 Hey everyone and welcome to today's Protocol Labs research seminar. Today we are joined by Dr. Jeff Sau who is a senior scientist at Sandia National Laboratories. His career spans research in a number of different areas including laser microchemistry, semiconductor epitaxy, solar state lighting and most recently meta research. Jeff has been associated with some major institutions which include Stanford University, Harvard University, MIT Lincoln Laboratory, the Institution of Materials Research and Engineering in Singapore, E2O Communications and of course most recently the Sandia National Laboratories. He is also most recently a co-author with Venkatesh Narayanamorti. He was also joining us and I hope I got your name right and they both co-authored the new book called The Genesis of Technoscientific Revolutions, The Nature and Nature Research. Today Jeff will be talking to us about that subject of the nature and nature research and modern synthesis. So now I'm just going to hand the floor over to Jeff and let you take it away. Thank you Liam and good afternoon or good morning everybody depending on what time zone you're in I guess and thank you all for the invitation to give this talk I'm pretty excited about it. This talk will be mostly an overview of the book that came out about half a year ago co-authored as Liam said with Venkatesh Narayanamorti, Genesis of Technoscientific Revolutions rethinking the nature and nurture of research. The overarching theme of the book is that research is fragile and must be nurtured for it to achieve its full potential but that effective nurturing of research requires that the nurturing be aligned with hence requires an understanding of the nature of research. So the first three chapters of the book are on the nature of research each chapter correcting a belief about the nature of research that is widespread but mistaken hence that leads in many situations to a miss nurturing rather than a nurturing of research. Then the fourth chapter is on how to nurture research in such a way as to be aligned with the corrections to those mistaken beliefs about the nature of research. So I'll run through in this talk each of these chapters one slide each I tend to talk a lot about on each slide so you know I'm going to fill up the slide for sure followed by a final slide on a topic five that was not covered in but is a natural follow on to the book. That topic is how to nurture research organizations that in turn are equipped to nurture research so that we might enable Bell Labs 2.0 research labs like the iconic Bell Labs 1.0 but with a modern understanding of how to bring them about. Before I dive in two slides one through five let me give sort of an ultra brief preview starting with three widespread yet mistaken beliefs about the nature of research. The first widespread yet mistaken belief up here number one is that technology is subservient to and follows from science and thus the advance of science is the pace setter of the advance of technology. When one believes this one tends to stovepipe science away from engineering and to think of engineering as without opportunities for research of its own. Instead both engineering and scientific research are important and both feed off of each other in what Venky and I call cycles of invention and discovery and that are equal parts of what we call the technoscientific method. Nurturing research means giving researchers the opportunity to cut across science and engineering allowing them to exercise that piece of the technoscientific method that makes most sense situationally. The second widespread yet mistaken belief is that the goal of research is to answer questions. When one believes this one tends to relegate finding new questions to a hobby activity weekend and evening work done as one writes a proposal for example. Instead question finding is just as important as answer finding and can be just as time consuming. So nurturing research means giving researchers the opportunity to invest the significant effort required to find new questions not just to answer existing questions. The third widespread yet mistaken belief is that outcome of research can be planned and its impact predicted. When one believes this one tends to projectize research not only setting up milestones but using their achievement as a sign of success. Instead research is all about surprise and only afterwards followed by development and a consolidation of that surprise. Nurturing research means encouraging researchers to seek surprise rather than to minimize surprise through projectized milestones. Given our corrected understanding of these three aspects of the nature of research the fourth topic is on the nurturing of research. Research is fragile much more fragile than development. It seeks the surprise and associated uncertainty that most organizations and organizational cultures try to stamp out. So research requires careful and attentive nurturing akin to tending a garden. The fifth topic is the nurturing of research organizations that that can in turn nurture research. For such organizations public private partnerships can be powerful. A public goods mindset supporting surprise and a private goods mindset providing critical knowledge domain inspiration expertise expertise and focus. One last thing before I dive in one might think that there have been so many books and papers written about research all the way from Francis Bacon in the 16th century to Brian Arthur in the 21st century. What new ideas could the two of us Venki and I possibly add? Well surely we do very much stand on the on the shoulders of giants but we are cautiously optimistic that we've