Engineering Serendipity: How to Tackle Scientific Problems in the 21st Century


– Hello everybody. It’s
really great to be here. I direct a group at MIT
that works on technology for mapping and repairing the brain, and this lecture’s been a
great opportunity to reflect, sort of, on the implications
of what we’ve been observing, as we try to pioneer inventions in an arena where there is no textbook, there are no instructions on what to do. And one of the things I wanna do today is take a step back and
say, well, first of all, what have we learned through our journey? And secondly, how general
are these insights? And thirdly, can we convert them into learnable, teachable things? Are these skills that can be applied? Can you actually make
yourself, if you will, lucky? And I’d argue that, you know, brain technology’s a very new
arena, and we’ve learned a lot by incubating it and growing
it in the last 12 years or so. And we’ve learned a lot,
you know, we’ve learned that we can think backwards
from complex problems. We can try to systematically think of solutions in comprehensive ways and we can really try to tap into natural structures of intellectual problem in order to look for patterns. So I hope is that in your
local range in today’s talk, from topics relating to cancer
to Alzheimer’s to philosophy to new methods of 3D
printing, if we get to it. And so, let’s see where we end up. Yeah. So the theme that I want to kick off with was this idea that in the 20th century we saw a lot of advances in the sciences that both were fundamental in a sense. Think of rockets land
on the moon or airplanes or transistors or lasers or
computers and the internet that also have a lot of
very practical implications for everyday life. The intentions of the 20th
century really stand out maybe in the history of humanity
in terms of their ability to empower people and to
allow people to create and to understand their world, and also to travel quickly
and to generate value. And I think if you look at the problems that a lot of us are
wrestling with right now, about a sixth of the way
in to the 21st century, whether it’s changes in climate or brain diseases or cancers or challenges in education or in poverty, these seem like hard problems. The failure rate is very high. The costs of potential
solutions is enormous. In my own field of brain technology, the cost to take a brain drug out of the lab and into
the marketplace is huge, maybe a billion or two dollars. The failure rate is over 90%
and it takes about a decade, and even then the treatments
often do not work. So, there’s a lot of worry that scientific progress is slowing and there’s a lot of worry that the problems that remain
to us are very challenging. And so, it’s fun to take a step back and ask, well, why are
these problems so hard? One possibility is that when you’re in the thick of things,
progress looks slow. It’s easy to forget now
that it took decades for the airplane to take off so to speak, between the Wright Brothers and eventually commercial aviation like the plane that got
me here late last night. From the transistor to
the microchip was 12 years and from the microchip
to the personal computer was another 16 years, and then from the personal computer to the internet was another 14 years. And so, maybe things look tough when you’re in the middle of it, but I think that actually
another possibility is that the problems that we are dealing with are actually harder in some ways. If you look at the 20th century, a lot of these discoveries and innovations relate to physics, the moon landing, the
transistor, the microchip. There’s a fairly small number of things that you have to think about in physics, and a fairly small number of ways that those things interact, electrons and protons, you know, molecular bonds, and all
sorts of things like that. But if you think about
education or biology or medicine or the kinds of topics that we are talking about
on the previous slide, there are lots of building blocks. The human genome contains what,
30,000 genes, and who knows how many combinations of
interactions there are? In economics or in
politics or in education, there’s so many variables, and these variables are hard to see and they’re hard to quantify
and they’re hard to control. So, I think what now often happens when we deal with brain
diseases or cancer or energy, is we often try and make
simplifying assumptions in our attempt to
understand these problems. But, assuming the problem is simple doesn’t actually make it simple. And so I think the problem is that we end up making assumptions and late in the game a lot of
the solutions can fall apart. So in my group at MIT, using technology of
the brain as a testbed, we’ve been really thinking about what can we learn, what can we solve, and are there generalized
insights that we can make that allow us to, maybe, solve problems in other fields as well? Can we de-risk our problem in
a way that increases our luck? Can we, as the title of
the talk speak towards, engineer serendipity? Now another point of view, and it’s a very popular one right now, is to think about the
concept of the moonshots. First thing, let’s just go for it, pour lots of money and
talent and time into it. Fail fast, plunge on, plunge on. And so, it’s useful, you know, I’d like to study the history of science to learn about its future and looked back and actually learned about the moon landing and it’s interesting. If you look at JFK’s speech proposing that we go to the moon, he wasn’t saying, here’s
this impossible goal, let’s foolishly try to conquer it. He actually argued that it’s actually pretty
straightforward to get there if we put our hearts and minds to it. He argued, within the last 19 months, 45 satellites have circled the earth. He argued that we are behind and we’re gonna be behind for sometime. In other words, it’s
not an impossible goal that we have no chance of getting at. It’s actually, if we put our hearts and
minds to it, a feasible thing. I don’t mean to trivialize it at all. Obviously, it’s one of the
great achievements of our time, but the risk was low
because landing on the moon was built on lots of solid science. We knew where the moon was. We know about gravity.
