Enduring Scientific Friendships
As told by James E. Rothman
This autobiographical sketch of a life in science mainly focuses on a question I am now often asked – when and how did you know you wanted to be a scientist, and how did you become one? I am also asked by young scientists for advice I could impart from my own experiences and observations. With this in mind, this essay essentially provides bookends of my life until now, and I hope it may be of interest less from the particulars and more from generalizations that may emerge in the eyes of a reader, especially a young scientist.
From the earliest time I can remember I wanted to be a scientist, especially a physicist. I am not entirely sure where this came from, but at least in part it must have come from my parents who deeply valued education, especially in science and medicine. I was really fortunate and owe my parents a lot – they made me feel that I could do anything, and they provided the resources to enable me a privileged education unencumbered by financial needs.
My mother Gloria, with her enormous focus and drive, would in today’s world have been a high-powered executive. But she grew up in an earlier era where women had far fewer options. She ran the home and my Dad’s pediatric practice and taught me how to organize and manage. My father Martin was an intellectually oriented small-town physician who had wanted to do medical research as a young man, but had graduated in the Great Depression and then been caught up in World War II. He was always keen to involve me in the things he did. At perhaps the age of eight I remember accompanying him on nocturnal house calls, at other times to the hospital; assisting him at home by measuring the intervals in his patients’ electrocardiograms; and helping him perform blood analyses in the small lab behind his office.
But I believe that my focus on science came at least as much from the times during which I grew up, and the values that I and other Americans internalized from the society around us. In the 1950s and 1960s science and technology were viscerally understood and applauded by most Americans as mainstays of economic and political power following the victories of World War II. This era began with the polio vaccine eradicating a dread disease and with atomic energy (for better and for worse). It ended with the transistor, the digital computer, and the first men on the Moon.
In such an environment, and with my supportive family, and with an abundance of curiosity and a natural talent for mathematics, it is not surprising that I was designing and building electronics and launching rockets while still in elementary school. Rockets were a big thing for me as a boy. I taught myself basic trigonometry in 7th grade so I could triangulate the height of the rockets, and then calculus two years later so I could better understand the physics involved. As I began to study more advanced physics and mathematics formally in high school, I devoured the subject and challenged myself far outside the excellent curriculum at my secondary school (Pomfret School), so much so that I was graduated after my junior year. Entering Yale College in 1967, I was absolutely committed to theoretical physics.
Yale provided the perfect environment in which a committed young scientist could develop while also immersed in the broader culture. Yale was big enough to provide every opportunity, yet organized into relatively intimate units (Colleges) small enough to foster the individual. The students had all varieties of interests, and my friends were drawn largely from outside the sciences, providing breadth to complement my personal scientific focus (these friendships continue today with annual summer reunions of the “812 Club,” named after a room in Branford College). I also studied and especially internalized from my friends a great deal about art, philosophy, and history.
As an entering freshman, I was accepted into an “Early Concentration” program which rapidly enabled me to focus deeply on mathematics and physics at an advanced level. Physics taught me how to rigorously analyze the components of a problem by first imagining the form a solution would take. This can be a useful approach when engulfed in the fog that envelopes the uncharted waters of biology.
As I began my junior year, perhaps with fatherly concerns about the poor employment prospects for physicists at that time, my Dad strongly encouraged me to at least give biology a try. I was not especially open-minded, as there was a well-understood intellectual pecking order that every budding physicist was soon informed of. Theoretical physicists were the brightest. Experimental physicists were failed theoreticians, but nonetheless useful for confirming theories. Chemists were not so bright, but still socially acceptable. Biologists were said to be even less bright, and generally not worth mentioning. But, even at the very first lecture in the general biology course, I was amazed that (in contrast to the highly structured field of physics) the research frontier in molecular biology seemed instantly accessible, and yet could be equally rigorous and structure-based.
