Chapter 6: Divide and Rule

When talking about his earlier life and times, Sir Paul Nurse, President of the Royal Society and Nobel laureate, uses one word rather frequently. It is, somewhat surprisingly, failure. A clever grammar school boy from a working class family, it took him a while to get to grips with passing exams at school, and his route into university was more tortuous than most. He did an unexciting PhD, publishing two papers, which in the years since have garnered only five citations. After his postdoc, working on an untrendy subject, he failed to get any of the lectureships for which he applied and had to take a post funded by short-term money at the University of Sussex, to keep afloat. When that money ran out, he failed to get still more jobs and was on the brink of leaving the country for a laboratory in Germany when he was rescued by Walter Bodmer, Director of the ICRF.

In addition to this lexicon of failure, other facts fall out from past interviews with Paul. How did he get interested in science? In two ways: first, as a small, solitary boy, standing entranced in the street in his pyjamas as Laika the space dog and Sputnik 2 flew through the night sky over Wembley; subsequently, observing with fascination the life beneath his feet as he walked to and from school through the fields. Interviewers have covered other subjects as diverse as his Desert Island Discs (luxury: a telescope; favourite record: Billy Joel “Just the way you are”), his attempts to learn the recorder as an adult, and why he shaved off his moustache (“I thought it would make me look more vulnerable.”). In recent years, the bombshell of Paul’s discovery that his parents were, in fact, his grandparents, and his real mother was the person he had thought was his older sister, has added an extra level of tragic complexity to the story.

These snippets are, of course, nowhere near the whole truth, but they do supply some intriguing clues to what makes this apparently bumbling (mess is another word that recurs frequently) science enthusiast tick and how he became what he is today. And one of these clues is the constancy of the narrative itself. Science is too frequently disseminated to the public as a series of facts (“scientists have discovered that …”), and it is only rarely that the story behind the facts is regarded as relevant. But for Paul’s research, the narrative is everything, and what he did to win his Nobel Prize, what he is still doing today, is living out a scientific story that he has been telling since he was a young man in his 20s.

Paul Nurse’s baptism as a scientist came in a most unlikely place, just off the North Circular Road near the Hanger Lane gyratory in Willesden, North London, at the Guinness Brewery-owned Twyford Laboratories. He was 17 years old and had finished school a year early, leaving with good A levels, but crucially lacking the French O level he would need to get him into university in the 1960s. His school career had been almost comically inconsistent; he veered between the bottom and the top of the class, sometimes in the same subject, but his bête noire was definitely languages. Despite having a razor-sharp mind able to grasp almost anything as long as it has logical consistency, Paul struggled, and still struggles, with pronouncing unfamiliar words in English, let alone in French. Combined with a total ignorance of grammatical structure and an inability to associate the strange French words with either their English equivalents or the objects they described, he was a walking linguistic disaster. Accordingly, the original plan for his post–A level year was to stay on in the sixth form to work at his French and to redo an A level or two (an A and two B grades not being considered quite good enough). However, after a term of boredom and wanting to earn a bit of money to help with the family income, Paul dropped out. Resigning himself to taking French O level by himself (famously, he eventually failed it a grand total of six times), he got a job making biological media for a group studying Salmonella food poisoning at the Twyford Labs, while he reapplied to university.

Paul’s boss at the Twyford Labs was Vic Knivett, a shy but very kindly man with an incongruous interest in Russian dancing, of which he was an enthusiastic exponent. The new junior technician Nurse once caught him practising after hours on one of the benches in the lab, much to Knivett’s embarrassment. The job was undemanding, consisting of visiting the inhabitants of the lab every morning to take their orders for that day’s media, mixing it up from powders, and then delivering it. Paul realised quite quickly that because everyone always asked for the same items, he could make solutions up in bulk on Mondays, store them in the cold room, and then distribute them upon request. This left the problem of what to do for the rest of the week, so he approached a rather surprised Knivett to ask him for more work. Knivett, to his credit, recognised a gift horse when he saw one and put Paul onto a proper research project, looking at rapid ways of detecting Salmonella by using the new technique of fluorescence microscopy. Paul thrived on the work, and for the next few months was happily occupied during the day, although he still had to wrestle with intractable French vocabulary in his spare time.

Fortunately for the young Nurse, somebody high enough up in the hierarchy of a British university had the good sense to realise that incompetence in a foreign language was no barrier to becoming a good scientist. In 1967, after a journey on his motorbike up the new M1 motorway for a hastily convened interview, Paul started a degree in Biology at Birmingham University, thanks to John Jinks, head of the Genetics Department. Jinks’s own staunchly working-class background may have predisposed him towards bucking the Establishment’s desire for unnecessary qualifications. He cooked up a deal with a member of the French faculty to allow Paul to take and pass a semi-fictitious course in French in his first year, and, with the rules bent but not quite broken, Paul was free to start on his path to scientific glory.

The path certainly didn’t seem particularly glorious to begin with. Paul is remembered by Jack Cohen, one of his Birmingham lecturers, as being undistinguished, and Paul himself summarises his third-year undergraduate project, on the respiration rate of dividing fish eggs, as “a disaster, but a useful disaster,” falling at the last hurdle because a vital control had been omitted. Having started off with an interest in ecology and genetics, he abandoned them early on, the former because he “couldn’t bear to be muddy and wet and out of control” and the latter because of an excessive emphasis on cytogenetics, not the most exciting of topics. Instead, Paul took a classical biology degree, majoring in botany and zoology, and got a First, despite having missed all of the second-year zoology lectures in a valiant attempt, no doubt, to fail at something yet again.

The haphazard route by which he arrived at his first-class degree had provided Paul with two unusual mental resources, which give some clues to his subsequent outstanding success: he was very relaxed about failing, never regarding it as much of a problem, and his sense of intellectual excellence was entirely self-referential, making him highly competitive, but only with himself.

Here is Paul on the benefits of early failure:

Because I failed at so many things so often, because I was in a mess at school ... it gave me a sort of internal discipline—you take less note of what other people think of you, what other people say, because you don’t get off on being praised about things. I had to be resilient inside. … I was constantly comparing me to me when I did well, and not with other people. I realise it’s very odd, but it’s really useful, because when I … failed examinations, I couldn’t get into university, I couldn’t get a job, when you put all that together, it was a constant low to medium level [of] failure about things. So when I got to difficult problems and I failed, I didn’t go into depression or anything. And when you get into research, it’s constant failure all the time, and I was perfectly trained for it.

So what does a self-competitive optimist with no fear of failure do for a PhD? Probably influenced at least slightly by the fish eggs debacle in his final year, Paul had already decided that there was no point slogging away in a lab unless you were working on something that really mattered, something that was important enough to stand a good risk of failure on a grand scale. Paul’s lecturers at Birmingham, traditional biologists all, had encouraged him to apply to botany departments for his PhD, and, although he had been offered a project at Cambridge, the topic, on the biochemistry of RNA, was not to his taste. His omnivorous reading habit had led Paul far beyond the mundane nuts-and-bolts problems that such a PhD project would address, into a theoretical land of conjecture and speculation about how biological entities are ordered; how does an organism build itself up from a single cell, and how does the resulting community of cells interact during a lifetime?

Forty years on, Paul is still preoccupied with this question, which lies at the heart of understanding biology itself, and the length of elapsed time is indicative of the scale of the problem. Wisely, his younger self made a very logical decision to start small, studying one of the most important but probably the simplest developmental decisions a cell can make—how its structures are organised in space and time to enable it to divide into two. Understanding the molecular events that regulated this decision, dissecting the changes in enzyme and gene regulation that were required, might just be approachable at a single-cell level, even taking into account the rather limited molecular techniques then available.

Cell division occurs when a cell has completed one round of the cell cycle, the period between the formation of a cell by division of its mother cell and the time when the cell itself divides to form two daughters. Paul quickly realised that regulation of the cell cycle was pretty much a black box, ignored by the developmental biologists of the time. Cell cycle research was the preserve of a small band of zoologists, and what was known was essentially descriptive: patient observations made over many years by staring at cells under microscopes and carefully drawing what could be seen. Because the most spectacular part of the cell cycle is mitosis, the point at which one cell splits into two, there were plenty of drawings of that, and researchers were very interested in the mechanics of how the split happened, but the rest of the cycle, where the cell just sits there looking boring, was mostly unexplored. In the late 1960s, a few biochemists had realised that the ostensibly boring bit of the cycle was, in fact, the time when the cell had to work hard to double all of its contents, preparing for the mitosis that would split these contents between two daughter cells. Some work had started to look at what was going on there, but the field was very much in its sleepy infancy with a small number of people doing mundane things.