We know about rockets. This goes back for centuries of science that builds upon science
that builds upon science. and so, it was a great
feat of engineering, again I don’t mean to
trivialize in any way, but the science risk, if
you will, was fairly low. In 1962 at the time of JFK’s speech physics was a pretty known thing. Now, imagine that we
tried to land on the moon 400 years ago, let’s say the
year 1600, to pick a number. We don’t understand gravity very well. We don’t have the mathematics to figure out how to launch a rocket. We don’t know about aerodynamics. You’d probably end up
with something like this. People start launching hot air balloons, you’d start tying kites to chairs. In fact, I believe some
people tried such things. And, maybe all the
money on earth would not get you anywhere near the
moon in the year 1600. Now, I think sometimes you see a dichotomy that it’s not completely true put forth. Okay, you can do basic science at a very slow rate forever and ever. We don’t wanna wait 400
years to solve the brain, or come up with better
energy or cure cancer. On the other hand, we don’t
wanna take any shortcuts that end up making assumptions
that we later regret. And so, I would argue
there is a third path. What if we build the tools
that accelerate the science? What if we were, in the year 1600, to figure out the physics
and invent the mathematics, rather than tying kites to
chairs, or hot air balloons, and trying to get them into outer space? So this third path is a sort
of interesting way to think. Can we accelerate the
path to understanding? For these 21st century sciences, where there’s lots of building blocks, and lots of interactions, we can be creative by maybe building tools that let us observe and
control those building blocks and those interactions. This requires new technology,
which is one of the reasons why it isn’t yet a particularly
popular way to think, but we are getting there. You know, you see all of these
multi-billion dollar projects now emerging, they’re trying to make maps of the building blocks of the body. I think that’s a good sign. The map of the genome, of course, kicked off a lot of modern biology. And we are arguably still
in the early stages. But building these tools is hard. The tools for editing the genome, for visualizing molecules, these all were, sort of, stumbled across. CRISPR, I think a lot of
us have heard of that, was discovered by some
scientists studying yogurt, of all things. Fluorescent proteins, which
let you see the genes that are active in a cell,
those are stumbled across by a curious marine biologist who was obsessed with jellyfish. So, one way to ask this question is, can we get to the ground truth faster? Can we do, on purpose, what previous generations
did accidentally? One of my favorite stories is about this gentleman named
Julius Wagner-Jauregg, and he won the Nobel Prize in 1927. So remember, the greatest
idea of its time. And what do we get it for? Well, he would take patients
with dementia-paralytica, and he would deliberately
give them malaria. That might not seem like a
great idea for medical therapy, remember, it’s a Nobel
Prize winning discovery. Why is that? Well, at the time, this disease was caused by the parasite that causes syphilis. And malaria causes a high fever, which can kill the parasite. So at the time, this
was not a bad way to go, although it did have a 15%
chance of killing the patient, so that was not the popular
part of this therapy. So that was 1927. One year later, 1928,
penicillin was found. And to nowadays, if you look at dementia that’s related to syphilis,
it is pretty much unheard of. By going to the ground truth, by figuring out the germ
that is causing the diseases, and then coming up with antibiotics that selectively destroy the germ, you can actually wipe this out. Fleming of course found this accidentally. He had some plates of bacteria and he came back one day to find out that a fungal infection
had wiped them out. And famously he looked at the plates and said, that’s funny. So how can we actually start
to engineer serendipity? My day job is to work on the brain. And what I hope to do today is to, through some illustrative
examples from our group, but also taking a step
back and thinking about what general knowledge might emerge, is to see whether indeed we
can pick out a couple tricks that are again, learnable and teachable, that allows us to think
about how to be creative in the context of these
21st century sciences? So, why is the brain so difficult? Well, it’s incredibly complex. In a cubic millimeter of your brain, you have 100,000 brain cells, connected by a billion
connections called synapses. And they operate at a very high speed, around a thousand times a second, they can go up to the potential to release chemical transmitters, or fire off electrical pulses. So in my day job the goal
is to really build tools to achieve these ground
truth types of insights. Can we discover penicillin on purpose rather than accidentally? And to do that, we need to watch these high speed
interactions of these brain cells, we need to control those
high speed interactions, and we need to map out
how they’re wired up, how are they connected. If we can watch what’s
happening in the brain, we can see how those patterns go wrong, in diseases like epilepsy. If we can control the high speed dynamics, maybe we can repair the changes that go wrong in brain diseases. By mapping out how it changes
at the molecular level, maybe we can actually understand how molecular changes occur,
and how we can fix them in conditions like Alzheimer’s disease. So one of the things
