9UNP0184SD_Lee_Hood_WordPress

- Well, it's a pleasure and honor to be here. Oliver, you know, it's really terrific to speak to an overflowing auditorium. It's what every scientist dreams of. I'm hoping in the future I can give more lectures together with Oliver. 
(laughter)
 Oliver's instructions to me were tell the students a little bit about your career before you get into the science side of things. So I really thought I would do that. I grew up in Montana, my dad was an electrical engineer. He made me take circuit courses in electrical engineering when I was in high school, which I really hated. 

But I have to say in retrospect, they've turned out to be incredibly useful in ways I never, ever imagined at that point in time. The other seminal experience I had in high school, is I was helping my chemistry teacher when I was a senior, teach sophomore students biology, and I was lecturing from Scientific American. And I remember, this was back in just the post-historic days of the structure of DNA. I remember in 1956, an article in Scientific American on the structure of DNA that made me realize biology was truly incredible. Now I don't think I understood anything about DNA at that point in time, but just the structure of that molecule was really a defining moment in my life, and deciding to go into science. So I went to Cal Tech as an undergraduate. It was an overwhelming experience. I grew up in a town of 2000, with 140 kids in the high school. We had never had calculus. Going there to Cal Tech, where there were all these prep school students was a culture clash the likes of which I have never seen before. 

But Cal Tech was really an incredible place. There, you could get to know people. I had Feinman for freshman physics. I had Pauling teach me a lot of chemistry. And what really struck me about those individuals was their conceptual teaching. I decided that's really how we should teach. I'll talk more about teaching toward the end of my lecture. I went from undergraduate to medical school, as you heard. And there, really got interested in human biology. I think everything I am doing now I started thinking about really, in medical school. 

And the thing that most fascinated me was, I remember in 1961 writing a report on antibody diversity, it wasn't quite called that at the time, but it was trying to differentiate between instructionalistic and selectionistic theories. I thought gosh, this would really be tremendous to work on. I looked around after medical school, and went to Cal Tech for graduate school because Bill Dryer was there. I'll say more about Bill in just a moment. But he said, I have this great Saturday afternoon project you can come and work on, and that is, inducing multiple myeloma tumors in mice. You can purify the proteins, sequence them, and see patterns of antibody diversity. It was exactly the kind of thing I wanted, so it was a terrific match made in heaven. What was really lucky for me, we started doing the sequence just as this whole field of antibody diversity broke. And so I got, as a second year graduate student, all sorts of these conferences, and gave lectures on antibody diversity. And it was in that context that I first met Oliver. 

I have to say, in this field of antibody diversity, and there were many different people, and I think there were two individuals that really stood out in my mind, and Oliver was one of the two. And Oliver stood out, because on the one hand, I love the way he thought analytically about this, this problem with antibody diversity. I think, frankly, about all problems. But on the other hand, I was really interested in technology and I loved the way Oliver had the same attitude that I've come to have, mainly that biology should be the driver, but you have technologies to move biology ahead. So there was this coordinated and synchronous integration. And I think, in that sense, we were really soul mates. What I went away from my graduate years with is two dictums that my mentor had said. If you practice biology, always be at the leading edge. It's more fun there. And if you really want to change a field, invent a new technology. 

And in that, this quote by Freeman Dyson, I think, is really a telling one. "New directions in science are launched by new tools much more often than by new concepts. The effect of a concept driven revolution is to explain old things in new ways. The effect of a tool driven revolution is to discover new things yet to be explained." I really think that's true. We'll talk about that in some detail. Well, I went to NIH after graduate school, and that was a very exciting time. It was the Vietnamese War. Really terrific people, all the leaders in American medicine were there. But I left NIH convinced I wanted to really integrate a career in developing technologies with a career in doing biology. 

And I went to Cal Tech as a young assistant professor and got started in that sense in a series of, I think, really paradigm-changing adventures. I was only a part player in some of these things, but it was, it's been an enormously exciting time over the last 35 or 40 years. And they are: technology development and integration, something that was relatively new back in the early days of biology. The human genome project. Cross disciplinary biology. Systems biology, and its application to medicine, which is leading to P4 medicine. I'll talk about all of these things. I think the most fundamental thing I learned from participating in these revolutions was that it's really hard to make change in old institutions. And new ideas often need organizational structures. I'll go through and talk about some of the experiences I've had in that sense. 

So, as I said, when I went to Cal Tech, I told my chairman, Bob, that I really wanted to spend half my time doing technology development and half my time doing biology. He didn't say anything at the time. And so it was with some surprise when after three years at Cal Tech, he came in to me and said, "I've come to advise you in the strongest possible terms to give up this technology development." And I said, "Gee, it's going very well. I'm not going to do it." And, "I think it's really important." And 20 years later, I had the presence of mind to ask him why he came and said it. He said it because the senior faculty in biology felt it was unseemly to have engineering in biology. And their strong suggestion was I should move into engineering. He said at least I didn't ask you to do that. 

