Chapter Eleven
A Trout in the Milk
Some circumstantial evidence is very strong,
as when you find a trout in the milk
Henry Thoreau
One sunny afternoon in 1976, the normally sedate upper chamber of Parliament,
the House of Lords, was startled from its post lunch doze into sudden
wakefulness by a question from one of its aristocratic members. When, demanded
His Lordship the eighth Earl Clancarty, was the British Government going to do
something about the Unidentified Flying Objects that were flying into and out of
the Earth via the secret entrance situated at the North pole? Wasn't it time the
British people were told the truth about this scandalous cover up?1
Clancarty, better known as writer Brinsley Le Poer Trench, had
concrete evidence to back up his claim -- photographs taken from space by a NASA
satellite in 1968 which did, indeed, appear to show an unmistakable hole or
crater at the pole, several miles in diameter, exposing the dark interior of our
planet, and through which the UFOs of his question made their entrances and
exits.
Most people who consider themselves rational would probably
say that the noble Lord was completely off his rocker to believe such a thing.
Yet Clancarty was basing his claim not on hearsay or imagination, but on a pile
of both direct and circumstantial evidence that, taken in its entirety, amounts
to a case for his claim -- and moreover a case that must be answered. Merely to
dismiss a carefully prepared body of evidence -- however barmy it may appear --
is to make the same mistake as the crank; to base a judgment on opinion rather
than on empirical proof and logical argument. True skepticism demands more than
mere rejection.
Common sense says that Lord Clancarty is wrong; yet his
photographs and other data show he just could be right. The question is, how
exactly are we to tell the difference between a real crank
and someone who has stumbled across startling new knowledge, like Roentgen and
X-Rays? Or someone like the Wright brothers who really has achieved the
seemingly impossible? Or a researcher who discovers a phenomenon for which the
first evidence is weak and ambiguous, like the therapeutic
value of aspirin in heart disease?
The hollow Earth idea is the kind of theory that makes most of
us smile. Yet the evidence mustered by its adherents is far from weak. Or to be
more exact, the secondary physical evidence can be interpreted to mean different
things depending on what you already believe. Although this ambiguity can sow
the seeds of doubt in a trulymind, most people
accept the orthodox view that the Earth is not hollow and that UFOs do not go in
and out polar entrances. But what exactly is it that makes us so sure?
The common picture of the crank is, I suspect, that of the
lone, obsessive character with wild eyes and an anorak,
eager to buttonhole anyone who will listen, and espousing beliefs that most of
us find at best barmy and, at worst, barking mad. But it is not merely
uneducated laymen and laywomen with untrained minds who become obsessed with
crank beliefs; it is scientists as well.
Take the case of Rene-Prosper Blondlot a physicist at the University
of Nancy and distinguished member of the Academie des Sciences. In 1903, like
many of his contemporaries, Blondlot was experimenting with the newly-discovered
X-Rays. Through this he discovered hitherto unknown rays emitted by an
incandescent filament. The rays would pass through
aluminium but not through iron. In a very faintly lit room, said Blondlot, you
could actually see the very slight increase in illumination that the rays
caused when shone onto a piece of paper.
Blondlot announced these rays to the world in 1905. Since
other physicists had already inconsiderately bagged the more obvious letters of
the alphabet for their own forms of radiation (alpha, beta, gamma and even X)
Blondlot decided to give his university of Nancy a little useful publicity by
calling them 'N-Rays'.3
As his experiments progressed, Blondlot discovered that N-Rays
had some truly extraordinary characteristics. He found he could store the rays
by wrapping a brick in black paper and leaving it in the sunshine. Later when he
recovered the brick and took it into the darkened laboratory, he could see a
visible increase in illumination from the brick. Curiously, though, the amount
of illumination always remained the same -- he tried two bricks, three
bricks, ten bricks, but he did not get any more illumination.
Blondlot next found that many things give off N-Rays,
including human beings. He found that radiant heat increased the effect of
N-rays but that N-rays themselves were not identical with heat (infra-red)
radiation because radiant heat will not pass through aluminium whereas N-rays
will. Blondlot published a series of papers on his discoveries. Other
researchers took up the same line of research and also published papers, about
half of them supporting Blondlot's findings.
Eventually, the research attracted the attention of Dr R. W.
