Research papers are usually revisionist histories, imagined accounts driven by impeccable logic and unbroken experimental success, which in no way reflect the slowness, messiness, and serendipity of real life in the lab. To give a different hopefully more balanced perspective than what is often told, I want to tell you the story behind some of the discoveries that shaped my early career.“In reality, of course, I had stumbled on the control by complete accident.” It was 1974, and at the age of 25, I was working on the control of the cell cycle in fission yeast, one year into my post-doc with Murdoch Mitchison in Edinburgh. Hugely impressed by papers from Lee Hartwell, which described the isolation of cell division cycle (cdc) mutants in budding yeast, I started isolating cdc mutants in the rod-shaped fission yeast. These mutants could not divide but could still grow and thus became highly elongated. Screening for them was a laborious and slow business—only about 1 in 10,000 of the original mutagenized cells yielded a cdc mutant. As a consequence, it took the best part of a year to identify enough mutants to define just 30 cdc genes (we now know that there are 400–500 cell-cycle genes). To reduce the tedious workload of random visual screening, I needed a selection procedure and so hit on the idea of centrifuging cells after mutagenesis through a gradient to enrich for enlarged cells, then examining the micro-colonies formed from these cells under a microscope and micro-manipulating away elongated cells as potential cdc mutants. This was not such a bright idea, however, because mutagen-damaged DNA blocks onset of the subsequent mitosis, resulting in elongated cells not due to a specific gene defect but because of non-specific DNA damage, which affects many cells in the population. I struggled with this procedure for a couple of weeks, unfortunately finding fewer cdc mutants than by my normal procedure, and was on the verge of abandoning the approach altogether when I spotted something unexpected under the microscope. It was a micro-colony made up of small cells, shorter than the normal rod-shaped wild-type fission yeast cells. This was the complete opposite phenotype to the enlarged cells I was searching for. How these small cells got to where they did in the gradient I do not know, given that I was using a selection scheme designed to enrich for large cells. At first I was a bit annoyed, and then it gradually dawned on me that cells dividing at a small size might be finishing their cell cycle more rapidly than they could grow and, as a consequence, were being advanced prematurely through a rate-limiting process of the cell cycle that was determining the overall rate of cell reproduction. If correct, this small-sized mutant was defining a cell-cycle control of the type that I had hoped might eventually emerge from study of the cdc mutants. I had gotten there in one simple step—with no forethought, no impeccable logic, by total serendipity, and simply by following what nature had presented to me. This first mutant, which I called “wee” because it was small and isolated in Scotland (a name I thought witty at the time, though the wit wears thin after nearly half a century), was by chance temperature sensitive. This meant that it was of normal size at low temperature and small at high temperature. Following discussion with my fellow post-doc, Peter Fantes, we worked out that, by shifting temperatures, it would be possible to determine when in the cell cycle cells become advanced, and we could therefore establish what step was rate limiting for progression through the cell cycle. This revealed that wee1 acted at the G2-to-mitosis transition, so the gene was determining the length of G2 and thus the onset of mitosis. This was a surprise because at the time most researchers thought that rate-limiting cell-cycle controls would act at the beginning of the cell cycle in G1. I was excited by these results and began talking about them. And how did I explain what I had done? I am ashamed to say that I wrote a revisionist history. I started with having a great idea that small mutants would reveal rate-limiting cell-cycle controls, followed by a heroic search for small-sized mutants, leading to the eventual discovery of the mutant that I had imagined might exist, and finally an impeccable logical description of what it all meant. In reality, of course, I had stumbled on the control by complete accident. I decided to look for more wee mutants to define the rate-limiting steps of the cell cycle and the genes acting in these controls. I set myself the target of finding 50 wee mutants for this analysis. This search was even more tedious than the search for cdc mutants because wee mutants were even rarer. For much of the next year, I isolated new mutants, checking as I went along whether they were alleles of wee1 or, as I hoped, mutants that defined new genes and controls. About one or two new mutants were found every week, but all were alleles of wee1. I was making little progress. Near the end of my frustrating quest, I spotted wee mutant 48, but unfortunately it was on a plate covered with a filamentous fungus. It is difficult to purify a yeast strain away from a contaminating fungus that spreads much more rapidly across an agar plate. It was also a cold Scottish November Friday in the late afternoon, and it was raining. I was tired at the end of the week and was convinced that this mutant was yet another allele of wee1, which would only swell my collection from 47 to 48 mutants defective in wee1. I threw it away in the rubbish and went