that we do when we try to go for these ground truth insights is first of all to understand
the structure of the problem. And again, a lot of
these problems have a lot of building blocks and a
lot of ways they interact. But in the brain, there
are two other problems that really make it stand out
in the biomedical sciences. The first is the incredible spatial scales that we deal with. Brain cells are enormous. They’re centimeters in spatial extent. Single brain cells can go a
meter down our spinal cord. Single cells. And yet, if you care about the wiring, those are nanoscale wires called axons. There are nanoscale
connections between brain cells called synapses that are
zooming in the full cartoon. And at those connections, they are jam-packed with
nanoscale molecules. So how on earth can you see these large-scale three
dimensional objects without losing sight to
other building blocks? A very difficult challenge. And the other challenge is time. So if you care about memory, if you care about Alzheimer’s disease, if you care about
learning and development, those are processes that
take years, even decades. But the quantal building blocks, the most small, fine-scale things that occur in the brain are a millisecond in duration. Millisecond duration electrical
pulses within brain cells. Millisecond duration chemical
exchanges between brain cells. So, in some ways, our
challenge in the brain is that we not only have to deal with
all these building blocks, but we have to figure how they communicate across space and across time. Now one of the hopes here, of course, is if we understand how brains compute, this could maybe help us understand something fundamental
about the human condition. What is it mean when we think, what does it mean to have a feeling? What makes us different from this computer in
front of me right now? But of course, there’s a very practical
and urgent concern as well, which is brain diseases, which affect a lot of
people around the world. And, if you look at the list here, pretty much none of these can be cured, and the treatments are pretty partial. And have a lot of side effects. I mentioned earlier how costly
and long duration it takes to make a brain therapy,
and on top of all that, they often don’t work for everybody. So let’s talk about a couple
short stories, and then take a step back and try to
think about what can we learn, about creativity and thinking, that might apply to other arenas as well. Well, this first theme
that I want to talk about is going down to the ground truth, right? Invent penicillin, don’t
give people malaria. And so, one of the ideas
that we decided was, what if we could map every molecule
in every cell in a circuit? What if we can get down to the
ground truth for the brain? That’s a very challenging
thing to propose. How are the molecules
organized at the cells? How are the cells
organized in the networks? I think we’ve all seen pictures like this, you know, brain scans,
they are very very popular, because of course they’re not invasive, you could scan somebody’s brain without having to do anything surgical. But these blobs, or voxels that light up, they contain millions
and millions of cells, and two cells that are nearby can be doing completely different things. And each of these little
blobs that’s active reflects millions of cells. So, at the other extreme,
you have microscopes. Microscopes cannot be used
on living humans, of course, but they can be very powerful, cause you can stare at
tiny things like cells. But even microscopes
aren’t powerful enough. They can’t see those wires. They can’t see the connections. And they sure can’t see the molecules. So one of the things that we try to do to get down to the ground truth is to sometimes think about doing the opposite of
what people are doing. For hundreds of years people have been zooming in on the brain. What if we do the opposite
and try to blow the brain up? As it turns out, that a bunch of physicists
have been studying polymers, like the stuff that you
find in baby diapers. These are polymers that
absorb huge amounts of water. So in this cartoon, you can see a little sketch
of what it might look like if you zoomed way into a
baby diaper, and can see individual strands of the
molecules that are inside. When you add water, osmosis
will draw the water in, and the baby diaper will swell. I think anybody who has a
kid has done this experiment a lot of times, maybe
more than you want to. So we start thinking, what
if we can do this to a brain? What if we can weave these
threads of baby diaper polymer around the building blocks, around the biomolecules that make up life? And if we do it just right, maybe we can pull apart the molecules. If we do it just right, maybe like stars in a
constellation in the sky, we take a cell like the
one on the left here, and pull apart the building blocks until they look like
something in the right, hovering in space, but with the relative
organization preserved. So doing the opposite is
often an interesting strategy, and we apply this all the
time, as a creativity skill that I would argue is a
teachable, learnable thing. But it’s only the beginning. One thing that we also do a lot of is we look at old forgotten ideas. These polymers they were, the physics was studied very
heavily in the 1970s and 1980s. And furthermore, people
figured out, believe it or not, how to synthesize these polymers
inside of tissues in 1981. So we had to do a few extra steps in order to make this technology work. In this cartoon, you can see some of the building blocks of life, the biomolecules, shown in brown. And we had to invent little
