Founder Stories: Tillman Gerngross, Co-Founder of Adimab & Building Products for Biopharma

Good afternoon. It's my great pleasure to welcome you all to this Presidential Faculty Lecture for this year. And one thing probably won't surprise you is that selecting a faculty member for this is like an impossible job. There are just so many outstanding faculty members doing such great work at Dartmouth, and trying to pick one Trying to figure out which one rises to the top every year is a huge challenge, but once again this year, I am happy to say that someone rose strongly to the top, a single faculty member proving that at Dartmouth everything is possible. So, and this is someone who actually proves that day after day after day that in fact at Dartmouth nothing is impossible. So I'm talking, of course, about our own Tilden Gerdnow's Professor of Engineering at the Thayer School of Engineering. And I'm especially delighted that we're able to honor a member of the School of Engineering on its 150th anniversary. So let's all congratulate Thayer. Dr. Tillman joined our engineering faculty in 1998, and I could not be more proud of his work as a faculty member at Dartmouth, including his contributions to his field and to the biotech industry and the role that he continues to play in the success of Thayer School and its students. He's completed the 3-year term as well as Vice Provost of Dartmouth's Office of Entrepreneurship and Technology Transfer. Just a couple years ago in the spring of 2016. I guess that's a year ago. And in addition, as you probably all know, Tillman has co-founded 5 highly successful biotechnology companies: Glycopy, Adimab, Arsanis, Avitide, and Elector. Did I say those okay?

You did. Great. Yeah, great job.

And if there's a common theme that runs through Tillman's life's work, It's his passion for connecting science to human needs through engineering and for sharing that passion with the world. And a few short weeks ago, I'm happy to say that the National Academy of Engineering validated my choice of a faculty speaker by electing Tillman as a fellow of the National Academy. For those of you who may not be familiar with this, this is a really big deal. It's an honor bestowed on a select few who have made outstanding contributions to, and I'll quote, engineering research, practice, or education, including where appropriate, significant contributions to the engineering literature, and the pioneering of new and developing fields of technology, making major advancements in traditional fields of engineering, and developing and implementing innovative approaches to engineering education. And no one fits this set of descriptors better than Tillman. Tillman grew up in Austria and the United States. He earned a master's degree in biochemical engineering and a PhD in molecular biology from the Technical University of Vienna while working in Arnold Demaine's microbiology lab at MIT. The title of his lecture is The Impact Factor Reflections of a Translational Scientist. And so now please join me in welcoming to the stage our own entrepreneurial scientific bioengineering professorial wonder, Tillman Gribble.

Thank you. Let me start by thanking the tens of thousands of you who showed up this afternoon. Better? Yeah. The tens of thousands of you that showed up this afternoon to listen to my great words. Joking aside, I really wanted to thank you, Phil, for selecting me and for offering me this opportunity to talk about a body of work that now spans almost two decades. And while I did not intend to go into the blow-by-blow things that I've done over the past 20 years since arriving here. I did want to talk about 4 specific stories, 4 acts, if you will, or 4 vignettes that describe my evolution from an assistant professor arriving here many years ago to what I mostly spend my time on now. I think it's an evolution that could be of interest to some of you. It's an evolution that has these distinct, I think, events that informed me how to think about being an academic engineer. And in order to make the story sort of more interesting, I thought I would map that personal evolution onto the evolution that we have gone through as a species. And as such, I'll take you back to the Great Rift Valley of East Africa where about 1 million years ago, early Tillman climbed out of a tree. And this early Tillman had sort of mostly ape-like features, although he had parallel toes and opposing thumbs, but not much going on otherwise. And so this is how I arrived here in the fall of 1998, with my baggage, ready to report to my duties at the Thayer School of Engineering. And when I came, I joined a group of very dedicated faculty that had spent the better part of their career thinking about a world that is currently heavily reliant on fossil carbon to supply fuels and commodity chemicals, and how one could transition that economy to one that is less reliant on fossil carbon and drives these fuels and materials from renewable resources. And I personally was going to contribute to this effort after having spent the previous 8 years working in this area, both on the microbiology the fermentation science around using these microorganisms to feed them sugar to make thermoplastics. And I'd done that at MIT for 4 years and then 5 years in a private biotech company in Cambridge. But before I was going to spend my limited startup resources— and I'm not complaining, Joe— I wanted to make sure that what I was going to do passes the what-if test. And that means if I really invest the next 5, 10 years of my career in promoting this technology, what impact is it really going to have on society? What benefit is one really going to see? And when I asked that question, you always got the same answers. The first one is, well, we clearly have to move away from fossil carbon to renewable resources. And what's there not to like? That seems like a reasonable thing. The second reason was that these plastics that are made from this microorganism, these polyhydroxyalkanoates, are polymers that when they're in contact with an active compost environment are degraded. So they're biodegradable. So these are materials that you can make from renewable resources and upon disposal degrade back into CO2. So again, what's there not to like? On top of that, you would look at the reputation that conventional plastics had at the time. And this is a sort of PR piece that reflects that sentiment. It's the mother most diaper companies totally ignore. And what it's intended to do is make mothers that use diapers to keep their children's beds dry feel guilty. And when they feel guilty, there's an arbitrage opportunity between your wallet, their bank account, and the guilt that you have. But there's no real quantitative information of how much better are these technologies if we were really on a large scale to substitute 30 million tons of plastic manufacturing, which is what we do