I recently had the privilege of speaking with Professor Sydney  Brenner, a professor of Genetic medicine at the University of Cambridge  and Nobel Laureate in Physiology or Medicine in 2002. My original  intention was to ask him about Professor Frederick Sanger, the two-time  Nobel Prize winner famous for his discovery of the structure of proteins  and his development of DNA sequencing methods, who passed away in  November. I wanted to do the classic tribute by exploring his scientific  contributions and getting a first hand account of what it was like to  work with him at Cambridge’s Medical Research Council’s (MRC) Laboratory for Molecular Biology  (LMB) and at King’s College where they were both fellows. What  transpired instead was a fascinating account of the LMB’s quest to  unlock the genetic code and a critical commentary on why our current  scientific research environment makes this kind of breakthrough unlikely today.

It is difficult to exaggerate the significance of Professor Brenner  and his colleagues’ contributions to biology. Brenner won the Nobel  Prize for establishing Caenorhabditis elegans, a type of  roundworm, as the model organism for cellular and developmental  biological research, which led to discoveries in organ development and  programmed cell death. He made his breakthroughs at the LMB, where  beginning in the 1950s, an extraordinary number of successive  innovations elucidated our understanding of the genetic code. This code  is the process by which cells in our body translate information stored  in our DNA into proteins, vital molecules important to the structure and functioning of cells. It was here that James Watson and Francis Crick  discovered the double-helical structure of DNA.  Brenner was one of the first scientists to see this ground-breaking  model, driving from Oxford, where he was working at the time in the  Department of Chemistry, to Cambridge to witness this breakthrough. This  young group of scientists, considered renegades at the time, made a  series of successive revolutionary discoveries that ultimately led to  the creation of a new field called molecular biology.

To begin our interview, I asked Professor Brenner to speak about Professor Sanger and what led him to his Nobel Prize winning  discoveries.

Sydney Brenner:

Fred realized very early on that if we could  sequence DNA, we would have direct contact with the genes. The problem  was that you couldn’t get hold of genes in any way. You couldn’t purify  what was a gene. That is why right from the start in 1954, we decided we  would do this by using Fred’s method of sequencing proteins, which he  had achieved [proteins are derived from the information held in  DNA]. You have to realise it was only on a small scale. I think there  were only forty-five amino acids [the building blocks of proteins] that  were in insulin. We thought even scaling that up for proteins would be  difficult. But finally DNA sequencing was invented. Then it became clear  that we could directly approach the gene, and it produced a completely  new period in science.

He was interested in the method and interested in getting the  methods to work. I was really clear in my own mind that what he did in  DNA sequencing, even at the time, would cause a revolution in the  subject, which it did. And of course we immediately, as fast as  possible, began to use these methods in our own research.

ED:

This foundational research ushered in a new era of biological  science. It has formed the basis of nearly all subsequent discoveries in  the field, from understanding the mechanisms of diseases, to the  development of new drugs for diseases such as cancer. Imagining the  creative energy that drove these discoveries was truly inspirational. I  asked Professor Brenner what it felt like to be part of this scientific  adventure.

SB:

I think it’s really hard to communicate that because I  lived through the entire period from its very beginning, and it took on  different forms as matters progressed. So it was, of course, wonderful.  That’s what I tell students. The way to succeed is to get born at the  right time and in the right place. If you can do that then you are bound  to succeed. You have to be receptive and have some talent as well.

ED:

Today, the structure of DNA and how genetic information is  translated into proteins are established scientific canon. Brenner joked  that he “knew that molecular biology was doomed to success when [he]  heard two students speaking in a bus once and asking whether they would  get the genetic code in the examination. It had become an academic  subject.” But in the 1950s, the hypotheses generated at the LMB were  dismissed as inconceivable nonsense.

SB:

To have seen the development of a subject, which was  looked upon with disdain by the establishment from the very start,  actually become the basis of our whole approach to biology today. That  is something that was worth living for.

I remember Francis Crick gave a lecture in 1958, in which he  discussed the adapter hypothesis at the time. He proposed that there  were twenty enzymes, which linked amino acids to twenty different  molecules of RNA, which we call adapters. It was these adapters that  lined up the amino acids. The adapter hypothesis was conceived I think  as early as 1954 and of course it was to explain these two languages:  DNA, the language of information, and proteins, the language of work.

Of course that was a paradox, because how did you get one  without the other? That was solved by discovering that a molecule from  RNA could actually have function. So this information on RNA, which  happened much later really, solved that problem as far as origins were  concerned.

