Why we shouldn't map the brain

When the Human Brain Project was selected by the European Union’s Future and Emerging Technologies (FET) initiative as one of its two Flagship science projects, launched in October 2013 with funding of €1bn over ten years (half to be gathered from national research agencies and other sponsors), it never looked like a wise choice to me. Now it’s official that it wasn’t.

Sure, the brain is science’s next frontier—but only in the sense that it looms as a big mystery, and not because we have any clear notion of how to tackle it. There’s no doubt that we need a wide variety of approaches and ideas, with tools and expertise drawn from neurology and genetics, computer sciences and physics, biochemistry and beyond. But that was not on the agenda of the Human Brain Project (HBP), which started from the premise that to understand the brain we should use experimental techniques to map out all of its connections and then create a massive computer simulation: a “virtual brain.” By doing so, the project leaders proclaimed, we should find cures for neurological and psychiatric disorders.

There is an element here of the popular (but false) idea that you never truly understand something until you can build it. That, needless to say, is never an option for planetary scientists or cosmologists. And the fact is that you can build something and still not fundamentally understand it—there aren’t many car mechanics who know their thermodynamics. Theoretical models don’t need to throw in the kitchen sink, and indeed they are often more useful if they don’t, so long as they incorporate the key principles. But of course that’s possible only if you have a good idea of what they are. We have a tremendously rich (albeit still thrillingly incomplete) understanding of the origins and evolution of the universe while still drawing on (among other things) computer models that are little more than schematic caricatures.

The “virtual brain” idea, on the other hand, seemed predicated on a belief that understanding will just fall out of the data, once you have enough of it. But that’s never a good way to do science. The real art is in discerning what to measure and what to exclude, how to simplify, how to capture the essential architecture of the problem without getting bogged down in details. Plenty of neuroscientists recognize that, but within the Human Brain Project there was a sense of “data comes first, thinking can wait." “It is a chicken and egg situation,” one theoretical neuroscientist involved in the HBP has said. “Once we know how the brain works, we'll know how to look at the data.” It was one of the best (which is to say, worst) examples of the dangerous allure of Big Data.

Now this shortcoming has been officially recognized. Complaints from many potential participants about the unrealistic and ill-defined goals of the project culminated in an open letter of concern endorsed by nearly 800 neuro- and cognitive scientists last year. In response to this and the request of stakeholders in the HBP, the project agreed to undergo an assessment by an independent panel of 27 international experts. The panel’s report, released in March, endorses just about all of the complaints, and is a going to bring about a radical overhaul of the project. Among other things, it concluded that “The HBP should define a unique set of concrete and achievable long-term objectives, which can be realized within the projected timeframe and with the financial resources available. To this end, it is recommended that the scientific program be carefully re-evaluated.” It seems very likely that the “virtual brain,” which was one of the HBP’s big selling points, is going to be abandoned.

This judgement might salvage something of value from the HBP, but it raises extremely troubling questions for the process that got it approved in the first place. A part of the problem lies in the very nature of an initiative like this. At face value, the EU Flagship programme looks like just what science needs. The idea was to identify projects with a bold, visionary character, something akin to the Apollo missions that put men on the moon. With so much scientific research being increasingly forced into the straitjacket of wealth creation and called upon to justify how it is going to contribute to gross domestic product in five years’ time, it is good to see an attempt to think big and on a long timescale.

But it’s less obvious how to make that kind of ambition work. To compete for a pot of gold, it is not just tempting but virtually essential to make exaggerated claims and promise the earth (for after all, who can really say what will or won’t be possible a decade or two down the line?). Even in regular grant applications, this kind of more or less wild speculation masquerading as forecasting is becoming standard practice: everyone (both applicants and referees, who are from the same community anyway) accepts that you have to make unrealistic claims in order to grab attention. No one gets grants for saying that they want to go on carrying out careful, incremental research.

The rhetoric of Apollo missions and Manhattan Projects is totally misplaced in this kind of endeavour. Everyone knows that they both attracted such massive state support not because they were addressing social needs, or satisfying some abstract quest of curiosity or exploration, but because they were wartime priorities. That same rhetoric is implicitly deployed when scientific and political leaders speak of a “war on cancer” or on antibiotic resistance. There can be no “war” on such problems, and so no victory either.

Perhaps it’s no coincidence that the other Flagship project selected by the EU played it very safe: the Graphene project aims to develop this new carbon-based material into a host of useful applications. Did the committee decide that, having stuck its neck out with the Human Brain Project, it would steer a more predictable and modest course with the other selection? With this degree of attention, graphene research seems sure to yield fruit, but it won’t change the world, and much of the research would surely have happened anyway. One might see in all this an indication that the EU would have been damned either way: by being too bold or too risk-averse. But perhaps the real problem is in the whole notion of holding beauty pageants for Big Science. We need to find good ways of encouraging scientists to think big, but a huge pot (or two) of gold is not the best incentive.