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From Understarld~ng to
Manipulating DNA
JAMES D. WATSON
We have every reason to expect that, over the foreseeable future,
recombinant DNA-based science will provide masses of new and
unanticipated facts that will profoundly transform our knowledge
about ourselves and the all-too-many diseases that exist today, as
well as generate industrial and agricultural processes that are now
unimaginable. But to do so at the rate now potentially possible, using
already-worked-out methodologies, will require Q massive expansion
of our current research budgets. The question now for us to ponder
Is how to achieve this expansion.
I appear here because my name, together with that of Francis Crick, is
associated with the start of what now is properly regarded as the DNA
Deoxyribonucleic acid) revolution. But when we found the double helix
some 32 years ago, it was not the future that interested me. Instead, I saw
our discovery as marking the end of a distinguished 90-year-old intellectual
search for the nature of the gene. This climax, as I recalled in my book The
Double Helix, came suddenly, and it was with elation that we saw that the
final answer was indeed a golden one. Viewing the double helix with its
self-complementary nature brought joy not only to those of us who had won
the race, but to virtually all others, like Sidney Brenner, who quickly came
over to the Cavendish Lab from Oxford and heard Francis excitedly run over
the implications of our model. The question of how a gene could be replicated
was gloriously revealed by mere inspection of the double helix. No longer
should there be any further serious debate as to what the gene is. DNA just
could not have a self-complementary structure and not be the gene. Any
structure that simple had to be right, and almost without exception those rare
individuals who later failed to be swayed by its beauty had nowhere to go
scientifically. With time they became known only for their iconoclastic views,
213
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214
JAMES D. WATSON
of interest solely to those journalists who relished controversy more than
scientific truth.
Francis Crick, not being a biologist by training, was more interested in
the future than the past. [Ie had switched from physics to biology because
of what was not known, and he correctly told all who would listen that
biology would no longer proceed in its past, frequently desultory, fashion,
that at last we had a real starting, point for understanding how genes made
possible the existence of life. Here, of course, Francis was the optimist,
while I then could be perceived as either abnormally cautious in seeing what
we had staked or as Dying to excel many of my newly acquired English
friends in Heir capacity to understate the truly important.
In looking back first to the discovery of the double helix and then to the
several key steps that led to the emergence of recombinant DNA as an
economic force, I shall repeatedly refer to what I believe are several very
essential aspects of these scientific discoveries: (1) the need for sensible
dreams (long-term goals), (2) the value of imitating approaches that have
worked in the past, (3) the necessity of accepting rapidly unexpected assaults
on conventional wisdom, and (4) the virtual necessity for young scientists
to receive one or more forms of patronage, be it from former teachers, an
institution or foundation, or the government itself.
THE DOUBLE HELIX
Crick and I most certainly did not stumble upon the double helix. It seemed
then the most important of all coals, and knowing what we wanted, we felt
the most sensible approach was to imitate the best master of the present,
who was at that time Linus Pauling He had found the a-helix conformation
of the polypeptide chain by playing with molecular models, always following
He laws of chemistry, many of which he himself had discovered. So we
thought, Why shouldn't we succeed with these same tncks? Key to this
approach was the faith Hat the answer would not be too complex (life had
to arise spontaneously!), and so-from the start we limited our search to simple
answers. We suspected that we would never be clever enough for success if
the answer was abstrusely complex. Thus, we never searched for anything
but regular, helical answers. Equally important, we were prepared to change
our minds if someone could show us that we had the experimental facts
wrong. Essential to our final success was the pronouncement from our across-
the-room neighbor, the chemist Jerry Donohue, then fresh from Pauling's
lab: he said that we, like the textbooks and virtually all interested chemists,
used in our thinking the wrong conformations (tautomenc forms) for several
of the DNA buildin, blocks. After a few hours of reluctance we reversed
our sights, knowing that our current model had more awkward features than
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FROM UNDERSTANDING TO MANIPULATING DNA
215
we wanted. Only a week later came the now-famous base pairs and with
them the double helix.
But we would never have had the opportunity to find our golden treasure
if we had not had the patrons to let us challen Be the approaches of the past
that were going nowhere. Then, Francis and I were not generally perceived
as useful citizens, forever telling others that their problems, not ours, were
either unimportant or insoluble given the current state of experimental knowl-
edge. So we required enlightened patronage, which I found in Max Delbruck
and Salva Luna, and Francis got from Max Perutz and John Kendrew (but
not initially from Sir Lawrence 13ragg). Equally important was the necessity
of working within a well-equipped laboratory that provided the freedom to
work toward long-term important goals, and where we were not put under
the pressure of either succeeding fast or being banished to the second rate.