added some important new ideas and new language to frame those ideas and especially have created a modern synthesis of both new and old ideas that connects the nature and nurture of research into as much as possible a coherent so let's start with chapter one the technoscientific method. The synthesis of ideas on this slide is quite new. I doubt any of you have ever seen anything like it before but I think you will find it to be reasonable in hindsight maybe almost obvious. We start by positing as many others that there are two repositories of technoscientific knowledge science and technology. The science repository S in blue on the left has two bins both of which will be familiar to you facts and explanations of those facts. The technology repository T in green on the right also has two bins human desired functions and forms that fulfill those functions. These bins for technology are new and probably not familiar to you technology is commonly identified with forms while the functions those forms fulfill are often thought to lie outside of technology. In fact functions and forms are like facts and explanations tightly linked and almost inseparable just like explanations exist to explain facts forms exist to fulfill functions so there is a striking and elegant symmetry between the science and technology repositories of knowledge. Now what about the evolution of those repositories of knowledge that evolution happens via the technoscientific method a new phrase that Venki and I coined to represent the interacting combination of the scientific method which we call s dot and the engineering method which we call t dot s and t with and without dots is a new nomenclature that allows one to distinguish more carefully between the evolution of knowledge and the knowledge itself. Let's start with the scientific method on the left which will likely be familiar to you that method starts with s one dot the finding of facts both new facts that go beyond existing theory as well as new facts intended to test emerging theory this last piece being of course classic hypothesis testing and then with emerging explanations in hand the method proceeds to s two dot the finding of explanations for those facts this is classic theorizing and then with emerging explanations in hand the method proceeds to s three dot the generalizing of those explanations to predict possible new facts triggering a hunt for those new facts coming full circle back to the second half of s one dot that is hypothesis testing let me make a couple of comments on the scientific method first hypothesis testing is important but you see that it is only one sixth of the scientific method and to the extent that scientific research is often funded only if it proposes to test a hypothesis the other five six of the scientific method has great difficulty getting finding funding second the kinds of thinking involved in the various mechanisms of the scientific method can be very different for example generalizing is associated with deductive thinking one starts with an explanation a theory then deduces from that theory new facts that kind of thinking can be highly logical and symbolic explanation finding in contrast is associated with so-called abductive thinking one is basically making intelligent guests this kind of thinking can be highly analogic and intuitive so symbolic and intuitive thinking are both important to the technical scientific method okay let's turn now to the engineering method on the right which will be less familiar to you but is exactly annual as you will see beautifully analogous to the scientific method the method starts with t1 dot the finding of human desired functions practical utility may be behind some of those functions like alexander graham bell's desire to enable people to converse between new york and california but learning may also be behind some of the functions like alexander graham bell's mindset of curiosity about the world perhaps most importantly humans are complex so human desired functions are complex in fact this red dot at the top is meant to emphasize that human desired human human desired function ultimately comes from outside of technoscience it comes from human culture from the values and norms of human culture then with functions and functions in hand the method proceeds to t2 dot it's a finding of forms to fulfill those functions this is what most people associate with the engineering method but of course as you see is only one third of the method this brings us to the third leg t3 dot the co-opting of existing forms to fulfill functions they were not originally intended to fulfill this we call exacting a word borrowed from evolutionary biology in which biological forms like dinosaur feathers for thermal regulation are co-opted for other functions like flight in modern times steve jobs famously co-opted gorilla glass and multi-touch surfaces to create the iphone the reason we coined the technoscientific method as a new phrase is because as all bench researchers know but we've but here we've made more explicit the scientific and engineering methods are not independent of each other science can proceed without engineering and much science does proceed without engineering engineering can proceed without science and much engineering does proceed without science but science advances much faster when it makes use of engineering especially when facts are predicted and found using technology and engineering advances much faster when it makes use event when it makes use, but engineering advances much faster when it makes use of science, especially when forms can be ruled out and ruled in by science. Importantly, we view this