I arrived in Cambridge in the fall of 1951 sensing a majesty of place and intellectual style unmatched anywhere in the world. The city’s great university, reflecting almost 900 years of English history, is centered on the banks of the River Cam, whose modest waters move northeast across East Anglia to the market city of Ely. Ely’s massive 12th-century cathedral had long towered over the vast flat fenland marshes that emptied into the still 40 miles of river from Cambridge to the shallow waters of the Wash, the estuary over which tides from the North Sea still roar twice daily. It was the draining over many centuries of the fens that created the rich agricultural fields and wealth of the great East Anglia estate owners. Their benefactions in return helped create along the “backs” of the Cam the many elegant student residences, dining halls, and chapels that already many centuries ago marked out Cambridge as a market city of extraordinary grace and beauty.
For most of its history, Cambridge University was highly decentralized, with teaching carried out exclusively by the residential colleges, among which Trinity was long the grandest, having enjoyed the matchless patronage of Henry VIII. In a room off the great court had lived the young Newton, whose greatest science was done in his 20s and 30s before he went up to London to be master of the mint.
Until the mid-18th century, the primary role of the colleges was to educate clergy for the Church of England, a mission carried out by fellows (dons) who were themselves required to remain unmarried while part of college life. Only in the 19th century did science become an important part of the Cambridge teaching scene. Charles Darwin’s serious excitement about natural history and geology came from his exposure in the early 1830s to these disciplines at Christ’s College. Over the next half-century, the responsibility for instruction increasingly shifted away from the colleges to newly created academic departments under university control. In 1871, the duke of Devonshire, Henry Cavendish, donated funds for the creation of the Cavendish Laboratory and the appointment of the first Cavendish Professor: James Clerk Maxwell, whose eponymous equations first unified the dynamics of electricity and magnetism. Upon Maxwell’s early death at age 49 in 1879, the 29-year-old John William Strutt (Lord Rayleigh), famed for his ideas on optics, became the second Cavendish Professor of Physics. In 1904, he was to win a Nobel Prize, as would the next four successors to the chair: J. J. Thomson (1906), Ernest Rutherford (1908), William Lawrence Bragg (1915), and Nevill Mott (1977).
By the start of the 20th century, Cambridge stood out as one of the world’s leading centers for science, of the same rank as the best German universities–Heidelberg, Göttingen, Berlin, and Munich. Over the next 50 years, Cambridge would remain in that rarefied league, but Germany would be supplanted by the United States, much strengthened by its absorption of many of the better Jewish scientists forced to flee Hitler. England similarly benefited from the arrival of some extraordinary Jewish intellectuals. If Max Perutz had not had the good sense to leave Austria in 1936 as a young chemist, there would have been no reason for my now moving to the banks of the Cam.
Though winning the great struggle against Hitler had drained England financially, the country’s intellectuals took pleasure in knowing that victory had been much of their own making. Without the physicists who provided radar for British aviators during the Battle of Britain, or the Enigma code breakers of Bletchley Park who successfully pinpointed the German U-boats assaulting the Allies’ Atlantic convoys, things might have turned out very differently.
Emboldened by the war to think expansively, the then tiny Medical Research Council (MRC) Unit for the Study of Structure of Biological Systems was doing science in the early 1950s that most chemists and biologists thought ahead of its time. Using x-ray crystallography to establish the 3-D structure of proteins was likely to be orders of magnitude more difficult than solving the structures of small molecules like penicillin. Proteins were daunting objectives, not only because of size and irregularity but because the sequence of the amino acids along their polypeptide chains was still unknown. This obstacle, however, was likely soon to be overcome. The biochemist Fred Sanger, working less than half a mile away from Max Perutz and John Kendrew at the MRC lab, was far along the path to establishing the amino acid sequences of the two insulin polypeptides. Others following in his steps would soon be working out the amino acid sequences of many other proteins.
Polypeptide chains within proteins were then thought to have a mixture of regularly folded helical and ribboned sections intermixed with irregularly arranged blocks of amino acids. Less than a year before I arrived in England, the nature of the putative helical folds was still not settled, with the Cambridge trio of Perutz, Kendrew, and Sir Lawrence Bragg hoping to find their way by building Tinkertoy-like, 3-D models of helically folded polypeptide chains. Unfortunately, they got a local chemist’s bad advice about the conformation of the peptide bond and, in late 1950, published a paper soon shown to be incorrect. Within months they were upstaged by Caltech’s Linus Pauling, then widely regarded as the world’s best chemist. Through structural studies on dipeptides, Pauling inferred that peptide bonds have strictly planar configurations, and in April 1951, he revealed to much fanfare the stereochemically pleasing alpha helix. Though Cambridge was momentarily stunned, Max Perutz quickly responded using a clever crystallographic insight to show that the chemically synthesized polypeptide polybenzylglutamate took up the alpha-helical conformation. Again the Cavendish group could view itself as a major player in protein crystallography.