in the US, with this greener or more sustainable alternative. And so when you looked for that information, you would mostly find illustrations like this. The sun drives the sequestration of carbon into a corn plant. That corn plant can then be harvested. And through the process of corn wet milling, you can derive sugars. Those sugars you can feed into a fermentation process to make these plastics. And upon degradation, they degrade into CO2. Again, nothing not to like. However, nobody had asked the question, what are really quantitatively the inputs and outputs if one were to implement this at large commercial scale? And it seems simple, but before I was going to commit my limited startup resources, I was going to make sure that I had an answer to that question. And so in two papers, one published in '99 in Nature Biotechnology and a later piece in Scientific American, asked the question, well, how green are these green plastics? And the answer is not terribly encouraging. When you look at polystyrene, this is something we very often use in food packaging. This is plastic number 6. It's this clear stuff that you can often use in salad bars so you can see the salad. So it's often used in food packaging. In order to make 1 kilogram of this stuff, 1 kilogram of polystyrene, you need about 2.26 kilograms of oil and natural gas. So that's the fossil carbon input to then give you 1 kilogram of this material. And so now, if you were to ask, how does this greener process compare? You can do the analysis. You can say, well, what does it take to grow the amount of corn you need? What does it take then to feed that glucose into a fermentation process? What does it take to get the plastic out of the microorganism into a form where it's a polymer resin that you can use to injection mold? You can add all that up. And what we found, or what I found, is that when you do that, you actually spend more fossil carbon. You spend more energy just making the fertilizer, farming the land, everything that is needed to do that. And to make matters even worse, In this case, 1.26 kilograms of that carbon that you extract is combusted in the form of CO2. So that's emissions to the air. In this case, all of it is combusted. And so you have net CO2 emissions that exceed the prevailing technology at the time. So the cycle that I showed you before is not inaccurate. It's just incomplete. And so when you actually add all the fossil fuel equivalent inputs, to this process, the conclusion is that you are going to require more fossil energy. Upon disposal, most plastic ends up in landfills. And when you degrade this plastic under anaerobic conditions, it actually degrades to methane, which is a 20 times more potent greenhouse gas. So in summary, if you want to use more fossil energy, if you want to emit more greenhouse gases, If you want to use more agricultural land, this is your solution. If, however, you want to do something good for the environment, this isn't your solution. And so that's the bad news. And just to tell you, when you are in a situation as a human where there are certain expectations of what you're going to do, and then you find you just can't do it because it doesn't seem right, it creates internal conflict. And that's not fun. So I just want to remind you In retrospect, this is all kind of amusing, but at the time, it's not amusing at all. The only silver lining here is that the analysis itself, because it was surprising, got a lot of attention in the scientific press. But to summarize where we are, I've made it out of the Rift Valley. In other words, I was 37 years old, married, had 2 children, lived in a Dartmouth rental unit, behind the hardware store and I figured out what I'm not going to do. And that is not a blueprint for a great career, I can tell you that. So in fact, if you were to hire a career counselor for your child and they told you that's where I want you to be when you're 37, you would fire the person, right? So to make a long story short, That was the bad news. The good news was that I developed an acute appreciation of what problems are that are worth spending your time on versus problems you just slide into because you do one thing, you do the next thing, you do graduate work, then you end up doing a postdoc and before you know it you're working on something and you don't really ever analyze why am I doing this. And so believe me, after spending 8 years on something that I in retrospect decided was useless, you start thinking about that a lot. And so I would say this is one of those key take-home messages of figuring out that it's very important to ask the question of what are the things I'm going to commit to and then when you do it, you do it really well. But that was a key lesson from this experience. And so I was fortunate that in that timeframe, in 2000, in June of 2000, Tony Blair and Bill Clinton had a joint press conference, weren't those days, in the White House and Downing Street. Announcing the first draft of the human genome. And in fact, in February of 2001, the first full human genome was published in the journal Science in February of 2001. And the reason that is a seminal event in the drug discovery industry is that it really changed people's perception of how long it's going to take to develop drugs. And when that genome was published, people were convinced it is going to dramatically accelerate the time it's going to take to come up with new medicines. So there was a great deal of buzz and excitement around it. And I simply asked the question, OK, if that's true, what's that going to look like? And there are really two options. The first option is a class of drugs that you could come up with that we call small molecules. This is aspirin, ibuprofen, Lipitor, small molecules that are designed to inhibit specific biochemical reactions that lead to things that are bad. Bad can be prostaglandins. This is when you get a headache and so you take aspirin that inhibits an enzyme that makes stuff that gives you a headache and it works. Lipitor is a drug that inhibits the formation of cholesterol, so it makes you healthier, OK. So that's the kind of drugs that small molecules are. They're typically synthesized and taken orally. And the impact that the sequencing of the genome would have on small molecule drug discovery was— you could make the argument, but it was kind of a little bit far-fetched. However, the second, I would say, most important class of drugs are drugs called biologics or protein-based therapeutics or therapeutic proteins. They're all the same thing. And these drugs are drugs that are replicas, if you will, what is present in healthy people. So for example, insulin— if you don't have enough insulin, you're unable to regulate the sugar in your blood, and the net result is someone will diagnose you with diabetes eventually. Example number 2: if you don't make a blood clotting factor 8, your blood