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\JArtificial  Intelligence: A General  Survey by
Professor  Sir  James Lighthill,  FRS, in  \F1Artificial  Intelligence: a
paper symposium\F0, Science Research Council 1973.

	Professor   Lighthill  of  Cambridge   University  is   a  famous
hydrodynamicist  with a recent  interest in  applications to biology.
His review of  artificial intelligence  was at the  request of  Brian
Flowers, then head of the  Science Research Council of Great  Britain, the
main  funding body  for British  university scientific  research. Its
purpose was to help the Science Research Council decide  requests for
support of  work in  AI.  Lighthill  claims no  previous acquaintance
with the  field,  but refers to a large number of authors whose works
he consulted, though not to any specific papers.

	The \F1Lighthill Report\F0 is organized around a classification
of AI research into three categories:

	Category A is \F1advanced automation\F0 or \F1applications\F0,
and he approves of it in principle.  Included in A are
some activities that are obviously applied but also activities like
computer chess playing that are often done not for themselves but
in order to study the structure of intelligent behavior.

	Category C comprises studies of the \F1central nervous system\F0
including computer modeling in support of both neurophysiology and
psychology.

	Category B is defined as "building robots" and "bridge" between
the other two categories.  Lighthill defines a robot as a program or
device built neither to serve a useful purpose nor to study the central
nervous system, which obviously would exclude Unimates, etc. which are
generally referred to as industrial robots.  Emphasizing the bridge aspect
of the definition, Lighthill states as obvious that work in category B is
worthwhile only in so far as it contributes to the other categories.

	If we take this categorization seriously, then most AI researchers
lose intellectual contact with Lighthill immediately, because his three
categories have no place for what is or should be our main scientific
activity - \F2studying the structure of information and the structure of
problem solving processes independently of applications and independently
of its realization in animals or humans\F0.  This study is based on the
following ideas:

	1. Intellectual activity takes place in a world that has a certain
physical and intellectual structure: Physical objects exist, move about,
are created and destroyed.  Actions that may be performed have effects that
are partially known.  Entities with goals have available to them certain
information about this world.  Some of this information may be built in,
and some arises from observation, from communication, from reasoning, and
by more or less complex processes of retrieval from information bases.
Much of this structure is common to the intellectual position of animals,
people, and machines which we may design, e.g. the effects of physical actions
on material objects and also the information that may be obtained about
these objects by vision.
The general structure of the intellectual world is far from understood, and
it is often quite difficult to decide how to represent effectively the information
available about a quite limited domain of action even when we are quite
willing to treat a particular problem in an \F1ad hoc\F0 way.

	2. The processes of problem solving depend on the class of problems
being solved more than on the solver.  Thus playing chess seems to require
look-ahead whether the apparatus is made of neurons or transistors.
Isolation of the information relevant to a problem from the totality
of previous experience is required whether the solver is man or machine,
and so is the ability to divide a problem into weakly connected subproblems
that can be thought about separately before the results are combined.

	3. Experiment is useful in determining what representations of
information and what problem solving processes are needed to solve a
given class of problems.  We can illustrate this point by an example from
the \F1Lighthill Report\F0 which asserts (p. 15) that the heuristics of a chess
program are embodied in the evaluation function.  This is plausible
and was assumed by the first writers of chess programs.
Experiment showed, however, that the procedures that select what part of the
move tree is examined are even more important, i.e. when the program errs
it is usually because it didn't examine a line of play rather than because
it mis-evaluated a final position.  Modern chess programs concentrate on this
and often have simpler evaluators than the earlier programs.

	4. The experimental domain should be chosen to test the adequacy
of representations of information and of problem solving mechanisms.  Thus
chess has contributed much to the study of tree search; one Soviet computer
scientist refers to chess as the \F1Drosophila\F0 of artificial intelligence.
I think there is much more to be learned from chess, because master level
play will require more than just improving the present methods of searching
trees.  Namely, it will require the ability to identify, represent, and
recognize the patterns of position and play that correspond to "chess ideas",
the ability to solve some abstractions of positions (e.g. how to make use
of a passed pawn and a seventh rank rook jointly) and to apply the result
to actual positions.  It will probably also require the ability to analyze
a problem into subproblems and combine the separate results.  (This ability
is certainly required for a successful \F1Go\F0 program).

	Having ignored the possibility that AI has goals  of its own,
Lighthill goes on  to document his claim that  it has not contributed
to applications or to  psychology and physiology.   He exaggerates  a
bit here,   it seems worthwhile  to spend some effort  disputing his
claims that AI has not contributed to these other subjects.

