Lab Meeting: Ira Mellman
“In immunology there is enormous opportunity for mechanistic science to help human health.”
In the summer of 1972, an aging Paul Anka sought to revamp his musical act with some young talent. As part of this effort, he hired Ira Mellman—self-described “20-year-old dork” from Oberlin College & Conservatory. It was not a good fit: “I realized very quickly that this is not how I wanted to spend my life…so I left the tour and went back to school,” recounts Mellman.
Anka’s loss was science’s gain. Drawn to experimental work for its “hands-on” nature, Mellman soon published a Journal of Cell Biology paper (as an Oberlin undergrad) before making his way to Berkeley and then Yale for graduate school.
At Yale he trained under giants like Leon Rosenberg and George Palade and learned to marry the disciplines of genetics and cell biology—a skill that would come to define his career. An interest in immunology led Mellman to Rockefeller for a post-doc, where he arrived just in time: “Ralph [Steinman], one of the younger faculty, was embroiled in the most important piece of work I've ever seen up close…the discovery and characterization of dendritic cells,” says Mellman. This work would win Steinman the Nobel Prize, and inspire Mellman to dedicate his career to understanding how the immune system works on a cell biological level.
How do the immune cells that Steinman studied (macrophages and DCs) internalize, transport and present foreign protein “antigens”? As an assistant professor at Yale, Mellman set up a laboratory to tackle these questions. His work led to the discovery of the endosome and a mechanistic model of how dendritic cells internalize and present antigen to T-lymphocytes. For his efforts, he was elected to the European Molecular Biology Organization (2005), American Academy of Arts and Sciences, the Academy of the American Association for Cancer Research, and the National Academy of Sciences (2011).
In 2007, Mellman moved his laboratory from Yale to Genentech. It was a decision as much personal as scientific: “I went to Genentech to have a bigger impact on human health, especially as applied to cancer,” he recounts. Several of Mellman’s close family and friends have been impact by the disease, including his former mentor: “Ralph [Steinman] was diagnosed with pancreatic cancer, right around the time when I was considering moving to Genentech…I thought he would discourage the move. He had exactly the opposite reaction,” Mellman reflects
As VP of Cancer Immunology at Genentech, Ira Mellman has helped uncover how the PD/PDL1 axis works on a mechanistic level. He brought cancer immunotherapy to Genentech, beginning with the discovery and development of the anti-PD-L1 antibody atezolizumab; he also oversaw the discovery and development of a personalized mRNA cancer vaccine (iNeST-RNA), tiragolumab, cobimetinib, mosunetuzumab, and ipatasertib.
Currently, the Mellman lab works at the forefront of cancer immunology—probing how tumor “immunotypes” dictate response to checkpoint blockade, finding novel strategies for cancer vaccines and developing engineered cytokines or monoclonal antibodies that kill tumors. His lab lives by a simple credo: be interesting and useful. “In drug discovery, being ‘interesting’ is not sufficient; one also has to be "useful". You need to define your problems based on what you think is going to help illuminate disease and make a difference to treatment.”
In our interview we discuss the importance of mentorship, and the lessons Mellman picked up from scientists like Zanvil Cohn and Ralph Steinman. He shares the problems in oncology that motivate his current research and discusses findings that are moving towards the clinic. Lastly, he offers advice to those in science looking to have an impact, urging collaboration, creativity, and big thinking: “In the words of George Palade: ‘it is not enough to keep pace with the field, you must always be one step ahead.’ (Q#8)"
Below is an interview with Ira Mellman VP Cancer Immunology at Genentech, from August 2023:
1. What was your first taste of science? Briefly, what about this initial experience drew you in?
I came pretty late to science. My father was a chemist and actively discouraged me from doing science or medicine. My family was much more into the arts. I trained as a musician for quite some time and studied music in college. After a couple years, I realized that I wasn't going to be a great concert player; I started playing popular music instead—rock & roll and jazz mostly.
I kind of “flamed out” after doing a tour with a singer by the name of Paul Anka. He was a really good songwriter, and he traveled with an orchestra on tour. As a college kid, I was supposedly “updating” it by making the show look younger. But I realized that ultimately this is not how I wanted to spend my life. I still love music, but it’s a difficult profession—worse than science in many ways. Around this time, I was also starting to take science classes at Oberlin.