anchors, little handles, that we could attach to all of them, so we could pull them apart, shown as little purple
blobs in this cartoon. If we give every molecule a
handle, it can pull them apart, maybe that could help us get
down to this ground truth, level of description, that we crave. Then we have to weave
these polymeric threads, and as I mentioned earlier,
this was figured out in 1981, by two scientists in Germany. Basically you soak the
specimen than you want to embed in a solution of these
little building blocks called monomers, those
little white spheres, and they self-assemble
into these long chains. And the chains then can connect to the biomolecules through the handle. So if you think about it, we have the baby diaper
polymer, which can create force, and we have the handles,
which can convey them. We are almost there. But there’s one last thing we have to do. We have to soften everything up. The brain is very happy where it is, so we use heat and
detergent and other things to soften up the
molecules from each other. And then we add water, the
baby diaper polymer swells, and this time, the biomolecules
come along for the ride. So here is a little time-lapse movie, an actual piece of brain
that we’re gonna expand. We embedded it in the polymer earlier, and this is a time-lapse
sped up about 50 times, and here we add the water, right there. So I hope you could see this piece of brain is
growing before your very eyes. I’m sure it’s only a matter of time until some Hollywood script writer makes a horror movie out of this. (laughter) And because those polymers
are so tiny and so dense, we actually can get
resolutions approaching that of individual biomolecules,
which was our goal. We wanted to get to the ground truth, which meant seeing the entire system, the knowledge of sight,
of the building blocks. And so we published
this a couple years ago, and already we’ve
transferred the technology to hundreds and hundreds
of research groups all over the world, and they are investigating
all sorts of stuff with it. Parasites, and bacteria, and
cancer, and all sorts of stuff. But what we’re very excited about is the idea that now we can
actually make images of the brain that are three-dimensional, that can extend throughout circuits, that don’t lose sight of the wires. So here’s an example of a
little piece of the brain involved with memory formation, you know, what if we could some day read out exactly how memory is stored and the
architecture of the brain? I mentioned cancer earlier. We were approached by a
bunch of doctors, who said, Look, cancer is very hard
to detect when it is early. What if we could actually try
to see those early changes and diagnose cancer long
before it becomes a threat? So we worked with a
couple of pathologists, who work on breast cancer. It turns out that at the
early stages of breast cancer, doctors will disagree up to half the time, of the diagnosis, which is not good. And we showed that by expanding
breast cancer specimens, and using a committees vote to train a machine learning algorithm, an AI if you will, we could
actually do better diagnosis, than machine learning could
do, without the expansion. So expansion is bringing
these invisible features into the realm of the visible. So that’s the first part of the story. Get down to the ground truth. It sounds challenging, but you can build a tool to get you there. The next story I talk about is about time. So the first story’s about space, the second story I wanna
tell you about is about time. And the theme that I wanna bring forth in this part of the talk is, this concept of having
every possible idea. You know these are challenging problems. There are so many possibilities. How do you begin? And the strategy that
we’ve actually found, to be, actual useful exercise, is to try to think of every possible way to solve a problem. Now that may sound paradoxical, it might actually sound even a bit futile. And I agree that it’s not
provably possible in all cases. But even a partial attempt
to have all ideas can help. So the story I wanna tell
you about next is about how can we control the high
speed dynamics of the brain? How do we control the
high speed electric pulses the brain cells generate. It can be very dangerous
to pick just one path and stick with it, what
if it’s the wrong path? It’s also dangerous sometimes
to listen to experts. What if the experts haven’t been thinking of the problem at the right level? As the old saying says, that goes, you know if Henry Ford
listened to what people wanted he might of tried to breed faster horses. His customers didn’t have the concept of the automobile in their head. So it’s important to dig one level deeper. To get down to the ground truth, not just when you’re
trying to solve a problem, but when you’re trying
to pick the problem. I think that’s one of the essences of 21st century scientific creativity. One way to prove it quickly is if you’re thinking about
all the building blocks in a living system, or an economic system, or in education or these other complex 21st century problems. There are thousands of building blocks, they interact in so many ways. The probability that any
one is the most important, is pretty small. You can end up making assumptions. Rather than a moonshot you end
up with a shot in the dark. I sometimes call this the
illusion of reductionism. We try to pretend the problem is simple, but it doesn’t make it simple. So instead, can we consider
sets of hypothesis, as a group, rather than going
after them one at a time, and maybe failing over and over and over. This train of thinking goes
