Interview transcript

Michael Brown, co-recipient with your close collaborator Joseph Goldstein, of the 1985 Nobel Prize in Physiology or Medicine for your discoveries concerning the regulation of cholesterol and metabolism. Welcome to this archival interview with nobelprize.org.

Michael Brown: Thank you. I’m glad to be here.

I’d like to start, if I may, by exploring your scientific beginnings a little and I don’t know where they began so I don’t know where to start, but perhaps at University of Pennsylvania where you read chemistry and then did an MD. Did you know at that time that you were set to become a serious scientist?

Michael Brown: It’s an interesting story, it goes back even before that. I trace my interest in science to when I was 13 years old and a friend convinced me to get my license to do amateur radio operating, and I got my license when I was 13. He and I would build transmitters and receivers and obviously we didn’t design them, but we’d follow instructions and go out and buy the parts and put them together and solder all these wires. I remember very clearly that you’d work for days or weeks on something and you’d usually finish building it sometime around 2 or 3 in the morning and then I’d plug it in, and it would blow every fuse in the house. I wasn’t popular with my parents either but that’s when the science began because you had to go back and troubleshoot and try to figure out what was wrong, what had you done wrong, what was soldered wrong or what resistor was put in backwards or whatever. I think that that experience of troubleshooting and problem solving was really very important in my thinking about being a scientist.

I also always wanted to be a physician and when I got the Nobel Prize actually the New York post, the newspaper went to my father’s apartment in New York to interview him and he produced a baby picture of me, and they ran this thing in the newspaper and the caption said “He wanted to be a doctor ever since he was two years old” and actually I think it’s true. So I knew I wanted to be in medicine and I really liked this problem solving. I went back recently and looked at some papers I had from high school and when I was applying to college I sent out a little resume for people who were going to write letters of recommendation on my behalf and it said “Career interest” and I only listed one thing and it said “Medical research” so I guess I was interested in research. I remember very clearly, in fact I found a book report that I had written on Arrowsmith by Sinclair Lewis, which you know had a major influence on almost everybody of my generation, who went into medical science. I knew I wanted to be a physician and a scientist and so at university I majored in chemistry although I spent most of my time as editor of the Daily Pennsylvanian, this daily student newspaper.

Then in medical school I had an experience in a summer in elective rotation with a very impressive scientist who managed to be imaginative but critical at the same time, highly critical and it was that combination of being a critic of your own work along with imagination trying to drive yourself forward that really aroused my interest in science. And I did a residency in medicine and there I met Joe Goldstein and he and I immediately … We were in the same residency group and although our job was to take care of patients, what attracted us to each other was our common interest in the scientific basis of the diseases that we were seeing.

I want to explore that relationship in greater detail later.

Michael Brown: But at any rate and then I went to the National Institutes of Health after my residency and was exposed to a very inspirational scientist, a man named Earl Stadtman, whose other student, Stanley Prusiner, also received the Nobel Prize and he produced a lot of very successful scientists and was a very inspirational character.

You’ve spoken of how he taught you the principles of enzymology. What was it that particularly made him a good teacher, what did he have?

Michael Brown: Again, I think it was integrity. As I recall, if you made a novel observation and that lead to a new theory, his attitude wasn’t ok let’s design as many experiments as we can to prove that this new idea is right, his approach was let’s design as many experiments as we can to shoot down the idea and only if we can’t shoot it down do we then begin to accept it. Of course that’s straight out of scientific philosophy but watching it in practice by somebody whose sole devotion was the truth rather than self-promotion or any ulterior motive for doing science, I think that’s the characteristic, his characteristic that washed off on so many of his students.

Yes, I imagine a very rare characteristic to find.

Michael Brown: Yes, especially in medical research where people have a variety of motivations.

The fact that you read chemistry and then did medicine, I guess that’s a fairly standard path here but do you think that contributed a lot to your approach to medicine, doing basic science prior to clinical science?

Michael Brown: I always liked basic science and you know, I enjoyed chemistry, but I must say I wouldn’t have considered a career in pure basic science, I never thought about going to graduate school for a PhD in chemistry. I always had the over-riding motivation to become a physician. In fact, even after I came to Dallas and started my own laboratory and was also doing clinical work. Every time I spoke to my father, my father would say “Well, how many patients have you seen today?” I’d say “Dad, today I worked in the lab”, and he would say “Well, that’s not a very good thing”. It wasn’t until after Joe and I began to receive the prizes, the first one was in San Francisco, he lived in New York and we invited him to San Francisco to see us receive this prize and he came up to me afterwards and said “Well, maybe there is something about this research”.

But in a way you were very blessed to have such an unswerving determination to follow that path.

Michael Brown: I did and there were obstacles in the way. In the summers when I was in medical school, I had to earn money because we didn’t have very much money and so I worked for a pharmaceutical company in their lab, in fact Smith Kline now, you know, eventually became Smith-Kline Beacham and then Glaxo Smith Kline, but they were then called Smith, Kline & French in Philadelphia. I worked in their laboratories every summer and I had a very trivial kind of job injecting things into rats and all my friends who didn’t need the money were working in the summers in much more exciting labs at the medical school and I was quite jealous of that. So, I had a real eager desire to do serious science.

