Virtually everyone who came to our now even more cramped Cavendish office to see the large 3-D model made in early April was thrilled by its implications. Any doubt as to whether DNA and not protein was the genetic-information-bearing molecule suddenly vanished. The complementary nature of the base sequences on the opposing chains of the double helix had to be the physical counterpart of the Pauling-Delbrück theoretical postulation of gene copying through the creation of complementary intermediates. DNA double helices as they exist in nature must reflect single-stranded template chains hydrogen-bonded to their single-stranded products of complementary sequence. Two of the three big questions in molecular genetics, what is the structure of DNA and how is it copied, were suddenly resolved through the discovery of base-pair hydrogen bonding.
Still to be ascertained was how the information conveyed by the sequence of DNA's four bases (adenine, guanine, thymine, and cyto-sine) determines the order of the amino acids in the polypeptide products of individual genes. Since there were known to be twenty amino acids and only four DNA bases, groups of several bases must be used to specify, or code for, a single amino acid. I initially thought the language of DNA then would be best approached not through further work on the DNA structure but by work on the 3-D structure of its close chemical relative ribonucleic acid (RNA). My decision to move on from DNA to RNA reflected the observation, already several years old, that polypeptide (protein) chains are not assembled on DNA-containing chromosomes. Instead they are made in the cytoplasm on small RNA-containing particles called ribosomes. Even before we found the double helix, I postulated that the genetic information of DNA must be passed on to RNA chains of complementary sequences, which in turn function as the direct templates for polypeptide synthesis. Naively I then believed that amino acids bonded to specific cavities linearly located on the surfaces of the ribosome RNA components.
Three subsequent years of X-ray studies—the first two at Caltech and the last back with the “Unit” in Cambridge, England, in which I was joined by the Pauling- and Harvard Medical School-trained Alex Rich—frustratingly failed to generate a plausible 3-D structure for RNA. Though RNA from many different sources produced the same general X-ray diffraction pattern, the pattern's diffuse nature gave no solid clues as to whether the underlying RNA structure contained one or two chains. By early 1956 I decided to change my focus from X-ray studies on RNA to biochemical investigations on ribosomes when I began teaching in the fall at Harvard. Also then seeking a more tractable challenge was the Swiss-born biochemist Alfred Tissières, then studying oxidative metabolism at the Molteno Institute in Cambridge. He had already briefly dabbled with ribosomes from bacteria and liked the idea of our seeking out how they work across the Atlantic in the other Cambridge.
Alfred came from an old Valais family that long owned a bank in Sion. When he was less than a year old his banker father tragically died during the great influenza epidemic of 1918. Much later a minor inheritance let Alfred possess the sleek Bentley that he parked across the Cam on land adjacent to the school for the famed King's College boys’ choir. An even greater source of pride than his car was Albert's election to the British Alpine Club in 1950. His formidable ascents of the south face of the Taschhorn and the north ridge of the Dent Blanche led to an invitation to join the Swiss 1951 Everest reconnaissance expedition. Regretfully he had to decline, giving priority to his research efforts in the Molteno Institute that led, in 1952, to a research fellowship at King's. Climbing, however, always remained essential to his psyche. In the summer of 1954 he joined in the Alpine Club's reconnaissance of Pakistan's Rakaposhi, at almost eight thousand meters high one of the Karakoram's most daunting peaks.
Alfred Tissières braves an airy traverse of the Gilgit River in northern Pakistan in 1954.
After I left for Harvard, my successor as the Unit's geneticist was to be the South African-born Sydney Brenner. We first met when he was working for a Ph.D. at Oxford following medical training in Johannesburg. In the spring of 1953, Sydney was among those to have come to Cambridge to have a peek at our big molecular model of the double helix. He entered our lives more importantly, however, during the summer of 1954, when Francis and I were at Woods Hole on Cape Cod, talking genetic codes with the Russian-born, big bang theoretical physicist George Gamow. Then learning bacterial genetics at Cold Spring Harbor, Sydney came to Woods Hole for several days, greatly impressing Gamow and Francis by his quickness to catch on to their ideas and to propose experiments to test them.
Gamow, then a professor at George Washington University, was first drawn to the double helix through his reading in the summer of 1953 of our second Nature paper on the subject (“Genetical Implications of the Structure of DNA”). By early 1954, his seemingly wacky initial ideas had crystallized into a precise mechanics for the genetic code by which overlapping groups of three nucleotides coded for successive amino acids along polypeptide chains. On an early May 1954 visit to Berkeley, where George was on sabbatical, I proposed that we form a twenty-person code-seeking club, one member for every amino acid. George instantly reacted positively, much anticipating designing a tie and stationery for our RNA Tie Club.
Though there was never a convention of all its members, “notes” that circulated within the RNA Tie Club greatly advanced thought about genetic codes. The most famous of these notes, by Francis, in time would totally change the way we thought about protein synthesis. In January 1955 he wrote to the RNA Tie Club correctly suggesting that amino acids, prior to being incorporated in polypeptide chains, would attach to small RNA adaptors that in turn bind to template RNA molecules. For each amino acid, Francis postulated, there must exist a specific adaptor RNA (now called transfer RNA). In the absence then of any experimental evidence for small RNA, much less their chemical binding to amino acids, even Francis could not long remain buoyant about his adaptors. Six months were to pass before he was to regain a manic mood, but this time it was over a 3-D model for collagen that he and Alex Rich built over the summer of 1955.