back to an astrophysicist named Fritz Zwicky. Fritz coined the term supernova. He thought of how the
neutrons stars formed. He hypothesized the origin of cosmic rays, even predicted gravitational
lenses in 1937. And now in the last couple
years gravitational waves have become a hot topic. In other words he saw the future. He thought of many ideas in
the 1920s and 30s and 40s that are the hot topics
in astrophysics today, like dark matter. How did he do it? Well he practiced a strategy that he called morphological analysis. But I call it the tile tree method. Basically you try to take a space of ideas and you split it into subsets, that like tiles of a bathroom floor will cover the space of ideas, so you don’t lose any ideas. But ideally you get, you hone
in to finer and finer ideas until they become testable,
modelable, hypothesis. Think of every possible way of generating an energy producing system. Okay, well let’s split it
into two subcategories, renewable and nonrenewable. So together that pretty
much tiles the space right? We haven’t lost any ideas
so far, ideas so far. But then you can make
some interesting splits. Let’s split renewable
into solar and nonsolar. And already we’re starting
to think of things that maybe are not obvious
ways of generating power. Because what’s a nonsolar
renewable source? Maybe it’s the moon dragging
water to make the tides change. Maybe we go after
geothermal energy, right? Strategies that are not usually at the top of most peoples list with
how to generate energy. Nonrenewable we can
split into fossil fuels and nonfossil fuels, so
that gets interesting too. What’s a nonrenewable, nonfossil fuel? Well maybe we can think about
nuclear energy for example, that we remove from the ground. And then you can split the
trees in different ways, mined and not mined, right? So I love this exercise
because it allows you to take a very complex space of problems and break it down into smaller subsets, so you don’t really lose ideas by splitting them into parts
but you get closer and closer to actionable ideas. So in my own life, that’s what we did to try to come up with a new
way to stimulate the brain. My co inventor Karl Deisseroth and I, we were both students in the year 2000. We decided to try think
of every possible way to stimulate the brain. And so we started making a long list of the forms of energy we could deliver. It could be sound, it could be mechanical, it could be optical, it could be radial. Turns out there’s only
so many kinds of energy that you can deliver to a brain. And then we started evaluating them, and in the end we picked optical because light of course is very fast, and you could aim it at things. So imagine you could
take little solar panels, install them in brain cells. As I told you earlier, brain
cells compute using electricity so if we put solar panels in there, shine line at them, we should be able to turn them on or off. And then the brain
doesn’t really feel pain so you could bring optical
fibers in the brain and turn on or off different
parts of the brain. If you could do this you could
start to activate brain cells and figure out how they could
initiate patterns of activity, they might heal a disease state. Or turn off patterns of activity, what if you could shut
down an epileptic seizure or a parkinsonian tremor. Then the question became how to make the cells light activated? And then again you can kind of split the space of ideas into two parts. You can make a molecule
that converts light into electricity, or you
could find a molecule. And so we started reading papers and we found papers
that actually suggested that these molecules existed
that could work in brain cells. And then the one that really got us going was a paper that studied algae. So algae like the one in this cartoon, some of them have flagella, these tails. And there’s an ice spot, the
little brown spot in the back that receives light and
converts light from the sun into signals that make those tails swim. They do this so that algae can swim to be near the surface of a pond, and so the chloroplast can receive light, and photosynthesize better. Now in this little ice spot in the algae there are proteins, and these proteins when they’re hit with light
open up a little pore, and charged particles or ions will move from one side of the pore to the other. In other words, exactly what we want. Now when you’re building tools, there’s always an element of luck. You can engineer serendipity but you can’t guarantee success. I’m not saying that these strategies are always guaranteed to work. And actually when we get
to the end of the talk we’ll end on this idea
of failure being the key. So what did we find? Well it turns out that
this proteins encoded by a little snippet of DNA. We could put this snippet
of DNA into brain cells and then we got really really lucky. Turns out that you can
manufacture in brain cells, these very same molecules. And these molecules will be
installed in the membrane and they wound up in the right spot. They didn’t kill the brain cells. And they were fast
enough and strong enough so when you shine light
on the brain cells, they would actually respond and fire off electrical pulses. Not unlike the ones in
your brain right now as I’m saying these words. So it’s just luck, but you
know, we optimized our luck. What can you do with this? Well you can use all these tricks from the field of gene therapy which I’m not gonna go into, and you can put this snippet of DNA so that it’ll turn on in cells
of whatever kind you want. So for example, there
