Molecular Biology and Medical Research
DR. FRANCIS H. C. CRICK*

_J want to take a rather different topie from Dr. Beadle. My subject is
molecular biology and medical research. I am going to widen it slightly and
talk about molecular biology, cell biology, and medical research, My knowl-
edge of these three topics is very different. I have worked for many years on
molecular biology. Recently I have been trying to learn something about cell
biology, but about medical research I know very little.

My theme is that fundamental work in biology ig Boing to. have an in-
creasing impact on medical practice. I am sure you are all fairly familiar
with this idea, but I want to develop it with a reasonable amount of sci-
entific content. In a certain way we can see that this is acknowledged already
by considering the four speakers who are going to address you today, not one.
of whom is medically qualified. I am in origin a physicist. Dr. Pauling is a
chemist: and the other two speakers are biologists. I do not think that this
choice of speakers is an accident but rather that it reflects the theme I want
to bring out.

Let me first say what I mean by molecular biology. This is, of course, a
portmanteau word, including a lot of biochemistry, genetics, physical chem-
istry, and related subjects. At the present time the word is used in two rather
different ways. In the first usage it has a rather general meaning and covers
all the ways in which you can think about a biological problem in molecular
terms. The second meaning is rather more limited and covers in particular
that part of the subject which has advanced rather rapidly. Biologically it
deals with genes and gene products. Chemically it means nucleic acids and
proteins and their synthesis. I shall use the latter of these two meanings. One
of the characteristics of this sort of molecular biology is that the people
working in it were studying properties common to all biological systems. They
did not mind particularly, therefore, which organism they worked on pro-
vided it was convenient, and would often choose microorganisms, as was
‘done by Dr. Beadle in his classical work.

The general ideas must be very well known to all of you. The most basie
idea is that biological information is mainly earried by the sequence of side _
groups on the regular back-bone of a macromolecule. Genctically it is carried
by nucleic acid, but many such sequences can be translated into the amino
acid sequences of proteins by special and rather elaborate picces of bio-
chemical machinery. Another important idea is that the complicated three-
dimensional structure of a protein is formed by folding up its rather simple
linear chemical structure to give a’ molecule with a definite shape and in
many cases a highly specific catalytic activity. I think everyone would agree

* Nobel Laureate in Medicine and Physiology, 1962. Member of the staff of the Medical
Rescarch Council Laboratory of Molecular Biology, Cambridge, England.

178
MOLECULAR BIOLOGY AND MEDICAL RESEARCH 179

“that rather rapid fundamental progress has been made in these topics in the
“Jast fifteen or twenty years. This has been underlined very recently by the
announcement of the award of a Nobel Prize for medicine and physiology to.
Nirenberg, Khorana, and Holley for their work in this very field; that is,
on the genctic code and on the structure of transfer RNA.

I think it is useful to ask why classical molecular biology has advanced so
rapidly. I believe there are three main reasons. The first reason is that we
were very fortunate in having a well-defined theoretical framework from
which we could predict, to some extent, what was likely to be discovered.
Of course, the detail character could not always be foreseen, but one had a
general idea of the outline to be expected. This-theoretical framework was
provided in the middle fifties. The main reason this was possible is the nature
of nucleic acid molecules, the functions of which are rather limited. This
helps in constructing theories, because the easiest way to make a theory is to
impose a restriction of some sort, and it was such a restriction which helped to
give us the theoretical framework. One quite serious mistake was made. The
ribosomal RNA was mistaken for the messenger RNA but fortunately this
error was discovered fairly quickly. .

My second reason is, I think, really the most important one: during this
period there were available very powerful experimental tools for tackling
these problems. I will mention a few of them, although they are all very
familiar to you. For example: chromatography, both paper chromatography
and column chromatography; the ultracentrifuge—not only the classical
method developed by Svedberg but also the. more modern usages, such as
sucrose gradients and caesium chloride density centrifugation. These are
techniques which one can use every day and can be applied to a wide variety
of problems. Then again the electron microscope has proved a very powerful
tool, although it is not the instrument of choice for getting down to atomic
details. It is really best at the level of size immediately above the atomie
level. One can think, for example, of the demonstration of circular DNA and a
lot of modern work on the structure of viruses. For the atomic level itself
the method of x-ray diffraction, applied to crystals of macromolecules, has
turned out to be very powerful, especially when combined with very fast
computers and automatic data collecting.

