There has been some serious progress in the last few years on full functional imaging of the C. elegans nervous system (at the necessary spatial and temporal resolutions and ranges).
However, despite this I haven’t been able to find any publications yet where full functional imaging is combined with controlled cellular-scale stimulation (e.g. as I proposed via two-photon excitation of optogenetic channels), which I believe is necessary for inference of a functional model.
I was certainly overconfident about how easy Nemaload would be, especially given the microscopy and ML capabilities of 2012, but moreso I was overconfident that people would continue to work on it. I think there was very little work toward the goal of a nematode-upload machine for the four years from 2014 through 2017. Once or twice an undergrad doing a summer internship at the Boyden lab would look into it for a month, and my sense is that accounted for something like 3-8% of the total global effort.
I can’t say for sure why Boyden or others didn’t assign grad students or postdocs to a Nemaload-like direction; I wasn’t involved at that time, there are many potential explanations, and it’s hard to distinguish limiting/bottleneck or causal factors from ancillary or dependent factors.
That said, here’s my best explanation. There are a few factors for a life-science project that make it a good candidate for a career academic to invest full-time effort in:
The project only requires advancing the state of the art in one sub-sub-field (specifically the one in which the academic specializes).
If the state of the art is advanced in this one particular way, the chances are very high of a “scientifically meaningful” result, i.e. it would immediately yield a new interesting explanation (or strong evidence for an existing controversial explanation) about some particular natural phenomenon, rather than just technological capabilities. Or, failing that, at least it would make a good “methods paper”, i.e. establishing a new, well-characterized, reproducible tool which many other scientists can immediately see is directly helpful for the kind of “scientifically meaningful” experiments they already do or know they want to do.
It is easy to convince people that your project is plausibly on a critical path in the roadmap towards one of the massive medical challenges that ultimately motivate most life-science funding, such as finding more effective treatments for Alzheimer’s, accelerating the vaccine pipeline, preventing heart disease, etc.
The more of these factors are present, the more likely your effort as an academic will lead to career advancement and recognition. Nemaload unfortunately scored quite poorly on all three counts, at least until recently:
(1) It required advancing the state-of-the-art in, at least: C. elegans genetic engineering, electro-optical system integration, computer vision, quantitative structural neuroanatomy of C. elegans, mathematical modeling, and automated experimental design.
(2) Even the final goal of Nemaload (uploading worms who’ve learned different behaviors and showing that the behaviors are reproduced in simulations) is barely “scientifically meaningful”. All it would demonstrate scientifically (as opposed to technically) is that learned behaviors are encoded in some way in neural dynamics. This hypothesis is at the same time widely accepted and extremely difficult to convince skeptics of. Of course, studying the uploaded dynamics might yield fascinating insights into how nature designs minds, but it also might be pretty black-boxy and inexplicable without advancing the state of the art in yet further ways.
(2b) Worse, partial progress is even less scientifically meaningful, e.g. “here’s a time-series of half the neurons, I guess we can do unsupervised clustering on it, oh look at that, the neural activity pattern can predict whether the worm is searching for food or not, as can, you know, looking at it.” To get an upload, you need all the components of the uploading machine, and you need them all to work at full spec. And partial progress doesn’t make a great methods paper either, for the following reason. Any particular experiment that worm neuroscientists want to do, they can do more cheaply and effectively in other ways, like genetically engineering only the specific neurons they care about for that experiment to fluoresce when they’re active. Even if they’re interested in a lot of neurons, they’re going to average over a population anyway, so they can just look at a handful of neurons at a time. And they also don’t mind doing all kinds of unnatural things to the worms like microfluidic immobilization to make the experiment easier, even though that makes the worms’ overall mental-state very, shall we say, perturbed, because they’re just trying to probe one neural circuit at a time, not to get a holistic view of all behaviors across the whole mental-state-space.
(3) The worm nervous system is in most ways about as far as you can get from a human nervous system while still being made of neural cells. C. elegans is not the model organism of choice for any human neurological disorder. Further, the specific technical problems and solutions are obviously not going to generalize to any creature with a bony skull, or with billions of neurons. So what’s the point? It’s a bit like sending a lander to the Moon when you’re trying to get to Alpha Centauri. There are some basic principles of celestial mechanics and competencies of system design and integration that will probably mostly generalize, and you have to start acquiring those with feedback from attempting easier missions. Others may argue that Nemaload on a roadmap to any science on mammals (let alone interventions on humans) is more like climbing a tree when you’re trying to get to the Moon. It’s hard to defend against this line of attack.
If a project has one or two of these factors but not all three, then if you’re an ambitious postdoc with a good CV already in a famous lab, you might go for it. But if it has none, it’s not good for your academic career, and if you don’t realize that, your advisor has a duty of care to guide you towards something more likely to keep your trajectory on track. Advisors don’t owe the same duty of care to summer undergrads.