Here of prime importance was the Rockefeller Foundation and Warren Weaver.
Without the funds Weaver directed to several key university groups in Europe
(including the macromolecular structural group at the Cavendish Lab) and
in the United States (in particular, to Caltech and Indiana University) after
World War II, the dawn of molecular biology would have broken much later.
Equally farsighted was the support given to Sir Lawrence Bragg in a then
still ration-weary England by the Medical Research Council, then ably run
by Harold Himsworth.
THE CENTRAL DOGMA
The first major step forward after the double helix was the elucidation of
how DNA provides the information necessary for synthesis of protein. We
focused at the start on the structure of RNA (ribonucleic acid) for three
reasons: (1) DNA appeared to be absent from the cytoplasm, the most likely
site of protein synthesis; (2) it was simple to make a paper scheme for how
RNA might be made on a single-sanded DNA template; and (3) until then
RNA was a molecule without any known function. So we postulated that
DNA provided the information to make RNA, which in turn provided the
inflation to order the amino acids in proteins (DNA ~ RNA ~ Protein
= The Central Dogma).
Happily, our initial focusing on RNA turned out not only to be simple-
minded, but correct. But how RNA could order the amino acids in protein
proved much, much trickier to work out. Here the first real breakthrough
was a chemical intuition on He part of Francis Crick. He said that RNA had
to be a wretched template and that some other intermediate would be found
Hat had recognized amino acids. But from then on, real answers had to come
from biochemistry. Here there was growing optimism among the more astute
biochemists that macromolecules, as well as small molecules like sugars or
amino acids, might be made outside of living cells in extracts containing
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216 JAMES D. WATSON
vital cell components. So I, as well as many others, decided that we would
no longer get anywhere tying a Pauling-type approach, but should instead
follow in the traditions of the great biochemists of the past, like Warburg
and Lippman. Again we chose the right general approach, for within a decade
DNA, RNA, and proteins all could be made outside of cells under conditions
in which all of the vital molecular ingredients could be identified In doing
so, we had had many initial surprises and in some cases had to accept their
reality without yet deeply understanding their significance or evolutionary
origin. For example, we started out by assuming that all RNA is template
RNA. By 1960, however, we had found three different RNAs, only one of
which functioned in the template manner originally postulated.
By this stage, most innovative research on the Central Dogma was being
done by medium-sized groups, generally working with bacterial systems, in
many leading universities and research institutions. Modest help like that
initially provided to Caltech by the Rockefeller Foundation would never have
let molecular biology grow into what it already was by 1961 . If the National
Science Foundation (NSF) and the National Institutes of Health (NIH) had
not initially been so freely generous with their monies, we could never have
moved so fast, particularly in those days, when each new cell-free synthesis
seemed more like good luck than a reflection of the fact that cells exist
because they utilize enzymes that have been highly evolved to work well.
In those days, we virtually never talked about money. There was enough to
support the losers as well as the winners, and so science seemed the best of
all occupations to go into starting in the m~d-19SOs.
THE GENETIC CODE
Solving the genetic code became a commonly accepted goal virtually as
soon as the double helix became known. The physicist Gamow first ap-
proached it in late 1953 by focusing on how combinations of the four different
base pairs (AT, TA, GC, CG) might specify 20 different amino acids. Later
a semicollective approach by the 20 members of the RNATE CLUB,* led
to the circulation of a series of papers on research that utilized known amino
acid sequences to see if restrictions on amino acid ordering existed. By l9SS
it became clear that theory as opposed to experiments had no chance, which
led Crick and Brenner to genetic approaches. First they considered a poten-
tially very long term, brute force mutagenesis program, using the viruses
(phages) of the then intensively studied bacterium Escherichia coli. Within
several years, the mutants so obtained were used in a clever series of genetic
crosses that resulted in their 1961 proposal that groups of three nucleotides
*A loose association of physicists. chemists, mathematicians, and biologists all associated in some
way with Gamow.