After his uninspiring visit to Cambridge, Paul eventually settled on a PhD at the University of East Anglia (UEA) in Norwich. The Biological Sciences School at UEA had a lecturer, Tony Sims, who was just beginning a project on cell cycle changes in the enzymes involved in amino acid metabolism in the yeast Candida utilis, and this seemed to fit Paul’s criteria for fundamental cell cycle research very well. In addition to the suitability of the project, Norwich as a place was attractive to Paul, partly because his family originated from there and it was where he had been born, and partly because as a budding socialist, he was very taken by the idea of working at a new university, free from the Establishment constraints that he’d already had to fight against to even get a degree. UEA was less than 10 years old and had taken part enthusiastically in the period of student unrest sweeping through Europe in the late 1960s; the unfortunate Princess Margaret had had a blazing Union Jack thrown at her during a visit a couple of years before Paul’s arrival. Paul signed on and started work there in 1970.

The Norwich PhD was a hard slog, with very little to show for it—a “baptism of learning by failure” in Paul’s words. Tony Sims was a very good supervisor, who gave Paul a thorough grounding in the craftsmanship of experiments, but the experiments themselves were frankly tedious. Far from shining a light on how the cell cycle was regulated, Paul found himself growing up vats of yeast cells, concentrating them by centrifugation to make smelly beige pellets, and then measuring the amino acids and proteins he could extract from the pellets. He thought about other careers, perhaps studying the philosophy or sociology of science, but in the end, the camaraderie of the Sims lab, where drudgery was enlivened by the sympathy and support of his fellow investigators, carried him through. By the end of the second year in Norwich, Paul had decided to stay as a practising scientist but was starting to fret about what to do next for his postdoctoral work. He was still completely committed to working on regulation of the cell cycle, but he knew now that biochemical approaches were not likely to contribute many answers to the problem he wanted to solve.

His PhD work on amino acid metabolism, coupled to his bookworm tendencies, had led Paul into thinking a lot about metabolic pathways, and particularly the ways of controlling flux through a pathway. Metabolic pathways are the production lines of the cell, combining raw materials into more sophisticated molecules, which are then fed into the vast machinery required to maintain and drive the life of the cell. However, as for any production line, the rate of flow through the system must be controlled very carefully, in order to ensure that products are made in the right amounts, neither flooding nor starving the market, so to speak. Metabolic pathways can be regulated either at multiple points or in just a few places, depending on how they are set up, and it occurred to Paul that this sort of reasoning could be applied to cell cycle control. If the cell cycle were regulated in only a few places, then it should be possible to speed up the cycle drastically, or alternatively slow or stop it altogether, by messing with just one regulation point. To switch similes, if the cell cycle controls were like the sluice gates in a watermill, the speed at which the cell traversed the cycle, like the speed at which a mill wheel turns, could be entirely regulated by tinkering with just one item, the molecular equivalent of opening and closing a sluice. If this were true, then there should be cells that went into mitosis too early or went into mitosis late or not at all, and by finding the mutations that had caused the changes, the identity of the regulators could be established.

This theoretical daydreaming was all very well, but there was one big snag to it; much as he racked his brains, Paul was unable to think of how to approach the problem practically, how to find the mystery regulators of the cell cycle. Then, one night in 1972, staying late to do yet another boring experiment, he found the answer. It lay in a paper in the journal Proceedings of the National Academy of Sciences, written by an American called Leland Hartwell.

If Paul could be said to have worked his way down to yeast from a starting point of larger organisms, Lee Hartwell had done the opposite, coming up from the world of bacteriophages and viruses, where he had been involved in some of the earliest studies on how genes were regulated. Having decided somewhat prematurely that gene regulation was pretty well understood by the mid-1960s, Hartwell had set himself a new research problem—how cell growth was regulated. In looking for a suitable eukaryotic model in which he could apply the principles of bacterial genetics that he had learnt as a student, he was introduced to budding yeast, Saccharomyces cerevisiae, which at that time was one of the only single-celled eukaryotic organisms with easy genetics. It was possible to treat budding yeast cultures with an unpleasant chemical called nitrosoguanidine and then test the surviving yeast cells to see if their DNA had mutated, using a straightforward and quick assay, temperature sensitivity. The principle was extremely simple; mutated DNA would in some cases lead to mutated protein, and some mutant proteins cannot function properly at the wrong temperature. Such mutations can therefore be picked up by growing duplicate plates of cells, one at the right temperature and the other at the wrong, or restrictive, temperature, and then comparing the plates to detect changes or deaths at the restrictive temperature.

Using this method, Hartwell quickly isolated about a thousand mutants that were unable to grow at 36°C but were quite happy at normal room temperature, and began to categorise them based on their defects. Although some were too boring to study, he did find mutations that could be specifically attributed to defects in one of a number of cellular processes such as DNA, RNA, or protein manufacture, cell division, and cell growth. To prove the point that this genetic approach would work to identify the individual genes responsible for each mutation, Hartwell used his protein synthesis mutants to show that three were caused by specific defects in three particular proteins, and hence the genes that encoded them.

Hartwell’s entry into the cell cycle field was precipitated by one of his PhD students, Brian Reid, who noticed something very odd about some of the mutants. Budding yeast, as the name suggests, divides by growing a bud from the mother cell, with the bud eventually getting big enough to pinch off from its parent to form a new daughter. In a normal culture, all of the cells are at different points in the cell cycle, and, therefore, they all look different. However, looking down a microscope one day, Reid saw mutants that, when shifted to the restrictive temperature, all started to look the same—their buds were exactly the same size. He and Hartwell realised that they must all be stuck at the same position in the cell cycle and that, therefore, mutations affecting the cycle directly could be identified very easily, simply by looking at the cultures. Furthermore, because the size of the bud was an indicator of where exactly in the cycle the yeast was, mutants could be subclassified depending on bud size into those affecting different steps of the cycle.

Using time-lapse video microscopy, Reid, Hartwell, and a second PhD student, Joe Culotti, then went one step further. By filming mutant cultures continuously, starting at the time at which the cells were shifted to the restrictive temperature, they found that some cells stopped in the cycle almost immediately, whereas others went around another cycle before arresting at the same point. This meant that mutations could act at one particular point in the cycle and that if cells happened to have got past that point before the temperature shift, they would continue until they ran up against the mutation point in the next cycle. Careful tracking of the cells able to do another round of cycling also threw up another interesting observation—mutations did not necessarily act at the point where the cells arrested in cycle but could exert their effects much earlier on.

It was Hartwell, Culotti, and Reid’s paper describing this work that Paul fell upon during his nocturnal trip to the UEA library, and to someone searching for a way to get a grip on an intractable problem, it was an astonishing moment: As Paul says, “It completely blew my head off.” The more Paul discovered about Hartwell’s work, the more he became convinced that it was the simplest, most direct way to get to the heart of what regulated the cell cycle. The mutants would lead straight to the genes of most importance, and then identifying the genes and working out what they did would put the framework in place to solve the whole problem. Genetics, not biochemistry, was clearly the way to go. Fired with evangelical zeal, Paul began working out the steps that would enable him to follow Hartwell into the maze.

To do a postdoc studying cell cycle regulation in yeast, Paul was going to need several things. He knew something about yeast already, so that was a start, but he knew nothing about genetics, and he also had to find a postdoctoral supervisor who would allow him to work unimpeded on the project, without trying to foist their own interests on him. Paul briefly considered applying to Hartwell’s lab, but he and his wife Anne had no wish to go to the United States, and Anne, who had recently finished teacher training, was keen to stay in Britain and start work. This threw up a huge problem; the main person working on the cell cycle in yeast in the United Kingdom at that time was Murdoch Mitchison in Edinburgh, but he had no expertise in genetics and additionally worked, not on budding yeast, but on a very distantly related cousin, Schizosaccharomyces pombe, fission yeast. Undaunted, Paul wrote to him and went up on a bright, snowy winter’s day to Edinburgh for an interview.

Murdoch Mitchison, part of the “third of a ton of Biology Professors” born to the writer, poet, and activist Naomi Mitchison, and older brother of Av, David Lane’s mentor, was very definitely interested in cell division, having recently published an extremely influential book, The Biology of the Cell Cycle. Mitchison had shifted into the cell cycle field in the 1950s, after earlier work on sea urchins and red blood cell membranes, and had realised early on that fission yeast was a great model, perhaps better than budding yeast, because to divide, it simply got longer and longer until it split in two. This meant that position in the cell cycle could be measured by length, rather than the more subjective bud size. The fission yeast cell cycle also looked a lot more “mammalian” than that of budding yeast, because the timing of each part of its cycle was similar to that of higher eukaryotes, a fact that fueled Paul’s growing enthusiasm for his potential new laboratory workhorse.