After Alex returned in December to his job at the National Institutes of Health outside Washington, D.C., Francis and I focused for the winter of 1956 on the structures of small spherical RNA viruses, outlining how their cubic symmetry resulted from the regular aggregation of smaller asymmetrical protein building blocks. How their single long RNA chains were organized with their polyhelical protein shells remained to be seen. Our last time as a team of two was at a Johns Hopkins University-organized symposium in mid-June 1956, entitled “The Chemical Basis of Heredity.” Upon arriving at the Hotel Baltimore, Francis jubilantly pointed out that we had been assigned adjacent rooms in the top-floor presidential suite.
After that occasion staying at the top was to be a challenge we would have to face separately.
Remembered Lessons
1. Choose an objective apparently ahead of its time
Mopping up the details after a major discovery has been made by others will not likely mark you out as an important scientist. Better to leapfrog ahead of your peers by pursuing an important objective that most others feel is not for the current moment. The 3-D structure of DNA in 1951 was such an objective, regarded by virtually all chemists as well as biologists as unripe. One well-known scientist then toiling in DNA chemistry predicted that a hundred years would pass before we knew what the gene looked like at the chemical level. Before setting out, you need to figure out a new path by which to climb—or, even better, a new intellectual catapult that can potentially hurl you over crevasses seemingly too broad to be leapt over by experimentation. The model-building approach to the DNA structure in 1951 had the potential to let us get where we needed to go at a time when the more orthodox approach, limited to analyzing X-ray diagrams, was far from straightforward. Given Pauling's recent success using molecular modeling to find the a-helix, using this approach on DNA was far from outlandish; actually, it was a no-brainer.
2. Work on problems only when you feel tangible
success may come in several years
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Many big goals are truly ahead of their time. I, for one, would like to know now where exactly my home telephone number is stored in my brain. But none of my colleagues who think about the brain yet know even how to approach this problem. We might do very well by asking how the cells in the much, much smaller fly brain are wired so as to recognize the odor of a specific alcohol—that would be getting us somewhere.
I feel comfortable taking on a problem only when I believe meaningful results can come over a three-to-five-year interval. Risking your career on problems when you have only a tiny chance to see a finish line is not advisable. But if you have reason to believe you have a 30 percent chance of solving over the next two or three years a problem that most others feel is not for this decade, that's a shot worth taking.
3. Never be the brightest person in a room
Getting out of intellectual ruts more often than not requires unexpected intellectual jousts. Nothing can replace the company of others who have the background to catch errors in your reasoning or provide facts that may either prove or disprove your argument of the moment. And the sharper those around you, the sharper you will become. It's contrary to human nature, and especially to human male nature, but being the top dog in the pack can work against greater accomplishments. Much better to be the least accomplished chemist in a super chemistry department than the superstar in a less lustrous department. By the early 1950s, Linus Pauling's scientific interactions with fellow scientists were effectively monologues instead of dialogues. He then wanted adoration, not criticism.
4. Stay in close contact with your
intellectual competitors
In pursuing an important objective, you must expect serious competition. Those who want problems to themselves are destined for the backwaters of science. Though knowing you are in a race is nerve-racking, the presence of worthy competitors is an assurance that the prize ahead is worth winning. You should feel more than apprehensive, however, if the field is too large. This usually means you are in a race for something too obvious, not enough ahead of its time to deter the more conservative and less imaginative majority. The presence of more than three or four competitors should tell you that your chance of winning is not only low but virtually incalculable since you are unlikely to have a detailed knowledge of the strengths and weaknesses of most of your competition. The smaller the field, the better you can size it up, and the better the chance you will run an intelligent race.
Avoiding your competition because you are afraid that you will reveal too much is a dangerous course. Each of you may profit from the other's help, and an effective dead heat that allows you to publish simultaneously is obviously preferable to losing. And if it happens that someone else does win outright, better it be someone with whom you are on good terms than some unknown competitor whom you will find it hard not to at least initially detest.
5. Work with a teammate who is your intellectual equal
Two scientists acting together usually accomplish more than two loners each going their own way. The best scientific pairings are marriages of convenience in that they bring together the complementary talents of those involved. Given, for example, Francis's penchant for high-level crystallographic theory, there was no need for me also to master it. All I needed were its implications for interpreting DNA X-ray photographs. The possibility, of course, existed that Francis might err in some fashion I couldn't spot, but keeping good relations with others in the field outside our partnership meant that he would always have his ideas checked by others with even greater crystallographic talents. For my part, I brought to our two-man team a deep understanding of biology and a compulsive enthusiasm for solving what proved to be a fundamental problem of life.