home. And then I felt guilty. What if this mutant was special? Perhaps it defined something new and different, rather than yet another allele of wee1. I finished my dinner and got back on my bicycle. It was dark and still raining, and I cycled back to the lab. Delving into the rubbish, I found the plate and started the long process of sub-culturing the yeast away from the continually invading fungus. Eventually, I got a pure culture of the new wee mutant, crossed it with my wee1 alleles, and found that it was a new gene unlinked to wee1! I called it wee2, which of course sounds even sillier than wee1. So now there were two genes involved in cell-cycle control, wee1 and wee2. This was the 1970s before cloning, so the only experimental approaches possible had to be based on classical genetics. Out of 50 wee mutants, 49 were alleles of wee1 and 1 of wee2. That suggested that wee1 encoded an inhibitor of the G2-to-mitosis transition because loss-of-function mutations can be expected to be frequent. Given that only one wee2 mutation had been isolated, perhaps wee2 encoded an activator and the wee2 mutation made that activator more active. Such a positive acting gain-of-function change could be expected to be rare. But it would also mean that a loss-of-function wee2 mutation would fail to complete the cell cycle. So perhaps one of the cdc mutations that had already been isolated might define a cdc gene that could be hyperactivated to generate the wee2 phenotype. It was just possible that the equivalent cdc gene had already been identified. This was unlikely, however, as the 30 genes identified only represented a small fraction of the total cdc genes that were to be expected. But perhaps it was worth checking.“What would I do then about my job, paying the mortgage, feeding my babies? Bad thoughts began to enter my mind.” So I crossed the wee2 mutant to representative alleles of each of the 30 cdc genes. And I was lucky—really lucky. Wee2 was closely linked to cdc2. I explained all of this to my colleague, Pierre Thuriaux, my genetic guru, but he said that it was possible that wee2 was not the same gene as cdc2 but was simply adjacent to cdc2 or very nearby. How could this be solved using classical genetics? The only way was to construct a fine structure map of cdc2 and to map the wee2 mutant allele onto that map. This was another very slow project. New cdc2 alleles had to be found and mapped, linkage had to be determined, a fine structure map had to be made, and finally, wee2 had to be mapped onto the cdc2 gene map Another year went by—a mind boringly grind carried out with Pierre—that eventually showed that the wee2 allele did indeed map within the cdc2 gene. So wee1 and cdc2 acted as negative and positively acting regulators functioning in the major rate-limiting step of the fission yeast cell cycle acting at the G2-to-mitosis transition. I was really pleased with this result. But there was a problem. Unfortunately, the world was not as interested as I was in this result, because most attention was still on cell-cycle controls acting in G1. This was a particular problem for me because by now I had two small children and a mortgage, and my post-doc employment was coming to an end. I was still in Edinburgh working in the lab of Murdoch Mitchison, who was incredibly supportive but had no long-term salary for me, and I now had a family with two babies to support. I had published quite a number of papers from Murdoch’s lab, and his name does not appear on any of them because he said he “had not contributed with his own hands to the experiments,” a truly generous gentleman of science. But I had to find a job, and with the lack of interest in G2 cell-cycle controls, I thought I had better do some work on G1. But what could I do? Once again Lee Hartwell came to my rescue. He had defined a G1 control called “start,” revealed by clever studies with his budding yeast cdc mutants. He had taken a developmental biologist’s approach, asking at what point in the cell cycle did cells become “committed” to that cell cycle in the sense that alternative developmental pathways to the cell cycle are no longer possible. He had arrested cdc mutants at different stages of the cell cycle and challenged them to undergo the alternative developmental pathway of conjugation. Those before commitment, the point of no return, could conjugate, while those after could not. He called this control start and identified several start genes, one of which was called CDC28. I thought that it would be easy for me to do a similar analysis in fission yeast, and so I could make a contribution, albeit a minor one, to G1 cell-cycle control. If successful, perhaps I could even get a job. So I set up an assay system and quite rapidly made progress. Most of the cdc mutants blocked at a stage where they failed to conjugate, but I found one blocking in early G1 that conjugated very efficiently. This mutant defined cdc10, which encoded a transcription factor that was eventually found to be responsible for the transcription of gene products required for DNA replication. This gene acted prior to commitment and thus extended the start concept to fission yeast. My very last experiment before publishing was to test the mutants in cdc2, the best-studied cdc gene. These mutants blocked in G2 and so would be way past the start commitment point in G1. It was my negative control. But my negative control did not work. Cdc2 mutants blocked at their restrictive temperature could still conjugate—not that efficiently but around 20%–25%. I desperately wanted to ignore this result, but the