Monday, February 18, 2013

How Much BAM for the Buck, and Other Thoughts on the Brain Activity Map Project

Today's New York Times reports that the Obama administration is considering a massive, partly government-funded project to map the human brain, the Brain Activity Map (BAM!) Project, inspired by the success of the Human Genome Project.

Let me start by saying that I am all in favor of more research in neuroscience, because there is certainly a lot we don't know about how the brain works. While to outsiders like Ray Kurzweil it may look like progress is coming in leaps and bounds, and backing up the mind's hard drive is therefore a calculable number of years away, from the inside the effort to understand the brain often seems to zigzag from new idea to cool finding to neat technology without a clear forward trajectory. I am also a big fan of George Church, a genius and visionary of molecular biology who is one of the driving forces behind the new plan. (I even once co-taught a course on cognitive genetics at Harvard with George's wife, the geneticist Ting Wu.) But before we all jump on this bandwagon, let's discuss the pros and cons—based on what has been said publicly so far (mainly in the Times article, which was prefigured by a Neuron article by Church and several others published last June).

Per the Times, the project is expected to cost "billions of dollars" and last 10 years. Its goals are to "advance the knowledge of the brain's billions of neurons and gain greater insights into perception, actions, and, ultimately, consciousness." So far, so good—basic science. Some also hope that the project will "develop the technology essential to understanding diseases like Alzheimer's and Parkinson's, as well as to find new therapies for a variety of mental illnesses." That's certainly possible, though I cannot think of any treatments for mental illness or brain disease that have been derived from previous maps of the brain or knowledge of its activity patterns. Perhaps this is just an argument that we need better maps. Finally, "the project holds the potential of paving the way for advances in artificial intelligence." Certainly also possible, but I think AI has been doing pretty well lately by ignoring brain architecture and going with whatever algorithms work on computer hardware to produce intelligent-seeming behavior.

The Times account is short on details of what precisely is being proposed, which has led some people to think that the idea is to map every connection and the firing activity of every neuron in (at least) one human brain, or to make more maps of the functions of brain regions using neuroimaging techniques. But the Neuron article by the Brain Activity Map proponents makes it clear that, last June at least, the idea was to start with small circuits in very small organisms, where it may soon be possible to record from every participating neuron at once, and to work up to larger circuits and larger organisms. All these maps would record "the patterns and sequences of neuronal firing by all neurons" in the relevant circuit or brain, so they would be much more detailed, in both space and time, than any existing databases. A drosophila brain might be done in ten years, a mouse neocortex in fifteen. The entire human brain would be a more distant goal. And of course there would be ethical issues to be surfaced and solved along the way to that ultimate step.

There are a lot of things to like about this ambition. Although we already have lots of maps of the brain, none of them (but one—the structural connectome of the C. elegans worm) approach the spatial resolution of a neuron-by-neuron map. The main source of our knowledge about how neurons represent information, carry out computations, and communicate with other neurons is still the single-cell recording, a technique developed about half a century ago. Such methods are based on inserting tiny electrodes in or near living neurons, and have obvious limitations, not least their inability to scale to full circuits or brain regions. Recording entire circuits in action would be a fantastic achievement and probably would lead to all sorts of ancillary benefits for advancing brain research, some foreseeable and some not. And perhaps more neuroscientists would be able to find jobs along the way!

But there are some considerations on the other side of the ledger, too. One that should not be underestimated is the opportunity cost; always, but especially nowadays, it would be a mistake to imagine that the funding for a new, large project will appear out of thin air. If the BAM goes forward, other areas are likely to get less funding, and other neuroscience and behavioral science projects will likely be among the first to be reduced. Moreover, a single mega-project is likely to supplant many smaller projects. Is our neuroscience money best spent on one project costing, say, $5 billion, or instead a thousand projects of $5 million each, or ten thousand projects with $500K budgets? Gary Marcus has a suggestion for five $1 billion projects. Which funding strategy is likely to result in more important discoveries, as viewed from the perspective of the next generation of scientists looking back? Maybe the BAM, but maybe not. The answer is hardly obvious to me. The big project is concrete and tangible, with milestones in the near future. The net effect of the tinkering of ten thousand labs with comparatively small budgets is harder to conceive of, but might turn out to be much larger.