Mitchison had thought a great deal in biochemical terms about how the cell cycle might be regulated, and The Biology of the Cell Cycle, although a dry and dusty read, was the first clearly to lay out two new and important concepts. First was the relationship between the cell cycle and cell growth, the idea that because cells can only divide if they are big enough, they must therefore have a way of sensing size and tying that into cell cycle control. Second was the recognition of the causal dependency of events in the cell cycle, that one event had to happen in order that another, subsequent one could occur. Furthermore, Mitchison proposed that the time it took for a cell to complete the different steps in the cycle could be determined by these dependencies, and also by external, master timing mechanisms. This idea was a forerunner of more advanced theories of checkpoint control, which underpin our modern understanding of the cell cycle.

Paul, accustomed as he was to thinking about cell cycle control in splendid intellectual isolation, recognised a kindred spirit, who clearly had no regard for other people’s opinions, but simply wanted to write a book about something in which he was really interested. His trip to Edinburgh confirmed his suspicions. Mitchison happily spent an entire day with him talking about what Paul might do as a postdoc and, furthermore, acknowledging his own ignorance of genetics, suggested that in order to get to where he needed to be, Paul should spend a few months in Bern learning some tricks of the trade with Urs Leupold, the father of fission yeast genetics. Finally, Paul had found a decent system, a decent problem, a logical way of thinking about it, and a great place to work. He and Anne left Norwich in 1973, bound for Bern and then Edinburgh.

In Bern, Urs Leupold, a brilliant but eccentric geneticist, spent hours with Paul to teach him the rudiments of genetic analysis, although Paul remembers some of his wilder ideas as quite “barkingly mad.” Paul took to the abstract, highly theoretical subject material like a duck to water; his great strength had always been that he was almost pathologically orderly in his thought processes, and the rigorous logic of theoretical genetics matched his mind in a very satisfactory way. As well as the long hours with Leupold, Paul began to work with the lab’s fission yeast strains and set up his first temperature-sensitive screens, looking on the replica plates grown at the restrictive temperature for cells that were getting too long because they couldn’t complete the cell cycle and split into two. By the time he moved back to Edinburgh, and in the months following, he had isolated about 30 different cell division cycle (cdc) mutants. The Mitchison lab’s expertise in physiological studies of the cell cycle meant that he could categorise the cdc mutants on the basis of where they were blocked, just as Hartwell’s lab had done with budding yeast, and Paul found mutants blocked for DNA synthesis, mitosis, and cell division, aided in subsequent work by Kim Nasmyth, then a new and “frighteningly bright” graduate student in the Mitchison lab.

Despite his being the genetic cuckoo in a very biochemical nest, Edinburgh as a workplace was all that Paul had hoped for. Mitchison gave Paul complete freedom to do what he liked and was interested enough in Paul’s new approach to the cell cycle to talk to him endlessly. The lab was small, but Paul’s colleagues were smart and committed, and above all, the science there was always led by Mitchison’s belief that passionate interest in a subject is far more important than whether it is fashionable or not. In this very congenial environment, Paul began to lay the foundations for all of his subsequent work on the cell cycle. His first big intellectual breakthrough, however, was not the product of the theorizing of a finely honed mind, but a simple piece of serendipity brought on by a desire to cut some experimental corners.

The temperature-sensitive screens that Paul had been performing were proving to be very fruitful, but searching through thousands of colonies on agar plates looking for the small number that might have mutated was unexciting and long-winded. In a bid to speed matters up, Paul decided that a better approach might be to mutate the cells, grow them up at the restrictive temperature, and then separate them on the basis of their size; the mutant cells stuck in cycle would be much larger, and they should be easy to separate by spinning through a lactose gradient in a centrifuge because the largest cells would all collect at the bottom of the gradient. The big cells could then be recovered by growing on agar at a normal temperature, and then tested by temperature shift, as normal. In fact, the idea was a complete failure for what Paul wanted, because most of the mutant cells didn’t recover, and the normal cells swelled up too as a result of the stresses they were under. However, whilst fruitlessly looking for extra-long cells extracted from the bottom slice of the gradient, Paul noticed to his surprise that there were some strange-looking, small, round cells that had made it to the bottom slice because they had clumped into a ball, which to a centrifuge looks just the same as a big cell. He was about to throw the plate containing the tiny cells away but suddenly stopped. If cells that were too long were caused by a block in the cell cycle, then surely, cells that were too small might be caused by a cell cycle that ran too fast, dividing before the cells had grown enough? Long cells, he realised, were not the key to finding the rate-limiting control steps in the cell cycle, because any event necessary for the cell cycle would become rate-limiting if it were inhibited. However, if there were a mutant that speeded up an event rather than inhibited it, such a mutant would be in a bona fide rate-limiting gene, because speeding up a normal rate-limiting step would push the cells to cycle faster. It was the difference between getting a puncture in a bike tyre (necessary), which would cause a journey to be slowed, and pedaling faster (rate-limiting) to arrive earlier.

Although Paul was right, and the wee mutants (christened in acknowledgement of their Scottish origins) played a vital part in finding the key regulatory molecules of the cell cycle, his sudden flash of intuition did not get the reception he’d hoped for: “I was so excited by this, so excited! I went and showed people, but nobody quite got it. It was so frustrating, because I couldn’t understand why they just didn’t see that it was important. In fact, some people thought it was budding yeast, that I’d contaminated the culture, which I knew I hadn’t. It did make me realise that you do have to be very open-minded, see what you get and capture it.”

Paul’s 1975 Nature paper on the wee mutant phenotype, “Genetic Control of Cell Size at Cell Division in Yeast,” saw his arrival on the yeast cell cycle scene, and during the next few years in Edinburgh, he published another 15 papers characterising in detail the stable of cell cycle mutants that he had built up. At first, his work ploughed a very similar furrow to Hartwell’s, and Paul worried that he would always be running to catch up the budding yeast cell cycle community, which was much larger than the small band of fission yeast enthusiasts. However, Hartwell’s work ran into a slow patch, and without his input, budding yeast cell cycle work stalled for a few years, allowing the fission yeast community to draw level.

The cell cycle is split into four phases: G1, S, G2, and M. S phase is the time during which DNA is duplicated; M phase is mitosis, when the duplicated DNA is split and the cell divides into two; and G1 and G2 are the gaps on either side of S phase. The transitions between G1 and S phase and G2 and M phase are key regulatory points in the cell cycle, where go/no go decisions are made regarding DNA synthesis and cell division. Paul’s work in Edinburgh, done in collaboration with Peter Fantes, Kim Nasmyth, Pierre Thuriaux and others in the Mitchison lab, focused mainly on the G2/M transition, which is the preeminent control point in fission yeast. By the late 1970s, they had shown that all of the wee mutations Paul had isolated were causing changes in just two genes, called wee1 and cdc2, and that these two genes were rate-limiting for the G2/M transition, somehow telling the cell cycle that the cell was big enough to divide into two without stinting on the genetic and biochemical dowry of either daughter cell. Interestingly, the cdc2 gene had first been identified as a mutant in the elongated cell screen, and Paul and Pierre Thuriaux proposed in 1980 that cdc2 could be mutated either so that it lost its function, in which case, mitosis was blocked and cells elongated, or so that it became more active, in which case, cells divided too early and were too small. They further suggested that cdc2 and wee1 were working together in a network to regulate the G2/M transition and hence the onset of mitosis.

Although G2/M was the point of interest in the cell cycle for fission yeast biologists, this was not the case for their budding yeast colleagues. Budding yeast barely has a G2 phase, moving almost immediately from S phase into M phase, and the major control point is at the G1/S transition, christened “Start” by Hartwell. Start also had a counterpart in animal cells; in 1974, Art Pardee had proposed what he called the “restriction point” in the mammalian cell cycle. This was the point at which animal cells made a decision to divide or not based on the supply of nutrients, and it occurred at the same time as Start: at the G1/S transition.