But that's the flavor of good places, that they are conservative, and they have a silo view of how science should be done. That's something students want to get around. The other advice I'll give you is, do what you think is right. Don't worry about what other people say is right. You ought to figure out what is right. So, what the dictums that I had for tool development at that time were that there were these different types of biology information, DNA, RNA, and proteins. Later, as I'll discuss, there are these things called systems. I wanted to think about developing instruments that could decipher biological information. And as you'll see, that's what these instruments did. The second dictum that I really believed was this old one from Bill Dryer, mainly, that biology and medicine should drive the development of relevant technologies, but once they are developed, they have an opportunity to revolutionize biology. 

I'll show you some instruments. As you heard, we did the sequencers and synthesizers. I'll say for the DNA sequencer, one of your own, Boyd Smith, played absolutely a seminal role in developing the chemistry toward automated DNA sequencing and has never gotten the credit I think he deserves for that enormous contribution. When I moved to the University of Washington, we did the Ink-jet technology, that has been commercialized. That's when we started thinking more seriously about systems, as we'll discuss in a few moments. One of the really interesting things that happened to me, and the consequence of developing these things, is a good friend of mine came and said look, it's unfair. You've got these instruments, or you are developing the instruments. Why don't you commercialize them so they will be available for everybody? And I said gee, that's really a good idea. It got me thinking. 

I went to the president of Cal Tech and said, look, we've got these instruments, we'd like to commercialize them, what do you think about that idea? This was in '79, and he gave me the incredible lecture about the role of academic institutions. It's scholarship and education. We are not going to sally ourselves by commercialization. If you want to do that, you can do that on your own. That was the attitude those days. It's the attitude of many places, even now. And the real issue is transferring knowledge to society. I think that should be one of the fundamental roles every scientist plays. If you do useful and relevant things, get it to society in a way that it can be used. 

So the story was really interesting. I went out into the hinterland and I talked to 19 different instrument companies, and I said, gosh, we've got all these instruments, or we're going to have these instruments that will change biology, and how would you like to develop the instruments? And after a year and a half, I was 0-19. In fact, Beckman instruments, the leader at that time, told me after the third time not to come back. And this is interesting, as you will see in a moment. The only one that really took it seriously was Dupont. But in the end, they decided they would spend the money on a clinical analyzer, rather than these basic science instruments. Fortunately, someone who became a very a good friend, Bill, a venture capitalist in San Francisco, called me and said, I hear you've shopped these around unsuccessfully. I'll give you $2 million to start a company. I thought that sounds like a great idea. 

I went back to Merv Goldberger and he said we're not going to dirty ourselves with venture capital money. This is when Genetics Systems and Harvard were going through all the contortions, and everything. But I was persistent. After six months he said okay, I give in, because I had made the argument. It's the only way it was going to be done. And then faithfully, I gave a seminar to the Cal Tech trustees, the head of the trustees at that time was Arnold Beckman. And I gave the seminar about the revolution these instruments were going to cause, and everything. And Arnold came running up afterwards, and he said this is incredible. This is exactly what Beckman Instruments needs. 
(laughter)

 And I said, well, gee, you know, I'd been there, and I wasn't, I wasn't sure that they were very interested at all. And he said impossible. So, he flew up the next day and talked with them. And it led to complications that you can't even imagine, or I'm not going to describe. But, in the end, we did start the company called Applied Biosystems. And Applied Biosystems, because Mike had done such a superb engineering job on the first instrument, the automated protein sequencer, it was in the black within six months. It's done a wonderful job over the years in instrument commercialization, and so forth. So I realized then that it was really critical to take technologies and move them to the next stage through commercialization. So I've had a lot of experience in being involved in starting different companies, Applied Biosystems, and the same time we started Amgen. It was a different vein, but it was very much in the purveyance of looking at new kinds of opportunities that were really striking. 

And we played a role in sequencing Epo and the cloning of that first biotech product, and so forth. The really important point, was the instruments never would have gotten out there in a timely manner, unless we started the new entity, Applied Biosystems. And there were two things I learned from this experience. One was it's very fortunate none of those 19 instruments companies ever took me up on it, because we could never have hired the talent, we would never have had the focus, we would never have had the resources that we did through Applied Biosystems, to put into developing that kind of instrumentation. And the second lesson I learned which is equally important was, if you have a vision about things you want to change, only go to the top person. Don't go to middle level management that is worried about profit and loss, and things like that. It was the Arnold Beckman, who in one microsecond, thought what this would be. So again, I was really thankful I had gone there first so they could say no and we had Applied Biosystems. What came from the automated DNA sequencer, though, was a new kind of opportunity. And that was Bob invited me to the first meeting that was ever held on the Genome Project in the spring of 1985. 

