Thank you very much, James. It's just a privilege and an honor to be asked to give a talk like this, and also a daunting task to try to take a guy who's used to presenting data to talk about philosophy of innovation. I've got two screens. I'm going to have to look at this one, I think. I have some disclosures. They're pretty trivial in this context. I have one important disclosure, and that is I have not touched an arthroscope for 30 years, so I am not a competent, nor am I a competitor for any of you. Most of you, I mean all of us in our practices innovate practically on a daily basis, not only in inpatient, but on outpatient settings. Many of us have read a whole variety of books that are available, and they're wonderful that dissect innovation from a perspective of... Could I have the presenters' mode on the slides? Thank you. I'm going to go back one. Many of us have looked at these and have done some study on the science of innovation and looked at innovation from a stochastic process to a philosophical process to a manifestation of inspiration to a structurable, manageable process. I'm going to look at it today from a personal perspective and particularly the stochastic process that is driven by purposeful intent. Not predictable, but certainly facilitatable by conscious intent. One of the first things that I'll point out is that there's a difference between being really good at something and being really innovative at something. Excellence is defined, in my view, as the ability to hit a target that other people just can't hit. They're just not as good as we might be after training and practice and getting to an end result. But innovation is different. Innovation is this process of hitting targets that others just can't see, that aren't evident. The most common manifestation of that is in developing new techniques that might result in new discoveries, a new telescope, a new chemical process, a new drilling technique, or a new concept of the universe. This is also the kind of innovation that results in Nobel Prizes. But that is not the most common type of innovation. The most common type of innovation is what you and I have much more access to ourselves, and that is to take those basic principles of biology and chemistry and physics and math that we can see, that we can feel, that we can touch, and then convert them into something that other people can't see. And to do that and bring something new into the world that solves an engineering problem for a given purpose. There is a lot of jargon and good advice that I've gotten from my grandmother and my father that relate to this, of just personal characteristics of trying to think broadly and be a generalist rather than a specialist all the time, anticipate, seek out the best athletes to collaborate with, focus on effectiveness, anticipate where the puck will be, as Wayne Gretzky suggested, and be able to adapt to the time that you have. You can't always shoot at targets that you think are there because you just don't have the resources at the time. You're too early, you're too late. Avoid the crowd, think differently, not on purpose just because if you're thinking like everybody else, you're not likely to see anything differently than they're seeing. And so most important for me is this quote from Margaret Mead, and that is that never doubt that a small group of thoughtful, committed individuals can change the world, because in fact that's the only thing that ever changes the world, isn't it? And so all innovation ends up having to be personal, but also it's much more likely to happen if it's purposeful at the same time. And so there's a way to think about it, I think, that I didn't invent, that I think was dragged to by my nose by mentors along the way, about how innovation happens and how you can contribute to it. And so I've condensed this into this three-step concept of asking important questions, solving important problems, creating opportunity for not just ourselves, but for our patients, for our colleagues, for our students, for our fellows, and for society in general. And my first exposure, this was kind of my world view even as a young person, but my first exposure to being dragged into a world view that helped innovation in my life was a conversation I had with my chief as a third-year resident. So I don't know if many of you know or remember Vert Mooney, but Vert was an extraordinarily innovative guy and a strategic thinker, and I decided as a third-year resident to have a father-son talk with Vert and ask him what should I do with the rest of my life. And Vert was a spine surgeon, and so I was really surprised when the first thing that came out of Vert's mouth was, well, not spine. And he went on to say that, so George, you see, innovation happens in waves. And spine at that time had just gone through this wave of couture du brisee fixation and pedicle screws and intraspinal monitoring and CTs and MRIs, and spinal anesthetics and 360 procedures, wedges, graphs. BMP was not quite there but soon to be introduced. And he looked at me and says, you see, this has all just happened. By the time you're mid-career, it's going to be all over. We're going to spend the next 20 years of our lives arguing about what not to use all this fancy shit for, and so you'll just be frustrated. So it's not what I would recommend for you. So I was very shrewd in retrospect. I think I still would have been a good spine surgeon, but he went on then, and