I daresay the job gave you an insight into something that other people weren’t seeing anyway, which paid off later. So, after NIH and Earl Stadtman you then had these three choices that came together, it seems to me that you 1) decided that you were going to move to Dallas, 2) you decided that you were going to work on hypercholesterolemia …

Michael Brown: Cholesterolemia.

Cholesterolemia. Let’s call it FH for ease of pronunciation and the third thing was that you decided to work with Joe Goldstein, very close collaboration. Those these things inter-related …

Michael Brown: Oh, yes

… and they all paid off to a great degree and they’re all important, so I’d like to investigate each one.

Michael Brown: And they were all not very obvious. Let’s discuss Dallas first. I had grown up in the Northeast. I had gone to the world’s oldest medical school, sorry, the oldest school in the United States, which is University of Pennsylvania. Then I met Joe as residents at the Mass General in Boston and Joe kept telling me what a wonderful place this medical school was in Dallas and I had never heard of it. In fact, I remember when I first saw that they had accepted Joe Goldstein for a residency and it listed his institution as Southwestern Medical School in Dallas, Texas, I thought it was a bible school. You have to recall it, Kennedy was shot here in 1963, I was a second-year medical student at that time. Dallas had this terrible reputation of being sort of a far right wing city and it would have been the last place that I would have ever dreamed that I would have ended up. But Joe kept telling me what a wonderful place it was, not the city but the medical school, how exciting.

We had a chairman of medicine named Donald Seldin who was trained in medicine but had this strong belief in science and had recruited and inspired a whole generation of scientists, Joe among them. I came here for a visit and I was tremendously impressed, again by the intellectual rigour of the science that was going on in a clinical department of medicine. I decided to come here after the NIH, but the problem was my wife and I give her enormous, enormous credit because she too had grown up in the Northeast and certainly had no desire … I mean we lived outside of Washington DC at NIH, we thought that was the deep south and my other offer after the NIH, the other thing that I considered was going to San Francisco at the University of California, San Francisco, that was her favourite city and I will always give her tremendous credit for agreeing to come with me to Dallas. The promise was it was only going to be for a year, that was 36 years ago …

Never trust that sort of promise.

Michael Brown: … and we’re still here. But she fell in love with the city and we raised our children here and she’s never never wanted to go anywhere else but …

I guess it’s an easy place to live?

Michael Brown: Yes it is, it’s a wonderful place to do science because it is such an easy place to live. But at any rate, I did come here for a year and then I was so inspired by the place, it happens that Joe Goldstein was not here when I arrived. We were both at NIH together but he did an additional fellowship in Seattle, so when I came I was working alone on a sort of a cholesterol related project, not FH but a biochemical project. Fortunately I achieved some success so by the time he came, I had already at least established a certain reputation locally and so it made it easier for the two of us to work together.

Was the fact that you were here instrumental in the fact that he came back? Had you already made a pact?

Michael Brown: An informal pact. His story is that he was a student here and he was recognised as being literally a genius, while he was a medical student and doctor Seldin, Donald Seldin who is this great inspirational man who built this school, called him in as a student and said – and Joe at that time wanted to be a neurosurgeon – I hope you get him to tell the story, but he was like a second-year medical student and he was fascinated with neurosurgery. Seldin said “No, you’re not a neurosurgeon, you’re a geneticist” and Joe said “You know what’s genetics?” This is back in 1963 and there was no such thing as clinical genetics. Anyway, they arranged this training programme so Joe went to the Mass General where we met, then he went to NIH, and then he went to Seattle. The promise was that he would then come back to Dallas and start a genetics unit, so he had already promised to come back to Dallas and he basically wouldn’t let me rest until I agreed to come also.

But while we were at NIH we had seen these children – this gets now into the second part of your question of FH. We had both clinical duties and research duties when we were at the National Institute of Health and so we’re taking care of patients with rare diseases who had been referred there because their diseases were so rare that doctors of the community didn’t really know how to take care of them. We saw two children who had enormously high blood cholesterol levels, in the US units we talked about it in milligrams per desolator and their blood levels were over 1,000 milligrams per desolator, 10 times above the normal value for a child. Because of these very high cholesterol levels they were getting cholesterol deposits in their arteries and they were having heart attacks, very severe heart attacks and their hearts were failing. This was in 1969 and there was very little you could do for them. Coronary bypass surgery hadn’t been invented and certainly no-one was doing heart transplants. We put them on a zero-cholesterol diet hoping that their blood cholesterol would go down and they just ate rice for six months and didn’t budge.