Thus began a multi-year process in which I gradually learned to think like a biologist, while still retaining the orthogonal way of thinking like a physicist. I believe this mindset was critical not only in my choice of the problem whose solution was recognized by this Nobel Prize, but also in providing me the means to solve it (as elaborated in my Nobel lecture). Therefore, I will devote some detail here to this process of transition from physics towards biology.
The transition came in stages, initially via self-taught physical chemistry (though I never formally studied this subject or many others – in fact, I have completed only one term of college chemistry and biology and most of what I have learned in science and medicine has been self-directed). In physics, I had gravitated to statistical mechanics, probably because unlike quantum mechanics you can visualize it in simple terms. Statistical mechanics served as my intellectual bridge to biology. For example, consider that the three dimensional conformations of polymers (a classic problem in statistical physics and thermodynamics) such as polypeptides are a fundamental determinant of their biochemical mechanisms. A term of research (junior year) with the theoretical chemist Marshall Fixman on the statistical mechanics of polymers equipped me with a fluid way of visualizing individual versus ensemble behavior of molecules that to this day guides my thinking in biochemistry and cell biology.
The next stage in my transition (also junior year) came via Harold Morowitz, introduced by Fixman, a theoretical biophysicist with equal interest in science as in philosophy. Harold was a broad intellectual who has had many interests, but just then he was especially interested in the hotly debated question of the basic structure of biological membranes. His laboratory had just done some influential experiments demonstrating thermal phase transitions in the membrane of microorganisms mimicking the behavior of isolated lipid bilayers. In retrospect, I was attracted by a combination of the familiar (thermal physics and conformational changes of a polymer [fatty acid chain] in the phase transition) and Harold’s personal warmth and charm. Soon I was working in his lab with a postdoctoral fellow, designing and building an instrument to measure the phase transitions, and was deeply engaged.
Harold had a way of collecting interesting people around him, including his former PhD student Donald Engelman. Harold advised me to go to the research seminar that Engelman was to give during an upcoming visit to Yale. This was the first seminar I had ever attended, and as it turned out it was a “job seminar” resulting in Don joining the faculty of Molecular Biophysics and Biochemistry soon thereafter. He spoke about his now classic experiments with Maurice Wilkins (Nobel Prize, 1962) demonstrating the lipid bilayer in biological membranes using an elegant combination of microbiology and X-ray diffraction. I think Harold asked Don to take me under his wing, where in a sense I have been ever since (Don remains one of my closest friends and happily we are both now at Yale). We took on the problem of how cholesterol buffers the fluidity of the lipid bilayer, extinguishing the thermal phase transitions, and my earliest publications came from this. Don taught me by his example how to dissect each morsel of data to get the most from it.
In doing this, I learned another important lesson – the central importance of numbers. My students sometimes seem surprised that there are a lot of numbers that I have at my disposal whenever I may need them; this is true, and it is no accident. From Yale onwards, I have always made a point of remembering key numbers, and I have learned to do this automatically every time I hear a new one. For example, π and e in mathematics; Boltzmann’s constant in physics; absolute zero temperature, the diameter of a hydrogen atom, and the density of various materials in chemistry; the size of proteins and their secondary structure motifs, and the sizes of viruses, organelles and so on in biology; and the rates of fundamental processes (for example, diffusion in water, lipid bilayers; the rate of cell locomotion and so on). Ready knowledge of scale and rates allows one to quickly see if a hypothesis or a result or an experimental design is reasonable.
At that time Yale had an unusual program for a dozen or so seniors called Scholar of the House (sadly this wonderful program has been discontinued). This program allowed me to spend senior year fully in research (with Harold and Don) with no formal course work, and to graduate solely on the strength of a thesis, if it was accepted (if it was not I would need to repeat senior year conventionally). The thesis was evaluated by a committee of Yale’s most eminent scholars drawn mainly from the humanities. With so much riding on this, I was mortified when Harold playfully showed me the evaluation of my work he had written fully in limericks – I was sure I was doomed; but apparently it was just right for the humanists, and I was graduated (with the award for the best thesis).
