Since the early 21st century, some transhumanist proponents and futuristic researchers claim that Whole Brain Emulation (WBE) is not merely science fiction - although still hypothetical, it's said to be a potentially viable technology in the near future. Such beliefs attracted significant fanfare in tech communities such as LessWrong.
In 2011 at LessWrong, jefftk did a literature review on the emulation of a worm, C. elegans, as an indicator of WBE research progress.
Because the human brain is so large, and we are so far from having the technical capacity to scan or emulate it, it's difficult to evaluate progress. Some other organisms, however, have much smaller brains: the nematode C. elegans has only 302 cells in its entire nervous system. It is extremely well studied and well understood, having gone through heavy use as a research animal for decades. Since at least 1986 we've known the full neural connectivity of C. elegans, something that would take decades and a huge amount of work to get for humans. At 302 neurons, simulation has been within our computational capacity for at least that long. With 25 years to work on it, shouldn't we be able to 'upload' a nematode by now?
There were three research projects from the 1990s to the 2000s, but all are dead-ends that were unable to reach the full research goals, giving a rather pessimistic vision of WBE. However, immediately after the initial publication of that post, LW readers Stephen Larson (slarson) & David Dalrymple (davidad) pointed out in the comments that they were working on it, the two ongoing new projects of their own made the future look promising again.
The first was the OpenWorm project, coordinated by slarson. Its goal is to create a complete model and simulation of C. elegans, and to release all tools and data as free and open source software. Implementing a structural model of all 302 C. elegans neurons in the NeuroML description language was an early task completed by the project.
The next was another research effort at MIT by davidad. David explained that the OpenWorm project focused on anatomical data from dead worms, but very little data exists from living animals' cells. They can't tell scientists about the relative importance of connections between neurons within the worm's neural system, only that a connection exists.
- The "connectome" of C. elegans is not actually very helpful information for emulating it. Contrary to popular belief, connectomes are not the biological equivalent of circuit schematics. Connectomes are the biological equivalent of what you'd get if you removed all the component symbols from a circuit schematic and left only the wires. Good luck trying to reproduce the original functionality from that data.
- What you actually need is to functionally characterize the system's dynamics by performing thousands of perturbations to individual neurons and recording the results on the network, in a fast feedback loop with a very very good statistical modeling framework which decides what perturbation to try next.
- With optogenetic techniques, we are just at the point where it's not an outrageous proposal to reach for the capability to read and write to anywhere in a living C. elegans nervous system, using a high-throughput automated system. It has some pretty handy properties, like being transparent, essentially clonal, and easily transformed. It also has less handy properties, like being a cylindrical lens, being three-dimensional at all, and having minimal symmetry in its nervous system. However, I am optimistic that all these problems can be overcome by suitably clever optical and computational tricks.
In a year or two, he believed an automated device can be built to gather such data. And he was confident.
I'm a disciple of Kurzweil, and as such I'm prone to putting ridiculously near-future dates on major breakthroughs. In particular, I expect to be finished with C. elegans in 2-3 years. I would be Extremely Surprised, for whatever that's worth, if this is still an open problem in 2020.
When asked by gwern for a statement for PredictionBook.com, davidad said:
- "A complete functional simulation of the C. elegans nervous system will exist on 2014-06-08." 76% confidence
- "A complete functional simulation of the C. elegans nervous system will exist on 2020-01-01." 99.8% confidence
(disappointingly, these statements were not actually recorded on PredictionBook).
Unfortunately, 10 years later, both projects appear to have made no significant progress and failed to develop a working simulation that is able to resemble biological behaviors. In a 2015 CNN interview, slarson said the OpenWorm project was "only 20 to 30 percent of the way towards where we need to get", and seems to be in the development hell forever since. Meanwhile, I was unable to find any breakthrough from davaidad before the project ended. David personally left the project in 2012.
When the initial review was published, there was already 25 years of works on C. elegans, and right now yet another decade has passed, yet we're still unable to "upload" a nematode. Therefore, I have to end my post with the pessimistic vision of WBE by quoting the original post.