The buzz going round about G1/S and Start meant that there was not a lot of interest in G2/M control, and Paul, by now looking for a lectureship somewhere as a prelude to leaving Edinburgh, made a pragmatic decision to do a little bit of opportunistic work on the G1/S transition in fission yeast, in order to look more attractive to prospective employers. He and Yvonne Bissett, a technician in the Mitchison lab, set up a quick experiment to see whether any of their temperature-sensitive cdc mutants had anything to do with Start. The assay was simple, based on a normal lifestyle decision made by yeast cells, which divide happily in conditions of optimal nutrition, but stop dividing and mate (conjugate) when they detect problems with food supplies. The point at which cells make the decision to divide or to conjugate is Start, and once a cell has passed Start and is committed to divide, it cannot conjugate. Therefore, at the restrictive temperature, if a cdc mutant were needed for Start, cells would arrest in G1, would not be able to commit to entering S phase, but would still be able to conjugate. If the cdc mutant were irrelevant to Start, cells would arrest at some other point in the cycle and no conjugation would occur. The readout of the assay was to select for cells that could conjugate, which Paul and Yvonne did by rigging the medium on the agar plates they used such that only conjugated cells would stay alive.

The experiment was set up, and Paul chose as a negative control a cdc2 temperature-sensitive mutant—because cdc2 was a G2/M regulator, cells should arrest in G2 and would never conjugate. However, a gremlin seemed to have sneaked into the Mitchison lab; to Paul’s intense frustration, the seemingly simple control just would not work. Every time he and Yvonne ran the experiment, the cdc2 control plates always had a few surviving, conjugated colonies and were therefore very unsatisfactory controls, meaning that the rest of the data from the experiment could not be trusted. Paul tried two different cdc2 mutants and repeated the experiment time and time again, but always got the same result. What on earth was going on? As Paul says: “I thought and thought and thought. Of course I assumed I was stuffing it up. All the usual things—I thought the temperature wasn’t right—you go back to the waterbath with the thermometer. And then it came to me that it had a double block point.”

The “double block point” got the paper into Nature. What Paul had realised was that cdc2 might be not only the rate-limiting regulator for G2/M, but also the key to Start control at G1/S. Viewed in this light, the data made perfect sense; when shifted to the restrictive temperature, cdc2 mutant cells could either arrest in G2, in which case they’d be unable to undergo conjugation because they were in the wrong bit of the cell cycle; or just before Start, in G1, where they could conjugate with ease. This would appear as a dribble of surviving colonies at the end of the assay, just as Paul and Yvonne had seen.

Paul again: “That paper is one of my favourites because to get to that conclusion was not intuitive—it wasn’t how people were thinking about it; it wasn’t how I was thinking about it. To make the interpretation, to say, ‘Well, I can test that if I do this, but the chances of this working are zero.’ To do that, and then to get the result.… I don’t talk about it so much these days but it’s one of the three or four things I’m most pleased with.”

The Nature paper, “Gene Required in G1 for Commitment to Cell Cycle and in G2 for Control of Mitosis in Fission Yeast,” was published in August 1981, by which time Paul had moved on from Edinburgh, to a three-year position at the University of Sussex in Brighton. Despite his attempts to up his trendiness factor, he had been unable to get a lectureship anywhere and had had to settle for a short-term fellowship. Although not very secure in terms of job prospects, the location of Paul’s new lab was in one way ideal; the School of Biological Sciences at Sussex had expertise in what he was planning next—molecular biology.

Up until now, all of Paul’s work with fission yeast had involved the isolation and characterization of mutants that were assigned gene names but remained theoretical entities. The genes existed only on genetic maps, and the only way of taking the next step to find out what they actually did would be to switch over to exploit molecular biology techniques. DNA could quite easily be extracted from eukaryotic cells and manipulated in the lab by the end of the 1970s, and thanks to a paper in 1973 by Frank Graham and Alex van der Eb, a method existed for putting DNA, and hence eukaryotic genes, back into animal cells so that their function could be studied in the proper context. It took until 1978 for Gerry Fink and colleagues in the United States, and Jean Beggs in the United Kingdom to describe the same technique, called transformation, for budding yeast, but as soon as he read their papers, Paul realised that the writing was on the wall for fission yeast as a model organism; if there was no analogous transformation procedure, fission yeast biology would die out.

Not everyone was convinced of the potential of molecular biology. Distaste for molecular biology and its purveyors was quite common amongst the more intellectually fastidious geneticists, who viewed it as a rather grubby, menial discipline, where one could get so caught up in the minutiae of getting tricky new methodologies to work that there was no time to think about more important concerns. To some extent, they had a point, because biological problems had a tendency to be parked while techniques were honed to perfection, but those geneticists willing to engage with molecular biology reaped a large reward in terms of data.

The divide is well illustrated in a Nature News and Views article that Paul wrote in 1980, at the end of his time in Edinburgh, entitled, “Cell Cycle Control—Both Deterministic and Probabilistic?” The article marks a transition from a theoretical to a real universe in cell cycle theory and points out to the theoreticians that although their work had laid down the important concepts underpinning cell cycle research, it was time to get their hands dirty and start figuring out what was really going on. It was almost a description of Paul’s own journey from theory to practice:

I had all the thinking that those guys had, and all the theory stuff, I was comfortable with that, but I was also very practical. And that was really helpful, because most people who came after that had no idea of the earlier stuff—it sunk without trace. But it was very important for me to make the right research decisions, so it actually influenced me very positively, not because I took it seriously, because I didn’t, but because it made me think about the research problems and the issues round them much, much more thoroughly than I would have done otherwise. I owe a lot to it.

Paul had already decided before he left Edinburgh that he was going to concentrate all of his efforts on finding what cdc2 was doing because something with a crucial role at the two major control points of the cell cycle had to be important. However, once in Sussex, he stopped publishing papers on the cell cycle for a bit and threw all of his meagre resources into the task of getting molecular biology going in fission yeast. Somewhat dramatically, he gave himself a one-year deadline: if at the end of the year he had got nowhere, he would throw in the towel and join the budding yeast community.

There were two aspects to the problem: firstly, the transformation protocol itself, and secondly, getting DNA into a form that the fission yeast transcription machinery would be able to recognise and transcribe into protein. Paul was soon joined by David Beach, an escapee from a nearby lab, and the two of them split the work by category, Paul working on the problem of softening up the yeast cells so that they were ready to take up foreign DNA, and David trying to adapt the plasmid vectors that worked in budding yeast to make them suitable for fission yeast. The two got on well together because Beach was very effective and had a lot of experience of molecular genetics already. Vectors started to appear for testing, but Paul’s end of the experiment was not going so well. He had got his technician to make up a set of solutions according to Jean Beggs’s protocol for budding yeast, and very unexpectedly, they seemed to work very well for transforming fission yeast too. This was wonderful news, and Paul took the technique with him on a visit to another lab, eager to spread the word. Somewhat embarrassingly, however, when he tried to repeat his success, he couldn’t get a single transformed colony and returned home to Brighton with his tail between his legs. In Brighton, transformation continued, mysteriously, to work. For a time it seemed as though there might be a geographical restriction on fission yeast molecular biology, until Paul realised that the crucial solution in the protocol had been made up incorrectly, with one ingredient, sorbitol, missing. Sorbitol turns out to inhibit transformation in fission yeast, so by complete chance, Paul had hit on exactly the right modification to Beggs’s recipe. As an example of fortune favouring the slightly incompetent, this story can hardly be bettered, because by honest labour alone, it would almost certainly have taken a really long time to get to the same place.

Having saved himself from the dreadful fate of becoming a budding yeast person, Paul could now get to grips with the problem of cloning fission yeast cdc genes, with the highest priority being cdc2, the dual regulator of Start and the G2/M transition. He, Beach, and Barbara Durkacz, a new postdoc in the lab, decided to use a method published in 1980 by Kim Nasmyth, who had turned to the dark side following his PhD with Murdoch Mitchison and was now working on budding yeast as a postdoc in Ben Hall’s lab in Seattle.

Nasmyth and Steve Reed, a postdoc with Lee Hartwell, had got together to clone CDC28, the key regulator of Start in budding yeast. Their method, which they called complementation cloning, relied on the ability of a normal CDC28 gene to rescue, or complement, a yeast strain carrying a temperature-sensitive mutant of CDC28. Reed and Nasmyth reasoned that normal CDC28, although unknown, would be found in a library containing the whole of the budding yeast genome, which they had made by cutting yeast DNA with restriction enzymes and cloning all of the fragments into a plasmid vector. If this library were used to transform a CDC28 temperature-sensitive strain, the plasmid encoding CDC28 would be detectable because any colonies carrying it would have a normal cell cycle again and could be picked out by eye from the background of weird-looking cell cycle mutants. This turned out to work very well, and, fortunately, it was a simple matter to adapt the procedure for fission yeast.