technoscientific method, and here I will make a very strong statement as being complete. Each mechanism is essential, and there are no additional mechanisms. If you wanted to create an artificial intelligence to advance technoscientific knowledge, it would need to execute all of these mechanisms, and it would also only need to execute these mechanisms. And if you wanted to nurture human research to advance the technoscientific method, you would also need to nurture all of these mechanisms and no additional mechanisms. Okay, so now let's turn to Chapter 2, Questions and Answer Finding. The overarching idea here is that the facts and explanations of science and the functions and forms of technology are nested and loosely hierarchical. At any level of the science hierarchy on the left, there are facts. Those facts can be thought of as questions, looking for answers as explanations for those facts. But those answers, those explanations can be thought of themselves as questions looking for deeper answers, deeper explanations, deeper explanations for those explanations. The refraction of light is an observed fact at one level, explained by Snell's law at one level below, and in turn explained at a deeper level by the wave theories of Huygens and Fresnel, and then added even deeper level by Maxwell's equations. On a larger scale, cell biology presents questions that seek answers or at least partial answers, one level more foundational in molecular biology, and these answers are in turn questions that seek partial answers, one level more foundational still in chemistry. Likewise, at any level of the technology hierarchy on the right, there are functions. Those functions can also be thought of as questions looking for answers as forms that fulfill those functions. But those answers, those forms can be thought of themselves as questions looking for deeper answers, functions looking for deeper forms to fulfill them. An iPhone is a form that fulfills the human desired function of portable compute and communications, but it also represents an integrated collection of functions, all of which require subforms like gorilla glass or integrated circuits to fulfill. And these subforms represent functions that in turn require sub-subforms to fulfill. Let me make two points about this question and answer hierarchy, both points inspired by Phil Anderson, the condensed manner theorist who won the 1977 Nobel Prize in physics. The first point, point A, is that there is new and important knowledge at every level of the hierarchy. It is tempting to take a purely reductionist point of view and to say that knowledge at each level is based on knowledge at the lower level, so we only need research at the lower levels. Nothing could be further from the truth. At each level, there are new constructs that must be consistent with, but are not determined by constructs in the levels below. So there is imagination, creativity, and of course, research at every level of the question and answer hierarchy. This is what Phil Anderson meant in his classic More is Different paper. Nurturing research means not being snobbish about the level of the question and answer hierarchy one works in, but opportunities, but focusing on that level that is situationally and opportunistically most likely to bear fruit. The second point, point B, is that techno-scientific evolution isn't just the finding of new answers to known questions. It is the finding of new questions to answers that originally answered other questions. In science, this is, as we, as we mentioned before, generalizing. Like with special relativity, the answer to the question of why is the speed of light constant is found to answer a completely different and unexpected question of why there is energy release upon fission and fusion. In technology, this is exacting when the laser originally thought to be an improved way to do spectroscopy is found to be an improved way to do communications. Indeed, it is this constant generalizing and exacting with new question and answer pairs being linked across knowledge domains that creates what Phil Anderson called the seamless web of knowledge in which each link provides strength to the entire web and the entire web provides strength to each link. That said, although both question and answer finding are important, in our current environment, answer finding is much easier to find funding for. Only after one has found a question and one can write a proposal to find an answer to that question, can one usually find funding. In fact, it is often the finding of new questions that are that are the breakthroughs. It is often when moving into new fields that one finds new questions and and moving into new fields is not just a weekend hobby activity. It is an activity that requires enormous time and energy in and of itself. So nurturing research means allowing for the finding of new questions as well as the finding of answers to those questions. Finally, before leaving this slide, let me mention that finding questions and answers are often done independently. One has a question and seeks an answer to that question, or one has an answer and seeks a new question that could make use of that answer. But they are also sometimes done simultaneously and interdependently. You have an idea for a new light bulb that answers the question of how to better light the indoors. But you realize that that will require centralized production than distribution of electricity to the home, which becomes a whole new question that must be answered. We can think of this as as the co-finding of questions and answers. There isn't time to discuss this in detail, so I'll just mention that