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FROM UNDERSTANDING TO MANIPULATING DNA
217
specified amino acids. It is important to note that initially no elegant approach
seemed possible, and it was only through unexpected genetic results, which
implied single base-pair deletions and insertions, that Crick and Brenner
could really use their heads as well as their hands.
An even more important breakthrough came from the development of
systems for in vitro protein synthesis that could be used to test the concept
of messenger RNA. Nirenburg and Matthaei's discovery at NIH, also in
1961, that Poly U coded for polyphenylalanine made the genetic code a
problem attackable by biochemists and led by early 1966 to the solution of
the genetic code. Greatly assisting the biochemists were the techniques of
the organic chemists, which permitted the synthesis of short, repetitive RNA
chains of known sequences. These were used as rnRNA molecules in cell-
free syntheses. Here as in the working out of the Central Dogma, well-
equipped biochemical laboratories were essential for real steps forward, and
most of the funds came from a still very generous NIH.
THE ENZYMOLOGY OF DNA SYNTHESIS
The field of test-tube synthesis of DNA owes its existence almost entirely
to one individual, Arthur Kornberg, working first at Washington University
in St. Louis and then at Stanford University. Already by the spring of 1956
he had good hints that DNA could be made in a cell-free system made from
E. cold cells. By 1959 he had shown his synthesis was of double helical
DNA and that He templates were always single DNA chains, providing clear
proof for our 1953 conjectures about DNA replication arising from the self-
complemeneary double helix. Essential for such work was first-class enzy-
mology. Only later did the value to genetics first emerge through the 1971
discovery of a mutant E. cold cell that apparently lacked DNA polymerase.
This most unexpected (at first unwanted?) mutant led to He discovery of
two other forms of DNA polymerase, one of which is responsible for the
majority of DNA synthesis in cells. Subsequently discovered in several places
were the very important DNA ligases, which can link DNA chains as well
as the enzymes (kineses) that place phosphate groups at the ends of DNA
chains that lack them. Equally important has been the discovery and eluci-
dation of the mode of action of a large number of enzymes that degrade
DNA chains from their ends (exonucleases). By the mid-1970s this almost
entirely enzymological approach was importantly supplemented by genetic
approaches in which genes were sought that blocked the various steps in
DNA synthesis.
For the most part, DNA replication has been a very American field, totally
dominated initially by Kornberg's lab, with He several major DNA synthesis
labs coming into existence usually being led by scientists trained by him. In
all this basic research, the hands of the intelligent enzymologists, rather than
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218
JAMES D. WATSON
the ideas of the theorists, have been the route to success, and the still freely
available federal support was a companion of every major advance. Because
of the many enzymes now known to be involved in DNA replication, it has
become increasingly difficult for young unknown scientists to make Heir
mark in this field, and an apprenticeship period in a Kornberg-type lab has
become a virtual necessity.
RULES FOR GENE EXPRESSION
Gene expression was a problem initially opened up by geneticists who
isolated mutants in E. cold that led to either increased or decreased expression
of given genes. It was first inspired, as well as dominated, by the labs of
Jacob and Monod at the Institut Pasteur. With time, however, American
labs, led for He most part by Americans once residents in Pans, proved
increasingly incisive. Very major breakthroughs achieved by Gilbert and
Ptashne, working independently at Harvard in the 1965-1969 period, led to
the isolation of the first molecules (repressors) which controlled gene func-
tioning by binding to specific segments of DNA. Through such work the
elements (sequences of base pairs) within DNA Hat control gene functioning
(promoters, operators) first became attachable at the molecular level. Such
work first demanded the use of genes present on viral chromosomes, since
no way then existed, in general, for isolating specifically desired DNA seg-
ments. Isolation of these repressors marked the ending of a more-than-10-
year interval during which research funds were plentiful for the really top
scientists and available in lesser but adequate sums for virtually all competent
molecular biolo gists, biochemists, and geneticists. From then on, the con-
sequences of the Vietnam War became increasingly felt even at the better-
funded research-onented universities.