Back in Sussex, using a fission yeast genomic library, a plasmid carrying cdc2 was identified by complementation cloning, but to make the paper a bit cuter, Paul and his colleagues decided to see whether they could redo the experiment, but this time trying to complement mutant cdc2 using a library from budding yeast. In other words, did cdc2 have a budding yeast homologue, able to have the same effect on the cell cycle? A budding yeast library was duly screened, and sequences were pulled out that could, indeed, complement the fission yeast cdc2 mutation. This was a great result because budding yeast and fission yeast are only very distantly related in evolutionary time, having diverged maybe 400 million years ago; finding a gene that worked in both species was pretty amazing. But what was the gene? Because cdc2 is important at Start, it seemed a good idea to obtain plasmids carrying Start regulatory genes from Steve Reed and test them out individually in the complementation assay. Most surprisingly, the one that worked was Nasmyth and Reed’s original CDC28 plasmid: cdc2 and CDC28 were functionally homologous, functionally the same.

The news that CDC28, the budding yeast camp’s favourite Start gene, was the same as a gene thought predominantly to regulate G2/M in fission yeast sparked some disbelief to begin with, but the arguments subsided quickly once the truth dawned that both were required in both places. The genetic methods that Lee Hartwell and Paul had originally used to find CDC28 and cdc2 had been set up to detect where the genes were most important under conditions of optimum nutrition and rapid cell growth, and the differing lifestyles of the two yeasts meant that in budding yeast, CDC28 mutants arrested growing cells in G1, and in fission yeast, cdc2 mutants caused a G2 block. Two partial views of cell cycle regulation had merged to create a much clearer picture, thanks to molecular genetics.

Beach, Durkacz, and Nurse published their work in the Christmas 1982 issue of Nature, and in the final paragraph, they made a very prescient remark: if two yeasts separated by nearly half a billion years of evolution were using the same mechanism for regulating Start, might it not be possible that the mechanism was so evolutionarily ancient, so entrenched in a cell’s life cycle, that control of the analogous Restriction Point in mammalian cells might involve a functional equivalent of the cdc2 and CDC28 gene products? In that single sentence lay the seeds of a future Nobel Prize.

Getting fission yeast molecular genetics going had been a real coup for Paul and his small lab, and his rapid reemergence in the pages of Nature following his voluntary publishing shortfall should have been a good indicator to the scientific hierarchy that here was a future star in the academic firmament. Paul was enthusiastic, incredibly bright, charismatic, and working on a really important problem, and he should have walked into a job. But again, just as in Edinburgh, he went for many interviews but always came in as the second or third choice. In a profession that should be a meritocracy, he was hampered by the nonscientific prejudices of the hiring committees he faced. He had never worked in the secular cathedrals of genetics or molecular biology, did not have an Oxbridge degree, and did not have sufficiently influential mentors to drop a good word in the right ear. Furthermore, he was not doing the right kind of work, perched as he was on the fence between genetics and molecular biology at a time before the combined weight of fellow converts caused the fence to collapse. In short, he was a risk: he might be as scientifically gifted as he appeared, but he didn’t have a thoroughbred lineage, and nobody was prepared to commit themselves.

By 1983, Paul had just one offer, at the European Molecular Biology Laboratory (EMBL) in Heidelberg, but was reluctant to simultaneously ruin his wife’s teaching career and uproot her and their two young daughters. Fortunately, he was saved from making the decision. Walter Bodmer, Director of the ICRF, whose eye for scientific talent was in those days unmatched, had noticed that the young upstart in Sussex was lively, ambitious, and scientifically self-confident, and furthermore, was working on a problem, cell cycle control, that lay at the heart of cancer research. The fact that Paul was working on it in yeast was actually a plus, because the human cell cycle research community had all but stalled, and a new approach seemed a good idea. Despite the fact that the ICRF interview committee was less convinced, suggesting to Paul that in addition to his own research, he might also like to run a service facility helping other labs make proteins in fission yeast, Bodmer offered Paul a permanent tenured post, finally giving him the job security he needed.

In 1984, Paul began work in Lincoln’s Inn Fields, only slightly worried by hearing an interview with Bodmer on Radio 4 the morning before his first day, in which Bodmer suggested that model systems—flies, worms, frogs, and yeast—might have had their day because so much could now be done in mice and humans. Paul had brought with him the nucleus of an excellent lab, comprising two PhD students, Jacky Hayles and Tony Carr, and two postdocs, Paul Russell and Steve Aves, supplemented with a new technician, Jane Sandall. His leaving Brighton came as a blow for the ladies of the Brighton ICRF charity clothing shop, who were very sad to be losing one of their best customers, but they cheered themselves with the thought that at least they would now be raising money for his work.

The Nurse family with Paul Russell (at left), ca. 1984.

(Photograph courtesy of Anne Nurse.)

At ICRF, the reaction to the newcomers was not entirely positive. Because Paul was the only person working on a nonanimal system in the building and yeast was the most common contaminant of mammalian tissue culture cells, he and his lab were regarded by some as tissue culture poison, shedding spores wherever they walked. There was also disbelief that fission yeast, an organism at least a billion years away from humans, could have any relevance to cancer, something that Paul felt keenly; a Nature News and Views he wrote at the time, entitled “Yeast Aids Cancer Research,” is a riposte to the doubters, of which there were many, and not just at ICRF. However, Paul is nothing if not stubborn, and he was not about to abandon his long- and passionately held belief that understanding the cell cycle in a simple model would lead to an understanding of it in higher organisms. He just had to provide the evidence, and the time was ripe to do just that; with Paul’s own grasp of genetics and molecular biology now supplemented by postdocs and graduate students with expertise in biochemistry and cell biology, the lab was in a fantastic position to capitalise on the long years that Paul had spent characterising mutants, setting up molecular biology, and generally turning fission yeast into a great model organism.

The Paul Nurse of that time is remembered very fondly by his lab. Small, bouncy, and cuddly, with his 1970s-era droopy moustache still firmly in place, he had the energy of a whirlwind and enough charisma to motivate his lab into working hard merely to please him. He juggled the sometimes clashing personalities of the highly ambitious people who had gravitated to him with great skill, at the same time managing to create an atmosphere in which even the newest, lowliest recruit felt able to take part in scientific discussions without risk of humiliation. Sergio Moreno, a Spanish postdoc who arrived on a three-month contract in mid-1986 and stayed for seven years, puts it down to Paul’s talent for self-deprecation: “He has this special gift that he behaves in a silly way and then everybody else can do the same—you don’t feel bad if you ask something stupid. I think this is very British—in Europe we tend to be more serious!” The group went on regular outings, and they roughed it together in an assortment of grungy youth hostels, where science was fitted in around bracing walks in the rain and complaints about the bad beds and chores. Above all, it was a time of great intellectual intensity and anticipation, of knowing that what was going on in the lab was important.

Paul Nurse and glider, ca. 1985.

(Photograph courtesy of Anne Nurse.)

Iain Hagan, a PhD student with Paul from 1985 onwards, remembers the Nurse lab meetings with particular clarity: “The lab meetings in his group are still one of the highlights of my scientific career. They were amazing—just really, really exciting. Paul wouldn’t generally be dominant. He would be letting people discuss things but gently nudging the debate in the right direction.” In addition to these scheduled meetings, held for a time in the White Horse pub round the back of ICRF, the lab talked science all the time, chewing problems over for hours in the lab, in the canteen, in the sundry other pubs around Lincoln’s Inn, and quite frequently on the number 134 bus from Archway, on which Paul, Sergio, and Jacky came to work.

Driving all of these intense discussions about cell cycle theory, fission yeast lore, and technical troubleshooting was the day-to-day work of the lab, and here Paul’s mania for order and tidiness ruled. His own assessment of this is that he is “quite well organised in a shambolic sort of way,” but others are more illuminating. Sergio again:

He’s very organised. He can give the impression of being disorganised, but in fact he’s someone who is very tidy—have you seen his writing? It’s perfect—he’s got beautiful writing.

Everything in the lab was perfectly organised. Every six months, he would ask the technician of the time to find a date, and on that date everybody in the lab, including himself, would wear a lab coat (probably the only time we would wear lab coats!) and then we would clean the lab.

He also likes people who are very tidy and experimentally skilled. He really paid attention to how effective and tidy you were in your experiments, in addition to the intellectual part. Some people weren’t as effective as he wanted them to be, and they had to be really smart to compensate for it.

And then, there was Paul’s legendary appetite for data, starting with his eagerness for more of it getting in the way of laboratory good manners. Tony Carr remembers that after one key experiment, “I came in in the morning and he’d already been through all the plates, decoded them from my lab books and worked out what the result was. After that I used to hide my lab books on the top shelf where he couldn’t reach them.” Jacky Hayles, still working with Paul 30 years on, now as joint head of his lab at the London Research Institute, talks about his attention to detail and his ability to see things in experiments that no one else had noticed, although “he can be very irritating when you see it yourself and you want to tell him, but he wants to tell you first.”