What drew me to science was that it was very “participatory” or active—you read, think, ask questions, and work with your hands to solve those questions. Oberlin is a small liberal arts college that happens to have a very good biochemistry department—but there were no graduate students or post-docs. The faculty have to work with the undergrads to get anything done, and as a result they were very invested in teaching us how to be effective in the laboratory.
As an undergrad, I remember working on a project that involved isolating proteins from plant cell walls. We made the discovery that these cell walls contain a protein called extensin, which turned out to be a hydroxyl-rich collagen-like molecule with tensile properties. We were able to publish a nice Journal of Cell Biology paper from this work. I thought this [science] could be an awesome life, so I decided to get a PhD. I ended up going to Berkeley and then transferring to Yale for graduate school, initially with the aim of getting an MD-PhD, but I was much more motivated to get directly into the laboratory.
2. Who was your first great scientific mentor and what made them so great?
As a grad student at Yale, I joined the newly formed program in human genetics. The department was led by my PhD mentor Leon Rosenberg, who just recently passed away. Human genetics was very exciting to me because it felt close to impacting the human condition. I felt like I could be involved in medicine but spend most of my time in the lab.
I learned something important from Lee [Rosenberg] that young people need to understand: to succeed in science you need to raise your expectations for yourself. Pursue the most important problems you can think of. It is totally possible to be the one publishing papers in journals that others read and get inspiration from.
I learned during my training that as fun as science is, it requires an exceptional level of commitment, creativity, and intellectual discipline. Ultimately, it takes as much energy and commitment to something exciting as to do something boring or pedestrian. So why not at least try to do something that is inspirational, important and can have an impact?
In my lab today, I want everyone spending their time on problems that they feel are critical. This is where I hold people's feet to the fire: is this really the most important thing you can think of spending your time on? If so, why? Tell me why this gets you excited?
[On scientific mentorship]
I've had just wonderful mentors, starting with my undergraduate mentor David Miller [at Oberlin]. My PhD mentor Leon Rosenberg eventually became Dean of Yale Medical School and then head of R&D at Bristol Myers Squibb.
I went to Rockefeller for a post-doc. My department head was a brilliant man called Zanvil Cohn, who did excellent immunology and cell biology on macrophages. He was a member of the National Academy of Sciences and all of that, but was a very self-effacing, quiet and humble man. He taught me a lot about project selection: if you've chosen the biology correctly, the rest will take care of itself. I also learned from him that the best mentors act as logic filters. By logic filter I mean that a mentor should not be judgmental about someone's ideas, but should always ask: “does this really make sense?” Are there erroneous assumptions or other variables that are not accounted for? [Zanvil Cohn] taught me that this is the single most important thing a mentor needs to do well to support the progress of their trainees’ development as scientists.
3. What was your scientific high point during training?
Much of the work I did during my post-doc at Rockefeller was with Ralph Steinman. Ralph was one of the younger faculty and was embroiled in probably the most important piece of work I've ever seen up close, which was the discovery and characterization of dendritic cells. This work eventually won him a Nobel Prize.
I could see him [Steinman] struggling with something new. The scientific “macrophage mafia” was totally against him. He was also brash and opinionated, and his life was made difficult by all of these factors. But these problems were counterbalanced by the fact that he was doing something that was clearly of such importance; it entirely changed the field of immunology. Dendritic cells link innate and adaptive immunity, and he discovered how this happens. My late ex-colleague and friend Charlie Janeway, always referred to adjuvants as being immunology’s “dirty little secrets.” How do these molecules like LPS that stimulate the innate immune system also bolster adaptive or humoral immunity? Ralph showed how antigen presenting dendritic cells could detect these innate immune molecules [via TLRs], which was the missing connection for over 100 years. Ilya Metchnikov got the 1908 Nobel Prize for essentially describing macrophages and innate immunity, while Paul Ehrlich got the prize the same year for discovering humoral immunity. They thought they were working on two separate immunological processes, but Ralph was finally able to connect these two areas. By detecting innate signals to initiate adaptive immunity, perhaps the most important central function of dendritic cells must be the presentation of antigens to T cells. It was this realization that set me off trying to understand how these cells accomplish this feat, and do it better than almost any other cell we know of. So, I was cast in the direction of marrying the fields of immunology and cell biology.
