Daniel Kim ’19

One of the body’s most potent signaling molecules is not a complicated chemical or protein, but oxygen. Oxygen-sensing pathways play a critical role in the processes of cell survival, ranging from cardiovascular, neuronal, and hematological homeostasis to the maintenance of tumor cells in a variety of solid epithelial cancers. Yet the mechanism that detailed exactly how oxygen was involved in cell survival remained unclear until even 20 years ago. Professor William G. Kaelin, one of the leading pioneers of this field, was recently awarded the 2016 Albert Lasker Basic Medical Research Award for his work elucidating the molecular mechanism of oxygen-mediated pathways. Unlike most full-time researchers, however, Dr. Kaelin forwent the classic route of pursuing a Ph.D. degree, instead opting to prepare for his career at medical school. Shortly after Dr. Kaelin’s honoring at the 2016 Lasker Award ceremony, THURJ writer Dan M. Kim had a chance to speak to him about how he went about solving this particular puzzle, and how his unique story intertwining the worlds of research and clinical medicine led to his discoveries.

 

DK: First of all, what was your immediate reaction to winning the award?

WK: Well, of course I was very happy and proud and grateful, lots of positive emotions involved at once. The Lasker Prize is one of the world’s great scientific awards and I was very proud to win it. I was also very happy because when you win such prizes, it reflects upon all of the people who’ve worked for you and with you over the years.

 

DK: Definitely, and congratulations again.

 

WK: Thank you.

 

DK: You received it on your work on how core molecular pathways are influenced in the presence of oxygen. Do you think you could elaborate more on what projects you did specifically?

 

WK: Sure. When I was starting my lab in 1992, one of the important decisions when you start your lab is “What are you going to work on?” I was looking for something that would start to help distinguish my work and the work I had done as a postdoc. So, in the summer of 1993, a paper appeared in the journal of Science describing the cloning of the von Hippel-Lindau tumor suppressor gene, or at least a partial cDNA for what turned out to be the VHL gene. And [the authors of this paper] quickly confirmed that this was the gene that when mutated gives rise to a hereditary cancer syndrome, now known as  VHL disease.

I thought for many reasons that this would be the perfect thing to work on. One of the more important reasons for studying VHL is as follows: so at that time, a lot of the molecular excitement for oncology focused on cancers that were really fascinating, but frankly were from an epidemiological point of view fairly uncommon. For example, Burkitt’s lymphoma would be an example of something that was sort of “hot” at the time, but [it] was, at least in the USA, not a public health menace, and  if we were really going to make a dent in cancer mortality, we had to start tackling the more common epithelial cancers.

When I was at Hopkins, there was a young faculty member named Burt Vogelstein who was starting to make progress applying molecular techniques to colon cancer. So for a variety of reasons, I thought that the time was right to work on a solid epithelial cancer. Since kidney cancer is one of the diseases linked to VHL disease, you could sort of assume that the VHL gene would play an important role in this cancer.

I was clinically trained: I was Board-certified in internal medicine of oncology and I did a chief resident year at Johns Hopkins so I knew a fair amount of medicine. And so I knew the clinical features of VHL disease backwards and forwards. I knew, for example, that VHL patients developed kidney cancers, hemangioblastomas, pheochromocytomas, and a few other less common neoplasms. Another thing about VHL-associated cancers is that they are very rich in blood vessels, so we hoped we’d learn something about how cells regulate angiogenesis, which was a very hot topic in the 90s. A final interesting clinical feature of VHL disease is that the tumors occasionally produce the hormone erythropoetin and stimulate red blood cell production. he fact that the three main VHL-associated cancers share this property was always sort of conspicuous to me.

Angiogenesis and erythropoiesis are normally stimulated by hypoxia (low oxygen). [We hoped], therefore, that by studying VHL we would learn something about how cells and tissues would respond to oxygen. Fortunately, that turned out to be a good path to pursue. We began by showing that the VHL protein interacted with several proteins linked to ubiquitin-dependent proteolysis. It started to look like the VHL protein was part of the ubiquitin ligase complex. In parallel, we could show in the laboratory that cancer cells lacking the VHL protein produced so-called hypoxia-inducible mRNAs such as the mRNA that codes for VEGF, at very high levels, irrespective of oxygen availability. Without the VHL protein, you couldn’t sense oxygen anymore, and you would respond by pumping out these hypoxia-inducible mRNAs. Between our lab and several other labs including my co-awardees, we were able to show that the pathway intermediary was HIF, which is a transcription factor that regulates such hypoxia-inducible mRNAs. The pVHL ubiquitin ligase complex destroys HIF when oxygen is present.