ED:

(Professor Brenner was far too modest here, as it was he who  discovered RNA’s critical role in this translation from gene to  protein.)

SB:

So he [Crick] gave the lecture and biochemists  stood up in the audience and said this is completely ridiculous, because  if there were twenty enzymes, we biochemists would have already  discovered them. To them, the fact that they still hadn’t, went to show  that this was nonsense. Little did the man know that at that very moment  scientists were in the process of finding the very first of these  enzymes, which today we know are the enzymes that combined amino acids  with transfer RNA. And so you really had to say that the message kept  its purity all the way through.

What people don’t realise is that at the beginning, it  was just a handful of people who saw the light, if I can put it that  way. So it was like belonging to an evangelical sect, because there were  so few of us, and all the others sort of thought that there was  something wrong with us.

They weren’t willing to believe. Of course they just said,  well, what you’re trying to do is impossible. That’s what they said  about crystallography of large molecules. They just said it’s hopeless.  It’s a hopeless task. And so what we were trying to do with the  chemistry of proteins and nucleic acids looked hopeless for a long time.  Partly because they didn’t understand how they were built, which I  think we molecular biologists had the first insight into, and partly  because they just thought they were amorphous blobs and would never be  able to be analysed.

I remember when going to London to talk at meetings, people  used to ask me what am I going to do in London, and I used to tell them  I’m going to preach to the heathens. We viewed most of everybody else as  not doing the right science. Like one says, the young Turks will become  old Greeks. That’s the trouble with life. I think molecular biology was  marvellous because every time you thought it was over and it was just  going to be boring, something new happened. It was happening every day.

So I don’t know if you can ride on the crest of a wave; you  can ride on it, I believe, forever. I think that being in science is the  most incredible experience to have, and I now spend quite a lot of my  time trying to help the younger people in science to enjoy it and not to  feel that they are part of some gigantic machine, which a lot of people  feel today.

ED:

I asked him what inspired them to maintain their faith and pursue  these revolutionary ideas in the face of such doubt and opposition.

SB:

Once you saw the light you were just certain that you had  to be right, that it was the right way to do it and the right answer.  And of course our faith, if you like, has been borne out.

I think it would have been difficult to keep going without  the strong support we had from the Medical Research Council. I think  they took a big gamble when they founded that little unit in the  Cavendish. I think all the early people they had were amazing. There  were amazing personalities amongst them.

This was not your usual university department, but a rather  flamboyant and very exceptional group that was meant to get together. An  important thing for us was that with the changes in America then, from  the late fifties almost to the present day, there was an enormous stream  of talent and American postdoctoral fellows that came to our lab to  work with us. But the important thing was that they went back. Many of  them are now leaders of American molecular biology, who are alumni of  the old MRC.

ED:

The 1950s to 1960s at the LMB was a renaissance of biological  discovery, when a group of young, intrepid scientists made fundamental  advances that overturned conventional thinking. The atmosphere and  camaraderie reminded me of another esteemed group of friends at King’s  College – the Bloomsbury Group, whose members included Virginia Woolf,  John Maynard Keynes, E.M. Forester, and many others. Coming from diverse  intellectual backgrounds, these friends shared ideas and attitudes,  which inspired their writing and research. Perhaps there was something  about the nature of the Cambridge college systems that allowed for such  revolutionary creativity?

SB:

In most places in the world, you live your social life  and your ordinary life in the lab. You don’t know anybody else.  Sometimes you don’t even know other people in the same building, these  things become so large.

The wonderful thing about the college system is that it’s  broken up again into a whole different unit. And in these, you can meet  and talk to, and be influenced by and influence people, not only from  other scientific disciplines, but from other disciplines. So for me, and  I think for many others as well, that was a really important part of  intellectual life. That’s why I think people in the college have to work  to keep that going.

Cambridge is still unique in that you can get a PhD in a  field in which you have no undergraduate training. So I think that  structure in Cambridge really needs to be retained, although I see so  often that rules are being invented all the time. In America you’ve got  to have credits from a large number of courses before you can do a PhD.  That’s very good for training a very good average scientific work  professional.  But that training doesn’t allow people the kind of room  to expand their own creativity. But expanding your own creativity  doesn’t suit everybody. For the exceptional students, the ones who can  and probably will make a mark, they will still need institutions free  from regulation.

