The Bioinformatics CRO Podcast

Transcript of Episode 7: Adam Marblestone

Grant: Welcome to The Bioinformatics CRO Podcast. I’m Grant Belgard, and joining me today is Adam Marblestone. Adam, can you introduce yourself please? 

Adam: Sure. Hi Grant, I’m a Schmidt Futures Innovation fellow working on trying to roadmap and galvanize funding for new medium scale moonshot science projects. And previously I’ve done a bunch of research in a few different fields, many of them connected to neuroscience in some way: a bit on neuroscience-inspired AI, a bit on brain computer interfaces, and earlier some work on molecular biology tools and imaging tools for the brain. 

Grant: Thanks. I’d really like to get to some of your older work, but first let’s start out with FRO’s. What are they?

Adam: The basic observation behind FRO is that there’s a class of problem that is not a great fit either for academia or for startups. The reason why academia struggles with this type of problem is if it requires a certain level of concerted organization and scale of an effort beyond a, let’s say a handful of people tightly working together.

So an example of this is recently a deep DeepMind’s recent work on protein folding, where you have 18 co-first authors on one paper. And that would be very unusual in academia because in the end, everybody has to have their own thesis or their own postdoc or so on. So you do have people in academia who very much want to collaborate and can be very good at it, but from an incentive perspective, it’s hard to get say 20 or 30 people working in a tight-knit engineering organization for let’s say five or seven years to build something, a really complicated integrated system. On the other hand in startups, it is very possible to do that, but by the time you’d be five or seven years, and you really need a very clear path to revenue and product market fit and often for a fundamental, if you want basic science platform, that wouldn’t be a good fit. So FRO’s are simply an attempt to get both the government and philanthropists to fund dedicated nonprofit organizations to tackle this class.

Grant: How do you see this as different from what came before?

Adam: Well, I think there are definitely hints of this, and in some ways we’re just drawing attention to the need for more of this. I would say projects like Janelia Farm Research Campus doing a fly connectome, or the Allen Mouse Brain Atlas, some projects at institutes like the Broad and Sanger Institute.

There are certainly concerted projects, and there’s also examples that are much larger like the Genome Project was maybe $3 billion or so. The way we envisioned focus research organizations is 30 to 50 times smaller than that, roughly. So tens to hundreds of millions, rather than billions. Enough that you would meaningfully change the incentives and organizational structure and path of a field, but not necessarily have to put billions into a single project. So I think that really the observation is just that there’s more need for this type of model than is being satisfied by the existing mechanisms, and that it is possible to systematically go and try to identify what those are and push on them.

Grant: And what fields and projects do you think would be the best candidates for an FRO?

Adam: Well, that’s part of what we’re trying to figure out now. We’re going around to the scientific community pretty broadly and asking people, “what would you do if you were not only not limited by funding, but also not limited by structural affordances?” Imagine that you could take your research program that you want to do and spend four or five years doing that as a FRO with the optimal resources, and then spin off several companies, and then incorporate that back into universities or government labs. So we’re going around pretty widely. I think there are a few different categories of FRO that do emerge from that. One is where you have to build a prototype system that just involves a lot of complicated working parts, but it’s directed toward some kind of basic science problem.

The classic example I always use of this is next gen connectomic brain mapping. So normally with brain mapping, at the finest resolution where you could actually see connections between individual neurons, you are dealing with the electron microscope, which is the highest resolution microscope that there is.

You need that because the way you’re labeling the neurons is you’re just saying any given pixel is either black or white, basically a gray scale. Is this the membrane of the cell, or is this not the membrane of the cell? And then you have to image that very, very finely and then try to reconstruct the shapes and connections of all the neurons from that very high resolution, but at some sense, limited data, which is just membrane or non-members. Now with optical microscopes, you can get much more information out of any given pixel.

You can, first of all, have several colors, but more importantly, you can image the same spot many times because the light is not destructive and you could flow on different chemicals and reagents. So you can get a huge amount of information out of any one spot, but the resolution of optical microscopes is slightly lower.

You can overcome that with new chemistries, like expansion microscopy, which moves the molecules apart from each other, so that they’re more easy to resolve and with fancy microscopes and instrumentation that can boost that a bit. If you wanted to make a brain mapping technology or generally a biological tissue mapping technology based on this, where you can see lots of molecules and adapt this, to be able to actually see neural connections, you just have to put a lot of pieces together.