An intelligent teammate can shorten your flirtation with a bad idea. For all too long I kept trying to build DNA models with the sugar phosphate backbone in the center, convinced that if I put the backbone on the outside, there would be no stereochemical restriction on how it could fold up into a regular helix. Francis's scorn for this assertion made me reverse course much sooner than I would have otherwise. Soon I too realized that my past argument had been lousy and, in fact, the stereochemistry of the sugar-phosphate groups would of course move them to outer positions of helices that use approximately ten nucleotides to make a complete turn.
In general, a scientific team of more than two is a crowded affair. Once you have three people working on a common objective, either one member effectively becomes the leader or the third eventually feels a less-than-equal partner and resents not being around when key decisions are made. Three-person operations also make it hard to assign credit. People naturally believe in the equal partnerships of successful duos—Rodgers and Hammerstein, Lewis and Clark. Most don't believe in the equal contributions of three-person crews.
6. Always have someone to save you
In trying to be ahead of your time, you are bound to annoy some people inclined to see you as too big for your britches. They will take delight if you stumble, believing your reversals of fortune are deserved. They may reveal themselves only in the moment of your discomfiture: often you find them controlling your immediate life by, say, determining whether you will get your fellowship or grant renewed. So it always pays to know someone of consequence—other than your parents—who is on your side. My hopes to go for broke with DNA by going to Cambridge would have gone nowhere if my phage-day patrons, Salvador Luria and Max Delbrück, had not come to my rescue when my request to move my fellowship from Copenhagen to Cambridge was turned down. I was then judged, not without cause, to be unprepared for X-ray crystallography and urged to move instead to Stockholm to learn cell biology. Immediately John Kendrew offered me a rent-free room in his home, while Luria, through a personal connection, got my fellowship extended for eight months. Soon after, Delbrück arranged a National Foundation for Poliomyelitis fellowship for the succeeding year. In finding the funds that kept me in Cambridge, Luria and Delbrück were hoping that my new career as a biological structural chemist would succeed and do them proud. But they fretted about my being too far from their fold, knowing that I would likely leave empty-handed from my long Cambridge stay. The second year of my fellowship was, in fact, to be spent at Caltech, giving me at least a measure of security in the event the DNA structure was solved by others. In leaving one field for another, it never makes sense to burn your past intellectual bridges at least until your new career has taken off.
7. MANNERS PRACTICED AS AN UNTENURED PROFESSOR
THE HARVARD to which I moved in the fall of 1956 thought of itself as the best university in the United States. Most certainly it was the oldest, and with its endowment the largest of any university's, it saw no reason not to have the most distinguished faculty of any institution on the planet. Before any tenure appointment, a group of eminent experts in the field were assembled to advise the president as to how the proposed candidate ranked among peers worldwide. The use of such ad hoc committees dated from the administration of James Conant, a distinguished organic chemist and only the second scientist ever to lead Harvard. Taking over from Lawrence Lowell in 1933, he presided for twenty years, resigning in 1953 to serve as U.S. high commissioner and later ambassador to Germany. Deeply involved in the military-related science that helped the United States win World War II, he seized upon the improvements in the nation's scientific capability to raise the bar correspondingly at Harvard's mathematics, physics, and chemistry departments.
The Harvard biology faculty contained several world-class scientists, in particular the vision biochemist George Wald and the evolution authority Ernst Mayr. But too many of its faculty had pedestrian outlooks incommensurate with the quality of most Harvard students. All too typical was the Biology Department's uninspired introductory course. It abounded in dull facts for its largely premedicai enrollees to memorize. One year its abject dreariness provoked the studentwritten “Confidential Guide” to suggest that one of its instructors might do well to shoot himself.
Unlike Caltech, w
here genetics was the dominant biological discipline, Harvard's department, then chaired by the pedantic amber insect specialist Frank Carpenter, did not treat one field of biology as any more important than another. Together with his forlorn assistant, the former Rhodes scholar Orin Sandusky, Carpenter lumberingly oversaw the department's day-to-day activities in the massive five-story Biological Laboratories. It was built in the early 1930s in brick textile factory style, much of the money for its construction coming from the General Education Board of the Rockefeller Foundation, whose members wanted the benefaction to promote research as opposed to teaching. The nonexistence of a Biolabs lecture hall big enough for large biology classes was thus not a mistake but a matter of principle.
By the time the construction of the Biolabs started in 1932, the Depression had arrived and funds to outfit the north wing never materialized. Twenty-five years later, this wing's long empty factorylike floors suggested themselves to me as more than sufficient space for DNA-based biology to thrive at Harvard if the university was so inclined. Equally important to this objective, many senior faculty members were on the verge of retiring. Their large square corner offices, connecting to secretarial areas, themselves big enough for professors in less prestigious institutions, would soon be free. No lunchroom existed within the Biolabs either, and at noon the notables set off for the Georgian-style Faculty Club on Quincy Street. There they invariably lunched by themselves around the same rectangular table just inside the main dining room. Administrative minutiae, not ideas, dominated most conversations, with food chosen from a menu featuring horse steak, a proud holdover from wartime's austerity. Off the main dining room and usually entered by its own outside entrance was a separate room for women guests. Then there were effectively no women on Harvard's Faculty of Arts and Sciences.
Avoid Boring People: Lessons from a Life in Science Page 12