And 12 experts went to pass judgment. Bob was thinking quite seriously about setting up a center to sequence the human genome. And he wanted to get evaluation of the project. What was interesting about that day and a half meeting was the genome, which at that time seemed impossibly complicated, one of my friends in 1985 said it will take 100 years if it will take a day to sequence the genome. He said, only if you went to China, and got all the Chinese to each sequence three base pairs, then you might do it more quickly. But it was a really interesting series of conclusions that came from that meeting. One was that it was feasible, although enormously technically challenging. But two, we were split 6-6, on whether it was a good or bad idea. And people who were against it were really against it. What was interesting, is I went into the community in '85 to push this kind of idea. 

There was hostility against this idea the likes of which I had not seen. And I would guess initially, 90% of the biologists were opposed. They were opposed on two grounds. One was, this is big science, big science is bad, it will smother small science, small science will never have chance. I tried to explain how synergistic these things could operate, as they have. It didn't get through. But the other conclusion was, and there were a lot of people that felt that it's all junk, most of the information will be irrelevant, you are not going to find anything; you will not get good people to do the human genome, so it's going to be done poorly. And those were the two categories of arguments. But fortunately, there was a committee that endorsed it unanimously, and the bitterest opponent to the genome project, it's interesting to remember, in '85, '86 and '87, was NIH. NIH, the director of NIAID said, and I quote, "We are spending $300 million a year on the genome project, and it's called genetics." 

And of course that encapsulated how poorly people understood what the difference between genetics and genomics was all about. What really made it possible to do this was that NIH, a new institute was created. And it's mission was sequencing the human genome. It was successful, as we all know. Again, what came from developing the automated DNA sequencer was, my understanding again, in the mid-80s that to develop more and more technologies, we were going to require integration of different kinds of expertise, molecular biology chemistry, computer science, and engineering in the case of the sequencer. That got me to thinking about, why not reorganize biology departments, and create them along cross disciplinary lines. So I went to another president of Cal Tech in '89 or so, and said, you know, I've got this idea. I'd like to start a new department at Cal Tech called Molecular Biotechnology, and it's going to be cross disciplinary. So he said that sounded very interesting. If you can persuade your faculty colleagues, we'll do it. 

So, the chemists and engineers loved the idea. The biologists vetoed the idea. And that was when I had made the agonizing decision to leave Cal Tech and go to the University of Washington, enabled by a grant that Bill Gates gave us to start the new cross disciplinary department. And the idea was to bring all of these different flavors of scientists together in the context of focusing on the problems of biology. For the first eight years that we were there, this department was really successful. So, two of its faculty members really pioneered the two first key technologies in protiomics technology, and a program for computationally identifying proteins from mass spectrometry fragments. Phil Greene developed the key software for the genome project. Another developed an incredible new multi-parameter cell sorter. We developed an ink-jet technology that we actually went on to commercialize. We actually had, for interesting sociologic reasons, not one, but two genome centers for sequencing the human genome in our department. 

I had gone to the University of Washington, interestingly enough, with a commitment from the Dean of the School of Medicine to spend four years building up a cross disciplinary department. And at that time, to get another four, and more space and resources to develop a systems biology department. And what unfortunately happened at that time is he died at the end of the first four-year period in a avalanche in the Himalayas. The next Dean had a totally different set of priorities. And after attempting to work through our differences, and the differences weren't just differences with individual, but they were really differences with the system. And let me show you how different systems biology is, in some ways, at least in the classic department. So it was driven by this new vision of systems biology. It absolutely required this cross disciplinary environment, facilities, and a strong computational infrastructure, and a lot more space than I was ever going to get at the University of Washington. But it also had a sociology that was different. The problems were faculty had to work together in teams, and whether young and old faculty can work together, and tenure still works, is an issue everyone is facing today. 

We needed engineering staff. We needed to do strategic partnering. I'll talk more about that later. And I wanted to be able to deal with intellectual property, so I could create a future endowment for this institute. And I wanted to be able to fund raise. And essentially, none of those things could be done in the context of a traditional medical school. And it was for that reason that I went to, I resigned and started the Institute for Systems Biology that we'll talk about in just a few moments. Now, I had started thinking about systems biology at the behest of Max, in the late '70s and early '80s. This was when I was doing molecular immunology. And Max would come and he would nag at me and say, you know, you are never really going to solve the problems of immunology one gene or protein at a time. 