You have to put multiple types of chemistry, multiple types of biology, multiple types of engineering and instrumentation, and it’s just complex, building out that prototype system. Once you have that, scaling it is also challenging, but it’s a slightly different problem. So that’s an example where you’re building a prototype, and you also see things like that in completely different fields.

You can imagine making the first drill that can drill down into very high temperature rock for fine geothermal energy sources or something like that. It’s a completely different field. Similarly needs to integrate high temperature electronics from NASA with drills from the oil industry and geochemists or things like that.

So that’s a prototyping FRO.I think another category is something that’s more like a foundry where in general, there is some ability to do something already, to produce some kind of artifact already, but it’s not reliable enough and systematic enough that end users have access to it. So this is maybe closer to things that companies would do, but in some cases, the resource that you want to produce should be some kind of public good, and/or it’s deeply pre-commercial in the sense of the application space is not yet known.

So we see this in several areas of nanotechnology or nanofabrication where, for example, with the next generation of 3D integrated chips. Conventional chips, you basically have layers of silicon metal insulator on a flat surface, but what you might want to do in the future is have things like layers of carbon nanotubes, and very deep three-dimensional interconnects between these different layers, so very densely integrated in 3D with lower energy switches. And that’s something that requires you to go beyond the kind of foundry environment that Intel or TSMC or these other companies where you can order chips from already have. So you need to build a foundry for that. At the same time, it’s not clear exactly what the application is yet, because you would have to figure out what kind of software compilers and all sorts of other things you would make for that.

So you actually need a foundry just to be able to discover applications, let alone actually sell something. So that’s an example of FRO for a foundry, and we see that with a bunch of different areas of nanofabrication. Then I think a final category of, although this is not an exhaustive list, would be something like an observatory, which is a little bit more similar to the Human Genome Project, where you just need to collect a data set in a very unified way. Maybe you have existing- 

Grant: Maybe like the Allen Institute. 

Adam: So yes, I think the Allen Institute, many existing institutes, I think do something that’s more like this. They take a relatively mature set of technologies and they just integrate the data. They just create a more unified way of collecting and accessing that data. I see a lot of need for that in some fields of disease biology and in-vivo biology where a lot of the existing institutes that do the data collection at this scale actually are focusing mostly on the normal state.

One example of this would be human brain tissue, doing really deep proteomics, maybe even single cell level proteomics of human brain tissue samples. Another example would be in the field of aging or geroscience. There are a bunch of putative interventions that have emerged, including one that was recently on the cover of Nature, claiming to have ways of basically reversing aspects of the aging process.

And this is pretty amazing, but often different papers and labs in this field measured completely different things when they apply those interventions. So, one lab will have a relatively small number of mice and they’ll measure a few properties, but maybe not the lifespan or maybe not methylation clocks in the blood that are supposed to be predictive of the rate of aging. Another lab will measure the meth methylation clock but not measure cardiac function or something like that. And so how do you have a really unified basis on which to compare and combine these anti-aging type interventions? That would be an example of the kind of observatory I think you could build where you would really systematically look at the phenotypic effects of aging and interventions against aging. 

Grant: Very cool. So, if you could direct a $100 million to a specific FRO today on this podcast, you have to choose in the next minute, what would the topic be? 

Adam: Yeah, it’s hard to choose one. That’s part of why I think we want to create a- 

Grant: Wait, which of your children do you love the most?

Adam: You can’t answer it. I mean, I think that there are different ones that are appealing for different reasons. I think some are appealing because they so clearly fit the FRO category. They’re so clearly not doable in some other way. Others are perhaps more appealing because of the near-term impact that they would have, or the kind of clarity of the path to impact. I think we want to really add to the vocabulary of government and philanthropy that this is a more repeatable model to be used and complimentary to lots of other ones, including the ARPA or DARPA model, which is a bit more discovery oriented and yet also aims for a certain degree of scale or concertedness of efforts.

Personally, you know I have some long term interest in the brain mapping when I mentioned it, but that’s just one example. Yeah. 

Grant: So what would be the ideal outcome of your current position? What would constitute success? 

Adam: Well, I think if we could get philanthropists excited about essentially wanting to own topics this way. So if you have someone who’s really interested in antibiotics, then perhaps in addition to supporting a diverse set of research about antibiotics or investing in companies that have antibiotics near to the markets. The go-to thing would be to say, well, let’s figure out what the FRO would be for accelerating the field of antibiotics discovery.