ED:

I was excited to hear that we had a mutual appreciation of the college system, and its ability to inspire interdisciplinary  work and research. Brenner himself was a biochemist also trained in  medicine, and Sanger was a chemist who was more interested in chemistry  than biology.

SB:

I’m not sure whether Fred was really interested in the  biological problems, but I think the methods he developed, he was  interested in achieving the possibility of finding out the chemistry of  all these important molecules from the very earliest.

ED:

Professor Brenner noted that these scientific discoveries  required a new way of approaching old problems, which resist traditional  disciplinary thinking.

SB:

The thing is to have no discipline at all. Biology got  its main success by the importation of physicists that came into the  field not knowing any biology and I think today that’s very important.

I strongly believe that the only way to encourage innovation  is to give it to the young. The young have a great advantage in that  they are ignorant.  Because I think ignorance in science is very  important. If you’re like me and you know too much you can’t try new  things. I always work in fields of which I’m totally ignorant.

ED:

But he felt that young people today face immense challenges as well, which hinder their ability to creatively innovate.

SB:

Today the Americans have developed a new culture in  science based on the slavery of graduate students. Now graduate students  of American institutions are afraid. He just performs. He’s got to  perform. The post-doc is an indentured labourer. We now have labs that  don’t work in the same way as the early labs where people were  independent, where they could have their own ideas and could pursue  them.

The most important thing today is for young people to take  responsibility, to actually know how to formulate an idea and how to  work on it. Not to buy into the so-called apprenticeship. I think you  can only foster that by having sort of deviant studies. That is, you go  on and do something really different. Then I think you will be able to  foster it.

But today there is no way to do this without money. That’s  the difficulty. In order to do science you have to have it supported.  The supporters now, the bureaucrats of science, do not wish to take any  risks. So in order to get it supported, they want to know from the start  that it will work. This means you have to have preliminary information,  which means that you are bound to follow the straight and narrow.

There’s no exploration any more except in a very few places.  You know like someone going off to study Neanderthal bones. Can you see  this happening anywhere else? No, you see, because he would need to do  something that’s important to advance the aims of the people who fund  science.

I think I’ve often divided people into two classes: Catholics  and Methodists. Catholics are people who sit on committees and devise  huge schemes in order to try to change things, but nothing’s happened.  Nothing happens because the committee is a regression to the mean, and  the mean is mediocre. Now what you’ve got to do is good works in your  own parish. That’s a Methodist.

ED:

His faith in young, naïve (in the most positive sense) scientists  is so strong that he has dedicated his later career to fostering their  talent against these negative forces.

SB:

I am fortunate enough to be able to do this  because in Singapore I actually have started two labs and am about to  start a third, which are only for young people. These are young  Singaporeans who have all been sent abroad to get their PhDs at places  like Cambridge, Stanford, and Berkeley. They return back and rather than  work five years as a post-doc for some other person, I’ve got a lab  where they can work for themselves. They’re not working for me and I’ve  told them that.

But what is interesting is that very few accept that  challenge, providing what I think is a good standard deviation from the  mean. Exceptional people, the ones who have the initiative, have gone  out and got their own funding. I think these are clearly going to be the  winners. The eldest is thirty-two.

They can have some money, and of course they’ve got to accept  the responsibility of execution. I help them in the sense that I oblige  them and help them find things, and I can also guide them and so on. We  discuss things a lot because I’ve never believed in these group  meetings, which seems to be the bane of American life; the head of the  lab trying to find out what’s going on in his lab. Instead, I work with  people one on one, like the Cambridge tutorial. Now we just have  seminars and group meetings and so on.

So I think you’ve got to try to do something like that for  the young people and if you can then I think you will create. That’s the  way to change the future. Because if these people are successful then  they will be running science in twenty years’ time.

ED:

Our discussion made me think about what we consider markers of  success today. It reminded me of a paragraph in Professor Brenner’s  tribute to Professor Sanger in Science:

“A Fred Sanger would not survive today’s world of science. With  continuous reporting and appraisals, some committee would note that he  published little of import between insulin in 1952 and his first paper  on RNA sequencing in 1967 with another long gap until DNA sequencing in  1977. He would be labelled as unproductive, and his modest personal  support would be denied. We no longer have a culture that allows  individuals to embark on long-term—and what would be considered today  extremely risky—projects.”

