Talking with Professor of Pediatrics, Genetics and Medicine Harry (Hal) Dietz

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Interviewer: The whole concept of understanding innovation is a murky one. So what I would like to do is zoom back to the very beginning, to when you were a child or a young student, to find out how you approached learning, problem solving, and the idea, even at an early age, of coming up with something new.

Hal: One characteristic that I can describe about myself as a child was general curiosity. I wondered how things worked. In fact, I frequently got in trouble for taking apart the toaster or the radio, though that type of probing was actually encouraged rather than discouraged. I also had a tendency to find mentors from an early age. I developed true friendships with some of my teachers in elementary school and in junior high school. That really allowed me to have greater access to resources and to knowledge that would allow me to probe things that I didn’t understand. My family had a philosophy that curiosity should be encouraged, even if it was sometimes destructive.

Interviewer: So you were raised in an environment where question asking was a way of life?

Hal: Yes, and in a family that valued questioning authority. So we were never disciplined for asking the question why over and over and over again, even to basic tenets that everyone agreed were true. In fact, my father used to push us to probe the basis for something, rather than to just accept what is already known.

Interviewer: What were your parents’ backgrounds that led to fostering that sort of environment?

Hal: My father was initially trained as an electrician, but he ended up working in advertising. Even so, he really kept up with developments with regard to computer science and was always a tinkerer. My mom was a stockbroker and later an elementary school teacher. Neither of them, due to financial circumstances, had the ability to pursue a classic academic path of training, but both were very creative in their professional endeavors and very successful on that basis.

Interviewer: When you were growing up, a high school student for example, did you naturally gravitate toward a particular discipline?

Hal: I would have to say that math and science was my area of true love. Even from an early age, part of my recreational activity was to read about theoretical physics. I didn’t understand it, but I greatly enjoyed what I could understand. There was also the intrigue that related to how science was performed and how science was rewarded. I can say, from the age of 10 or so, that Einstein was my idol.

Interviewer: Many people think of science as a fairly dry, quantitative pursuit. But it seems like you naturally viewed it and grasped it as something more than that. Who might be the best example of a scientist that combined creativity with a scientific pursuit?

Hal: Well, I think Einstein was an excellent example to illustrate how unbridled creativity could work. He was not an experimental physicist but a theoretical physicist, so he used to just sit in a chair and think deep thoughts and in that manner uncover fundamental principles of nature. The way that he did it, and the way that many other successful scientists also found progress, was to find conundrums, find facts that didn’t add up and then to challenge the broadly held basis for those facts. Relativity was a discovery that was made based upon Einstein’s challenge of accepted doctrine, because accepted doctrine did not reconcile really fundamental problems in physics, as we observe it occurring in nature.

Interviewer: Do you think that being able to challenge accepted doctrine is an important attribute for a creative individual or an innovative environment?

Hal: Creativity can derive from many sources. In my own experience, finding problems and finding issues that just don’t add up has also been powerful. In my work to try to understand a disorder called Marfan syndrome, we assumed that it was due to a defect in the body’s connective tissue, the material between cells that gives the tissues form and strength. Based on the progress in the study of other connective tissue disorders, it was widely believed that many or all of those conditions would be explained by an inherent weakness of the tissues due to the deficiency of a structural protein. In fact, in 1991, when we identified the gene for Marfan syndrome, we realized that gene encoded a structural protein called fibrillin-1.

That was an answer, but in many ways it was a very disappointing answer because we didn’t know—and we still don’t know—any mechanism to change the inherent quality of the connective tissue throughout the body. If you wanted to try to help someone with Marfan syndrome, there was no clear path forward. It’s sort of like a house with a rotten frame. There is no way to make it better, other than tearing the house down and starting again.

I also recognized that there were many features of Marfan syndrome that were difficult or impossible to explain, based upon simple weakness of the tissues. For example, why should weakness of the tissues cause the bones to grow excessively? Why would weakness of the tissues cause the low muscle mass and low fat stores that are seen in Marfan syndrome? The weakness model explained aortic enlargement, meaning a failing blood vessel in the body that is exposed to stress. The weakness model explained destructive emphysema, again due to wear and tear on a weak tissue. But that model just simply couldn’t reconcile a number of other important findings. That is what really pushed us to ask what else is going on. There is a missing part of the puzzle, so what might that be?