And then it’s a big ticket item compared to too many things, but for some of the larger scale philanthropists out there, tens of millions of dollars is not a completely unreasonable amount to spend. You might spend that much on having a building or something. How about instead, just nail antibiotics discovery platforms or something like that. That would be on the philanthropic side. On the government side, while there are multiple potential governments, but on the US government side, what we wrote in this white paper that we’re circulating in the policy community through this entity called the Day One Project- day one referring to the first day of a new presidential administration.

The idea there is there’s an entity called the Office of Science and Technology Policy, which is part of the White House, and it helps to coordinate the priorities that the president and the White House have with what the individual agencies like the National Institutes of Health or the Department of Energy are doing.

I think perhaps an ideal outcome on the government side would be the Office of Science and Technology Policy (OSTP) coordinated initiatives where multiple different agencies each have their own. If you want interpretation of how to push more research into these kinds of concerted moonshot projects, you could therefore have FRO’s in multiple domains that way.

Grant: So going way, way back, I want to go to your PhD, but I’m just curious to go back even further. Tell us about your childhood, where you grew up. Were you already interested in science or did that come later? 

Adam: Yeah. So I grew up in Western Massachusetts, and as a young kid I wasn’t necessarily the most scientific. I had some of my elementary school colleagues were much more scientifically advanced than I was.

I was doing a bunch of sports, karate, and gymnastics and horse riding, and eventually got really into gymnastics for a while. But my dad had a telescope. He was an amateur. He was an economist but an amateur astronomer. I got exposed to astronomy that way, so I knew that was cool. I had supportive parents that would buy books and stuff for me.

So I’d sometimes end up in the Barnes and Noble. I don’t know what you have local to you, but when I was a kid, the Barnes and Noble bookstore was where you would go. I sort of use it as a library cause you could basically read stuff that was on the shelf, so I would go to the science section of Barnes and Noble, which presumably was a consequence of my dad helping me get excited about both stars, galaxies, and robots or so on. So that seemed like the natural place to go, and eventually in doing that, I stumbled across books that got me interested enough. One was about nanotechnology and introduced me to the idea that you could have general purpose technologies that would very broadly impact multiple key areas of human life.

Grant: Do you remember the title of the book?

Adam: Oh, that was Drexler’s book called Engines of Creation. 

Grant: That was one of my formative books too, actually.

Adam: Wow. Yeah. It’s funny how it doesn’t necessarily have to be a successful academic field for something to be absolutely transformational for generations of people.

So that was one, there was another popular science book at the time that I was a kid called The Elegant Universe by Brian Green, which was about string theory and cosmology. So between those two, I knew that there was a lot of cool things you could do with biotech and a component to getting at that through physics, and so that set my path. So eventually gymnastics was taking too much time away from my reading physics books, and I eventually got to the Feynman books and stuff. Once gymnastics was in the way of the physics books, then it was clear what the choice was.

Grant: Great, and maybe we can jump forward several years. Tell us about what you did during your PhD. 

Adam: Well, PhD was a pretty crazy ride because I had a high freedom graduate program called the biophysics program at Harvard, which was really a kind of wild card where you could basically work in any department or lab in the broader biomedical sphere at both Harvard and MIT. It’s kind of an underappreciated program in how much freedom it gives you.

And then I ended up with a very high freedom advisor, George Church, who is first of all, very creative and open-minded, but second of all has, I don’t know, fifty to a hundred people in the lab at any given time. I had a lot of freedom there, and I also ended up with a high freedom fellowship. So I really did have this free phrase. Enough rope to hang yourself, and I definitely had that many times over. As a result, basically as a PhD student, I was trying to pursue somewhat perhaps unrealistic moonshot projects, very much of the nature of what we’re now trying to do with FRO’s, and it was only along the way that we managed to publish a few kind of basic papers to actually do the PhD.

But I started out interested mostly in biomolecular self-assembly and trying to make the so-called DNA origami structures, which self-assemble in a programmable way, I wanted to make those much bigger so that we could integrate those onto silicon chips and make a kind of bio chip that would have nanometer to centimeter levels of control all the way in the single platform.

With that one, I think we made a little bit of progress. We did make some unusually large DNA origami, but I also realized somewhere in the middle of that I didn’t have a very clear path of what the applications would really be of that. So midway through, I sort of switched to neuroscience and had also a very unambitious goal of trying to record simultaneously all neurons in the mouse brain.