During that last year at Yale I became a scientist.
My father had convinced me that I should go to a medical school rather than directly to a PhD program. At that point my knowledge of biology was as narrow as my knowledge of physics was deep, and it would have been impossible to make an informed choice of which discipline in biology to focus on. Therefore, I entered Harvard Medical School (in 1971) with the idea of learning biology and then doing research, rather than ever practicing. I succeeded in the former, ultimately leaving the MD program more or less after the basic sciences (but with enough clinical exposure to gain a lifetime of respect for clinical medicine).
The first year at Harvard Medical School easily proved to be the greatest didactic experience of my life because HMS offered an unencumbered platform for self-directed learning with wonderful access to first-class research professors built on a broad and well-organized curriculum. I still rely on the many things I learned in that first year or so.
In particular, it was as a first year medical student in histology that I first learned about the secretory pathway, at a time when the discoveries of George Palade (Nobel Prize, 1974) were still fresh and remarkable. What an astonishing process – how could cells make vesicles from membranes? How could each vesicle know where to go? How could it fuse? It was particularly amazing because at the time it was not even possible to begin to imagine the form a molecular solution might take. This captured my imagination, but not enough was known to productively take up the problem then. But it would ultimately become a lifelong focus when I started my own laboratory at Stanford in 1978.
My PhD thesis (initially as part of Harvard’s MD-PhD program) was with Eugene Kennedy, a master of membrane biochemistry. Kennedy, who was a brilliant intellectual and an original thinker, taught me how to formulate a complex problem in biochemical terms. Some of this work was in collaboration with John Lenard, whom I will soon mention. We established how lipid bilayers in cell membranes are formed by asymmetric biosynthesis, following on the PhD thesis work of Roger Kornberg (Nobel Prize, 2006), which had at that time just established the basics of the physical dynamics of lipids in membranes.
Harvard, therefore, is where I became an experimentalist and in particular a professional biochemist. Everything that happened afterwards followed from that.
Deep and enduring scientific friendships
A life in research provides many opportunities to meet remarkable people as a student and afterwards around the world. It is hard to over-emphasize the importance of several formative, warm and enduring friendships for my development and success as a scientist. Some evolved from what we would today call mentoring relationships, initially with somewhat older (but still young) scientists who were nonetheless more established than me. Th s group included (in the order of our fi st acquaintance) Donald Engelman, John Lenard, Qais Al-Awqati, Roger Kornberg and Per Peterson. I fi st met each of these extraordinary individuals essentially as teachers. I have already mentioned Engelman.
John Lenard was a young full professor at Rutgers when we met in 1974. He took me into his lab (and his home) while I was still a graduate student so we could understand the topology of lipids in viral envelopes. We worked day and night together and we soon bonded personally. Though we never collaborated experimentally again, many ideas and personal decisions have been subject to John’s wise counsel. We wrote several review articles together over the decades, and in each case he taught me how to improve the framing of ideas and my writing style. Happily, we see each other regularly for dinners, museums, and theatre in Manhattan.
Qais Al-Awqati was my teacher in renal physiology when I was a second year medical student (1972) and he was junior faculty at Mass General. We met again much later (1986) when coincidently we both were at Cold Spring Harbor Laboratory summer lab courses, and we had many lovely evening walks together discussing books and occasionally science. We have been close ever since. Qais is not only one of the world’s best physicians and cell biologists, but without doubt one of the most intelligent and cultured people I have ever met. What a privilege it is to continue to learn from and enjoy him, whether we talk about science or he guides me through the Metropolitan (be it the art museum or the opera).
