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and not delayed until the machine can learn from books how to carry on
a discourse.   <P>

I like Marvin Minsky's suggestion that the ability of a program to
learn should be proportional to what it already knows.  Such a program
when and if it is achieved, can be exploited in a dramatic
(frightening?) way.   <P>

Causality is another important research area in AI.  As our
intelligent programs, such as expert systems, begin to fail, we want
to move from "shallow" (statistical) rules toward "reasoning from
basic principles".  Several research programs are pushing in this
direction.  I believe the key here is to move toward basic principles,
a step at a time, and not to basic principles in one step.  For
example, knowledge of actions can be classified by levels of
causality.  I will try to explain this by first giving an example.  If
one holds an object in his hand five feet above the ground and
releases it, it will   <P>
<OL>

<LI> 	   Fall toward the ground <P>
	 
<LI> 	   Fall toward the ground with increasing velocity <P>
	 
<LI> 	   Fall, with its height y, in feet, governed by the equation  <br>
                          
                                                     
                    y = 5 - 16.1t^2 <br>

             with t measured in seconds <P>

<LI> 	   Fall according to Newton's law of attraction <P>

<LI> 	   Same as (3) but also accounting for air friction <P>

<LI> 	   Fall according to the laws of general relativity <P>

</OL>


For most applications the first answer is enough: "If you release it,
it will fall".  For example, we might say to a child, "if you drop
that rock it will hurt your foot".  This might be called the
"shallow" level.  Deeper levels give information that is more and
more precise, but at a higher cost.   <P>

A human could never get anything done operating continuously at the
third level, let alone the fifth, and neither could an expert system.
The early expert systems tended to operate at the first level of
causality, the shallow level.  This was fortunate because it allowed
these programs to exhibit a great deal of expertise for minimum cost.
Such successes of expert systems have been of great value to the field
of AI.  They not only helped build confidence in the AI researchers
that worthwhile accomplishments are possible, but also promised
financial returns in the near term which can help pay for further
research and development.  So operating at the shallow level is not
bad at all when it works.   <P>

The problem comes when that level is not adequate, when deeper causal
reasoning is needed.  And it is at this point that our machines need
to be directed one step deeper in the causality chain.   <P>

Using causality properly, then, does not mean jumping to the deepest
causal level, but rather working down through levels as needed.  I
believe that the recent work on qualitative reasoning is a correct
step in this direction.  But to make it work properly, an overall
knowledge structure, governed partly by common sense, is needed to
control the process.   <P>

These new Super Expert Systems (for the coming decade) will absorb a
large percentage of the research and development effort over the next
several years, and rightfully so.  I mean expert systems which have
been endowed with: large structured knowledge bases; ability to reason
through various causality levels (preferring the shallowest but
resorting to deeper levels as needed); limited ability to learn
automatically from experience and to accumulate knowledge by analogy;
truth maintenance systems; enhanced human interfacing to facilitate
knowledge acquisition from experts and for ease of use; etc.   <P>

These super expert systems will evolve into the "thinking" part (as
opposed to the moving and sensory parts) of our dreamed-of intelligent
machines of the future.  Later versions will have enhanced ability to
learn (e.g., learning directly from machine--readable text), and
reason by analogy, and much more.   <P>

Now let me list some of the areas that I feel will dominate AI
research over the next decade.  I have discussed most of these already
and now list one more: automatic reasoning.   <P>


                   
<H3>IMPORTANT RESEARCH AREAS</H3>
<UL>

<LI> Large Structured Knowledge Bases  <br>
  Knowledge Representation  <br>
  Knowledge Storage, Retrieval, and Use <P>

<LI> Expert Systems Technology (A large Effort) <P>

<LI> Machine Learning  <br>
  Controlled by knowledge structures <P>

<LI> Causality  <br>
  By depth levels <P>

<LI> Human Interfacing  <br>
  Natural Language Processing  <br>
  Speech Recognition and Generation <P>

<LI> Automatic Reasoning  <br>
  Analogical Reasoning  <br>
  Common Sense Reasoning, Default Reasoning <P>

</UL>

I have not tried to be complete in this listing and have not even
mentioned some important areas such as robotics, automatic
programming, and planning.   <P>

Automatic reasoning is another area of research that is becoming
increasingly important for a number of reasons.  Earlier expert
systems required only modest inferencing power because they operated
on rules at the shallowest levels. But as we reach toward deeper
causality, the reasoning component is challenged to handle the
switching of levels and the added complexity of the deeper levels.  In
this, as always, knowledge plays a crucial role.   <P>

Also the emergence of logic as a basis for programming languages
(PROLOG, LOGLISP, PARLOG, etc.), and as a means for storing knowledge
(in Logic data bases, logic based rules for expert systems), has
suddenly placed a new load on our automatic reasoning programs (our
provers).  Thus we see the great interest in "Kilolip" machines,
that perform a large number of logical inferences per second.  Such
high performance will not only be needed for horn-clause problems,
such as the use of PROLOG, but also for reasoning in first order
logic, and even in modal logic, and higher order logic.  Thus the
renewed interest in Automated Theorem Proving.   <P>