Which in the Church lab, which was mostly focused on DNA based technologies, the natural way to think about doing that was to try to record neural activity into DNA molecules inside your cell, so we did a lot of ideation and kind of team building around that. A little bit of preliminary experiments, where we were exploring whether you can get these DNA polymerases which copy DNA to encode information about the ion concentrations in their environment, which would be reflective of neural activity, into patterns of errors in copying DNA. And then we sort of branched out from there, both to collaborating with a number of other labs on applications of DNA barcoding and DNA encoding to structural brain mapping, and on trying to understand more from a physics perspective a number of different ways you could record neural activity and super large scale. Including but not limited to these kinds of molecular methods, so that was a pretty weird PhD. 

But it definitely was the breeding ground for thinking about these kinds of focus research organizations and what would it actually take to properly execute on some of those ideas that as a grad student, I was nowhere close to being able to do on my own or with the few people I was collaborating with.

Grant: And somehow in the middle of all that you co-founded BioBright. 

Adam: Yeah. Well,  I met another person who was interning in the Church lab at the time named Charles Fracchia, and one way to put it, maybe unflatteringly to both of us, is that neither of us were that great at wet lab experimentation. Charles was maybe a little better than I was. He had had an undergrad in biology and mine was in theoretical physics, but we were interested in whether there was a way to make it easier to keep track of what was going on in your wet lab experiments, and there was a popular and exciting notion just emerging around that same time of cloud labs.

What if you were to basically have a web interface to an external lab that would do the experiments for you with companies like Emerald and Transcriptic popping up, and our feeling was that that was part of the story. But the other part of the story would be, how do you augment the scientist in situ in their own lab and make it easier for them to take notes about what’s happening and to compare what happened in the experiment to what the protocol should have been, or even simply to gather and centralize data from all the different experiments and equipment in the lab into a central way of looking at what was happening.

So eventually Charles did some more work on this in the MIT media lab as a master’s student, and then went off and became CEO of his company. I was a co-founder and helped it get some grant funding and recruit some initial people, but Charles has really been leading the charge on that.

And that has just evolved a lot by interactions with customers and contracts and understanding what different commercial entities need in terms of tracking and analysis of their experiments. But that’s also been a really interesting thing to see happen. Yeah.

Grant: And so after you finished your PhD, you went to work with Ed Boyden at MIT. Can you tell us about what you did there? 

Adam: I developed a lot of ideas around these issues of large-scale brain mapping in the PhD, as I mentioned. The idea there was that teaming up with Ed and others, we could increase the scale beyond individual experiments that I was doing. And so how can we launch larger initiatives and projects?

It’s just seeing the line from where I was towards doing focus research organizations. This is where we started to think about how to move in that direction. So a lot of the work I was doing with Ed, I wasn’t doing experiments in the lab, but I was doing a lot of grant writing and a lot of coordinating of teams and developing strategies and collaborations to try to particularly develop some of these next generation structural brain mapping methods.

The main thing that was exciting at the time and continues to be really exciting to me is in 2014 or so between the Church lab and Tony Zador’s lab at Cold Spring Harbor which had been leading the development of these so-called DNA barcodes for identifying individual neurons in the brain. With Ed having some input into that as well, we were thinking about how do you combine all these pieces together into an ultimate brain mapping technology for the structural and molecular end of brain mapping, not for the living state.

It seemed really promising, but there was this one missing piece, which is that you have to really fancy microscopy in order to make this work. You’d have to slice the tissue really thin, and it was just challenging. And the church lab had just come out with this idea of fluorescent in-situ sequencing which was kind of working, but it was a bit hard to get it working in actual intact slices of tissue, as opposed to just cultured cells. The tissue processing and the microscopy were just hard. But Ed at the time took me into his office and said, “You know, we have this cool thing that we’ve been working on, which is a new way of doing microscopy that solves all the problems that you’ve identified.”

And I was like, wow, that’s pretty crazy, and this was this expansion microscopy thing where you physically swell the brain tissue with the hydro gel to move the molecules apart from each other in an isotropic uniform fashion, 

Grant: Like everyone in the neuroscience world did a journal club on that.