Roger was an assistant professor in the department of Biological Chemistry at Harvard Medical School and I met him as a PhD student. We had a common interest in membranes, but soon we were discussing ever-widening scientific terrain because of his deep and penetrating mind. He broadened and sharpened my perspective on biochemistry, first as a student and then soon as faculty colleague at Stanford. At Stanford we met many times a week, and I turned to him for criticism and inspiration. After I left Stanford (1988) this of course diminished in frequency, but never in intensity. I also suspect that Roger’s endorsement after “road-testing” me at Harvard somehow figured importantly in the job offer from his father Arthur Kornberg (Nobel Prize, 1959) and the other faculty to join their Biochemistry department, which came while I was still in the MD-PhD program in 1976.
Per Peterson, as he puts it, “discovered me” at a membrane meeting in Heidelberg (1980). Per is a cellular immunologist, and was at that time the director of the Wallenberg Laboratory in Uppsala (Sweden). As he told me, my findings were good raw material, but needed polishing. Of course, he was correct. He has been trying, with occasional modest success, to improve me ever since. Per has a rare combination of great analytical power with a genuinely sympathetic understanding of human nature. This has enabled him both to contribute centrally to science, and to build and run large and successful organizations, most recently as the Chairman of Research and Development at Johnson & Johnson. During his evolution Per has kept me at his side, and taught me a tremendous amount about the dynamics of industry and approaches to management that have proven very useful to me. He continues to inspire me and help me focus on what really matters.
Other important friendships started on more personal terms but soon evolved into long-term informal intellectual or actual collaborations where new ideas could be debated with absolute intellectual honesty in friendly ways and often in nice settings as well. I met Graham Warren (Figure 4, top) in 1976 when he was a postdoctoral fellow at Cambridge (UK) on an extended visit to Harvard, and we immediately hit it off, his reserve a complement to my exuberance, Graham harboring a well-known (merciless) intellectual rigor salved by his gracious humor. Graham and his family spent a summer at Stanford in 1978, so we could work together (actually starting my lab jointly) on what turned out to be a bold but ultimately ill-conceived hypothesis that we had convinced ourselves was the key to the sorting problem. Although in the past few years, with his responsibilities directing the Max Perutz Institute in Vienna, and mine at Yale, our contact has been less, we have seen each other numerous times every year and many of my best ideas have often drawn on our discussions.
I met Felix Wieland in 1985 at Regensburg (Germany) where he was then an assistant professor. He came up to me after my lecture on cell-free reconstitution with the idea of spending two years at Stanford trying to figure out how membrane fusion worked. As with Graham, we also immediately hit it off, though in Felix’s case it was his contagious Bavarian exuberance and humor synergizing with mine. Soon, he was in Palo Alto. Wieland was a real enzymologist who taught me (and the rest of my lab) how the business is really done, having himself learned at the hands of a master (his uncle) Fyodor Lynen (Nobel Prize, 1964). Without Felix, I doubt there would have been NSF, SNAP, SNAREs or coatomer, and even if there were they would not have been as much fun. By 1987 Felix moved back to Germany (at Heidelberg) but we still see each other frequently. I look forward to our annual escapes with our wives to Bad Drei Kirchen (Bolzano), and the Rothman and Wieland children continue their childhood friendships to this day.
Without a doubt the most important, deepest, and most vital relationship is of course with my wife, Joy Hirsch. In addition to the personal side, Joy is also my scientific partner. She is my sounding board on every subject, and has been my critic and supporter through the many early years when my work was not accepted as it is now. Joy comes from a successful farming family in Salem, Oregon and from this very American background is imbued with the Yankee attitude that every problem can be solved if you think about it enough and try hard enough. Joy also lives by this belief in her research. She is also a Professor at Yale, and is gifted scientist who is renowned for her fundamental studies of human cognitive processes and related diseases.
Observations on style from a life in science
As a closing bookend, I will offer some observations that may be of interest to others, especially younger scientists. This is not necessarily to impart specific advice, which would be disingenuous as I rarely followed the advice I was given as a young man; it is more to offer the use of some of my personal experiences as a springboard for generalizations that may apply to the reader. Some of these thoughts will be familiar to several generations of my students, who may recall having heard one or another as a frequently trodden-out aphorism. Some are from my own teachers.