Wood, a respected physicist from Johns Hopkins University, who
decided to investigate Blondlot's phenomena at first hand and visited the Nancy
laboratory. The set-up that Blondlot showed Wood consisted of a filament
generating the N-rays which passed through a slit about 2mm wide onto an
aluminium prism and were refracted in the same way that a beam of visible light
is refracted by a glass prism. Blondlot was able to measure the angle (and hence
the refractive index) of several beams into which the N-rays were split by the
aluminium prism and it was the making of these measurements that Blondlot
demonstrated to the American, in his almost-dark laboratory.
Wood later described how his suspicions were first aroused by
the precision with which Blondlot appeared to be making his measurements. The
N-ray beam could not be less than 2mm wide (the width of the slit through which
it had to pass) yet the Frenchman claimed to be able to detect its position to
within a tenth of a millimetre. When he questioned Blondlot on this point, the
Frenchman told him, 'That's one of the fascinating things about the N-rays. They
don't follow the ordinary laws of science that you ordinarily think of. You have
to consider these things all by themselves.'4
Wood then asked Blondlot to repeat some of the measurements
for him, but as the Frenchman began to do so, Wood
surreptitiously picked up the aluminium prism and slipped it into his pocket,
unnoticed in the darkness. despite the fact that the prism was no
longer there, Blondlot recorded the same refractive indices he had obtained
earlier. Once Wood published this story, Blondlot was permanently discredited.
This example was recounted in some detail by Dr Irving
Langmuir, a physical chemist who won the Nobel prize for chemistry in 1932 for
his studies of molecular films. He worked from 1909 to 1950 in the U.S. General
Electric Company's research laboratory at Schenectady. In the course of his
career he collected examples of what he called 'pathological science', cases of
otherwise respected scientists deluding themselves into believing that they have
discovered novel phenomena. Langmuir never published his work but in 1953 he
held a colloquium on the subject at General Electric's Atomic Power Laboratory.
In 1966 a recording of the lecture was discovered in the Library of Congress and
a former colleague of Langmuir's, Robert N. Hall, later transcribed and edited
the recording. The result was published in the magazine Physics Today in October
1989.5
The examples of 'pathological science' collected by Langmuir
are worth examining in some detail because they provide many instructive clues
to the nature of the self-delusion mechanism that affects people such as
Blondlot. Equally, I believe, they illuminate the critical difficulty involved
in separating the delusional from the novel.
The next example concerns an experiment carried out in 1930 at
Columbia University by Professor Bergen Davis and his colleague Dr Arthur Barnes
that attracted wide attention in the physics community. Davis and Barnes
constructed an apparatus that generated alpha particles (the nuclei of helium
atoms) and electrons and they devised a way to send a stream of both particles
through a glass tube towards a target. By changing the voltage on the tube they
could adjust the speed of the electrons until they matched that of the alpha
particles and when they did, they believed that the alpha particles captured the
electrons as they flew along beside them to make whole atoms. This capture
phenomenon was signalled by a dramatic decrease in the number of alpha particles
observed to arrive at the target.
Davis and Barnes could measure this decrease because they
arranged that the particles coming out of the end of their
apparatus would strike a screen and cause visible scintillations that could be
seen through a microscope. Because each flash was quite small, they viewed the
screen in the dark (a little like Blondlot looking at his
N-rays).
If they set the apparatus so no electrons at all were
generated, all the alpha particles were observed to strike the target screen, at
the rate of about 50 counts per minute. When they turned the voltage up to a
critical value, electrons were sent through the tube at the same speed as the
alpha particles, were captured, and only a few scintillations were visible.
Langmuir and his colleague, Clarence Hewlett, visited Columbia
University to see the Davis-Barnes experiment for themselves. Langmuir describes
what happened next.
"We sat in the dark room for half an hour to get our eyes
adapted to the darkness so that we could count scintillations. I
said I would first like to see these scintillations with the field on and with
the field off. So I looked in and I counted about 50 or
60. Hewlett counted 70, and I counted somewhat lower. On the other hand we both
agreed substantially. What we found was this: these scintillations were quite
bright with your eyes adapted, and there was no trouble at all counting when the
alpha particles struck the screen. They came along at the rate of about one per
second. When you put on a magnetic field and deflected them out, the count came
down to about 17, which was still a pretty high percentage --
about 25% background. Barnes was sitting with us, and he said that's probably
radioactive contamination of the screen. Then Barnes counted and he got 230 on
the first count and about 200 on the next, and when he put on the field, the
count went down to about 25. Well, Hewlett and I didn't know what that meant,
but we couldn't see 230. Later, we understood the reason . . ."