Adam: So what we were trying to launch, maybe we were a little ahead of ourselves, we were trying to launch big initiatives to move this into really developing a strategy and workflow for doing a very integrated form of brain mapping. In practice, it took several years just to be able to get any kind of grants at all about this, for example because it just seems so crazy to people. Even though they had done a really great job and validating this, so it took some time just to gain basic acceptance by the community, and what we ended up accomplishing and Ed’s lab and collaborators with me kind of helping coordinate a bit of it.

What they ended up accomplishing is really demonstrating a bunch of different ways in which this can be used, including so-called double expansion or iterative expansion, where you can expand twice and get twentyfold expansion instead of fourfold expansion. This integration of the chemistry of the in-situ sequencing, or physique, so-called multiplexing methods with the expansion, which is now in a pre-printed bioRxiv and going to be published pretty soon, expansion microscopy where you’re staining the lipids much in the way you would stain with the electron microscope to make it more relevant for connectomic brain mapping in the more traditional sense.

We also just pushed forward a bunch of other ideas, including a still-theoretical approach to how you do single molecule protein sequencing, a bunch of things that sort of related to microscopy and molecular multiplexing, and it was a really amazing time with lots of people. Just seeing a lot of possibilities emerge.

Grant: And after that you went to work with Brian Johnson at Kernel, yeah? 

Adam: Right. Seeing the difficulty at the time of having anything quite close to a focus research organization for this brain mapping, I decided that maybe my best bet would be to use that same strategic roadmapping approach that I’ve applied to these different areas and try to push it in the context where we really did have a very scalable team that was commercial driven, but also thinking long-term because Brian Johnson had been making a big commitment of his own funds in his own time to run Kernel.

And at the same time Elon Musk was starting Neurolink. I had some discussions with those people as well, and there was kind of this burgeoning brain interface mini industrial boom around late 2016. All of a sudden people are like, we should start gigantic Brayton computer interface companies.

Whereas they hadn’t been saying that before weirdly. So Kernel was a great experience, and we basically went through and tried to figure out all the possible things that Kernel could do, ranging from deeply invasive medical devices to super next gen physics of how you would do noninvasive things, and then sort of met in the middle with what they’re doing now, which is a set of relatively practical but still quite new approaches to non-invasive brain activity, mapping headsets basically. They recently released a headset that does what’s called functional near-infrared spectroscopy, fNIRS, which is an optical way of measuring brain activity.

They’ve basically released a much faster, cheaper, better, more portable fNIRS headset and are starting to give that to a bunch of collaborators to discover what can you actually do with that. Can you decode speech? Can you decode mental imagery? Can you use it to help train AI? Can you use it to detect if a patient with a coma is conscious? A bunch of different things.

If you have more accessible imaging technology that you could potentially do and yeah, it’s super exciting to see that progress. 

Grant: And then you went to DeepMind. I don’t know how much you can tell us about that. 

Adam: Yeah, yeah, DeepMind was cool. I was on the neuroscience team. That was a really great experience, basically at the point where Kernel identified its product direction.

My crazy scientific roadmapping I think was a little bit less relevant. I chose to let them push on the commercial execution of that and the engineering of that, which is not really my strength, but it’s definitely the strength of some other people they have there and scratch my AI itch. Because in all of this time, thinking about how we could map brain circuits or brain activity, I had of course been reading a huge amount about the neuroscience literature and what do people think these things actually do? What’s the actual functional interpretation of brain circuits? So that’s what I tried to learn about in the time that I spent at DeepMind, which was amazing. I was on the neuroscience team there, and we explored a bunch of ideas, a lot of them having to do with how memory works. They’re on the AI side. It’s not directly possible to connect it to circuits yet. You know, so there’s nothing we can say, well, okay, we mapped this thing over here with in-situ sequencing or electromicroscopy, and then here’s the AI algorithm. Although we I spent a lot of time learning about exactly how close we are or are not to that in different systems.

And there are some systems where it’s much closer, like the way that the songbird does reinforcement learning for learning how to sing its song. That is something where we have both an algorithm understanding and a circuit understanding. Some of the higher level questions about how to get memory to work have a flexible way of accessing working memory and short-term memory in much the way we think about thinking is sort of “I remembered this and I combined this idea with that idea in some compositional way.” It seems to rely on having memory buffers basically, and we were thinking a lot about how that works in a way that’s inspired by what we know about neuroscience, but it’s still a little bit loose. But it was really cool.

I got to learn about how AI researchers think and write a bunch of AI code to try to test out these types of models of how memory might work. It’s a completely different perspective than conventional circuit neuroscience, but I think that I remain super optimistic actually, that these things are going to converge. But of course it might take some time. Yeah. 

