Lessons from the history and philosophy of science regarding the Research Assessment Exercise


Lessons from the History and
Philosophy of Science regarding the
Research Assessment Exercise

D O N A L D G I L L I E S

1. Introduction

The Research Assessment Exercise (henceforth abbreviated to
RAE) was introduced in 1986 by Thatcher, and was continued by
Blair. So it has now been running for 21 years. During this time,
the rules governing the RAE have changed considerably, and the
interval between successive RAEs has also varied. These changes
are not of great importance as far as the argument of this paper is
concerned. We will concentrate on the main features of the RAE
which can be summarised as follows.

At intervals of a few years, RAEs are carried out in all the
universities of the UK. The first step is to appoint a committee of
assessors in each subject. These assessors are usually academics
working in the field in question in the UK. Next most members of
each department in a subject have to select a set of pieces of their
research. The department then submits all these pieces of research
produced by its members to the assessment committee. The
members of the committee study this research output, and, on its
basis, grade the department on a scale running form very good
downwards. The departments which score well on the RAE are
provided with research funds. Those which don’t score so well are
less fortunate. They are provided with much smaller funds for
research, and the members of such departments have to spend
more time on teaching. Recently there have even been moves in
some universities to close altogether departments which perform
badly on the RAE.

Such then in rough outline is the procedure followed in the RAE.
It should be pointed out that the RAE is a costly operation, both in
money terms and in the amount of academics’ time which it
absorbs and which they could, in the absence of the RAE, spend on
their research. The question then naturally arises as to whether this
expensive procedure has actually improved the research produced
in the UK. Strange to say this question is rarely asked. Academics

37



devote themselves with great energy to evaluating each other’s
work, but seem to be little concerned with evaluating an important
government policy. Perhaps the reason for this is that it seems at
first sight rather obvious that the RAE should improve the UK’s
research output. The procedure conforms to common sense. If we
want to improve research, we should first find out who is doing
good research and then give funding to the good researchers while
withdrawing funding from the bad researchers. The RAE appears
at first sight to be doing just this, and so the conclusion seems
inevitable that introducing such a system will improve research
output.

In social life, however, things are rarely simple, and judgements
based on common sense can often mislead. The RAE, which is so
costly in terms of money and time, is designed to improve the
research output of the UK, but could it be having the opposite
effect? Could it be making the research output of the UK worse
instead of better? In this paper I want to argue that the RAE is
indeed likely to have a negative effect on the research output of the
UK. My argument will be mainly based, as the title suggests, on
results which have been obtained from the study of the history and
philosophy of science, and I will next consider why history and
philosophy of science (henceforth HPS) is relevant to the RAE.

Let us begin with history of science. Historians of science study
the great episodes of scientific advance, and the research
programmes which led to exciting discoveries and to new and
important knowledge. However, they also study the research
programmes which failed to produce any advances, and the
obstacles and difficulties which have sometimes stood in the way of
scientific progress. All these matters are surely relevant to the
design of a government policy intended to improve scientific
research. Moreover it is not just the individual episodes which are
relevant. One needs to analyse the underlying general principles
which favour scientific advance, or, conversely, the general nature of
the obstacles which impede scientific progress. This task of
generalising from history of science falls to the practitioners of
philosophy of science. Thus I think there can be little doubt that
HPS is highly relevant to assessing the effectiveness of the RAE.

Of course, HPS is mainly relevant to the RAE as applied to
science. For the purposes of this paper, I will take ‘science’ in a
broad sense to include mathematics, computer science, and
medicine as well as the standard natural sciences such as astronomy,
physics, chemistry, etc. However, I will not include in ‘science’, the
social sciences and the humanities. Although my focus then is on

Donald Gillies

38



science in the sense just defined, and although by main arguments
will be drawn from HPS, I will digress slightly in the next section
by considering a branch of the humanities with which I am quite
familiar—namely philosophy. Thus in the next section (section 2), I
will raise the question of whether the RAE has improved
philosophy in the UK. This digression will prove useful since it
will suggest some methodological procedures which I will use
when, in sections 3 to 7, I come to apply results from HPS to the
problem of the effectiveness of the RAE.

2. Has the RAE improved philosophy in the UK?

I will begin by considering philosophy in the UK in the period
1900–1975, that is to say in the twentieth century but before the
introduction of the RAE. This period of almost three quarters of a
century was one of great brilliance as regards philosophy in the
UK. It begins in the years before the First World War with the
Cambridge school founded by Moore and Russell. Moore wrote an
outstanding work on ethics while Russell made his remarkable
contributions to logic and philosophy of mathematics. They were
followed in the next generation by Keynes who was at this time still
a philosopher rather than an economist, and who made important
contributions to the philosophy of probability and induction.
Wittgenstein also came to Cambridge at this time, and, working
with Russell, he developed his early philosophy. After the First
World War, philosophy continued to flourish at Cambridge. The
prodigious Frank Ramsey died in 1930 at the age of only 26, but
not before he made remarkable contributions to the philosophy of
logic, probability and mathematics. In that same year, however,
Wittgenstein obtained a post at Cambridge where he remained with
short interruptions until 1947, rising to the position of professor. It
was during this period that Wittgenstein developed his later
philosophy, and wrote most of his book: Philosophical Investiga-
tions. Wittgenstein died in 1951, and Philosophical Investigations
was published posthumously in 1953. Many people regard this
book as the greatest philosophical masterpiece of the twentieth
century.

After the Second World War, in the period 1945–75, philosophy
continued to flourish in the UK, but Cambridge was no longer the
main centre. Instead this period is dominated by the ordinary
language school of philosophy at Oxford, and by Popper’s school in
London. Ordinary language philosophy had much in common with

Lessons from the History and Philosophy of Science

39



Wittgenstein’s later philosophy, but it was developed in a somewhat
different way at Oxford by figures such as Ryle and Austin. Popper
and his school focussed on philosophy of science. The school
included not only Popper himself, but Lakatos, and, one might say,
half Feyerabend. I say ‘half Feyerabend’ because Feyerabend
started as Popper’s assistant, and his first lectureship was in Bristol
in the UK. However, he later worked in the USA and continental
Europe. Still up to the death of Lakatos in 1974, Feyerabend
visited London frequently giving regular lecture courses there.

The Oxford school and Popper’s school were not on the best of
terms. Their feud was foreshadowed by a famous argument
between Popper and Wittgenstein which took place in 1946, and
has become the subject of Edmonds and Eidinow’s interesting 2001
book: Wittgenstein’s Poker. However, a feud between two rival and
very different schools of philosophy is surely yet another sign that
philosophy was flourishing in the UK.

Moreover in the period 1945 to 1975, there were other significant
developments in philosophy in the UK which lay somewhat outside
the main schools just described. Perhaps the most important of
these was the beginning of the philosophy of artificial intelligence.
In his classic article published in Mind in 1950, Turing argued that
computers could eventually equal if not surpass human beings in
intellectual skills. Lucas replied in 1961 with a famous argument
which used Gödel’s incompleteness theorems to try to show that
the human mind would always remain ahead of any possible
computer.

So surveying philosophy in the UK in the years 1900–1975 one
cannot but conclude that this was a brilliant period in which
philosophy of the highest quality was produced in abundance in the
UK. However, this was all before anyone had thought of
introducing the RAE, and there was no system in operation which
resembled the RAE in any way. Doesn’t this begin to suggest that
the RAE may be quite unnecessary?

At this point, however, a stern defender of the RAE might say:
‘This is all very well, but there is never any good reason for being
complacent. Even if things are going well, there is still always room
for improvement, and the RAE was designed to achieve such
improvement.’ Well, the RAE may have been designed to bring
about improvement, but did it succeed? The RAE has been with us
since 1986. Has the philosophical output of the UK improved
during these nearly 21 years?

Having formulated this last question, I have to confess that I am
unable to answer it. I am genuinely unsure as to whether

Donald Gillies

40



philosophy produced in the UK in the last 10 years say has been
good or not. Naturally some pieces of UK philosophy have struck
me as good, while others have appeared to me as quite bad.
However, even these judgements I hold tentatively and with
considerable uncertainty, while I am, at the same time, completely
certain that others hold quite different opinions from mine about
what is good and what is bad. Earlier I talked about philosophy in
the period 1945 to 1975, and here I felt confident about the
opinions I expressed. After the lapse of thirty years, a historical
perspective has been obtained and it becomes easy to judge who
were the important philosophers, and to evaluate the significance of
their contributions. The situation is quite otherwise with contem-
porary philosophy where it is hard to say which philosophical works
have a real importance, which are now esteemed only because of
some passing fashion, and which are at present unjustly neglected
because their true significance has not yet been grasped.

Just as I have been writing about philosophy in the UK in the
period 1945 to 1975 which ended thirty years ago, let us imagine
someone writing about the period 1986 to 2007 in the year 2037.
Can we guess what such a writer might say? There could be a
spectrum of judgement along a scale running from those most
favourable to the RAE to those most hostile to it. A very favourable
judgement might go like this: ‘Although few realised it at the time,
the year 1986 proved a turning point for philosophy in the UK.
The introduction of the RAE in that year stimulated the
philosophy community in the UK to greater efforts and we can now
recognize that the works they produced in the subsequent decades
outshone those completed in the first three quarters of the
twentieth century.’ A very hostile judgement might go like this:
‘There was a brilliant flowering of philosophy in the UK in the
first three quarters of the twentieth century. Unfortunately after
about 1975, a decline set in and the situation was made worse by the
introduction of the RAE in 1986. In the decades following this
introduction, philosophy in the UK, which earlier in the century
had been so brilliant, sank to a very low point.’ These two
judgements could be taken as marking the extreme points of a scale.
Where along this scale will the majority of writers in 2037 be
found? I really would not like to say.