This seems like a research area where you have multiple groups working at different universities, trying for a while, and then moving on. None of the simulation projects have gotten very far: their emulations are not complete and have some pieces filled in by guesswork, genetic algorithms, or other artificial sources. I was optimistic about finding successful simulation projects before I started trying to find one, but now that I haven't, my estimate of how hard whole brain emulation would be has gone up significantly. While I wouldn't say whole brain emulation could never happen, this looks to me like it is a very long way out, probably hundreds of years.
This is discouraging.
Closing thoughts: What went wrong? What are the unsolvable difficulties here?
Update
Some technical insights behind the failure was given in a 2014 update ("We Haven't Uploaded Worms"), jefftk showed the major problems are:
- Knowing the connections isn't enough, we also need to know the weights and thresholds. We don't know how to read them from a living worm.
- C. elegans is able to learn by changing the weights. We don't know how weights and thresholds are changed in a living worm.
The best we can do is modeling a generic worm - pretraining and running the neural network with fixed weights. Thus, no worm is "uploaded" because we can't read the weights, and these simulations are far from realistic because they are not capable of learning. Hence, it's merely a boring artificial neural network, not a brain emulation.
To see why this isn't enough, consider that nematodes are capable of learning. [...] For example, nematodes can learn that a certain temperature indicates food, and then seek out that temperature. They don't do this by growing new neurons or connections, they have to be updating their connection weights. All the existing worm simulations treat weights as fixed, which means they can't learn. They also don't read weights off of any individual worm, which means we can't talk about any specific worm as being uploaded.
If this doesn't count as uploading a worm, however, what would? Consider an experiment where someone trains one group of worms to respond to stimulus one way and another group to respond the other way. Both groups are then scanned and simulated on the computer. If the simulated worms responded to simulated stimulus the same way their physical versions had, that would be good progress. Additionally you would want to demonstrate that similar learning was possible in the simulated environment.
Furthermore, in a Quora answer, davidad hinted that his project was discontinued partially due to the lack of funding.
If I'd had $1 million seed, I wouldn't have had to cancel the project when I did...
Conclusion: Relevant neural recording technologies are needed to collect data from living worms, but they remain undeveloped, and the funding simply isn't there.
Update 2
I just realized David actually had an in-depth talk about his work and the encountered difficulties at MIRI's AI Risk for Computer Scientists workshop in 2020, according to this LW post ("AIRCS Workshop: How I failed to be recruited at MIRI").
Most discussions were pretty high level. For example, someone presented a talk where they explained how they tried and failed to model and simulate a brain of C. Elegansis. A worm with an extremely simple and well understood brain. They explained to us a lot of things about biology, and how they had been trying and scanning precisely a brain. If I understood correctly, they told us they failed due to technical constraints and what those were. They believe that, nowadays, we can theoretically create the technology to solve this problem. However there is no one interested in said technology, so it won't be developed and be available to the market.
Does anyone know any additional information? Is the content of that talk available in paper form?
Update 3
Note to the future readers: within a week of the initial publication of this post, I received some helpful insider comments, including David himself, on the status of this field. The followings are especially worth reading.
- David explains why this field was understudied and underfunded in the past 10 years - a main reason of the slow progress.
- it's getting better now. Here's a list of recent works.
- Delton explains recent progress on C. elegans simulations and what happened with the OpenWorm project.
- Especially worth noting: CarbonCopies Foundation did a workshop in June 2021 with Steven Larson on the OpenWorm project. A recording of the 4 hour event is online.
Let's look at a proxy task. "Rockets landing on their tail". The first automated landing of an airliner was in 1964. Using a similar system of guidance signals from antenna on the ground surely a rocket could land after boosting a payload around the same time period. While SpaceX first pulled it off in 2015.
In 1970 if a poorly funded research lab said they would get a rocket to land on its tail by 1980 and in 1980 they had not succeeded, would you update your estimated date of success to "centuries"? C elegans has 302 neurons and it takes, I think I read 10 ANN nodes to mimic the behavior of one biological neuron. With a switching frequency of 1 khz and it's fully connected you would need 302 * 100^2 *1000 operations per second. This is 0.003 TOPs, and embedded cards that do 200-300 TOPs are readily available.
So the computational problem is easy. Did David build an automated device to collect data from living cells? If not, was the reason it wasn't done because of some sudden unexpected huge difficulty that 100+ people and multi-million dollar budget couldn't solve, or was it because...those people weren't there and neither was the funding?