So, we knew they had a genetic problem and it wasn’t due to anything in the diet and we decided that, we talked about various hypothesis what might account for this and we decided that if we were both ever to be united in Dallas that we would collaborate and try to work this out. So we actually had a plan but it was nowhere near. The idea was always that each of us would have our own separate interests but we would do this one project jointly. I think as I remember it, this was not going to be the central focus for either one of us, in fact I was working on an enzyme in cholesterol biosynthesis at the time, trying to understand it’s bio-chemistry and to isolate the enzyme and Joe, when he came here, was working on roosters, you have to ask Joe about his rooster days, but in administering oestrogen hormones to roosters which would raise their blood cholesterol levels enormously and try to figure out how that was working.

Should annoy them as well, I imagine.

Michael Brown: It was, not only annoying them, but they would run around and the image I have of Joe running down the hall chasing a rooster, I’ll never forget. But anyway, we both had separate laboratories but we decided to do this one project together in trying to figure out what was wrong with these children and the important approach we took – it was different than what people had done before – was not to study the children directly but rather to take cells from the children, grow them in tissue culture. Tissue culture was just coming in as sort of an experimental tool for human genetics. It had been used by few other people to study genetic defects prior to us and we realised that this was the only way, if whatever was wrong with the children was also manifested by the behaviour of their cells in tissue culture, then we’d be able to figure it out. I think that’s where our basic science training came in because as we mentioned I trained with a very basic enzymologist.

Joe trained with Marshall Nirenberg who was a molecular biologist, a Nobel Prize winner and the person who figured out, deciphered the genetic code. So both of us had been exposed to the most rigorous science at the most reductionist levels and we realised that if we’re going to solve a complicated problem like this high cholesterol, we had to reduce it down to something where you could really do experiments. Our whole goal was to be able to do an experiment each day and get the result before we went home that night and if we couldn’t have done that we wouldn’t have done the project. The idea was having these tissue culture cells, we could study what was wrong with them and fortunately the defect was manifest in these tissue culture cells so we were able to work out the defect. What happened then was that work expanded, the joint work, we both abandoned our separate work and just decided to work together to solve this problem.

Things went so terribly fast, didn’t they, because you got together on that project in 1972 and by -73 you had the LDL receptor concept and then in -74 you merged your labs, you just said this is working.

Michael Brown: Right. And I, at that time I gave up my clinical specialty so I hadn’t been trained in gastroenterology which is a technically demanding field. When I started it wasn’t. When I started it was a very nice sort of cerebral thing, people came with abdominal pain, or some problem with absorbing things and they had ulcers and it was all sort of a rational feel. That’s what I like about it, but over that time these endoscopes were invented, these flexible scopes where you could look into somebody’s stomach or intestines and that required a lot of technical dexterity. I was very good at it but I realised that if I were going to keep doing that, it would require that I spend many hours every week just to stay competent in it technically and so I didn’t want to do that so I gave up that specialty.

So that was becoming a technician rather than a problem solver right.

Michael Brown: Exactly, and so, even though I enjoyed it, I enjoyed interacting with patients, and it is problem solving to figure out what’s wrong with somebody and figure out how to fix, it but at any rate, that was a very big step for me to sort of give up my independent lab, give up my specialty and I remember agonising about it for a very long time. It was not easy for the two of us to establish this working relationship because both of us were sort of super-achievers. Both of us had been at the top of our classes throughout education including medical school, that’s how we got to the Mass General, you had to be at the top of your class to get to the Mass General, and we both had a lot of ego invested in science. We realised that if we were going to work together we would have to share the credit. It wouldn’t be possible for me to say oh, I thought of this experiment, and if you go back through our entire 36 years that we’ve been collaborating, we’ve never made the public statement or the private statement even between the two of us. To say oh that was your idea, this was my idea. We’ve actually worked it out in a lot of conversations as we were starting to collaborate and what we said was if I say something brilliant on a Wednesday it’s probably because he’d said something that just as brilliant on Tuesday that planted the seed. We we’re just not going to try to distinguish it’s going to be Goldstein and Brown or Brown and Goldstein and not the genius of Michael Brown or Joseph Goldstein. That was not easy to do.

No, and particular when you’re still trying to establish yourself, there must have been the thought in the back of both your minds that what may happen is that one of us gets ahead on the back of this work.

Michael Brown: We actually, and you can ask Joe his recollection, but I remember clearly there were issues like that because Joe actually was more recognised than I was in the beginning, because when he was in Seattle he had done a monumental clinical study of high blood cholesterol and delineated several diseases of which one was FH. He was recognised as an expert in the cholesterol field already and I had no standing in the cholesterol field. I had done this work with Stadtman on bacterial enzymes, so the natural tendency would have been to have given him the credit for what was going on, but we agreed that we would split invitation. If one person got invited to give a lecture somewhere then the next person would do the other one. We alternated senior authorships on the papers, if you go back to the early papers I’m always the last author on one paper and then, or the first author. I think the most important thing that made it possible was that our university recognised this as a joint effort. It’s extremely hard … For example, there are many many universities where this couldn’t happen because when it comes to making decisions about tenure, when you’re promoted to tenure, they want to know that you did x otherwise you’ll never get to be a tenure professor. In our case, that was not possible and so the school promoted us equally at every step. We were both treated almost as a single entity.