so I really loved peds. And then he said, well, not peds, because even though the kids are great, it's not very scientific. Kids vary too much from one to another. The cohorts are really small. Genetics has not caught up with this, and until genetics catches up with the cause for all these deformities, then it's not going to be very scientific. And in his words exactly, he says, pediatrics is going to be ruled for the next 20 years by charming men in bow ties with no data, and they're just going to frustrate you. And it's not entirely fair, but it was telling. And so the next step was, well, but tumors are interesting, because look at tumors. Because now we've got this world where MRI and CT and PET scanning have given a new world of illumination to tumors. There's custom endoprostheses that at that time could be prepared in six weeks. Now we can pull them off the shelves, but at the time it wasn't easy. Chemotherapy had just been invented, so suddenly people went from 20% survival rates for osteosarcoma to 70% survival rates. Cell biology was creeping into this. Pathology was expanding. Databases were being generated. And so to him, this seemed like a really fertile ground where there was really no end. And so I took his advice. He did want me back at UT Southwestern, it turned out, as a tumor surgeon. But he told me to go to New York and learn how the game was played. And so my fellowship ended up being a two-year fellowship at Sloan Kettering and at the Hospital for Special Surgery. And it was very good. But that experience with VRT was that first touch of, well, innovation, if you want to fly close to the flame, has got to be a purposeful process. Or you're going to be much more likely to get there if you make it strategic. So I'm going to double back for a moment on this and talk just for a second about asking important questions. So there are a lot of important questions. How are you? How can I help? What am I missing? How could I have done that better? My favorite innovation question is this. And one of my heroes is Herbie Fleisch. And I don't know if you all know Herbie, but we lost him about four years ago. But he asked this question when he was a surgery resident at Rochester in New York and then at Barron, Switzerland. And he said, why don't we turn to stone? Because he had made this observation that the calcium and phosphate product in serum and in extracellular matrix and in urine was precariously close to the precipitation products for calcium and phosphate. So it would be only logical to think that you would just continue to make mineral. And the physical chemistry can't be wrong, right? So he hypothesized that there was an inhibitor to this process. And it's interesting. He's the first person that systematically went after this as a surgery resident. And he hypothesized that there is an inhibitor that presents the accumulation of mineral on a mineralization front. He talked about poisoning the mineralization front. Oops. And I have one slide that's not dropping. But anyway, what he proved was that it was two balls, two pyrophosphate molecules, two phosphates linked together that would drop into this place and prevent a place for the next calcium to land. And he was ridiculed for it because they talked about Harvey's balls. And he had this diagram of two balls dropping down on a surface and protecting it. But what we got out of Harvey's question was technetium pyrophosphate bone scans, all of the bisphosphonates that we use for treating osteoporosis, for limiting the risk of metastases, for drug targeting to bone. So it was quite a find with a really interesting question. There's a lot of stories to tell about Harvey. So the world of innovation, though, changes, of course, throughout life. As a young investigator, the questions and the problems and the opportunities that you have are different. There's a long and onerous checklist for new investigators. And I don't know how many people in the audience are in their first six or eight years of practice. A few. I'm not seeing that many hands. But you know these guys. And so this list of asking important questions, figuring out what you're going to study, figuring out how to assemble the resources and the people and the funding and the track record and the time to study these things, and then how to take advantage of whatever resources you have through leadership skills and mentoring skills. That's the ticket, the entry ticket to an independent life as an investigator. And so this is a combination of things that you don't do by yourself. But there are mentors involved in many of these early steps. There's external sources of funding from institutions and resources institutions can provide. There's funding that organizations like the ORF can do, and it's very important in orthopedics. And then also mentoring that program officers at NIH do to help young investigators tick off all these things and get into a stage where they can be dangerous, essentially. But there's this big chasm of death in this range between getting a lab, getting started, hiring somebody, and then proving that you can do something with money and getting more money. And so that chasm of death for me was about an eight-year period from 1988 to 1996. And between the time I started as a new staff person at the Cleveland Clinic and the time I got my first NIH grant, which was a long, long time, that almost killed me and had me questioning whether or not I had made the