Grant: So what areas of science and technology are you most excited about and do you expect might have the highest likelihood of affecting a major transformation to people’s lives and in society?

Adam: Lots of them, lots of them. Yeah. I’m excited about a number. I would say that with my initial push on nanotechnology as a teenager, right.

As I was mentioning, I still want to see a path to make that work. I see that still as having sort of fallen behind biotech. Lots of things we want to do with the material world we can do either with chemistry or with biology right now. And so general purpose atomically precise fabrication I think is one of these things that is really great, but it has a limited foothold in what the research community is doing right now to actually bootstrap that.

So in terms of things that seem on the cusp of really exciting developments and that I’m particularly interested in, looking at with focus research organizations,I would point to a few. One is aging and age-related diseases, and I think the aging field is really starting to take off. You can always debate this.

Have we actually understood anything fundamental about how aging happens and until you see results in humans, extending a mouse lifespan could mean something completely different. You know, mice die for very different reasons than humans do. Mice apparently mostly die from getting cancer. There’s not as much let’s say heart disease or various other things or Alzheimer’s or things like that, but I’m really interested in the idea that we can, including with animal models, identify common roots fundamental drivers of age-related diseases. 

I’m really interested also in neuropsychiatric diseases where many pharma companies have basically killed their neuro R&D divisions, but I’m optimistic that some of the brain mapping and proteomics and related types of technologies we’ve been thinking about now for a years, can circle back and tell you more mechanistic insights with what’s going on with brain diseases.

I’m weirdly really interested in geothermal energy these days, as a possibly underappreciated source of clean energy that requires its own moonshot to figure out how to drill deep in the earth. 

I’m interested a bit in applications of AI to social technologies and discourse. Can you make recommender systems that would be more genuinely helpful to people rather than just recommending what you will be most likely to click on? Can you recommend what will be most helpful to you as judged a month later or a year later? Or can you use that to sort of do fact checking or improve people’s reasoning ability with all these new AI based natural language and prediction technologies? So, I mean, I’m just excited about so many things and that’s, that’s why I’m trying to focus on organizational enablement right now. It partly means I don’t have to choose one. 

Grant: So since you’ve been investigating these areas, can you maybe give kind of the take home points of your understanding of where the aging field is today? What we know, what we don’t know, what maybe we think we know that we may not actually know. 

Adam: Hmm. I can try, but that’s a hard one, but I can try.

There was maybe a basis many decades ago for things to be kind of exciting just in the realization that different species age at very different rates, you have things like naked mole rats that seem somewhat similar to other rodents, and yet live much longer.

Things started to get exciting when people like Cynthia Kenyon were doing genetic screens in C elegans where they could pass for low lifespan and they could identify genes in a somewhat random way that would have a dramatic effect on the sea elegance lifespan, empirically. 

And then that started to hone in on metabolic regulation of how much we are doing something like repair versus how much we are just consuming as much as we can and growing as fast as we can. So sort of growth versus repair lead to the discovery of rapamycin and Metformin and stuff sort of emerge on that axis.

That was one stage. And then I think there’s been a more recent stage that in some significant part comes out of both this revolution of induced pluripotent STEM cells and the Yamanaka Nobel prize for work that I think was done around 2006 era whereby you can by dumping a few transcription factors on differentiated and aged cells, you can “reprogram” them back to a polypotent state, but also one in which a number of aspects of their physiology seem to revert back to a younger configuration. For cells in a dish, this was already exciting. 

One of the things that they measured in that Yamanaka paper was DNA methylation. And they said, look we know that as cells differentiate their methylation patterns change, and this procedure has actually reversed that methylation change. Perhaps, partly as a result of that, or just as a result of the growth of DNA array technologies and sequencing technologies, others have started to develop these ideas of epigenetic clocks that measure aspects of the rate of aging, that seemed to be somehow related to this differentiation versus reprogramming spectrum.

In that same era, there was also the discovery that if you want non-cell autonomous or sort of circulating factors that operate in the blood–this is not clear how exactly it relates to this metabolic access of the first Kenyon kind of discoveries–but in some as yet not very well understood way seems to restore the kind of regenerative proliferative capacity of cells through circulating factors. For example, famously if you take the blood from young mice and put it into old mice.