That’s amazing on so many levels. It’s amazing that you two had the maturity to adopt this approach at such a young age, it’s amazing that the university had the confidence in you. Was this driven by Don Seldin?

Michael Brown: It was driven by Seldin, yes. It was his vision that made it possible, but the only reason that it worked was that both of us had enormous amounts of respect for each other. It wouldn’t work in the slightest, if for a minute I thought he was just wrong about things and just not up to the task, not shouldering his load and vice versa. I think the idea that we both respect tremendously … Not that we agree all the time or even most of the time, I mean we disagree on all kinds of minor things, how much calcium to put in the buffer or whether to do a pH curve or a salt curve or something like that. The students who work with us know that and you know, the smart ones, when one of us suggest one thing and the other suggest another, the smart ones do both. The fact is that on the major issues we’ve always agreed and on the major steps and the directions that we take because in a long career like ours there are a lot of turns and twists that you have. Sometimes you have to abandon projects because the technology just isn’t there to get you to the next step. Other times you have to just take a leap of faith and try something new, then and we’ve always agreed on those and those kinds of questions. Sometimes one of us has to convince the other one but it works.

Forgive me for dwelling on it, but it’s such a rare thing to find such a productive and long-lived collaboration. How does it work in practice, you share the same office space pretty much, your labs are completely inter-changeable if you like or inter-twined and your students come to one or the other or both?

Michael Brown: No, we don’t take separate students. Every student basically has a do-all mentor, the labs are as you mentioned our offices are immediately adjoining with an open door in between so we’re rarely out of earshot of each other. We have joint lab meetings, we’re always present, we have lab meetings with different groups every day during the week and the two of us are always there and there’s a tremendous give and take during these meetings between the two of us, that the students get to participate in and watch. There have been long-term collaborations, the Coris are classic, they were married to each other, but to have one so close as ours is maybe almost unique.

Are you aware of anybody who has actually modelled themselves on you?

Michael Brown: No, we’ve tried, we’ve written articles extolling the benefits of it. I remember times when crucial experiments, back in the early days before we even had students it was just the two of us and a couple of technicians working in the laboratory. We would do really important experiments and the results would come off and usually in those days we were doing things with radioactivity so there would be a liquid simulation counter and the counts, it would printed out on a tape and you’d be looking at this tape as it emerged from the machine and looking at these numbers. When we saw something really dramatic … The kinds of discoveries you really like in the laboratory are ones that open new areas that you know that you know my goodness now that x is true, we can do y, z, a, b and c and d and you just see the next six months of your work right laid out before you and everything you’re going to find during that six months is going to be new. Those are rare moments but they happen and when you share that moment, when the two of you look at each other and the sense of excitement … We never had a press conference in the whole 35 years working on cholesterol which is certainly a topic of great interest, we’ve never had to brag about our work, we’ve never had to go out and give talks, pointing at ourselves as being important and the reason is because the two of us. For me the most important critic is him and vice versa and if both of us realise hey, this is really spectacular, we don’t need to tell anybody else.

I realise that you don’t want to apportion credit individually, but can you identify at least what it is that is complimentary, what each of you brings to this relationship?

Michael Brown: It’ll be interesting to see how Joe answers this, but I always think about it this way. In the beginning, when we used to look through a microscope at tissue culture cells or of sections of tissues from animals, we would go to the microscope and Joe would always immediately switch the lenses to the lowest power so he could see this broad field. I would instinctively always go to the highest power, so I could see the most intimate detail and Joe has the kind of a mind that can connect things that no-one else can connect. He’s got this very very eclectic kind of a mind and makes connections between concepts that other people just wouldn’t see connection. I’m probably more analytical in trying to really focus on how does this actually work, what are the nuts and bolts of it. But it doesn’t always work that way, it changes, sometimes I’m the guy who connects two crazy things and he’s the one who says no we’ve really got to understand how this little detail works.

But presumably you’ve learnt a great deal from each other so /- – -/ ends at the spectrum.

Michael Brown: That’s exactly, it’s funny you should say that because sometimes now I see reactions in him in the other kinds of ways that I would have reacted earlier, and I’m sure he sees that in me too. You’re right, we have learned from each other.

And broadening it to the students who work in the lab, I imagine that in some ways it’s quite an intense relationship for them to break in on. Obviously the practices of sharing credit and things must be very appealing but at the same time it’s a bit like being the gooseberry when you’re out with a couple. Do you think that’s something that you’ve addressed?

Michael Brown: That’s an interesting point, I haven’t been that sensitive to that. One thing that I have noticed, it’s been very very rare that a student will try to play one of us off against the other. I’ve always been worried that you might have a student who would come to me and say that Dr Goldstein just told me to do this, but I think it’s a stupid idea, that kind of thing. Somehow the students learn that you don’t do something like that, so they really always try to get the approval of both us and I really think that they enjoy having two opinions, kind of like having two parents, I think they like having both of us. Very frequently a student will have a conversation with Joe about something and then come in and say to me, here’s what Joe and I decided what do you think about this and vice versa. It’s funny, one or the other things that distinguishes ourselves is Joe tends to like to stay in his office and call the students in for confidences. I on the other hand, like to walk around the lab.