The unit’s resident theoretician was by then the physicist Francis Crick, who at 35 was two years younger than Max Perutz and one year older than John Kendrew. Francis was of middle-class, Nonconformist, Midlands background, though his father’s long-prosperous shoe factories in Northampton failed during the Great Depression of the 1930s. It was only with the help of a scholarship from Northampton Grammar School that Francis moved to the Mill Hill School in North London, where his father and uncle had gone. There he liked science but never pulled out the grades required for Oxford or Cambridge. Instead he studied physics at University College London, afterwards staying on for a PhD financially sponsored by his Uncle Arthur, who after Mill Hill had chosen to open an antacid-dispensing pharmacy instead of joining the family shoe business.
Unlike Max and John, who came into science as chemists and now held PhDs, Francis had not completed his doctorate. He had done just two years of thesis research, winning a prize for his experimental apparatus to study the viscosity of water under high pressure and temperature, when the advent of the war moved him to the Admiralty. He joined the high-powered group set up to invent countermeasures against German magnetic mines, and in 1943, his boss, the Cavendish-trained nuclear physicist Harrie Massey, gave him the challenge of combating the German navy’s latest innovation. In great secrecy, German shipyards had under construction a new class of mine sweepers (Sperrbrechers) whose bows were fitted with huge 500-ton electromagnets designed to trigger magnetic mines lying a safe distance ahead. Crick came up with the clever idea that a specially designed insensitive mine would not explode until a Sperrbrecher passed directly over it. By the end of the war, more than 100 Sperrbrechers were so sent to the bottom of the ocean.
After Harrie Massey left to lead the British uranium effort at Berkeley, the Cambridge mathematician Edward Collingwood became Francis’s mentor. He saw Francis as both a friend and an invaluable colleague, inviting him for weekends to his large Northumbrian home, Lilburn Tower, and taking him to Russia in early 1945 to help decipher the workings of a just-captured German acoustic torpedo.
After the war’s end, Francis’s new bosses did not need to be as forgiving of his loud, piercing laughter or of the distaste for conventional thinking that often inspired it. Though formally made a member of the civil service in mid-1946, Francis soon lost interest in military intelligence and wanted a bigger challenge. He saw in biology the greatest range of potential problems to engage his inquisitive mind.
Apprised of Francis’s desire for a radical change of course, Harrie Massey sent him along to see the physicist Maurice Wilkins at King’s College London’s new Biophysics Laboratory. After the war, while still in Berkeley, Massey had changed Wilkins’s life by giving him a copy of Erwin Schrödinger’s What Is Life? Its message that the secret of life lay in the gene was as compelling to Maurice as it had been to me, and he soon began to make his move into biophysics. He would join J. T. Randall at St. Andrews and then move with him to London. Immediately he and Francis became friends, with Maurice soon asking Randall to offer a job to Francis. Randall thought better of it, though, correctly seeing Francis as a mind he could not control. The Medical Research Council, mindful of Francis’s high wartime repute, came to his rescue and funded his learning to work with cells at the Strangeways Laboratory on the outskirts of Cambridge.
His task during the next two years at the Strangeways–observing how tiny magnets moved through the cytoplasm of cells–did not win Francis any kudos. At best it was busywork that gave him time to seek out more appropriate challenges. These at last came when he moved his MRC scholarship across Cambridge to Max Perutz’s protein-crystallographic unit. Though his new job was no better paid, it would let him work toward the PhD, by then a prerequisite for meaningful academic positions.
By the time I came to Cambridge, Francis’s forte was increasingly seen to be crystallographic theory, though his early forays in the field had not been universally appreciated. At his first group seminar in July 1950, entitled “The Theory of Protein Crystallography,” he came to the conclusion that the methodologies currently used by Perutz and Kendrew could never establish the three-dimensional structure of proteins–an admittedly impolitic assertion that caused Sir Lawrence Bragg to brand Crick a boat rocker. Much more harm came a year later when Bragg presented his newest brainchild and Francis told him how similar it was to one he himself had presented at a meeting six months earlier. After the infuriating implication of his being an idea snatcher, Sir Lawrence called Francis into his office to tell him that once his thesis was completed he would have no future at the Cavendish. Fortunately for me, and even more so for Francis, Cambridge was unlikely to grant him the degree for another 18 to 24 months.