You have to take a more systems approach. He was doing that, actually, at the time, although we didn't really have the tools to do systems biology then. And I realized in the mid-'80s that this was really going to be the way that the future. I sent a couple grants to NSF that never came close to getting funded. I don't think the reviewers understood what I was trying to do. I'm not sure I understood what I was trying to do. What really changed, of course, was the sequence of the human genome project, which came shortly after the turn of the century. Because there for the first time we had a parts list, we knew all the genes, and by inference, all the proteins. They opened up, obviously, the fields of genomics and protiomics, and new computational tools and new measurement and imaging tools, coupled together with the system's view of biology was really transformational. Underlying systems biology is this idea that biology is an informational science, I'll say more about that in just a moment. 

But when you point these systems approaches at disease, you realize very quickly that our current reactionary medicine is going to be replaced by what I call P4 Medicine, Predictive, Personalized, Preventive and Participatory. I'll talk in a few moments about what I mean all of that. But let's talk about this idea of biology as an informational science. It lies really at the heart of our system's view of what biology should be all about, medicine should be all about. So, there really are two types of basic biological information. The digital information in the genome, and the environmental information that comes from the outside, impinges on. And indeed, the purveyance of systems biology is to understand how these two types of information interact and lead to evolution, development, physiologic responses, aging and disease, as we will talk about later. And I think these are all areas that are ripe for attack from systems approaches. The biologic structures that manage the information fall into two classes. One, there are biological networks of various types that do it. 

Protein networks, gene regulatory networks, MicroRNA networks. And two, the information from these networks is directed at simple and complex molecular machines. It's they that actually execute a lot of the biologic function. Here is the most sophisticated gene regulatory network that we understand to date. It has about 65 transcription factors in it. Davidson has pioneered this network, which hardwires and specifies the nature of development in the early sea urchin larval development, the first 30 hours of its life. Basically, what that network does is specifies precisely the nature of the blue and the red territory here. The skeletal for red, and the endoderm for blue. And that network predicts virtually every feature of the behavior of that, those developmental processes, even to the point, very recently he's gone back 50 years in the literature and explained a whole series of early sea urchin development that couldn't be explained before by this network. And of course, what that means, is we, for the first time-- Let me say two things about this network. 

One, it is enormously dynamic in what you see here is the composite network. It changes at every phase of that developmental process. And how you capture the changes is one of the grand challenges of systems biology, dealing with the dynamics of networks. Number two, we understand in such exquisite detail, the hard wiring of the networks, that we can predictably re-engineer the network to create predictable phenotypes. Eric has re-wired this network to create a sea urchin with two stomachs, or a sea urchin in which pigment cells are converted into skeletal cells. And what's interesting about that is, in the future we're going to deal with disease perturbed networks by designing drugs that will make networks behave in a more normal manner, at least abrogate their more deleterious functions. The final idea is, of course, the biological information has many, many different hierarchical levels. It's multi-scaler. It is very important to capture information at all of the levels that you have here between the phenotype that you want to describe, say the cell cycle for a single cell, all the way back to the digital information in the genome. Because we know that at each of those levels, including DNA, the environment impinges upon and alters the basic digital information. 

Hence, we have to be able to integrate these different types of information, where what we mean by integrate is capture the environmental modifications of that information in the context of how they modify biological functions. So again, one of the grand challenges of systems biology is not only the capturing of data at these different levels, but it's the integration of data at these different levels, and the creation of predictive models that explain biology or that explain disease. So, as you heard, the institute was born in 2000. We have about 2200 staff, 13 faculty. We're interested in the systems approach of biology and disease. We're interested in using those biological and medical problems to drive the development of series of measurement and visualization technologies, and computational tools that let us handle that type of information. And finally, the institute really is interested in changing the sociology of science, in creating strategic partnerships, and I'll describe some of these, and figuring out really interesting new ways to transfer knowledge to society. I won't have any time to talk about that at all. I would say systems biology, the essence of it, is encapsulated in this slide. Systems biology is no different than classic hypothesis-driven biology, except in the dimensionality of data it manages and handles. 

So, you take a system like the cell cycle, you take the data and the literature, you create a model, you create hypotheses from that model, and perturbations to test them. You gather, hopefully, global data sets and analyze that information, and you see how the juxtaposition of that information lies up against the original model. You modify it accordingly. You do this in an interpretive kind of fashion. Let me tell you that data space is infinite. That doing the systems perturbations that are relevant to your system is a non-trivial assignment in this endeavor. And there are interesting computational methods that we can begin to develop to deal with this kind of complexity. Measurement should be global. Everything should be looked at, because we don't understand biology at any level in very great depth. The need to integrate these multi-stage hierarchical levels of information, I've discussed in the ability to assess dynamical changes. 