Could be taken as a sign of broad picture versus /- – -/ again.

Michael Brown: I guess it could be, maybe it’s related but you know, just walking up to a student and saying what’s new, what’s wrong, what’s the problem, anything I can help you with? I think that helps.

Incidentally that was Paul Janssen’s way of working, he founded Janssen Pharmaceutical, he walked round the lab every day and said what’s new to everybody.

Michael Brown: Exactly, I think you learn so much just by asking that one question because you get them sort of unexpectedly and instead of having some prepared presentation the student will tell you oh gosh, I just did this and it didn’t work and then you can sit down and go through it and figure it out. Anybody, any scientist who runs a big lab will tell you that a huge part of it is just trouble shooting, just helping the students figure out why an experiment hasn’t worked or what technique to use, or which way to go. Both of us do that and the students seem to react very well. We’ve never had a student that couldn’t adjust to this system.

We should move on, but last question on this shared lab topic, there’s a current trend for shared first authorship to try and get away from the problem of distributing experiments among individuals when they were actually done by more than one person. Do you have a view on the way to proceed there, because it sounds as if you should.

Michael Brown: Yes, we’ve done it with some of our students. It’s a little sad that the reason that you have to have shared first authorship is because everyone just assumes that the first author is the real driving force. I like the idea that some journals are doing now, which is very extreme where they actually have a footnote and say this author did x, y and z, this one wrote the paper and this one designed figure 3, 7 and 9. That’s really telling it like it is and I think that would be ok. But I just hate the whole ego thing in science. I think it’s one reason why we lose a lot of young students who don’t go into science because they’re sort of afraid, they see is as a competition and that there are winners and losers and it’s really a shame that they can’t see the excitement of actually doing the experiments.

It’s hard for people to escape the draw of the hierarchy and ticking off the next box. Moving on from that fascinating topic. You were a very productive team, have been a very productive team all these years and you’ve had, in an uninterrupted way, produced the LDL receptor concept and then the receptor pathway and then the transcription factor controlling the receptor and now a co-factor that controls the translocation of the transcription factor.

Michael Brown: Good for you, you’ve read something.

That’s just a toe in the water, but often the award of a Nobel Prize can at least knock people for six for a while but you seemed not to have suffered from that. Do you think the fact that you were together allowed you in some ways to share the load that comes?

Michael Brown: Definitely, it’s a tremendous benefit of having a partnership because as you know, all the hoopla that goes on around the Nobel Prize and the lot of distractions that happen immediately afterwards, being invited to dinner parties and be trotted out for donors. I always say that Joe Goldstein and I have been so /- – -/ more often than the Brooklyn Bridge. The fact is you have a lot of those distractions and then invitations, speaking invitations, and you know, joining boards and advisory committees and things like that, but Joe and I helped each other to keep our feet on the ground. We literary said to each other, what do we really like to do, what’s the thing that I like the most, coming in to work in the morning. What I like the most coming into work in the morning is to have some excited graduate student or post doctor fellow having been there all night and run up with some result that they’re so excited about where you can sit down with them and really talk about the implications and what it all means and where it’s going. We both decided that we wanted all these other things to interfere as little as possible and we made a certain rule. For example, if somebody calls up and asks you to speak somewhere a year from now, the tendency is always to say yes ok, but we had this rule that you always imagine that it’s tomorrow. Ok. And would you want to get on an aero plane this afternoon and fly to this far off city, no matter how enticing if it had to be tomorrow. As a result of that we’ve been able to avoid a lot of temptations.

In the last few years though, we both have developed more outside interests and we’re less intensely involved in the lab and we’re more dependent on our students and we’ve always run … People who run laboratories run them in very different ways. We’ve always had a very strong … Some people let students develop their own projects, and a lot of people think that’s the right way to teach sciences, where the students come in, give them a good environment but let them develop their own project. Our view has always been we’re committed to understanding certain things, if a student wants to come and join us and help work on that, then that’s wonderful. I’m not saying students don’t make suggestions and aren’t helpful and active participants, but it’s all along the themes that we’ve established in the lab, the things that we’re fundamentally interested in, so again that helps keep us more firmly involved in the laboratory because the goals are goals that we ourselves set. We were young, I was 44 years old and Joe was 45, we always kid each other because he’s a year older, there are five days every year, my birthday’s April 13th and his is April 18th and there are five days every year where we’re the same age and then he jumps ahead.

I like that it still matters, it matters greatly when you’re 10 but I’m glad to see it still does.

Michael Brown: Now it’s negatively, now he’s decided to be …

I know there was a positive slant on the way you said it and I’m glad to hear it. When you gave your banquet speech in Stockholm, you mentioned that there were two attributes you saw were essential to good clinical research, one is basic science and basic science training and you’ve touched on that. The other was a technical courage, the ability to go out and try new things and you mentioned that for instance with cell culture in your approach to FH but how do you go about making sure that these two attributes are taught to the medical students here?