are cells in the brain that are known to generate
interesting rhythms, brainwaves if you will. And one of my collaborators
actually took this molecule that we borrowed from algae, and used a gene therapy vector to make little star shaped cells in the brain sensitive to light. When you dry these cells with light, they have a resonance,
like a bell ringing. They like to go to certain frequency of around 40 times a second. This is kind of magical
number in neuroscience so you know, when you pay
attention to something your brain will have these
oscillations that occur. For example, in some regions that occur at 40 times a second. So my collaborator Li-Huei Tsai went on to try to figure out if you
could drive these patterns of brain activity, and could they ever induce a healing state? And so Li-Huei’s an expert
in Alzheimer’s disease, and so she used some mice that had been genetically engineered to have some of the mutations that in humans cause Alzheimer’s. So they’re not perfect
models by a long shot but you’ve got start somewhere. And she found that if you
drive the brains of these mice at 40 times a second through this trick which we call optogenetics. Opto for light and genetic
because we lucked out and small gene that we can
borrow from a little critter. Then the brain’s immune system turns on and you actually clean up a bunch of the different molecular hallmarks of Alzheimer’s disease like
the over phosphorylated tau or the amyloid plaques
or the inflammatory state of microglia cells. So that’s interesting, a
pattern of brain activity can actually cause the brain
to go into a healthier state in Alzheimer’s to boot, one of the hardest to treat diseases of any kind. So with Emery Brown, an anesthesiologist and expert in brainwaves,
the teams went on to try to figure out, could
you induce this problem without the optogenetics? We don’t want the optical
fibers and the genes in our brain if we can get away with it. What if we could do it
just by watching a movie or hearing something or seeing something? And so the teams went and showed that when mice would actually
watch a blinking light that blinked at this high
speed over 40 times a second. No genes, no optical fibers, no optigenetics, just a movie basically. Then the immune system would turn on and the mice actually would get better. And so Li-Huei and I
recently co-founded a company Cognito Therapeutics which
is now actually working on designing and testing in human trials, movies to treat Alzheimer’s. So once you have a foot in the door you can cast the net more systematically. Once we knew we could activate
brain cells with light we went on and examined how we could shut down neurons with light. We can search the entire tree of life for molecules that let us get control over different functions of cells and allows to control different things in brain cells with mice. And so now we have a
full suite of molecules. Let’s turn neurons on,
let us turn neurons off and so forth. Turning neurons off is particularly useful because you can delete cells momentarily. What if you could figure out the cells that would shut down
would ameliorate a seizure or turn off a tremor. Or some of my colleagues would try to look at Post Traumatic Stress Disorder, could you help reverse a traumatic memory? So we found molecules
from, that molecules from certain kinds of microbes you could put into brain cells and then shine light and turn off their electrical potentials. I’ll just give you one
of the many many examples of what people have done with this. One of my collaborators, Akihiro Yamanaka studies narcolepsy,
where people fall asleep at random and inopportune times. And in patients of narcolepsy, a tiny cluster of cells deep deep in the brain actually atrophies. And so he asked the question, if you turn off these cells
is that enough to cause sleep? Or maybe when these cells
are gone other changes occur in the body and that’s what causes sleep. So he engineered mice to have
these cells light silenceable, and he put an optical fiber into the brain connected to a laser. And here’s what he found,
this is the probability of being awake over
time, and the orange bar is when the laser turned on, and so the mice started out mostly awake, and then the light turns
on and you can see bam, within half a minute they’re all asleep. That’s what you see down here,
I’ll use the mouse I guess. And then when you turn the
light off they all wake back up but you can see they’re
a little bit groggy and they pass out again. So what we’ve learned this
process is really this idea of having all possible
ideas is a useful exercise. It’s not guaranteed to work,
but it could help you think of things that you might not
ordinarily of thought of. And it provides a structure for thinking that could really help make
more creative applications come to mind when you’re
dealing with something of almost infinite apparent complexity. So we started with ground truth, went on to all possible
ideas, and I wanted to end on the note of failure. Because failure is right at
the heart of everything we do. We try things out, and most
of the time it’s gonna fail. But I like to argue for
constructive failures. So in other words, we’re
gonna try something that’s gonna fail, but we’ll see something that nobody’s seen before, and that will tell us what to do next. I like this way of framing things because we’re not just
failing fast, you know, we’re learning from the process. We’re not just continuing
blindly on either, we will celebrate failure, but not enough, a way that feels false, we
don’t wanna celebrate failure in a way that seems artificial. We wanna celebrate failure in a way that really points to the future. And so the strategies that