this might also be called co-design in the next adjacent possible and has been responsible for many technoscientific breakthroughs, including the iPhone itself. Let's now turn to Chapter 3, Surprise and Consolidation. We think of the evolution of knowledge as proceeding in a manner similar to the evolution of species in biology. As depicted in the diagram on the left, there are long periods of extension and consolidation of knowledge represented by these vertical bars that thicken as existing facts and explanations, existing functions and forms, are extended and consolidated. Then every once in a while, these periods of consolidation are punctuated by surprise. Some new question or answer contradicts or goes beyond common wisdom and creates a brand new vertical bar that then undergoes its own thickening as the new question or answer consolidates into a common wisdom. To put more common names to this punctuated equilibrium, we think of extension and consolidation of existing knowledge as the outcome of development, and we think of surprise to existing knowledge as the outcome of research. Importantly, research and development both cut across S dot and T dot. There is both scientific research and scientific development, just as there is both engineering research and engineering development. But as we know, research is often conflated with science and development is often conflated with engineering with two unfortunate consequences. First, we underfund engineering research because we think there is only engineering development. Second, we underfund scientific research because we think by funding scientific advance, we are automatically funding scientific research when in fact we are often instead funding scientific development. I do also want to make one level more concrete what we mean by surprise versus consolidation illustrated in these two diagrams on the right. Imagine you've come up with a possible new nugget of knowledge. It could be a scientific nugget, it could be a technological nugget. Imagine that the common wisdom of experts made guesses as to whether that possible new nugget of knowledge is likely to be useful. Their guesses might form a prior probability distribution over utility like this one in red at the left. Now imagine that that possible new nugget of knowledge has been played out. So now you know whether it's useful or not. Now you have a posterior probability distribution over utility like the one in blue. The blue distribution is narrower the uncertainty in the usefulness of the nugget of knowledge has been reduced. The blue distribution is also shifted. The usefulness of the nugget in this particular case is much greater than was originally thought. So common wisdom has been surprised. There are four possible permutations for how these prior and posterior probability distributions might line up illustrated on the right. In permutation one, prior common wisdom thought the possible nugget of knowledge would be useful and indeed it was useful. Belief was confirmed. In permutation two, prior common wisdom thought the possible nugget of knowledge wouldn't be useful and indeed it wasn't useful. Disbelief was confirmed. In permutation three, prior common wisdom thought the possible nugget of knowledge would be useful but instead it wasn't useful. Belief was disconfirmed. In permutation four, prior common wisdom thought the possible nugget of knowledge wouldn't be useful but instead it was useful. Disbelief was disconfirmed. Now you can guess what we mean by surprise versus consolidation and by research versus development. For permutations one and two, the nugget of knowledge was compatible with common wisdom. So common wisdom didn't need restructuring and indeed was strengthened. This is what we call consolidation and is what we associate with development. With development and consolidation, funders can much more easily anticipate and take advantage of what one finds as private goods, hence for funders to take the risk of funding the work. For permutations three and four, the nugget of knowledge was incompatible with common wisdom. So common wisdom needs restructuring in some way, possibly a profound way. This is what we call surprise and is what we associate with research. With research and surprise funders can't anticipate what you will find and even more so cannot anticipate the impact of what you will find. The impact of what you will find is just as likely, actually overwhelmingly more likely to have impact beyond the institution that funds your work than to the institution that funds your work. Thus research overwhelmingly produces public goods and suffers from the usual problem that public goods have. They will be underfunded. And the last three slides were all about the three aspects of the nature, about three aspects of the nature of research. Let's now turn to the nurturing of research. What should the characteristics of a research organization be to optimally nurture research in a manner consistent with the nature of research? I've divided these characteristics into three bins, A, B and C that you see here, and we'll walk through each of these bins in turn. But overarching all three bins is the notion that research is fragile, much more fragile than development. So research requires careful and attentive nurturing and is very much like tending a garden with fragile but unique and beautiful plants while also carefully uprooting the weeds. Let's start with bin A, the nurturing of individual researchers with care and accountability throughout their career lifecycle. First, research is a specialization requiring a certain temperament, a temperament that wants to explore and push