Michael Brown: It’s very very difficult. I’m actually helping to direct what we do the MD PhD programme here where students get both an MD and PhD degree and the whole goal of that programme is to expose the students to a basic scientist working on a basic science problem, not to have a student work in a lab that’s working on a clinical problem. What I say to the students is listen, if you want to solve cancer and you go train with the best cancer researcher, in the end the best you can be is a copy of that person, you’re not bringing anything new to cancer research. But if you go out and you train in something else, genomics or biochemistry or some molecular biology and then you start working on cancer now you’re coming to a fresh approach. The MD PhD programmes are designed so that the students work with a basic science and basic scientists learn, view the world differently.

I’ve given talks to the students about this and what I say is that physicians are trained to have an enormous amount of knowledge because when you see a patient who is sick, you don’t have time to look things up in books you don’t even have time to look it up on your Palm Pilot. You’ve got to react and you have to have reflexes and you have to react and you have to be totally sensitive to all the attributes of a disease you have to know all about the disease and what fits and what doesn’t fit and medical students don’t like memorisation but in fact there’s a reason why medical students have to remember a lot because that’s what you do. You really don’t have time to think about where the gaps are in knowledge whereas scientists, a good scientist … The stuff that’s already known is not of much interest, what you want to know is what’s unknown and I would say it’s kind of like looking at a Henry Moore sculpture, the physician looks at the solid bronze and sees the facts of the thing. The scientist looks at the air spaces between the bronze and a good physician scientist is able to do both, to deal with patients and disease through this factual knowledge base and then to somewhat switch your brain in your spare time and think about what the real unknowns are and how really weak the knowledge is. Doctors have to do so many things which are really not based on the knowledge that rigorous scientists would accept but just because you have to do something, and this is the way Doctors do x, you have to learn to do that. Anyway, for Joe and me I think the fact that both of us had training in basic science labs, things that had absolutely nothing to do with human disease, really helped us enormously, and there’s no way that we could have done anything.

I imagine that the MD PhD programme forces people to take the time to take the other approach because otherwise you are just so pressured by the need to get through your exams and get onto the next stage that you just can’t afford to step away from great learning.

Michael Brown: Exactly, exactly, so they take a three or four year period out and do a thesis and really do a full PhD programme.

Is it easy to get people to sign up for that?

Michael Brown: It’s not that easy, we have a medical school class of about 200 students of whom 15 are doing this dual degree. But I think it’s the future of medicine, I think that you, when we talk about technical courage, that’s what we’re talking about, we’re talking about people who are trained enough so that they’re not afraid to reach into this tool bag of tricks that the basic scientists have given us and use those to solve a problem related to disease.

I’d like to turn to turn to a related, but slightly different topic which is your involvement in the world of drug discovery in pharmaceutical research. You’re on the board of Pfizer and I imagine given the history of your research and the fact that your research has been partly to the development of statins that you have a very strong belief in the need for basic research within the drug discovery field and I wondered how you feel drug discovery does generally in bringing basic research into the environment of industry.

Michael Brown: My view is that the pharmaceutical industry is essential in bringing basic discoveries to the bedside. There’s been a notion circulating around the United States in the last couple of years that universities should do more in developing drugs and then National Institutes of Health have something called a road map which is trying to produce funds for universities to set up drug screening laboratories and produce drugs. I personally think that’s a wasted misguided effort. It’s really really difficult to produce a drug and the hurdles are getting higher and higher because the drugs that we already have are safe and effective for many many conditions so that if you want to have the next drug it’s got to be even more safe and more effective or it has to treat a disease for which no previous drug has ever been developed, all of which are very very high hurdles. I think it requires the intense focus of pharmaceutical companies to do this but pharmaceutical companies are under their own pressures from their shareholders because it’s the lead times in the industry are so long. Between the time a discovery is made and the time it becomes a commercial product is a minimum of 10 years. From the same point of investors who are funding the pharmaceutical effort, that’s an enormous amount of time. So we have this problem.

I personally think that the system, in the US anyway, is actually working very well, because a company that finds a new drug and they have a period of exclusivity to sell that drug under patent protection and again because all the time that it takes to get the drug to market, they usually have only about 8–10 years of exclusivity before it becomes generically available and other companies can make versions of it and give it away for nothing. That means that the big pharma companies have to keep reinventing themselves every 10 years or so they can’t rest on their laurels. The pressure in these big companies to develop new drugs is just enormous. That guarantees that there’s either going to be new productivity or these companies are going to go out of business and they’ll be replaced by other companies that are more productive. The cost to society is the founding, for the first 10 years when that drug is under patent, patients and society has to pay for it as long as they believe that the benefits of the drug are worth the cost. But then after the 8–10 years it becomes generic and basically society gets it for free. I can’t think of a better system to incentivise people to discover and develop and yet force them to have to keep doing it over and over again. The question is can the companies really keep doing this and a company like Pfizer develop Lipator, the statin that lowers cholesterol, their market right now for laboratories are approximately 13 billion dollars a year. Lipator will go off patent in 2011 that’s only four years from now. They will lose 13 billion dollars worth of income. 13 billion dollars is more than the total sales of any other pharmaceutical company or close to it anyway, so the company will probably not be able to replace that drug and the company will have to downsize and will have to find new inspiration and new discoveries.