figure of 20%–25% was rather high. How could I explain what was obviously an incorrect result? Perhaps the temperature of the water bath being used to block the cdc2 mutants was not correct. I find that biologists often blame the temperature when experiments do not work. So I checked the water bath, repeated the experiment, and got 25% again. I bought a bigger thermometer, checked the temperature of the water bath, repeated the experiment, and once again got 25%. I got depressed, stopped doing experiments for a month, did the experiment again, and still got 25%. I was in a dilemma. Everything else had worked perfectly—either no conjugation or conjugation. But what did an intermediate result of 25% mean? If I reported this intermediate result in my research paper, I was certain that it would undermine the other results and the paper would be rejected. What would I do then about my job, paying the mortgage, feeding my babies? Bad thoughts began to enter my mind. Perhaps I should just forget about the cdc2 results. That would be easy to do, as only I knew about them and if I did that then perhaps I could get my paper published.“I began to say to myself, ‘Let’s imagine that it was true just so I could savor a successful outcome if only for a couple of days.’” Fortunately, I soon realized that this was unacceptable. I kept racking my brain for why I was not getting the “right” result. Then I had a new thought. What if 25% was actually the correct result? I had never thought of that before; I had always assumed it must be wrong. So if 25% was right, how could it be explained? I am a glider pilot, and a possible explanation came to me a few days later, when I was gliding in the hills around Edinburgh. I have always found that doing something quite different like flying helps new ideas to form, whereas thinking constantly about the same problem stifles really novel approaches. Once thought of, it was rather obvious. If cdc2 was required twice during the cell cycle—in G2 for mitosis as already shown, but also in G1 before S phase—then a value of 25% might be explained. Because G1 is short in fission yeast, when arresting a population of cells, only a small part of the population blocks in G1. These days, a FACS would sort this out immediately, but then these machines were not generally available. To test this possibility, I arrested cells in G1 and released them into the cdc2 block. To my relief, they all remained blocked in G1 and could conjugate very effectively, so they were all blocked before start. This meant that cdc2 had two roles in the cell cycle, both of them controlling. The first acted at the commitment control start in G1, and the second acted in the rate-limiting control acting at G2 determining the onset of mitosis. I was now very excited indeed, and I had also learned an important lesson. I had been convinced that I knew the “right” answer, so when the “wrong” answer came along, I had assumed the experimental result was incorrect. The lesson that I learned was to always take results seriously and never sweep uncomfortable results under the carpet. The coming together of the G1 commitment and the G2 mitosis controls showed that cdc2 was crucial for understanding how the cell cycle is controlled. But there were two difficulties. The first was that the understanding I had come to was abstract in nature, couched in terms of concepts and gene names but lacking any molecular mechanism. The second was that it applied to fission yeast, which, although dear to my heart, was of rather limited interest to the rest of the world. Both problems could be tackled through molecular genetics. If the cdc2 gene could be cloned, its function could be investigated in molecular terms and comparisons could be made more easily with other organisms. By this time, I was at the University of Sussex in Brighton working as an independent research fellow with a small lab, and I made the decision to establish methods to transform fission yeast and develop vectors, gene libraries, and gene manipulation techniques, working with my colleague David Beach. It took a year or so to get all of this in place. Then, the lab cloned the cdc2 gene by rescue of a temperature-sensitive cdc2 mutant using a fission yeast library, essentially a genetic complementation approach. This was a great moment. We had the physical presence of the cdc2 gene on a 2 kb DNA fragment in an Eppendorf tube. All of the previous abstraction could become more concrete. At this time, sequencing even such a small fragment such as 2 kb took many months, so in the meantime we decided to use the same approach of cloning by rescue of a cdc2 mutant, but this time using a budding yeast library to see if the same gene existed in budding yeast. I was excited about the possibility of finding functionally equivalent genes from different organisms using genetic complementation, so I kept popping into the lab to see if any yeast clones grew up. By this time, I was on a 50 cc moped—an advance on my bicycle, but not much of one. And to my great surprise, early one morning I spotted some colonies growing up; it appeared that a gene equivalent to cdc2 might exist in budding yeast. Perhaps cell-cycle control was conserved, at least among simple eukaryotes. The question was which budding yeast gene was it? Only four cdc genes had been cloned from budding yeast by Steve Reed, and he generously sent them so we could test if one of them was the gene we had cloned. Once again, we had no right to be so lucky, given that there are more than 5,000 genes in yeast, but by Southern blotting we showed that the