One of the final pieces of the puzzle was how VHL knows whether oxygen is or is not available and hence whether or not it should destroy HIF. That’s when Peter Radcliffe’s group and our group working independently discovered that this signal was an oxygen-dependent post-translational modification of HIF that served as the signal for VHL to bind to HIF.

So now, with this circuit in hand, there are several places in the pathway where you could potentially think about drugs where you could make the pathway more active or less active. It’s pretty clear that in some cancers you want to block the pathway. It turns out, fortunately for us, that by the mid 90s there were drugs already being developed to block VEGF, a direct HIF target. We now have six of those approved for kidney cancer. The responses can be quite dramatic, but the patients unfortunately eventually relapse, so of course we have to do better. But at least we have a foot in the door. And now, there’s actually a drug in development in Phase II trials that directly inhibits HIF itself, specifically HIF2.  Conversely, drugs that stabilize HIF look promising for anemia and diseases such as heart attack and stoke.

 

DK: While you were talking about your project, you mentioned how your background as a doctor helped you be able to notice certain things. What were your years at Duke and at Johns Hopkins like, in becoming a doctor?

 

WK: I feel as though you can always look back at your life and assess what things you did right and what things you did wrong. Amongst the things I did right: taking classes in mathematics and philosophy. The most important thing you learn at a younger age, I think, is how to think clearly and critically, and that never goes out of style. I did get a degree in chemistry, in addition to mathematics. I gravitated more towards the sciences that were more at the time quantitative and more conceptual. So I actually liked physics and chemistry more than I liked biology. Now you have to remember, especially then, biology was much more descriptive than it is today. I think biology’s catching up, but at that time, a lot of biology was in my opinion descriptive.

The second thing I did was I worked in an independent study project in a chemistry lab when I was an undergraduate. There I made a mistake: I picked a lab that had a strong track record of placing students into medical school. That turned out to be a very bad way to pick a laboratory, because I wound up working on a project that I’ve described as being “uninteresting, unimportant, and undoable,” all of which was true. I really floundered in this laboratory because my mentor wasn’t around very much, and what I was doing wasn’t very similar to what anyone else in the lab was doing, so I just assumed at that point that I wouldn’t be a scientist because I couldn’t do it. The lessons there: one is that if you’re struggling in a lab, it could be your problem, but it could be that the lab is the problem. Secondly when I mentor people, I’m very mindful that the most important thing for a young person in the lab is to get a taste of something working in their hands so their imagination can start to work and they can think about what they can now do. Another thing I learned from this is that it’s really important to step back and say “what’s the question this project is addressing?” I meet scientists from around the world who are perfectly competent technically, but in some cases in my opinion are asking really pedestrian boring questions. Admittedly, some of this is a matter of taste, but that’s why you’ve hopefully trained in good places with people from whom you’ve acquired some degree of taste.

So in part because of that lab experience, I wanted to go to medical school, fully expecting I was going to be a clinician rather than a scientist. In hindsight, that was good because I really jumped in with both feet. That’s one of the reasons why I did a chief resident year, and it served me very well in multiple ways. Knowing a lot of clinical medicine has helped me think about VHL disease and has helped me in other problems we’ve worked on in the lab. It’s helped me interact with our colleagues and biotech and pharma, because I understand the clinical needs they’re trying to address as well as the science that they’re trying to do.

Through sheer luck, I wound up in David Livingston’s lab, when I was a postdoc and everything sort of clicked. Maybe in part because my expectations were so low, I was very elated when things started working and I found out that I actually could do this.

I think there are some valuable lessons from my postdoc with David, in addition to what I just said. I learned that sometimes being a little naïve can be good. Because when you know too much, you can always think of reasons why your experiments are going to fail. So the fact that I was so wide-eyed when I started in David’s lab was very good because I didn’t spend time talking myself out of doing experiments that “shouldn’t work”.  I simply tried them, and fortunately, some of them actually worked. Secondly, because I was so naïve, I didn’t know the classical solutions to certain problems, so sometimes I invented my own solutions, and sometimes the solutions I invented were actually pretty helpful. I think that’s why sometimes certain types of experiments are best done by graduate students or people who are relatively green, rather than 5th year postdocs who are really jaded in their thinking. I think it’s really important to sometimes just step up to the plate and try.

 

DK: Do you think having taken a lot of courses in your undergraduate years such as mathematics and philosophy, that those were a big part of your thinking?

 

WK: It was. I think throughout my career as a laboratory investigator, you see how thinking clearly and quasi-mathematically is very helpful. For example, when people show me results that are correlative in nature, I might push them in terms of “okay, A correlates with B, but can you say A causes B? Can you say B causes A? Both? Neither? Does this mean that A is necessary for B? Does this say that A is sufficient for B? Etc.?” You’d be amazed at how many people get all flustered at this point, because they don’t actually know. They’re used to using soft, wishy-washy language, “this is associated with,” and I want to know “No, what does this experiment really mean?” There’s a certain logic and a symmetry to experiments that are laid out very nicely, in terms of positive and negative controls, and just through my mathematical training, I see experiments in that way.