right decision. And what this looked like, two ORF grants were critical to that, funding from the Cleveland Clinic contributed some. Actually, the lion's share of what filled that gap while I wrote two unsuccessful, it was black blocks or two unsuccessful NIH grants, was funding from industry. And in collaboration with industry around my area of interest of bone repair and bone remodeling and bone grafting materials and animal models for bone grafting materials. And so that enabled this process. And what it did is partly prove that I could survive this process, but more importantly for me, it built this team of people that had the skills and the ideas and the model systems and the equipment and a culture and some discipline and some track record and, fortunately, time to take a next step and to act on the opportunity that we had created. That's a real task and it's a place where all of us can think about where we can be the best mentors. And it's not just about money, of course. It's about people, and I'll kind of walk you through a few of those people. And many of you, as I name these people, can probably see faces in your own lives where these kind of individuals have touched you in some way and guided your progress. The first is Bob Buhols for me. Bob was a staff member and then later chair at UT Southwestern where I did my residency. was remarkable in many ways, but reinforced this idea that beyond all the people you touch with your hands and all of the patients that you have, the biggest impact and opportunity that you have in creating a legacy is in what you write, what you teach, who you teach, and then the opportunity that you create for other people. And so that had a profound effect on me. Mary Beth Ozaki, who as many of you know, his wife, is Bob's spouse, also ended up as an ABOS president, just emulated this concept that you could be an academician and extraordinarily compassionate and close to patients and extraordinarily technically accomplished. And so it really reinforced the idea, and even in this macho culture of Dallas that I was in, that the quietest voice in the room could often be just by far the most powerful. Pete Carter is a wonderful hand surgeon involved in the compression screw for scaphoid fracture development. Had a wonderful idea about research. Everybody should be involved in research. It didn't matter. You either were supportive, meaning you encouraged, gave money, shared ideas. You were involved, meaning you showed up, or you were committed. And he looked at me over his glasses at the operating table one day and he said, I can't do his Texas access very well, but you do know, George, the difference between being involved and being committed. I said, no, no, Dr. Carter. Well, it's like the difference between ham and eggs. You see, the chicken was involved. The pig was committed. And it's really, I mean, it's hard to say that that's, there's, anyway, so here we are in a fellowship. So this was two years that I spent at Sloan Kettering in hospital for special surgery where my chief was Joe Lane, who many of you may know, an ORS president. And just a remarkable person, a consummate physician, a scientist, just a brainstorming genius, just a tornado of ideas and energy and goodwill and just was wonderful at creating opportunity and bringing teams together. And then his counterbalance is Adele Bosky, who is the director of research at hospital for special surgery. And her superpower was to hear you say something stupid. And we refer to this as a samurai method of criticism. She would just cut your head right off. You wouldn't even know until you heard it hit the floor. But then she was patient enough to put it back on. And while she was sewing you back together, explain all the mistakes that you had made, all the ways that you could do better. And so she reinforced this idea that if you are going to make some really stupid idea or spend too much time doing something or completely misinterpret your data, it's better to hear it from your friends. And so that has stuck with me for a long time. Murray Brennan, a remarkable surgeon, intimidating man, but I really learned a lot from, was the chief of surgery at Sloan Kettering. And his idea was, hey, ideas are cheap. If you want to do anything with an idea, you need data. Don't even come to me with an idea until you have a plan of how you can prove it. And if you really want to have an effect as a surgeon, make your practice into a laboratory. That's where you can leverage your opportunity. And then finally in my fellowship, Hugo Castor Malaspina was one of these incidents in life where I'm listening to a lecture that was required on aplastic anemia. And I'm an orthopedic surgeon. Aplastic anemia is important, but it's not going to be a big part of my life. And I'm about ready to fall asleep, and he's telling me all about transplanting stromal cells into the backs of nude mice. And about five minutes to the end of the lecture, he makes this observation that he's just realized that one out of the ten clones that he's transplanting into the backs of these mice is making bone. And the bone is human bone. And I wake up and say, I want to make bone. And so the next three weeks, he was gracious enough to have me come into his lab, learn how to culture cells, learn how to do these stromal isolates, understand a little bit about stromal biology. And then I took that, and that has become the core resource of what we ended up using in