[A paper that I had already written about has been published in PLoS Computational Biology about half a year after its preprint was up on on bioRxiv, and it has been making the rounds again in social media and amongst scientist circles. The paper I'm referring to is, "Could a neuroscientist understand a microprocessor?" I had written a longer treatment of it in an email that was more elaborate than my previous blog post, so I am converting it to blog format and posting here as a "continuation" of sorts of my previous post.]
The paper is quite the shocker, to put it bluntly. I think most neuroscientists quaked in their boots when they read this because it directly and effectively criticizes most of the approaches we use that we think are helping us with "understanding" the brain. This is a paper with primarily philosophical and methodological implications. It cleverly (and deviously!) uses "standard" neuroscience tools or, more precisely, signal processing and statistical tools (spectral analysis, Granger causality, dimensional reduction, etc.) on a microprocessor to generate data that is strikingly similar to what we see when we apply these techniques to neural tissue (power law, oscillations, transistor tuning curves, etc). And yet, the brain is obviously not a microprocessor, not even close. So what kind of understanding can these tools alone give us if they basically can't distinguish between two strikingly different structures of high complexity? The authors say "not much", and it's really, really hard to avoid agreeing with them after reading the paper. :)
The blow is softened for those researchers who, from the very beginning, emphasize that it's not good enough to build a model just for the sake of building a model, but rather to ask why we're building it, i.e., to answer a specific biological question. Answering a specific question means that we end up thinking about functional relevance a lot. So it's not enough to just measure power spectra and so on, we have to link it to biological function. I think the authors of the paper tacitly acknowledge this kind of more "sophisticated" approach by contrasting it with, as they put it, "naive" uses of standard neuroscience tools. This relates to the Aristotelian "four causes" (especially the final cause), but I think the authors of the paper would probably argue that even finding a formal cause is not good enough, and moreover that a final cause has important overlooked dependencies that make it particularly difficult to obtain.
The most important of these dependencies in my mind is knowing inputs and outputs to the system, because the evolutionary inputs and outputs are really what drives the development of an organism and its nervous system in the first place. And this is where we are sorely lacking in neuroscience. The section in the paper titled "What does it mean to understand a system" goes into this a little bit, as well as in the discussion towards the end, where they say, "In the case of the processor, we really understand how it works. ... for each of these modules we know how its outputs depend on its inputs." Now I think the authors could have made a much stronger case for neuroscientists to focus on getting more information on inputs (e.g., the pattern of synaptic inputs in a specific in vivo behavioural context) and outputs (what is the specific efferent fiber activity, on a per axonal basis, from a system in a specific in vivo behavioural context). Because once you have that, the way the inputs are transformed into outputs (on a per-brain system level) might almost easily "fall out" since you'll just be able to observe them, after which point you can generate a theory to account for the general case.
This is incidentally why comparative neuroscience is so appealing, because there, more than anywhere else, we have some hope of actually mapping out inputs and outputs. If you have "only" a few thousand cells in an invertebrate ganglion, you can more or less start characterizing the inputs and outputs. I'll never forget how a former colleague once said that when he felt depressed about the state of neuroscience he would go take a look at the invertebrate posters at SfN to be reinvigorated, and I've since then always taken this advice myself.
But even here the task becomes monumentally complex. Here's a particular favourite comparative neuro paper of mine, titled "In Search of the Engram in the Honeybee Brain" (published as a book chapter).
One of the key arguments of the paper is that the memory engram is not just something found in the "memory region" of the brain, but rather a product of the entire nervous system of the organism, from sensory to motor representations. You can demonstrate this quite directly in the bee since these pathways are much more completely characterized than in mammals. But even with mammals we are starting to learn (or be reminded of), for example, the mass of extrinsic connections between hippocampus and all sorts of brain regions that we wouldn't typically think of when we consider "cognitive" spatial and semantic maps - these include the amygdala, nucleus accumbens, even olfactory bulb for god's sake (see almost any of James McClelland's works for perspectives on this, as well as more recently Strange et al 2014, "Functional organization of the hippocampal longitudinal axis", Nature).
Yet if the results in the bee hold true as a general principle of nervous system function, it means that we will have to understand how each and every one of these regions generate information flow into, and out of, the hippocampus, before we can truly and fully "understand" how the hippocampus works. Slowly we're moving in that direction, with the hippocampal field becoming more aware of longitudinal differences and how dorsal hippocampus is more involved in spatial memory whereas the ventral is more implicated in emotional and fear processing (after many years of neglecting some of the early studies that hinted at this way back). This even brings up the question of whether the hippocampus is even one unified structure or rather a system of somewhat loosely coupled modules pivoting around a dorsal and ventral pole, as the gene expression studies might suggest (Bloss et al 2016 from Spruston's lab) that is nevertheless bound together, as the theta travelling waves studies suggest (e.g. Patel et al 2012 from Buzsaki's lab). In which case, even talking about studying "the hippocampus" is not correct anymore, since someone could then ask "Which hippocampus?" or "Which hippocampal module?"
