Talking to Torsten Wiesel: lessons in science

Perhaps the highlight of the Lindau Nobel Laureate meeting for me was meeting Torsten Wiesel who, together with David Hubel won the Nobel Prize in 1981 for their discoveries on the response properties of neurons in early visual cortex. Wiesel gave a talk in which he gave an overview of his work with Hubel. There wasn’t much time left for discussion that afternoon, but Jolien and I had the chance to talk to him in person the day after, on a very sunny terrace overlooking for Bodensee. Here’s some of the lessons I took from our conversation. Tip of the day: a short email requesting a meeting can really make your week.

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  1. Get your PhD out of the way, then go on to do the interesting science. Wiesel trained as a medical doctor and never did a PhD. Many of the Laureates at the meeting agreed on the fact that a PhD should be seen as a training, and that it’s the phase afterwards that really matters for building your own line of research. A good reminder for us doctoral students when we’re at the brink of despair about our chosen topic.
  2. Have a plan B. Wiesel admitted that he never felt too stressed or pressured in his research, since he could go back to Sweden and practice medicine anytime he stopped liking science. While certainly not all of us have such a good back-up, alternative career options are valuable to keeping your enthusiasm for science. After all, would you rather be in academia because you consciously chose so, or because you don’t see any other viable career options?
  3. Pick your question first – you don’t need an hypothesis. When asked whether they had many hypotheses that weren’t borne out by the data, Wiesel responded “we didn’t have hypotheses, we just had a question”. I think that Hubel and Wiesel’s way of moving from a general question (how do neurons respond to visual patterns?) to observations (each neuron response mostly to one part of the visual field, and one orientation) and then theory (neurons show receptive fields and orientation tuning) is immensely powerful. Sadly, perhaps because we picked all the low-hanging fruit, very few people do experiments that answer questions so clearly, with such basic equipment.
  4. Neuroscience is not ready for many of the question’s we’re asking. Wiesel was adamant that most of cognitive neuroscience, and perhaps all of human neuroscience, is lacking the fundaments it needs on the cellular and circuit level. He took face perception as an example, and argued that without the circuitry (some would call it connectome) or the FFA, we will never have a mechanistic explanation of face perception.

Upfront, I don’t agree with Wiesel on his last point, so I want to digress a bit, and talk about models and complexity. I found it very timely that barely a week later, the furore about the Human Brain Project led some to state that “[its] main apparent goal is radically premature”. The more I talk to scientists from different fields, the more apparent it seems that they agree on two things. First, we need mechanical explanations for the effects we’re studying. Second, the level they work at provides exactly this type of explanation. This is of course what we want from scientists: that they study the world at the level of complexity and detail of their choosing.
People calling for more mechanical explanations are, in my opinion, falling into a trap. Mechanical explanations are only desirable if you want to predict more low-level properties of the system you’re studying. A neural mass model is as useful to a clinical psychologist as enzyme pathways are to me (that is, not very useful at all). Of course, your model can be too simplified and therefor lack in predictive or explanatory power: this happens in science all the time, and so models are adjusted and made more detailed. This top-down specification and progress has worked great for as long as the scientific method is around. Recently there seems to be a lot of big talk about going the other way; simulating the brain from the ion channels up is thought to eventually give us an understanding of behavioural and cognitive effects. This is a very high-risk assumption to make, and it’s the reason why there has been so much anger directed at the HBP after they decided to cut out most of their cognitive neuroscience. When working from the bottom-up, we need theory and high-level models to embed all the simulations and low-level features in; generating loads of data without a higher-level framework around is is like throwing lots of sand in a pile and hoping it will form a castle.

Science as an enterprise necessarily builds simplified models of the world in order to understand and make better predictions (and possible interventions) about that world. The absurdity of models that fully represent the system of study are nicely captured by Arturo Rosenblueth “The best material model of a cat is another, or preferably the same, cat” and Lewis Carroll “We actually made a map of the country, on the scale of a mile to the mile!”. A model that doesn’t simplify is not a useful model – so work on the level of detail you find most interesting, and stop throwing around big words about mechanical explanations. After all, if we really wanted to find mechanical descriptions for all phenomena we’re studying, we’d all be particle physicists.

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