won't clot, and you're then diagnosed with a disease called hemophilia. You can go on and on and on. Erythropoietin— if you don't have enough erythropoietin because you have kidney disease, an important signal that is supposed to go to the bone marrow to tell cells in the bone marrow to become red blood cells— if that signal doesn't arrive, there are no red blood cells, and you suffer from a disease called anemia, and it goes on and on and on. So there's many diseases where the lack of a specific protein is the root cause of the disease, and the only way to fix that is to provide that particular protein. And the way we do that is we isolate the gene that encodes the protein, then engineer that into a cell that makes a lot of it, and then we purify it and give it to people that need it. And you can see, once you have a blueprint of every single human protein, the direct impact on discovering these drugs was self-evident. So it was pretty clear that it's going to have a very profound effect. And so what happened is that in that same time frame then, you looked at analyst reports of what's going to happen in this industry and they all said the same thing, there's going to be a crunch in biomanufacturing. And however they said it, whether it's a bottleneck or whether it's another bottleneck, everyone was saying the same thing. Because we're now going to be developing all these biologic drugs or protein-based drugs, we're going to run into a manufacturing crunch or into a shortage of manufacturing capacity. And so to make matters even worse, 2/3 of these drugs that could be life— many of them are life-saving— are drugs that in their native state in humans have sugars attached to them. And when they have sugars attached to them, they are called glycoproteins. And that makes the whole thing even more complicated because now you have to take the human gene and engineer it into a cell that is able to put these sugars on that look like human sugars. Otherwise, the protein isn't active and functional in the human body. So the challenge is, how do you make these proteins such that they contain the sugars and more or less replicate what's present in humans? And that problem was solved by this young lady. It's a Chinese hamster. And as early as in the 1950s, we were able to isolate cells from the ovaries of Chinese hamsters and cultivate them in culture. And if you now introduce a human gene into these Chinese hamster ovary cells, they will make a lot of the human protein. And they will put sugars on the protein that aren't quite human but close enough that they pass as a drug. And so by 2000, virtually every single glycoprotein that was administered to a patient was made in the Chinese hamster ovary cell. And this is not because we make everything in China. It just happened to be historically that we ended up with this cell line. All right? So that's part 1. You were locked into Chinese hamster ovary cell lines. And there's another little secret, which is that these Chinese hamster ovary cell lines they like to be in Chinese hamster ovaries. And in order to coerce them to grow in a bioreactor, you had to give them growth media that were typically derived from animals, mostly from cows. So you would give them bovine calf serum and things like that. Remember 2000? Remember mad cow disease? Everyone was completely terrified by the fact that you were giving these animal-derived materials to or into— feeding them into a process to then make a drug that you inject into people. So the story doesn't get any more attractive. In fact, when you make a protein in a CHO cell, a Chinese hamster ovary cell, and then take away the protein and analyze the sugars, what you will find is that you're not actually making a drug. You're making a bunch of different drugs because there's a lot of different sugars. Actually, they're all human, but there are different sugars attached to the protein. And the reason that's not good is because you don't know which one actually is the best drug. Each of these sugars confers different half-life. Different tissue-specific targeting, all sorts of differences, and yet we can't even make one homogeneous product. We have to make these mixtures. And amongst the mixtures, you're lucky if this is your most active ingredient. You're less lucky if it's this, and you're really not lucky if it's this. So we had no manufacturing technology that actually allowed you to make a uniform product. So this was the state of the art in 2000, and so here I was, essentially not knowing what to do. So I thought this is an interesting problem that I could solve potentially. And so I looked at where do people that make a lot of recombinant protein— in other words, clone genes into organisms to make lots of it— where do they go when they want to make it cheap and in large volume? And that's the industrial enzyme business. These are people that make enzymes like cellulases so you can stonewash your jeans or lipases as detergents. Where do those people go? They all go to yeast and fungi because they can make a lot and they can make it really, really cheaply. And so by 2000, I started formulating the idea that one could take yeast and one could engineer the secretory path of the yeast to make human glycoproteins. And I did what any academic would do. You go and write grants. Well, you could do it like this. Not like this. Back then, it was like this. No, joking. You would write grants, and the answer to my grants that I had submitted to the NIH and to the National Science Foundation and to Whitaker Foundation for Biomedical Research is, it's a really tough problem. If anyone's going to solve it, it's not you, because you are not a glycobiologist and you're not a yeast geneticist. And both of them are true. And I'm not going to complain about our funding system. It is what it is, and it's one of the situations where it's the best you can come up with, but everyone complains about it. But to make a long story short, if you want to change careers in this current environment, it is very, very, very difficult. And it's not just that people will tell you don't do it, you just won't have any money. And so when you don't have any money, you're not going to do it anyway. But that's the situation I was confronted with in 2000. And I was fortunate because at the time I was teaching a course with— the former dean of the engineering school, Charles Hutchinson. And he asked me, like, what are you doing? And I told him about this problem. And he said, hey, if you are right and this is a potential solution to this problem, we should start a company, which we ended up doing. And so in 2000, he and I started this company, Glycofy. And we raised money from Dartmouth Angels, Dartmouth-affiliated venture capitalists, and started the work. And lo and behold, let me remind you, when you made these proteins in mammalian cell culture or in Chinese hamster ovary