Ed Boyden http://edboyden.org/
Engineering revolutions and de-risking biology
EA Global 2016
Alright, so with that, Professor Ed Boyden is a professor of biological engineering and brain and cognitie sciences at MIT Media Lab. He leads the Synthetic Neurobiology group which develops tools for analyzing and repairing complex systems such as the brain. These technologies which are often created in interdisciplinary collaborations includes expansion microscopy, optogenetic tools which enable the activation and silencing of neural activity with light, and optical and nanorobotic interfaces for reporting and control of neural dynamics. He has launched an award-winning series of classes that teach the basic principles of neuroegineering, including strategies for launching companies in the nascent neuroscience space. He has given over 300 invited talks. Please join me in welcoming Ed Boyden.
Alright, well thank you for the invitation and very kind introduction. I direct a group at MIT Media Lab that's trying to figure out how can we de-risk our approaches to curing diseases. We all would like to end diseases and unnecessary suffering. It's a complex problem and we often don't know where to begin. There's a whole class of diseases that for all practical purposes have become considered intractable. These includes various kinds of cancers, brain diseases, autoimmune disorders, diseases of aging and development, and so on, amongst many others.
Let's just pick brain disorders, which is one of the many areas that my group focuses on. Perhaps a billion people around the world have experienced some kind of brain disorder, including Alzheimer's, parkinsons, or chronic pain. These can effect our time to live but also how we live, including how we interact with our loved ones. What can we do about these? Well it turns out that treatments for brain disease have so far been somewhat grim.
This was a 2010 article, and the numbers are I think even worse now, but if you try to develop a therapy for treating a brain disorder, the failure rate is very high. That is, the failure rate if you get the treatment out of the lab and into the clinic it's over 90% failure rate. The cost is enormous. These are 2010 numbers. Almost $900 million dollars. I think most recent numbers have been in the few billion range. And to top it off, the treatments often don't work very well. So this is a worrisome state of affairs.
It turns out that similarly pessimistic numbers hold for many areas of disease that I have mentioned, such as diseases of the immune system, endocrine system, the heart, and so forth. It's been very difficult to get new effective therapies out there. And part of the problem is that these are all diseases that are of incredibly complex body systems that we often don't understand many things about. If you look at the brain, the amount of complexity is enormous. We don't even know all the types of cells that are in the brain. It seems that new cells are discovered every few weeks.
If you were to zoom into the brain, you would find incredibly complex circuitry-- cubic millimeters of your brains would have 100s of thousads of cells connected to each other with a billion connections between them. If you ould zoom into those cells, you would find thousands and thousands of biomolecules, different proteins, different products of the genome and genes that are orchestrated in many different complex patterns which of course we don't yet know. So one of the big questions is that if we want to understand how to tackle these diseases, could we de-risk this process of curing or treating this disease, by having better knowledge or groud-truht knowledge of the composition of the body in that disease state?
Therapies begin with an educated guess. A hypothesis. If the genome has 30,000 genes, and hundreds of thousands of different kinds of biomolecules, a gien guess-- say you build a drug that binds to one of those molecules, is of course a very tiny space out of the entire possibilities. So one question is, how do you maximize the chance of that educated guess or hypothesis is actually true? If you have 10s of thousands of genes, and hundreds of thousands of gene products, what are the chances that your hypothesis that one drug that you built that binds to one target is the very best or even works at all? The chances are very very tiny.
So one might observe that this is a very luck-driven endeavour. You have to have a hypothesis. You have to get that correct. Perhaps not surprisingly, it's become difficult enough that in some areas of biology and medicine that some people have given up on finding such treatments. People have noticed that in for example in the realm of brain disorders that many pharmaceutical companies have been retracting their interest and moving into areas that they think are more sure-fire. My colleague at MIT, finance professor Andrew Lo, published about a year ago a series of studies where he talked about given the risk of developing a new treatment for a disease like Alzheimer's disease, which has a low chance of success, that he actually sees there being a lack of interest in the industry going after that, which is not the right direction that we want to be moving in.
So the question really is then, how do we turn the development of new medicines less of a luck-driven process, but rather more of a skill-driven process? There's so many fields of engineering where you can have an idea, and then you can go implement it in a predictable way with a finite amount of time and you can go make it work. In medicine though, you often see where a drug will be developed but at a certain stage in clinical trials it will be revealed to not be effective, or have daunting side-effects that make it unpractical to deploy.