I was by then having lunch with Francis almost daily at the nearby pub, the Eagle, which during the war was favored by American airmen flying out of nearby airfields. Soon we would be upgraded from desks beside our lab benches to a largish office of our own next to the connected pair of smaller rooms used by Max and John. There, Francis’s ever irrepressible laughter would less disturb the work habits of other unit members. At our first meeting, Francis had spoken of his much valued friend Maurice Wilkins, who, like him, had made a wartime marriage that soon disintegrated with peace. Because he was curious to know whether Maurice’s crystallography had generated any new, perhaps sharper x-ray photos from DNA, Francis invited him for a Sunday dinner at the Green Door, the tiny apartment on top of a tobacconist shop on Thompson Lane, across from St. John’s College. Earlier occupied by Max Perutz and his wife Gisela, it had been home to Francis and his second wife Odile since their marriage two years before in August 1949.
At that meal, we learned of an unexpected complication to Maurice’s pursuit of DNA. While he was on an extended winter visit to the United States, his boss, Professor J. T. Randall, had recruited to the King’s DNA effort the Cambridge-trained physical chemist Rosalind Franklin. For the past four years she had been using x-rays in Paris to investigate the properties of carbon. Rosalind understood from Randall’s description of her responsibilities that x-ray analysis of DNA was to be her responsibility solely. This effectively blocked Maurice’s further x-ray pursuit of his crystalline DNA. Though not formally trained as a crystallographer, Maurice had already mastered many procedures and had much to offer. But Rosalind didn’t want a collaborator; all she wanted from Maurice was the help of his research student Raymond Gosling. Now, though out in the cold for two months, Maurice could not stop thinking about DNA. He believed his past x-ray pattern did not arise from single polynucleotide chains but from helical assemblies of either two or three intertwined chains bonded to each other in a fashion as yet to be determined. With the DNA ball sadly no longer under his control, Maurice suggested that if Francis and I wanted to learn more we should go to King’s in a month’s time, November 21, to hear Rosalind give a talk.
Before it was time to go to London, Francis had reason to feel good about his place in the Cavendish. He and the clever crystallographer Bill Cochran derived easy-to-use mathematical equations for how helical molecules diffract x-rays. Each of them, in fact, did so independently within 24 hours of being shown by Bragg a manuscript from Vladimir Vand in Glasgow, whose equations they immediately saw as only half baked. Theirs was an important achievement, for Francis and Bill had given the world the equations that could predict the diffraction patterns of helices according to specific dimensions. The next spring I was to deploy them to show that the protein subunits of Tobacco Mosaic Virus are helically arranged.
The best way to reveal DNA’s 3-D structure might well then have been through building molecular models using Cochran and Crick’s equations. Until a year before, this approach had made no sense, since the nature of the covalent bonds linking nucleotides to each other in DNA chains was unknown. But after work by Alex Todd’s nearby research group in the Chemical Laboratory at Cambridge, it was clear that DNA’s nucleotides are held together by 3’-5’ phosphodiester bonds. A focus on model building was a way to set oneself apart from the alternative approach of focusing on x-ray photograph details being pursued at King’s College in London.
On the day of the lecture, Francis was unable to go down to London, and I went alone, still oblivious to the difference between the crystallographic terms “asymmetric unit” and “unit cell.” As a result, the next morning I mistakenly reported to Francis that Rosalind’s DNA fibers contained very little water. My error only came to light a week later, when Rosalind and Maurice came up from London to look at a three-chain model that we had hastily constructed. It had DNA’s sugar-phosphate backbone in the center with the bases facing outward. Upon seeing it, Rosalind immediately faulted its conception, saying the phosphate groups were located on the outside, not the inside, of the molecule. Moreover, we had proposed DNA to be virtually dry, whereas, in fact, it was highly hydrated. And we got the unmistakable impression that the King’s group considered the pursuit of the DNA structure to be their property, not one to be shared with their fellow MRC unit in Cambridge. All too soon we learned that Sir Lawrence Bragg was of the same mind, when he told us to refrain from all subsequent DNA model-building activities. In stopping us Bragg was not motivated solely by a need to remain on good terms with another MRC-supported group. He wanted Francis to focus exclusively on research for his PhD and be done with it.