Another factor that provoked us to think more broadly was an encounter with a father of a patient. He was the first one to say, “Dr. Dietz, you are describing this weakness of the tissues. Why are my son’s fingers so long? Why does that lead to facial abnormalities?”

So, I think it’s a combination of a mindset where I was already beginning to question authority and a receptiveness to a perspective for science that was not traditional and the father of a patient, a layperson, that really crystallized, in my mind, that we needed to back away from all of the scientific approaches that we were taking to understand weakness of the tissues and look for a reconciling new model.

The real breakthrough came when we asked a really simple question: “What else does the fibrillin 1 protein, the protein that is deficient in Marfan syndrome, what other protein in nature does it look like?” It was sort of a Hail Mary exercise.

The answer came back that this fibrillin-1 protein looks very much like a second family of proteins called the latent transforming growth factor beta binding proteins. Transforming growth factor beta, or TGF-fl, is a growth factor that instructs cellular performance. That could underlie overgrowth of bones. It could underlie altered facial development. So, it was a weak link, but it had at least the potential to explain what was left unexplained by the weak tissues model.

Fortunately, at that moment in time, I also had discretionary funding that allowed me to take risks. It was not NIH funding that was specifically dedicated to a well-developed hypothesis-driven next logical step series of experiments. It was money that allowed me to take risks, to try something new.

Interviewer: What stage were you in, in your faculty development?

Hal: At this point, I was a junior-to-early-mid-level faculty member. Very early on, I was fortunate to receive one of the first, if not the first, Richard Ross Research Grants, which allowed me to take some risks and to avoid lots of clinical responsibility. Very shortly thereafter, I was also appointed as a Howard Hughes Medical Institute Investigator, again giving me discretionary money. At the same time, a very important benefactor named Mr. Smilow gave money to form a Marfan Research Institute at Hopkins, with me as director. So, from all of those sources, I had money that I could play with. Also, early in my career I had made a long-term investment in Marfan syndrome and became a very public figure for the National Marfan Foundation, so they decided that I was someone worthy of investment. They figured this young guy is around a lot, he is a constant presence. He is even here in the dark days, when we can’t find a path forward, when it looks hopeless, because it is simply a structural weakness issue. He is staying with us, we’ll stay with him, and they gave me discretionary funding to take risks.

All of those sources added up to money that allowed me to say, “Well, I’m not sure about this TGF-fl hypothesis. But, unless we find something new, there is no path forward.” It turned out that we learned that excessive activity of this TGF-fl molecule was the driving force in many important aspects of the Marfan condition.

The way that we learned this was through the use of a mouse model for Marfan syndrome. We learned that in fibrillin-1 deficient mice that still had inherent weakness of the tissues due to a deficiency of this structural protein, you could prevent aortic aneurysm. You could prevent emphysema. You could prevent skeletal muscle issues simply by blocking TGF-fl.

So, if we injected the mice with a TGF-fl blocking antibody, aortic growth was perfectly normal. The structure of the aortic wall, as assessed by microscopy, remained normal over time. The skeletal muscle became bigger and stronger. The lung proved resistant to break down to emphysema. It suggested that we could bypass the major primary problem that is a deficiency of this structural protein and still make a big difference for patients, simply by targeting TGF-fl activity.

Interviewer: I’m sure that this notion of risk taking is crucial to how you were able to do this. In hindsight, it doesn’t sound risky. Maybe that’s how a lot of new knowledge evolves. Once it becomes established, it’s the new standard. That’s how knowledge accumulates. But, I would say that maybe the prevailing intellectual climate today, due to funding concerns and other issues that impact our ability to take risks, is crucial in terms of fostering innovation at large. What is your take on how younger scientists and physicians should approach this topic of risk taking in their work?