I found this particularly striking given that another recent Nobel  prize winner, Peter Higgs, who identified the particle that bears his  name, the Higgs boson, similarly remarked in an interview with the Guardian  that, “he doubts a similar breakthrough could be achieved in today’s  academic culture, because of the expectations on academics to  collaborate and keep churning out papers. He said that: ‘it’s difficult  to imagine how I would ever have enough peace and quiet in the present  sort of climate to do what I did in 1964.’”

It is alarming that so many Nobel Prize recipients have lamented that  they would never have survived this current academic environment. What  are the implications of this on the discovery of future scientific  paradigm shifts and scientific inquiry in general? I asked Professor  Brenner to elaborate.

SB:

He wouldn’t have survived. Even God wouldn’t get a grant  today because somebody on the committee would say, oh those were very  interesting experiments (creating the universe), but they’ve never been  repeated. And then someone else would say, yes and he did it a long time  ago, what’s he done recently?  And a third would say, to top it all, he  published it all in an un-refereed journal (The Bible).

So you know we now have these performance criteria,  which I think are just ridiculous in many ways. But of course this money  has to be apportioned, and our administrators love having numbers like  impact factors or scores. Singapore is full of them too. Everybody has  what are called key performance indicators. But everybody has them. You  have to justify them.

I think one of the big things we had in the old LMB, which I  don’t think is the case now, was that we never let the committee assess  individuals. We never let them; the individuals were our responsibility.  We asked them to review the work of the group as a whole. Because if  they went down to individuals, they would say, this man is unproductive.  He hasn’t published anything for the last five years. So you’ve got to  have institutions that can not only allow this, but also protect the  people that are engaged on very long term, and to the funders, extremely  risky work.

I have sometimes given a lecture in America called “The  Casino Fund”. In the Casino Fund, every organisation that gives money to  science gives 1% of that to the Casino Fund and writes it off. So now  who runs the Casino Fund? You give it to me. You give it to people like  me, to successful gamblers. People who have done all this who can have  different ideas about projects and people, and you let us allocate it.

You should hear the uproar. No sooner did I sit down then all  the business people stand up and say, how can we ensure payback on our  investment? My answer was, okay make it 0.1%. But nobody wants to accept  the risk. Of course we would love it if we were to put it to work. We’d  love it for nothing. They won’t even allow 1%. And of course all the  academics say we’ve got to have peer review. But I don’t believe in peer  review because I think it’s very distorted and as I’ve said, it’s  simply a regression to the mean.

I think peer review is hindering science. In fact, I think it  has become a completely corrupt system. It’s corrupt in many ways, in  that scientists and academics have handed over to the editors of these  journals the ability to make judgment on science and scientists. There  are universities in America, and I’ve heard from many committees, that  we won’t consider people’s publications in low impact factor journals.

Now I mean, people are trying to do something, but I think  it’s not publish or perish, it’s publish in the okay places [or perish].  And this has assembled a most ridiculous group of people. I wrote a  column for many years in the nineties, in a journal called Current Biology. In one article, “Hard Cases”,  I campaigned against this [culture] because I think it is not only bad,  it’s corrupt. In other words it puts the judgment in the hands of  people who really have no reason to exercise judgment at all. And that’s  all been done in the aid of commerce, because they are now giant  organisations making money out of it.

ED:

Subscriptions to academic journals typically cost a British  university between £4-6 million a year. In this time of austerity where university staff face deep salary cuts and redundancies, and adjunct faculty are forced to live on food stamps, do we have the resources to pour millions of dollars  into the coffers of publishing giants? Shouldn’t these public monies be  put to better use, funding important research and paying researchers  liveable wages? To add insult to injury, many academics are forced to  relinquish ownership of their work to publishers.

SB:

I think there was a time, and I’m trying to trace the  history when the rights to publish, the copyright, was owned jointly by  the authors and the journal. Somehow that’s why the journals insist they  will not publish your paper unless you sign that copyright over. It is  never stated in the invitation, but that’s what you sell in order to  publish. And everybody works for these journals for nothing. There’s no  compensation. There’s nothing. They get everything free. They just have  to employ a lot of failed scientists, editors who are just like the  people at Homeland Security, little power grabbers in their own sphere.

If you send a PDF of your own paper to a friend, then you are  committing an infringement. Of course they can’t police it, and many of  my colleagues just slap all their papers online. I think you’re only  allowed to make a few copies for your own purposes. It seems to me to be  absolutely criminal. When I write for these papers, I don’t give them  the copyright. I keep it myself. That’s another point of publishing,  don’t sign any copyright agreement. That’s my advice. I think it’s now  become such a giant operation. I think it is impossible to try to get  control over it back again.

