Evaluation of the FGCS Project 

David H. D. Warren 
Department of Computer Science 
University of Bristol 

General Impact 

The FGCS project had a major political impact from the time it was first an-
nounced. The originally described plan was rather broad and fuzzy, with some appar-
ently grandiose objectives, and its announcement generated a lot of hype. It was some 
time before Fuchi's clear and far-sighted vision of future computer systems, in which 
logic programming would provide the central link between parallel architectures and 
knowledge processing applications, became widely understood. Many international de-
velopments were stimulated by the perceived "threat" of the FGCS project, including 
Alvey in the U.K. and MCC in the U.S.A. Other international developments were more 
directly inspired by the scientific vision of the project, and included the setting up of 
institutes such as SICS in Sweden and ECRC in Europe which were very much overseas 
counterparts of ICOT with very similar research directions. 

Overall, the project has had a major scientific impact, in furthering knowledge 
throughout the world of how to build advanced computing systems. It certainly pro-
vided a tremendous boost to research in logic programming. In a real sense, FGCS 
has become an international research effort. This clearly has enhanced Japan's inter-
national prestige. The project has also led to Japanese researchers becoming far more 
"plugged in" to the international research community than they were at the time of 
the project's announcement. A further general benefit of the project to Japan must 
surely be the transfer to Japanese industry of research ethos and experience, provided 
by staff returning to their home companies after their three-year assignments to ICOT. 

Organisational Issues 

The project appears to have been handicapped, in tackling its very ambitious re-
search goals, by being set in a framework more suited to an industrial development 
project. Ten years of basic research cannot be tightly laid down in advance, as much 
of ICOT's programme seems to have been, with its predetermined duration, phases, 
milestones and hardware deliverables. The inflexibility of ICOT's programme seems to 
have prevented the possibility of changes of direction and reevaluation that are neces-
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sary in an advanced research project. 

The research leaders of ICOT are scientists of very high calibre much respected by 
their international colleagues. Most of them have been with the project for its du-
ration and have provided continuity of direction. Most of the other ICOT staff have 
been working on three-year assignments from the companies. The resulting lack of 
long-term continuity of ICOT staff, and the fact, as I understand it, that ICOT could 
not hand-pick the majority of its staff, are additional handicaps to pursuing advanced 
research not shared by comparable institutions such as ECRC, MCC and SICS. 

Major Technical Achievements 

The FGCS project has produced many significant technical achievements. Some of 
the major accomplishments which are of particular interest to me and which I would 
highlight are the following. 

First, ICOT has achieved its foremost concrete objective of building a parallel infer-
ence machine with a performance exceeding 100 megalips. Given the state of the art at 
the time the project was announced, when Prolog performance was at best 40,000 lips 
and large-scale parallel machines hardly existed, this achievement is quite remarkable 
and should not be underestimated. Although KL1 lips are not quite as powerful as 
Prolog lips, ICOT's achievement still represents a leap forward by more than three 
orders of magnitude. 

On the language side, I consider GHC to be a most significant contribution. It 
embodies, in my opinion, the most elegant encapsulation of the committed-choice lan-
guage (CCL) concept, simplifying and clarifying what was introduced by Parlog and 
Concurrent Prolog. 

In its parallel implementations of KL1, ICOT has significantly advanced the imple-
mentation technology for CCLs. My own group has drawn on this work, and on the 
key idea of GHC, in our implementation of Andorra-I. 

Although I have some reservations about that ICOT has committed itself entirely 
to CCLs and the concurrent logic paradigm, it cannot be denied that ICOT's PIM 
machine and operating system PIMOS are a powerful demonstration of what is possi-
ble in terms of building a machine and operating system entirely based on a CCL. It 
strikes me as something of an heroic feat, akin to climbing Everest or putting a man 
on the Moon, which opens our minds to future possibilities while perhaps not bringing 
immediate economic benefit. 

As part of its programme for producing demonstrations of KL1 and PIM, ICOT 
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has created a number of innovative parallel symbolic applications, notably in the areas 
of VLSI CAD, molecular biology, natural language analysis, and theorem proving. 
For me, they are particularly interesting in showing the potential for parallelism in 
algorithms very different from the kind of regular andĽ repetitive numeric computations 
which are typical of parallel computing today. 

Technical Issues 

There are some specific technical issues on which I would criticise the approach 
taken by ICOT. While I can appreciate some of the reasons why ICOT took the path 
it did, I feel the project might have achieved more, and remained closer to its original 
vision, if certain key decisions had been made differently. 