a lot of the work that we subsequently went. So New York, in many, many ways, was my movable feast for you Ernest Hemingway fans. So then you start practice. I'm back into this. That's the beginning of the chasm. So you're supported up until the time you're a fellow. And so now we've already talked about the money part of that chasm. But then there's the people part, which is extraordinarily important. And so one of the first people that I encountered, even before I was hired at the clinic, was Bernadine Healy, one of the most impressive women I've ever met in my life. She ended up as NIH director and the director of the Red Cross and sadly lost her to glioblastoma too young. But she made the observation and said, listen, if you can make your lab into a national resource, which for her was two or three NIH grants running in combination, you can make not only more money but more prestige, more impact, more recruiting opportunity, more research opportunity available for our institution and for the rest of the world than any surgeon can do with their two hands. So if you're in, if you're committed, in Pete Carter's definition, I'm here to support you. So that was extremely pivotal and part of the reason why I chose to go to the Cleveland Clinic. And then my department chairman, Fred Cornhill, at Biomedical Engineering, was also a remarkable person. I could tell you a lot about him, but he was particularly artful in identifying opportunities where groups of people could do a lot better work when they worked together than separately and built these collaborative networks. He was mostly a data scientist, but he illustrated this point, taught this point, mentored this point, and so was extraordinarily instrumental in helping me envision how that might be done in the rest of our world. And then finally, Joe Hahn, who was our chief of staff, came to me about five or six years into my time at Cleveland Clinic where I'm building a tumor practice and trying to run a laboratory and trying to have toddler children, and be a good father, and stay married, and all of those other important things. And he came to me with a proposition. He said, hey, listen, we need a musculoskeletal biology section. And we don't have anybody better than you to run it. And if you run it, there's only one catch. I can't afford to have you spend 100% of your time in the operating room, and then pretend to leave this important effort for us. So here's the deal. You're going to have 50% of your time in biomedical engineering, 50% of your time in orthopedics. I'm actually giving you a raise to do this if you'll commit to do it. And so again, that doesn't happen very often. But I owe Joe a tremendous amount for having that kind of vision and willingness to invest. And then finally, in my early life as now a section head in biomedical engineering, my first and most potent act was to give up my title so I could recruit a renowned scientist from the NIH to join our team, Vince Haskell. So he took my role as the section head for musculoskeletal biology, and then became one of my most important mentors in just the art and the science of how to think about data and science, and how to love the process. So he's my Yoda in science. And we all need one or more of them. So the next 12 years, it was a blur. Still is a blur to me, honestly, because there was an awful lot happening. But the next 12 years, it was a combination of not only finding money to support our lab, but building networks that Fred helped inspire me to do, and the Cleveland Clinic helped with, that really brought about $100 million of resources in, not all to the Cleveland Clinic, but if you add up Cleveland Clinic, and Ohio, and then collaborators that were part of these networks, it was a lot of opportunity that we created by just thinking a little bit more broadly. And I'll tell you a little bit about how we did that. So doubling back on this, and returning to the theme of, now if I'm, this is my lab in 2008. I have a whole different set. Now I'm an established investigator, a whole different set of questions and problems. This focus of ours was primarily on finding the cells that were most important in our wounds, and that expands into a whole other range of questions that you can ask about what cells you want, and how can you assay them, and where are they, and how could you process them, and what concentration would you need, and how would you transplant them, and all of these things. And I can't, and I won't pretend to walk you through all of those things, but I'll try to just spend a little time just dancing across the surface of some of this, and how the, particularly how the collaborative networks and the tools played in. So one of the first challenges I had was in nomenclature. So people would have this, this is what I learned from Hugo Malaspina, to do a colony assay, throw cells out in a dish, find out how many colonies grow. Each one of these colonies came from a single founding cell. But now what do you call these? He called them stromal cells because they supported hematopoiesis. That was what he was studying. Other people called these CFUS, Colony Forming Unit Fibroblasts, because they all looked fibroblastic, but they weren't all destined to be fibroblasts. Other people would call these mesenchymal stem cells. So Arnie Kaplan and that team would take this dish and allow it to culture expand. I'll tell more about that later. And then the cells looked homogeneous. They