Langmuir then played what he himself called 'a dirty trick'.
The various voltages being applied to the apparatus were under the control of a
laboratory assistant called Hull. The number of scintillations observed, said
Davis and Barnes, depended on the exact voltage applied. They further claimed
that the effects were sensitive to even a one hundredth of a volt change.
Langmuir now wrote out a list of ten test voltages, some of
which were zero, and passed this to Hull, thinking to catch Barnes out with the
zero readings. The trick failed to work at first, because
when Hull was not reading a voltage he sat back in his chair, away from the
instrument, thus giving Barnes a subconscious clue that there was nothing to
measure, and he registered a nil result.
Langmuir explained; 'So I whispered [to Hull] "don't let
him know you're not reading" and I asked him to change the voltage from 325
down to 320 so he'd have something to regulate. I said, "regulate it just
as carefully as if you were sitting on a peak [of electron capture]". So he
played the part from that time on, and from that time on Barnes's readings had
nothing whatever to do with the voltages that were applied. Whether the voltage
was at one value or another didn't make the slightest difference.'
'After that he took 12 readings, of which about half were
right and the other half wrong, which was about what you would expect out of two
sets of values.'
Langmuir confronted Davis with his findings. 'He couldn't
believe a word of it. "It absolutely can't be", he said."Look at
the way we found those peaks before we knew anything about the Bohr theory. We
took those values and calculated them and they checked exactly." . . . He
was so sure from the whole history of the thing that it was utterly impossible
that there never had been any measurements at all that he just wouldn't believe
it.'
Langmuir also describes what he felt sure was the cause of
Davis and Barnes's delusion. '[Barnes] was counting hallucinations, which I find
is common among people who work with scintillations if they count for too long.
Barnes counted for six hours a day and it never fatigued him. Of course it
didn't fatigue him, because it was all made up out of his
head. He told us that you mustn't count the bright particles. He had a beautiful
reason why you mustn't pay any attention to the bright flashes. When Hewlett
tried to check his data [Barnes] said: "why, you must be counting those
bright flashes. Those things are only due to radioactive contamination or
something else." He had a reason for rejecting the very essence of the
thing that was important.'
Langmuir wrote to Danish physicist Nils Bohr to 'head off' any
further experimentation. A year and a half later, Davis and Barnes published a
short letter in Physical Review6 saying that they had been unable to reproduce
the effect. 'The results reported in the earlier paper,' they said, 'depended on
observations made by counting scintillations visually. The scintillations
produced by alpha particles on a zinc sulphide screen are
a threshold phenomenon. It is possible that the number of counts may be
influence by external suggestion or autosuggestion to the observer.'
Langmuir observed that, 'to me [it is] extremely interesting
than men, perfectly honest, enthusiastic over their work, can so completely fool
themselves. Now what was it about that work that made it so easy for them to do
that?'
Langmuir's next example was one described earlier, that of
mitogenic rays associated with living organisms described by
Professor Alexander Gurwitsch of the First State University of Moscow in 1923
(see Chapter Five). The rays were believed to be a form of ultraviolet light
emitted by all living cells because they would pass through a quartz screen but
not through glass.
Gurwitsch and others found that they could just detect
mitogenic rays on a photographic plate. Of these experiments, Langmuir
says that 'if you looked over the photographic plates that showed this
ultraviolet light you found that the amount of light was not much bigger than
the natural particles of the photographic plate so that people could have
different opinions as to whether it did or did not show this effect.
The result was that less than half of the people who tried
to repeat these experiments got any confirmation of it. .
.'
