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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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220 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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222 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.

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