Perhaps the most important issue is the decision (or assumption?) that parallelism 
has to be expressed explicitly in user programs, rather than designing systems to ex-
ploit parallelism automatically (taking advantage of the fact that logic programming, 
as a declarative formalism, allows parallelism to be expressed implicitly). Requiring 
the user to take direct responsibility for expressing parallel algorithms adds greatly 
to the programming burden, especially for the kind of complex knowledge processing 
applications which are the main target of FGCS. This route is only appropriate for 
problems which are computationally very intensive and where adequate performance 
cannot be achieved by other means. But for such problems, the first priority before 
tackling parallelism is probably to ensure that the sequential algorithm is as fast as 
it possibly can be, using as low-level a language as is necessary. This tends to argue 
against using a high-level approach such as logic programming. 

On the other hand, there are many problems which may be potentially speeded 
up by exploiting implicit parallelism automatically and where logic programming may 
provide reasonable performance (perhaps via the parallelism) in relation to software 
development cost. If parallel computers become the norm, as seems technologically 
inevitable in the near future, software systems which can exploit parallelism automat-
ically will have a major role to play. It is a pity ICOT didn't take the opportunity 
to pursue this direction, which is being actively explored by other research groups (in-
cluding my own). 

The decision to go for explicit parallelism was linked with the decision to adopt 
the concurrent logic programming paradigm as central to all aspects of the project. In 
particular, all user programs in practice have to be expressed in, or implemented via, 
the concurrent LP paradigm, by means of the kernel language KL1. While the concur-
rent LP paradigm is of considerable interest in its potential for formalising interactive 
systems, and may be appropriate for many purposes including implementing operating 
systems, It is not, in my opinion, suitable for most user programs. 
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For most user programs, a much more high-level approach is needed, and ideally one 
would like to use declarative logic programming, i.e. logic programming as it was origi-
nally conceived. In declarative logic programming, the program expresses a declarative 
view of the problem as well as providing an operational solution to the problem. By 
contrast, the concurrent LP paradigm provides no declarative view of the problem. At 
best, it can be said to consist of a declarative description of a concurrent algorithm for 
solving the problem. In practice, users of the paradigm take an exclusively operational 
view. Without the declarative underpinning, there is no particular reason to maintain 
the original connection with logic, and every reason to modify the formalism to make it 
better fit its operational purpose. For these reasons, it is arguable whether concurrent 
LP is indeed logic programming in its original sense. 

Be that as it may, the present situation with ICOT systems is that the main user 
language, KL1, is considerably lower level than traditional logic programming lan-
guages such as Prolog. Other, more high-level, user languages have been provided, but 
have had to be implemented on top of KL1. Although ICOT believes the use of KL1 as 
an intermediate language does not entail any unacceptable overhead, there seems good 
reason to believe that higher level languages and inference systems (including Prolog for 
example) could be implemented much more efficiently if a lower level implementation 
language than KL1 were used. In my view, KL1 is too low-level as a user language for 
most purposes, but too high-level to serve as the lowest level implementation language. 

For a kernel language based on logic programming to be acceptable as a general user 
language it must, in my view, provide at least the basic capabilities of Prolog. This 
certainly seemed to be the view in the original FGCS proposal and in the early stages 
of ICOT's work. KL1, however, is considerably weaker than Prolog in that it does 
not provide a builtin search mechanism for finding at least one (and possibly all) solu-
tions to a problem, although it is more powerful than Prolog in that it provides builtin 
coroutining (necessary, amongst other things, to support the concurrent LP paradigm). 

It should be noted that it would be possible to have a kernel language providing 
all the capabilities of Prolog together with all the essential features of KL1 (including 
at least all of flat GHC which is the heart of KL1). Such a language would be quite 
acceptable as a user language, while providing the necessary basis to implement an 
operating system according to the ICOT approach. Such a language is provided by 
the Andorra-I system implemented by my group at Bristol. This language is viewed 
primarily as a high-level extension of Prolog. However, since it includes flat GHC as a 
subset, it is capable of supporting the concurrent LP paradigm. 