My third reason is of a totally different type: it might be described as the
romantic appeal of the subject. I think it is true that molecular biology,
operating at the border-line between the living and the non-living, and dealing
with this difference in a very fundamental way, has attracted into it many
people for just this reason. Quite a number of them were influenced by a
little book by the physicist, Schroedinger, called “What is Life?” I certainly
was, and I know that both Watson and Benzer also read it. There are, of
course, many reasons why people go into a particular field of work and study
a particular research problem. It may be because their professor has sug-
gested it to them, or because it is fashionable (that is to say, the subject is
moving rapidly and the techniques are easily available) but this ‘particular
180 FRANCIS H. C. CRICK

reason—the romantic appeal of the subject—should not be overlooked. To
give an example from quite a different branch of science, I think it is often
the reason why people go into:such fields as astronomy and cosmology.

The next question’ we have to ask is: Has classical molecular biology al-
_yeady had important medical applications? I think the short answer to this
is no. So far direct applications have been rather. few. There has been nothing
as spectacular or as useful as, say, penicillin. Nobody would deny that
molecular biology has not already been helpful in certain lines of medical re-
search. For example, the preparation of antibodies to a virus is certainly
easier if one understands the different functions of the protein component
and the nucleic acid component. Then again, the amino, acid sequences of
antibodies is giving us some insight into the sort of ways in which the body
‘an. produce the immense yariety of antibodies which it needs. The ideas of
molecular biology have also been useful in casting doubt on certain theories
which one could see would be unfruitful. For example, Burnett's early theory
of antibody formation violated an idea called the Central Dogma*, which
says that one cannot translate backwards in detail from a protein sequence to
the corresponding nucleic acid sequence. This cleared the way for his later
much more interesting theory which is the dominant one today. The recent
work on viral transformation (the transformation of a ecll when infected
with a cancer virus) could hardly have reached the sophistication it has with-
out the knowledge and methods of molecular biology. Most people would
agree that this is one of the most active and promising, fields in cancer re-
seareh at the present time, .

There are a few examples which have a more immediate medical applica-
tion. It has been much easier to accept the existence of drug-resistant epi-
comes (which carry drug resistance from one bacteria to another) because
of the fundamental knowledge of similar phenomena acquired by molecular
biologists.

Nevertheless, when we look at the things one might hope to have achieved
using some of this basic knowledge, such as, for example, a cure for can-
cer, or for various heart disorders, we must admit that so far there has been
little in the way of dramatic medical applications. I think it is important to
realize this. And so one has to go on to the next question: why is molecular
biology important to medicine? I think it, is important for two reasons. In
the first place, it provides a very solid framework of fundamental facts and
ideas at the molecular level for the whole of biology. The most useful com-
parison to make here ix with the early development of chemistry. For ex-
ample, the understanding of the tetravalency of carbon and the direction of
the four valencies in space, and similar ideas. They did not immediately
produce an enormous impact on society, but as time went on, 48 we can sec
from all the manifold applications of chemistry in the modern world, this

* The Central Dogma docs not state that errors in translation or transcription cannot be
caused by changes to certain proteins (or to transfer RNA). The views of Dr. B, Commoner
on this point are not widely accepted.
MOLECULAR BIOLOGY AND MEDICAL RESEARCH 181-

“knowledge began to be increasingly exploited and, in fact, somewhat taken
‘for granted, so that we sometimes’ forget that it is a necessary basis for
modern industrial chemistry.

The second reason I have already mentioned, It is the provision of very
powerful experimental techniques. I would emphasize that these techniques
are not something static. The nature of the subject is such that they are
continually being added to and what is even more remarkable the techniques

are getting faster all the time. .
We had a dramatic instance of this in our laboratory this summer. As you

know, Dr. Holley got his recent prize for the first determination of the
sequence of a transfer RNA. This involved two’steps: the fractionation of the
RNA (which can take a considerable time) and then the actual determina-
tion of the sequence. Both these steps proved very difficult and the skill and
persistence of Dr. Holley and his team has been rightly recognized by the
award of a Nobel Prize. ey

This summer a young visitor to our laboratory, Moshe Yaniv, working
with Mr. B. Barrell, determined the sequence of the valine tRNA from #. colt
in a period of three months, though admittedly the material had previously
been fractionated for him.