cells, you got these mixtures. Within a few years, we were able to engineer yeast cell lines that were able to make these proteins with exquisite uniformity. So you could say, I want this guy, and we could clone the gene into this yeast and you would get that. You said, I want this guy. So anything you wanted, we would engineer yeast cells that would make these proteins at exquisite uniformity. Did not exist before this technology. So now you could at large scale interrogate the question, which ones are the best? What's the best way to actually make this drug? And so things were going well, I would say, within a few years. And again, the scientific press was quite generous in covering the work. And so by 2005, we had lined up half a dozen pharma companies that were working with us that came to us with their believe me, worst problems. Jürgen is sitting here, he knows. And in January of 2006, we went to the largest healthcare conference that is held every year in the second week of January in San Francisco and Hatch and I met with one of our partners which was Eli Lilly and they met with us on Monday and said, guys, we love what you are doing, we want to do more. We want to do 8 more programs and we said, we would love to but we're fully at capacity, we had just done the deal with Merck, so we just did not have any way of accommodating them. And so we left the meeting, got a message, can we meet tomorrow, which was Wednesday. So we met with them again on Wednesday and on Wednesday they said, we understand that you have no capacity, but we want to acquire the company. And so that then led to a bidding war between Eli Lilly and Merck and in June of 2006, the company became a wholly owned subsidiary of Merck and was essentially gone. And so let me tell you two observations that I think are important. The first one is, had I not decided not to do what I was intending or what I was asked to do when I came, there was no way I could have done this. So creating the optionality by turning something down that wasn't easy then opened this opportunity and so I'm very fortunate in retrospect I made this decision. The other thing I want to talk about briefly is the role of basic science versus engineering. None of the work at GlycoPhy would have ever been possible had it not been for the investment of thousands of men and women years to understand the basic science to even start the conversation. Someone had to figure out how does yeast glycosylation work? How does human glycosylation work? How do glycosyltransferases locate at different parts in the secretory pathway? What are the genes encoding these enzymes? How do you analyze carbohydrates on the surface of proteins? It goes on and on and on. That body of knowledge was created by people that we as the taxpayers support and fund through the National Institutes of Health, the National Science Foundation, and collectively we spend about $40 billion in figuring out how the world works in the United States. And this is about 0.3% of the GDP. Roughly 1% of the budget. We're like most other advanced societies, Japan and Europe, in our respective spending to support the understanding of the world around us. OK? And so let me now tell you what my understanding is, or has become, of what the role of the engineer is. There's something called human needs. And oh, one more thing before I move on. When you are a basic scientist, your metric of success is finding new stuff. Figuring out new things that we didn't know before or figuring out things that we thought were this but in fact they were something else. And the more orthogonal your findings are to conventional wisdom, the more exciting it is, the more publications, etc., etc. Okay, so that's how you measure success as a basic scientist. As an engineer, your job is somewhat different in my opinion, and that job is to understand what goes on in the basic sciences and and to figure out what is possible with what we know now. In other words, create a solution space that sort of envisions all possible solutions and looks at where does that overlap with the human need. Where can I build something based on what we know about the science that ultimately benefits a human? And what that does is it then changes your metric of success conversation because it's not merely I've published all these papers, It's how many lives have I touched or how many people's lives have I changed. And when you have that conversation, it gets a little bit more complicated, as I will show you a little bit later. But so you need engineering, in my opinion, to go from here to here. Let me give you one other great example. One of the most exciting areas in modern medicine is the ability to edit human genomes. And how did we find that? We supported basic microbiologists to figure out stuff. And what did they find? They found these repeats in the genomes of bacteria that they sequenced. They're like, what's this? They look further, they found there's a protein complex that is akin to a bacterial immune system to help the bacteria defend themselves against phage invasion that has the ability of in a very specific way making incisions in DNA with the help of a guide RNA. And it is that system that we ultimately hacked and engineered to then allow us to engineer human genomes. So had we not made that basic investment to look for stuff that we had no idea what implications it could have, we wouldn't have that capability. So I think it is enormously important to sort of retain the sanctity around basic discovery and not putting basic scientists under the pressure, show me what you've got, how are you impacting lives in an immediate way. I just don't think that that's how we should approach this particular activity that I think is noble and very important. So if, however, you want to be an engineer as I describe it that wants to connect these two things, you need to have some engineering skills. That helps typically. You need a lot of capital. There's a complete underappreciation. I see some of you in the room here, you'll know this, right? And Joe, you'll attest to this, right? The underappreciation in academia of what it takes to move something from here to here, I can't tell you how big that delta is, but it's big. I currently, as Phil already mentioned, I'm involved in 4 companies that I founded over the past 10 years. Those 4 companies annually, well, they employ 200 people. They annually spend $60 million just to move stuff from here to here. And just again, context, $60 million, that's $250,000 a day. So I'm going to have to wrap this up soon here because if things go up— and so where does that money come from? Where does that capital come from? It comes again from philanthropic organizations, Bill Gates or Bill and Melinda Gates, venture capital, they spend about $6 billion a year in R&D in pharma. Pharma spends a lot of money trying to turn insight into drugs that change the