Adam Marblestone might have more insight on this question; he was at the Boyden lab in that time. It also seems like the kind of phenomenon that Alexey Guzey likes to try to explain.
For point 2, is it possible to use the system to make advance in computer ai through studying the impact of large modifications of the connectome or the synapses in silicon instead of in vivo for getting eeg equivalent? Of course, I understand the system might have to virtually sleep from time to time unlike the pure mathematical matrix based probability current systems.
This would be the matter of making the simulation more debuggable instead of only being able to study muscles according to input (senses).
Also, isn t the whole project making some completely wrong assumptions? I heard about the ideas that neurons don t make synapses on their own and that astrocytes instead of just being support cells is acting like sculptors on their sculptures with research having focused on neurons mainly because eeg detectability. And to support this, that it is the underlying reasons different species with similar numbers neurons shows smaller or larger connectomes and they are research that claimed to have improved the number of synapses per neurons and memorisations capabilties of rodents (compared to those without) by introducing genes controlling the astrocytes of primates (thus I recognise this theory is left uninvestigated for protostomes and their neuroglia instead of the full fledged astroglia of vertebrates).
Having results with completely wrong assumptions doesn t means it doesn t works. For example, geocentric models were good enough to predict the position of planets like Jupiter during the medieval time but later inadequate and hence the need to shift to simpler heliocentric models. Getting all clinical trials on Alzheimer of the past 25 years failing or performing poorly in humans might suggest we are completely wrong on the inner workings of brains somewere.
As an undergraduate student, please correct me if I said garbage.
I got initial funding from Larry Page on the order of 10^4 USD and then funding from Peter Thiel on the order of 10^5 USD. The full budget for completing the Nemaload project was 10^6 USD, and Thiel lost interest in seeing it through.
I might have time for some more comments later, but here’s a few quick points (as replies):
There has been some serious progress in the last few years on full functional imaging of the C. elegans nervous system (at the necessary spatial and temporal resolutions and ranges).
A good summary of the state of play as of late 2020 can be found in this opinion article: https://www.sciencedirect.com/science/article/pii/S0959438820301689
State-of-the-art work is currently happening in Shanghai, Hefei, Wuhan, and Beijing. See https://doi.org/10.1002/cyto.a.24483 and https://arxiv.org/pdf/2109.10474.pdf
However, despite this I haven’t been able to find any publications yet where full functional imaging is combined with controlled cellular-scale stimulation (e.g. as I proposed via two-photon excitation of optogenetic channels), which I believe is necessary for inference of a functional model.
I was certainly overconfident about how easy Nemaload would be, especially given the microscopy and ML capabilities of 2012, but moreso I was overconfident that people would continue to work on it. I think there was very little work toward the goal of a nematode-upload machine for the four years from 2014 through 2017. Once or twice an undergrad doing a summer internship at the Boyden lab would look into it for a month, and my sense is that accounted for something like 3-8% of the total global effort.
Why there was not a postdoc or a PhD hired for doing this work? Was it due to the lack of funding?
I can’t say for sure why Boyden or others didn’t assign grad students or postdocs to a Nemaload-like direction; I wasn’t involved at that time, there are many potential explanations, and it’s hard to distinguish limiting/bottleneck or causal factors from ancillary or dependent factors.
That said, here’s my best explanation. There are a few factors for a life-science project that make it a good candidate for a career academic to invest full-time effort in:
The project only requires advancing the state of the art in one sub-sub-field (specifically the one in which the academic specializes).
If the state of the art is advanced in this one particular way, the chances are very high of a “scientifically meaningful” result, i.e. it would immediately yield a new interesting explanation (or strong evidence for an existing controversial explanation) about some particular natural phenomenon, rather than just technological capabilities. Or, failing that, at least it would make a good “methods paper”, i.e. establishing a new, well-characterized, reproducible tool which many other scientists can immediately see is directly helpful for the kind of “scientifically meaningful” experiments they already do or know they want to do.
It is easy to convince people that your project is plausibly on a critical path in the roadmap towards one of the massive medical challenges that ultimately motivate most life-science funding, such as finding more effective treatments for Alzheimer’s, accelerating the vaccine pipeline, preventing heart disease, etc.
The more of these factors are present, the more likely your effort as an academic will lead to career advancement and recognition. Nemaload unfortunately scored quite poorly on all three counts, at least until recently:
(1) It required advancing the state-of-the-art in, at least: C. elegans genetic engineering, electro-optical system integration, computer vision, quantitative structural neuroanatomy of C. elegans, mathematical modeling, and automated experimental design.