ED:

It does seem nearly impossible to institute change to such  powerful institutions. But academics have enthusiastically coordinated  to strike in support of decent wages.  Why not capitalise on this collective action and target the publication  industry, a root cause of these financial woes? One can draw  inspiration from efforts such as that of the entire editorial board of the journal Topology, who resigned in 2006 due to pricing policies of their publisher, Elsevier.

Professor Tim Gowers, a Cambridge mathematician and recipient of the Fields medal, announced in 2012, that  he would not be submitting publications to nor peer reviewing for  Elsevier, which publishes some of the world’s top journals in an array  of fields including Cell and The Lancet. Thousands of  other researchers have followed suit, pledging that they would not  support Elsevier via an online initiative, the Cost of Knowledge. This “Academic Spring”, is gathering force, with open access publishing as its flagship call.

SB:

Recently there has been an open access movement and it’s beginning to change. I think that even Nature, Science and Cell  are going to have to begin to bow. I mean in America we’ve got old  George Bush who made an executive order that everybody in America is  entitled to read anything printed with federal funds, tax payers’ money,  so they have to allow access to this. But they don’t allow you access  to the published paper. They allow you I think what looks like a proof,  which you can then display.

ED:

On board is the Wellcome Trust,  one of the world’s largest funders of science, who announced last year  that they would soon require that researchers ensure that their  publications are freely available to the public within six months of  publication. There have also been proposals to make grant renewals  contingent upon open access publishing, as well as penalties on future  grant applications for researchers who do not comply.

It is admirable that the Wellcome Trust has taken this stance, but  can these sanctions be enforced without harming their researchers’  academic careers? Currently, only 55% of Wellcome funded  researchers comply with open access publishing, a testament to the fact  that there are stronger motivators at play that trump this moral high  ground. For this to be successful, funders and universities will have to  demonstrate collective leadership and commitment by judging research  quality not by publication counts, but on individual merit.

Promotion and grant committees would need to clearly commit both on  paper and in practice to these new standards. This is of course not  easy. I suspect the reason impact factors and publication counts are the  currency of academic achievement is because they are a quick and easy  metric. Reading through papers and judging research by its merit would  be a much more time and energy intensive process, something I anticipate  would be incompatible with a busy academic’s schedule. But a failure to  change the system has its consequences. Professor Brenner reflected on  the disillusioning impact this reality has on young scientists’ goals  and dreams.

SB:

I think that this has now just become ridiculous  and its one of the contaminating things that young people in particular  have to actually now contend with. I know of many places in which they  say they need this paper in Nature, or I need my paper in Science because I’ve got to get a post-doc. But there is no judgment of its contribution as it is.

ED:

Professor Brenner hit upon several hot topics amongst academics  in all disciplines. When Randy Scheckman won his Nobel Prize this year  in the Physiology or Medicine, he announced his boycott of “luxury” journals such as Nature, Science, and Cell, declaring that their distorting incentives “encouraged researchers to cut corners and pursue trendy fields of science instead of doing more important work.”

Because publications have become a proxy for research quality,  publications in high impact factor journals are the metric used by grant  and promotion committees to assess individual researchers. The problem  is that impact factor, which is based on the number of times papers are  cited, does not necessarily correlate with good science. To maximize  impact factor, journal editors seek out sensational papers, which boldly  challenge norms or explore trendy topics, and ignore less spectacular,  but equally important things like replication studies or negative  results. As a consequence, academics are incentivised to produce  research that caters to these demands.

Academics are slowly awakening to the fact that this dogged drive to publish rubbish has serious consequences  on the quality of the science that they produce, which have far  reaching consequences for public policy, costs, and human lives. One  study found that only six out of 53 landmark studies in cancer research  were replicable. In another study, researchers were only able to repeat a  quarter of 67 influential papers in their field.

Only the most successful academics can afford to challenge these  norms by boycotting high impact journals. Until we win our Nobel Prizes,  or grant and promotion structures change, we are shackled to this  “publish or perish” culture. But together with leaders in science and  academia such as Professor Brenner, we can start to change the structure  of academic research and the language we use to judge quality. As  Brenner emphasised, it was the culture of the LMB and the scientific  environment at the time that permitted him and his colleagues to uncover  the genetic basis of life. His belief that scientists like Professor  Sanger would not have survived today are cautionary words, providing new  urgency to the grievances we have against the unintended consequences  of the demands required to achieve academic success.