In the example of mitogenic rays, Langmuir seems to have
shifted his ground somewhat. He has moved from experiments that were difficult
or impossible to confirm to those that are confirmed by only 'less than half'
those who try to replicate them. He has also moved from
phenomena that are wholly imaginary to those that are difficult to discern or
discriminate, and where it is difficult or impossible to say on the data
presented whether they were real or not.When he was
delivering his speech in 1953, Langmuir was not to know that two decades later,
in 1972, Gurwitsch's experiments would be repeated and strikingly confirmed
using modern instrumentation by S. P. Shchurin and a team from the Institute of
Clinical and Experimental Medicine in Novosibirsk, Russia.7
Langmuir was partly basing his conclusion on the statement of
the American Association for the Advancement of Science that Gurwitsch's
experimental results were delusory and mitogenic rays all in his mind.
Langmuir's final example is even more striking than those
given earlier. It concerns research conducted by Professor Fred Allison of the
Alabama Polytechnic Institute and published in 1927. As a result of Allison's
work, scores of papers were published in journals such as Physical Review and
Journal of the American Chemical Society and Allison and his co-workers even
claimed to have discovered new isotopes and new elements.
Indeed, as we will see later, there is a good case to be made
for saying that Allison was instrumental in the first confirmation of the
existence of tritium, the rarest isotope of hydrogen.
The apparatus built by Allison made use of an effect first
noticed by Michael Faraday; the effect in which if you shine a beam of polarised
light through a liquid, and then you turn on a magnetic
field round the liquid, the plane of polarisation of the light is rotated by the
magnetism. You can see this effect easily because the light beam will appear to
get lighter or darker as it rotates.
The apparatus Allison and his co-workers built had two glass
tubes in line that could be filled with liquids, and with coils
of wire wound round them in a circuit. The light source was an electric spark
that also sent current through the coils. You could visually observe the amount
of rotation due to the Faraday Effect by looking down the second glass tube and
rotating it until it just compensated for the amount of rotation caused in the
first tube. However, Allison also discovered that the amount of rotation
depended on a second factor; the composition of the liquids inside the glass
tubes. If you used plain water in the second tube you got
one reading. If you dissolved some salt in the water you got another reading.
Allison made use of this ability to discriminate between
solutions as an analytical tool. For instance if you put ethyl alcohol in the
tube you got one characteristic measurement, while if you put in acetic acid you
got another. But if you put in ethyl acetate (a compound of both chemicals) you
got two characteristic measurement peaks. This meant that you could analyse
compounds using the apparatus.
A further important point about this ability to discriminate
solutions was that it appeared to be amazingly sensitive. You got the
characteristic measurement peaks from the compounds in solution even if that
solution was as weak as a 10-8 molar solution, which is something
like a pinch of salt in a bathful of water.
The most important discovery came when Allison realised that
his apparatus was capable of discriminating between different isotopes of the
same element. This was remarkable because discriminating isotopes by chemical
methods is usually a very complex and time-consuming process, while Allison's
apparatus was relatively simple. Using his apparatus, Allison announced that
there were 16 isotopes of lead. A little later, he made an even more important
discovery; that the apparatus could also detect entirely new elements. By the
1920s, the modern periodic table of elements had been drawn up, but chemists had
not yet been able to identify physically some of the elements that it predicted
should exist. Using his effect, Allison now came up with two new elements which
he named Alabamine and Virginium.
The end of the Allison story is curiously inconclusive and ambiguous. Langmuir
left his audience in no doubt that he personally believed the 'Allison effect'
was an example of pathological science; that it existed only in the mind of its
discoverer and his colleagues. Yet Langmuir himself tells the following story,
concerning two of his friends and colleagues, Gilbert Lewis, Professor of
physical chemistry at Berkeley, and Wendell Latimer, head of the chemistry
department at the University of California.
Langmuir records Latimer as saying, "There's something
funny about this Allison effect, how they can detect isotopes. I think I'll go
down and see Allison, to Alabama, and see what there is in it. I'd like to use
some of these methods."
Latimer's main interest at that time, says Langmuir, was the talk there was in
physical chemistry circles about the possible existence of traces of hydrogen of
atomic weight 3 (today called tritium) for which there was some spectroscopic
evidence.
Latimer shared these thoughts with Gilbert Lewis, who is
said to have replied, 'I'll bet you ten dollars that you find there's nothing in
it.'
Latimer visited Allison in Alabama and stayed three weeks
studying his methods. He returned to University of California,
built a duplicate apparatus and got it working so well that Lewis paid him the
ten dollars. He identified tritium using Allison's magneto-optic method and
published a short paper in Physical review in 1933 announcing the detection of
the isotope of hydrogen of atomic weight 3.8 Curiously, however, most text books
credit the discovery to Ernest Rutherford and colleagues in the following year.