	In my opinion,   AI's contribution to  practical applications
has  been significant  but so  far mostly  peripheral to  the central
ideas and  problems  of AI.   Thus  the  LISP language  for  symbolic
computing was  developed for  AI use,   but  has had  applications to
symbolic computations  in other areas, e.g.  physics.  Moreover, some
ideas  from  LISP  such  as  conditional  expressions  and  recursive
function definitions  have been used in  other programming languages.
However,  the  ideas that have  been applied elsewhere  don't have  a
specifically AI character  and might have been but  weren't developed
without AI  in mind.  Other examples  include time-sharing, the first
proposals for which had AI motivations and some techniques of picture
processing that were first developed in AI laboratories and have been
used elsewhere.   Even the current  work in automatic  assembly using
vision  might have been developed  without AI in mind.   However, the
Dendral work has always had a specifically AI character,  and many of
the recent developments  in programming such as  PLANNER and CONNIVER
have an AI motivation.

	AI's  contributions to  neurophysiology  have been  small and
mostly of a negative character, i.e. showing that  certain mechanisms
that neurophysiologists propose are not well defined or inadequate to
carry  out the behavior they are supposed to  account for.  I have in
mind Hebb's proposals in his book \F1The  Organization of Behavior\F0.
No-one  today would believe  that the  gaps in  those ideas  could be
filled without adding something much  larger than the original  work.
Moreover, the  last 20  years experience  in programming machines  to
learn  and solve problems  makes it implausible  that cell assemblies
\F1per se\F0  would learn  much without  putting  in some  additional
organization, and  physiologists today  would be unlikely  to propose
such a theory.  However, merely showing that some things are unlikely
to work is not a \F1positive\F0 contribution.
I think there will be more interaction between AI and neurophysiology
as soon as the neurophysiologists are in a position to compare
information processing models of higher level functions with
physiological data.  There is little contact at the nerve cell level,
because, as Minsky showed in his PhD dissertation in 1954, almost any
of the proposed models of the neuron is a universal computing element,
so that there is no connection between the structure of the neuron and
what higher level processes are possible.

	On the other  hand,  the  effects of artificial  intelligence
research  on  psychology have  been  larger  as  attested by  various
psychologists. First of all, psychologists have begun to use models in
which  complex  internal  data structures  that  cannot  be  observed
directly  are attributed to  animals and people.   Psychologists have
come to use these models,  because they exhibit behavior  that cannot
be exhibited by models conforming  to the tenets of behaviorism which
essentially  allows  only connections  between  externally observable
variables.   Information processing  models in  psychology have  also
induced dissatisfaction  with psychoanalytic and  related theories of
emotional behavior.  Namely,  these information processing models  of
emotional states  can  yield predictions  that can  be compared  with
experiment or experience in a more definite way than can the vague
models of psychoanalysis and its offspring.

	Contributions  of AI to  psychology are  further discussed in
the paper  \F1Some Comments  on the  Lighthill Report\F0  by  N.   S.
Sutherland which  was included  in the same  book with  the Lighthill
report itself.

	Systematic  comment on  the main  section,   entitled \F1Past
Disappointments\F0  is  difficult because  of  the  strange  way  the
subject is divided up but here are some remarks:

	1. Automatic  landing systems for airplanes are  offered as a
field in  which conventional  engineering techniques  have been  more
successful than AI  methods.  Indeed, no-one would  advocate applying
the scene analysis or tree search techniques developed in AI research
to automatic landing  in the context in  which automatic landing  has
been developed.  Namely, radio signals are available to determine the
precise  position of  the airplane in  relation to  a straight runway
which is  guaranteed clear  of  interfering objects.   AI  techniques
would  be  necessary  to make  a  system  capable  of landing  on  an
unprepared dirt strip with no radio aids which had to be located  and
distinguished  from roads  visually  and  which  might have  cows  or
potholes or muddy places on it.  The problem of automatically driving
an automobile in an  uncontrolled environment is even more  difficult
and will  definitely require AI  techniques, which, however,  are not
nearly ready for a full solution of such a difficult problem.

	2.  Lighthill  is  disappointed  that  detailed  knowledge of
subject matter has to be put in if programs  are to be successful
in theorem proving, interpreting  mass spectra, and game playing.  He
uses the word \F1heuristics\F0  in a non-standard way  for this.   He
misses the fact that there are great  difficulties in finding ways of
representing knowledge of  the world in computer programs and much AI
research  and internal  controversy are  directed  to  this  problem.
Moreover,  most  AI  researchers  feel that  more  progress  on  this
\F1representation problem\F0 is essential before substantial progress
can be made on the problem of automatic acquisition of knowledge.  Of
course, missing  these particular points is a  consequence of missing
the existence of  the AI  problem as distinct  from automation  and
study of the central nervous system.