The transition from luck to skill has happened in other disciplines. In the 20th century there were so many technological triumphs-- like internet, computers, lasers, all sorts of ways of traveling, even landing on the moon as a famous example. The 20th century seems very successful technologically, whereas in the 21st century we don't seem to be doing so well. And I would hypothesize or put fort hthat one one of the reasons why the 20th century technologies were so successful and reliable is that they were built on well-understood physical and scientific principles. If you look at the laws of physics, there's only so many laws, you could fit them on a single page if you want. Quantum dynamics, the laws of electrodynamics and gravity, and the laws of electromagnetism, you could actually build off of them very reliably. It's not like you're going to have a problem where the science goes suddenly wrong. Now, don't get me wrong, there's still a lot of risk in engineering and deployment and realization. But the science risk is relatively low. Contrast that to the science risk of biology and medicine. There are so many different building blocks, biomolecules, nanoscale in dimension and organized in nanoscale precision; that one could make a hypothesis, try to take it to clinic and yet still have high science risk throughout the entire process.
Well, one question then is whether there is a way to reduce the science risk. And of course, if you don't reduce the science risk, then the kinds of technology we're talking about, like landing on the moon and the internet, would not have happened. As a thought experiment, try to imagine landing on the moon 500 years ago before we understood gravity, calculus and all the you know the properties of aerodynamics like rocketry in support. You might find people tying kites to chairs or trying to fly hot air balloons into outer space. If you think about it, all the financial resources on the planet 500 years ago would not have got you anywhere near the moon.
One of the big questions is how do we accelerate the process of deriving the laws of biology and the laws of medicine? How do we look at those building blocks that are present in brain cells, cancer cells and so forth? And understand how they are configured so that we can build more targeted therapies, that go to the target and not interfere with everyday life.
I would postulate that one of the reasons we need to think about this problem is that we need new tools. It's not for lack of trying to find fundamental laws of biology in medicine, but that we're limited by technology. If you look at this microscope here in this slide, we're limited by looking at tiny things and understanding how life is configured. And how the building blocks of cells and organs are organized is really critical. Microscopes are limited. You can't see down to the individual molecules and see the receptors and molecules that are transmitting from cell to cell that are thought to be so important for the operation of the brain and the body, and that go awry in brain disorders and other clinical pathologies.
Well, one question then is: can we build the right kind of tools? Can we accelerate technology development? And those technologies would ideally give us ground-truth understandings of the configurations of complex biological systems. From those maps of biology, one could then go and develop new targeted therapies and in this way you might turn biology and medicine into more mature engineering sciences.
That's the hypothesis that we are trying to put forth for how one might de-risk medicine and for how one might make it easier to develop new successful therapies and treatments and maybe even cures. So this is an exciting time. I think this kind of agenda is starting to really take place in many labs around the world. Can we build tools that get down to the fundamental building blocks of life?
To illustrate this, I would like to show off one of the technologies that my group has been working on, which is to see if we could image cells or tissues or organs down to single-molecule precision. What I have here is a schematic of a polymer. And what we're going to try to do is use this polymer to physically move apart the molecules of preserved tissues, such as cancer biopsies and brain circuits. If we could move the molecules apart, and make room around them, then perhaps we can tell them apart by attaching barcodes to identify the different cells. This would give identity to the components.
The core idea here goes back to a half-century ago. The idea is responsive polymers. These are the kinds of polymers you find in diapers. If you add water, the tiny fiber chains will absorb water and the molecules will move apart from each other. When you add a liquid to baby diapers, the material inside is absorbing water and the polymer inside the material are moving apart. What if we could do this to a biological specimen, to push apart the biomolecules in a cancer biopsy or brain circuit? We need to install those polymers that swell into the tissue sample somehow, either through external addition of the polymers or genetic encoding of the relevant polymers.
Here's the idea that we've been pursuing. You can take, we've zoomed into a cell in this artistic rendering. Each of the brown blobs are biomolecules. We are attaching little handles or anchors, shown in purple here, to each biomolecule. Maybe you could use each handle to pull these apart from each other. We can't dump polymers on top of each particle; so we need to use the monomers and form long chains that wind around and between biomolecules and sometimes it will encounter the handles and now we've attached the biomolecule to the swellable polymer. The final step is to loosen up the biomolecules from each other, so that they are no longer bound to each other. Then we add water, so that the polymers swell, and then the molecules move apart. And then you can image the particles on conventional microscopes. There's lots of room around these biomolecules. You can move in color codes or barcodes to help you understand which molecules are which. You can do this to map molecules in cancer. You can think of this tech as if you are drawing a picture on a balloon as you blow up the balloon; it's the same thing but does it work for cells?