One important point has emerged from the preceding discussion,
namely that it is often very difficult to judge the quality of
contemporary research. It is often only after the elapse of a
considerable interval of time—say thirty years or more—that one
can say with any confidence that a piece of research was either

Lessons from the History and Philosophy of Science

41



genuinely good or really very bad. The situation is indeed worse
than this, for, as we shall see later in the paper, contemporary
judgements on the quality of pieces of research, are often wildly
mistaken in the light of what emerges later on. But this exposes a
key weakness in the RAE. The RAE naturally relies on
contemporary judgements as to which researchers are good and
which are bad, but such judgements are difficult to make and may
often be found to be quite wrong in the light of later developments.

I will pick up this point again in what follows, but I would like
now to consider another approach to assessing whether the effect of
the RAE on philosophical output is likely to be good or bad. As we
have seen the direct approach of asking whether the introduction of
the RAE improved the quality of philosophy in the UK did not
yield any very clear answer. This is why I suggest using another
approach which I call the ‘counterfactual methodology’. The idea
here is to consider research carried out in the past, and ask whether,
if the RAE had been in existence at that time, it would have
improved that research or would, on the contrary, have made it
worse.

Let us apply this counterfactual methodology to philosophy in
the UK in the 1930s. Suppose the RAE had been introduced in say
1936, what effect would it have had on philosophy in the UK. This
was the time when Wittgenstein was developing his later
philosophy at Cambridge and writing early drafts of what later
became his Philosophical Investigations, judged by many to be the
greatest philosophical book of the twentieth century. How would
Wittgenstein have fared in a RAE conducted according to the
existing rules?

Actually we can answer this question quite easily. Wittgenstein
was offered a position at Cambridge in 1930, rose to becoming
professor there, and resigned from his chair in 1947. During these
17 years he published nothing. In fact the last philosophical work
which he published in his lifetime was a paper entitled: ‘Some
Remarks on Logical Form’ which appeared in the Journal of the
Aristotelian Society in 1929. Wittgenstein had agreed to give a talk
to the Aristotelian Society that year. The Aristotelian Society
insists that papers are always printed in advance, and this is why
Wittgenstein’s paper was published. However Wittgenstein decided
shortly after the printing had taken place that the paper was
worthless, and at the meeting, actually talked on another topic (see
Monk, 1990, 272–3 for details). After this experience, Wittgenstein

Donald Gillies

42



became very reluctant to publish anything which he had not worked
on for a long period, and this explains why he published nothing
further for the next 17 years.

Now what happens under the RAE rules to academics who
publish nothing? They are classified as research inactive, and their
fate is not agreeable. Their research time is removed, and they have
to spend more time teaching. Moreover they are at risk of being
sacked. If the RAE had been in existence in 1936, and the rules had
been applied without fear or favour, then this is the fate which
would have overtaken Wittgenstein.

Now a defender of the RAE might at this point object to my
analysis on the following grounds: ‘Wittgenstein published nothing
between 1930 and 1947 because he was under no pressure to do so.
Had the RAE been introduced in 1936, he would certainly have
‘knuckled under’ and published some stuff.’ Unfortunately for this
argument, numerous memoirs and the magnificent (1990) biogra-
phy of Wittgenstein by Ray Monk have given us quite a vivid
picture Wittgenstein’s character, and this leaves no doubt that
Wittgenstein was the last person on earth to have ‘knuckled under’
and obeyed the directives of the RAE.

In fact Wittgenstein, despite his great intellectual brilliance,
seems to have disliked the company and habits of academics and to
have preferred associating with simple folk. Karl Britton, a former
student of Wittgenstein’s, very clearly describes this attitude of the
master (quoted from Pitcher, 1964, 12):

He had, he said, only once been to high table at Trinity and the
clever conversation of the dons had so horrified him that he had
come out with both hands over his ears. The dons talked like that
only to score: they did not even enjoy doing it. He said his own
bedmaker’s conversation, about the private lives of her previous
gentlemen and about her own family, was far preferable: at least
he could understand why she talked that way and could believe
that she enjoyed it.

As a result of these attitudes, Wittgenstein showed a strong
propensity to abandon seats of academic learning, and go off to
remote spots in the country where he could associate with simple
country folk. This propensity manifested itself as early as 1913,
where he decided to go off to live alone in a remote area of Norway
for two years. Russell tried in vain to dissuade him, and wrote
about it in a letter as follows (quoted from Monk, 1990, 91):

Lessons from the History and Philosophy of Science

43



I said it would be dark, & he said he hated daylight. I said it
would be lonely, & he said he prostituted his mind talking to
intelligent people. I said he was mad & he said God preserve him
from sanity. (God certainly will.)

This episode illustrates the extreme obstinacy and determination of
Wittgenstein’s character. He was really not the sort of man who
would have been prepared to ‘knuckle under’ and obey some
government regulation which he regarded as mistaken.

Wittgenstein went to Norway but did not stay for two years
because of the outbreak of the First World War. After the War,
despite having become famous in philosophical circles because of
the publication of his Tractatus, he decided to give up philosophy
and worked as a schoolmaster in remote Austrian villages between
1920 and 1926. He refused to attend any of the meetings of the
Vienna Circle which greatly admired his work. However Wittgen-
stein was eventually persuaded to return to academic life in
Cambridge in 1930. Yet he remained full of longings for a simple
life of manual toil in some remote country location. He even
applied in 1935, at the height of Stalinism, to work as a labourer on
a collective farm in Russia. Perhaps luckily for him the Russians
turned down his application (see Monk, 1990, 351). So Wittgen-
stein went back to his hut in Norway for a year instead.

Many people might regard the job of being professor of
philosophy at Cambridge as rather an agreeable one, but not so
Wittgenstein. In a letter to Malcolm in 1945, Wittgenstein wrote:
‘ ... the absurd job of a prof. of philosophy ... is a kind of living
death’ (quoted from Malcolm, 1958, 38). At this time he was
contemplating resigning his professorship at Cambridge, which he
did in 1947. Just before his resignation, Wittgenstein wrote (quoted
from Monk, 1990, 516):

Cambridge grows more and more hateful to me. The disintegrat-
ing and putrefying English civilization. A country in which
politics alternates between an evil purpose and no purpose.

After resigning his chair, Wittgenstein went off in 1948 to live in a
remote country district in Galway on the west coast of Ireland.

These episodes give a vivid illustration of Wittgenstein’s
character and tastes. In the light of these, is it possible that, if the
RAE had been introduced in 1936, he would have agreed to its
demands and started publishing some of his work? I find it quite
inconceivable that he would have done so. Malcolm in his Memoir
records (49) that in the academic year 1946–7, Wittgenstein stated

Donald Gillies

44



that ‘he was not going to be ‘stampeded’ into publishing
prematurely.’ In fact he had published nothing for over 17 years at
that stage of his career.

If there is still any doubt on this point, it could be added that
Wittgenstein was also highly contemptuous of the typical academic
procedures which are enshrined in the RAE. This is illustrated
vividly in letters written by Wittgenstein to Malcolm in 1945 and
1948. It should be explained that Wittgenstein was very fond of
reading American detective magazines—particularly those pub-
lished by Street and Smith. In the 1930s and 1940s, Mind was a
leading English philosophy journal, as indeed it still is today. To
have a series of papers published in Mind would be regarded as a
strong point in favour of any researcher according to the usual RAE
criteria. Wittgenstein, however, far from endorsing these RAE
criteria is very sarcastic about them, and compares Mind
unfavourably with the detective magazines of Street and Smith (cf.
Malcolm, 1958, 32). In 1945 he wrote to Malcolm:

If I read your mags I often wonder how anyone can read ‘Mind’
with all its impotence & bankruptcy when they could read Street
& Smyth mags. Well, everyone to his taste.

In another letter to Malcolm in 1948, he elaborated the
comparison:

Your mags are wonderful. How people can read Mind if they
could read Street & Smith beats me. If philosophy has anything
to do with wisdom there’s certainly not a grain of that in Mind,
& quite often a grain in the detective stories.

Suppose then that the RAE had been introduced in 1936. Are we
seriously to suppose that Wittgenstein would have ‘knuckled under’
and submitted papers for publication in Mind? Given his character
and views, it is altogether out of the question that he would have
done so. His reaction is entirely predictable. In the face of such a
demand, he would have undoubtedly have left Cambridge in
disgust and gone off to his hut in Norway.

The effect of the introduction of the RAE in 1936 would then
have been to hound Wittgenstein out of Cambridge. Hardly a result
which should increase our confidence in the merits of the RAE!
What actually happened was that Wittgenstein was offered a Chair
in Philosophy at Cambridge in 1939, despite having published
nothing for ten years. Such an appointment would of course be
almost impossible under a RAE regime. Even if the members of
the appointments panel were sympathetic to a candidate who had

Lessons from the History and Philosophy of Science

45



published nothing for ten years, they could hardly overlook the fact
that such a professor would contribute nothing to the RAE, and
would indeed set a bad example to the rest of the department. So if
the RAE had been introduced in 1936, Wittgenstein would have
been very unlikely to have become Professor of Philosophy at
Cambridge.

Wittgenstein was perhaps rather excessively reluctant to publish,
but how can we condemn his strategy in general terms?
Wittgenstein was not of course really research inactive while at
Cambridge. Although he published nothing between 1929 and
1951, he produced roughly thirty thousand pages of notebooks,
manuscripts, and typescripts on philosophy in that period
(Malcolm, 1958, 84). That is an average rate of about 26 pages a
week. Wittgenstein’s view was that he shouldn’t publish anything
until he had thought and rethought about it, and worked through it
many times revising and correcting. He believed that only in this
way could he produce philosophical work of lasting value. Now
how can we say he was wrong about this? After all, his strategy
worked. At the end of his long years of rethinking, revising and
correcting, he produced a book (Philosophical Investigations) which
many regard as the philosophical masterpiece of the twentieth
century.