Another most important issue, of a completely different nature, is the question of 
whether ICOT was wise to concentrate so much effort on building specialised hardware 
for logic programming, as opposed to building, or using off the shelf, more general pur-
pose hardware not targeted at any particular language or programming paradigm. The 
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problem with designing specialised experimental hardware is that any performance ad-
vantage that can be gained is likely to be rapidly overtaken by the ever continuing rapid 
advance of commercially available machines, both sequentiual and parallel. ICOT's 
PSI machines are now equalled if not bettered for Prolog and CCL performance by ad-
vanced RISC processors. And it seems very possible that commercial multiprocessors 
such as Sequent Symmetry, the new Butterfly, and other recent machines could come 
close to equaling the PIM performance if ICOT's software technology were ported to 
those machines. 

A subsidiary issue is whether it was necessary to target KL1 so much at distributed 
memory hardware, with all the attendant problems of achieving good locality of com-
munication and good load balancing, rather than adopting a virtual shared memory 
approach, for which scalable solutions are becoming increasingly well developed, in-
cluding ones supporting a quasi-UMA (uniform memory access) model (c.f. KSR-1 
and the closely similar work on DDM that I have been involved in). In general, I feel 
that ICOT perhaps devoted too great a proportion of its effort to developing hardware 
and operating systems, and could perhaps have focussed its efforts more on the knowl-
edge processing software and applications which were central to the original conception 
of the project. 

This section of my report is rather long! Its length should be interpreted not so 
much as a measure of criticism of ICOT's approach, which given the many constraints 
they were operating under has been very productive I believe, but rather as a measure 
of the complexity of the issues that I felt needed to be mentioned. 

Overall Evaluation 

The nature of the original FGCS announcement raised a lot of expectations that the 
project could never have satisfied and certainly have not been satisfied. Unfortunately, 
this makes it difficult for the project to be judged a success by the world at large,
which includes most of the media. However, I strongly believe that overall the project 
has been a considerable success, and I think most fair-minded and properly informed 
observers will share my view. 

The project was a major success in galvanising worldwide activity and more im-
portantly for its scientific impact in stimulating worldwide research in new directions 
inspired directly by the FGCS vision and ICOT's work. The project has also succeeded 
in achieving its main concrete target of 100 megalips plus, an outstanding accomplish-
ment that shouldn't be diminished with the benefit of hindsight. 

But above all, any research project such as FGCS should be judged in comparison 
with comparable efforts by comparable institutions elsewhere. I believe the specific 
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research and development achievements of ICOT are on a par with the three institu-
tions, MCC, ECRC and SICS, which are most comparable with ICOT and which are 
representative of the very highest level of computing research in the world. Moreover it 
should not be forgotten that those three institutions came into being largely following 
in the footsteps of ICOT and the FGCS project. 

Recommended Future Steps 

I strongly recommend that ICOT's work should be continued in some form beyond 
the 1993 official end date of the FGCS project. The nucleus of highly gifted people 
and expertise built up at ICOT should not be allowed to evaporate, but should be 
continued within a smaller and more flexible framework. The KL1 software should be 
made available on widely available standard hardware, including Unix uniprocessors 
and multiprocessors such as Sequent Symmetry and perhaps BBN Butterfly. The PIM 
hardware should be examined to see whether it might potentially form the basis for 
commercial products if standard languages and operating system were supported. More 
effort should be put into evaluating the FGCS results, and especially in comparing the 
performance and usability with the best conventional alternatives. Speedups and good 
load balancing are not enough by themselves; one needs to show that applications 
perform better than they would by other approaches with comparable implementation 
effort. There should also be continuing research, especially in the areas of knowledge 
processing and applications. I would suggest that all this would best be done within 
a much smaller research institute, with selected long-term staff, and a focussed but 
flexible ongoing research programme (c.f. for example SICS). 

It is understood that MITI is anxious to have official overseas collaboration in any 
extension of the FGCS work. My own group would be interested in collaborating 
with ICOT (or its successor) in evaluating ICOT's parallel applications developed in 
KL1, to see to what extent the same problems can be solved through more directly 
declarative logic programs, and whether comparable performance and parallelism can 
be obtained from logic programming implementations supporting implicit parallelism 
(such as Andorra-I). Unfortunately, DTI (the UK counterpart of MITI) requires 50% 
funding from UK industry for any research it supports. So long as the ICOT work is 
only available on custom hardware, it is unlikely that UK industry would be interested. 
And even if the ICOT software were ported to standard hardware, the likely payoff 
from such research is too long-term for most UK industry (with its rather short-term 
horizons). Therefore, I am afraid the chances of official UK involvement, through DTI, 
in continuations of the FGCS work seem poor, for the near term at least. 
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