The next few years of the Nurse lab read like a Greatest Hits album for cell cycle research. Paul, despite his brief flirtation with G1/S and Start, was still focussed on G2/M control and what cdc2 was doing to regulate it, and answers were now coming thick and fast. Viesturs Simanis, a postdoc who arrived in 1985 from David Lane’s lab at Imperial College equipped with the ability to get almost any experiment, however difficult, to work, showed that the cdc2 gene encoded a protein kinase, able to put phosphate groups on other proteins and thereby regulate their activity, and Sergio Moreno went on to show that the kinase activity varied during the cell cycle and peaked just before mitosis, as might be expected for a rate-limiting regulator of G2/M.

Paul Russell, who had migrated up to London with Paul from Brighton, worked out how the variation in activity occurred by showing that wee1, the mutant that Paul had found by accident all those years ago in Edinburgh, was a negative regulator of cdc2, and that another cell cycle mutant, cdc25, was a positive regulator. Russell had come to Paul’s lab from Seattle thanks to a recommendation from Kim Nasmyth, was very focused, and worked fantastically hard, despite having an onerous commute, because he was still living down in Brighton. Tony Carr, another London–Brighton commuter, recalls competing with him for the coffee-room floor on the nights when neither could make it back home on the last train, although Paul did better than Tony, having equipped himself with a blow-up mattress for sleepovers at the lab.

Russell and Nurse’s two Cell papers on cdc25 and wee1 in 1986 and 1987, and Simanis and Nurse’s on cdc2 in 1986, together with the constellation of papers surrounding them, were the vivid proofs of the theories that Paul had formulated back in Norwich as a PhD student. In the intervening years, Paul, with the help of his colleagues, had worked out how to find rate-limiting steps in the cell cycle, had gone out and isolated mutants in those steps, had taught a whole field how to do molecular genetics, and now knew the DNA sequences of the mutants and could see exactly how they worked together. The whole saga was an amazing tour de force, especially given the stunning lack of interest shown by the rest of the scientific world. cdc2, the master kinase that was responsible for flipping the on/off switch for the G2/M transition, was itself decorated with phosphate groups (phosphorylated) by the wee1 proteins, also kinases, and this phosphate decoration inactivated it. When cdc2 needed to be switched on, cdc25, which encoded a phosphatase (a protein able to remove phosphate groups), undid wee1’s work, and cdc2 protein became active. It was beautifully simple. But did it matter anywhere other than yeast? Paul, pretty much alone in the field as usual, thought that it did.

Paul’s conviction that cdc2 would be present in other species besides yeast had been bubbling under for some time, because he knew that entry into mitosis from G2 was regulated just as tightly in higher eukaryotes as it was in fission yeast. In 1971, Yoshio Masui, working on frog oocytes, had discovered the existence of a mysterious activity, which he called Maturation Promoting Factor, or MPF. Frog oocytes arrest naturally in G2 before fertilisation but can be forced to mature and go through mitosis by injection of MPF, contained in an extract made from mature egg cytoplasm. MPF activity turned out to be present in all of the higher eukaryotic cell types, including mammalian, that could be tested, and to be fundamentally important; it was a rate-limiting G2/M regulator just like cdc2, but its true identity was still unknown by the early 1980s, despite strenuous attempts to purify it from the cytoplasmic soup in which it hid.

While he was in Sussex, Paul had started a collaboration with Chris Ford, a frog person there, to see whether injection of cdc2 into oocytes could induce maturation, but despite some tantalising hints that something might be going on, the data were too inconsistent to be convincing, and the experiment had been abandoned. cdc2 might well have something to do with MPF, but clearly, another way had to be found to test the theory.

In 1985, Paul hired a new postdoc from Jean Beggs’s lab at Imperial College. Melanie Lee was looking for a second postdoc, and knowing that Viesturs Simanis, an old friend from Imperial, was having a great time in the Nurse lab, decided to apply there herself. The application process started in a pub near ICRF, where Melanie discovered Paul, “scruffy, little and very vibrant,” having a drink with a vision of male pulchritude “all in white, tall and Adonis-like,” who turned out to be Kim Nasmyth. Paul, much to her astonishment, said yes to Melanie almost immediately, and she started work shortly afterwards. Her first day in the lab featured a meeting with the boss to discuss possible projects, and she remembers Paul presenting her with two options: “He said, ‘You can do one of two projects. You can work on cdc10, which is fairly ordinary, or you can work on a project that’s high risk but justifies my presence in a cancer institute; that is, you clone human cdc2.’” Melanie, without hesitation, went for cdc2.

Melanie Lee and Freeway, 1987.

(Photograph courtesy of Melanie Lee.)

Paul had tried to sell the human cdc2 idea to other new lab entrants but had got no takers, because of the high likelihood that it would be a total bust. Of course, by Paul’s lights, this made it a fine project: “If I wasn’t doing things where I thought there was a reasonable chance of failure, I wouldn’t think we were doing anything important. I begin to realise I’m a bit odd in that way.” Spending years looking for a protein that might exist only in the mind of their boss was not a high priority for anyone hoping to get a good job on the back of their postdoc work. Besides, there was so much else to be done that it was easy to pick less-risky winners; other projects might require elegant genetics and tricky biochemistry, but as long as you were good at the bench and worked hard, the payoffs were almost guaranteed.

Melanie, however, was a bit different. This was her second postdoc, so she wanted to do something startlingly good. More importantly, she was a risk taker, just like her new boss, and the thought of doing something quite so wacky was exciting; if it was really possible that cdc2 had jumped the billion years or so of evolution dividing humans from fission yeast, she wanted to be the person to find out.

There was another factor too, that of her relative inexperience in the field. Unlike the rest of the lab, she came from a non-fission-yeast, non-cell-cycle background, and she lacked the knowledge to dispute Paul’s judgement that the project had a chance. As Paul says: “Melanie was the only one who said she’d have a go at it, because I said in my view this was the most interesting project in the lab. She was receptive to my advice, which was useful for a project like hers. I was suggesting she did quite bold things and she was prepared to trust me. I don’t think the others would have necessarily done that.… She was also extremely capable and stable, and really efficient and effective, which was necessary for this project.”

The human cdc2 project illustrates very well the hard slog and serial failures that accompany most scientific ventures. After many months of painfully slow nonprogress, it became very obvious to Melanie why Paul had emphasised the difficulty of the project and why nobody else had wanted to take it on. Very simply, there appeared to be no good way of even looking for a human cdc2 homologue by conventional methods, let alone finding something.

When searching for relatives of known proteins, there were at that time two standard ways to proceed: look for similarities at the DNA level and find the gene encoding the protein, or search for similarities at the protein level and then work back to the gene. Both methods were molecular fishing expeditions, in Melanie’s case using fission yeast baits dipped into enormous pools of human genes or proteins. To search by DNA homology, Melanie probed a human gene library with an antisense version of the fission yeast cdc2 gene sequence, hoping that the fission yeast antisense DNA would be able to pick out its human sense counterpart. To look for protein homology, she used an antibody able to recognise fission yeast cdc2, this time fishing in a human protein library, hoping that the antibody would recognise some shared structural component enabling it to hook out human cdc2.

The workload involved in spreading the huge libraries on to hundreds of soup-bowl-sized agar plates, probing them, and then processing the results was enormous, and after a few months, Paul gave Melanie a technician, Martin Goss. However, despite receiving a great deal of help from Viesturs Simanis, who had made the anti-cdc2 antibodies and was a whiz with the type of hybridisation experiments that Melanie and Martin had to do, they got precisely nowhere. Either the baits pulled out nothing, or under less stringent conditions, they pulled out junk. Too much evolutionary time had elapsed between fission yeast and humans, and if there was indeed a human cdc2 gene, it was untouched by the molecular overtures from its distant relative.

Matters came to a head at a group meeting in the summer of 1986, about nine months after Melanie had started, when as usual, she had to present yet another litany of failure to the assembled lab. It was obvious that pursuing her current strategy was pointless, but what else was there? The only other method of finding homology was by functionality, as Beach, Nurse, and Durkacz had done when they had discovered that cdc2 and CDC28 were doing the same thing in fission and budding yeast, but how on earth could one do that between yeast and human? Leaving aside the sheer unlikeliness of a human gene being close enough in function to be able to rescue a fission yeast mutant, there was no way of doing the experiment, unless there was a human protein library that would work in fission yeast, which, surely, there wasn’t.