I am not saying that every philosopher should adopt Wittgen-
stein’s strategy. Other philosophers work in a quite different way
and yet produce just as good philosophy. It is partly a matter of
style and temperament. Russell, for example, who was in my
opinion just as good a philosopher as Wittgenstein, worked in quite
a different way. He had no inhibitions about publishing, and, when
thinking about a problem, would often publish in rapid succession a
series of papers considering different solutions before finally
settling on a particular approach. But, although Wittgenstein’s way
of working is not the only one, it is certainly a possible way of
working which has produced great philosophy. It is thus obviously
wrong for the RAE to rule out this strategy of delaying publication,
and this is a great weakness of the whole system.

Let us now consider what response a defender of the RAE might
give to this objection. He or she might reply along the following
lines: ‘Philosophy is a peculiar intellectual discipline, and tends to
attract peculiar people. Even by the standards of philosophers,
Wittgenstein was exceptionally strange. Now if we turn from
philosophy to more serious intellectual disciplines such as
mathematics, medicine, physics or astronomy, we shall find that
these scientific disciplines are carried out by more serious people

Donald Gillies

46



for whom the criteria of the RAE are certainly appropriate.’ To
meet this challenge, we must turn to a consideration of science, and
this therefore is a good point at which to begin the main line of
argument of the paper.

In fact we will discover that many of the great scientific
innovators had personalities which were no less unusual than
Wittgenstein’s. It will also emerge that Wittgenstein had some
advantages which several of those who made great advances in
science lacked. Wittgenstein’s work was recognised very early on by
individuals such as Russell and Keynes who could exercise a
powerful influence in the academic world. Some other notable
pioneers had the less agreeable experience of finding that their
innovative work was not recognised by anyone, and indeed was
rejected as absurd by those in powerful academic positions.

In considering how the RAE might affect research in science in
the UK, I will apply the ‘counterfactual methodology’ introduced
by the case of Wittgenstein. I will consider a number of great
advances in science which occurred in the past, and ask whether, if
the RAE had existed in those days, it would have helped or
hindered that advance. The result of the cases which I will consider
is the same as the result in the case of Wittgenstein—namely that
the RAE, if it had been in existence, would constituted an obstacle
to the advance.

I have chosen three cases which are designed to cover a range of
different sciences. The first is in mathematics, the second in
medicine, and the third in astronomy. I have chosen cases where a
very striking scientific advance was made at a theoretical level. I do
not, however, want to focus on theory and neglect practical
applications. It is now generally agreed that the development of
new technological applications of science is very important in order
to make the UK competitive in the era of globalisation. I have
therefore chosen three theoretical advances which had very
important wealth-generating applications.

3. First Case-History: Frege and Mathematical Logic

My first example is taken from the field of mathematics and I want
to consider an important advance made in a branch of the subject
known as mathematical logic. This advance was made by Frege in a
booklet published in 1879, and which is usually referred to by its
German title of Begriffsschrift, which means literally: ‘concept-
writing’. It might be objected to this example that Frege was a

Lessons from the History and Philosophy of Science

47



philosopher rather than a mathematician. It is true that Frege wrote
some very important works on philosophy, but that does not make
him any less a mathematician. Other famous mathematicians such
as Descartes and Leibniz also wrote on philosophy. Frege worked
all his life in the mathematics department of Jena university. The
Begriffsschrift does contain some interesting philosophical remarks,
but it is mainly formal in character. Its contribution is to what is
now called mathematical logic and it is difficult to deny that
mathematical logic is a branch of mathematics.

Indeed Frege’s Begriffsschrift may justly be said to have
introduced modern mathematical logic. In this work Frege presents
for the first time an axiomatic-deductive development of the
propositional calculus and of the predicate calculus (or quantifica-
tion theory). The propositional and predicate calculi are the first
things introduced in any modern treatment of mathematical logic.
What is still more surprising is that the expositions of these calculi
in contemporary textbooks are often quite close to the original
expositions of Frege. Two well-known and widely used textbooks
of mathematical logic are Mendelson (1964) and Bell and
Machover (1977). Mendelson introduces the propositional calculus
and quantification theory in chapters 1 & 2, while Bell and
Machover introduce them in chapters 1, 2 & 3. Of course they both
give many results and approaches which were discovered after
Frege, but they do also give an axiomatic-deductive treatment
which has a lot in common with Frege’s and indeed uses some of
the same axioms that Frege used.1 Frege’s treatment in the
Begriffsschrift includes what is known as higher-order logic,
whereas modern treatments usually limit themselves to first-order
logic. However, leaving this subtlety aside we can say that Frege’s
treatment of both the propositional and predicate calculi is
complete from a modern point of view, though his axiomatic
presentation was subsequently simplified by reducing the number
of axioms. Thus Frege created in the Begriffsschrift a whole new
formal theory which is still today taken as the core of mathematical
logic.

Frege’s remarkable achievement has been fully recognised by
experts in the field since the 1950s. In Appendix II to his English
translation of the Begriffsschrift, Bynum very usefully collects
together some evaluations by well-known scholars writing in the

1 A detailed comparison of the Begriffsschrift with the treatment of the
corresponding material in Mendelson (1964) and Bell and Machover
(1977) is to be found in Gillies, 1992, 275–6.

Donald Gillies

48



1950s and 1960s. Here are some extracts from the passages he gives.
They are all quoted from Bynum, 1972, 236–8.

Quine, 1952 (236): ‘ ... the logical renaissance might be identified
with the publication of Frege’s Begriffsschrift in 1879 ... 1879 did
indeed usher in a renaissance, bringing quantification theory and
therewith the most powerful and most characteristic instrument
of modern logic ... with the aid of quantification theory modern
logicians have been able to illuminate the mechanism of
deduction in general, and the foundations of mathematics in
particular, to a degree hitherto undreamed of.’

Dummett, 1959 (238): ‘There can be no doubt that Boole
deserves great credit for what he achieved ... however ... Boole
cannot correctly be called “the father of modern logic”. The
discoveries which separate modern logic from its precursors are
of course the use of quantifiers ... and a concept of a formal
system, both due to Frege and neither present even in embryo in
the work of Boole.’

Bochenski, 1962 (237): ‘Among all these logicians, Gottlob Frege
holds a unique place. His Begriffsschrift can only be compared
with one other work in the whole history of logic, the Prior
Analytics of Aristotle. The two cannot quite be put on a level, for
Aristotle was the very founder of logic, while Frege could as a
result only develop it. But there is a great likeness between these
two gifted works.’

William and Martha Kneale, 1962 (236–7): ‘Frege’s Begriffss-
chrift is the first really comprehensive system of formal logic... .
Frege’s work ... contains all the essentials of modern logic, and it
is not unfair either to his predecessors or to his successors to say
that 1879 is the most important date in the history of the
subject.’

Frege carried out his researches in mathematical logic for purely
theoretical reasons, but, as so often happens, his results turned out
to be of great practical importance. Mathematical logic is one of the
fundamental tools of present-day computer science, and one can
further say that the computer as we know it today could not have
developed without a prior development of mathematical logic.
Detailed accounts of the use of mathematical logic in computer
science and in the development of computing are contained in
Davis (1988a & b) and in Gillies (2002). There are many specific
examples of the application of mathematical logic in computer

Lessons from the History and Philosophy of Science

49



science, but at a very fundamental level one can say that the
Begriffsschrift is the first example of a fully formalised language,
and so, in a sense, the precursor of all programming languages (see
Davis, 1988b, 316).

Thus Frege’s research turned out to provide some of the
fundamental tools for a wealth-generating technological advance.
Consequently Frege’s research work must be the kind of research
work which a nation like the UK should try to encourage. This
brings us to the question of whether Frege’s research would have
been helped if, counterfactually, there had been a RAE regime
operating in Germany in his day. Suppose there had been a German
RAE in the 1880s, how would Frege have done? The answer is: ‘not
very well.’

In Appendix I to his translation of the Begriffsschrift, Bynum
gives in full the contemporary reviews of the work, all written in
the years 1879 and 1880. It is very interesting to compare these
with the evaluations of the same work made with the benefit of
historical perspective in the 1950s and the 1960s. These are given
by Bynum in his Appendix II, and we have already quoted some
passages.

Turning now to the contemporary reviews of the Begriffsschrift,
they were 6 in number—all quotations from them will be from the
versions in Bynum, 1972, 209–35. Four were written by Germans,
one by a Frenchman (Tannery) and one by an Englishman (Venn).
Only one of these reviews, which was written by a German:
Lasswitz, is favourable. The other three German reviews do make
some favourable remarks, but one cannot help wondering whether
these are designed to be polite to a compatriot and colleague, since
they are contradicted by the majority of the detailed comments on
the work which are highly unfavourable. Thus Hoppe concludes his
review by saying (210): ‘On the whole, the book, as suggestive and
pioneering, is worth while.’ However earlier in the same review he
had written (209): ‘... we doubt that anything has been gained by
the invented formula language itself.’ Similarly Michaelis concludes
his review (218): ‘His work ... certainly does not lack importance.’
However, this rather contradicts the following harsh judgement
given in the body of the review, where Michaelis says (217): ‘...
Frege has to pass over many things in formal logic and detract even
more from its content... . The content of logic which has been
much too meagre up to now, should not be decreased, but
increased.’ In contrast to the later critics who saw Frege as having
made an enormous step forward in logic, Michaelis actually thinks
that Frege has decreased, or detracted from, the content of logic.

