Neuroscience and other theory-poor fields: Tools first, simulation later

I have written about the ‘Big Brain Project’ a few times before including a post for the Canadian TV channel TVO last year. The project basically seeks to make sense of that magnificent 3-pound bag of jelly inside our skull at multiple levels, from molecules to neurons to interactions at the whole brain level. The aims of the project are typical of ‘moon shot’ endeavors; ambitious, multidisciplinary, multi-institutional and of course, expensive. Yet right after the project was announced in both the US (partly by President Obama) and in Europe there were whispers of criticism that turned first into a trickle and then into a cascade. The criticism was at multiple levels – administrative, financial and scientific. But even discounting the administrative and financial problems, many scientists saw issues with the project even at the basic scientific level.

The gist of those issues can be boiled down to one phrase: “trying to chew on more than we can bite off”. Basically we are trying to engineer a complex, emergent system whose workings we still don’t understand, even at basic levels of organization. Our data is impoverished and our approaches are too reductionist. One major part of the project especially suffers from this drawback – in-silico simulation of the brain at multiple levels, from neurons to entire mouse and human brains. Now here’s a report from a committee which has examined the pros and cons of the project and reached the conclusion that much of the criticism was indeed valid, and that we are trying to achieve something for which we still don’t have the tools. The report is here. The conclusion of the committee is simple: first work on the tools; then incorporate the findings from those tools into a bigger picture. The report makes this clear in a paragraph that also showcases problems with the public’s skewed perception of the project.

The goal of reconstructing the mouse and human brain in silico and the associated comprehensive bottom-up approach is viewed by one part of the scientific community as being impossible in principle or at least infeasible within the next ten years, while another part sees value not only in making such simulation tools available but also in their development, in organizing data, tools and experts (see, e.g., http://www.bbc.com/future/story/ 20130207-will-we-ever-simulate-the-brain). A similar level of disagreement exists with respect to the assertion that simulating the brain will allow new cures to be found for brain diseases with much less effort than in experimental investigations alone.

The public relations and communication strategy of the HBP and the continuing and intense public debate also led to the misperception by many neuroscientists that the HBP aims to cover the field of neuroscience comprehensively and that it constitutes the major neuroscience research effort in the European Research Area (ERA).

This whole discussion reminds me of the idea of tool-driven scientific revolutions publicized by Peter Galison, Freeman Dyson and others, of which chemistry is an exemplary instance. The Galisonian picture of scientific revolutions does not discount the role of ideas in causing seismic shifts in science, but it places tools on an equal footing. Discussions of grand ideas and goals (like simulating a brain) often give short shrift to the mundane but critical everyday tools that need to be developed in order to enable those ideas in the first place. They are great for sound bytes for the public but brittle in their foundations. Although scientific ideas are often considered the progenitors of a lot of everyday scientific activity by the public, in reality the progression can equally often be the opposite: first come the tools, then the ideas. Sometimes tools can follow ideas, as was the case with a lot of predictions of the general theory of relativity. At other times ideas follow the tools and the experiments, as was the case with the Lamb Shift and quantum electrodynamics. 

Generally speaking it’s more common for ideas to follow tools when a field is theory-poor, like quantum field theory was in the 1930s, while it’s more common for tools to follow ideas when a field is theory-rich. From this viewpoint neuroscience is currently theory-poor, so it seems much more likely to me that ideas will follow the tools in the field. To be sure the importance of tools has long been recognized in neurology; where would we be without MRI and patch-clamp techniques for instance? And yet these tools have only started to scratch the surface of what we are trying to understand. We need much better tools before we get our hands on a theory of the brain, let alone one of the mind.

I believe the same progression also applies to my own field of molecular modeling in some sense. Part of the problem with modeling proteins and molecules is that we still don’t have a good idea of the myriad factors that drive molecular recognition. We have of course had an inkling of these factors (such as water and protein dynamics) for a while now but we haven’t really had a good theoretical framework to understand the interactions. We can wave this objection away by saying that sure we have a theoretical framework, that of quantum mechanics and statistical mechanics, but that would be little more than a homage to strong reductionism. The problem is we still don’t have a handle on the quantitative contribution of various factors to protein-small molecule binding. Until we have this conceptual understanding the simulation of such interactions is bound to suffer. And most importantly, until we have such understanding what we really need is not simulation but improved instrumental and analytical techniques that enable us to measure even simple things like molecular concentrations and the kinetics of binding. Once we get an idea of these parameters using good tools, we can start incorporating the parameters in modeling frameworks.

Now the brain project is indeed working on tools too, but reports like the current one ask whether we need to predominantly focus on those tools and perhaps divert some of the money and attention from the simulation aspects of the project to the tool-driven aspects. The message from the current status report is ultimately simple: we need to first stand before we can run.

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