This debacle, however, would not have occurred if Francis and I had started to think as if we were chemists. Even without the King’s x-ray patterns, there were clues in the chemical literature that should have led us to propose a double helix as the basic structure of DNA. From the start we should have restricted ourselves to models in which externally located sugar-phosphate backbones were held together by hydrogen bonds between centrally located bases. Strong physical-chemical evidence for bases so held together had come from the postwar experiments of John Gulland. In 1946, his Nottingham lab showed that within native DNA molecules the bases are so arranged as to hinder them from exchanging hydrogen atoms. These data suggested widespread hydrogen bonding between DNA bases. This insight was widely available, published by the Cambridge University Press in the 1947 SEB Symposium volume on nucleic acids.
Furthermore, given Linus Pauling and Max Delbrück’s prewar proposal that the copying of genetic molecules would involve structures of complementary shape, Francis and I should have reasonably focused on two-chain rather than three-chain models. In a two-chain model, each DNA base would hydrogen-bond exclusively to one with a molecule of complementary shape. In fact, experimental data pointing to this conclusion, too, already had been published, most coming from the lab of the Austrian-born chemist Erwin Chargaff in New York. Without understanding the significance of his discovery, Chargaff reported that in DNA, the amounts of the purine adenine were roughly equal to the amounts of the pyrimidine thymine. Likewise, the amount of the second purine, guanine, was similar to the amount of the second pyrimidine, cytosine.
The exact shape of such base pairs would depend upon where the atoms available for hydrogen bonding were located on each base. In 1951, few chemists knew enough quantum mechanics to make such inferences. So that fall we should have sought advice from the several British chemists trained in this esoteric field. In retrospect, Alex Todd’s lab, after determining the covalent linkages in DNA, should have moved on to determining what the molecule looks like in three dimensions. But in those days, even the best organic chemists thought such problems were better left to x-ray crystallographers. In turn, most x-ray diffraction experts felt the time had not yet arrived to tackle biological macromolecules. In a sense, then, the field was wide open.
Even after he found the alpha helix, Linus Pauling remained only moderately attentive to DNA, never seriously believing that it had a genetic role. Even so, when hearing of Maurice Wilkins’s crystalline photo, he asked to have a look, being misinformed that Maurice himself was not seriously trying to determine the structure. As that was precisely what Maurice was up to, he quickly replied that he wanted more time to look over the photo before releasing it to others. Undeterred, Linus wrote directly to the King’s boss, John Randall, but this approach was likewise unsuccessful. Linus lost the scent until a year later at a summer phage meeting outside of Paris, where he first learned of the work recently completed at Cold Spring Harbor by Alfred Hershey and Martha Chase, showing that phages were also made from DNA. The news convinced Linus he must go after the DNA structure despite his lack of high-quality DNA x-ray photos. His voyage back to the States could have been a great fortuitous opportunity. Also on board the transatlantic boat was Erwin Chargaff, who like Pauling had come to Europe to attend that summer’s International Biochemical Congress in Paris. But instead of learning about the equivalence of A with T and G with C, Linus took an instantaneous dislike to his shipmate and avoided him all across the Atlantic.
Preoccupied much of the fall of 1952 with the race against Francis Crick for the coiled-coil structure of alpha keratin, Pauling only turned to DNA in earnest in late November. Soon he was very much attracted to a DNA model in which three sugar-phosphate backbones coiled around each other. He was hung up on three chains because of the reported high density of DNA. At no time did he seriously consider a two-chain molecule. For the three chains to hold together, he reasoned, DNA would have to be uncharged, forming hydrogen bonds between opposing phosphate groups. Soon satisfied that he had found the general structure for nucleic acids, he wrote to Alex Todd a week before Christmas adding that he was not bothered that his structure provided no clues as to how DNA functions in cells. That problem was for another day. At no time did he ever take into account Chargaff’s base compositions, published more than a year before in several journals. The essential parameters for Linus that December were bond angles and length, not what DNA did biologically or how it behaved in solution. It was immediately evident that the atoms of his model were not fitting together as neatly as they did in the alpha helix. Even his best structure was stereochemically shaky, with several central phosphate oxygens uncomfortably close to each other.