You might be wondering hey that sounds cool in theory but does it work. So we've made a little timeline of this video here. This is a small piece of brain tissue, preserved of course. This is the polymer already. We're going to add water. This is a video that is sped-up by about 60x. You can see this piece of grain growing between your very eyes, until it gets to the point where you can take a picture of the fine structures within with inexpensive optics.
What this lets you do is take this technology and apply it to brain tissue samples related to memory, involed in say Alzheimer's disease, which corrupt these structures. What we're trying to do is obtain these tissue samples, and we try to get tissue from tissue banks in some cases; and we can swell these tissues to the point where we can see the structures and connections between cells and understand the changes that might allow us to develop therapeutic targets that might help us treat brain disorders.
Here's a human breast cancer sample, in collaboration with a group at Harvard. We're also trying to look at tumors. If you can blow up a tumor until you can inspect the molecular composition inside, then you could build drugs that go for those molecules and only those molecules, and do targeted destruction of tumors in the body. The practice of blowing up tissues has helped other groups at Harvard, to blow up bacteria big enough to the point where they can take pictures using modified cameras of commercially-available webcams. Imagine taking pictures of bacteria or other pathogens where you take a picture with cell phone cameras and you might be able to bring diagnostics into a very inexpensive and productive realm to be deployed in the field.
Taking a step back for a moment, what does this convey and where does this leave us? Well, I hope I conveyed a few important messages today. Number one, there's so much going on in the body, so many kind sof molecules, that we really need to lower the risk of developing new therapeutics. The risk is too high, and people and companies are actually leaving the development of therapeutics, which I think presents us with a moral imperative to figure out how to make the risk lower. Number two, if we look at history, we can see that it is possible to take a risky science and make it into a low-risk science. You have to get down to the ground-truth, the fundamental building blocks of the system, how do they interact, and the methods of mapping this interaction perhaps through expansion microscopy we can begin to reduce the surface space for creating new theraapetucis for "intractable" disease. We also need new technology. Through new tools, we can accelerate the basic science of understanding the mechanisms of disease and life.
Thank you very your time and I'm happy to brainstorm with you about ways to de-risk the medical enterprise.
Q: You mentioned the goal of finding and understanding the laws of biology and perhaps even the laws of medicine, perhaps analogous to the laws of physics. Do we have good reason to think there are laws of biology? Can we fit them on to a piece of paper?
A: Since we haven't built the tools to understand all the biological mechanisms, it's hard to know the answer to that. I think biology will be too complex to fit on a single piece of paper. I think we're going to need software to help us comprehend all the details of biology. Right now you see a new set of endeavors where people are trying to make models of cells. There are too many moving parts to keep in your head. Maybe we need better software structures and software programs to help us understand and figure out the most important processes in a cell. Suppose that you could expand a cell, barcode those molecules like I showed earlier in the talk, and now we can try to make a computer model of the processes that occur. This is a futuristic vision that might take many years to realize, but then you could then maybe run experiments on the simulated cell; what happens if you perturb this biomolecular pathway, and then you would realize it impacts some downstream process. It's not enough to map the biomolecules, you also have to understand and map their functions. In a high-throughput way, could you screen using different assays to figure out what different gene products do?
Q: Sounds like this could be in the direction of engineering or it could more turn into weather where there's a lot of noise in the system that you can't see beyond a few days out, even if you have broad trends, but 17 days from now, who could say. Do you have worry about fundamental noise in the system to frustrate the efforts to get to laws?
A: Anothe rgreat question. It's true that these complex systems will always be effected by noise. Simulations are hard to predict beyond a certain point. However, if we look for common structures, in some ways, there are diseases that have convergent phenotypes. There are 100s of different mutations and causes that converge on a single genetic pathway. If I have schizophrenia or autism or something, there are many potential causes, but there's usually final pathways that they converge on, and perhaps there would be specific switches to turn that off.
Q: It has been recently in the news that there was a bug found in a common open-source fMRI package and it has called into question a huge amount of research. Any thoughts or reassurances or anything?