I think that the system’s actually working now, people say oh, but the number of new drug approvals hasn’t gone up. We have the genome sequence now, we have 30,000 drug targets and why don’t we have all these drugs. I think that’s what happened is that the genes have gone ahead of the physiology and we know all these genes but we really really don’t know what the proteins actually do and we don’t know where the Achilles heal of a given disease is. We’re almost in a time of trial and error, companies select the target, some receptor or some enzyme, they develop an inhibitor, they get it into human testing and then 19 times out of 20 it doesn’t do what they think and they have to abandon it. The success rate at that level is only 5% once you get even to the stage of humans. But each time we hit a try target and it doesn’t work we discard that target, we go onto the next target and actually we’re going to have a lot of great drugs but we’re in the period now where there’s a lot of trial and error, that’s basically what’s going on.

You mention at the beginning of the NIH drive to take drug discovery back into the academic lab, and that’s probably mainly a financial thing I suppose, that you try to get some of the revenue so drugs back into the public sector.

Michael Brown: They have other motivations, I think they also think that the big pharma companies only work on diseases that have big markets and that the universities will and there’s certainly truth to that.

But the need for, as you say, pharma to reinvent itself on a regular cycle means that they need a discovery engine which creates new possibilities although that very phrase discovery engine is rather worrying because it indicates that it should happen in some kind of processed way and discovery probably I suppose doesn’t happen like that. But is there, therefore, a need to take basic drug research from wherever one can possibly find it and to broaden the base of research that’s feeding into the pharma pipeline.

Michael Brown: I think that’s certainly true and I think the other side of it, at least the big pharma companies have always been dominated by chemists. These companies were all built on chemistry and the ability to make new molecules that can do impressive things. They’ve been actually weak on biology. These big companies generally, generally I mean, obviously there are exceptions, but they don’t have a deep understanding of the diseases that they’re trying to cure. I think one thing that’s necessary is to bring more basic biology into the companies to complement their basic chemistry. The biotech industry has grown up and has the image of being more creative and they certainly try more things, but there are 2,000 bio tech companies and less than 20 actually earn a profit so I’m not sure they have any special way of doing drugs.

There’s another interesting thing about drug development and discovery. We went back at Pfizer and looked at, this was done a couple of years ago, and they looked at all of their drugs that were selling over a billion dollars and at that time I think there were 10 of them, and they went back and said who were the inventors of these drugs and in all 10 cases the inventors were chemists. All of the chemists were young, they were in their early 30s when they did this discovery. The drugs had been discovered about 15 years earlier because of this time lag and get on the market and then work up to a billion dollars so these chemists had an additional 15 years to make a second discovery and not a single one of them had ever made a second discovery. And it’s very very rare in the industry to have somebody who can actually discover two drugs. Once somebody discovers one drug you might as well retire them. And so my interpretation of that is that it’s not brilliance, whereas if these people were so brilliant they made one drug, then why don’t they make a second and third and a fourth. I think there’s definitely a certain randomness here, a certain stochastic chance that any given drug will turn out to be hugely important. The story of the statins, some day when we have time, I’ll go over that story, it’s a fascinating fascinating story, but the actual discovery of the first stand was made in Japan.

Joe and I had been working on these human fibroblast tissue culture cells and studying their cholesterol synthesis and discovered the LDL receptor and realised that the receptor was regulated so that when cells had too much cholesterol in them they actually down regulated the gene for the receptor and they made fewer receptors so if you could ever deplete a cell of cholesterol it would make more receptors. If you could do this in the body, especially in the liver, if you could deplete the liver of cholesterol so that the liver would make more receptors it would take more of this cholesterol particle out of the blood and the LDL and the level would be low. Just at that moment this guy in Japan, named Akira Endo at the Sankyo drug company, discovered the first statin. He was screening moulds, extracts of penicillin type moulds, and he found this compound and it blocked this enzyme HMG-CoA reductase and stopped cholesterol synthesis. We immediately wrote to him and said please send us some of this. because we wanted to see whether it would cause the cell to make more LDL receptors in this tissue culture system and he actually came to the United States to a meeting on drugs affecting lipid metabolism and gave a talk. The meeting was in Philadelphia and we invited him to stop in Dallas on his way back to Tokyo and when he stopped in Dallas on his way home and we met him he was really dejected and we said why, he said no-one came to my – his English isn’t perfect but in translation – you know, no-one came to my talk. Why is that, nobody seems to think it’s important that you can stop cholesterol production. At that time the whole field was interested in these resins that actually bind bile acids in the intestine and remove them from the body. But we were very interested and so we arranged a collaboration and we worked together and showed basically that when you trigger this regulatory response that leads to an increase in LDL receptors.