An even more striking example has been the determination, to 3.5 A, of
the three-dimensional structure of the protein clastase in our laboratory by a
research student, Mr, D. M. Shotton, working under the supervision of Dr.
If. C. Watson, after only one man-year of work. Shotton, who is in origin
a protein chemist, hopes that he may have both the primary sequence and the
tertiary structure finished for his thesis. .

We have a saying in our Jaboratory that the difficulty of a project goes
from “Nobel Prize” to “M.Sc.” in about 5 to 10 years! This shows you the
very rapid acceleration of techniques which is coming about.

Having discussed the nature of molecular biology and some of the reasons
for its suecess, we must now turn to consider its future. This is always a
hazardous operation, but I think we can safely make a few general predie-
tions. In the first place, we are likely to sce a fairly massive consolidation
operation. Although we know the answers to many problems of molecular
biology in outline, we do not yet know them in detail. For example, we do
not know in detail, even at this stage, how DNA replicates. Filling in of all
this biochemistry will take a large amount of work and will involve a large
number of people. We can already see this process going on.

In addition, we can expect an invasion from what used to be called the
more exact sciences, such as physical chemistry. Already many physical
chemists are entering the field and it is likely that many more will do so, not
only so that we can study structure faster and better, but also to explore
chemical mechanisms. .

We are also likely to see the fairly rapid extension of work to adjacent
areas of molecular biology. In many of these research hhas been going on for
some time, but we may now expect to see a greatly increased effort. One such
182 FRANCIS I. C. CRICK

field, for example, is the structure and function of membrancs. This is not
only important because membranes occur almost universally in biology, but
also because of the very many different processes which are associated with
membranes. To give one example, they are of great interest for anyone study-
ing the nervous system.

There are; of course, a number of areas which are already being intensively
studied. One could mention oxidative phosphorylation and the strueture of
mitochondria as an example of a fidld which is already fairly well populated.
The same might be said of a number of topics Which are relevant to only
part of the biological kingdom: such fields as photosynthesis on the one hand
and muscle on the other. Here again there has been:a fairly considerable
effort over the past decade, although there are many mechanisms which are.
still not understood in atomic detail. One would hardly be surprised if re-
search on animals usually turned out to be more relevant to medical problems
than research on plants.

However, it is not these particular problerns that I want to draw your at-
tention to today. I think what is of more interest ig the fact that the tech-
niques and ideas of molecular biology are going to be inereasingly applied to
cell biology. The distinction between cell biology and: molecular biology is
somewhat arbitrary but I hope it will be clarified by some of the examples
I am going to give you. So we must now turn to ecll biology and see how that
stands today.

Cell biology has a long and distinguished history. Interesting things have
heen discovered at a fairly steady rate over rather a long period, but I
would prefer to look at the subjectin a different way, and inquire what frac-
tion of what we would like to know has already been discovered. If we ask
ourselves this question, I think it is clear that cell biology still has a long way
to go, and consequently is a field in which strikingly important discoveries are
likely to be made.

Let me give a few examples from recent work. Much of what I am going
to mention has been done on small mammals. With one or two exceptions
they have not yet been done on man, but as we know, it is often not a very
big step from mammal to man. I think many people have been surprised by
the recent work, pioneered by Ephrussi and by Harris on the fusion of cells,
even cells from different animals. Cells can be fused together so they will
survive at least in tissue culture, though natirally it has not been possible to
produce hybrid animals in this way! The properties of these fused cells are of
very great theoretical interest. At the next level of organization we should
remember the fusion of early embryos, done by Beatrice Mintz. This proc-
ess, Which has been repeated many times, does indeed produce “hybrid” mice,
which, in many cases, are perfectly capable of having offspring. For ex-
ample, by starting with one early embryo from a black mouse and one from
a white mouse, she has been able, by fusing them, to produce a zebra
mouse. This seems to me a most striking and-promising technique.

