectured that the situation was similar
elsewhere, and I suppose student preferences are similar in different
places.

	I'll begin with a few recriminations and then try to be more
constructive.  First the Government, specifically DARPA and NSF, had
a fit of extreme "practicality" in the early 1970s.  The Mansfield
amendment required DARPA to claim short term military relevance for
what it supported, and NSF diverted much of its resources to "Research
Applied to National Needs".  The older sciences were able to resist this
in NSF but lost their DARPA support completely.  AI, which was more
dependent on DARPA than the others were, survived but wounded.  The
situation has improved in both places in recent years.

	Second the opportunities to make money have perhaps lured
some people away from research per se.  I don't really know the
extent to which this is true.  Maybe they were tired of research.

	Third much of the theoretical work in AI is beside the point
and unlikely to lead to advances toward human level intelligence.
The mathematically talented like well-defined conjectures
the wherein the mere statement of the result that has been proved or
the asymptotic behavior of the algorithm discovered wins instant
scientific recognition.
AI badly needs mathematical and logical theory,
but the theory required involves
conceptual innovations - not just mathematics.  We won't reach
human level intelligence by more algorithms reducing the complexity
of a problem from  n↑2  to  n log n  and still less by proofs that
yet another problem is unsolvable or  NP-complete.
Of course, these results are often very significant as mathematics
or computer science.

	Fourth, like many fields AI is given to misguided enthusiasms
in which large numbers of people make the same errors.  For example,
much of the present work in natural language processing seems
misguided to me.  There is too much emphasis on syntax and not enough on
the semantics.  Natural language front ends on programs that convert
between existing AI formalisms and English miss the point.
What we can learn from natural language is not how to express in English
what we already know how to express in computerese.  Rather we must
study those ideas expressible in natural language that no-one knows
how to represent at all in a computer.

	We also won't reach human level intelligence by building
larger and larger production systems involving more and more facts
all on the same level.  Of course, these systems of limited intelligence
may have substantial practical utility.

	Now that I've finished grumbling, I'll try to be constructive.

	1. People beginning their research careers should think about the
long term goals of AI and should think how to apply their own talents
in the best way.  If they can do first class basic research they should.

	2. In my opinion, the key problem at present is the formalization
of common sense knowledge and reasoning ability.  It still looks to me
that separating epistemology from heuristics will pay off.

	3. We need to think hard about how to make experiments that
are really informative.  At present the failures are more important
than the successes, because they often tell us that the intellectual
mechanisms we imagined would intelligently solve certain problems
are inadequate.

	4. We need good problem domains - the AI analog of what the
Drosophila did for genetics.  The Soviet computer scientist A. S.
Kronrod once referred to chess as the Drosophila of artificial
intelligence, because it permitted comparison of human and artificial
intellectual mechanisms.  Unfortunately, chess was discouraged as
a serious problem domain, and most chess programming is carried on
at the level of sport rather than science.  In particular, there is
little publication about the intellectual mechanisms involved, and
the race often involves merely faster hardware.

	5. I also believe there is a large payoff in a more general
analysis of the concept of pattern.

	Finally, let me cheerfully admit that general harangues
like this one are no substitute for scientific papers setting
forth specific problems in detail.

	I hope that other members of AAAI will express their own
opinions about what the basic research problems are.