Those are all quite critical. And the more we can make the measurements quantitative, the closer we are to being able to move, either from descriptive or graphical models, to detailed mathematical models. And let me tell you, descriptive or graphical models can be incredibly powerful, depending on the granularity of resolution you need in understanding the system. For medicine, you need much less than you do for biology. As I said earlier, biology drives technology and technology in turn drives the computational tools. We've created the cross disciplinary culture at ISB that has all these listed types of scientists. And the key things about the cross disciplinary culture is one, every scientist learns the other scientist's languages to the level of being able to communicate effectively, at least. Number two, non-biologists have to learn biology they are working at in a very, very deep way. And three, you have to learn to work effectively as teams. We've taken eight years to do this, and we're still just learning. 

But it is a very, very powerful approach to looking at biology. We've created large facilities that can feed the information into computational mathematical analytic tools. They, in turn, can be pointed at simple and complex model systems ultimately at human health. And setting up and establishing the facilities so that they are accessible to every single faculty member has been a critical part of what we have done at the institute. Let me just take a moment and talk about systems medicine. As I said earlier, it arises from a really simple hypothesis. Namely, disease arises in the affected organ as a consequence of the genetic and/or environmental perturbation of one or more networks. What happens in these networks, then, is the envelope of information they express is changed, and is changed in a dynamical manner that changes during the progression of the disease. It's that changed dynamical envelope of information, that basic pathophysiology of the disease. But as well, it gives us completely new approaches to diagnostics, therapy and prevention. 

I only have time to talk about the first, diagnosis. So let me give you a simple view of the system we understood, and have studied in most detail. The systems approach to disease. This is prion disease in mice. Prion is a protein molecule that converts from its normal form, on your left, to the disease form, on your right. This disease or infectious form with the altered 3-dimensional structure has two properties. One, it is catalytic in its ability to convert normal prions to the disease form. That's what makes the disease auto catalytic within the animal. Number two, in most cases, those infectious prions are utterly resistant to any proteases, so if they're taken up in nerve cells, they are probably the beginning of what leads to destruction of the nerve cells in the pathophysiology of disease. So what we decided to do was study five different embryoid strains of mice, and two transgenic strains, and one knockout strain to look at essentially ten time points across the duration of disease induction, which ranged from 60 days to 350 days. 

We looked at the transciptome of the whole brain. We interrogated these slides, looking at essentially all of the mouse genes. We tallied the relevant change in genes. And among the eight strains, there were roughly 7,500 of the mouse genes that changed. And of course, the signal to noise in these large high throughput data sets is enormous. One way you can deal with it, a minor way you can deal with it, are statistics and mathematics, and those kind of tools. The real way you have to deal with it is biology. And the reason we did all these strains is we could use clever biology to get rid of a lot of noise. For example, if we took just the five major inbred strains, and said, of the 7,500 genes, how many changed in the five inbred strands. It went from 7,500 down to about 900 or so. 

And if we applied a series of other biological filters, we could find that in fact there were probably a core of fundamental differentially express genes, roughly 320, 330, something like that. So what we did then was to map onto a series of networks that captured the described histopathology of the disease, including microglial and astrocyte activation. And the degeneration, presynaptic and postsynaptic of nerve cells. And finally nerve cell death, and prion replication and accumulation. We mapped those 324 genes onto provisional networks we had from the literature and regenerated by experimental data. And let me show you what that looks like. On the left-hand side, you've got the time of analysis. This is ten weeks out of a mouse that lives about 23 weeks. There are no clinical signs at ten weeks after infection. On the right-hand side, you see staining for the infectious prion particle. 

And you don't see very much at ten weeks. The yellow indicates the diseased. The control animals have the same transcript at that particular site Red indicates an elevation of diseased over normal. And Green, just the inverse. The lines around the subsets in the network are subnetworks that explain specific aspects of the pathophysiology, the disease, just beautifully. So if we go from ten weeks to 14 weeks, you can see more transcripts are turned on and/or are turned down in fewer cases. There's a little more infectious prion. There are no clinical signs, 16 weeks, no clinical signs nor infectious prion. More changes in the networks, and so forth. And a week before the animals are to die, they have full born clinical signs, and full born staining in the brain and so forth, and a change in the histopathology. 

So what we can say is that if we look at the nature of the network changes in each of the six networks that map to those six pathophysiologic features, they can explain virtually all of the known aspects of the disease in the right temporal context. But what was really interesting is, one of the questions is, how do we know if we made the assignments with clever biology to the right cell types, and so we used the Allen Brain Institute in situ hybridization analyses. They looked at roughly 20,000 mouse genes and assigned them to particular cell types. We picked 128 genes, and we were right in every case. So biology is very powerful in making these assignments. But even more interesting, only roughly a third or so of the genes encoded the known histo-pathophysiologic pathways, and two-thirds of these differentially expressed genes accounted for phenomena that were not associated previous to this time with the disease. And yet, in almost all cases, we can see how they map very nicely into the disease. And the only point I would make here that's really key is this is why global analyses are important. No matter how much you think you know about a process, you only know a fraction of its reality. And if you do global studies, you can really see everything. 

