On not being in Kansas anymore

16 December 2012

Long, long ago, in a galaxy far, far away, I was a physicist. Or at least I trained as one. And even now, far removed from anything like what I did in grad school, I still wouldn’t trade that background for anything. But by this point, I’ve been a neuroscientist long enough that the hours I spent staring forlornly at equations on chalkboards have begun to seem like they happened to someone else.

More recently, though, the ghost of physics past has started haunting me again. I’ve been thinking seriously about what it would mean to lead a lab full of people doing the kind of science I do, and the realization I’m coming to is that probably means recruiting students with backgrounds similar to mine. Hate to say it, but the kind of quantitative skills one gets from physics or computer science or stats or EE is a little like academic Magyar: you either learn it early, or you tend not to learn it at all.

But I’d also be the first to say that coming into biology from the quant sciences carried it share of downsides, too. It’s a reason to be wary of trainees like myself. And so here, in no particular order (and mostly for my own edification), are the five hardest lessons I had to learn on the way to becoming a real biologist:

1. Nope, you do not automatically know how to do it better. Sadly, that really needs to be said. I used to joke with friends that the unspoken motto of our department was “physicists can do anything.” That is, we chose to do physics, though we were clearly smart enough to have mastered Derrida or Rawls or sports. Right. Weirdly enough, for people who’ve spent n years defending their study of abstruse and intricate questions untestable with any conceivable particle accelerator, former quants can have an awfully hard time believing that anyone else has actually thought hard about the basic problems of her field. The old joke about physics exam questions (“imagine a spherical cow”) is a great method for doing the kinds of back-of-the-envelope calculations that are the bread and butter of quant thinking, but it’s also a fair lampoon of the kind of ridiculous and uninformed approximations we tend to make the first time we look at a problem. What we tend to forget, of course, is that plenty of smart people thought about these problems long before we showed up to teach them how it’s done.
2. No, you are not going to solve it with a simple model. You are probably not even going to solve it with a complicated model. To be fair, I see fewer physicists than, say, software engineers head down this road. The unspoken prejudice being that, if biologists were really thinking hard, just one key insight would be enough to unlock the mysteries of the brain. This putative insight is usually some offshoot of a really good computer algorithm, and might work if the brain were composed of GPUs or repeated, identical computational units instantiating a basic set of recursive rules. In other words, if the brain were a digital computer, the secret would all be in the algorithms. Sadly, the last several decades of AI research, computer vision, and, you know, basic biology show this not to be true. In the real world, the nervous system shows complexity at every conceivable level, and while it’s not clear how much of this diversity really affects function, it’s probably a safe bet to assume that some of it does. To those of us reared on the successes of Maxwell’s equations, general relativity, and quantum field theory, that’s a disappointing prospect, but hey, it’s biology. What do you expect? It is in fact possible, even likely, that the mammalian nervous system utilizes more than one key computational idea.
3. Mathematical elegance is not winning you any points. Speaking personally, this was a hard one to internalize. I chose my grad school path based on the science I thought was cool, and what I thought was cool was theoretical elegance. Still do, in fact. But in the world I inhabit now, let’s be honest, nobody cares if your model is exactly solvable. Sure it’s a huge attraction in fields where the fundamental equations (or at least good approximations of them) are known, but the fact is, if you can solve the system in closed form, the system is probably too simple to be realistic. Put bluntly, there just aren’t a lot of conic sections and trig functions running around out in the wild. Not to say that some very smart people haven’t built some really brilliant toy models (Hopfield networks, Fitzhugh-Nagumo), but it’s probably better for one’s own productivity to realize that the entire theoretical neuro edifice is sitting on a throne of convenient lies (we call them “approximations”) and spend time trying to make the model look more like real data. (Though that last is personal prejudice. Plenty of great work still gets done on mathematically tractable toy models. I just think the majority of people like me are apt to do better, more relevant work by moving in the other direction.)
4. The data don’t float down out of the sky on a magic cloud. This misconception was my own fault, but speaking candidly, until you’ve stared at a computer screen asking yourself, “Is that a spike? Am I recording one unit or two?” while an animal does who knows what to screw up your beautifully designed task, I’m not sure you should be analyzing neural data. Meaning, until you realize how much uncertainty is involved in data collection and interpretation prior to those data being delivered hot and fresh (or old and stale, case may be) to your model, you’re likely to make very fundamental mistakes about how reliable and model-able those data are. We all tend to replace the real world with models from time to time. It’s easy and it helps us conceptualize. But the process of making sense of real, noisy, ambiguous data is humbling in a way most trainee theorists are not prepared for.
5. Even if you don’t become a real experimentalist, you need to make friends with a few dozen of them. I owe a tremendous career debt to a friend of mine who invited me to come do an experiment. Just to try it out. And get this: the moment I was responsible for designing a study of my own, a whole world of previously “irrelevant” detail suddenly started mattering a whole hell of a lot. And for the first time, I began to get an inkling of the kinds questions experimental neuroscientists, the 99% of our field, actually care about. For someone who did not grow up a bio nerd, this was transformative. And it constantly reminds me that the real goals we are pursuing center around understanding the brain and treating illness, not making sophisticated models of isolated phenomena. Even on a practical note, it’s clear that the top theorists in my field all have long-term collaborations with experimentalists. And sure enough, these top theorists are also the ones who spend time with real data and ask the questions the rest of the scientific world cares about.

To reiterate: I’m not against theory. I owe most of my success as a researcher to a few skills I’ve honed that are relatively rare in biology. I’m just hoping that, as I set out to lure some future quant trainees away into the jungles of the brain, I can get them excited about bushwhacking through the dense, thorny detail of biology instead of sticking close to the elegant, well-mannered path they came in on.