	3. A  further disappointment is  that chess  playing programs
have only  reached an "experienced amateur" level  of play.  Well, if
programs can't do better than that  by 1978, I shall lose a \F3B\F0250  bet
and will  be disappointed  too though not  extremely surprised.   The
present  level of  computer chess  is based  on the  incorporation of
certain intellectual  mechanisms in the  programs.  Some  improvement
can be made by further  refinement of the heuristics in the programs,
but probably master  level chess  awaits the ability  to put  general
configuration patterns into the programs in an easy and flexible way.
I don't see how to set a date by which this problem must be solved in
order to avoid disappointment in the field of artificial intelligence
as a whole.

	4. Lighthill discusses the \F1combinatorial explosion\F0
problem as though it were a relatively recent phenomenon that
disappointed hopes that unguided theorem provers would be able to
start from axioms representing knowledge about the world and solve
difficult problems.  In fact, the \F1combinatorial explosion\F0
problem has been recognized in AI from the beginning, and the usual
meaning of \F1heuristic\F0 is a device for reducing this explosion.
Regrettably, some people were briefly over-optimistic about what
general purpose heuristics for theorem proving could do in problem
solving.


Did We Deserve It?

	Lighthill had  his shot  at AI and  missed, but  this doesn't
prove  that  everything in  AI  is ok.    In my  opinion,  present AI
research suffers  from some  major deficiencies apart  from the  fact
that  any scientists  would  achieve more  if they  were  smarter and
worked harder.

	1. Much  work in  AI has  the "look  ma, no  hands"  disease.
Someone programs  a computer  to do  something no  computer has  done
before and writes a paper pointing out that the computer did it.  The
paper is not directed to the identification and study of intellectual
mechanisms and often contains no  coherent account of how the program
works  at all.  As an  example, consider  that the  SIGART Newsletter
prints the scores of the  games in the ACM Computer  Chess Tournament
just as though the programs were human players and their innards were
inaccessible.  We need to know why one program missed the right  move
in a position  - what was it thinking  about all that time?   We also
need  an  analysis of  what  class of  positions  the  particular one
belonged to and how a  future program might recognize this class  and
play better.

	2. A second disease is to work only on theories that can be
expressed mathematically in the present state of knowledge.
Mathematicians are often attracted to the artificial intelligence
problem by its intrinsic interest.  Unfortunately for the mathematicians,
however, many plausible mathematical theories with good theorems
such as control theory or statistical decision theory have
turned out to have little relevance to AI.  Even worse, the applicability
of statistical decision theory to discriminating among classes of
signals led to the mistaken identification of perception with
discrimination rather than with description which so far has
not led to much mathematics.
More recently, however, problems of theorem proving and problems of
representation have led to interesting mathematical problems in logic
and mathematical theory of computation.

	3. Every now  and then, some AI scientist gets  an idea for a
general  scheme of  intelligent behavior that  can be  applied to any
problem provided the machine  is given the specific knowledge  that a
human has about  the domain.  Examples of this  have included the GPS
formalism, a simple predicate  calculus formalism, and more  recently
the  PLANNER  formalism  and  perhaps   the  current  Carnegie-Mellon
production formalism.  In the first and third  cases, the belief that
any problem solving  ability and knowledge could  be fitted into  the
formalisms led to published  predictions that computers would achieve
certain  levels  of  performance  in certain  time  scales.    If the
inventors of  the formalisms  had been  right about  them, the  goals
might have  been achieved, but  regrettably they were  mistaken. Such
general purpose formalisms will be  invented from time to time, and,
most  likely, one of them will eventually prove adequate.
However, it would be  a great relief to the rest of the workers in AI
if the  inventors of  new general  formalisms  would express  their
hopes in a more guarded form than has sometimes been the case.

	4. At present,  there does not exist  a comprehensive general
review of  AI that discusses all the main approaches and achievements
and issues.    Most likely,  this  is not  merely because  the  field
doesn't have a  first rate reviewer at present,  but because the field
is confused about what these  approaches and achievements and  issues
are.   The production  of such  a review  will therefore  be a  major
creative work and not merely a work of scholarship.

	5. While it is far beyond the scope of this review to try
to summarize what has been accomplished in AI since Turing's 1950 paper,
here is a five sentence try: Many approaches have been explored and
tentatively rejected including automaton models, random search,
sequence extrapolation, and many others.  Many heuristics have been
developed for reducing various kinds of tree search; some of these are
quite special to particular applications, but others are general.
Much progress has been made in discovering how various kinds of
information can be represented in the memory of a computer, but
a fully general representation is not yet available.  The problem
of perception of speech and vision has been explored and recognition
has been found feasible in many instances.  A beginning has been made
in understanding the semantics of natural language.

	These accomplishments notwithstanding, I think that artificial
intelligence research has so far been only moderately successful;
its rate of solid progress is perhaps greater than most social sciences
and less than many physical sciences.  This is perhaps to be expected
considering the difficulty of the problem.\.



				John McCarthy - 9 March 1974