[On the gulf between the scientific disciplines of cell biology and immunology]
I have long felt that there is a large gulf between the fields of immunology and cell biology. Metchnikov is a point of connection because his work on macrophages led to the discovery of endocytosis, intracellular degradation and lysosomes. But from that point, the fields really diverged. The only way I can rationalize this divergence is as follows: most immunologists [although there are increasing number of exceptions] generally don’t care very much about understanding how the cells they study actually work. Cells are viewed as functional units that must be understood in the context of a complex system. On the other hand, cell biologists lose interest in problems as a function of the square of the number of cells involved. They view an immune system with millions of cells engaging in complex interactions as hopelessly abstruse.
Understanding the mechanistic [cell biological] basis by which complex systems work is probably one of the greatest challenges that that exists. Neuroscientists do this better than almost anybody else but [the brain] is such a complex system. In immunology there is enormous opportunity for mechanistic biology to help human health. The immune system is probably the best site for therapeutic intervention that we have—you can literally take it out of an organism, modify it and put it back. You can’t do this with the brain.
The part of immunology that has fascinated me the most is its relationship to cancer. I had some dear friends, family members, lab members, and colleagues who were diagnosed with, and eventually succumbed to cancer—Ralph Steinman was diagnosed with pancreatic cancer around the time I decided to move to Genentech. When I discussed this move with him, I thought he would say that going to a company would be a terrible idea and an abandonment of science. He had exactly the opposite reaction—he wasn’t going to live long enough to impact human health but he felt that I [at Genentech] would have a far better chance of moving the field forward and having an impact. So I joined Genentech, and remain here today. As usual, Ralph was correct.
4. What set of research questions or projects has you most excited about coming into lab today?
I moved to Genentech to try and have a bigger impact on human biology and health, especially as applied to cancer. Even for the basic projects my lab pursues, I want them to be “useful” in addition to interesting.
If you have an academic lab, you can become a successful scientist by just being serially interesting. But in drug discovery, being “interesting” is not sufficient. You have to define your problems based on what you think is going to help illuminate disease pathophysiology and what will make a difference to treat disease. This is a long way of saying that we often try to connect what we do in the lab to human data. A great example is the field of checkpoint blockade.
Originally, PD1 blockade was thought to work by reversing the process of T cell exhaustion; it was brought successfully to the clinic on the basis of this assumption. After years of laboratory inspired by the dramatic clinical benefit observed, we are finding our view to change dramatically. Checkpoint blockade seems to have nothing to do with reversing “exhaustion” but rather it appears to work by directing T cells on a differentiation pathway that avoids exhaustion altogether. This changes entirely the conception of when you would use [checkpoint therapies] and why or how you would use it clinically.
Because we have patients in the clinic taking these agents, patients are now our “Drosophila” or “C.elegans,” because you can perform real-world interventions and then analyze this experimental data. A lot of our most exciting projects are really looking at something we don't understand clinically and uncovering mechanism. Vaccines are very much on our minds at the moment, particularly with the paper that we published with Vinod Balachandran in Nature earlier this year (2023). Why do some cancer vaccines work, especially in the adjuvant setting? Is it just because there's less tumor [in the adjuvant setting]? Or is it because of something else?
Another really interesting feature [of tumor immunology] is that when we first started looking at samples from cancer patients, we found that different tumors, even within the same genotype, had different immunological profiles. We are now referring to these as “immunotypes.” Different immunotypes will respond differently to checkpoint inhibitors—the so-called “immune inflamed” class harbors most of the positive responses. But there are also immune excluded tumors that generate T cell responses, but there is a stromal environment that blocks T-cell infiltration. Then there are immune deserts that never generate an anti-tumor T cell response at all—so why is this happening? How are these immunotypes established? How do you manipulate them? There has been some beautiful recent work led by Christine Moussion, studying how these immunotypes develop in mice.