Langmuir then recalled that around this time there was a
meeting of the American Chemical Society at which there was much discussion of
whether to accept any more papers on the Allison apparatus for its Journal. The
decision, says Langmuir, was against accepting any more papers, a ruling that he
says was also adopted by Physical Review.
Despite adopting this policy, however, both journals did
publish other papers on the Allison effect, both of them by groups who felt that
a perfectly valid effect was being marginalised and suppressed. The paper in the
Journal of the American Chemical Society in 1932 by J. L. McGhee and Margaret
Lawrentz, said that, 'In December 1930 one of us (McGhee) handed out by number
to Prof. Allison twelve (to him) unknowns which were tested by him and checked
by two assistants 100 per cent correctly in three hours.'9
The paper by T.R. Ball of Missouri's Washington University published
in Physical Review in 1935 gave a very detailed review of the magneto-optical
method and included a statistical study of 1,698 readings made over three years
by five different observers.
It included the correct identification of unknown substances in several blind
tests where the odds were 34 to 1 against selection by chance alone.10
However Langmuir concludes that the Allison effect is
nevertheless an example of pathological science because after discovering
tritium, Latimer told him; 'You know, I don't know what was wrong with me at
that time. After I published that paper I never could repeat the experiment
again. I haven't the least idea why. But those results were wonderful. I showed
them to G. N. Lewis and we both agreed that it was all right. They were
clean-cut. I checked them myself every way I knew how to. I don't know what else
I could have done, but later on I just couldn't ever do it again.'
From his list of examples, Langmuir suggested the existence of
a generalised pathological approach to research that can afflict perfectly
honest scientists, and he drew up a list of tell tale signs by which such
research can be recognised.
'The Davis-Barnes experiment and the N-rays and the mitogenic
rays all have things in common. These are cases where there is no dishonesty
involved but where people are tricked into false results by a lack of
understanding about what human beings can do to themselves in the way of being
led astray by subjective effects, wishful thinking or threshold interactions.
These are examples of pathological science. These are things that attracted a
great deal of attention. Usually hundreds of papers have been published on them.
sometimes they have lasted for 15 or 20 years and then they gradually have died
away.'
The symptoms of pathological science, according to Langmuir,
are as follows:-
* The maximum effect that is observed is produced by a
causative agent of barely detectable
intensity.
Moreover, the intensity cannot be increased
by
multiplying the source: ten bricks still only
yielded
the same number of N-rays as one brick. This, says
Langmuir, is to make it easier to fool yourself.
* The effect is near the threshold of visibility or the
threshold of any other sense used to detect
it.
Alternatively, many, many measurements are
needed
because of the very low statistical significance of the
results.
'This enables people to find plausible reasons for rejecting
data that does not fit. 'Davis and Barnes were doing that right along', says
Langmuir. 'If things were doubtful at all, why, they would discard them
depending on whether or not they fit the theory.'
* There are claims of great accuracy, great sensitivity,
or great specifity. This was particularly true of the
Allison effect, says Langmuir.
* Fantastic theories contrary to experience are suggested.
* Criticisms are met by ad hoc excuses thought up on the
spur of the moment.
* The ratio of supporters to critics rises up to somewhere
near 50 per cent and then falls gradually to
oblivion.
In the example of Allison, Langmuir seems to have shifted his ground yet again
in defining what constitutes pathological science. It is easy to see why his
suspicions were aroused in the light of Latimer's remarks to him. Equally one
can see that Allison's effect conforms in many respects to the definition of
classic pathological research: It depends on visual observation of a critical
measurement; it claims to function without any variation at fantastically high
dilutions; and Allison came up with 16 isotopes of lead while orthodox chemistry
recognises only three isotopes (although acknowledging that discriminating the
atomic weights of these isotopes is very difficult). There is also the issue of
the so-called new elements Virginium and Alabamine, the latter ostentatiously
named after the discoverer's own state polytechnic rather like Blondlot's
N-rays, and which do not appear anywhere in the periodic table today.