looked purified. It looks like they could do multiple things. And so he called them stem cells. But in fact, at this stage, I don't know what these cells can become. And so because all these terminologies were out there, and we wanted to study this question about, well, how many, there's a diversity of cells there. If you look at those colonies, you can tell that the cell that gave rise to the little one is different than the cell that gave rise to the big one or the dark red one. There's a lot of heterogeneity here. You can't call them all the same thing. And so having a tool, just a nomenclature that allowed us to think a little bit out of the box about where other people were defining these cells gave us the privilege suddenly to measure them and count them and establish heterogeneity and do things that other people just were not caring about. So we looked at lots of things. I'm just going to run past these things about where to find them, not just bone marrow, but really any tissue, brain, lung, heart, liver. You can find connective tissue progenitors that will make one or more conductive tissue and make colonies. If you're aspirating, small volume aspirates are the best way to maintain your yield. Otherwise, it gets diluted with peripheral blood, but patients differ vastly from one another. So that opened up the next question of, well, what about interoperative processing? If I just use marrow as it comes, I might have on the order of about 10,000 cells per cc or 10,000 to 20,000 progenitors per cc. They come outnumbered 20,000 to one. But is that the right number? Because if I think about the way cells survive, they live off of oxygen. Oxygen diffuses slowly. If I put cells in a big space in large numbers with no blood supply, if they're a long way from a capillary, most of them are going to die, which is what happens to most of our autographs. And so the question was, well, how could we prevent this problem and keep cells either close to a blood vessel or transplant them in small enough numbers so that they're likely to survive? And so it also taught us that mouse models and rat models were way too small to study this, because the cells were close enough to survive in those models. It needed a bigger model that was more like human size in order to study the survivability of cells after transplantation. So that led us to developing three separate new models of increasing size. So we can look at spinal fusion, the regrowth of cells into a defect where we could even measure oxygen tension. That little dip curve that you see there is an oxygen tension curve over 18 days. And then even getting up in this goat model into a big enough defect where this has now become relevant to our blast injuries and road traffic accidents, where there's muscle loss as well as periosteal loss. So we looked at a number of different options. The first was centrifuge. It's been around for a while and still is. You can get a four, maybe six-fold concentration of cells out of a centrifuge. We showed that the progenitor cells we were looking for would preferentially attach to the surface of a demineralized bone fiber. And so this was a way in which we could separate cells that were progenitors from non-progenitors by a preferential attachment. And so we designed this affinity column method, essentially, to concentrate cells. Now we could get two to 20-fold concentration. It was dependent on how many cells we use, what kind of matrix, what kind of surface area, what kind of flow rate. And we worked through a number of those things. But even with this, the benefit of the preclinical data incorporated this into my practice. And even DePue marketed a device that helped people do this. And I, in my own practice, had 74 non-unions that we've written up. And with 94% success, seven I had to regraft, but none that ultimately failed, just grafting with bone marrow concentrate with allograft. We looked at hyaluronic acid. We made the observation that hyaluronan, which is not uniformly distributed throughout the marrow cavity, but is very preferentially patched around in blood vessels in the marrow cavity, could be preserved on cells at the time of harvest if we did it right. We could tag cells that had hyaluronan on their surface. And there are a lot of reasons why hyaluronan was interesting. The oocyte is surrounded by hyaluronan. So it's a stem cell niche in many parts of biology. And it turned out that if we isolated cells that had hyaluronan on their surface, that we could concentrate cells, have higher prevalence of progenitors, more bone-forming cells. And when we transplanted these into animals, that it improved bone healing, and particularly the rate of bone remodeling. So there were these options. The interesting thing was we got to a point where we were interested in going farther. But then we ran out of money to go farther because NIH wasn't interested and companies weren't interested because there was a regulatory barrier. The minimal manipulation of cells that is required for a 361 exemption kicks in. And so both selective retention, they decided, even if it's patients' own cells and existing allograft, a device that does selective retention is a class 3 device. And no company felt that it was worth their time and energy of going through the PMA process with clinical trials to do that. So I could teach people how to do it. I've taught a lot of people how to do it. I still do it in my own practice when I need