We also published a paper last year on T cell killing. This story came from a clinical observation that T-cells are not very efficient at killing tumors, unless equipped with co-stimulatory molecules or CARs. But if you look at an endogenous tumor antigen specific T cell, killing is very inefficient. We characterized the immune synapse between these T-cells and the target cells, and found that the tumors were repairing the perforin holes as quickly as the T cells were making them. There's a basic cell biological mechanism [ESCRT complex] that that repairs the holes or pores in the plasma membrane. I’m sure this repair mechanism has some endogenous role in protecting our cells against invading viruses and bacteria; but nevertheless this system affects cancer biology. It is ironic that I learned about ESCRT complexes years ago from experiments in yeast because they were relevant to my lab's studies on endocytosis and antigen presentation.
5. On the industry side, in 2023, what are some of programs (clinical or late preclinical) that you are looking forward to seeing develop or readout?
I'm excited about everything that has made it as far as the clinic. For example, we have developed several novel approaches to deplete regulatory T cells in cancer and to change the architecture of the tumor stroma, which we believe can act to exclude T cells from entering tumor nests. These therapies are incredibly active preclinically. While the only real model for human cancer is human cancer, we are nevertheless very excited to have used observations of human cancer to model specific mechanisms in mice, and then to devise ways of addressing those mechanisms that are now being taken forward as exploratory therapies in cancer patients. We will have to wait and see how the clinical trial goes.
We are also interested in engineering cytokines and other therapies that are relatively straightforward—these types of agents are developed faster, present fewer technical challenges. We were discussing personalized vaccines before, and I am perhaps most excited about these approaches. But it is very early days, and so far we've only seen benefit in the adjuvant setting. Why don't we see benefit in the metastatic setting? How do we optimize these vaccines to work in later stage disease? What do we really know about vaccine immunology? The answer that question is very little.
The granddaddy of all these approaches is cell therapy and cell engineering. So far this has been synonymous with CARTs, which are exciting but difficult to scale, very expensive and so far only work well in hematopoietic cancers like leukemia, lymphoma and to a lesser extent myeloma. These early approaches have not worked for solid tumors. Other questions remain: can you make these therapies out of induced-pluripotent stem cells [allogeneic]? Can you engineer these cells in situ by injecting viruses or LNPs to deliver CRISPR constructs? How exactly should we modify these cells—should we just put in CARs or TCRs? Why not add other constructs? Lastly, if we consider metabolic disease: generating new pancreatic beta-cells for treatment of diabetes has always been the dream. Do these cells even have to be beta-cells or can they be another cell type, like a macrophage, that has been engineered to respond to glucose and secrete insulin? I don't know the answer to these questions. But there is huge opportunity to do some really exciting basic science that could be incredibly useful to patients.
6. Which areas of science, outside of your direct field, are you most excited about seeing develop in the next 5-10 years?
Probably at the top of the list has to be neuroscience and diseases like Alzheimer's and Parkinson's. The older you get, the more of your friends and family are affected by these conditions. There is not that much that can be done for these patients, which is horrible. Why can't we make progress on these conditions? Both of in-laws died from AD—my father in-law was a neurologist who knew exactly what was happening to him, until he didn’t. This problem has been around for a long time, and we need better therapies.
7. Who are a couple up-and-coming scientists not at Genetech, whom you think we should watch? Why is their work so exciting to you?
We just heard at talk at Genentech from David Liu at the Dana Farber, who does these longitudinal studies in individual patients, which are incredibly interesting. Aaron Ring and Nik Joshi at Yale are both doing fantastic work. This is a very unfair question, but there are lots of exciting early-stage scientists in oncology.
8. What is one piece of advice for a young scientist aspiring to have a career in academia, and make some important discoveries?
At the top of my list is to take your time choosing a problem. Be sure that you address a problem that is significant and profound, and not just an incremental advance. Then, at the very least you'll be wrestling with the most important aspects of biology. I would also advise young scientists to be collaborative--don't be afraid to share information. If you identify yourself as somebody who's really in it to advance the science, rather than you own self-aggrandizement, you'll get a lot more help in the long run. Sure, some people may steal information from you, but you will get back a lot more than you give up (been there, done that).
A final piece of advice is that it’s not sufficient to be as good as your friends, you have to be one step ahead conceptually. The Wayne Gretzky hockey analogy is that you have to skate to where the puck will be. In the words of George Palade: “it is not enough to keep pace with the field, you must always be one step ahead.” You always have to think big and creatively. Details are great and necessary, but if all you can think of is details you become a tactician and not a strategist. Strategic thinking is what sets the course of science.