world. So I think one has to appreciate how much money is consumed by that activity. The other thing I want to talk about is this concept that everyone talks about, innovation. It's one of those things that everyone talks about and everyone actually thinks it's something different. And so I want to just give you some thoughts of what I think it is or what resonates with me. This is a definition that Peter Drucker, who is sort of the father of institutional management and behavioral science of organizations, came up with. And he said it's the innovation— sorry, innovation is the specific instrument of entrepreneurship, the act that endows resources with a new capacity to create wealth. Most of you know that silicon in the form of silicon oxide or sand is one of the most abundant elements on the planet, actually the second most abundant element on the planet, and therefore it is mostly worthless. However, if you take sand and you turn it into this, an integrated circuit, it's worth a lot. You have now endowed sand with the ability to create wealth, and that's innovation. I'll give you another example. This here is a yeast— oh, no, this is not. This here is a yeast that you can buy at the co-op for $0.75, and this here is a yeast that we taught some tricks. And Merck bought this yeast for $400 million. So you can see that there is something going on here in the innovation department that has endowed this yeast with the ability to create wealth. All right, so let's go back to this question that I had addressed or thought about before or mused about, which is impact. So what about the impact? So if you look at this whole glycofy experience, if you measure impact by traditional academic metrics of impact factors, we had published papers in Science, in Nature Biotech, in Nature Reviews, in the Proceedings of the National Academy of Sciences, You would say impact factor, check. Next question, financial success. The investors that put money and allowed this to happen put $35 million into Glycofy. When the company was acquired by Merck, they owned about 85%, and so they were able to sell their stake in the company for $340 million. Financial success, check. Okay, for them at least. All right. And then when you go back to what I had talked about before, namely, what was the actual impact on patients? Well, it's a pretty sad story. The actual impact on patients was nothing. Merck acquired the company. They ran 2 clinical trials. One of them, they could not recruit enough patients. In other words, they designed it that the enrollment criteria were so odd that they couldn't find enough patients to run the trial. So that's gone. And the second one is a story that is worth telling because it's just so interesting in my opinion. In the 2005 time frame, the biggest biotech drug ever was a drug based on recombinant human erythropoietin called Epogen. Amgen was selling $5.5 billion of Epogen every year. And when in a free market economy, when someone does that well, other people want a piece of the action. And so two folks, Roche and Hoechst-Marin-Roussel, which is now Sanofi, challenged Amgen's patents and wanted to get a piece of the action. And so there was massive litigation going on for several years. In fact, many friends of mine were expert witnesses and were involved in these lawsuits, which were quite interesting. But what came out of it is something that is unusual, namely very crisp clarity of what the patents actually mean. Most people don't know this. You have a patent, means nothing until you litigate it, OK. These were thoroughly litigated, believe me. And so what was clear in 2008 is that Amgen had protection for anyone to make erythropoietin until 2008. Nobody could make it. And then from 2008 and 2011, they had one remaining patent that claimed the production of recombinant human erythropoietin in vertebrate cells. So a Chinese hamster has a vertebra, can't make it. The clever patent lawyers that drafted those claims never envisioned that there would be a yeast under the radar that doesn't have a vertebra engineered to make a product that is in fact superior. And so Merck was very excited to run these trials following the acquisition, but what happened was, that a study on a large patient population showed that there was some cardiotoxicity in patients that had received erythropoietin. And whether it was actually the erythropoietin or because they had renal disease and there was other— nobody knows. But there was caution in order, and the FDA issued guidance and said, if you want a new erythropoietic drug approved, you're not running trials with 400 people. You're going to be running trials with 8,000 people. And that moved the price tag from a trial from $40 million to $800 million. And at that point, Merck said, I think we're out. And so that never materialized. And so the lesson from this experience in my view is if you finally have a tool, don't give it away. Don't sell it too early. Hold on to it. Here is where the next story sort of evolved. And by, again, the mid-2000s, a whole new class of drugs based on human antibodies emerged as having major impact in the clinic and, for that reason, having major impact commercially. And these drugs— I'm going to show you a quick video. So what you see here on the left side is a human B cell. That on its surface makes a protein called CD20. And when these human B cells proliferate beyond control, you have a disease called non-Hodgkin's lymphoma. It's a cancer that you can treat by killing these cells. And we all know that you can treat them with chemotherapy. In fact, we're very good at killing cancer cells, by the way. What we're not good at is killing cancer cells and leaving healthy tissue intact, right? So it's the specificity that is the issue. So in this case, a drug was developed based on human antibodies called Rituxan. And this antibody, shown in green here, with exquisite precision binds to this one protein that is only present on the cancer cell but binds to nothing else. And once it binds, it recruits natural killer cells from the immune system. They release cytotoxins and kill the cell. And they do this in a very specific way. So now I think with this video alone, you can get why the drug industry was like all over this. These drugs really promised profound change in the care of patients. You may remember recently Jimmy Carter had skin melanoma that had metastasized to the kidney and to the brain. 