One reason to be suspicious of the potential return-on-investment of a massive BAM project is that it's being sold by comparing it to the Human Genome Project (HGP), with a claim that the HGP produced $141 in economic activity for every $1 the government spent on it. President Obama cited this figure in his State of the Union Address. That's a return of fourteen thousand percent! Can that be right? If so, it would mean that about $800 billion in economic activity has been generated by that one government "investment." It turns out that this claim comes from a Batelle report (which is cited by the BAM advocates in their Neuron article) that was sponsored by a company that makes equipment used in life science research.

I find this figure hard to believe, not to say preposterous. Does it really represent net economic activity, or does it account for activity displaced from other spheres, and was all that economic activity the best activity that could have been done, or was it activity that pursuit of grant funding and other non-market incentives encouraged? What if the same amount of government money had been spent in funding lots of individual genetics researchers instead, or on other biology researchers, or other science entirely? The certainty with which these sorts of analyses are presented makes it hard to see counterfactual alternatives, but they lurk everywhere. At a minimum the $800B value must rest on a lot of assumptions, and the specific assumptions made probably have a large impact on the value that comes out of the analysis.

To be clear: I think the genome project was a great scientific idea, I suspect that it has produced a lot of benefits, and I am personally happy it was done. I just don't think it should be oversold. As Richard Feynman pointed out in his famous "Cargo Cult" speech, public support for research will eventually erode if it is sold with outrageous-sounding claims or promises of early benefits.

But suppose it is true that the Human Genome Project was the single best thing the U.S. government ever spent its money on—sorry, "investment it ever made"—the government's version of buying Apple stock for $5 and selling at $700. Should we expect similar returns from the next big science project? Or should we expect to see the economic return and gains in knowledge achieved by the average of the big science projects that the government has funded over the past decades? The abandoned supercollider, the war on cancer, the cancelled breeder reactor, and I am sure many others fade from memory—and certainly never get mentioned—when we are told about the 141X ROI of the genome project (worthy as it was). An analysis that looked at all the comparable projects rather than just the all-time outlier might come to a different projection of the likely value of the BAM. We might still expect a positive return, but without the 141X (or whatever the true value is), it will have a tougher time competing with other priorities, or with other ways of parceling out neuroscience funding.

Europe has thrown its lot behind the single mega-project approach, with an effort to simulate an entire brain at a cost of over 1 billion Euros. Regardless of the (questionable) merit of this idea, perhaps the U.S. should play a different strategy in the competition for research glory by letting a thousand flowers bloom rather than planting one ginormous tree. Indeed, such a contrarian approach may have value precisely because of the limits of the mapmaking approach to understanding the brain.

Forty years ago, single-cell neurophysiologist Horace Barlow famously proposed that "a description of that activity of a single nerve cell which is transmitted to and influences other nerve cells and of a nerve cell's response to such influences from other cells, is a complete enough description for functional understanding of the nervous system." The BAM Project seems to be a plan to create exactly this sort of description, but at a much larger scale. But as David Marr explained in his 1982 book Vision, and as Hilary Putnam also suggested in his 1973 Cognition article "Reductionism and the Nature of Psychology," there are several other levels of explanation that are equally important in reaching a "functional understanding" of how the brain works. The representations, algorithms, and computational functions of the brain and its circuits, as well as the relationship of the brain to the organism and its environment and niche, are just as important as a map that shows how the neurons are wired up and how they send signals to one another.