To get back on point, perhaps the most important missing piece of info then is the pattern of inputs and outputs to any brain region, crucially as measured in an actual behavioural state. The authors of the Jonas and Kording "microprocessor paper" make two brief mentions of efforts where this is taking place, and interestingly enough both are in neuroengineering. One of them is the Berger/Marmarelis hippocampal prosthetic chip (that I'm very familiar with, having followed their work for several years). To me this is an odd work to cite in their section "What does it mean to understand a system" because although they do look at inputs and outputs (which is why they cited it), the work is importantly not setup in any way to actually understand the input/output transformations. In a nutshell, they implant a chip in CA1 with electrodes both near the DG border as well as CA3 (this has been done in rodent and monkey so far). They then place the animal in a specific learning paradigm, such as delayed non-match to sample task. During the delay period (i.e., when the rodent needs to remember what lever was signalled in the sampling phase so that they can push the other one when queried by a light turning on after the delay period is over), they record the pattern of activity seen in both the input and output electrodes. They then take these multunit data and fit the coefficients of the kernels of a set of Volterra series (think of them as Taylor series with built-in historicity or "memory"). Then what they can do is repeat the experiment but inject NMDA blockers locally to CA1. At that point of course the rodent performs terribly. But then if they turn on the chip - i.e., taking the DG inputs (at a very coarse level of course since they only have a few sampling electrodes), feed them through the fitted Volterra series, and then output the corresponding spike trains on the output electrodes, the rodent can recover and perform the task. Amazing! What's scary is that with no NMDA blocker and the chip turned on the rodent performs even better than in control! (So if you've seen any sci-fi movies with augmented humans with superhuman memory etc... it might actually be coming one day!)
Now the catch with this approach is that it treats the CA1 region as a black box! There is no real understanding of the input/output transformations, because they have simply captured the correlation of input to output activity in one behavioural paradigm, i.e., the activity produced by the functioning of the actual CA1. They have not captured the general mechanism for how the CA1 produces these transformations. The proof of this is that the fitted kernel coefficients only work for that specific behavioural task! To this point, one of the PIs, Ted Berger, said (personal communication but perhaps also mentioned in some interviews) that as a general tool for human memory enhancement (e.g., during old age and dementia) they would want to create a set of coefficients for particular useful contexts. So there would be a "kitchen program", a "bathroom program", and so on (kind of like in the Matrix where they would give Neo programs for specific skills like piloting a helicopter and learning different martial arts). This is fine for clinical use, but not enough for understanding the brain of course, since we have yet to realize how the CA1 (and all the other regions involved) perform the input/output mappings in a general way, under any context.
In conclusion, my argument is that the Jonas and Kording "microprocessor" paper ends with too broad of a set of lessons. Everything they conclude with is true taken individually: we need better models in neuroscience, better data analysis methods, etc., but all in all the common point that these share (I assert) is that having a knowledge of input/output patterns is crucial. I actually think we'll be fine since new technologies are making it easier and easier to record single unit activities from very large amounts of neurons at once. The CaMPARI work for instance is one of these new techniques that seem incredibly promising; see e.g., Zolnik et al 2016.
To use the microprocessor analogy again, we already have the tools to analyze large scale activity and response properties of individual units/neurons (the spectral analyses, dimensionality reduction, and all that). But what network-wide neuronal interrogation in behavioural contexts gives us is the exact instructions that are being fed into the microprocessor, as well as the outputs, and this is what will tell us the computation itself. Then how the computation arises will fall out almost inevitably by observing how the input gets transformed into the output. Then we might be able to develop some theories about overall function of that component in question; e.g., in the microprocessor case we could then produce a theory of the ALU (arithmetic logic unit) and describe its function in detail, which is to perform arithmetic operation on a bitwise level, i.e., on the individual bits of the input numbers encoded in base-2. We would then even be able to immediately make inferences for why certain design decisions were made (by evolution in the case of the brain). For instance, the ALU and microprocessors in general use base-2 (rather than base-10) because it's an extremely convenient way of representing numbers that can allow for a wide range of arithmetic operations (addition, subtraction, multiplication) to be performed using minimal operations that entail simply comparing or shifting the bits in one direction or another, so it's easy and efficient to implement in hardware. This is also the kind of inference we'll be able to make once we get a much more complete map of input/output to any brain region. The ultimate test for whether we've understood the brain might then be, as Jonas and Kording state for the microprocessor case, when "many students of electrical engineering would know multiple ways of implementing the same function."
My own take-home from this paper was to reassess how I view my own (very limited) work in the overall sphere of neuroscience, and to reaffirm a commitment to linking neuronal activity with function rather than being satisfied with examining how some measure of neuronal output changes in response to some manipulation, without also having an idea of what it means for the overall system the model is embedded in. To repeat the end of my previous post on this subject which contains a useful analogy (I quite like using analogies to help with thinking things through, what the cognitive scientist Daniel Dennett would call "intuition pumps"):
"This results in a state of affairs in neuroscience (at least systems level) where we are content with scratching the surface, e.g., measure changes in frequencies under different conditions. It's like measuring the spectral signature that the sound of a car's engine makes, and thinking that by comparing the peak power under idle vs driving conditions we are any closer to understanding how the engine works. However, we are actually in a very primitive state of "understanding". We don't know anything about pistons and drivetrains, let alone the principles of internal combustion. Yet it's only by understanding these that we would truly know how a car engine works. The same applies to the brain."