Donald Gillies

50



However, the harshest German review comes from the most famous
German logician of the time: Schröder. Schröder actually upbraids
Lasswitz for having written a review supporting the Begriffsschrift,
and says of this review (220) that he casts ‘a disapproving glance at
it’. He refers to Lasswitz later (221) as ‘the Jena reviewer’, which
seems to imply that Lasswitz’s favourable judgement arises from
some personal connection with Frege. Schröder’s own judgement
on the Begriffsschrift is very negative indeed. He thinks that Frege
has done nothing which has not already been done much better by
other people. As he says (220): ‘... the present little book makes an
advance which I should consider very creditable, if a large part of
what it attempts had not already been accomplished by someone
else, and indeed (as I shall prove) in a doubtlessly more adequate
fashion.’ It soon becomes clear that this other person is Boole.
Indeed Schröder goes on to say (221) that, leaving aside the
question of function and generality and some applications, ‘... the
book is devoted to the establishment of a formula language, which
essentially coincides with Boole’s mode of presenting judgements
and Boole’s calculus of judgments, and which certainly in no way
achieves more.’ Here Schröder does seem to make an exception in
favour of Frege’s treatment of generality but this appearance is
deceptive for he later goes on to say that Frege’s treatment of
generality is in no way superior to the Boolean. He writes (229–30):
‘Now in the section concerning “generality”, Frege correctly lays
down stipulations that permit him to express such judgements
precisely. I shall not follow him slavishly here; but on the contrary,
show that one may not perchance find a justification here for his
other deviations from Boole’s notation, and the analogous
modification or extension can easily be achieved in Boolean
notation as well.’ (Logicians will at once see from this that Schröder
has completely failed to grasp the importance of introducing the
quantifiers.) But could Frege at least be defended on the grounds
that he has shed some light on the logical nature of arithmetical
judgements? ‘Not so’, argues Schröder, ‘for that matter too has
already been cleared up by someone else.’ In his own words (231):
‘According to the author, he undertook the entire work with the
intention of obtaining complete clarity with regard to the logical
nature of arithmetical judgements, and above all to test “how far
one could get in arithmetic by means of logical deductions alone”.
If I have properly understood what the author wishes to do, then
this point would also be, in large measure, already settled—namely,
through the perceptive investigations of Hermann Grassmann.’
After dismissing Frege’s work so completely, it is rather surprising

Lessons from the History and Philosophy of Science

51



that Schröder concludes (231): ‘May my comments, however, have
the over-all effect of encouraging the author to further his research,
rather than discouraging him.’ Perhaps Schröder felt some pangs of
guilt about writing so harshly about the work of a young researcher
in his field. The two non-German reviews of the Begriffsschrift are
if anything even more dismissive than the German reviews, and
contain no favourable remarks at all. Tannery in France writes
(233): ‘In such circumstances, we should have a right to demand
complete clarity or a great simplification of formulas or important
results. But much to the contrary, the explanations are insufficient,
the notations are excessively complex; and as far as applications are
concerned, they remain only promises.’ Nowadays one of Frege’s
great advances is considered to be the replacement of the
Aristotelian analysis in terms of subject and predicate by an
analysis using function and argument. Tannery notes this change
but regards it as a mistake (233): ‘The [author] abolishes the
concepts of subject and predicate and replaces them by others which
he calls function and argument... . We cannot deny that this
conception does not seem to be very fruitful.’ Finally Venn in
England entirely agrees with Schröder that Frege has made no
advance over Boole and has indeed taken a step backwards. Venn
writes (234): ‘... it does not seem to me that Dr. Frege’s scheme can
for a moment compare with that of Boole. I should suppose, from
his making no reference whatever to the latter, that he has not seen
it, nor any of the modifications of it with which we are familiar
here. Certainly the merits which he claims as novel for his own
method are common to every symbolic method.’ Venn, moreover,
has no kind words at the end of his review, but concludes by saying
(235): ‘... Dr Frege’s system ... seems to me cumbrous and
inconvenient.’ It is worth noting here that Frege’s advances over
Boole which seem so obvious today and which are mentioned by
Dummett in the passage quoted above, were not appreciated at all
by Schröder and Venn—two of the leading logicians of Frege’s
time. So to sum up. If we go carefully through the six
contemporary reviews of Frege’s Begriffsschrift, we find only one
which takes a positive view of Frege’s work. In the other five, there
is a consensus to be found that the Begriffsschrift makes no advance
on what has already been done, particularly by Boole and the
Booleans, and indeed that it is in many respects inferior to and a
step back from already existing logical works.

What is remarkable is that Frege was not discouraged by these
damning reviews, but continued his work on his logicist programme
for the next 24 years. However, his subsequent books were, if

Donald Gillies

52



anything, even less successful than the Begriffsschrift. The
Foundations of Arithmetic published in 1884 received only 3
reviews—all unfavourable. In 1891 Frege wanted to publish a third
book in the series, but, perhaps not surprisingly, found it hard to
find a publisher. Eventually, however, (Bynum, 1972, 34): ‘the
publisher Hermann Pohle in Jena ... agreed to print the book in two
instalments, the publication of the second part to be dependent
upon a good reception of the first. So, in late 1893, the first volume
of The Basic Laws of Arithmetic appeared.’ This book got only two
reviews—both unfavourable. In the light of this Frege had to
publish the second volume which appeared in 1903, at his own
expense. In the 1890s and 1900s a few avant-garde researchers—
notably Peano and Russell—did begin to study and develop Frege’s
ideas. However, even when Frege retired from Jena at the age of 70
in 1918, general recognition had still eluded him. The situation was
well summed-up by Bochenski in 1962 (quoted from Bynum, 1972,
237–8):

It is a remarkable fact that this logician of them all had to wait
twenty years before he was at all noticed, and another twenty
before his full strictness of procedure was resumed by
Lukasiewicz. In this last respect, everything published between
1879 and 1921 fell below the standard of Frege, and it is seldom
attained even today.

Anyone who is concerned with formulating policies concerned with
research, should in my opinion read carefully the two appendices to
Bynum, 1972. They amount to only 30 pages, but they demonstrate
in a conclusive fashion that the method of peer review can, in some
cases, go very wrong. It does happen that the majority of
contemporary researchers in a field can judge as worthless a piece
of research which is later, with the benefit of historical perspective,
seen as constituting a major advance.

Now the RAE does clearly rely on peer review because the value
of each researcher is judged by a committee of experts in the field.
Indeed the RAE in a sense involves a double use of peer review,
because the members of the RAE consider only research which has
been published, and, to get a piece of work published, a researcher
has usually to submit it to a journal which uses peer review to assess
whether it is worth publishing. The problem facing those like
Frege, whose work is judged of little value by the majority of their
peers, is that they may find it difficult to publish at all. This applied
to Frege himself. He wrote two papers replying to the criticism of
Schröder and Venn that his work was inferior to that of Boole.

Lessons from the History and Philosophy of Science

53



However he was unable to publish these papers (cf. Bynum, 1972,
21), and they only appeared long after Frege’s death. Those who
find their peers against their work will certainly be excluded from
publishing in the more famous journals and may have to resort to
publishing in lower quality journals or even to publishing the
material in book form at their own expense, as Frege did in 1903.
Now theoretically the RAE committee reads carefully and judges
on their merits all the works submitted to it, but of course in
practice papers which have appeared in high ranking journals, or
books which have been published by prestigious firms such as
Oxford University Press, are likely to be judged more favourably.
Conversely papers which have appeared in low ranking journals, or,
worse still, books published at the author’s own expense—
something usually called ‘vanity publishing’—are likely to be
judged more harshly. We have therefore to conclude that if the
RAE had existed in Germany in the 1880s Frege would have got a
very low rating.

Even in the RAE free Germany of the period, Frege did not have
an easy time. A fascinating portrait of him in the years 1910–14 is
given by Carnap in his intellectual autobiography (Carnap, 1963).
Carnap’s involvement with Frege appears to have come about
rather by chance. Carnap’s family lived in Jena and Carnap went to
the local university where Frege taught. Carnap writes (1963, 5):

In the fall of 1910, I attended Frege’s course “Begriffsschrift”
(conceptual notation, ideography), out of curiosity, not knowing
anything either of the man or the subject except for a friend’s
remark that somebody had found it interesting. We found a very
small number of other students, there. Frege looked old beyond
his years. He was of small stature, rather shy, extremely
introverted. He seldom looked at the audience. Ordinarily we
saw only his back, while he drew the strange diagrams of his
symbolism on the blackboard and explained them. Never did a
student ask a question or make a remark, whether during the
lecture or afterwards. The possibility of a discussion seemed to
be out of the question.

Earlier in his account, Carnap says (1963, 4):

Gottlob Frege (1848–1925) was at that time, although past 60,
only Professor Extraordinarius (Associate Professor) of math-
ematics in Jena. His work was practically unknown in Germany;
neither mathematicians nor philosophers paid any attention to it.

Donald Gillies

54



It was obvious that Frege was deeply disappointed and
sometimes bitter about this dead silence.

Carnap, however, took a liking to Frege’s work and attended his two
advanced courses “Begriffsschrift II” in 1913 and his course Logik
in der Mathematik in 1914. Carnap records that “Begriffsschrift
II” was attended by 3 students: Carnap, a friend of Carnap’s, and
(Carnap, 1963, 5) ‘a retired major of the army who studied some of
the new ideas in mathematics as a hobby.’