it. But it's kind of off the rails as far as active research development. And the same thing is true with magnetic separation. So we are currently left with centrifuges, but I don't want you to forget about these other opportunities for the future. So I'm going to try to go faster because I'm going to be over time here. On the front of collaborative networks, our first collaborative network was just within the clinic and we focused on teams, culture, infrastructure, strategic opportunities, investigator support, and partnerships. That led very quickly into an opportunity within the state of Ohio to take two grants that totaled up $9 million overall to support work in five different institutions, 35 investigators, in this kind of fairly simple structure. And that brought about a return of about $39 million into the state of Ohio, just this one effort. And two new companies and a variety of new patents. And so it was quite a success. But that also prepared us for a next step, which happened only two years later, which was at the time of the major injuries that were happening in Iraq and Afghanistan from IEDs, that the military recognized that there were opportunities in tissue engineering that might be applied to the treatment of these serious injuries. And so the Bush administration initially set aside $42.5 million to do this. They got two proposals to accelerate these regenerative solutions, both from us, the Rutgers Cleveland Clinic Consortium, and Wake Forest Pitt. So they ended up funding both. It was an $85 million process to put people into a collaborative network with a much more complicated, if you're in the military, hierarchical structure of reporting to address many of these things. And I'll just touch on just one of those outcomes, which was a great network we put together for bone repair. And I'll single out particularly work that we did with Mike Yazemsky at the Mayo Clinic, Linda Griffith at MIT, and her fellow at the time, Lou Alvarez. So we were able to develop this caprine, this GOAT model, to look a little bit more deeply into severe injuries. So this is a 9-centimeter segmental periosteal defect, 5-centimeter bone defect, 10 grams of muscle removed, intramedullary rod fixation after reaming. So a paucity of cells. And it gave us the opportunity to look at a variety of different graft materials and new biomaterials. But ultimately, what we showed was that the best available material was not autograft, not other biomaterials, but allograft, with either the addition of bone marrow aspirate. But it was additive to add bone marrow aspirate to BMP. And so our biggest bang for the buck was a combination of BMP with bone marrow aspirate, even in these large defects. And so this was just a stake in the ground for a next step, which was a much earlier time point in the project, which was work from Linda and Lou's hands. First, trying to link small molecules, signaling molecules to the surface of biomaterials. So the idea here is if you put in BMP and close the wound, the BMP very quickly dissolves and floats away from that site. It's a soluble factor. And so this is the result that gets diluted very quickly. It doesn't stay that long. And it also creates an inflammatory response because of its secondary action. But if you tether something to a surface and retain it there, it doesn't float away. So you control its concentration, control its localization much more closely. So we initially tried to do this with EGF. They've gone on now from the time we spent in a firm in 2013 to subsequent work to change to a variant of BMP2, which just in the last two years received a breakthrough status from the FDA and is now on its way to clinical trials. So some of you might, if you're interested in bone repair, might see Lou's company, which is Theradaptic, and a clinical trial that they have of this material, which is a direct outcome of the firm project. As I said, I'm going to try to go faster. I'm not going to spend much time on setting up quantitative methods for measuring those cells because the ASTM accepted methods we have. Some of you who are interested in MSCs will be interested in the fact that the way we make MSCs right now, mesenchymal stromal cell populations, is to put cells into culture, culture expand them, let them grow over each other, and then they compete with each other. And some win, some lose. But the end result, you can kind of influence with some combination of weed killer and fertilizer along the way. But the outcome is stochastic because you haven't picked the winner. You just get whatever gladiator comes out of the arena. And this has been demonstrated very clearly in a series of papers by this guy, Selleck. And so this is a barcoding method for labeling individual cells when they first hit the dish. And you see their progeny rise and fall over the course of time. This is umbilical cord blood. But this is the same process with MSC fabrication, where you can start with 50 colonies. And then over time, you lose some, you gain some. You end up with the biggest brutes in the forest. But if you wanted that red colony, if that was the one that would make cartilage for you, or if that was the one that would make bone for you, then you lost your opportunity. And the only way to get the opportunity to do that is to know something about that colony when it's young, way early, like you see on the bottom here. And then have the opportunity to reach into that dish at a time when