What about diagnosis, how can we take a systems view of disease and get new diagnostic approaches? If you look at the three panels at two, 12, and 20 weeks, you can see we can see changes in the transcripts of six or eight weeks before you see any clinical signs whatsoever. The really interesting question is could those transcripts that have been elevated, be expressed as proteins that secreted in the blood, and could we see the elevations in the blood. And the answer to that turns out to be yes, you can do beautiful early diagnostics. We have a lot of data for that, and I'm not going to show it to you. But rather, I'm going to raise a more general question about blood protiomics and protein diagnostics. That's the question of if we had been spending a couple of billion dollars on biomarkers for three years now, why is it we have so few biomarkers that work? And I think the answer to that is really crystal clear. If we look at 20 women, if we look at the bloods from 20 women that have ovarian cancer, and compare them with 20 normal women, we can use classic protiomic techniques and find an whole series of proteins that differentiate the two classes beautifully. But if you take those markers that differentiate them and you look at them in the context of ten other diseases, they behave in utterly unpredictable ways. 

The reason for that is because virtually all those markers are synthesized in multiple organs, and they're subjected to different environmental stimuli. And if something changes, you never know where the change comes from. So the answer to that is to identify organ specific blood markers. And we have essentially done that for all of the major organ systems in humans and mice using analyses of 60 organs in each case. And then analyzing each organ against all the other organs to look for unique or relatively unique blood markers. And the power of this vision is it makes the blood a window for health and disease. And let me be really explicit about that. Blood is the organ that bathes all other organs. All other organs secrete proteins into the blood, and it's easily accessible for diagnosis. The idea would be if we have 50 major organ systems, each would secrete multiple organ-specific proteins. 

And they constitute a molecular fingerprint. And the ratio of those proteins expressed would reflect the ratio of the network activity in the organ. The idea is if the organ becomes disease perturbed, some of those proteins would alter their levels of expression, and so be reflected in the fingerprint. So the fingerprints, then, could give us ratios of expression levels that correlate with normal and disease. And if disease, which disease it might be. Cancer, fibrosis, whatever. The idea is that diagnostics is multi-parameter, and the fingerprint is an analytic, not for a particular disease but all diseases. That's the power of it, to be able to do it we have to be able to-- If we want to do 50 proteins for 50 organs, and the reason we want to do that is with that many proteins, we can begin to develop computational methods for beginning to infer the nature of the disease perturbed networks in the diseased organs. If we want to do 50 times 50 proteins, 2,500 proteins, we can't do it with any techniques we have today. How we are going to do it, we'll talk about in just a moment. 

But let's assume that we can do it. Then what can we do? Number one, we can do disease diagnostics. That has three features. We can do very early diagnostics for cancer. That would be very important in using ordinary approaches for curing. Number two, we can stratify the disease. And number three, we can assess the stage and progression of the disease. I would argue that stratification and progression are dimensions of disease that will play in the future, with regard to therapy. They're going to change, either with stratification, that's clear, or you're going to change with the stage of progression. 

The second thing that we can use is pharmacoprobeomics. The idea these fingerprints will assess the responsive drugs in individuals. So in individual patients, we can titrate dosages. We can look at effective dose responses. We can look at inadvertent toxicity, and so forth. But in clinical trials, we can immediately and early stage, begin to assess, is the drug on target or is it off target? And on and on. So I think this is really going to revolutionize how we do early drug toxicity and efficacious studies, and so forth. Number three, by using the computational methods I talked about, I think from the blood, we can begin to get an assessment of the disease, the nature of the organs that have been diseased, the nature of the networks that have been disease perturbed and relevant organs. And this, of course, is the key to beginning to think about how you can manipulate network behavior with drugs to get early effective responses. 

and so forth. In the future, I think each of us are going to do this twice a year. It's going to be a wellness assessment. The individual is going to be the control against which their change indices will be assessed. We won't have to do cross populational comparisons in the face of enormous genetic polymorphism, and so forth. And finally, I would say it's going to be an incredible assay for studying human biology. We're beginning to set up some studies in aging humans, thinking about these kinds of tools. So, let's talk about emerging technologies that can change our ability to deal with digital information and environmental information, and most important, their integration together. I've listed some of the tools that I think are most important, and I'm going to end up talking about a couple of them. But high throughput DNA sequencing is going to be key. 