Again, it is not that a BAM would have no value. I would personally be fascinated to see its results, and those results might well help us to crack the problem of how higher-level properties emerge out of agglomerations of lower-level events (which the psychologist Stephen Kosslyn, a founder of cognitive neuroscience, proposed as one of the hardest problems in social science). But the sheer size of a full BAM project might focus our attention and hopes on the BAM as the be-all and end-all of neuroscience, and distract the field from devoting energy to those other levels. Cognitive scientist Mark Changizi has eloquently argued, in fact, that the massive project we ought to be pursuing is a map of the "teleome," his coinage for the suite of functions and abilities that the nervous system was designed by evolution to perform. Without knowing more about function, it will be hard to understand the BAM's results, and perhaps even harder to build the EU's whole-brain computer simulation. As the proposal moves forward, I hope the decision-makers keep in mind that maps, while incredibly useful tools, don't give answers to every important question.


  1. Personally, I'd prefer to see a massive "Cancer Genome Project" to see if we could genetically analyze many different kinds of tumors across many different kinds of populations, at all four stages. But I'll take any big project at this point.

    You brought up the War on Cancer, but we actually have seen some major reductions in cancer mortality over that time period, particularly among certain populations (such as young people). It's just that cancer, like the human genetic code and its interactions with everything else in our body and the environment, turned out to be vastly more complex than we thought.

  2. The opportunity cost is a real issue, but we should wait to see how the funding is actually being structured. For instance, will this be a project by just a few labs under coordinated leadership, as you imply? I think it's likely (and it's what I hear rumored) that there will be a portion of this project that's a funding pot. So multiple labs could all apply for their chunk, and in the end it's not so different than normal neuroscience.

    Also worth bearing in mind that, as you point out, what they're proposing is basically "let's do systems neuroscience". Which hopefully means that all the systems neuroscientists will get a shot at the money - money they would already be trying to get from normal NIH pools.

    I'm just curious to see whether the "mind control" part works out :-)

  3. Nice points. There's also the issue of whether there is such a thing as a single BAM. The interconnections and functional relationships between neurons are incredibly dynamic and can change from moment to moment based on neuromodulation and all different types of plasticity. Thus the variability between equivalent areas/behaviors among subjects could be tremendous. Even in worms, were the connections between neurons are well worked out, their functional relationship can vary dependent on neuromodulatory influences. So you could end up with as many BAMs as you have individuals.I bet that even when they start with C. elegans, they will encounter this variability except for very simple tasks. You could make the same argument about the human genome, that there is quite a bit of variation, but having a template allows you to have something to compare variation to. However, I think a similar approach will be difficult to apply in regards to a brain map. At best they might be able to derive some important computational principles about how groups of neurons solve specific problems, but not the total map they seem to be proposing.

  4. The European project is not a single mega-project. Though we heard that 1 billion is beging given to the technical uni of Lausanne, later we heard that this is to be divided among over 70 projects.

    >Europe has thrown its lot behind the single mega-project
    >approach, with an effort to simulate an entire brain
    >at a cost of over 1 billion Euros.

    It should be clear that study of a computer model of the brain will give information about the model, not about the brain. Any discrepancies would help make improvements to the model. It's wishful thinking to say that this will help us cure Alzheimers etc. Some of the publicity was really over the top. (I'm a layman)

  5. This is probably a dum idea. Knowledge takes time and the idea of the computer as answer to everything is a teenage-boy-brain gee-whiz enthusiasm.

    But brain research, and marketing, suggests it is a lot easier to sell a "big" idea and project that includes the word computer than real science - to decision-makers brains.

    I hear it would be a lot more productive to fund basic anatomy research, including animals. But that's "boring."

    70 projects under one "umbrella" will be an absolute mess. Our brains are not evolved to manage that! lol

    Already these silly projects are using up all the oxygen.

  6. I've been following the neurosciences for some time and have the impression that theories and models of brain activity have lagged behind ingenuity in making observations. See this old post of mine:

    I wonder whether or not this won't be more of the same. Merely having richer data isn't going to get people think deeper thoughts.

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