Yet it seems to me that in setting out quite properly to nail abuse
of the scientific method, Langmuir has unconsciously drifted
across the line that separates his definition of pathological science from the
foggy zone out of which real discovery emerges, faint and fuzzy round the edges.
How was Allison able to identify 12 unknowns in three hours with 100% success,
if it was all in his mind? How were Ball and his colleagues at Washington
University able to repeat similar blind tests if the effect was imaginary? How
did Latimer discover tritium in the first place?
As Langmuir himself said of McGhee's paper (the last such
paper published by the American Chemical Society) 'You'd think that would be the
beginning, not the end.' You would, indeed. Except that both the AMC Journal and
Physical Review took a policy decision not to publish anything further on the
Allison effect, and prominent physical chemists like
Langmuir were discouraging any further research. So far as I know, no-one has
recorded Wendell Latimer's reaction to not being credited with the discovery of
tritium, but seeing the credit go a full year later to
Britain's Ernest Rutherford.
In setting out to evaluate Langmuir's hypothesis of
pathological science, I want to attempt to apply his diagnostic techniques to a
rather different kind of experiment: one drawn from the realms of physics, but
one that has assumed a position central to modern science and about which there
is absolutely no doubt in orthodox circles. The experiment I have in mind is
that first carried out by Dr Robert Millikan, Director of Physics at the
California Institute of Technology and winner of the Nobel prize in 1923 for
measuring the charge of the electron.
This experiment was crucial to the development of twentieth century atomic
physics. It established that all electrons have the same unit charge, and that
there are never fractions of this charge found in nature. And for the first
time, Millikan accurately quantified that minutely small charge. The experiment
he devised to enable him to measure something so small was brilliantly
ingenious.
He made tiny droplets of oil fall through a hole in the lid of
a box with transparent sides and he observed through a microscope the time they
took to fall. From this he was able to deduce their size. He then switched on a
voltage between the top and bottom plates of the box. From the effect on the
rate of fall he was able to calculate any electric charge on the drop. Sometimes
this charge would abruptly change, but by a constant amount and Millikan
reasoned that this was because it had either lost or captured an electron. By
performing this experiment over and over, searching carefully through all his
measurements of many thousands of drops, Millikan was able to find the number
that represented the charge of a single electron (he found it to be 1.6 x 10-19
coulombs). This measurement provided the basic scale parameter for the whole of
atomic physics.
What is particularly interesting is that Millikan's laboratory
notebooks have survived and so we can gain an insight into his thought processes
in the very moments that he was conducting his famous experiment, a little like
paying the sort of personal visit favoured by Irving Langmuir. What those notes
reveal, however, is just as suspicious as anything that Langmuir turned up in
his investigations.
After one run of measurements, Millikan noted 'This is almost
exactly right!', while after another less satisfactory trial he noted down,
'very low -- something wrong'. How did Millikan know in advance what was the
'right' result and what was 'wrong'?
Does this mean that Millikan was acting in some way
dishonestly -- setting out to prove a preconceived idea? No, it merely shows
that scientific research is a complex business that sometimes depends on
intuition as much as on deduction (and that it is foolish to expect scientists
not to theorise in advance of the data.)11
Millikan's experiment has been repeated many times since.
Indeed it is frequently carried out by school and university students because it
is in essence so simple. Yet anyone who has ever repeated Millikan's experiment
knows that you never, ever get exact results, and that you frequently do
apparently find fractions of a unit charge. These findings were rejected by
Millikan as due to experimental error, and are still rejected today because the
atomic theory is so powerful and because Millikan's experiment is crucial to
that theory.
Some modern scientists believe that there are fractional
atomic charges. Professor Bill Fairbank of California's Stanford University has
claimed to have measured particles with one third of the charge of the electron
in experiments which have been repeated over a five year period with increasing
accuracy, using apparatus far more sophisticated than that used by Millikan in
1916. Against this, Dr Peter Smith of the UK's Rutherford-Appleton laboratory
has constructed similarly sophisticated apparatus which he claims does not
replicate Fairbank's results.
Regardless of the outcome of this modern controversy, how does
Millikan's original experiment stand up to Irving Langmuir's criteria? The
answer is that it fails on practically every point of
comparison. It is a threshold effect involving visual observation of
microscopically small oil particles. The magnitudes involved are unimaginably
small. Large numbers of trials have to be carried out and statistical results
closely examined for trends. Some data is rejected as
being 'wrong' because it does not fit the theory, while
other data is accepted as being 'almost exactly right'. Fantastic accuracy is
claimed for the result. Ad hoc excuses are offered for the existence of
anomalous data ('experimental error').