We can see from this that Frege’s career was hardly a great
success, but, if there had been a RAE regime in Germany, things
would have gone even worse for him. As we have seen, Frege would
undoubtedly have got a low rating in the RAE exercise, and the
inevitable penalties would have fallen on his head. His research
time would have been cut and he would have been forced to take on
extra teaching duties. Thus he would not have had the necessary
research time to develop his mathematical logic. Moreover, as we
can see from Carnap’s description, Frege may not have performed
particularly well as a teacher. He seemed to attract very few
students, and his teaching technique does not appear to have been
of the kind recommended by educational experts. Having failed as
both a researcher and a teacher, there is little doubt than, under a
RAE regime, Frege would have been forced to retire early rather
than allowed to stay on until he was 70. Thus Carnap would never
have been able to attend his lectures, and the development and
diffusion of the new important ideas of mathematical logic would
have been held up still further.

4. Second Case-History: Semmelweis and Antisepsis

My second case-history, as we shall see, has many points in
common with the first. However, it does differ very strikingly as
regards the branch of science in which the research was conducted.
Frege’s research was purely theoretical, and was carried out in a
branch of mathematics, mathematical logic, which is closely linked
to philosophy. Semmelweis’s research by contrast was highly
empirical, and was carried out in medicine. In fact Semmelweis’s
investigation was into the causes of a terrible disease (puerperal
fever) which affected women who had just given birth. Puerperal
fever was, at the time, the principal cause of death in childbirth.

Semmelweis was Hungarian, but studied medicine at the
University of Vienna. In 1844 he qualified as a doctor, and, later in

Lessons from the History and Philosophy of Science

55



the same year obtained the degree of Master of Midwifery. From
then until 1849, he held the posts of either aspirant to assistant or
full assistant at the first maternity clinic in Vienna. It was during
this period that he carried out his research.2

The Vienna Maternity Hospital was divided into two clinics
from 1833. Patients were admitted to the two clinics on alternate
days thereby producing, unintentionally, a system of random
allocation. Between 1833 and 1840, medical students, doctors and
midwives attended both clinics, but, thereafter, although doctors
went to both clinics, the first clinic only was used for the instruction
of medical students who were all male in those days, and the second
clinic was reserved for the instruction of midwives. When
Semmelweis began working as a full assistant in 1846, the mortality
statistics showed a strange phenomenon

Between 1833 and 1840, the death rates in the two clinics had
been comparable, but, in the period 1841–46, the death rate in the
first clinic was 9.92% and in the second clinic 3.88%. The first
figure is more than 2.5 times the second—a difference which is
certainly statistically significant. The quoted figures actually
underestimate the difference since some severe cases of puerperal
fever were removed from the first clinic to the general hospital
where they died—thereby disappearing from the first clinic’s
mortality statistics. This rarely happened in the second clinic.
Semmelweis was puzzled and set himself the task of finding the
cause of the higher death rate in the first clinic.

Semmelweis followed a procedure rather similar to Popper’s
conjectures and refutations. He considered in turn a number of
hypotheses as to what might be the cause of the difference between
the two clinics. He then compared these hypotheses to the facts, and
found that each one of a long series of hypotheses was refuted by
this comparison. Eventually, however, Semmelweis did hit on a
hypothesis which was corroborated by the observations.

The first hypothesis considered by Semmelweis was that the
higher death rate in the first clinic was due to ‘atmospheric-cosmic-
terrestial’ factors. This sounds strange but is just a way of referring
to the miasma theory of disease which was standard at the time.
However Semmelweis pointed out that it could not explain the

2 This account of Semmelweis’s research is a shortened version of the
one given in my paper: Gillies (2005). That paper also contains more
detailed references to the considerable literature on Semmelweis.
Semmelweis’s own account of his researches in Semmelweis (1861) is also
worth consulting.

Donald Gillies

56



different mortality rates in the first and second clinics. These were
under the same roof and had an ante-room in common. So they
must be exposed to the same ‘atmospheric-cosmic-terrestial’
influences. Yet the death rates in the two clinics were very different.

The next hypothesis was that overcrowding was the key factor,
but this too was easily refuted since the second clinic was always
more crowded than the first, which, not surprisingly had acquired
an evil reputation among the patients, almost all of whom tried to
avoid it.

In this sort of way Semmelweis eliminated quite a number of
curious hypotheses. One concerned the appearance of a priest to
give the last sacrament to a dying woman. The arrangement of the
rooms meant that the priest, arrayed in his robes, and with an
attendant before him ringing a bell had to pass through five wards
of the first clinic before reaching the sickroom where the woman
lay dying. The priest had, however, direct access to the sickroom in
the case of the second clinic. The hypothesis then was that the
terrifying psychological effect of the priest’s appearance debilitated
patients in the first clinic, and made them more liable to puerperal
fever. Semmelweis persuaded the priest to come by a less direct
route, without bells, and without passing through the other clinic
rooms. The two clinics were made identical in this respect as well,
but the mortality rate was unaffected.

After trying out these hypotheses and others unsuccessfully,
Semmelweis was in a depressed state in the winter of 1846–7.
However a tragic event early in 1847 led him to formulate a new
hypothesis. On 20th March 1847, Semmelweis heard with sorrow of
the death of Professor Kolletschka. In the course of a post-mortem
examination, Professor Kolletschka had received a wound on his
finger from the knife of one of the students helping to carry out the
autopsy. As a result Kolletschka died not long afterwards of a
disease very similar to puerperal fever. Semmelweis reasoned that
Kolletschka’s death had been owing to cadaverous matter entering
his bloodstream. Could the same cause explain the higher death
rate of patients in the first clinic? In fact professors, assistants and
students often went directly from dissecting corpses to examining
patients in the first clinic. It is true that they washed their hands
with soap and water, but perhaps some cadaverous particles still
adhered to their hands. Indeed this seemed probable since their
hands often retained a cadaverous odour after washing. The doctors
and medical students might then infect some of the patients in the
first clinic with these cadaverous particles, thereby giving them

Lessons from the History and Philosophy of Science

57



puerperal fever. This would explain why the death rate was lower in
the second clinic, since the student midwives did not carry out
post-mortems.

In order to test this hypothesis, Semmelweis, from some time in
May 1847, required everyone to wash their hands in disinfectant
before making examinations. At first he used chlorina liquida, but,
as this was rather expensive, chlorinated lime was substituted. The
result was dramatic. In 1848 the mortality rate in the first clinic fell
to 1.27%, while that in the second clinic was 1.30%. This was the
first time the mortality rate in the first clinic had been lower than
that of the second clinic since the medical students had been
divided from the student midwives in 1841.

Through a consideration of some further cases, Semmelweis
extended his theory to the view that, not just cadaverous particles,
but any decaying organic matter, could cause puerperal fever if it
entered the bloodstream of a patient.

Let us now look at Semmelweis’s theory from a modern point of
view. Puerperal fever is now known as ‘post-partum sepsis’ and is
considered to be a bacterial infection. The bacterium principally
responsible is streptococcus pyogenes, but other streptococci and
staphylococci may be involved. Thus, from a modern point of view,
cadaverous particles and other decaying organic matter would not
necessarily cause puerperal fever but only if they contain a large
enough quantity of living streptococci and staphylococci. However as
putrid matter derived from living organisms is a good source of
such bacteria, Semmelweis was not far wrong.

As for the hand washing recommended by Semmelweis, that is of
course absolutely standard in hospitals. Medical staff have to wash
their hands in antiseptic soap (hibiscrub), and there is also a
gelatinous substance (alcogel) which is squirted on to the hand.
Naturally a doctor’s hands must be sterilised in this way before
examining any patient—exactly as Semmelweis recommended.

Not only are Semmelweis’s views regarded as largely correct
form a modern point of view, but the investigation which led him to
them is now held up as model of good scientific method. In fact
Hempel in his 1966 book: Philosophy of Natural Science gives a
number of examples of what he regards as excellent scientific
investigations, and the very first of these is Semmelweis’s research
into puerperal fever.

This then is the modern point of view, but how did
Semmelweis’s contemporaries react to his new theory of the cause
of puerperal fever and the practical recommendations based on it?

Donald Gillies

58



The short answer is that Semmelweis’s reception by his contempo-
raries was almost exactly the same as Frege’s. Semmelweis did
manage to persuade one or two doctors of the truth of his findings,
but the vast majority of the medical profession rejected his theory
and ignored the practical recommendations based upon it. I discuss
some of the detailed responses to Semmelweis in my longer paper
on the subject (see Gillies, 2005, 178–9). Here I will only mention
one typical reaction. After Semmelweis had made his discovery in
1848, he and some of his friends in Vienna wrote about them to the
directors of several maternity hospitals. Simpson of Edinburgh
replied somewhat rudely to this letter saying that its authors
obviously had not studied the obstetrical literature in English.
Simpson was of course a very important figure in the medical
world of the time. He had introduced the use of chloroform for
operations, and had recommended its use as a pain-killer in
childbirth. His response to Semmelweis and his friends is very
similar in character to Venn’s review of Frege’s Begriffsschrift.

In Vienna the Professor and Head of the Maternity Clinics,
Johann Klein, was opposed to Semmelweis’s ideas, and his
opposition, and that of others, caused Semmelweis to leave Vienna
in 1850. He did however get a position in a Maternity Hospital at
Budapest in his native Hungary. Here he wrote up his new theory
of the causes of puerperal fever, and answered the objections which
had been made to it. These writings were published in book form in
1861, but once again had no success in persuading the medical
profession to adopt his ideas.

Semmelweis’s case is very similar to Frege’s. Semmelweis, like
Frege, had great difficulties, and, if counterfactually, there had
been a RAE regime at the time, these difficulties would have
become worse. Semmelweis’s work would obviously have been
judged by peer review to have no value, and his allowance of
research time would have been reduced, so that he might not have
had the time to write up his results in book form and to answer his
critics.