One of the reasons I went into medical school was that I liked interacting with people and I thought this would be a way to do science and also interact with people. And I liked clinical medicine, but… There’s the old saying: “common things are common.” If you’re a clinician, even if you’re at a referral center, you’re going to start to see the same patterns over and over again. And some of the puzzle solving in medicine was becoming a little less exciting for me. Now, you can live for the occasional rare case of this or that. We used to say that there are horses, zebras, and unicorns: most of the time when you hear hoof-beats, it’s horses; occasionally it’s a zebra; and it isn’t very often that it’s a unicorn. I think when people are training in medicine, it’s important to realize that common things are common. Obviously, medicine is a wonderfully noble career, but just to be aware that you may wind up seeing certain things over and over again. I also thought that especially in a field like cancer, it was clear that the only path forward was to have a much deeper understanding of the disease and to come up with better therapies than the things we were using when I was a fellow, which always felt like fixing a television set with a hammer.

 

DK: Do you still see patients?

 

WK: No, I stopped seeing patients some time ago because I promised myself I would not allow myself to become the type of doctor who was still wearing a white coat when he probably shouldn’t have been. When I was younger I always thought to myself that my patients were lucky to have me as a doctor. I thought if I couldn’t look myself in the mirror and say that anymore, I should walk away.

 

DK: Was there any point in time when you were doing both?

 

WK: Yes, there was a time when I was spending a month or two a year attending patient service, as well as moonlighting in a local intensive care unit.

I like clinical medicine; it’s got its own set of rewards. Frankly the reason why a lot of physician-scientists give up becoming scientists and instead become physicians is because firstly, it’s a rewarding career, and secondly, there are unique frustrations to working in a laboratory. You can have a series of wonderful, lovely, compelling hypotheses that all turn out to be wrong. Or things that should work technically that don’t. Or peer reviewers who don’t like your latest grant or your latest paper. All sorts of frustrations. And then you put that white coat on and you walk into an exam room and suddenly you’re a god again and you’re completely in control of the situation and you know what you’re doing and you’re getting accolades from your staff and patients and their families and you think “wow, this doesn’t feel quite so bad.” There were times when I said “look, I like being a clinical doctor, I worked hard at being a clinical doctor, maybe I should be a clinical doctor.”

Again, I don’t mean to disparage the profession in any way. It’s an incredibly noble profession, and I have nothing but admiration for my clinical colleagues. I certainly appreciate the care they have provided for my family over the years, but that’s the reality: if you want to be a scientist, you have to really understand that there are times that are quite frustrating. On the other hand, there are also unique rewards of being a scientist, and when you look at a result or think you understand something that has never been understood before for the first time, and that you’ve solved a particular puzzle, it’s a particularly gratifying feeling. If you also on rare occasion are lucky enough to understand something that now enables for the first time a new therapeutic approach, for example, that’s also tremendously rewarding. To have even some minor role in the development of a new drug that gets approved is really quite exhilarating.

 

DK: Along the same lines – a lot of students at Harvard are interested in science, but aren’t really sure if they want to do something in the clinical field or something more research-oriented. You touched on this before, but do you have any advice for such students?

 

WK: Well, I always caution that most people if they’re well-adjusted can rationalize why what they did was the right thing for them to do. So you always have to be a little bit careful when people project onto others to do what they did. I do think everything else being equal, any year where you’re surrounded with good people, learning lots of things, and you’re getting paid and have a roof over your head is a good year. So I have no regrets about how I spent my time. Not burning bridges is also a good thing. If you are thinking about medicine at all, and if you are thinking about science at all, certainly going to medical school in my opinion opens lots of doors for you, only one of which is to be a practicing physician. It gives you a very good base to do biomedical research. I think the question for students is “Do I get an M.D.-Ph.D., or do I get a straight M.D.?” I applied to a couple M.D.-Ph.D. programs and I didn’t get in, but in hindsight I think it was fine, because I’m happy I trained to be an M.D. thinking I was going to be a clinician, and then looped back in to become a scientist later on, and there are certainly many people who have done that. Both are possible. One advantage of getting an M.D.-Ph.D. is that most M.D.-Ph.D. programs still come with a fairly sizable stipend. I was fortunate to be able to pay my medical school tuition, but I know that there are some people who graduate from medical school with a fair amount of debt, and they carry so much debt that they’re almost obligated to become practicing clinicians.

When in doubt, do something where you’re going to learn to think. Think critically. And also, sometimes it’s good to challenge yourself and get outside your comfort zone and maybe take some courses that teach you different ways of thinking.

 

 

 

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