the frontiers of knowledge. So recruiting and hiring must be extremely selective. Here perhaps the most common error is to hire for disciplinary knowledge because one has a project that needs that particular knowledge. This isn't to say that disciplinary knowledge isn't important, but it's important mostly as a signal for temperament and mindset, not for the knowledge per se. Second, because research is so difficult in its own peculiar way, even those with a research temperament will find it easy to drift away from it, to not seek surprise so as to avoid its associated uncertainty. Perhaps the most common error is to assume that researchers are adults. If they know what is expected of them, surely they will perform. Yes, they are adults, but and I can say this at my age, do we ever become immune from the vicissitudes of not succeeding when research is mostly about not succeeding? I don't think ever. All humans need moral support and only with such moral support, with mentoring, with a caring eye, can researchers know that they actually have the freedom to fail and only by giving them a long leash can they know that you actually have the patience for them to succeed. Third, of course, this is the real world and ultimately research is not for everyone. Opting out in favor of other pursuits, other pursuits that a person is better matched to, that's sometimes easy, sometimes hard, but regardless is sometimes necessary. Researchers must be cared for, but they also must be accountable to achieving surprise. Now, with carefully hand selected researchers on board, it is easy again to say, these are adults, let them free run and surely they will produce surprise. Again, nothing could be further from the truth. Venki and I like to say we are humans first, intellects second. We respond first and foremost to the social cues around us, what is rewarded and what is not, what is accepted and what is not, before we turn our intellects on. That brings us to Ben C. The culture researchers are surrounded by must be one that is aligned with research with what we call holistic techno scientific exploration. First is the idea outlined in slide one, that techno scientific method is a cycle that includes both S dot and T dot. One never knows where surprise will come. And by valuing both scientific and engineering research, one increases one's chances of finding surprise. Vannevar Bush knew better, but in some of his writings, he gave the misimpression that science comes first, technology second. And this goes against a core aspect of the nature of research. Second is the idea outlined in slide two, that research involves both question and answer finding, not just answer finding. In the scientific method, answer finding is most often answering the question of whether hypothesized facts are observable and true. Classic hypothesis testing in the spirit of Karl Popper. In the engineering method, answer finding is most often answering the question of what form would satisfy a known human desired function. Classic problem solving in the spirit of in the spirit of DARPA and George Heilmeier. But finding new hypotheses and finding new human desired functions to finding a new questions are just as important as answering those questions and must be given time and space and not just treated as hobbies. Third is the idea outlined in slide three, that research is all about surprise. That means research is all about being contrary and going up against conventional wisdom. That means taking the peer review of conventional wisdom into account, but being informed enough to know when to trust oneself and to go beyond peer review, when to be an informed contrarian. I can't overstate how difficult it is to be an informed contrarian. We all admire historical figures who went against conventional wisdom and changed the way people think and do, but it is really difficult to put ourselves in their shoes and understand the kind of social courage they must have had. This is why Venky and I also often say insulate but don't isolate research from development. Development is about consolidation of knowledge. It's about seeing how far one can take the current knowledge paradigm. It's not about being contrary and overturning the current knowledge paradigm. So research and development, although they feed on and shouldn't be isolated from each other, must be insulated from each other, shouldn't be isolated from each other intellectually, must be insulated from each other culturally. They must be in different organizations, each different organizations, each with its own culture in order for them both to thrive. Finally, Ben C is about the importance of research leadership. Again, it's easy to say researchers are adults. Just let them free run. Surely they will come up with great things. Again, nothing could be further from the truth. First, research requires collisions between ideas in different but not too different knowledge spaces. It requires a critical mass of researchers in those knowledge spaces and building such critical mass doesn't just happen by itself. It requires leadership with technical and people, wisdom and vision. Second, research requires leadership to be empowered and to have the resources to hire and build capability. In other words, resources must be allocated from the top down. Instead, in many research organizations, resources are matrixed in from the bottom up via individual researchers winning external proposals with research leadership ending up being little more than a tax on the projects that result from those proposals. The result is often a hodgepodge of research without coherence or a critical mass. Third, research requires