Another dramatic piece of cell biology has been the transplantation of
MOLECULAR BIOLOGY AND MEDICAL RESEARCH 183 ~

nii¢lei from one cell to another, and especially into egg cells. This work was
started by Briggs and King using amphibians and in recent years has been
exploited very beautifully by Gurdon. Originally the technique scemed to be
very difficult, but it seems that’ with experience people are getting more
skillful at it. The application of such a technique to human beings would

raise very disturbing problems for us.
Then again, for example, one should remember those experiments in which

it is possible to change an adult animal, so that part of its tissues have come
from another individual. This can be done if the immune response has been
knocked out by x-rays, or some similar device. Under these circumstances
bone marrow cclls of another individual can colonize the marrow of the
irradiated animal. I think these examples will give you some idea of What I |
mean by cell biology.

The main impression I want to leave you with is that cell biology is a
field in which dramatic experiments of the above type are likely to be made
fairly frequently in the near future. I doubt if this is still true of molecular
biology, at least of the classical part of the subject, where I think most of
the work will be more in the nature of a consolidation of what we, know in
outline already.

It is therefore clear that the next question we must ask is: Where is cell
biology going? If we look around and sce what is already happening I do not
have much doubt in my mind as to where most of the effort will be placed. I
think it will go into embryology. It seems to me that this field is ripe for
scientific development at the present time. As you can sec, many of the
examples I have mentioned are very relevant to problems in embryology.

It is probably not possible to make an exhaustive catalogue of the general
problems which embryology faces, but we can eertainly consider the main ones.
For example, how are genes turned on and off? Of course, in microorganisms
we do have some idea of how this happens and we hope before long to know
in some detail. When we come to consider mammals we can only guess what
mechanisms are likely to operate. Then we have the problem of how eells com-
municate. Here again, we know that they communicate in some cases by
hormones. We know a lot about the chemical structure of hormones. We know
a certain amount about the action of hormones, but there is clearly very
much that needs to be discovered before we can say that we understand
it in molecular detail.

Then there is a whole class of molecules which have hardly yet been dis-
covered, which I would call gradient molecules. These are the molecules whose
concentrations are probably responsible for controlling the shape of an orga-
nism, and which help to decide, for example, that we should have a thumb
and four separate fingers on cach hand. This is indeed a very difficult field
but I should not be surprised if we sce dramatie progress in it during the
next ten years. Other general topies would include the adhesion between cells,
originally pioneered by Moscana; intercellular junctions and the study of
what molecules can move freely from one cell to the next, which is being
184 FRANCIS H, C. CRICK

studied by Lowenstein for example; the great problem of how cells divide,
that is, the biochemistry °of mitosis and what controls it; the problems of how
cells migrate, not only what makes them move but also how they know in
which direction to move.

‘For anybody wanting to enter the field of embryology, there is always the
very difficult choice of which organism to study. In almost all cases man is
not the ideal experimental animal, though I should mention in parenthesis that
he proved quite useful in| molecular biology because of his hemoglobin,
mainly- because there are so many physicians looking at so many patients,
It seems very unlikely that we shall find a single animal which will be the best
for all these very broad questions in embryology. It is more likely that dif-
ferent aspects of the subject will be best studied in. different animals. For
example, my colleague Sydney Brenner has already started to work oh nema-
todes. The genetics of this ix going beautifully. I think from the work he has
already done it is possible to see that the genetics of nematodes could easily
be worked up to the level of the genetics of Drosophila. These small animals
have only about a thousand cells and of these a few hundred are nerve cells, It
is possible to study fairly intensively the anatomy of the animal by using
the electron microscope. Unfortunately, the eggs present extremely difficult
technical problems and it is not clear that they are the system of choice for
the study of the early embryo.

In all the various areas of cell biology there is one field which I think will
attract more attention than all the rest. This is the study of the nervous
system, Of all the branehes of human physiology this is probably the one
about which we have the most to learn. This is, of course, tied up with the
fact that it is difficult. It is difficult largely because of its complexity, but
we should always remember that if it were not complex we would not be
clever enough to be able to understand it! :

For many years there has been much interesting pioncer work on the nerv-
ous system. There is, for example, the topie of the embryology of the nervous
system, How do nerves grow to make the right connections? Sperry was one
of the first to do some rather dramatie experiments in this area. There has
been mueh work on the chemical transmitters which operate at synapses
and the action of drugs of various sort. A problem of a very different
character is that of the overall design of the nervous system. One wonders
what type of structure nervous tissue can easily be programmed to produce?
We know already that what individual cells ean do rather casily is to make
proteins, but we lack the corresponding generalization for tissucs. Kase of
assembly must surely have an influence on which patterns of interconnec-
tions are used to carry out the various signalling operations.