10 years ago, we're done with the conversation, right? He gets one of these antibody treatments, recovers, cancer disappeared. It's in remission. Not just like we extended his life for 18 months or something. I mean, these are really miracle drugs that when they work— they don't work in everyone— but when they work, they have a very, very profound effect. And so you could see that this was an estimate from 2006. At that point, there was about $18 billion worldwide in worldwide sales of antibodies, and that was expected to double in the next 5 years. So it was an extremely active area within the pharmaceutical industry. And if at the time you listen to any CEO from any major pharma company, what they would tell you is 30% of our pipeline is going to be biologics or antibody-based. Whoever it was, they were tripping over each other to make that number as big as possible because that's where they saw the future. So seemed like an interesting situation where they were promising certain outcomes and at the time I was looking at, well, what technologies they have, to discover these drugs. And it turned out it wasn't a really pretty picture. This is like someone showing up in a Speedo and flip-flops telling you they're going to climb Mount Everest and you say, maybe, but you're going to need a jacket, you're going to need shoes, you're going to need a bunch of things to make that happen, right? And so this is kind of the delta between the technology that was available at the time and the ambition that was driving the desire to get into these drugs. And so I thought if you build something better, then you would have people wanting to use it. And as you will see, these companies are all hypotheses. You say, I think there is a need or I think there is a problem, I think if I build something better, people are going to want it, and that's exactly what happened. And as I was studying and reviewing this field, I kept on coming across the name of a colleague of mine at MIT named Dane Wittrup. Who is actually here. And Dane had— at the time was a really world-renowned protein engineer that had used yeast to engineer proteins and to improve them. I'd spent the previous 6 years at Glycofy engineering yeast to make yeast make better, higher-quality proteins. And so the 2 of us and a former student of mine decided that we were going to start a company to develop technology to discover these antibody drugs more effectively. And so this is what this roughly looks like. So what you see here is, I don't know, 7 different yeast cells. And we were able to engineer these yeast cells in a way where each of the yeast cells produced a fully human antibody and presented that antibody on the surface of the yeast cell. And we don't just have these 7. In fact, we did this in a way where we have 10 to the 10th, which is 10 billion different yeast cells, each making a different fully human antibody. By the way, each one of you in this room, your circulating B cell repertoire is about 10 to the 8th, so much, much smaller. So this is essentially the immune system of 100 people in a tube or in a bunch of tubes. So that is the first step. The next step is then you take whatever you want to develop an antibody against. For example, the surface molecule that I showed you before, CD20, you would take that and you would chemically modify it to make it fluorescent. And then you would throw it into the sea of different yeast cells. And what happens is when you have 10 billion, some of them just by accident are going to bind what you just threw in. And sure enough, when that happens, that one yeast will sequester the proteins on the surface. And because we made the protein fluorescent, that yeast is going to be fluorescent. Whereas all others are not going to be fluorescent. And if you can afford this instrument that some of you are familiar with, a FACS sorter, you can actually separate those two by taking this population that is mostly red, in other words, non-binding, with a few binders in it. You send them single file through a capillary tube. And you interrogate them with a laser. And when the laser sees fluorescent, it switches this plate down here and switches the charge. And then throws the yellow cells to the left and the red cells that you don't care about to the right, and you get rid of them. So in summary, this process can be shown here, where again, this is the yeast cells that on the surface have human antibodies. You throw in a protein that you want to develop antibodies against. You make them fluorescent. Some of the yeast will sequester them on the surface. You send them into this fax machine. The fax machine will give you populations that don't bind, which you clearly don't care about, so you throw them in the trash. And the ones that bind, they go up here. And we engineered this in a way where once they're here, we simply change the growth medium, and the yeast now no longer presents the antibodies on the surface but secretes them into the medium. A day later or 2 days later— Jürgen tells me it's a day later now— you purify the antibodies. Put them in a tube, and now from the beginning to the end of this, this is a process that takes weeks that formerly took months, if not years. And so this dramatically changed not just the time frames it took to discover these drugs, but now you can test them and see, do they actually have the biological activity I'm looking for? Are they actually really going to be drugs? And that question that used to take years to answer or months to answer is now answered in a much, much shorter period of time. And so time is a big component. However, I will tell you, because this is a synthetic immune system, we can ask questions in a way and we can tease out molecules that you just simply can't get to any other way. And I would say one of the biggest compliments we got was, again, from one of our collaborators, which happened by accident or by chance to be Eli Lilly again. The head of biopharma at Eli Lilly said, you gave us in 3 months what we couldn't do in 5 years. This is a guy that runs an organization with 250 people in discovery. And so it is that differentiation that allowed us within a relatively short period of time convince the world of drug discovery that if they want to develop these kinds of drugs, they should come to us. And so again, you can ask the question, what's the impact? And we had a paper in Science last year. We had a paper in PNAS this year. So I think we're doing OK on that sort of conventional metric of publications. And the problem is that in drug discovery, from discovering a drug to getting a drug approved, that takes typically on average 13 years. So you have to be a very patient fellow if you want to really claim that success of having a drug that actually touches someone's life and changes their outcome. And so I can't tell you— that we've been able to achieve that, but I can present you with some surrogate metrics that show how much impact this technology has had over the past 10 years. And so the first one is just the number of partnerships that we have. And again, this is— this is no time to be modest because really I do not know of another technology, a discovery technology that was introduced to the pharma industry that within such a short period of time has had such a broad adoption rate and in these 40 years— sorry, not 40 years— in these 8 years since 