It will be interesting to see whether the new concepts for handling
Horn clauses and first order logic, which are expected to produce
"raw horsepower" in the Megalip range, will be enough to cope with
the load that will be imposed by the next generation applications, or
whether these methods will have to be "spiced" with special
reasoning-knowledge-units for speeding up proofs for particular
applications.  In any event automatic reasoning research should become
more relevant in the near future.   <P>

Let me not be misunderstood.  General purpose reasoning machines
(theorem provers) alone are not enough.  Knowledge is still the key.
But the requirements for reasoning about knowledge will be intensified
and partly satisfied by these new high speed provers that are
beginning to appear.   <P>

I have great faith that the AI community is headed generally in the
right direction.  About half of the new crop of graduate students
admitted to the Ph.D. program in Computer Science at the University of
Texas this year selected AI as their preferred field of study.  This
preference for AI seems to be duplicated throughout the world, and we
are talking about some of the very best students.  These young people
hold in their hands the future of this discipline.  The power and
influence of the earlier pioneers will wane as these new researchers
emerge.   <P>

I urge these new students and all new researchers to set themselves a
vision of the future and to have the courage to make major new
departures, to question the old and get on with the new.  There is
much to learn from us, we have pointed generally in the right
direction, but the major gains are yet to be made.   <P>

I personally favor the bold approach over the timid.  And there are
certain bold experiments that have to be made.  One such effort was
the Mechanical Translation (MT) work of the early 1960's.  Some have
called it a failure, but I do not!  It had to be tried.  It seems
rather obvious now that you cannot have MT without language
understanding.  That awareness was made much clearer by these earlier
experiments -- they helped focus research in the important area of
Natural Language processing.  And look how exciting that has become
and where it has led, even to the resurgence of MT!  A similar story
could be told about early speech recognition -- quality speech
recognition is not possible without language understanding.  Early
experiments with Perceptrons represent another such example.  In all
these cases a lot of work compensated somewhat for the lack of a great
idea. (The "Shakey" robot project at SRI is another example but in
that case the value of the early work is widely appreciated.)   <P>

The principle I want to make is this: when you have what looks like a
good idea, give it your "best shot", waste a little money to get
some early feedback.  Don't take "forever" to study the problem
because that is even more expensive (and less exciting).  Of course,
this strategy (this scientific method) requires character on the part
of the researcher.  He/she must be willing to analyze those
experiments, reformulate theories, and press on.  Otherwise, that
person does not qualify for the work and should not be entrusted with
research funds.   <P>

I was recently reading about Thomas Edison and his team at the time
they developed a successful light bulb.  He started with what he
thought was a good idea and plowed ahead.  He was brash, he was cocky,
he bragged about what they would do (build a widely usable electric
light bulb), his early ideas were wrong.  I believe that they were
lucky, even with all their brilliance; it could have taken years.  But
this is another example, like Language Translation, where an early
expensive failure returned information that helped finalize a
successful solution.   <P>

I believe that AI is in a position today where these kinds of bold
experiments are needed (but not the bold bragging).  They need to be
conducted by men and women with character, with wisdom and persistence
enough to succeed.   <P>

Another concern I have is the "flash in the pan" researcher, the
person with a limited theory, who does a trivial application of it, or
none at all, gets no useful feedback, he builds a program that cannot
surprise him in any way, and leaves to others to prove and extend his
work.  His fragment had better be pretty brilliant if anything is to
become of it.  More likely a real researcher will rediscover the
fragment as part of a larger effort and absorb most of the credit.  We
might recall that most AI pioneers are well known for what they did,
not what they theorized.   <P>

What is the most important characteristic of a good researcher?
Answer: he does good research.  Successful people somehow find a way
to succeed, others fail.  Of course, native intelligence is an
important ingredient, but it alone is not enough.  An equally important
characteristic is the ability (and inclination) to combine theory and
experiment.   <P>

So again I would say to young people.  Set a dream.  Set a goal (your
part of bringing about that dream).  Tool up: education, employment,
facilities.  Pursue it with vigor -- and impatience, want it today.
I've never seen a content researcher who was worth his salary.  Don't
be easily deterred by those who don't have your insight and training.
Work hard, provide momentum, don't give up easily.  Don't spend too
much time extolling the work of others; you will never
be properly recognized or satisfied until you make your own personal
contribution.  Compare and compete.  These are rules for a researcher
in any field.  My conviction is that the field of AI is worth your
finest efforts.   <P>

I have told you about my dream, have offered advice for young
researchers, and have offered my opinion on important areas of AI
research.  But of all the predictions that I could make, the one that
I'm most sure about is that we will again be surprised.   <P>


<hr>

Acknowledgement.  I want to thank Doug Lenat, Mary Shepherd, Clive
Dawson, Joe Scullion, Hassan Ait--Kaci, Elaine Rich, Dick Martin, and
Dick Hill for helpful comments.  The title is obviously due to Martin
Luther King.



<hr>