There are of course many other problems. For example, what is the physical
basis of memory? The faet that we cannot even give outline answers to
questions of this sort demonstrates how extraordinarily little we know about
the brain. Moreover, ] have said nothing up to now about the behaviour of
whole animals, covered by such subjects as psychology and animal behaviour.
MOLECULAR BIOLOGY AND MEDICAL RESEARCH 185

These are disciplines in their owr right but we can reasonably hope that when
we understand betier the mechanism of the brain the behaviour of whole ani-
mals will be easier to study. , ,

The main thing I want to say about most of these fields is that I think
they are scientifically underpopulated. How does one judge whether a field is
underpopulated? I think there is a very simple test. If the classical experi-
ments in the field have never been adequately repeated, then that field is
underpopulated. The test for overpopulation is also simple. If a discovery—
not necessarily an enormously important discovery, but a useful and interest-
ing discovery—is made morc or less simultaneously by three or four different
groups, and if this is happening rather often, then I think it ean be “said
that such a field is overpopulated. Incidentally, this is exactly what is happens
ing in certain areas of molecular biology, such as protein synthesis. It is one
of the reasons why it is becoming, less and less fun to work on such problems,
heenuse too many people are trying to do what one is trying to do oneself.

If we apply these criteria to some of the fields I have mentioned, such as
embryology and the nervous system, I do not get the impression there are
many areas which are overpopulated. Moreover, if you talk to the people
working in these fields, the atmosphere is very much more relaxed than in
molecular biology. It may surprise some of .you, who have perhaps read a
dramatic book about scientific research, to know that in the early fifties, by
and large, molecular biology was relaxed. When I went to work with Perutz
he told me that he liked to be able to write a draft of a paper, put it away
in a drawer for a couple of months and then ‘look at it again to see how it
read, Nobody ever docs that now. But in these other fields one gets quite
a different impression. This comes out especially when people arc discussing
their future work. They might do such and such an experiment this year or
perhaps next year. There does not seem to be any particular urgency.

I must tell you that I think this state of affairs is likely to change. I think
there is likely to be a considerable migration of people working in other
fields to both embryology and the nervous system. There are good reasons for
this. In the first place, there is the romantic appeal of both these subjects.
Secondly, I have noticed that some of the younger pioncers of molecular biol-
ogy do not wish to stay in their own subject, because they feel it is over-
crowded, and in almost all cases they are moving into “some branch or other
of these two subjects. And thirdly, I think partly because of the influence of
the techniques of molecular biology, there will be a considerable expansion of
useful techniques in the near future and this itself will attract people.

It is certain that new techniques are needed. For example, consider the
problem of the mapping the precise details of the nervous connections. In a
piece of nervous tissue, such asthe retina, this is now being done using the
electron microscope, but it is an extremely tedious business. We have no
methods at the moment of doing it rapidly. Certainly, here is a case where
technical improvements are greatly needed, and there are very many other
examples of this sort.
186 FRANCIS H. C. CRICK

For the reasons I have just stated I think that these fields will soon have &
large number of people working in them, using a varicty of advanced tech-
niques. As far as I can see there is only one thing lacking. In neither of these
areas do we yet have a good general theoretical framework. People are trying
very hard to produce ideas about both the nervous system and embryology
‘vhich will have the appeal which the ideas.of molecular biology had, I do
not yet feel that they have been successful. We may, of course, have to face
the fact that there may not be a framework of ideas which is quite as
simple and easy as the one we had for nucleic acids and proteins.

But leaving this aside, I would say that both these fields are certainly set
for rather dramatic advances. We should therefore turn to consider what
is going to happen in the lifetime of the present medical students. How far
this will take us depends on how you calculate it, but a very rough estimate
shows that we have to consider the period from the present time to about the
year 2000 or a little after. .