A: It highlights the importance of understanding our tools. If we have a new tool, we try to get it into everyone's hands as much as possible. We want constructive criticism. We started an expansion microscopy startup. We are trying to send kits and get feedback. We're trying to understand the constraints. I think it's important that technologies be understandable. There's a real burden of proof on technology innovators to not only make the technology available, but also understandable. This can be difficult, but I think this can be achieved. At MIT, we try to convince visitors to run experiments with us. We're launching an initiative at the campus near DC in collaboration with Erik Begseg's group to teach a couple dozen people to teach them these tools and maybe get feedback, that for certain clinical contexts perhaps there are some differences needed.
Q: For comprehensibility, in the talk you showed animations and maybe that was an artist's rendering of molecules coming into place... and it struck me that they look like lego blocks. I realized I had no idea how realistic that was. Are they lego blocks that snap together and hold together? Or is that a crude understanding that I should discard?
A: To be honest, we don't really know what life looks like at that scale. We know the structure of proteins because of x-ray and cryo crystallography. Cells have millions of molecules. With our expansion microscopy, we are hoping to see the structures in cells, and whether they are stereotyped between cells, or whether they are idiosyncratic between cells. Honestly we don't hae enough data yet.
Q: Have we learned anything about cell structure from this expansion technique that has been surprising or particularly interesting so far?
A: The technology is a little new. Last year we published. In July of this year we published showing how to do this in simple form. Already investigators are looking at tumor samples and bacterial samples and brain circuits. One of the areas we are looking at is whether tumor expansion works, and whether there are pre-expansion similarities between tumors and then after expansion whether there is still similarity or not. In brain circuits, we look at proteins on both sides of a connection. We can already see patterns where some synapses have distributions of proteins that are close, while others have proteins that are far apart. Are they reserving the machinery for later usage, like when memory is expressed then it's activated perhaps? Well we can start to be more exploratory about the technology of life.
Q: To me, it sounds like you're pulling things apart and indeed physically that is what it is, but also trying to look and understand at specific things. An audience question was, do you think machine learning has a role to play? Can you throw the data into a black box and have it tell you instead of you looking one on one?
A: Oh absolutely. The sheer quantity of data and also the diversity of kinds of things you see in these biological datasets will indeed benefit from machine learning. Our group has been more molecular for years, but we're dipping our toes in this area now. Suppose we want to classify the expanded views of the different diseases, and we find out that one disease was actually ten different types. Another exxample is seeing these nanostructures as they are configured in 3d space-- do we find common motifs? If they are all randomly organized, it will be disappointing but good to know. We might be able to mine out patterns about how these proteins are organized, and some might be pathological. There are so many diseases where proteins aggregate. In Alzheimer's we hae the plaques; huntingon's diseases, parkinson's and so on. Is there something causing the proteins to form these structures? We don't really know. In all of these diseases, some cells are more effected than others. This might be a clue that some cells might have precipitating factors that others don't. If ew could figure this out, it might be helpful. In ALS, some neurons are okay, such as the ones that move our eyes, and this might help us figure out the changes at the cellular level.
Q: Perhaps the last question for those who want to explore your fundamental motiation, for de-risking progress, what areas would you recommend looking into?
A: I'm very interested in the question of how do we build new tools that help us get down to the ground truths of biology. In Kevin's talk, we heard about CRISPR. I think biology is very technology driven, and they are coming from many different areas of science and engineering. CRISPR came from studies of very basic bacterial processes that at the beginning we might not have had any hope of .. at any practical level. The polymers for water expansion-- that goes back to basic chemistry from last century. Can we connect dots across different disciplines to help catalyze this and help us build tools and figure out the fundamental details of biology? It's a bit of an art form to build people together and build tech.
Q: So you have to be deep in one area, and make connections between people.
A: A lot of the transformative technologies that have revolutionized our understanding of biology often come from obscure parts of science. The green fluorescent protein used in I don't know a million studies now, those came from studies of jellyfish. CRISPR came form bacteria. A technology that our group used to do much more, optogenetics, came from studies of microbes that came from very high salt concentration environments. I think we need to connect the dots between these areas of technologies. You have to stumble across the dots and then have the wisdom to realize that something interesting is happening. This is a role that I hope to play some humble role to contribute to in the years to come, to connect scientists together in interesting ways.
Q: You are off to an amazing start. Thank you very much.
A: Thank you.