it's still separate, and either biopsy it to prove that it's what it is, to pull it out and culture it differently, or to weed out everything else, and then culture expand from there so that you don't eliminate that competition. And so a lot of the work that we've done most recently has been around enabling that strategy, which you can't do very well by hand. So now we needed a robot to do that. And so we built this robot. Parker Hannafin is a company with World Headquarters in Cleveland that allows us to capture a large field of view images rapidly in a sterile environment, pick sterile tips up, characterize exactly where those tips are in three-dimensional space, and then use those tips to go and pick up and move things that we see in that image. So we've been using this to accomplish that work of separating those individual clones of MSCs, building banks that we can study and understand the relationship between colony morphology and secretome and other factors and how to predict cartilage or bone formation. This is what our lab looks like now, a long way from the original work that we did with Hugo Castromalespina. And this is where we're headed, but we're headed there because of a call we got about six years ago from a guy named Bud Tucker at the University of Iowa. It's just a serendipitous call that said, hey, I heard you're picking cells out of a dish, separating clones, and I need to do that. Would you make a device for me? And his need was to take cells from children who had photoreceptor deficiencies from rhodopsin mutations and make induced pluripotent cells from them, correct the mutation, and then treat their blindness by reimplanting new cells that had a corrected mutation. A long way from orthopedics, but we were able to, we actually had to make a company to do this because the Cleveland Clinic doesn't make devices, so they had to make a company in order to make one device to give to Bud Tucker. But then we've gone on now to show that this method can be used to monitor the formation of these clones, to make value judgments about the clones, to separate fibroblasts from non-fibroblasts, to identify areas of spontaneous differentiation, to identify mutations while they're still very small populations in this group. And then we've essentially taken his whole process, starting from the left on the top, going to the far right, of making iPS cells, and then going on and making photoreceptor cells that are implantable and that would detect light, and use the robotics along the way, and even build in informatics into the idea of taking what choices he makes in green about what cells he wants, and then putting that into what's called a CNN, a computational neural network, and predicting where he should make those same decisions if he wants to repeat them in the future, and then also applying some of these measurement strategies from radiomics about how to choose cells to act on either to weed or to pick in these things. So for those of you who think I've abandoned my roots, I haven't. There's actually some method in the madness, and that is that even though right now iPS cells are focused on making neurons, islet cells, cardiomyocytes, skin, immunomodulatory cells, the next steps, of course, will be to be able to make other things. So liver, lung, gut, but also chondrocytes, and Farsch-Gelak, who many of you know, is involved in that process already of making chondrocytes out of induced pluripotent cells. So having a automated method that makes the process of getting to a starting point efficient will certainly facilitate that next step. So again, as soon as these things get above the line of sight then suddenly they can be connected. I'm gonna close with a few last thoughts. Questions are important. Remember Harvey Fleisch. Do whatever you can in terms of solving problems to put yourself and others in an environment where innovation can occur. And I refer to this as flying close to the flame. And so these environments are important, and particularly if you're in a position of leadership in your institution, nobody has better opportunity than you do to try to make that happen for people. Build and join and cherish those collaborative networks because there's nothing that makes you feel more loved and productive than those networks. Don't forget untapped opportunities, even if they've been temporarily delayed by regulatory or financial problems, they're still fundamentally scientifically sound and they will come back. Keep peripheral vision. Sometimes the best things that can happen to you can happen by accident, and so be open to them. And then finally, and perhaps most importantly, is recognize that each one of us, and I know most of you realize this, but whether you realize it in your gut or just intellectually, I don't know. But the opportunity we have right now to engage in these collaborative networks in the form of registries and clinical trial networks is truly extraordinary. These are like the web telescope of our lives right now and will truly inform us about ourselves and our position in the universe and the position of our patients in a way that we just can't see for ourselves just yet. And so I encourage you to get involved, take advantage of that, recognize how important that is, and support that process. So thank you very much, I really appreciate the opportunity. Thank you.

innovation

excellence

personal

collaboration

adaptability

mentors

research

regenerative medicine