My larger point is that if the '... (read more)
Good points, I did more digging and found some relevant information I initially missed, see "Update". He didn't, and funding was indeed a major factor.
I might have time for some more comments later, but here's a few quick points (as replies):
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 alre
... (read more)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
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.
While we're sitting around waiting for revolutionary imaging technology or whatever, why not try and make progress on the question of how much and what type of information can we obscure about a neural network and still approximately infer meaningful details of that network from behavior. For practice, start with ANNs and keep it simple. Take a smallish network which does something useful, record the outputs as it's doing its thing, then add just enough random noise to the parameters that output deviates noticeably from the original. Now train the perturbed version to match recorded data. What do we get here, did we recover the weights and biases almost exactly? Assuming yes, how far can this go before we might as well have trained the thing from scratch? Assuming success, does it work equally on different types and sizes of networks, if not what kind of scaling laws does this process obey? Assuming some level of success, move on to a harder problem, a sparse network, this time we throw away everything but connectivity information and try to repeat the above. How about something biologically realistic but we try to simulate the spiking neurons with groups of standard artificial ones.. you get the drift.
The tone of strong desirability for progress on WBE in this was surprising to me. The author seems to treat progress in WBE as a highly desirable thing; a perspective I expect most on LW do not endorse.
The lack of progress here may be a quite good thing.
As many other people here, I strongly desire to avoid death. Mind uploading is an efficient way to prevent many causes of death, as it is could make a mind practically indestructible (thanks to backups, distributed computing etc). WBE is a path towards mind uploading, and thus is desirable too.
Mind uploading could help mitigate OR increase the AI X-risk, depending on circumstances and implementation details. And the benefits of uploading as a mitigation tool seem to greatly outweigh the risks.
The most preferable future for me is the future there mind uploading is ubiquitous, while X-risk is avoided.
Although unlikely, it is still possible that mind uploading will emerge sooner than AGI. Such a future is much more desirable than the future without mind uploading (some possible scenarios).
This is so incredibly far from where I would place the equivalence, and I think where almost anyone would place it, that I'm baffled. You really mean this?
Imagine you have two points, A and B. You're at A, and you can see B in the distance. How long will it take you to get to B?
Well, you're a pretty smart fellow. You measure the distance, you calculate your rate of progress, maybe you're extra clever and throw in a factor of safety to account for any irregularities during the trip. And you figure that you'll get to point B in a year or so.
Then you start walking.
And you run into a wall.
Turns out, there's a maze in between you and point B. Huh, you think. Well that's ok, I put a factor of safety into my calculations, so I should be fine. You pick a direction, and you keep walking.
You run into more walls.
You start to panic. You figured this would only take you a year, but you keep running into new walls! At one point, you even realize that the path you've been on is a dead end — it physically can't take you from point A to point B, and all of the time you've spent on your current path has been wasted, forcing you to backtrack to the start.
Fundamentally, this is what I see happening, in various industries: brain scanning, self-driving cars, clean energy, interstellar travel, AI development. The list goes on.
Laymen see a point... (read more)
It seems to me that this task has an unclear goal. Imagine I linked you a github repo and said "this is a 100% accurate and working simulation of the worm." How would you verify that? If we had a WBE of Ray Kurzweil, we could at least say "this emulated brain does/doesn't produce speech that resembles Kurzweil's speech." What can you say about the emulated worm? Does it wiggle in some recognizable way? Does it move towards the scent of food?
Quote jefftk.
(just included the quotation in my post)
A study by Alcor trained C. elegans worms to react to the smell of a chemical. They then demonstrated that the worms retained this memory even after being frozen and revived. Were it possible to upload a worm, the same exact test would show that you had successfully uploaded a worm with that memory vs. one without that memory.
Study here: Persistence of Long-Term Memory in Vitrified and Revived Caenorhabditis elegans
I want to point out that there has been some very small amounts of progress in the last 10 years on the problem of moving from connectome to simulation rather than no progress.
First, there has been interesting work at the JHU Applied Physics Lab which extends what Busbice was trying to do when he tried to run as simulation of c elegans in a Lego Mindstorms robot (by the way, that work by Busbice was very much overhyped by Busbice and in the media, so it's fitting that you didn't mention it). They use a basic integrate and fire model to simulate the n... (read more)
As someone interested in seeing WBE become a reality, I have also been disappointed by the lack of progress. I would like to understand the reasons for this better. So I was interested to read this post, but you seem to be conflating two different things. The difficulty of simulating a worm and the difficulty of uploading a worm. There are a few sentences that hint both are unsolved, but they should be clearly separated.