Rudy, at the Institute and at the ETH in Switzerland has really developed targeted MRN mass spectrometry to the point it's going to be the ideal tool for the discovery of protein components of these blood fingerprints we've talked about. We'll talk in a moment about nanotechnology and microfluidic approaches to measurement of these same molecular fingerprints. I think one of the seminal transformations in biology is going to come from single cell analyses. I just won't have time to talk about that today. Finally, in vivo and in vitro imaging is obviously going to be critical in medicine. There are eight companies that I know of that are inventing new next generation DNA sequencing. and who's going to be the big winner, I don't know. But I would say that what I find terribly attractive, are those whose strategy is involved single strand DNA sequencing. I say that because the simplicity of preparation and samples. And number two, you have to be able to massively parallel the analytic process. 

We would like to be able to do one or several billion DNA strands simultaneously in order to get whole human genomes done very effectively. These techniques will be here certainly within ten years or so. The other platform that we pushed together with Jim Heath at Cal Tech is developing microfluidic and nanotechnology platforms for this endeavor. I see this is the one slide that's blank. What you should see here on the slide is just the simple statement of, we can use the parallelization of microfluidic and nanotechnology approaches to make 2,500 measurements. And we can do it with regard to diagnosis assessment of progression, etc. The approach that Jim, together with Ryan Bailey, a post-doc we share, developed is called DNA Encoded Antibody Library. It's basically a way of making protein chips. One, you conjugate to a protein capture agent, a single stranded DNA, one 20 mer for each of the different types of protein capture agents. And then number two, the cognate of those DNA strands are spotted on an array. 

Then the antibodies that have been conjugated or poured over the array, and the cognate DNA strands bind together, and particular capture agents or localized to particular spots. And the assays we use for this are really a simple kind of straightforward assay. If you want to make it super sensitive you can put gold tags on the assays. Jim has done that, and actually he's been able to show you can get digital count, you can count, if you want that kind of sensitivity, beautiful, individual protein molecule. That may be important for some really low abundance proteins that we are interested in. What Jim has also done is created a front end separation, microfluidic separation technology for sorting cells from the plasma. He's actually been able to show that we can take the cells and beautifully sort them by creating arrays that have different cell surface markers, capture agents and so forth. So we can do the separation and the analysis of the single cells, as well as what I'm talking about here, the analysis of the plasma. So, you take the plasma, 300 nanoliters, throw it over the protein chip, and you can read out-- We have chips now that have 20 features on it, that is 20 assays on it. The dynamic range is 10 to the 7th to 10 to the 8th. 

That's really important, because you want to be able to see fingerprints for very small organs, like the beta cells in the pancreas, as well as large organs like the liver. The sensitivity is high attomole, low fentomole And there's a five-minute measurement time. There may be the chance in the not too distant future for highly focalized point of care analyses. And the challenges we're facing with this technology are two. One, where we get all the capture agents we're going to need. And I'll guarantee, it isn't going to be antibodies. And number two, how do you make these chips manufacturable on a large scale. We're working in various ways on both of those challenges. But the system's view of disease, the new technologies, the computational tools, I haven't really talked about those, all lead to what we call this thing, P4 medicine. And let just give you an idea where I see it going in roughly ten years. 

I think in ten years, we'll begin to have individual genomes on all of this. And from that, we can begin to compute probablistic future health histories. And of course, that's limited in the context of how influential the environment is on these analyses. Number two, I think we'll be able to assess, realtime, how far we've moved down this supposed trajectory of your future health history, by having a hand-held device that can prick your thumb and take a fraction of a drop of blood, take 2,500 measurements, and send that by a wireless to a server. And have that analyzed and back to you and your physician in an email that says you're fine, do it again in six months, or whatever. Personalized, we all differ by six million bases. We're susceptible to unique combinations of disease, but the tools we just talked about in the predictive part allow us to look at the individuals in really, a very powerful sort of way. And in the future, the essence of personalized medicine, is that each person is going to be the control against which their transition from health to disease will be measured along the lines that we have just discussed. There will be a focus on wellness. Vaccines are really going to be key in the future. 

The Institute is now taking a systems approach to understanding immunity, and how to induce the cellular immune responses that have plagued the billions of dollars, the fruitless efforts for AIDS vaccines, and things like that. Participatory means that if we can educate patients and physicians, we're going to give the patient enormous ability to be involved in making their own decision. These are going to lead to what I call the digitalization of biology and medicine, that is, the ability to analyze the information from a single molecule, from a single cell, or from single individuals at each of these levels. That revolution is going to be, I think, far greater in its societal implications, than the revolution, communication and information technology, and for exactly the same reason. I think there will be a time in the future, and we can argue when that time is, when there will be an enormous break in the ever-escalating cost of healthcare, and they'll be dramatically turned around to the point where in the future, I think we can export P4 medicine to the developing world. And that would be the foundation for the kind of global medicine that the Gates Foundation is actually promoting. The final point I'd make here about P4 medicine is it is going to transform the business plan of every single sector of the healthcare industry, from pharmaceuticals, and biotech, diagnostic companies, IT, healthcare companies, all the way down to care providers, health insurance, medical schools, and the like. And I think what's really interesting here is any time you've got disruptive change, there are enormous opportunities economically and scientifically. And are all companies going to be able to adapt to new strategies? I think in most cases, the answer is going to be no. 