Fearing that someone in England might beat him to the punch with a similar model, Linus hastily submitted a manuscript for publication in the Proceedings of the National Academy. Then he triumphantly sent two manuscript copies to Cambridge–one to Bragg, the other to his son, Peter. We were instantly engulfed in anxiety until we realized that Linus had used hydrogen atoms belonging to the phosphate groups to hydrogen-bond the three chains together. We knew at once that his model must be wrong, since DNA–an acid–normally releases all its hydrogen ions in solution. So Francis and I rushed around Cambridge to see whether the local chemical hotshots also found Pauling’s concept totally implausible. Quickly reassured by Alex Todd that Linus had indeed made a gigantic chemical goof, I went down almost immediately to London to show the manuscript to Maurice Wilkins and Rosalind Franklin, the latter preparing to move to J. D. Bernal’s group in Birkbeck College, where she would no longer work on DNA.
Maurice was more than relieved to learn that Linus was so far off base. In contrast, Rosalind was annoyed at my showing her the manuscript, tartly telling me that she had no need to read about helices. In her mind, the crystalline DNA A-form structure was most certainly not helical. In fact, six months before, she had sent out invitations to a July “memorial service” to celebrate the death of the DNA helix. Here Maurice thought that Rosalind had been badly deluding herself, and to prove it, he impulsively showed me an x-ray photo that the King’s group had been keeping secret since Raymond Gosling took it more than nine months before. Originating from a more hydrated B-form DNA fiber, this picture displayed unequivocally the large cross-shaped diffraction pattern to be expected from a helical molecule. My jaw dropped, and I rushed back to Cambridge to tell everyone what I had learned. I thought we should not wait a moment longer before commencing to build models. Someone was bound to tell Linus that his was dead on arrival. Sir Lawrence Bragg instantly agreed, and with him finally behind us, Francis and I soon were back playing with cutout shapes. By then I realized that DNA’s density did not, as I originally thought, rule out two strands as opposed to three. It thus made sense for me to focus first on possible ways for two DNA chains to twist around each other.
In fact, Rosalind should also have been focusing on two-chained DNA models. More than a year before, she had carefully measured her x-ray diffraction patterns from crystalline A-form DNA looking for possible molecular symmetries. Finding her data compatible with three possible chemical “space groups,” she went up to Oxford to get advice from Dorothy Hodgkin, then England’s premier crystallographer, justly famed for solving the structure of penicillin. As soon as Dorothy saw that Rosalind was considering space groups involving mirror symmetry, however, she sensed crystallographic callowness. Experienced crystallographers would never postulate mirror symmetry for a molecule made up exclusively of 2-deoxy-D-ribose. Instead, Dorothy believed, Rosalind should have been considering only the implications of the third monoclinic space group (a rectangular prism of three unequal axes). Upset by Dorothy’s sharp put-down of her crystallographic acumen, Rosalind left Oxford, never to return. If she had gone instead to Francis for help, she would have immediately learned that the C2 monoclinic space group suggested that DNA was a double helix with its chains running in opposite directions.
Francis only learned of DNA’s monoclinic space group through reading a nonconfidential King’s progress report sent to Max Perutz in mid-February. By then, through a new burst of model building, I had found that a sugar-phosphate backbone of 20-angstrom diameter optimally repeats every 34 angstroms, the repeat distance measured in B-form DNA. Francis now argued, in light of Rosalind’s space group, that the two chains must run in opposite directions. But I didn’t initially buy this assertion, not understanding the underlying crystallographic symmetry argument. Until I knew how the centrally located bases bonded to each other, I didn’t want to worry about backbone directions. Then, unknown to me, my model building was being hindered by faulty textbook descriptions of the structures of guanine and thymine. Using such false configurations, I had become momentarily excited about a pairing scheme similar to that found in crystals of adenine.
That scheme, however, would have given a 17-angstrom repeat along the helical axis, not the 34-angstrom figure observed by Rosalind. Happily, the Caltech structural chemist Jerry Donohue, then spending his sabbatical year in Cambridge, set me on the right track by arguing that the guanine and thymine hydrogens should have keto rather than the textbook-ascribed enol configurations. Needing only a day to incorporate Jerry’s reasoning, I changed the locations of the hydrogen atoms on my paper-cutout models of thymine and guanine. Almost instantly I found myself forming the A-T and G-C base pairs we now know to exist in DNA. Coming a half-hour later into our office that Saturday morning, Francis took only a few minutes to conclude that the symmetry of the base pairs demanded that the chains run in opposite directions. Rosalind’s monoclinic space group was in a true sense a prediction of a model derived by Francis and me from purely stereochemical arguments. The double helix had to be correct. All that remained to be done was to build a backbone segment and measure its atomic coördinates to show that all the bond lengths and angles in our model agreed with those previously found in smaller molecules. This task, which for the first time in months took Francis away from his desk, took less than three days to complete. The double helix was ready to let loose upon the world.