Science and art. Science at the edge is an art form as much as a strictly logical development of ideas. The rare artists and the rare scientists capable of performing at the edge have a lot in common. They both have an intuitive vision carrying strong emotional content. Neither is easily discouraged from their work, even with strong obstacles in their path. These are essential traits.
Choosing a problem. As a new junior faculty member at Stanford, I asked Arthur Kornberg why he chose to understand DNA synthesis in the early 1950s. He said that the problem was of the greatest importance; that everyone else assumed it could not be done; but that he thought it could be. I listened very carefully when he said this.
The importance of a clear hypothesis. I often tell people in my lab “if you want to hit a home run, you have to be in the ball park. If you are outside the ball park you can swing all day but you will never hit a home run.” This idea comes from physics where computationally complex problems are approached by making simplifying “ball park” assumptions so that the main variables can be identified. To do this in biology, you imagine you are designing the system and therefore how you would design it for the required function. This provides a model – a hypothesis – of the form that a likely solution will take. You are now in the ball park, because you can now design specific tests of the model. Your exact model is almost certain to be wrong in detail (evolution rarely works by Cartesian rules) but is likely to be correct in spirit, and this will allow you to get to the truth faster. This process is very basic to my approach to science, as I described in my Nobel Lecture.
Troubles Are Good For You (TAGFY). The “TAGFY Philosophy” was first enunciated by the master enzymologist Ephraim Racker, and I pass it on. TAGFY has proven true for me over and over again. For example, after Erik Fries and I first published cell-free transport, we had great difficulty repeating our exact results, and it would have been easy to be discouraged. But TAGFY meant that we were really about to discover something basic that we had no idea about. Indeed, in resolving the “trouble” we found that we had reconstituted intra-Golgi vesicular transport, a process not previously known to exist (as documented in the Nobel Lecture). TAGFY can give you strength in hard times.
If you are hitting your head against a brick wall, find a new wall. It is so human to try that experiment one more time hoping for a better result. It almost never pays. Try a new approach. Remarkably, most people don’t.
It is much harder to stop a project than to start one. To do so takes real intellectual honesty and a complete disregard of ego. Worse, stopping involves a huge sunk cost of time and emotion, but if you don’t, then the next phase (which may hold success) will be only further away.
Don’t be afraid to be “stupid.” If you don’t understand it, it is probably unclear. If you don’t know how to do something, ask. It is far better than losing days in the lab because you didn’t. It is amazing how many people don’t ask. I always did and it made a difference.
Smart is good; lucky is better. Eugene Kennedy always said this, and he was right. In other words, in spite of any and all, don’t over-think and be open to chance.
Additional personal history
In addition to me (1950) my parents Gloria Rothman (née Hartnick, born 1923) and Martin Rothman (1915–2005) had two children, Richard (1953) and John (1955). My brother Richard is an MD-PhD who recently retired from the NIH after many years as a leading researcher in neuropharmacology, and is now in practice in Psychiatry. John is a successful attorney specializing in mediation. I am married to Joy Hirsch who is an eminent professor at Yale in Neurobiology and Psychiatry. She is a graduate of the University of Oregon (BS) and Columbia (PhD). We reside in New York and New Haven. I am always dazzled by her beauty and elegance but equally by her brilliance and compassion. Joy is the glue that holds together our wide circle of personal and scientific friends, and our extended family. She has also been an exceptional stepmother to our children, and we are very proud of their accomplishments. Matthew (1977) graduated from Yale (BA) and Columbia (MBA) and is a senior executive in a major investment firm. He is married to the former Sarah Levinson, a senior executive in a national public relations firm. Sarah and Matthew are superb parents to our two delightful grandchildren, Alexandra (2010) and George (2012). Lisa (1982) graduated from Yale (BA) and Columbia (MD) and soon will start her residency in Dermatology at NYU.