2009 when we started partnering, we first did 2 deals with Merck and Roche and from then on, it just kept on going and over those 7 years, we have partnered with half of top 20 pharma, many publicly traded biotech companies and more recently have even had academic institutions like MD Anderson and Memorial Sloan Kettering come to us And this is not like, hey, let's write some grants together. This is they are paying us to discover drugs for them so they own more of the drug at the end. So if you look at the innovation waterfront, we are working with people very early on in academia all the way to some of the largest pharma companies in the world. So over these 40 partnerships now, we have worked on 160 drug discovery programs, which is really an incredible number. And of those 160, at this point, there are 4 in the clinic. There are 4 more expected to go into the clinic this year. The most advanced program is a phase 2 clinical trial that I want to tell you about a little bit because the excitement that we have by doing this is really remarkable in the following sense. This lead program that I was just mentioning is a trial that is carried out by one of our partners, Arsanis, in an indication called VAP, which is ventilator-associated pneumonia. If you have a bad car accident and you end up in an emergency room— not an emergency room, in the ICU— you typically can't breathe. So they intubate you and they assist the breathing. And when that happens, when that tube is inserted, it often is colonized with staph. And that colonization, in a third of the patients, leads to the development of pneumonia. And of those, a third die. And so it's— and again, forget current antibiotic treatment. This is— they get everything we have. It's just not effective anymore. So this disease VAP is something that we, with this partner, Astana, developed a set of antibodies against that completely neutralize the toxins that are involved in this process. And so there's a trial going on now with 500 patients in 10 countries, 50 medical centers where these 500 patients are selected into 2 groups. One group gets placebo treatment, one group gets our treatment. And what we expect to see at the end of that, in the placebo group, you should see about 80 mortalities. And in our group, we don't know. If it's 75, you don't have a drug. If it's 5, you definitely have a drug. And we see this now. Every year, we're going to be turning over and unblinding data on trials where we were the ones that first created these molecules. And you can see why that's a really incredibly exciting time for us, that as these programs go to the clinic, seeing that sort of impact is really remarkable or exciting. And so if you look at this pipeline by now, by 2025, we expect to have 9 approved drugs. This is drugs actually treating people every day. So we've now finally arrived at the last and final act, Act 4, which I already told you that in order to come up with a new drug, you have to first discover the drug. You then have to produce the drug. You then have to purify the drug. And then you put it in a vial. And then a doctor can administer the drug to a patient. And the reason I'm telling you this story as the final story is because I give versions of this talk in other places and typically over dinner people sort of lean over the table and they say, what's the next big problem that I should be thinking about, right, as if I'm like the whisper— the horse whisperer of good problems to solve. And I have to tell you, I don't really look for problems. They somehow present themselves and I listen to people what they say and then I say, well, if that's what you want to do, what do you have to achieve that? And if there's a big delta, there's an opportunity to do something. So this is a case that I want to talk about because it shows you how these problems arrive sort of at my doorstep, if you will. And again, just for clarification, I told you about production. That's what Glycofy was doing. I told you about discovery. That's what Adimab is doing. And so there's one gap, which is purification.— and that's what I'm going to tell you about in a minute here. And so what happened here is that I had a student in my lab, a graduate student, Kevin Isett, who had worked for many years in the Merck vaccine process development group. And when he was a grad student in my lab, he kept on telling me, you have no idea how bad life is there, how many programs have to be abandoned because they can't actually come up with a process to make a drug that is pure enough that you can inject it into a patient. So this purification problem is a really, really big problem. And he was very insistent. I first didn't believe it. I then did believe it because he was so insistent. And so what happened is that Kevin, my former grad student then, Warren Kett, who was a researcher in my lab, and John Scheller at Dartmouth '09, who had worked with me in other companies, we got together and founded this company Avitide to solve this protein purification problem. And again, it's a hypothesis. Do you really have a problem? And whatever you come up with, is it really a solution that people are willing to pay you for? And so Kevin and his team have really done a remarkable job that in just like 3.5 years signed up 8 pharma partnerships working on 14 different programs. The company employs 35 people now. And so it really came from like, hey, here's a problem to something that I think within the next couple of years has the chance of really touching processes that actually lead to drugs that end up touching patients. So with that, I have reached the end of Act 4. And at this point, I don't know what the evolution is. I'm considering going into politics, or I will just stay calm and motor on. I don't know. But in closing, I would just like to say the following. I've had the privilege of working on some really incredibly interesting technologies and have had my successes, and none of this wouldn't have happened with the partners that I found to do this. I really think that it is through these partnerships that both I have grown as a person, and it's not about who's the president and who's the king. We know. But it is developing a joint vision of what do you want to actually do. And Dane and I had both started companies, sold them. We know what that feels like. But if you really want to truly impact your field, you have to stick with it for much longer. And so we both have been at the helm of Adamab now for 10 years as this company is just entering into this phase where you're going to see real drugs changing the outcome of patients. And I think I just have been incredibly fortunate to have these partners, and I would be remiss in not recognizing them here and thanking them for being such awesome partners. So with that, I want to thank you all for your attention and open the floor for any questions that you may have.