(2) Even the final goal of Nemaload (uploading worms who’ve learned different behaviors and showing that the behaviors are reproduced in simulations) is barely “scientifically meaningful”. All it would demonstrate scientifically (as opposed to technically) is that learned behaviors are encoded in some way in neural dynamics. This hypothesis is at the same time widely accepted and extremely difficult to convince skeptics of. Of course, studying the uploaded dynamics might yield fascinating insights into how nature designs minds, but it also might be pretty black-boxy and inexplicable without advancing the state of the art in yet further ways.
(2b) Worse, partial progress is even less scientifically meaningful, e.g. “here’s a time-series of half the neurons, I guess we can do unsupervised clustering on it, oh look at that, the neural activity pattern can predict whether the worm is searching for food or not, as can, you know, looking at it.” To get an upload, you need all the components of the uploading machine, and you need them all to work at full spec. And partial progress doesn’t make a great methods paper either, for the following reason. Any particular experiment that worm neuroscientists want to do, they can do more cheaply and effectively in other ways, like genetically engineering only the specific neurons they care about for that experiment to fluoresce when they’re active. Even if they’re interested in a lot of neurons, they’re going to average over a population anyway, so they can just look at a handful of neurons at a time. And they also don’t mind doing all kinds of unnatural things to the worms like microfluidic immobilization to make the experiment easier, even though that makes the worms’ overall mental-state very, shall we say, perturbed, because they’re just trying to probe one neural circuit at a time, not to get a holistic view of all behaviors across the whole mental-state-space.
(3) The worm nervous system is in most ways about as far as you can get from a human nervous system while still being made of neural cells. C. elegans is not the model organism of choice for any human neurological disorder. Further, the specific technical problems and solutions are obviously not going to generalize to any creature with a bony skull, or with billions of neurons. So what’s the point? It’s a bit like sending a lander to the Moon when you’re trying to get to Alpha Centauri. There are some basic principles of celestial mechanics and competencies of system design and integration that will probably mostly generalize, and you have to start acquiring those with feedback from attempting easier missions. Others may argue that Nemaload on a roadmap to any science on mammals (let alone interventions on humans) is more like climbing a tree when you’re trying to get to the Moon. It’s hard to defend against this line of attack.
If a project has one or two of these factors but not all three, then if you’re an ambitious postdoc with a good CV already in a famous lab, you might go for it. But if it has none, it’s not good for your academic career, and if you don’t realize that, your advisor has a duty of care to guide you towards something more likely to keep your trajectory on track. Advisors don’t owe the same duty of care to summer undergrads.
Adam Marblestone might have more insight on this question; he was at the Boyden lab in that time. It also seems like the kind of phenomenon that Alexey Guzey likes to try to explain.
Note, (1) is less bad now, post-2018-ish. And there are ways around (2b) if you’re determined enough. Michael Skuhersky is a PhD student in the Boyden lab who is explicitly working in this direction as of 2020. You can find some of his partial progress here https://www.biorxiv.org/content/biorxiv/early/2021/06/10/2021.06.09.447813.full.pdf and comments from him and Adam Marblestone over on Twitter, here: https://twitter.com/AdamMarblestone/status/1445749314614005760
For point 2, is it possible to use the system to make advance in computer ai through studying the impact of large modifications of the connectome or the synapses in silicon instead of in vivo for getting eeg equivalent? Of course, I understand the system might have to virtually sleep from time to time unlike the pure mathematical matrix based probability current systems.
This would be the matter of making the simulation more debuggable instead of only being able to study muscles according to input (senses).
Also, isn t the whole project making some completely wrong assumptions? I heard about the ideas that neurons don t make synapses on their own and that astrocytes instead of just being support cells is acting like sculptors on their sculptures with research having focused on neurons mainly because eeg detectability. And to support this, that it is the underlying reasons different species with similar numbers neurons shows smaller or larger connectomes and they are research that claimed to have improved the number of synapses per neurons and memorisations capabilties of rodents (compared to those without) by introducing genes controlling the astrocytes of primates (thus I recognise this theory is left uninvestigated for protostomes and their neuroglia instead of the full fledged astroglia of vertebrates).
Of course, this would had even more difficulty to the project https://www.frontiersin.org/articles/10.3389/fcell.2022.931311/full.
Having results with completely wrong assumptions doesn t means it doesn t works. For example, geocentric models were good enough to predict the position of planets like Jupiter during the medieval time but later inadequate and hence the need to shift to simpler heliocentric models. Getting all clinical trials on Alzheimer of the past 25 years failing or performing poorly in humans might suggest we are completely wrong on the inner workings of brains somewere.
As an undergraduate student, please correct me if I said garbage.
I got initial funding from Larry Page on the order of 10^4 USD and then funding from Peter Thiel on the order of 10^5 USD. The full budget for completing the Nemaload project was 10^6 USD, and Thiel lost interest in seeing it through.
Do you know why they lost interest? Assuming their funding decision were well thought out, it might be interesting.