The failure of the research community to recognise Semmel-
weis’s work had of course much more serious consequences than
the corresponding failure to appreciate Frege’s innovations. In the
twenty years after 1847 when Semmelweis made his basic
discoveries, hospitals throughout the world were plagued with what
were known as ‘hospital diseases’, that is to say, diseases which a
patient entering a hospital was very likely to contract. These
included not just puerperal fever, but a whole range of other
unpleasant illnesses. There were wound sepsis, hospital gangrene,

Lessons from the History and Philosophy of Science

59



tetanus, and spreading gangrene, erysipelas (or ‘St. Anthony’s
fire’), pyaemia and septicaemia which are two different forms of
blood poisoning, and so on. Many of these diseases were fatal.
From the modern point of view, they are all bacterial diseases
which can be conquered by applying the kind of antiseptic
precautions recommended by Semmelweis.

In 1871, over twenty years after his rather abrupt reply to
Semmelweis and his friends, Simpson of Edinburgh wrote a series
of articles on ‘Hospitalism’. These contained his famous claim,
well-supported by statistics, that ‘the man laid on the operating-
table in one of our surgical hospitals is exposed to more chances of
death than the English soldier on the field of Waterloo’. Simpson
thought that hospitals infected with pyaemia might have to be
demolished completely. So serious was the crisis, that he even
recommended replacing hospitals by villages of small iron huts to
accommodate one or two patients, which were to be pulled down
and re-erected periodically. Luckily the theory and practice of
antisepsis were introduced in Britain by Lister in 1865, and were
supported by the germ theory of disease developed by Pasteur in
France and Koch in Germany. The new antiseptic methods had
become general by the mid 1880s, so that the hospital crisis was
averted. All the same, the failure to recognise Semmelweis’s work
must have cost the lives of many patients.

In my longer paper on the Semmelweis case (Gillies, 2005,
180–1), I argue that, in the history and philosophy of science, it is
customary to cite historical examples of excellent science in order
to exemplify what are claimed to be good methodological principles
for science. However instances in which the scientific community
makes a mistake, as happened in the Semmelweis case or that of
Frege, can also be valuable in suggesting new rules of practice
designed to make such mistakes less likely in the future. From this
point of view, the RAE is clearly a step backwards. Instead of
learning from the mistakes which were made regarding Frege and
Semmelweis, and introducing a system designed to make such
mistakes less likely in the future, it does the opposite. If the RAE
had been in existence in the days of Frege and Semmelweis, it
would, as we have seen, have made their position even worse than it
already was. Naturally the same will apply to any future brilliant
innovators like Frege and Semmelweis who have the misfortune to
be working in a RAE regime.

This point can also be made by introducing a distinction taken
from the theory of statistical tests. Statistical tests are said to be
liable to two types of error (Type I error, and Type II error). A

Donald Gillies

60



Type I error occurs if the test leads to the rejection of a hypothesis
which is in fact true. A Type II error occurs if the test leads to the
confirmation of a hypothesis which is in fact false. Analogously we
could say that a research assessment procedure commits a Type I
error if it leads to funding being withdrawn from a researcher or
research programme which would have obtained excellent results
had it been continued. A research assessment procedure commits a
Type II error if it leads to funding being continued for a researcher
or research programme which obtains no good results however long
it goes on. This distinction leads to the following general criticism
of the RAE. The RAE concentrates exclusively on eliminating
Type II errors. The idea behind the RAE is to make research more
cost effective by withdrawing funds from bad researchers and
giving them to good researchers. No thought is devoted to the
possibility of making a Type I error, the error that is of
withdrawing funding from researchers who would have made
important advances if their research had been supported. Yet the
history of science shows that Type I errors are much more serious
than Type II errors. The case of Semmelweis is a very striking
example. The fact that his line of research was not recognised and
supported by the medical community meant that, for twenty years
after his investigation, thousands of patients lost their lives and
there was a general crisis in the whole hospital system.

In comparison with Type I errors, Type II errors are much less
serious. The worst that can happen is that some government money
is spent with nothing to show for it. Moreover Type II errors are
inevitable from the very nature of research. Suppose research is
required on some problem, and there are four different approaches
to its solution which lead to four different research programmes. It
may be almost impossible to say at the beginning which of the four
programmes is going to lead to success. Suppose it turns out to be
research programme number 3. The researchers on programmes 1,
2 & 4 may be just as competent and hard-working as those on
programme 3, but, because their efforts are being made in the
wrong direction, they will lead nowhere. Suppose programme 3 is
cancelled in order to save money (Type I error), then all the money
spent on research in the problem will lead nowhere. It will be a total
loss. On the other hand if another programme (5) is also funded,
the costs will be a bit higher but a successful result will be obtained.
This shows why Type I errors are much more serious than Type II
errors, and why funding bodies should make sure that some
funding at least is given to every research school and approach

Lessons from the History and Philosophy of Science

61



rather than concentrating on the hopeless task of trying to foresee
which approach will in the long run prove successful.

The same analysis also shows why peer review as a system can
often give wrong results. Let us return to our example of the
problem being tackled by four different research programmes, of
which programme number 3 ultimately proves successful. Let us
suppose further (which indeed is often the case) that initially
programme 3 attracts many fewer researchers than programmes 1,
2 & 4. Now it is characteristic of most researchers that they think
their own approach to the problem is the correct one, and that other
approaches are misguided. If a peer review is conducted by a
committee whose researchers are a random sample of those
working on the problem, then the majority will be working on
programmes 1, 2 & 4, and are therefore very likely to give a
negative judgement of the merits of programme 3. As the result of
the recommendation of such a peer review, funding might be
withdrawn from programme 3, and the solution of the problem
might remain undiscovered for a long time.

5. Third Case-History: Copernicus and Astronomy

I now turn to my third example which I will deal with more
concisely both because it is more familiar and because my general
line of argument should by now have become fairly clear. However,
it is worth looking at this example because it deals with yet another
branch of science (astronomy) and also a different historical
period.3

Copernicus (1473–1543) was born in which is now Poland and
studied at Universities in both Poland and Italy. Through the
influence of his uncle, he obtained the post of Canon of
Frauenberg Cathedral in 1497, and held this position until his
death. Copernicus’ duties as canon seem to have left him plenty of
time for other activities, and he seems to have devoted much of this
time to developing in detail his new theory of the universe. This
was published as De Revolutionibus Orbium Caelestium, when
Copernicus was on his death bed. In the preface Copernicus states
that he had meditated on this work for more than 36 years.

There is little doubt that during Copernicus’ lifetime and for
more than 50 or 60 years after his death, his view that the Earth

3 A more detailed account of Copernicus’ work on astronomy is to be
found in Kuhn (1957).

Donald Gillies

62



moved was regarded as absurd, not only by the vast majority of the
general public, but also by the vast majority of those who were
expert in astronomy. It is significant that De Revolutionibus was not
put on the index by the Roman Catholic Church until 1616. It was
not until then that Copernicanism had sufficient adherents to be
considered a threat.

Although the majority of expert astronomers of the period would
have dismissed the Copernican view as absurd, a few such
astronomers, notably Kepler and Galileo, did side with Copernicus
and carried out researches developing his theory until, in due
course, it won general acceptance by astronomers not influenced by
the Roman Catholic Church’s opposition.

Copernicus’ research, like that of Frege and Semmelweis, had
very important practical applications. Despite the Roman Catholic
Church’s opposition to his theory, his calculations were used in the
reform of the calendar carried out by Pope Gregory XIII in 1582.
Ironically the Protestant countries, whose astronomers were the
first to accept the Copernican theory, rejected the Gregorian
calendar for a long time on the ground that it had been introduced
by the Roman Catholic Church and must presumably therefore be
bad. Copernicus’ theory was also used to produce improved
astronomical tables. Reinhold used De Revolutionibus in the
production of his Prutenic Tables which appeared in 1551. These
were the first complete tables prepared in Europe for three
centuries. In 1627, they were superseded by the Rudolfine Tables
which Kepler produced using his much improved version of
Copernicus’s theory. The Rudolfine Tables were clearly superior to
all astronomical tables in use before. Of course astronomical tables
were applied in navigation, and so were an important tool for
promoting the growth of European maritime trade.

Let us now once again apply our counterfactual methodology and
consider how Copernicus would have been affected if, instead of
being a Canon of Frauenberg, he had lived under a RAE regime. Of
course it is indeed rather anachronistic to suppose that something
like the RAE might have been in existence in such a distant
historical period. Yet I think we can still say with some confidence
that if it had existed then, it would have impacted negatively on
Copernicus. Under a RAE regime, Copernicus would not have
been allowed to continue his research peacefully as a Canon of
Frauenberg. On the contrary, he would have been brought to
account to make sure he was not wasting the tax-payers’ money. In
order to be allowed time to continue his research, he would have
had to submit samples of his research work to a committee of

Lessons from the History and Philosophy of Science

63



experts in the field. Now nearly all these experts, as we have already
pointed out, would have judged that Copernicus’ research was
absurd and not worth funding. Thus Copernicus would have been
sent off to a teaching university with little time for research, and
would have had to devote most of his time to teaching astronomy to
undergraduates. Naturally, as the syllabus would have been
determined by the majority of his colleagues, he would have had to
teach, not his new theory, but the standard Aristotelian-Ptolemaic
account of astronomy. So Copernicus, under a system of funding of
RAE type, would have been deprived of his research time, and
forced to spend his days teaching the Aristotelian-Ptolemaic
account of astronomy. Meanwhile the leading experts of the
Aristotelian-Ptolemaic theory would have had posts at the
well-funded research universities giving them plenty of time to
pursue their research. No doubt they would have developed
Aristotelian-Ptolemaic theory by means of ever more mathemati-
cally ingenious combinations of epicycles. It need hardly be said
that all this would have acted as an extreme dampener on the
progress of astronomy.