Breaking the news to Wilkins that we very likely had solved the DNA structure was bound to cause his heart to spasm. A day after we had verified appropriate coördinates for all the atoms, a letter from him arrived informing Francis that Rosalind was out of King’s and that Maurice was about to resume work on DNA. Perhaps to soften the blow, John Kendrew, not Francis, called Maurice to report that Francis and I had a promising novel structure for DNA. Coming up the next day, Maurice instantly recognized the double helices’ elegant simplicity and agreed that it was likely too good not to be true. Knowing that we would not have found the DNA structure without knowledge of x-ray results from King’s, Francis and I suggested to Maurice that his name also be on the manuscript we planned to send to Nature. Without hesitation, he declined, possibly not knowing how to deal with Rosalind Franklin’s and Raymond Gosling’s equally important contributions. The April 25, 1953, issue of Nature, besides containing the 900-word description of our model, also included separate continuing contributions from the two warring DNA groups at King’s. Maurice was later to write that his refusal to publish jointly with the two of us was the biggest mistake of his life.
In every sense, solving the double helix was a problem in chemistry. Alex Todd facetiously told me that Francis and I were good organic chemists, not wanting to admit that a major objective in chemistry had been solved by nonchemists. In reality, Francis and I would not have been first to see the structure if Todd’s fellow chemists had not done botched jobs. Linus had all the keys to unlock the DNA structure but inexplicably didn’t use them that fall of 1952. Rosalind Franklin would have seen the double helix first had she seen fit to enter the model-building race and been better able to interact with other scientists. If she had accepted rather than rejected Maurice as a collaborator, the two of them could not have failed to realize the significance of the monoclinic space group. Dorothy Hodgkin’s Oxford put-down of Rosalind as a crystallographer would not have been the fatal wound that it seems in retrospect.
In contrast, Francis and I were far from being on our own. One flight up was the clever Bill Cochran, who put the Bessel functions of helical diffraction theory into Francis’s working vocabulary, whence they entered mine. Even more important, Jerry Donohue’s spartan desk was no more than 12 feet from mine and Francis’s when his quantum chemistry expertise squelched my initial desire to build a double helix based on like-with-like base pairing (e.g., A-A and T-T). The Cavendish then was a magnet for minds that wanted to be challenged by others of equal power. In contrast, Linus Pauling’s Caltech was a chemistry garden of mortals hovered over by a god who saw no need to assimilate the ideas and facts of others. If Linus had only spent a few days in Caltech’s libraries perusing the literature on DNA that fall, he would most likely have hit upon the idea of base pairing and would now be celebrated for both the alpha helix and the double helix.
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, the DNA structure by which genetic information is carried and how it is copied, were thus 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 cytosine) determines the order of the amino acids in the polypeptide products–the stuff of the proteins forming all living things–of individual genes. Since there were known to be 20 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 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 already several-years-old observation 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 that 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.
After 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–I 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 returned to the States to begin 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 buy 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 1951 Swiss 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 8,000 meters high one of the Karakoram’s most daunting peaks.
Francis was keenly awaiting the arrival of my successor as the unit’s geneticist, the South African-born Sydney Brenner. We first met when he was working for a PhD 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 in the summer of 1953, when he read our second Nature paper on the subject (“Genetical Implications of the Structure of DNA”). By early 1954, some of 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 20-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 among 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, Francis wrote to the 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 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.
Alex returned in December to his job at the National Institutes of Health outside Washington, DC, and 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.
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 three-dimensional 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 100 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 of analyzing x-ray diagrams was far from straightforward. Given Pauling’s recent success using molecular modeling to find the alpha helix, using this approach on DNA was far from outlandish; actually, it was a no-brainer.
2) Only work on problems when you feel tangible success may come in several years
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 only feel comfortable taking on a problem when I feel meaningful results can come over a three- to five-year interval. Risking your career on problems when you have only a tiny chance of seeing the 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, 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 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 his or her 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 to also 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 having kept good relations with others in the field outside our partnership, he would always have his ideas checked by others with even more 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, that the stereochemistry of the sugar-phosphate groups would of course move them to outer positions of helices that use approximately 10 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 person 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 come to nothing 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 be successful 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, you should never burn your past intellectual bridges, at least until your new career has taken off.
James Watson’s Avoid Boring People: And Other Lessons from a Life in Science will be published by Knopf in September.