But what is really going on there? And just in the past year or so, there’ve been a number of advances along that, including one from UC Berkeley, where they simply rather than put blood of young mice, they simply dilute the blood of old mice. And they just put back one protein called albumin and saline. And that seems to have some of the same effects, although this is just a sort of preliminary study.  

And another paper where they have an as yet undisclosed fraction of a young blood proteome. They put that into old rats and they measure a bunch of physiology. They measure methylation clocks and things like that, and they see a bunch of seemingly kind of coordinated effects from these circulating factors. 

And meanwhile, all of these lines have proliferated and developed, and there’ve been a number of different compounds discovered that have some kind of effect in enhancing the re regeneration or blocking cellular killing senescent cells, understanding the interactions between how things like senescent cells drive systemic inflammation and how inflammation can in turn cause a bunch of other aspects of aging related problems like atherosclerotic heart disease and things like that. 

So I think there’s a lot of progress in understanding the physiology of different levers. It’s still not a unified picture where you can completely say, these are the core drivers versus these are the effects.

And there’s a so-called set of hallmarks of aging and, at the same time, there was this other paper about the pillars of aging, each of which I think identified eight or nine different underlying features. But none of those are completely understood. Is that really the right list of seven? Could you instead parcellate that in a different way that would reflect cause and effect more closely?

That’s still not really known, but I think it’s a great time to push towards these concerted FRO-style moonshots to really measure everything about what’s happening in those processes. You can never really measure everything, but to have a really systematic kind of genome project style attack on, on understanding how each one of these levers affects all of the others for more data-driven hallmarks of aging.

Grant: It’s really exciting. I love the optimism here. I’m a big fan of that. I was wondering if before we wrap up, if we could change tack a bit, and as you think about these various scientific and technological moonshots, what do you think is the greatest, realistic dystopian threat that could come out of this? And what can we do to mitigate it?

Adam: Yeah. I spent some time. I’m not really an expert on this, but I spent some time trying to ascertain what people are thinking about more versus less in these areas. I think sometimes there’s a lot of emphasis on risks from artificial intelligence. And in particular, sometimes people say that if you do neuro-inspired AI, that would actually be even more risky because if you sort of try to copy the brain for AI, it will be harder to prove theorems about that and basically prove bounds of sort of controllability or correctness because you never derived it from math in the first place. You’re just taking heuristic hints and then seeing what happens. 

I’m not sure I agree with that. I think that potentially, the brain may have some understandable, relatively unified set of learning principles that it uses. And that if we actually understand that better, we may be able to design AI safety or alignment mechanisms that are actually just more reflective of how the algorithm actually works. It doesn’t have to be totally inscrutable.

I also think that there’s potentially some software engineering ways that you can make really capable AI systems that are not agents in the sense of optimizing some single objective function that you’re worried about getting out of control, but rather just a very tightly sort of supervised sets of processes that are more like Microsoft word than they are a person. I think there’s a lot to be understood there, broadening out the research in AI safety. 

I generally feel that the obvious one is pandemics both natural and engineered. And I think we need to have ubiquitous DNA sequencing everywhere. Apparently it’s actually possible to see so-called viral chatter. So if, if a virus is starting to make its way to the point where it could start spreading in the human population, before that happens, you would start to see in patient samples, just a little bit of an uptake of this virus. So even if you aren’t going and sequencing the rivers or something like that, if you’re just sequencing people that come in for primary care visits or physicals or whatever, if you’re just sequencing the population, it should be able to track the emergence of viral pathogens. 

But I don’t think we have anything like that in place, let alone, globally to be able to anticipate. But we should also have something like ready-made vaccine candidates for each of the 20 or so major categories of viruses, so that you really know whether an mRNA or a peptide or what is going to work and maybe you have to customize it a little bit. 

So I think that we are still very under-prepared for biological risks and hazards. And then I think we’re very sociologically at risk of mass scale misunderstanding and vindictiveness. As we see playing out on the internet and I hope that particularly AI technologies can be used to actually sort of mitigate some of that rather than amplify it. But right now it might be on balance just by optimizing for attention or engagement. It might be on balance actually increasing the infighting of humans that need to be focused on moving forward as a species. 

Grant: Yeah, I think that’s still overall, relatively optimistic answered a dystopian question. So unfortunately we’re out of time. I wish we had more. 

Adam: Thanks a lot for this very wide and thought provoking discussion Grant.

Grant: Yeah. I really appreciate you coming on. Thanks Adam.