So why did Langmuir not include Millikan's experiment in his
catalogue of pathological science? What scientifically distinguished Millikan's
work from Allison's? The honest answer is that nothing so distinguished it
except the final criterion that more than 50 per cent of scientists supported
his results and have continued to do so. In the final analysis it was a matter
of acceptance, not a matter of evidence.
Langmuir's lecture on 'pathological science' was published in
the U.S. magazine Physics Today in October 1989, a few months after Fleischman
and Pons had announced their discovery of cold fusion and shortly after a
speaker at the American Physical Society's annual meeting in Baltimore said that
physicists were 'Suffering from the incompetence and perhaps delusion of doctors
Pons and Fleischmann.' Although Physics Today published Langmuir's lecture
without direct comment, even the most unworldly reader could see who it was
aimed at given the furore that the two scientists had created.
In the United Kingdom, science journalists were nothing like
as reticent about making the connection and accused Fleischmann and Ponsy.
Writing in the Daily Telegraph Steve Connor asked, 'how two respected
chemists could apparently make such a blunder'? The answer, supplied Connor
helpfully, was that they were victims of Langmuir's pathological science. 12
At the height of the Velikovsky affair described in the previous chapter Dr
Laurence Lafleur, Associate Professor of Philosophy at Florida State University,
wrote an article in Scientific Monthly also setting out to define the criteria
by which we will be able to recognise a crank from a real scientist.13 Lafleur
gave seven criteria, as follows;
1. Is the proposer of the hypothesis aware of the theory he proposes to
supersede?
2. Is the new hypothesis in accord with currently held theories
in the field of the hypothesis, or, if not, is there adequate reason for making
changes, reasons of weight at least equal to the weight of evidence for the
existing theories?
3. Is the new hypothesis in accord with the currently held
theories in other fields? If not is the proposer aware that he is challenging an
established body of knowledge, and does he have sufficient evidence to make such
a challenge reasonable?
4. In every case where the new hypothesis is in contradiction with an
established theory, does the hypothesis include or imply a suitable substitute?
5. Does the new hypothesis fit in with existing theories in
all fields, or with substitutes proposed for them, to form
a world view of an adequacy equivalent to that of the currently accepted one?
6. If the new hypothesis is at variance with theories capable
of prediction or of mathematical accuracy, is the new theory itself capable of
such prediction or mathematical accuracy?
7. Does the proposer show a predisposition to accept minority
opinions, to quote individual opinions opposed to current views, and to
overemphasise the admitted fallibility of science?
Lafleur goes on to add, rather disingenuously, that, 'It is
not our primary purpose to examine the merits of Velikovsky, but in
defence of his critics it is necessary to point out that he qualifies as a crank
by almost every one of these tests, perhaps by every one.'
It is rather difficult to tell now, from a distance of more
than 40 years, whether Professor Lafleur actually expected his remarks to be
taken seriously outside of the context of the Velikovsky affair. For it is hard
to see how any of the seven criteria above could be anything other than remarks
addressed directly to Velikovsky. It is not until we get to proposition 6, that
we even hear about the quality of the evidence that supports the new hypothesis;
that is to say, the scientific issues themselves.
The first five propositions are concerned almost entirely with
how far the new idea offends against the beliefs of the elders and betters of
science and whether such disgraceful impertinence can be justified. The seventh
is even more bizarre: the fewer the people who agree with you, the more likely
you are to be wrong. Again we have a criterion which ignores the scientific
evidence and dwells instead on the crucial importance of maintaining a
scientific consensus, whatever the facts may say.
Again it is acceptance that counts, not evidence. A better
idea of Lafleur's true position on Velikovsky is gained from the introductory
paragraphs of his article.
'. . .the general public as represented by the editors and
readers of Harper's has failed to grasp the reasons for the scientific rejection
of Velikovsky's hypothesis, and many of them may therefore be led to think of
scientists as a dogmatic crew, blindly maintaining their own unverified
doctrines; intolerant of opposition, and suppressing it by denying free
expression to their adversaries. The scientists, in general, have not been aware
of the enormities attributed to them. They have not realised that the tempest is
over something more than the purely scientific question; therefore, since they
know that all other scientists agree with them in the rejection of Velikovsky's
hypothesis, they are inclined to consider the question closed and turn their
attention to less depressing matters.