A PAUSE WITHIN THE GOLDEN AGE
The feeling Mat we all knew where we were going which marked the 15-
year interval of 1953-1968 began to disappear with He finding of He re-
pressors that acted on specific bacterial genes. What future history would
regard as equally significant became much less obvious, and several noted
molecular biologists (Brenner, Benzer, and Stent) already had moved toward
neurobiological objectives that at least for the short term were far from
molecular. For most of us, however, seeing whether the genes of higher
organisms were regulated like those of bacteria seemed the safest way to
proceed We [eared, however, we might not be too excited with our first
results. Even given a burning desire to home in on, for example, human
genes, how to do incisive experiments was not obvious, since to start with,
genetic analysis of the type possible with E. cold was impossible. Morever,
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FROM UNDERSTANDING TO MANIPULATING DNA
219
there existed no effective way to study the DNA of higher cells. There was
even much too much DNA in bacterial cells, which contain only 1/1000 the
DNA of mammalian cells. In fact, bacterial genes had only become accessible
through the study of their viruses, whose DNA molecules were small enough
that we could at last dream of deeply understanding them at the molecular
level.
The best way to move on to higher cells, though, seemed to be an initial
focusing on their viruses, some of which contained only several thousand
base pairs. Luckily the animal viruses whose double helical chromosomes
were the smallest also had been recently found to cause tumors when injected
into certain animal hosts. So by the 1970s, a steadily increasing group of
highly motivated scientists gave up on bacterial cells for research on several
groups of DNA tumor viruses. Those viruses that were particularly focused
on SV40, polyoma, and adenoviruses all could multiply in cells growing
in culture as well as cause the transformation of normal-appearing cultured
cells into their cancer equivalents.
This intellectual migration into tumor-virus research was strongly en-
couraged by two additional factors. First, even if higher-cell DNAs followed
the same rules as found earlier for bacteria, by emphasizing tumor viruses,
important if not incisive facts might be found about putative cancer genes
we suspected were present on their chromosomes. Second, any problem that
the National Cancer Institute supported strongly invariably received more
money than comparably good research aimed at further understanding bac-
tenal DNA. So when many good labs working on bacteria began to feel
pinched for money, fiscal worries did not plague those working on cancer
viruses. Moreover, when the "War on Cancer" was begun in 1972, there
literally were not enough good cancer-oriented labs to consume the funds
Congress was more than eager lo appropriate.
THE UNANTICIPATED DISCOVERY OF RESTRICTION ENZYMES
Masses of money, however, would not have been enough to ensure the
eventual success of one of the several stated goals of the War on Cancer,
to understand the biochemical uniqueness of cancer cells. Even though
the DNA (and RNA) chromosomes of several tumor viruses could be isolated
in chemically significant amounts, as late as 1969 there was no way for Hem
to be molecularly dissected. Only in 1970 did the first effective enzyme
become available (through the work of Hamilton Smith of Johns Hopkins)
that cut DNA at well-defined positions into highly reproducible smaller frag-
ments. With this most unexpected discovery the whole nature of DNA re-
search changed. Happily, it soon became apparent that a large member of
such specific DNA-cutting (restriction) enzymes existed, each with its own
unique specificity. So any given DNA molecule could lee routinely cut into
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JAMES D. WATSON
large numbers of well-defined fragments. The existence of such fragments
immediately provided an incentive for methods to be developed that could
sequence fragmented pieces of DNA containing several hundreds of base
pairs. By 1977 such methods not only had been developed by Gilbert and
Maxam at Harvard and by Sanger of Cambridge, England, but they were
highly efficient. Only 2 years later, a small bacterial plasmid chromosome
of more than 5,000 base pairs was to have its complete sequence determined
in less than a year.
The history of how the DNA-cutting enzymes became found serves as a
classic example of the value of so-called pure research. At the same time as
the double helix was discovered, a bizarre exception to conventional genetic
behavior emerged from studying bacterial viruses that grew in several types
of bacteria. Experiments by Bertani and Luna at Indiana University and by
the Swiss physicist Jean Weigle, then at Caltech, revealed that growth in
new hosts often leads to modification of the respective viral DNAs that make
them more capable of multiplying in similar bacteria. Without such modi-
fications these DNA usually were degraded (restncted). Such modification
was not the result of classical gene mutation but somehow dependent on
some chemical alteration of the viral DNA brought about by the host bactena.