I’ve been talking about today all had a long history between the idea, which would often happen several years before we actually got something to work. And sometimes the failure
was a failure of recognition. We’d have the idea, but maybe
not realize how important it was until sometimes later. We brainstormed up the idea
for the optogenetic control in the year 2000 but we didn’t bother with our first experiments
until four years later. Because it took us time to
realize how important this was. The idea for expansion of the brain, we thought up probably
around 2007 in our group. It took about five years
until again we realized, this is actually a really good idea. So one thing that I do a lot of is also try to learn from
other people’s failures. To talk to people and understand
what has hit a brick wall. And we can sometimes reboot
the failures into successes. If a failure is not due
to a fundamental problem, maybe it can be rebooted because now we have faster computers or we have mobile telecommunication, it’s our better genome
sequencing or who knows what. And that makes a past failure
enter a current success. As mentioned earlier I really
like to study the history of science to learn about it’s future. And if you look at some of
the most important discoveries of our time, they also had a
history of failure rebooting. And I think this is not
an uncommon observation. Google wasn’t the first search engine. Facebook wasn’t the first social network. Very often people came close but they were missing a certain thing. And by rebooting a failure
with a slight plot twist, you could actually make it successful. Let’s talk about PCR, the
Polymerase chain reaction. Maybe the most famous
reaction in all of biology. This is how you detect DNA
at a crime scene, right? Karry Mullis had the idea in 1985, kicks off a whole industry,
wins a Nobel Prize for it. But the actual outline of how
to do PCR was sketched out in a paper by some MIT scientists in 1971. A full 14 years earlier, what changed? Why was it not recognized? You could argue that there’s a, if we were to more deliberately
try to reboot failures. Maybe we would be able
to accelerate progress. Maybe one of the most famous examples of our time is machine learning. A lot of the mathematics
for machine learning and AI was worked out in the 1980s
and 1990s or even earlier. And now in the last few
years, algorithms based on these mathematics,
and extensions of them have been getting headlines for learning how to beat
people in chess and in go. What’s different now? Well we have a lot of data, we
have a lot of compute power. Back in the 80s and 90s those
two things were not there. So a good strategy is to
really track failures, both yourselves and others,
and look for opportunities to reboot them when the
world is a different place. So one of my jobs is really
to be chief failure tracker in my group and to
figure out when something that seemed like an okay idea or bad idea, might be time to make reality. My personal dream is that
we can not only continue to innovate, waste, innovate, like these ground truthing ideas, like the all possible idea strategies and like the structuring of projects with constructive
failures, but to make tools that are very practical and that tell us how the brain works. So tell me a few short stories about how we’re actually
building these tools. My dream is we can
bring in the next decade these tools together. What if we could watch a brain in action, and then map it out? And then in a computer
make a model of the brain so we can understand what
a decision really is, what a feeling really is. Would that help understand something about what it means to be human? What it means to have
thoughts and feeling? Maybe even become more enlightened and understand something about the nature of suffering and happiness. So for me, the long term goal is to really to start to merge science and philosophy. Can we understand something
about why we’re here, and what we should do in life. But along the way I’m very happy that we’ve been able to come up with lots of practical strategies that might actually help
with different arenas like Alzheimer’s and cancer and so forth. And so that’s maybe the closing
not that I wanted to end on. You know this is a long
path we want to take, or a tall mountain we wanna climb. Pick your favorite
metaphor, but along the way, we should try to reflect
upon what we’ve done and understand when something
is of general importance. And to teach it and make
it available for others. So thank you very much
and I can take questions. (applause) This of course is the
most important slide, this is a very large team with literally a hundred
collaborated groups around the world and in
a short talk like this we can’t acknowledge every individual but I wanna end by acknowledging
how omnidisciplinary this effort is and how many people led the different products. – We’re gonna open it up to the questions and we’ll repeat them so
that we can catch them on the video okay? – Yeah so I though that was
a really interesting note that you mentioned at the end, taking philosophy and science
and starting to merge that and I think, you know, throughout history we’ve done a lot of amazing things but it’s largely been external to us, you know the environment around us. And I think now we’re approaching a time where it’s starting to
look more internally, into the brain looking at how we can engineer our own genetics. And do you ever pause to