fission yeast cdc2 gene was the same as the budding yeast CDC28 gene. This was one of the four genes that Steve had cloned and the one that Lee had shown acted at the G1 commitment controls. It was uncanny how it was all falling into place. Then the cdc2 sequence was completed. There was just one hit in the database—the src oncogene, thought to encode a protein kinase. This tenuous clue allowed my lab working with cdc2 and Steve Reed’s lab working with CDC28 to show by molecular genetics and biochemistry that cdc2/CDC28 was a protein kinase and that cell-cycle control was based on protein phosphorylation. I was happy to continue working with fission yeast to work out the details of this control. But I was also wondering if the control was conserved in all eukaryotes. Budding and fission yeast are not so closely related, so if there was conservation between these yeasts, perhaps there was a cdc2 in humans too. I had now been recruited to the Imperial Cancer Research Fund Lincoln’s Inn Fields Laboratory in London by Walter Bodmer, and I was always being asked by my senior colleagues if cell-cycle control was the same in human cells. But I was nervous of wasting my lab colleagues’ time on such an obviously long-shot project. Then a bold post-doc, Melanie Lee, came to my lab and asked for a difficult project. We decided that looking for cdc2 in human cells would be sufficiently difficult, especially given that the last common ancestor between the yeasts and humans may have been around 1.5 billion years ago, quite a long time for conservation to be maintained. Melanie started by looking for DNA fragments from human cells that were structurally similar to the fission yeast cdc2 gene by using two approaches: first, using antibodies against the yeast protein combined with a human expression library, and second, using reduced stringency Southern blotting. It is important to remember that there were no whole-genome sequences, no PCR, and only limited gene libraries. It was a very hard project for Melanie, with the occasional leads not leading anywhere. It also inherently seemed unlikely to work, given the huge divergence between humans and yeast and the fact that there were hundreds of different protein kinases. Given this, how would it be possible to know if the correct one had been identified, given the evolutionary divergence? The only certain way to show that a candidate human gene had the same function as cdc2 was that it could rescue a fission yeast cdc2 mutant. Therefore, the way forward had to be to clone by rescue, just as CDC28 had been cloned. A good human cDNA library was generously given by Hirota Okayama and Paul Berg that, by chance, was found to be expressed in fission yeast. Melanie went to work. Many petri dishes later, a clone derived from a cdc2 temperature-sensitive mutant was found to be growing at high temperature. But was it a contaminant, a revertant, a plasmid that had picked up a yeast gene, or a human gene acting as a suppressor? Checking all of this was probably the most stressful period of my working life because if this growing clone did indeed contain the human cdc2 gene, then it was likely that cell-cycle control was common to all eukaryotes, and that was important. As every week passed, each experiment eliminated yet another trivial explanation. However, I was very concerned that the clone would eventually be shown to be an artifact. I began to dread going to the lab in case the experiment of that day would show that we had failed. Melanie always seemed to be calm, but I was not. I began to say to myself, “Let’s imagine that it was true just so I could savor a successful outcome if only for a couple of days, which would then be dashed the next week.” As we eliminated more and more of the trivial explanations, the worse it became. Eventually we were on the edge: we knew that it was a human DNA segment that was rescuing the cdc2 temperature-sensitive mutant, but was it just a high copy-number suppressor, or was it a human homolog of cdc2? The DNA sequence and the translated protein sequence were the final test. It appeared on the computer screen around the middle of the day. I had been nervously pacing about the rather gloomy and somewhat claustrophobic corridors of the Lincoln’s Inn Fields Laboratory waiting for the result. The computer did its work, and we all huddled around the screen as the letters marched across, marking out the predicted protein sequences. The DNA sequences were highly diverged, but the translated protein sequences were not. The proteins showed identities and similarities everywhere in their amino acid sequences; overall, the proteins were more than 60% identical, and the proteins were only one amino acid different in length. The yeast and human genes were structurally similar and functionally equivalent. They were the same genes with the same function despite up to 1.5 billion years of divergence. We were ecstatic, completely ecstatic. A story that had begun 13 years previously and had involved many colleagues in the lab had led to an outcome that I had only dreamed of. The principles underpinning cell-cycle control had been worked out in yeast cells and were much the same in human cells. Given that, they were probably the same in all eukaryotic cells. What do I remember most about it all? An enormous satisfaction, a sense of wholeness that the extraordinary diversity of the living world was built on common principles, and perhaps most of all, an overwhelming relief that it was true.
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Feb 14, 2024
Robin A. Weiss 
Open Access