For almost a decade this phenomenon was of limited interest to only several
molecular biologists. That its importance eventually became known was the
culmination of virtually a decade of patronage driven by Weigle to a small
incipient molecular biology group that he founded within the physics de-
partment of the University of Geneva. Weigle, as one of the initial discoverers
of this so-called res~iction-modification behavior, wanted someone to un-
derstand the phenomenon at the molecular level and provided space in the
new physics building for this research. By 1965 it was clear, from Werner
Arber's and John Smith's work in Geneva, that DNA became modified by
the addition of methyl groups which prevent sequence-specific nucleates
from cutting their respective ONAs. The first such enzymes isolated in 1968
proved ineffective for DNA research, and only in 1970, from Hamilton Smith,
did a useful enzyme first emerge. In today's climate of chancy grant support,
such an apparently off-beat phenomenon most likely would not make it
through our peer review procedures, which increasingly favor projects with
high probabilities for success.
THE MAKING OF THE FIRST RECOMBINANT DNA MOLECULES
Dreams existed for making recombinant DNA molecules long before it
became technically feasible. In fact, one of the potential attractions of the
small DNA tumor virus genomes was that they might someday be engineered
to carry cellular genes from one cell to another. Paul Berg, one of the first,
if not the first, scientists to seriously dream thus, was the logical person to
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FROM UNDERSTANDING TO MANlPUl~ATlNG ONA
221
encourage the development of procedures for putting back into functional
chromosomes the DNA fragments made by specific DNA-cutting (restriction)
enzymes. The first such success in Berg's lab at Stanford Medical School
came in 1972 using the DNAjoinin=, enzymes DNA li~ase to link the ap-
propnate fragments. Greatly aiding such events were the so-called sticky
ends created by the action of many restriction enzymes. Such sin ,le-stranded
tails like to find their complements, and it proved particularly easy to rejoin
fragments containing such sticky ends. However, 1973 marked the date when
the first universally effective method for making recombinant DNA was
announced. Then Boyer and Cohen, working nearby to the Berg lab, inserted
DNA fragments into tiny bacterial chromosomes (plasmids), whose small
size allowed them to be relatively easily reintroduced back into bacteria.
Once so reinserted, such recombinant DNA plasmids multiply autonomously
to yield 25 to 50 copies per cell. Subsequently growing cultures of the
bactena-beanng recombinant plasmids effectively "clones" the DNA se=-
ments inserted into the respective plasmids. Such recombinant DNA plasmids
can be made by virtually any trained scientist, and soon it became clear that
with time, virtually any gene could be so cloned in bacteria. The problem
then became one of learning how to identify which, say Drosophila, gene
had actually been inserted into a given recombinant DNA plasmid. Now
some 1 1 years later, a variety of increasingly practical, if not ele pant, methods
exists to isolate genes of choice.
PRODUCTION OF FOREIGN PROTEINS
BY RECOMBINANT DNA-BEARING PLASMIDS
The isolation of, say, a human DNA molecule into a bacterial cell will
not generally lead to the production of the respective human proteins. Several
factors underlie such failures. First, the signals (promoters) encoded into
ONA which signify the start of RNA synthesis (transcnption) are not the
same in widely divergent forms of life. To have a reasonable chance for a
human gene to be transcribed in the commonly used bacterium E. coli, the
gene's own promoter should be cut away and replaced by an appropriate
high-level bacterial promoter. Second, the study of the genes of higher cells
(as opposed to bacteria) has revealed them to have an organization very, if
not bizarrely, different from bacterial genes. Higher cells' genes are usually
split into DNA segments (exons) that specify amino acids interspersed with
segments (introns) that do not code anything but nevertheless are transcribed
into RNA. Soon after their synthesis, such noncoding regions (introns) be-
come cut out (spliced away) yielding functional RNA molecules containing
only coded segments (exons). Given such structures we must anticipate that
most human genes would not function in bacteria. What can function, how-
ever, are the so-called cDNA clones made by copying the messages of given
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JAMES D. WATSON
mRNA molecules back into DNA chains that subsequently can be inserted
into appropriate plasmid DNA.
EXTENSION OF RECOMBINANT DNA METHODS
TO CELLS OTHER THAN BACTERIA
In 1973 we only knew how to clone genes within bacteria. Now, however,
there exist plasmids (vectors) that can be used to insert DNA into the cells
of many forms of higher organisms, including vertebrates. Already by 1978
DNA could also be reproducibly inserted into yeast cells. By now, very
highly sophisticated recombinant DNA procedures exist for putting in and
pulling out specific yeast genes from their respective chromosomes These
methods have transformed yeast genetics into a field almost rivaling in its
power that of the much more established E. cold genetics. Even more un-
anticipated has been the relatively rapid success in genetically engineering
the fruitfly Drosophila by injecting DNA into fertilized Drosophila eggs.