Hal: It is very important for young people to focus. If I had not allowed myself to become an authority on Marfan syndrome, the question from that father would have fallen on deaf ears. If I had not committed to Marfan syndrome over the long term, I would not have the funding from the National Marfan Foundation and from Mr. Smilow and from other sources to take a risk. You have to balance your lab’s research initiatives with relatively safe questions that will allow you to maintain productivity, and that will allow you to be competitive in your next grant cycle.

But I think that you also need to look for opportunities that will change the world. You need to have leadership in your division and your department that not only allows but also encourages risk taking, and that lets you know that if you try and if it is a good try and it is a good question, that you will be rewarded, even if it’s not successful.

Interviewer: Did you feel that you had that support when you were going through the process or that it was against the tide?

Hal: I had tremendous support, but I think that that support related to wise decisions that I had made along the way in my career. At a certain point in time, I was associated with one division that was an excellent clinical division. It had wonderful leadership. It was really a nurturing, caring leader, but that leader simply didn’t understand what it took to be successful in basic science. I had to make the tough choice that I was going to walk away from that division and find a home that understood what I was trying to do and that understood what I needed to be successful.

My ability to make that switch really gets to an important, fundamental characteristic of this university. Imagine this: I was a clinical pediatric cardiologist; I knew that A went with T and G went with C in the DNA code, about 50 percent of the time. I had no research background at all. I walked into the office of the chair of Genetics and said, “I’m a clinician. I have a deep commitment to try to help a specific patient population. The cystic fibrosis gene was just identified. So I know that the methods are available. I want to find the gene for Marfan syndrome in order to understand its pathogenesis, the sequence of events leading to disease manifestation. My ultimate goal is to help these people, but I need your help. I know nothing and I have lots of samples. They are very meticulously characterized at the phenotypic level, but I don’t know any genetics.”

I can imagine, in fact I know, that at many other places I would have gotten the answer, “Well, isn’t that quaint? Here is what you can do for us. Give us your samples. Give us your clinical data. Act in a marginal supportive role, but basically get out of the way.”

Instead, within about 20 minutes, this chair, Haig Kazazian, had assembled a group of 10 people in his office, who were excited at the prospect of allowing me to succeed. There was no discussion of who would get credit. There was no discussion of where the funding would come from. It was just a group of people who were visibly excited at the prospect of helping a young person launch a career in a new discipline.

You might say that that was a single time and circumstance, but throughout the 25 years or so that I have had a research career at Hopkins, I have seen that same scenario play out over and over and over again. There’s something about this place that prioritizes knowledge and not credit and not other practical obstacles.

What I have observed is that Hopkins makes long term investments in people. When people are recruited, they are recruited with the expectation that they are going to be around for the next 30 years. There is not this live or die philosophy that says, “We are going to toss 10 of you into the ring and two of you are going to succeed.” What I see is people really getting the quality commitment of time and resources and excellent intellectual environments and lab space that will allow them to succeed if they work hard.

Interviewer: How do you think we retain or encourage or improve that type of environment? It sounds like an almost intellectually pure pursuit of knowledge. It’s never that pure in the sense that it is a functioning enterprise that has all sorts of other agendas. I would personally agree that that is our main mission. If we are not here for that, why are we here at a place like Hopkins? But I sometimes wonder whether or not that foundation is being eroded a little bit. What do you think about the idea of promoting them and retaining them?

Hal: During my career, there have been flush times with regard to research funding, the research funding environment, and there have been lean times. We are going into what I consider to be a major lean time. The university will need to further prioritize people and programs, rather than simply physical infrastructure, to promote the ongoing success of junior investigators. We are about to be tested in a major way. Given our track records, I have optimism, but I’m waiting to hear what the bold response will be. I have not yet heard that articulated. I know that the university has put a lot of emphasis into increasing endowments and generating potential funding sources from other than the federal grant support that would be considered more routine.

I think that people who get what young people are trying to do, people who really understand the process, the path, and the obstacles should be part of the leadership that is deciding how those funds will be allocated. We continue to attract the best and the brightest young people into our training programs, and Hopkins has a long track record of keeping its best people, which is different from other universities where there is some negative connotation to recruiting from within. I think that we do that frequently. I think that we do that well. I think we benefit from that practice.

