On the first day of medical school at University of California (UC), San Diego, I met Professor Eugene Braunwald, and that pretty much set the course of the rest of my professional career. He presided over and presented in a course called Introduction to the Clinic which, in that year, highlighted a case of rheumatic heart disease that grabbed my imagination because it united infection, physiology, pathology, socioeconomic considerations, medical management and surgical treatment all in one package. The combination sold me on the potential of cardiovascular medicine, and then I went to work in Prof Braunwald’s group, and started to work on experimental myocardial infarction. I never looked backwards.
From Berkeley to Boston
As the founding chairman of the department of medicine UC, San Diego’s new medical school, Prof Braunwald put a very strong stamp on the value of research excellence, emphasising cardiovascular and pulmonary considerations. We students understood that, before us lay a great opportunity not just to master facts, but to add to knowledge in a way that would improve understanding of disease and improve patient care.
This environment was exciting, particularly because I am, by nature, a bit of a contrarian. I was born and bred in Berkeley, California, steeped in the world of not accepting the status quo unexamined. In the US, we complete general studies before beginning professional school. I earned my bachelor’s degree in biochemistry and French literature in 1969 at the University of California, Berkeley. The ‘people’s republic of Berkeley’ fostered an anti-authority streak and was in the vanguard of shaking off the student torpor of the 1950s. I think being part of that experience is one of the reasons I’ve never been content to jump on the bandwagon, but have always sought my own path — including in my research career.
As a medical student and then as a postdoctoral trainee, I worked on experimental myocardial infarction (MI) in Prof Braunwald’s lab. But I soon grew unsatisfied because we were dealing with the end stage of a disease that had its inception usually decades before we would meet a patient with acute coronary syndrome (ACS). Instead of putting my finger in the dyke at the ultimate stage of the disease, I wanted to understand more about the pathogenesis of the root cause of atherosclerosis. At that time, the research on atherosclerosis was dominated by lipids and, although I have turned back to lipidology a great deal since, I was not satisfied that the association with cholesterol alone explained how atherosclerosis develops.
I needed to understand more about the connection between traditional risk factors and heart disease that had emerged from observational epidemiology. I felt the need to develop a deeper scientific background which, at the time, meant delving further into cell biology and biochemistry. I was also a bit of a rebel and so, after several years, I rather brashly told Prof Braunwald that I wanted to reach beyond work in his group. And Prof Braunwald, to his eternal credit, arched only one eyebrow, and then arranged for me to meet some of the fundamental scientists at the Harvard Medical School — which led me to a three-year postdoctoral fellowship in a basic science laboratory.
Breaking new ground
I had strayed from the traditional pathway, and then after I did my clinical speciality training in cardiovascular medicine, I set out to establish my own independent research group. The tools had become available to culture the endothelial cells of blood vessels in the mid-1970s, which led to the development of vascular biology. So when I started my own laboratory in 1980, I decided to devote myself to this new field, ultimately with the aim of learning more about the root causes of atherosclerosis — well before the current strong links that now exist between the traditional lipid community and vascular biology.
It was a perhaps foolhardy ambition; it was certainly risky and careless. But I was young and had a certain degree of confidence —
not necessarily in myself — that, if I failed, I could always earn a living as a cardiologist, a practice that I enjoy immensely. That attitude allowed me to take the risks. I also had the unstinting support through thick and thin of my wife, Professor Beryl Benacerraf (of Harvard Medical School), who is much smarter, talented and more accomplished than I (see Figure 1 and 2).1
I then began to encounter early failures with trying to obtain grants, being told that I had no background in atherosclerosis. But I wanted to grasp the golden ring, to follow my curiosity and motivation to learn more. I became quite used to having scepticism about where I was going, and the doubts and the difficulties I encountered initially in getting funded only strengthened my resolve to persevere, and that trait continues to this very day. It’s part of my success, and probably also has gained me reputation for being perhaps a contrarian in some circles.
But that’s skipping ahead. At that time (among other work), based on some emerging science, I hypothesised that the newly discovered pro-inflammatory cytokine, interleukin-1, had a role in inflammation and immunity in atherosclerosis.2 My laboratory published that hypothesis based on laboratory experiments in 1986,3 and large-scale clinical trial published in August 2017 has now validated that conjecture.4 This success reflects a measure of good luck, being in the right place at the right time, but also doing the right things for the right reason, along with some hard work, patience and persistence. It also requires considerable fortitude and willingness to accept risk to subject one’s cherished laboratory hypothesis to the acid test of a clinical trial.
I’ve continued to tackle the questions that I considered at the forefront of clinical challenge at various junctures of my career where I thought that my toolkit, both intellectual and technical, could have a chance at cracking them. For example, there was a time when transplantation atherosclerosis was a key problem, and so my lab started work towards understanding its pathogenesis. As a matter of fact, few remember that I did that work, because it’s in the textbooks as accepted knowledge now, but over about 10 years we produced a body of work to gain insight into the adaptive immune mechanisms that contribute to this problem.2
When balloon angioplasty was introduced, re-stenosis presented a huge challenge, and many considered re-stenosis a matter of thrombosis. There was a great deal of interest in platelets and smooth muscle cell proliferation. My lab was perhaps among the first to determine the link between arterial injury and inflammatory activation.5 I certainly can’t take credit for developing the concepts that led to our current generation of drug-eluting stents, but these devices deliver immunosuppressive agents, and some of the basic work that we did when we attacked the problem of re-stenosis bolstered that approach.