And, at first a highly su~pnsing, but now an almost routine, event is He
production of the so-called transgenic mice which have been genetically
altered by injecting DNA into fertilized mouse eggs. Already, faster-growing
mice (supermice) that resulted from excess production of growth hormones
not only exist, but have been shown to be genetically stable for several
generations. Genetic engineering of certain plants also is possible working
with tobacco; corn is still refractory but hopefully only temporanly.
The first easily reproducible method for introducing DNA into vertebrate
cells growing in culture emerged in 1977. Only several years were to pass
before elegant procedures were developed for cloning vertebrate DNA within
vertebrate cells (as opposed to bacterial cells). Such procedures are now In
widespread practice for He important insights that emerge as to the nature
of gene regulation in higher cells. They are now also proving in many
situations to be indispensable for He large-scale production of commercially
desirable human products. Many human proteins (e.g., the blood-clotting
factor VEI and the blood-clot destroyer plasminogen activator) are folded
up into incorrect three-dimensional forms in bacteria. To make them in
functional fonns and in the amounts needed for human use, their respective
genes must be introduced back into vertebrate cells under conditions which
allow their maximum expression. Industrial-scale techniques are thus being
developed to enable very large numbers of animal cells to be grown efficiently
in large fe~`entaiion-type containers. Even though recombinant DNA pro-
cedures using higher cells are necessarily more expensive Han comparable
production using bacteria as factories, they may be the only way to obtain
many human proteins. Their development into commercially satisfactory
procedures is thus an immediate problem for He recombinant DNA industry.
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FROM UNDEMANDING TO M^IPU~UNG DNA
DECREASING BE STILL HARMFUL REGULATION
OF RECOMBINANT DNA
223
It was both the novelty and extraordinarily potential power of recombinant
DNA procedures that led in the mid-1970s to the fear that they might generate
new forms of life that would pose real dangers to life as it now exists. So
initially many leading molecular biologists accepted He need for some form
of regulation governing recombinant DNA experimentation. But when it
came, it was much more stringent than virtually any practicing scientist
wanted or thought necessary. So during the past decade much time and anxiety
have gone to chipping away at many of the worst rules that stifled the scientific
community. For example, until 1979, He rules prevented effective application
of recombinant DNA procedures to understand cancer.
Now E. cold is effectively regarded as safe to work win, without the
crippling "safe" modifications that make their respective `'safe strains"
difficult to grow. There now also exist specifically modified vertebrate viruses
that can be used to clone desired vertebrate genes within mouse or human
cells. Stamug to work with new systems (for example, an until now poorly
characterized bactena), however, still requires the approval of the recom-
b~nant advisory committee (RAC) of NIH. Thus, younger scientists who
often wish to innovate are now temporarily held back when they cannot prove
the safety of Heir proposed research, rawer than the burden being on Hose
who wish to assert potential danger.
Given our still very incomplete knowledge of biology, what initially ap-
pears to be dangerous may be totally safe (working win laboratory swains
of polio virus) and what seems safe could conceivably be risky. So personally,
~ would abolish aD regulation of recombinant DNA. This idea, however, is
far from generally accepted, and most molecular biologists, no longer being
directly held up by current regulations, see no reason to fight for Heir total
removal. For example, we are sUll obliged to sterilize all recombinant DNA
organisms that we create, so that we cannot be accused of releasing any to
the outside world. This can be a nuisance for the individual scientist but is
tolerable as long as he or she works win microorganisms or cells in cultures
that can be easily killed by autoclaving (steam sterilization). At the ~ndus~y
level, however, real expenses will be incurred in seeing Hat noting escapes.
Of course, if we thought that there was something essentially dangerous
about recombinant DNA-contain~g organisms, Hat is He way we should
behave. But if we find He whole distinction without meet, Hen we as
scientists, and especially industry, are in He long term harrmng ourselves
as well as our county by going along win false distinctions, merely to seem
to be doing good.
Possibly the most ill-conceived regulations now deal win higher plants
and animals. Genetically engineered plants, for example, can only be grown
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224
JAMES D. WATSON
in greenhouses that preclude their release to the outside world. Moreover,
when we are finished with our experiments, we must autoclave the discarded
corn plants! In addition, we must prepare lengthy environmental impact
statements for each new genetically engineered plant, to be approved by the
Environmental Protection Agency before we can grow such new corn strains
in the field. I find it impossible to believe that any genetically engineered
corn plant could pose a threat to anything except a corn seed company not
possessing the means to genetically engineer a similar plant. Therefore, the
sooner we exempt all plant manipulations from regulation, the better.