I think it is clear that we may expect many striking scientific advances
within this period, and that many of them are likely to have an important
impact upon medical practice. In other words I am saying that the present
situation, in which the impact has been on the whole rather small, is not likely
to last for much longer. If the new gencration of doctors is going to be able
to cope with these discoveries it will clearly be important for them to have
had some general background on their scientific basis to enable them to ap-
preciate the new techniques that are likely to come along. I am very con-
scious that this is a problem which I am not really qualified to deal with. It
seems to me to be very difficult to plan medical education so that it has
sufficient grounding in the fundamentals of biology, without at the same time
overloading the curriculum. Nevertheless, we have to face the fact that in the
lifetime of the present generation of students this fundamental biological
knowledge is going to be one of the most useful things that they could learn.

It would seem to me, as a complete outsider, that if scientific research goes
on at the present hectic pace, the medical profession will have to consider
seriously the question of refresher courses at periodic intervals. It may be
necessary to arrange that medical practitioners have one year off in seven,
as many academic people do, or one year off in ten perhaps, so that they can
go back to school and be trained in the recent developments. It may turn out to
be important to give many more of them the opportunity to specialise in mid-
career in the new specialities that will come up. All this means, of course,
that more doctors will be needed, without allowing for the fact that there are
really not enough of them already.

I notice both in your country and in my own that there is a rather dis-
tressing situation. Both of us are importing too many doctors. It is true, of
course, that this may be only a temporary thing, but I think it is something
that people concerned with medical education should take ‘seriously. You are
going to need more doctors, but you are nét even producing enough now. It
MOLECULAR BIOLOGY AND MEDICAL RESEARCH , 187

is for this reason that onc particularly welcomes new medical schools at the
"’ present time.

Following on what Dr. Beadle said, I also notice that you will have a prob-
lem, which is not quite so serious in my own country, of the racial nature
of your input. This is somewhat dramatically shown by the racial composition
of the ‘Audience in front of me. It certainly does not-reflect’ the composition
of your country as a whole.

There is one other topic I should like to mention briefly. Because of the
very fundamental discoveries which are going to be made, you are going to
have a change in the nature of medicine. It is often said that whereas, in the
past, doctors mainly dealt with people who were rather obviously: ill, in the
future there will be more emphasis on preventive medicine. But beyond that.
I think that within this period there will be a different sort of medicine coming
into existence, the medicine which applies to people who are basically healthy
but who want to change in some sort of way. .

There already exist branches of medicine which have this character, for
example, cosmetic surgery. Someone has too big a nose and thinks it would be
nicer to have a smaller one. I think there will be many more demands of this
sort and especially for drugs which will alter people’s behaviour. Incidentally,
I should tell*you that in preparing this talk T did notice one rather interesting
omission in current medical research. As 1ar as I know, there does not seem to
be any federal money spent on research for a good aphrodisiac. I do not be-
lieve this is because somebody in authcrity thinks it would increase the popula-
tion rate, which might be a good reason. I suspect it is due to your puritan
tradition, even though this is already changing rather rapidly. I think we may
expect a demand for many drugs of this general character. For example, a
drug to help people memorize things more easily. As for myself, I would
particularly like a little drug which would deal with the time shift I have to
suffer every time I come to your country.

I also think one is going to be faced with demands for modifications before
birth. I do not want to say much about the genctic side because Sir Pcter
Medawar is going to deal with that topic. But if there were a technique which
could produce, say, more intelligent children, I have no doubt there would be
a very heavy demand for it. At the moment we know so little that it is not
clear whether something like this will ever be a practical possibility.

Finally, although I only want to touch on this briefly, I think everybody
realizes that many of the new discoveries will present us with very considerable
ethical problems. These are of course with us already. Who should have the
use of the limited number of kidney dialysis machines? When is it proper to
turn off the oxygen to somebody who is little better than a vegetable? Un-
fortunately; there will be more and more? of these problems and they will
increasingly apply to people who are not really ill in the ordinary sense of the
word. You already have an example of this in the contraceptive pill, which I
imagine must be giving considerable trouble to Catholic doctors.
"188 FRANCIS H. C. CRICK

In summary, then, my prediction is that we are likely to see in the decades
ahead of us an enormous development in basic biplogical research, During the
time.in which the medical students of today will have to practice, this re-
search will have a considerable impact on what they will be doing. This means
that,it.is important to think ahead and try to foresee how they could cope with

jt, not only on the medical side, but also on the ethical side:

Personally, I find these problems a little intimidating, certainly challenging,
but also very exciting, and for me this is perhaps the most encouraging thing

about the whole situation. Thank you.