Uploading a worm requires being able to read the synaptic weights, thresholds, and possibly other details from an individual worm. No... (read more)
One complication glossed over in the discussion (both above and below) is that a single synapse, even at a single point in time, may not be well characterized as a simple "weight". Even without what we might call learning per se, the synaptic efficacy seems, upon closer examination, to be a complicated function of the recent history, as well as the modulatory chemical environment. Characterizing and measuring this is very difficult. It may be more complicated in a C. elegans than in a mammal, since it's such a small but highly optimized hunk of circuitry.
There’s a scan of 1 mm^3 of a human brain, 1.4 petabytes with hundred(s?) of millions of synapses
https://ai.googleblog.com/2021/06/a-browsable-petascale-reconstruction-of.html
Do we at least have some idea of what kind of technology would be needed for reading out connection weights?
This post was a great dive into two topics:
I think this post was good on it's first edition, but became great after the author displayed admirable ability to update their mind and willingness to update their post in light of new information.
Overall I must reluctantly only give this post a +1 vote for inclusion, as I think the books are better served by more general rationality content, but I'm terms of what I would like to see more of on this site, +9. Maybe I'll compromise and give +4.
This is a total nitpick but there is a typo in the title of both this post and the one from jefftk referenced by it. It's "C. elegans", not "C. elgans".
There's a fundamental difficulty with these sorts of attempts to emulate entire nervous systems (which gets exponentially worse as you scale up) that I don't think gets enough attention: failure of averaging. See this paper on simulating single neurons: https://pubmed.ncbi.nlm.nih.gov/11826077/#:~:text=Averaging%20fails%20because%20the%20maximal,does%20not%20contain%20its%20mean.
The abstract:
"Parameters for models of biological systems are often obtained by averaging over experimental results from a number of different preparations. To explore the va... (read more)
Curated. The topic of uploads and whole-brain emulation is a frequent one, and one whose feasibility is always assumed to be true. While this post doesn't argue otherwise, it's fascinating to hear where we're with the technology for this.
Hey,
TL;DR I know a researcher who's going to start studying C. elegans worms in a way that seems interesting as far as I can tell. Should I do something about that?
I'm trying to understand if this is interesting for our community, specifically as a path to brain emulation, which I wonder if could be used to (A) prevent people from dying, and/or (B) creating a relatively-aligned AGI.
This is the most relevant post I found on LW/EA (so far).
I'm hoping someone with more domain expertise can say something like:
- "OMG we should totally extra fund this
... (read more)OpenWorm seems to be a project with realistic goals but unrealistic funding in contrast to the EU's Human Brain Project (HBP): a project with an absurd amount of funding, with absurdly unrealistic goals. Even ignoring the absurd endpoint, any 1billion Euro project should be split up into multiple smaller ones with time to take stock of things in between.
What could the EU have achieved by giving $50million to OpenWorm to spend in 3 years (before getting more ambitious)?
Would it not have done so in the first place because of hubris? The worm is somehow... (read more)
My impression of OpenWorm was that it was not focused on WBE. It tried to be a more general-purpose platform for biological studies. It attracted more attention than a pure WBE project would, by raising vague hopes of also being relevant to goals such as studying Alzheimer's.
My guess is that the breadth of their goals led them to become overwhelmed by complexity.
It's possible to donate to Openworm to accelerate the development, via their website
Maybe the problem is figuring out how to realistically simulate a SINGLE neuron, which could then be extended 302 or 100,000,000,000 times. Also due to shorter generation times any random c.elegans has 50 times more ancestors than any human, so evolution may have had time to make their neurons more complex.
One review criticized my post for being inadequate at world modeling - readers who wish to learn more about predictions are better served by other books and posts (but also praised me for being willing to update its content after new information arrived). I don't disagree, but I felt it was necessary to clarify my background of writing it.
First and foremost, this post was meant specifically as (1) a review of the research progress on Whole Brain Emulation of C. elegans, and (2) a request for more information from the community. I became aware of this resea... (read more)