I have given three examples of cases in which a regime of RAE
type would have impeded rather than helped scientific advance. Of
course many more cases along the same lines could be described,
but it will now be more fruitful to turn from history of science to
philosophy of science. In the next section, I will try to analyse the
factors, which in the cases of Copernicus, Frege and Semmelweis,
led to the failure of the peer review method. As we shall see, this is
not a problem which has arisen in just a few cases, but is an
underlying pattern in the development of science.

6. Kuhn’s Distinction between Normal and Revolutionary
Science

The part of philosophy of science which I would like to consider is
Kuhn’s theory of scientific development as set out in his The
Structure of Scientific Revolutions (1962). Kuhn’s view is that
science develops through periods of normal science which are
characterised by the dominance of a paradigm, but which are
interrupted by occasional revolutions during which the old
paradigm is replaced by a new one. Kuhn gives three main
examples of scientific revolutions. These are the Copernican

Donald Gillies

64



Revolution, the Chemical Revolution, and the Einsteinian Revolu-
tion. As we have already discussed Copernicus, I will illustrate
Kuhn’s views by a brief account of the other two examples.

The Chemical Revolution. The main theme of the chemical
revolution was the replacement of the phlogiston theory by the
oxygen theory, though there were many other important changes as
well. According to the phlogiston theory, bodies are inflammable if
they contain a substance called phlogiston, and this is released
when the body burns. The phlogiston theory was also used to
explain the calcination of metals. When a metal is heated in air, in
many cases it turns into a powder known as the calx, e.g. iron →
rust. Conversely the calx is usually found in ores of the metal, and
the metal itself could often be obtained by heating with charcoal.
These transformations were explained by postulating that

calx + phlogiston = metal

When we heat a metal, phlogiston is given off, and the calx remains.
Conversely when we heat the calx with charcoal, since charcoal is
very rich in phlogiston because it burns easily, the phlogiston from
the charcoal combines with the calx to give the metal.

In the oxygen theory, burning is explained as the combination of
the substance with oxygen; while the calx is identified with the
oxide of the metal. So turning a metal into its calx by heating in air
is explained by the equation

metal + oxygen = metal oxide

Similarly obtaining the metal by heating the calx with charcoal is
explained by the equation

metal oxide + carbon = metal + carbon dioxide

The oxygen theory was developed by Lavoisier. At the beginning of
his researches in 1772, he was already sceptical of the then
dominant phlogiston theory. In the next decade or so, many
experimental discoveries concerning gases were made. These
discoveries were mainly owing to the English experimental
chemists—particularly Priestley and Cavendish. However, these
English chemists remained faithful to the phlogiston theory. For
example Priestley referred to what we now call oxygen as
dephlogisticated air. Lavoisier, on the other hand, reinterpreted
their results in terms of his new and developing oxygen theory.
Lavoisier’s new paradigm for chemistry was set out in his Traité
élémentaire de chimie of 1789, and within a few years it was adopted

Lessons from the History and Philosophy of Science

65



by the majority of chemists. Priestley, however, who lived until
1804 never gave up the phlogiston theory.

The Einsteinian Revolution. The triumph of the Newtonian
paradigm initiated a new period of normal science for astronomy (c.
1700—c. 1900). The dominant paradigm consisted of Newtonian
mechanics including the law of gravity, and the normal scientist
had to use this tool to explain the motions of the heavenly bodies in
detail—comets, perturbations of the planets and the moon, etc. In
the Einsteinian revolution (c. 1900—c. 1920), however, the
Newtonian paradigm was replaced by the special and general
theories of relativity.

Further research in the philosophy of science has shown that
Kuhn’s model, with some modifications, can be extended to
mathematics and medicine. Thus Frege’s work can be considered as
a initiating a revolution in logic analogous to the Copernican
revolution in astronomy. The change was from an Aristotelian
paradigm, whose core was the theory of the syllogism, to a new
paradigm whose core was propositional and first-order predicate
calculus.4 Then again Semmelweis’s investigation can be seen as
one of the first steps in a revolution in medicine. The change was
from a paradigm whose core was the miasma and contagion theories
of disease to a new paradigm with the germ theory of disease as its
core.5

Now one of the strengths of Kuhn’s theory is that it explains
why the scientific community made such mistaken judgements
regarding figures like Copernicus, Semmelweis and Frege. On
Kuhn’s model, at the beginning of a revolution almost all the
researchers in the field accept the dominant paradigm, and, from
the point of view of this paradigm, the new revolutionary approach
will indeed seem absurd.

Another important consequence of Kuhn’s theory is that the
mistaken judgements regarding Copernicus, Semmelweis and
Frege are not features of science’s past, but are likely to recur over
and over again. Of course, long before Kuhn, the Copernican
revolution had been studied by historians of science. However, it
tended to be regarded as something of a ‘one-off ’ event—a
dramatic change which had introduced modern science, but was not
likely to recur. This is reflected in the fact that it was often referred
to as: The Scientific Revolution. Kuhn’s originality was to suggest
that all branches of science develop through periodic revolutions.

4 For more details, see Gillies (1992).
5 For more details, see Gillies (2005).

Donald Gillies

66



This new view was obviously suggested by the revolution in physics
in the first few decades of the twentieth century which led to the
triumph of relativity theory and quantum mechanics. Kuhn’s
model of scientific development was roughly as follows. For most
of the time we have ‘normal science’ in which the scientists working
in a particular area all, except perhaps for a few dissidents, accept
the same dominant paradigm. Within the framework of that
paradigm, steady, if perhaps somewhat slow, progress is made.
Every so often, however, a period of revolution occurs in which the
previously dominant paradigm comes to be criticized by a small
number of revolutionary scientists. This small group succeeds in
developing a new paradigm, and in persuading their colleagues to
accept it. Thus there comes about a revolutionary shift from the old
paradigm to a new one. Although revolutions occur only
occasionally in the development of a field of science, such
revolutions are the exciting times in which really big progress is
made in the field.

Kuhn’s model of scientific development is, in my view, strongly
confirmed by studies in the history of science. Indeed it applies not
just to the natural sciences considered by Kuhn, but also to science
in the broader sense considered in this paper which includes also
mathematics and medicine. In the next section, I will use Kuhn’s
model to examine the likely effects of the RAE on scientific
research in the UK.

7. Analysis of the Likely Effects of the RAE

Let us begin by considering the effects of the RAE on normal
science. In a period of normal science, those working in a branch of
the subject will all accept the dominant paradigm, and no
revolutionary alternative will have been suggested. It will then be
an easier matter for the experts in the field to judge who is best
according to the criteria of the dominant paradigm. Allocating
research funding to these most successful ‘puzzle solvers’, as Kuhn
calls them, will usually enable the normal science activity of puzzle
solving to continue successfully. One qualification to this must,
however, be introduced on the basis of the discussion of Type I
and Type II errors which was given at the end of section 4. We
there gave an example of research into a problem, where there are
four different approaches to its solution leading to four different
research programmes. This situation is still possible, and indeed
often occurs, in normal science, for the four different research

Lessons from the History and Philosophy of Science

67



programmes could all be compatible with the dominant paradigm.
As we pointed out, in such circumstances, a thoughtless use of peer
review as a tool could easily lead to wrong decisions. Suppose
programme 3 in fact turns out to be the one which leads to the
solution of the problem, but suppose initially it is supported by
only a few researchers. A peer review conducted by a committee
chosen at random from those working on the problem might well
contain an overwhelming majority of researchers working on
programmes 1, 2 & 4, and such a committee could easily
recommend the cancellation of funding for research programme 3,
a decision which would have disastrous long term results. With this
qualification, however, we can say that the RAE is not likely to have
too damaging an effect on normal science. The only problem is that
normal science tends to be routine in character and to produce
small advances rather slowly. Surely, however, we want a research
regime to encourage big advances in the subject, exciting
innovations, breakthroughs, etc.

It is precisely here that the RAE is likely to fail. Any big advance
is likely to have something revolutionary about it, something which
challenges accepted ideas and paradigms. However it is precisely in
these case, as we have shown above, that the RAE with its excessive
reliance on peer review is likely to have a very negative effect. Our
conclusion then is the RAE is likely to shift the UK research
community in the direction of producing the routine research of
normal science resulting in slow progress and small advances. At
the same time it will have the effect of tending to stifle the really
good research—the big advances, the exciting innovations, the
major breakthroughs. Clearly then the overall effect of the RAE is
likely to be very negative as regards research output in the UK.