I think there will be the opportunity for really a lot of new companies who know what the future is going to be. And this is particularly interesting in the arena of pharmaceutical companies. And I can tell you, I could talk for 15 or 20 minutes about my experiences with pharmaceutical companies in this regard. But instead, let me make just a few final comments to get on with things. One, we have decided that the challenge of P4 medicine is way too great for any small institution to really take on. So we have focused, over the last four years, on strategic partnerships that are attacking this problem from the level of creating a P4 medical institute that's going to integrate leading edge companies from all of the healthcare disciplines. I can talk about that with anyone that's interested. Number two, we finally found a medical school who's willing to revolutionize its thinking, and practice, and teaching of medicine from the old-fashioned to the more systems approach, and everything. I can talk about that. We are thinking about bringing systems biology P4 medicine to a country in Europe and a country in Asia. 

And in fact next week, we'll probably be signing an agreement with the country in Europe. And it is really an incredible opportunity, because it is going to bring in about $100 million over five years. With that, we are going to do two really transformational projects. One is the genome analysis of normal and disease families, highly selected, we'll start out initially with coding regions, but we'll move to full genome as soon as possible. And in fact, we think we will have five complete genomes by the end of the year in this particular project. But what we are really interested in, again, is this collision between the environmental and the digital information, that manifests itself, of course, in these blood molecular fingerprints. So the second project is to analyze the blood molecular fingerprints and their readouts, and from them, to begin to infer back to network behavior. This is something we have come to call systems genetics. I think it's going to be an enormously powerful analytic tool, far beyond any of the things we have now, because any time in biology, you analyze information in terms of functional modules rather than in terms of bits and pieces, you end up winning big. And I think that's really what's going to happen here. 

Number two, I think our teaching should be radically transformed at every level. I think K-12, we have seven people who work full-time on that. I'm not going to talk about that. I think undergraduate, graduate and even the higher levels, and I think the whole approach is to take this systems view of education. I think the teaching should be conceptual rather than detailed. I think, in biology, I think the systems view lets us look at all the different major fields in biology in a very, very different fascinatingly integrative way. I think it's really critical that undergraduates have good backgrounds in physics and chemistry, and especially mathematics and statistics. I like the idea at the undergraduate level of dual majors, where you have biology and another major. If you learn to think analytically-- and how you do that, I mean, you know, problems and things like that are interesting, but there are new computational tools. I'm really excited about game boxes, and what we can do in terms of not only teaching people how to think analytically, but teaching them how to think out of the box. 

That is important, too. Mini-courses are really great for extending the breadth and giving you, knowing where to go, and so forth. And thinking about how science impacts society is really key. I think that's something that is largely been I think ignored. Oh, this is great New Yorker cartoon! And what it is, is a guy looking down at his cat who is standing right next to its cat box and saying, "How many times have I told you not to think outside the box?" 
(laughter)
 Now, that's exactly what we want our students to do, is to think outside the box. And so the challenge is, how do we get them to think outside the box, and I think that's interesting. I think academics should have four rather than two missions. 

So Merv Goldberger told me back in 1979, the Scholarship in Education, I'd argue transfer of knowledge to society is really key. There are a lot of ways you can do it. I'd argue community leadership is really key, because you can really change a lot of things in your community by that kind of leadership. And we have done that very well with K-12 science education. The final point, this is for students, but it's also for faculty to think about as well-- Oh, no! God! Okay. Anyway, it is the typical career of the scientist is a beautiful bell-shaped curve. You go up to a max, and you kind of fade away, okay? Norton Simon, a great industrialist said there's a way to circumvent this difficulty is as you get near the max, you totally change fields, and then you go through this insecurity and learning process and you go up again. 

But you've got to be willing to do it multiple times. And the really interesting question is, what is the kinetic of when you have to bail and start something new. That's something only you can answer, but I'll guarantee you, if you handle your career, and I think Oliver has handled his career beautifully in that particular regard, you can be productive and useful a lot longer than most scientists are. And you won't be as conservative and a stick in the mud as most scientists are, because you are always thinking about how to change. Anyway, with that, I'll turn it over to Oliver and let him make his comments.