The 'us and them' attitude; the patronising assumption that
non-scientists' dissent is caused by their ignorance; the casual distortions
('all other scientists agree . . .') are still attitudes
that can be found in science today, although it would be a great deal harder
these days to find any scientist or philosopher willing to sign his name to them
so publicly.
One contemporary scientist who is concerned at the perception
of anomalous phenomena as 'heretical' is Dr Peter Sturrock, Professor of Space
Science at Stanford University in California, who together with like minded
scientific colleagues, such as Professor Laurence Frederick of the University of
Virginia, founded the Society for Scientific Explorations in 1982.
Sturrock points out that; 'Sometimes, the nature, and even the
reality, of a phenomenon may be obscure. If the case rests on only a few reports
scattered in dusty, inaccessible journals, they cause no problem: they are
simply ignored. If, however, the reports are so frequent that the topic cannot
be ignored by the scientific community, scientists may become emotional and
confused. Is it possible that the difficulty with "anomalous
phenomena" is that scientists may perceive them as heresies?'14
Sturrock says that within his own field of astronomy some new
claims are regarded as respectable and other as heretical. Quasars and, later,
Pulsars were truly anomalous objects but astronomers readily accepted
them.
On the other hand some astronomers, notably Halton Arp, now at the Max Planck
Institute for Physics and Astronomy in Munich, claimed to have evidence that the
red shift of quasars cannot be due entirely to processes that are already known.
There has been great resistance to this claim, and Arp says that this resistance
led to political repercussions that forced him to leave his observatory in the
US for a more congenial place of business.
Sometimes, says Sturrock, anomalies deserve to sink without
trace, and he cites Irving Langmuir's symposium on pathological science. But,
'the problems of evaluating anomalous phenomena would be solved more rapidly if
it were only a question of applying the right scientific methodology.
Unfortunately, however, the interested community may be organised into
advocacies, arguing powerfully either for or against the reality and the
importance of a particular phenomenon. There are clearlycollective processes at
work. That is to say, social and political factors play a role in determining
how the scientific community responds to anomalous phenomena.'
Sturrock offers the following as guidelines to those willing
to research anomalous phenomena;
* In studying any phenomenon, face up to the strongest
evidence you can find, even if it is in conflict with current orthodoxies.
* Go to the original sources for your data. Do not trust
secondary sources.
* Deal with "degrees of belief", which can be conveniently
characterised by probabilities. It is important to avoid assigning probability
P=0 (complete disbelief) or P=1 (complete certainty) to any proposition since,
if you adopt either of these values, that value can never be changed no matter
how much evidence you subsequently receive.
* Focus on evidence and testing.
* Subdivide the work into categories so different people take
on different tasks.
* Where possible work in teams; first because a combination of expertise may be
required, and secondly, because a team is more likely to be self-correcting
than someone working alone.
* In theoretical analyses, list all assumptions. This seems a
simple, innocuous request, yet it will not always be easy to put into effect.
In one sense, it is refreshing to read a physical scientist advocating such a
rigorouslyminded approach to anomalous phenomena. Sturrock's guidelines
contrast starkly with Lafleur's dogmatic 'if it's different, it's wrong'
approach. yet in another sense, it seems to me almost incredible that three
centuries after Galileo, some professional research scientists should have to
receive counselling on how to beminded in research.
Most of the examples of crank beliefs cited earlier in this chapter have quite a
high entertainment value and are capable of providing us with that most
delightful of human pleasures; a laugh at someone else's expense. But the
laughter is apt to obscure what is perhaps the most important lesson in all
this: that a crank is not only one who, through self delusion rather than
evidence, believes a theory to be true when it is actually false. A crank is
also one who, through self delusion rather than evidence, believes a theory
false when it is actually true.
Thus, it is not only Lord Clancarty and believers in a hollow
Earth who are cranks; it is also Lord Kelvin, who thought that X-Rays were a
hoax, and the editor of Nature who said that cold fusion was 'licensed
magic' and a waste of time.