wonder if we should continue at the speed we’re going forward just for the sake of going forward? ‘Cause I think in a lot of elements, we’re just looking to change things and push new things back
for the sake of doing it. And maybe that’s part of
being human on some level, but I think that, maybe
on some other levels reflection’s important within. And maybe even do some permanent changes into what it means to be human? Do you think on that often? – Yeah that’s why I wanted to end on the note of philosophy, you know, where are we going and why, is important. And if we’re just
changing for changes sake in some random direction,
it’s very important… Very possible that one
could be efficiently going in a direction you
don’t wanna be going in. And so for me what got me interested in the brain at first place was this idea that maybe we could understand something about suffering and happiness. And curing people is
of course a great goal, but to me it’s almost like a byproduct of the long term goal of
understanding the human condition. That said, I do want to
figure out, how you now, we’re in an era now where Elon Musk is launching neuralink and Brian
Johnson’s launching Kernel, and we’re seeing Apple’s
hiring neural engineers. We’re seeing neural
technology become a thing and so one of things
that I’ve been working to figure out now is
whether we could launch what might be the first global
neural ethics conference, where we want to bring together companies and large and small, and
governments, and religious leaders, and lawyers and lots of
people, doctors of course, and to really figure out
what do we want to do. So 1975, that’s what the field
of molecular biology did, or gene cloning, and then
the half century since there’s been huge numbers
of therapies for cancer and hemophilia and all sorts of stuff. And the number of disasters
have been very very small, nearly zero frankly. And so I think that’s a suggestion that maybe we should get
out ahead of the problem. Let’s figure out how to talk about it. Let’s figure out how to self-govern, how do we decide what we wanna
do, what we don’t wanna do? Or what do we want to
do but let’s figure out how to do it better. And I think that we can, you know, again I think one of the themes that what I’ve been
trying to talk about today is how do we do on purpose what previous generations
did accidentally? We saw what worked, can we
make it more deliberate now? Yes. – I think kind of building
on that there have been in a lot of the discoveries we have made there’s been a lot of push back like in genetically modified
organisms for example. People are very uncomfortable with that, so have you seen or do you
expect to see a pushback on these ideas as well? – Well so the way that we’re
approaching the problem is to think of how to heal the sick. So can we build therapies to help people with different conditions? And the reason I think
that’s a good way to start is because you have to think about how risk and reward are balanced. When I get uncomfortable is when people are pushing to augment the brain when we don’t fully understand
the consequences of that. So for example there are people doing do it yourself brain stimulation. We don’t know that the long term effects of brain stimulation in humans, ’cause all of the studies
are fairly short term. So I would hate to think
that somebody would be stealing their brain maybe over a fairly trivial
quest like becoming better at a video game or something, and what happens 30 years later? But I do think can
emerge, through talking, but also if you look at
the history of medicine is that sometimes if a therapy comes out and it’s helping people
with very severe illness, but it is showing to
be safe and effective, maybe it can broaden a utility. And we’ve seen cases
where it has happened. We’ve also seen cases where people find out a therapy’s no good and they fold up. So, I do think there might
be a natural time scale over which medical ethics in 2018 would allow augmentation to occur, but does it make sense to try
to break the risk reward curve in an unnatural way, in a way
that might violate ethics, I don’t think so. Other questions? Yes. – I really love the idea
of constructive failures and I’m wonder if you’d share with us one of your personal failures. – Oh sure. (laughter) Well the two of them that I mentioned I think really stick out in my mind. The idea that between the idea for optogenetic controlled neurons and the idea of expansions and actually bothering to give it a try was about a four or five year period. I think this was sort
of a failure of wisdom. I’ll give an example for
the expansion of Croscopy. So a postdoc, Yongxin Zhao and I were brainstorming up this
idea of expanding brains but this was one year after a bunch of people were all working on nanoscale resolution microscopes so I was thinking yeah
they’ll figure it out. So fast forward to the point where Fei Chen and Paul Tillberg,
my two grad students who were the first authors
of the paper with the group. And Fei was trying STORM microscopy and Paul was trying electron microscopy and a year in it was looking like, wow it’s gonna take forever
to map a 3D brain circuit. So, you know, when we look at it is maybe we have the
knowledge in year 2007 but we didn’t have the wisdom until Fei and Paul actually
wrestled with the problem and went through a constructive failure. And so we then abandoned
the electron microscopy work and we abandoned
Super-resolution microscopy work but that wisdom then helped
us go into the next stage which turned out to be a big thing. – [Student] Oh yeah, very good, thank you.

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