And then someone—Tony Carr, Viesturs Simanis, nobody can quite remember who—realised that there was. It was probably only the Nurse lab that had the combined knowledge and audacity to contemplate it, but there was a library that might, just might, work. It had been made by Hiroto Okayama in Paul Berg’s lab in Stanford, California, and funnily enough, Melanie had already been using it for her fruitless fishing experiments. The Okayama and Berg library contained pretty much every gene in the human genome cloned into a plasmid vector able to grow in Escherichia coli bacteria, just like many standard libraries from that time. However, the neat factor about it was that Okayama had worked out how to get the library to switch on, or express, all of its proteins in mammalian cells as well as E. coli, by topping and tailing the gene sequences with control elements that the fussy transcriptional machinery of mammalian cells could recognise and use.

The reason that nobody had thought of using the Okayama and Berg library for a complementation experiment in fission yeast before was that just as mammalian cells are very picky about their transcriptional control elements, so are some yeasts. Budding yeast was well known only to express proteins using its native control elements, and everyone had assumed that fission yeast was equally xenophobic. However, Paul’s lab had recently been tinkering with the particular control element, called the SV40 early promoter, that Okayama had used to drive his library genes, and they had found to their surprise that it worked quite happily in fission yeast, which turned out to be far less fussy than its budding yeast cousin. There was a slim chance that the Okayama and Berg library could be coaxed into expressing human proteins in fission yeast cells.

Even if the library could be put into fission yeast, many further obstacles loomed, but as the lab discussed the idea with a mounting sense of excitement, the realisation flew around the room that although it would be bold to try it, it was not totally foolhardy. One by one, the requirements for getting the experiment on the road fell into place. There were two main issues. First was the question of what strain of yeast the library should be put into. Paul and Jacky had that one nailed instantly, because they knew that they had a cdc2 temperature-sensitive mutant strain, cdc2-33 leu1-32, which was totally watertight, stopping absolutely dead at the restrictive temperature. If the library went into that and any colonies grew at the higher temperature, then it had to be caused by an incoming gene rescuing the defective cdc2. Next was how to tell whether the library had made it into the yeast cells at all—the transformation procedure had to be maximally efficient to make sure that every human gene possible was represented. The way round that one was to use the Okayama and Berg plasmids to piggyback a second plasmid carrying a selectable marker, LEU2, into the cells. If the transformed cells were grown in medium lacking leucine, only those carrying the LEU2 plasmid would survive, because the cdc2 mutant strain that Paul and Jacky had suggested using had been modified so that it could not synthesise leucine on its own. The bare bones of the experiment were there: transform the library into cdc2-33 leu1-32 cells, along with the LEU2 plasmid, and plate at the permissive temperature in the absence of leucine; after a day, when any transformed cells would have had a chance to recover and start growing, shift to the restrictive temperature, and look for any colonies that could grow normally. Easy.

Nobody thought that it would work. Peter Goodfellow, whose lab was next door, came by Melanie’s bench almost every day, and invariably said, “stupid experiment—it’ll never work.” Even Paul was a bit dubious. It was four years since he had published the cdc2 and CDC28 complementation paper, the human project had been on his mind ever since, and he had had ample time to try to make a library himself, but he “wasn’t prepared to … because it was such a long shot.” It was an act of desperation, but the one fact in its favour was that it was a quick experiment, and Melanie and Martin would know soon enough, one way or the other.

Like decorating, the secret of doing successful experiments lies in the time spent on preparation, and this experiment took a lot of forethought. The logistics were frightening. Normally, yeast transformations are done using about 10 million cells and ∼1 µg (a millionth of a gram) of plasmid DNA. To get enough colonies to ensure that every human gene had a decent chance of getting into a yeast cell, the procedure had to be amplified a hundred-fold; unfortunately, this was not just a matter of finding a big bucket to put all the cells in, but of doing a hundred separate transformations, because the protocol did not scale up efficiently. The hundred transformations then had to be spread onto hundreds of agar plates, which all had to be jammed into incubators, and then the massed plates had to be checked daily for growing colonies. It was just as well that Melanie was, in Paul’s words “about the most well-organized worker I’ve ever had,” and that Martin Goss, in Melanie’s opinion, was “perfect—he didn’t care whether it was a mad experiment or not, he still provided the technical help, and he was a good pair of hands at the bench, a jolly good technician.”

After a couple of small-scale runs, to maximise the transformation efficiency, Melanie and Martin ran their first big experiment, got nothing, and managed to really annoy the rest of the lab all at the same time; putting a vast number of coldish agar plates into the lab’s 36°C incubators turned out to cause such a drastic drop in temperature that everyone else’s temperature-sensitive mutants started growing again, wrecking a good few experiments. They tried again, being a bit more careful about the temperature issue. After two weeks, “just when you’re about to throw the plates out because you’re fed up with it,” they saw one or two rather pathetic colonies struggling along on the otherwise empty plates. By this time, Melanie and Martin were on a roll, so they set up another huge experiment and left the plates to cook whilst Melanie flew off to Banff in Alberta for that year’s annual yeast scientific beano, more formally known as the 13th International Conference on Yeast Genetics.

In Banff, Melanie had an interesting time fending off David Beach, who had learnt on the grapevine that the Nurse lab were looking for a human cdc2 homologue. Beach, now running his own operation at Cold Spring Harbor, had also been trying to clone human cdc2, had got nowhere, and was desperate to find out what was going on in London. Relations between him and Paul having deteriorated since their days together in Sussex, he figured that perhaps the postdoc doing the work would be more forthcoming and cornered her one night in the bar. A rather surprised Melanie fought off the barrage of questions valiantly and managed to escape in the end, with Beach none the wiser, but considerably crosser. In a way, it was quite reassuring to know that someone else in the world thought the project was worth fighting over, but the experience was less than pleasant.

Back in London after the meeting, any vestiges of jet lag and alcohol poisoning dissipated instantly when Melanie looked at the latest experiment. This time, there were five colonies, and they looked really promising. There was an emergency lab meeting to decide what to do. Because fission yeast is very good at scrambling introduced DNA sequences, sometimes disassembling plasmids and stuffing them into its own genome, the most urgent task was to rescue the plasmid DNA from the cells before it vanished. The colonies were plated out on new agar to amplify them up, and when Paul came to take a look at them, he realised that they were really onto something, because whatever was rescuing the large cdc2 mutant cells had to have come from a library plasmid. Sergio Moreno, who had arrived in the lab only a few weeks previously, remembers: “Paul was not doing experiments at the time, all he was doing then was looking at the cells—he really liked to look at cells under the microscope. It was clear when he looked at [one of] the colonies that it was really growing. When he picked the colony and spread it he realised there were small cells that were the complementing ones mixed with large cells that were losing the plasmid. He was really excited about that and everybody in the lab was aware this was going to be very important.”

In the event, only two of the five colonies still had rescuable plasmid DNA in them, but it was enough. Melanie transformed the precious DNA back into the cdc2-33 leu1-32 cells, to see whether either plasmid would complement the cdc2 mutation, and to wild excitement, she hit the jackpot with both; at the restrictive temperature, cdc2-33 leu1-32 cells were able to cycle normally as long as the plasmids were present. Comparison of the two plasmids showed that they contained an identical DNA insert, and the insert was also present, although chewed up, in the three other original colonies from the screen.

Being at the frontiers of science carries with it a certain degree of fear; it is frightening to be out of the limits, chasing after things that might not exist, and good scientists live with varying levels of anxiety that any new work they do might be wrong. And so it was in the Nurse lab. Finding human cdc2, particularly by such a frankly bonkers approach, was so important and so unlikely that wholly justifiable paranoia started to set in. What if the inserts were contaminants, that somehow a yeast cdc2 or CDC28 had sneaked into the library, or had just been in the air in the lab and got into the hundreds of plates undetected? The possibility of the result being an artefact was alarmingly likely, and the only way of finding out was to establish the DNA sequence of the inserts, which was going to take a few weeks. Melanie and Martin started sequencing, and the lab held its collective breath.

Paul was probably most affected:

I didn’t want to burn us, by just following nonsense. When the clones came up, when we showed it was due to a plasmid … what I remember is that every time Melanie did something, we discussed why it might not be saying what we hoped it would say. I then went through this psychologically peculiar time where I assumed it would fail at each step, but we just kept going. I was in this schizoid thing—I was keeping myself safe assuming it wouldn’t work, then I’d go home at night and think, “I’m just going to imagine it has worked, because I’ll go in tomorrow and it will be gone.”