~ sense, however, that there is a passive acceptance in government of the
need to administer such unnecessary regulation rather than to find ways to
end it. It seems to me that this is due primarily to the historical absence of
high-level officials in government with thorough training and experience in
molecular biology, at the Ph.D. level as a minimum. Recognizing Hat so
new a major science cannot yet have achieved its full appreciation, never-
theless, on balance, ~ believe biology has not been a high enough priority
concern in the past, but it must become one now. In my opinion, the United
States must treat this major new science with the same attention that it has
traditionally given other newly emerging fields of science and technology.
There is a great need for decisive and informed action on the DNA regulatory
issue. A group of high-level DNA experts from both academia and industry
should be urgently convened by the White House to discuss these issues,
and to prepare a report which can guide policymakers in the filture. If followed
by appropriate appoinunents of knowledgeable officials, the present inade-
quate situation can change, since continued indifference will not help He
United States maintain its leading position in biotechnology. I believe the
pursuit of its competitive edge in this area is a tembly important matter for
He future economic grown of the county and needs urgent attention.
POTENTIAL TO DO SCIENCE FAR EXCEEDS
CURRENT FINANCIAL BASE
Venally every new week brings form in the scientific journals one or
more examples of important research whose accomplishment would have
been unsinkable even a decade ago. Then, we knew that recombinant DNA
would speed up our science and open new frontiers, but even He most
opiimisuc scientist could not then predict what we now accept as comrnon-
place. Today, we can almost realistically dream that He DNA sequence for
a complete human genome will be completely known within this century,
and that with two to three more decades we shall be able to identify all He
key genes that underlie the functioning of our immunological and nervous
systems. By now, we have every reason to expect that, over the foreseeable
future, recombinant DNA-based science will provide masses of new and
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FROM UNDERSTANDING TO MANIPULATING DNA
225
unanticipated facts that will profoundly transform our knowledge about our-
selves and the all too many diseases that exist today, as well as generate
industrial and agricultural processes that are now unimaginable. But to do
so at the rate now potentially possible using already worked out methodol-
ogies will require a massive expansion of our current research budgets. Wisely
spending twofold more money should be possible within, at most, 10 years.
The question now for us to ponder seriously is how to achieve this ex-
pansion. If we can reach this funding level there is no doubt that the United
States will maintain its current overwhelming dominance of biological re-
search, and this is bound to have powerful positive economic consequences.
By now, however, we have the effective tradition Hat our federal gov-
emment still favors spending more on research on the physical sciences. The
government has indeed appropriated large amounts of funds for National
Institutes of Health-sponsored research, and in fact, Congress often insists
on greater expenditures than does the administration. But I fear that only
with active pressure from the administration will biology's budget become
commensurate with its importance to mankind, and to our leading position
in this area, and ~ urge them to do so.
Were support to somehow be mobilized, the next several generations of
scientists could continue to dream in the daring ways necessary for furler
quantum leaps in the human condition.
BIBLIOGRAPHY
For the history of research that led to the double hectic, the Central Dogma, and Me genetic code, see:
H. F. Judson. 1979. The Eighth Day of Creation. New York: Simon and Schuster.
J. D. Watson. 1980. The Double Helix: A Norton Critical Edition. G. S. Stent, ed. New Yoric:
Norton.
For a current understanding of gene structure and function, see:
J. D. Watson, N. Hopkins, J. Robens. J. Steitz, and A. Weiner. 1986. Molecul~rB:ology of the
Gene. 4~ ed. Menlo Park, Calif.: Benjamin/Cummings.
B. M. Lewin. 1985. Genes. 2nd ed. New York: Wiley.
For the history of the recombinant DNA controversy, including the Asilomar meetings, see:
J. D. Watson and J. Tooze. 1981. The DNA Story. San Francisco, Calif.: W. H. Freeman.
For the scientific impact generated by the recombinant DNA revolution, see:
J. D. Watson, J. Tooze, and D. T. Ku~z. 1983. Recornb~n~ DNA: A Short Course. New York:
W. H. Freeman.
OCR for page 226
Representative terms from entire chapter:
double helix