Easy. Jeff, please, could you briefly tell us what Avitide's technology is?

Yeah, it's basically— it's large libraries of peptides that have been designed to be very resistant to chaotropic agents, to changes in pH, which is the environment they have to go through to survive the clean-in-place processes. So it's libraries of peptides where you find peptides specific to a drug product and then you attach them to resins. It's not rocket science, but doing it well is more challenging than you would think. How important is the sort of interplay between between the research at Thayer and the companies? So of the companies I told you about, Adimab had virtually no— there was no contact at all. With Glycofy, Dartmouth was very generous in allowing us at the very beginning to incubate the company at the college, and so that really helped us get the company off the ground. In the case of Avitide, the students had done some work in the lab, and so in exchange for that, we gave start with an equity position in the company and so that's how that was solved. So sometimes there is a relationship and sometimes there isn't. Intellectually, there is the source of some of these ideas, does that play out in the lab? So the source of the ideas, so virtually all universities in the United States have a policy that if you come up with something as part of a consulting arrangement or you're thinking about something in the shower or wherever you think, that that is stuff that we don't own, that we leave that to the faculty. And so they can then do whatever they want with it. Now that you have such a wonderful understanding of how to engineer this innovation process, can you go back and solve the garbage problem? Um, it's— it's— so this— I'm not going to answer that question, but I'll answer the question of what I think are important problems and problems that, again, the older you get, the more you think about different things and the more you care about different things. One thing I really care about a lot at this point is criminal justice reform. A lot of people in jail in this country based on junk science, bite mark identification, stuff that people are spending decades in jail that we are paying for that shouldn't be there. And I think having brought science to that discussion and to the criminal justice system has done a lot of good. And so that's something I'm very interested in supporting and spending time on. And the trash problem, I mean, I hate to spend my time on bad human behavior. No one should have thrown the trash away in the first place. And so that's not something I am super excited about spending any time on. Any other questions? All right. Oh, do you have a question?

I would actually just follow up a little bit more, I think, not on the ownership question of the insurance, but between the companies that you're working with and the lab, but more on the intellectual side and sort of how do you stress test some of the art of the possible against what the requirements are? —what you do in your lab. I mean, you've given a really fascinating set of stories, and I think there's a lot to be gained from that.

What is the question?

So the question that you were asked— I think you were asked a slightly different question than you answered. OK.

I think you were asked about— I do that? My wife says that all the time.

I think you were asked about some of the benefits of having the corporate interactions that you've enjoyed as opposed to some of the intellectual rights issues.

I would say the corporate interactions as far as pharma is concerned, just seeing how they operate, you have no idea when you're in academia. You think these are all logic actors and I mean all these things that you assume that aren't true. So I think having had that insight and having a much better understanding of how they struggle to do anything innovative, because everything happens by committees. And by the way, the worst thing you can do when you're employed in a large pharma company— is this video still on? The worst thing you can do is be wrong. In the companies that I'm involved in, we're wrong all the time. But we look at the data, we make the best decision. If we're wrong, we go back and make a new decision. In pharma, you're gone by then, right? And so you're much more interested in hedging against wrong decisions than being willing to make decisions, revisit the data. If the data tells you something new, you go back and make a new decision. It's not a big deal. And we do that all the time. And that culture, I mean, is intoxicating. It's really, really fun. And so again, part of the challenge as founders is how do you create a culture where the truth prevails, the best ideas float to the top— they're not mine, they don't have to be, whoever's ideas they are. That's not easy to do. But when that happens, It's magical in my view. Yeah, so? Why do you stay in academia? Ha, see, I was hoping someone would ask that question. I have to say— I'm listening to the answer. Let's talk about that startup package. No. I, to this day, am in contact with students that left this institution on a regular basis. 15, 20 years ago. And the reason that is, is because I must have played some important role for them at the time when they were here and they were going through a very transformative and important experience in their life. And it is extremely rewarding to see them go out and do their own thing and still call me and say, hey, I'm thinking of doing this, what do you think? And it doesn't happen again in every class every year, but it happens sufficiently frequently that it is an incredible source of satisfaction over time. To have these relationships and to be able to nurture them and you get something back from it and I'm sure you know what I'm talking about but it's a very long-term investment that you don't get anywhere else.

So on that inspiring note, please join us for a reception out back and Bob Fuller, Tilman Lustig, Tilman one more time.