That was the first paper published outside of Japan on this class of drugs and we knew it was very important. And it just happened that Roy Vagelos was the head of science at Merck. Vagelos is a scientist. He was a member of the National Academy, he was chairman of biochemistry at Washington University at St Louis but then he’d gone to Merck as their head of drug discovery, but he had worked in the field of lipids. He had studied fatty acids and we studied cholesterol, so we knew him and we worked with him and helped him and his colleagues to develop this drug because we really thought it was important. Then, ten years later in 1987, it gets approved by the FDA and by that time the clinical trials had shown that it was very effective in lowering cholesterol, but the question of safety was really, because you can only test these drugs … At that time it would have been tested on maybe 5,000 people before.

I remember just for the first year after it came on the market … Every time the phone rang I was afraid of somebody saying oh we just found this horrible side effect and everybody was just very fortunate that the drugs are remarkably safe. But there was no way to predict that in advance. How do you know that you wouldn’t have had liver failure? A lot of our friends said oh this is terrible because cholesterol production is so important in the body and if you block that pathway you’re going to definitely have some terrible side effect and we certainly didn’t know that it wouldn’t happen, but we were hoping it wouldn’t.

The story illustrates at least two things, one is that the importance of biology and the importance of understanding the relevance of the target and also the ability to take risks, the ability to have enough programmes going at once that if you do find that it was a mistake to block cholesterol production you can abandon that approach.

Michael Brown: You’re very perceptive. That risk thing is exactly right, and I’ve noticed, I’ve known this man Roy Vagelos for years and I have always noticed that whenever he takes a risk he has an alternative strategy. It’s never the final risk that will bury the company. I think risk taking is part of the business and I personally think that people who run these big pharma companies are pretty courageous folks even though the actual reputation of the pharma companies now is very very low. Why they’re considered to be profit mongers and inventing diseases …

They face an enormous public relations challenge these days.

Michael Brown: Enormous. But in the end, I think society’s going to have a lot of new medicines that do things that we can only dream, even now certain kinds of leukaemia that we had thought were incurable are now converted at least into a chronic disease. Anybody old enough to remember AIDS in the 1980s knows what a death sentence it was and the fact that the industry has produced drugs that now convert it into a manageable chronic disease. We get very little credit from the public but these are not easy things to do and science has done it.

One last question on the pharma, there’s a large growth in the field that is called experimental medicine, these days, but experimental medicine is basically what you’ve been talking about all the time isn’t it?

Michael Brown: Yes, they’re calling it experimental medicine or translation or research. One of my pet peeves is that people talk about translational research and they’re always talking about taking basic discoveries and translating them to the bedside. But I think that real medical research always starts at the bedside. Starts at the bedside and then it goes to the basic scientist and then it goes back to the bedside. I point out that all these basic scientists, a lot of them are trying to cure three diseases of the brain, Alzheimer’s disease, Parkinson’s disease, Huntington’s disease. Why do we know about those diseases? Because there were three doctors named Parkinson, Alzheimer and Huntington who discovered them. There would be no way that a basic scientist would even know what a disease was unless there are perceptive physicians out there, describing them and trying to figure out where the actual real central defect lies. I think this interaction between people that understand medicine and people that understand basic science, that interface is the real place where the action happens. Joe Goldstein and I were lucky to have been able to stay in that interface for 35 years and it’s been a great interface to be in.

Yes indeed. So to close, just the question of what will happen to the Brown Goldstein environment as time marches on. It sounds like it’s not possible to conceive of bringing in two new people to take over those roles.

Michael Brown: I don’t think so. First of all, we hope to continue to do this for as long as we are both mentally competent. As you can imagine we’ve both had lots of offers to do other things, but again we’re still getting kicks out of doing it. Now we’re seeing something else because some of the junior people who started out as post doctor fellows with us have now become independent and some of them have actually stayed on our faculty in our department. They’re working on their own, we’re not authors of their papers and yet they have enough confidence to confide in us and tell us their results and ask for guidance. I’m getting a tremendous kick out of just /- – -/ and guiding these young people and so maybe that’s how we’ll fade out and give me grandfatherly advice.

Not that’s imminent at all, but do you have a plan to retire on the same day?

Michael Brown: Hopefully we’ll both do that, whenever that happens. It’d be very hard to think. I can say this, if for some reason something happened and Joe wasn’t there, there’s no way that I would continue to do what I was doing, I’d have to stop.

Well, particularly given the next day rule to agreeing to do things that you referred to earlier, I’m extremely grateful that you gave up the time to do this interview.

Michael Brown: Thank you. I think it’s very important and I’m grateful to you for doing this series. I think this kind of record even if three students ever look at it, might still influence somebody.

I think there’s some very inspirational stuff in there.

Michael Brown: Ok, thank you.

Good thank you very much indeed.

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