We also focused on plaque rupture as a cause of ACS for some 20 years, and I think we helped to solve its mechanisms. Although it wasn’t just my laboratory, we did a lot of work that showed that inflammation and inflammatory pathways make an atherosclerotic plaque susceptible to rupture, and determined the cellular and molecular mechanisms in detail. When statins came onboard, our work provided insight into how lipid lowering could calm inflammation, and render plaques less likely to rupture.6
Yet when on hospital duty, I commonly see patients who have taken statins for years and have well-controlled low-density lipoprotein (LDL) yet still present with ACS. So we’re not done yet, and that’s why, about four years ago, I told my lab we should move on from studying plaque rupture. It was a conscious change in direction in my laboratory to study another mechanism that I think is becoming more important in the statin era: superficial erosion.7,8 I’m constantly pushing myself to look around the bend to deal with today’s and tomorrow’s disease, not yesterday’s.
Lessons from the past, looking to the future
The world has gone through the epidemiologic transition. Cardiovascular disease (CVD) and atherosclerosis no longer affects primarily Caucasian males in developed countries, people of higher socioeconomic status. Many factors contribute to this shift: use of tobacco, consumption of fast food, increase in leisure time, decrease in physical activity due to mechanisation, and longevity due to the conquering of many communicable diseases. People in the developing world now live longer, and CVD has spread worldwide, driven by obesity and diabetes. I think we’re sowing the seeds of a two-pronged epidemic and will start seeing younger people pay the price of these epidemic cardiovascular risk factors on one end, while CVD increases in the accumulating elderly population on the other, as ageing potently promotes atherosclerosis.
For patients who have well-controlled low-density lipoprotein (LDL) using statins, we have to address the other risks. The recently published, large-scale clinical trial has provided proof of principle that some people may be helped by an anti-inflammatory agent,4 but what about those people who have elevated triglycerides? We started a new trial in the last year investigating pemafibrate, a novel selective peroxisome proliferator-activated receptor alpha modulator, which lowers triglycerides and reduces triglyceride-rich lipoproteins — risks not necessarily addressed by anti-inflammatory or lipid-lowering agents. In five years, we hope to be able to tell you whether we’re making inroads against this triglyceride-rich lipoprotein risk.
The next step is making connections between immunology, infectious disease, oncology and haematology within cardiology. Patients who have clonal proliferation of white blood cells most often die of cardiovascular events, providing an exciting new avenue to pursue that seemingly has nothing to do with lipids, but with inflammation.9 This connection was completely unknown a few years ago, and now I’m working with a really wonderful haematology/oncology group to understand the cardiovascular risk associated with clonal proliferation of white blood cells. Making these connections forces me to master a new field, a challenge I relish, and that has enabled innovative science.
Committing to your own path
Younger people with research interests should pursue such connections — scientifically, personally and professionally. It’s the recipe that worked for me and my career, but then I have a bit of a restless curiosity and bore easily. Shaping a career requires courage to leave your comfort zone so that you can innovate. If you’re comfortable, you’re probably not doing something important. I have learned to thrive on being uncomfortable and to embrace intellectual insecurity. When I think I have a hypothesis, an insight that could enrich the field, I tend to pursue it. This trait requires willingness to be wrong, to learn from mistakes, and to regroup. After doing this for 40 years, I’ve begun to gain the confidence that, perhaps, my contrarian concepts might actually bear fruit. I’ve become very used to putting my foot in a field, encountering resistance, yet persevering; eventually, this path usually pays off.
The cross-fertilisation between practising cardiology and working in the lab keeps me from becoming bored. When I’m caring directly for patients, I realise how little we know and how far we have to go to answer questions and meet their needs. Then I return to the laboratory, where I can be a ‘big-picture’ person and try to enrich the field with my clinical perspective. I like to go into an area and make some early observations and then, as other people are mining the details of that topic, I’m off looking to the next thing. Some have said that, when you find the secret of life, it will be a matter of a few ångströms — a tiny shift in some molecule that you can perceive only with structural biology. That’s not my kind of science. It’s very important. It’s beautiful, it’s elegant. It’s necessary, but it’s not me.
It has been very nice to receive recognitions over the course of my career, but such awards actually drive me to delve deeper and strive harder. They stimulate me to ask myself, ‘What have I done lately?’ rather than rest on the laurels. Receiving the Gold Medal of the European Society for Cardiology was a particularly meaningful honour, especially because I consider myself a globalist. But the real reward is not the plaques or medals, it’s what you accomplish. My motto is two little words: “change medicine.” The ultimate reward is seeing many people whom I have trained and mentored over the years have a multiplier effect through their own contributions. That’s the really enduring satisfaction.
I’ve had the immense privilege of embarking on a path that started in a basic science laboratory and have persevered to see it pay off clinically. It’s been quite an adventure for me — starting out very lonely, not even able to publish in the cardiology literature — and now able to reap the harvest of some of the concepts we helped to establish. I can’t see not continuing to bash away at the problems with which I grapple. If Prof Braunwald is still going strong and starting studies that are slated to last five years, so can I. The opportunities have never been greater, and the need is commensurate. So long as I am able, I’m going to be combatting the enemy.