What I hope to see is the development of dedicated programs to help young people succeed through lean times. It would be nice to see the development of communal initiatives. Right now, if I had to broadly characterize research at Johns Hopkins, it more or less takes the model of being many successful small businesses. What I would love to see is Hopkins plant its flag in some major initiative that would require the expertise of many people from many disciplines and, at the same time, would benefit the career development of young people from many disciplines.

The new era of harnessing the power of the human genome and its application to health has the makings of something bigger than any one person or group. What I would love to see is a very creative, bold initiative by the university to tackle that problem, a problem of that magnitude, in a very comprehensive, creative, and purposeful way.

Interviewer: You have talked about the kind of innovation that seems to evolve really over years and is the cumulative result of many, many years of effort and less about things that are sudden flashes of brilliance or insight. What I infer from your words is that love is a big component of your ability to innovate, because you loved your topic area. What was it about your work in Marfan syndrome? What captivated you early on?

Hal: It gets back to my motivation for choosing a research career fairly late in my career. I had been trained as a clinical pediatric cardiologist. Because of the pioneering work of Victor McKusick over the last 50 years, this place had become the center of care for Marfan syndrome for people all over the world. As a result of that, as a clinical cardiologist, I was caring for people with Marfan syndrome and I was becoming emotionally attached to my patients. That is a trait of mine, for better or worse. I was immensely frustrated that clinical protocols that were being applied didn’t appear to be making any difference in their lives.

It was really because of the individual people and individual stories that I felt motivated to leave clinical cardiology behind and to learn the new discipline of genetics. My purpose was to make life longer and better for that patient population. That has been my motivation ever since. I go to sleep at night, every night, thinking about specific patients and families that I worry about and that I care for. I get up every morning with the intention of trying to find something that will make life better for them.

That was enough to sustain me through low points in my research cycle. When we thought this was a structural deficiency of the tissues and there was nothing you could do, those were truly dark days. I was having trouble writing grants to justify further investment in that research field.

It was this realization that there is more to this, that there is something that we can manipulate, and that we can even manipulate it after birth and it will make a difference that really fulfilled my initial and ongoing mission to help these people.

I think everyone has his or her own personal basis for passion, but I think it is important that everyone be passionate about what they do. That will force you to think differently. I think it will force you to take risks. I think it will force you or, perhaps better put, it will allow you, to capitalize on opportunities for innovation.

Interviewer: It has been a story of hope, that’s the way it seems to me. As a last, parting thought, what do you hope for in the future in terms of the development of your field?

Hal: We have played a pretty big role in changing the philosophy not only about connective tissue disorders but also about how genetic disorders can be treated in general. So, the old belief was that you had to replace the protein that was missing and that was the only successful path forward. That largely relied on the discipline of gene therapy, which I think still remains a very promising discipline, but it’s got problems, there are big obstacles to overcome. The new view is that you don’t have to hit a home run to make a difference. Even if you don’t correct the primary defect, you can change the course of disease for the better, simply by nudging downstream consequences of that primary defect.

I have already seen that play out in other connective tissue disorders and now in many different types of genetic disorders that have no inherent connection to Marfan syndrome. I think people are truly thinking a bit differently, based upon our experience. I hope to see that grow. I hope it’s going to make a big difference for many different patient populations.

But my personal goal? Sure, I would love to cure cancer. But if I just help Montie and Blake and Steven and my other patients—the people who I care for and for whom I care—that will be enough. I think we have to fight little battles. Every time we win, we have to rejoice. We have to derive personal benefit from that, because that’s what’s going to sustain you to make the next discovery or chip away at the problem a little bit more.

Interviewer: There is so much wisdom that you have to impart just to the university at large, especially also to young faculty members who are trying to figure out how to have innovative careers so that they can look back and think about what helped them along the way. Is there anything else you want to add, possibly that I haven’t asked you about or we haven’t touched upon?

Hal: No. I really think we covered a lot of territory.

Interviewer: Thank you so much for your time. I really appreciate it.