Sequencing of the 2000 bp (base pairs) of DNA in the inserts carried on throughout the autumn, but by Christmas 1986, the work was finished and the complete sequence assembled. The good news was that the DNA sequence didn’t match either the fission yeast or the budding yeast cdc2 genes, and thus had to be something different, but depressingly, there were no obvious similarities between the new sequence and the yeast genes at the DNA level. But what about at the protein level? The yeast cdc2 and CDC28 proteins, although not completely similar, have one region that is invariant because it is needed for their activity as protein kinases. The region has the amino acid sequence proline–serine–threonine–alanine–isoleucine–arginine–glutamate, commonly abbreviated using the amino acid one-letter code as PSTAIRE. Melanie ran her new sequence through a programme that could decode the DNA, translating it to see what amino acids any protein made from it would contain, and with literally bated breath, she, Paul, and the lab stood over the old dot matrix printer as it churned out the result.

Over to Melanie: “I will never forget that day. The printout came off with PSTAIRE on it. It was unbelievable. We were all watching it and I said, ‘There is PSTAIRE there!’ and Paul said, ‘Are you sure?’ I said, ‘Yes, but it’s a different DNA sequence, it’s completely different.’ I remember Paul Russell said, ‘It’s a Eureka moment! It’s worked, it’s amazing!’ Paul was very excited and I was like, ‘Oof, thank goodness for that!’”

After that wonderful, climactic moment, there was still a fair amount of work to be done to show that the new sequence really did originate from a human source and to show that human cdc2 protein could be detected by the yeast cdc2 antibody (easier to do now that it was obvious what they were looking for), but the paper by Lee and Nurse, “Complementation Used to Clone a Human Homologue of the Fission Yeast Cell Cycle Control Gene cdc2,” was submitted to Nature in March and came out in early May 1987. The last sentence of the article was a vindication of Paul’s vision: “The identification of a cdc2-like function in human cells suggests that elements of the mechanism by which the cell cycle is controlled will probably be found in all eukaryotic cells.”

The appearance of such a major paper, the culmination of many years of speculation, hard work, boldness, and the odd bit of luck, should have been an occasion of great celebration for Paul and Melanie, but unfortunately, things didn’t quite turn out that way. The paper came out while both its authors were attending a conference in Heidelberg, and Paul was due to give a talk about its contents towards the end of the meeting. However, just before leaving Britain, Paul had picked up an ear infection, the pain of which was exacerbated by the flight from London to Frankfurt, and he ended up being admitted to the local hospital, spending most of the meeting there. He did manage to show up for his talk, but the import of what he was saying was overshadowed by his head being swathed in a huge white bandage. “I was in such pain I can’t even remember what I talked about. I had a horrible ear infection—it was unbelievably painful. The hospital had to puncture my eardrum and drain it. It was awful, awful. The worst pain.” Melanie fared little better, but for a nicer reason. She was in the first trimester of her first pregnancy and had awful morning sickness. Her summary of their triumph says it all: “I felt dreadful and Paul was really poorly.”

Paul and Melanie’s paper started a revolution in cell cycle research. Because all eukaryotes turned out to have cdc2-like genes, the genetics established in fission and budding yeast laid down a roadmap of what the biochemists in higher eukaryotes should be looking for. Research leapt ahead when the two fields synergised, and Paul suggests that the yeast work may have saved somewhere between five and 10 years of research in mammalian systems.

One of the first and most important molecules to fall to the newly unified field was MPF, Maturation Promoting Factor. In 1988, after almost two decades of effort, MPF was purified by Jim Maller’s lab in Denver and was shown to consist of two proteins, one of which was a kinase. Using antibodies raised against the PSTAIRE region of cdc2, two collaborative teams, the Nurse and Maller labs, and David Beach and John Newport’s labs, published back-to-back papers in Cell showing that the MPF kinase was, indeed, cdc2, as Paul had almost shown with Chris Ford back in Sussex in 1980. The primary mechanism regulating G2/M in both yeast and higher eukaryotes was not just similar; it was identical.

In a particularly nice twist, MPF was also the means of uniting the work of two researchers who met in the early 1980s, hit it off instantly, and have kept the cell cycle world entertained with their energetic sparring ever since. When discussing science, Tim Hunt and Paul Nurse have the air of two small boys playing on a beach together, falling out, and making up, endlessly fascinated by the rock pools, the funny looking shells, and the task of building huge and sometimes precarious sandcastles. In 1982, Tim had accidentally stumbled into the cell cycle world through his work on protein degradation in sea urchin eggs, when he discovered cyclins, the keys to how the cell cycle turns. Cyclins must be made, degraded, and then made anew in order for cells to divide properly, and the reason for this became clear once MPF was purified. MPF comprises one molecule of Tim’s cyclin protein bound to one molecule of Paul’s cdc2 protein, and cdc2 cannot work without the assistance of cyclin; indeed, cdc2’s official biological name, CDK2, cyclin-dependent kinase 2, shows the defining nature of the interaction. Functional MPF is created when enough cyclin has built up to switch on cdc2 activity, thereby driving cells into mitosis. Cells cannot exit mitosis unless MPF activity is switched off, and for this to happen, cyclin must be degraded. At the end of mitosis, the cell divides, cyclin starts to build up again, and the process is repeated.

Tim’s cyclin and Paul’s cdc2 were the founder members of two protein families, each with multiple related members. Today we know that progression through the cell cycle in higher eukaryotes is driven by a cell cycle engine composed of particular CDKs in partnership with different cyclins. Distinct cyclin–CDK pairs are needed at different points in the cycle, but they all work in the same way, switched on by the presence of cyclin in order to push cells through a rate-limiting control step, and then switched off by cyclin degradation when the step has been passed (a good example of this is John Diffley’s preRC, one of the stars of Chapter 4). By means of phosphorylation and dephosphorylation by enzymes such as wee1 and cdc25, and the action of CDK inhibitors, the cell cycle engine is tuned to respond with exquisite sensitivity to changes in the environment of the cell in which it resides, going faster or more slowly, or stopping altogether depending on the prevailing conditions. As might be expected, the complexity of this regulation is greater in multicellular organisms such as ourselves than in unicellular yeasts, but the basic principles of cell cycle control laid down by Hartwell and Nurse have held firm. Not surprisingly, the two geneticists have won any number of prizes over the years, culminating in the award of the 2001 Nobel Prize in Physiology or Medicine, which they shared with Tim Hunt.

The Hug: Paul Nurse and Tim Hunt, 2001 Nobel Prize ceremony, Stockholm.

(Photograph courtesy of epa/Gerry Penny.)

Nowadays, despite being loaded down with awards, a knighthood, and far too much administration in his current schizophrenic incarnation as President of the Royal Society and CEO of the Crick Institute, Paul’s heart still belongs very much to the lab; seeing him discussing science with his group reveals a happier, more relaxed persona, and he has never lost the early idealism that led him into research:

I think it’s a privilege to do what we do. I did make a pact with myself. I thought when I did a PhD, “Should I do something obviously useful, like work on malaria, for example, where contributing to our understanding, even in a small way, might be useful, or could I just indulge my own curiosity and work on whatever I like? And what I decided was, as long as I’m at the top of the tree I can do the latter. But if I slip from that then I will shift onto something more obviously useful.” And you’ll notice that I’ve had administrative, managerial posts for a long long time. People don’t believe me, but I don’t actually really enjoy it and I’m not even that good at it. I never remember half the things I’m supposed to remember or do. I do it because I feel I’m paying back a debt. So by spending half my time doing this other stuff, I justify what I do in the lab.

The last word goes to Melanie. After an extremely successful career in the pharmaceutical and biotech sector, she looks back on her adventures with cdc2 thus: “Martin Goss played a big role—all the lab played a big role. Paul was utterly convinced it was there, and the lab, who had more experience than me of fission yeast, were the ones saying, do these wild and wacky things, especially Tony Carr and Viesturs. I didn’t detect any jealousy from anybody—they were all lovely. It surprised me that this project was available, but it was available because it couldn’t be done. The fact that Paul and I came together for those two years was meant to happen.”

Nurse lab outing, ca. 1987.

(Photograph courtesy of Sergio Moreno.)

Web Resources

www.bbc.co.uk/programmes/p0094839   Paul’s Desert Island Discs.

www.nobelprize.org/nobel_prizes/medicine/laureates/2001/nurse-autobio.html#   Paul Nurse, Tim Hunt, and Lee Hartwell on the Nobel Prize website.

Further Reading

Murray A, Hunt T. 1993. The cell cycle: An introduction. Freeman, New York. The clearest and most interesting book I found about the cell cycle amongst the many out there.