The RAE is also likely to impact very negatively on the
production of wealth-generating science-based technologies in the
UK. The reason for this is that the most striking technologies from
the point of view of wealth-generation are often based on
revolutionary scientific advances. This is well-illustrated by the
three examples considered in this paper. Copernicus’ new
astronomy led, as we have seen, to a much improved navigation,
and this was essential to the profitable development of European
sea-borne trade in the 17th and 18th centuries. The new
mathematical logic introduced by Frege was essential for the
development of the computer. It is significant here that Bertrand
Russell was one of the first to recognise and develop Frege’s work.
Russell established an interest in mathematical logic in the UK,
which passed on to two later researchers at Cambridge: Max

Donald Gillies

68



Newman and his student Alan Turing. After the Second World
War, Newman and Turing were part of the team at Manchester
which produced the Manchester Automatic Digital Machine
(MADM). This started running in 1948, and can be considered as
the first computer in the modern sense.6 Thus Russell’s early
recognition of Frege’s revolutionary innovations led indirectly to
the UK taking an early lead in the computer field. This early lead
was later lost, as we know, but this was owing to lack of sufficient
investment by either the public or private sectors. There was no
problem with the UK’s research community in those pre-RAE
days. Our third case was concerned the revolutionary introduction
of antisepsis in conjunction with revolutionary new theories about
the causes of disease. We focussed on Semmelweis whose research
work was rejected by the medical community of his time. As we
remarked, however, Lister was more successful, and was able to
persuade the medical community in the UK to accept antisepsis.
This was obviously of great benefit to patients, but I would now
like to add that it led to very successful business developments. For
his new form of surgery Lister needed antiseptic dressings, and he
devoted a lot of time and thought to working out the best design
and composition of such dressings. As his ideas came to be
accepted, the demand for these dressings increased and companies
were formed to produce them. One of these was founded by a
pharmacist Thomas James Smith. In 1896, he went into
partnership with his nephew Horatio Nelson Smith to produce and
sell antiseptic dressings. They called the firm Smith and Nephew.
Today Smith and Nephew is a transnational company operating in
33 countries and generating sales of £1.25 billion. The company is
still involved in wound care as one of its three main specialities, but
it has expanded into orthopaedics and endoscopy. One of its
well-known products is elastoplast which was developed in 1928.
The general design of elastoplast is based on some of the antiseptic
dressings developed by Lister. The commercial success of Smith
and Nephew is a good illustration of the importance of having a
satisfactory research regime in the UK. If Lister’s research on
antisepsis had met the same fate as that of Semmelweis only 17
years earlier, then the firm of Smith and Nephew would not be
with us today.

6 For more details about the Manchester Automatic Digital Machine
and its claim to be the first computer in the modern sense, see Gillies and
Zheng, 2001, 445–9.

Lessons from the History and Philosophy of Science

69



8. General Conclusions

The RAE is very expensive both in money and in the time which
academics in the UK have to devote to it. I have argued in this
paper that its likely effect is to shift the UK research community in
the direction of producing the routine research of normal science
resulting in slow progress and small advances, while tending to
stifle the really good research—the big advances, the exciting
innovations, the big breakthroughs. Thus a great deal of tax payers’
money is being spent on an exercise whose likely effect is to make
the research output of the UK worse rather than better. Only one
conclusion can be drawn from this, namely that the RAE should be
abolished straightaway.

My general argument has brought to light three major faults in
the RAE. (1) The RAE rules out the research strategy of working
for many years on a piece of research before publication. Yet this
strategy has proved very successful in the past. We gave Copernicus
and Wittgenstein as examples of the success of this strategy, but
many other examples could of course be given. (2) The RAE relies
too strongly on peer review, which may work not too badly for
normal science, but which can give very erroneous results when it
comes to the most important revolutionary advances in science.
Frege, Semmelweis and Copernicus were all examples of this. (3)
The RAE concentrates too much on trying to eliminate Type II
error, that is the error of funding bad research, but devotes no
consideration to eliminating Type I error, that is the error of failing
to fund good research. Yet Type I errors have much more
damaging effects on the progress of research than Type II errors.
This was illustrated above all by the case of Semmelweis where a
Type I error of failing to recognise and support important research
led to thousands of patients dying and a general crisis in the
hospitals.

Abolition of the RAE could be accomplished very easily because
it would produce no disruption in the system. Indeed research in
the UK was very successful for many decades with no RAE. We
argued for this in detail in the case of philosophy but the same
applies to other areas of research. However, here it might be
objected that we can’t just go back to the status quo ante RAE, for
the whole university system and research community has expanded
considerably since 1975, and so can no longer be run along the lines
which were used in this earlier period. I agree with this point, but
would still stress that there is no hurry to introduce a new system
for organising research, and that there should be a great deal of

Donald Gillies

70



thought, discussion and consultation before doing so. What our
critique of the RAE has shown is that research is rather a subtle
and complicated activity and that producing a regime in which it
flourishes is not an easy matter. Perhaps the biggest difficulty lies in
the fact that we cannot tell immediately whether a piece of research
is good, and sometimes it is only after a period of as long as thirty
years that a fairly definite judgement can be reached. In this respect
research differs very strikingly from competitive sports such as
tennis or football. We can grade tennis players at a particular
moment simply by getting them to play each other in tournaments
and seeing who beats who. However, we cannot be sure that a
researcher whose work is now judged to be of poor quality may not
turn out after all to be a Copernicus, a Semmelweis, or a Frege.
Even in cases where it is recognised that a scientific discovery has
been made, the importance of that discovery may not become
apparent for many years. A good example of this is Alexander
Fleming’s discovery of penicillin which was made in 1928, and
published by Fleming in 1929. Fleming was not harshly treated like
Semmelweis or Frege, but the significance of his discovery was
certainly not recognised immediately. The head of the laboratory
where Fleming worked (Sir Almroth Wright) was a Fellow of the
Royal Society and a great admirer of Fleming. In 1930 Wright
proposed Fleming for the Royal Society citing his discovery of
penicillin and some other research achievements. Fleming, how-
ever, was not elected in 1930 or in the four following years. In fact
Fleming only became a Fellow of the Royal Society in 1943 when
he was 62 years old.7

But if it is not possible to tell whether a piece of research is good
except after a long lapse of time—perhaps as long as thirty years,
how can we possibly decide what research to fund at a given
moment? It almost looks as if the problem of devising a sensible
system for funding research is insoluble. This is not really so,
however, and there are ways of overcoming the difficulty. Needless
to say, however, they are not along the lines of the RAE. What is
needed here is some new thinking and a quite different approach. I
have my own ideas of what this different approach might be like,
but it would not be appropriate to give them here since my aim in
this paper is to give a critique of the existing system. I hope,
however, that my paper might be useful to those trying to devise a
new system for organising research in the UK by suggesting a way

7 These details about Fleming and the Royal Society are taken from
Macfarlane, 1984, 140–1, & 202.

Lessons from the History and Philosophy of Science

71



in which their ideas can be tested. I would suggest that anyone who
has thought out a possible research regime should consider a
number of major research achievements of the past such as those of
Copernicus, Frege, Semmelweis and Wittgenstein, and examine the
effect that the proposed research regime would have had on those
achievements. If the effect turns out to be negative, then the
proposed research regime should be rejected and something better
devised to replace it.

References

Anderson, A.R. (ed.) (1964) Minds and Machines, Prentice-Hall.
Bell, J.L. and Machover, M. (1977) A Course in Mathematical Logic,

North-Holland.
Bynum, T.W. (ed.) (1972) Gottlob Frege. Conceptual Notation and Related

Articles, Oxford University Press.
Carnap, R. (1963) Intellectual Autobiography. In P.A.Schilpp (ed.), The

Philosophy of Rudolf Carnap, Library of Living Philosophers, Open
Court, 3–84.

Davis, M. (1988a). Mathematical Logic and the Origin of Modern
Computing. In Rolf Herken (ed.), The Universal Turing Machine. A
Half-Century Survey, Oxford University Press, 149–74.

Davis, M. (1988b). Influences of Mathematical Logic on Computer
Science. In Rolf Herken (ed.), The Universal Turing Machine. A
Half-Century Survey, Oxford University Press, 315–26.

Edmonds, D. and Eidinow, J. (2001) Wittgenstein’s Poker. The Story of a
Ten-Minute Argument between two Great Philosophers. faber and faber.

Frege, G. (1879) Begriffsschrift, eine der Arithmetischen nachgebildete
Formelsprache des reinen Denkens. English translation in Bynum (1972),
101–203.

Gillies, D.A. (1992) The Fregean Revolution in Logic. In D.A.Gillies
(ed.) Revolutions in Mathematics, Oxford University Press, 265–305.

Gillies, D.A. (2002) Logicism and the Development of Computer Science.
In Antonis C.Kakas and Fariba Sadri (eds.) Computational Logic: Logic
Programming and Beyond, Part II, Springer, 588–604.

Gillies, D.A. (2005) Hempelian and Kuhnian approaches in the
Philosophy of Medicine: the Semmelweis case, Studies in History and
Philosophy of Biological and Biomedical Sciences, 36, 159–181.

Gillies, D.A. and Zheng, Y. (2001) Dynamic Interactions with the
Philosophy of Mathematics, Theoria, 16, 437–59.

Hempel, C.G. (1966) Philosophy of Natural Science, Prentice-Hall.
Kuhn, T.S. (1957) The Copernican Revolution, Vintage, 1959.
Kuhn. T.S. (1962) The Structure of Scientific Revolutions, University of

Chicago Press, 1969.

Donald Gillies

72



Lucas, J.R. (1961) Minds, Machines and Gödel, Philosophy, 36. Reprinted
in Anderson, 1964, 43–59.

Macfarlane, G. (1984) Alexander Fleming. The Man and the Myth, Chatto
& Windus

Malcolm, N. (1958) Ludwig Wittgenstein. A Memoir, 2nd Edition, Oxford
University Press, 1989.

Mendelson, E. (1964) Introduction to Mathematical Logic, Van Nostrand.
Monk, R. (1990) Ludwig Wittgenstein. The Duty of Genius, Jonathan Cape.
Pitcher, G. (1964) The Philosophy of Wittgenstein, Prentice-Hall.
Semmelweis, I. (1861) The Etiology, Concept, and Prophylaxis of Childbed

Fever. English Translation by K. Codell Carter, The University of
Wisconsin Press, 1983.

Turing, A.M. (1950) Computing Machinery and Intelligence, Mind, 59.
Reprinted in Anderson, 1964, 4–30.

Wittgenstein, L. (1953) Philosophical Investigations. English Translation
by G.E.M.Anscombe, Blackwell, 1963.

Lessons from the History and Philosophy of Science

73