leadership that is of course relentlessly focused on a nurturing with care and accountability and on b building and maintaining a culture of research. So what we've discussed just now is how a research organization can best nurture research, but research organizations themselves don't just magically appear. They themselves need to be nurtured. It is not sufficient for an organization to want to do research, to want to produce the public goods that first and foremost benefit humanity and only secondarily benefit the parent organization. My sense in talking with Liam earlier before we started the seminar is that protocol labs is an organization that wants to produce public goods that benefit humanity. But that is not easy for an organization to do. Alexander Graham Bell, the founder of AT&T, would famously invoke advancing knowledge as fulfilling a larger national national calling to improve all of human society. But even AT&T with its iconic Bell Labs, what we'll call it Bell as 1.0, would not have been able to do research without a public service source of revenue. For AT&T, this revenue was essentially the monopoly profits it earned as a result of the 1913 Kingsbury commitment in which AT&T became a regulated monopoly in exchange for ensuring interconnection of local carriers to its long distance network. When these monopoly profits went away in 1984 due to the breakup of AT&T, Bell Labs began to die as a research organization despite its researchers trying to maintain their culture of research. And Bell Labs was not alone. In the late 20th century, all of the great industrial research labs, including GE Research, IBM Research Labs, Xerox PARC suffered, not necessarily because they lost monopoly power, but just because the Wall Street pressures of short-term and private return on investment on invested capital became more and more pronounced everywhere in the economy. And I want to emphasize this is not necessarily a bad thing. It was Wall Street's single-minded focus on such returns that helped U.S. corporations become among the most competitive in the world. It just means that research as a public good must be nurtured separately, not by Wall Street. How might we do that? Here on the right, I sketch one possibility, one way to nurture research organizations in a way that would be aligned with how, as outlined on the previous slide, research organizations might best nurture research. Let's call these Bell Labs 2.0s. You can see that there are two sides to how these Bell Labs 2.0s could be nurtured, one private, one public, in a public-private partnership. At the bottom is a private goods funder, a parent corporation that sees a need for the private goods utility that research can provide, even if it knows that because the greatest benefit of research is not private, it cannot afford to support such research on its own. But it is willing to put out matching dollars for such research, it is willing to manage the research, and most importantly, it is willing to put its knowledge to work on behalf of research, its expertise, its problem-rich environment, and a focus which translates to building appropriate critical mass in a right-sized knowledge domain. When we said on the last slide, insulate but don't isolate research from development, this is what we meant. Research must be its own organization with its own culture, so these Bell Labs 2.0s must be organizationally separate from the parent company, but research must not be isolated intellectually and infrastructurally from development because there is so much opportunity for synergy between the two. At the top is a public goods funder, an organization that wants to fund public goods and only needs to see public, not private, return on its investment. This is uniquely only philanthropy or government agencies, but importantly, not all philanthropies and not all government agencies. Many philanthropies have a narrow mission to cure cancer, for example, and are less motivated to fund research that would spill over well beyond curing cancer. It might not even have any impact on curing cancer, and many government agencies have a narrow mission and are less motivated to fund research that would spill over beyond that narrow mission. Perhaps most importantly, some mechanism must be put in place for the funding to be awarded competitively. Research is not a free lunch, cannot be a free lunch. A Bell Labs 2.0 that wins a competition, for example, for public goods funding, must show after some period of time that it is producing surprise, otherwise it mustn't be renewed. Exactly how one judges public good surprise is non-trivial, much more difficult than judging private goods utility, but it is worth thinking deeply about how best to do it. One possibility, the default possibility, of course, would be committee judgment, similar to prize committees that make decisions on, for example, what has most transformed particular knowledge domains, Nobel prize committees, for example. Here, though, the stakes would be much higher. We would be talking tens and hundreds of millions of dollars, as opposed to just one million dollars. Of course, conflicts of interest and politics could be difficult to avoid, but at least there is some existence proof for how it might be done. Another possibility is decentralized quadratic financing, a method that I think some folks at Protocol Labs might be exploring. I personally don't know enough about this to comment on it, except to say that it does seem worth exploring ways in which one can judge, one can evaluate the production of public goods. That's worth thinking deeply about. Okay, so with that, thank you for your attention.