“Seeing” the Big Picture: Vision Revolution Author Mark Changizi

As research scientists, many of us spend a very large amount of time working on a very small subject.  In fact, it’s not unusual for a biochemist to go through their entire career without ever physically observing the protein or pathway they work on.  As we hyper-focus on our own niche of science, we run the risk of forgetting to take the blinders off to see where our slice of work fits in to the rest of the pie.

For Dr. Mark Changizi, assistant professor and author of The Vision Revolution, science starts with the pie.  We spoke with Dr. Changizi about why losing focus on the big picture can hurt our research, how autistic savants show us the real capacity of the brain and what humans will look like a million years from now.

BenchFly: Your book presents theories on questions ranging from why our eyes face forward to why we see in color.  Big questions.  As a kid, was it your attraction to the big questions that drew you into science?

Mark Changizi: I sometimes distinguish between two motivations for going into science. First there’s the “radio kid,” the one who takes apart the radio, is always fascinated with how things work, and is especially interested in “getting in there” and manipulating the world. And then there’s the “Carl Sagan kid,” the one motivated by the romantic what-does-it-all-mean questions. The beauty of Sagan’s Cosmos series is that he packaged science in such a way that it fills the more “religious” parts of one’s brain. You tap into that in a kid’s mind, and you can motivate them in a much more robust way than you can from a here’s-how-things-work motivation. I’m a Carl Sagan kid, and was specifically further spurred on by Sagan’s Cosmos. As long as I can remember, my stated goal in life has been to “answer the questions to the universe.”

While that aim has stayed constant, my views on what counts as “the questions to the universe” have changed. As a kid, cosmology and particle physics were where I thought the biggest questions lied. But later I reasoned that there were even more fundamental questions; even if physics were different than what we have in our universe, math would be the same. In particular, I became fascinated with mathematical logic and the undecidability results, the area of my dissertation. With those results, one can often make interesting claims about the ultimate limits on thinking machines. But it is not just math that is more fundamental than physics – that math is more fundamental than physics is obvious. In a universe without our physics, the emergent principles governing complex organisms and evolving systems may still be the same as those found in our universe. Even economic and political principles, in this light, may be deeper than physics: five-dimensional aliens floating in goo in a universe with quite different physics may still have limited resources, and may end up with the same economic and political principles we fuss over.

So perhaps that goes some way to explaining my research interests.

Tell us a little about both the scientific and thought processes when tackling questions that are very difficult to actually prove beyond a shadow of a doubt.

This is science we’re talking about, of course, not math, so nothing in science is proven in the strong mathematical sense. It is all about data supporting one’s hypothesis, and all about the parsimonious nature of the hypothesis.  Parsimony aims for explaining the greatest range of data with the simplest amount of theory. That’s what I aim for.

But it can, indeed, be difficult to find data for the kinds of questions I am interested in, because they often make predictions about a large swathe of data nobody has. That’s why I typically have to generate 50 to 100 ideas in my research notes before I find one that’s not only a good idea, but one for which I can find data to test it. You can’t go around writing papers without new data to test it. If you want to be a theorist, then not only can you not afford to spend the time to become an experimentalist to test your question, but most of your questions may not be testable by any set of experiments you could hope to do in a reasonable period of time. Often it requires pooling together data from across an entire literature.

In basic research we are often hyper-focused on the details.  To understand a complex problem, we start very simple and then assume we will eventually be able to assemble the disparate parts into a single, clear picture.  In essence, you think about problems in the opposite direction- asking the big questions up front.  Describe the philosophical difference between the two approaches, as well as their relationship in the process of discovery.

A lot of people believe that by going straight to the parts – to the mechanism – they can eventually come to understand the organism. The problem is that the mechanisms in biology were selected to do stuff, to carry out certain functions. The mechanisms can only be understood as mechanisms that implement certain functions. That’s what it means to understand a mechanism: one must say how the physical material manages to carry out a certain set of functional capabilities.

And that means one must get into the business of building and testing hypotheses about what the mechanism is for. Why did that mechanism evolve in the first place? There is a certain “reductive” strain within the biological and brain sciences that believes that science has no role for getting into questions of “why”. That’s “just so story” stuff.  Although there’s plenty of just-so-stories – i.e., bad science – in the study of the design and function of biological structure, it by no means needs to be. It can be good science, just like any other area of science. One just needs to make testable hypotheses, and then go test it. And it is not appreciated how often reductive types themselves are in the business of just-so-stories; e.g., computational simulators are concerned just with the mechanisms and often eschew worrying about the functional level, but then allow themselves a dozen or more free parameters in their simulation to fit the data.

So, you have got to attack the functional level in order to understand organisms, and you really need to do that before, or at least in parallel with, the study of the mechanisms.

But in order to understand the functional level, one must go beyond the organism itself, to the environment in which the animal evolved. One needs to devise and test hypotheses about what the biological structure was selected for, and must often refer to the world. One can’t just stay inside the meat to understand the meat.

Looking just at the mechanisms is not only not sufficient, but will tend to lead to futility. An organism’s mechanisms were selected to function only when the “inputs” were the natural ones the organism would have encountered. But when you present a mechanism with an utterly unnatural input, the meat doesn’t output, “Sorry, that’s not an ecologically appropriate input.” (In fact, there are results in theoretical computer science saying that it wouldn’t be generally possible to have a mechanism capable of having such a response.) Instead, the mechanism does something. If you’re studying the mechanism without an appreciation for what it’s for, you’ll have teems and teems of mechanistic reactions that are irrelevant to what it is designed for, but you won’t know it.

The example I often use is the stapler. Drop a stapler into a primitive tribe, and imagine what they do to it. Having no idea what it’s for, they manage to push and pull its mechanisms in all sorts of irrelevant ways. They might spend years, say, carefully studying the mechanisms underlying why it falls as it does when dropped from a tree, or how it functions as crude numchucks. There are literally infinitely many aspects of the stapler mechanism that could be experimented upon, but only a small fraction are relevant to the stapler’s function, which is to fasten paper together.

In explaining why we see in color, you suggest that it allows us to detect the subtleties of complex emotions expressed by humans – such as blushing.  Does this mean colorblind men actually have a legitimate excuse for not understanding women?!

Probably, but there’s no direct data on whether colorblind men really are worse at sensing emotions. One would have thought that there would at least have been lots of personal stories to that effect. E.g., my Dad was colorblind, and indeed he was a bit emotionally obtuse. But no one has tried to test this. We do know that colorblind doctors have complained for a couple centuries about their handicap at seeing clinically related color signals, which are often due the same hemoglobin oxygenation and concentration modulations underlying regular emotional modulation.

How much of what we experience in life on a daily basis do you think we take for granted (or overlook), even though we actually have no idea why it works the way it does?

A lot of our most amazing powers are right before our eyes; we use them so integrally that we have no idea they’re there at all. For example, if you look at your hand it is practically impossible to see it as something whose morphology needs explanation. When we grow up seeing it millions of times, over and over, we adapt to its shape so strongly that it perceptually feels like a mathematical tautology that hands should look like that. But if you look at the hands of other primates, or other mammals, you are better able to really perceive the morphology, and get that there’s something to explain.

Autistic savants provide an example of this as well. They do certain amazing things, like recounting the first ten thousand digits of pi. But what’s going on is that their brain is incorrectly harnessing some mechanisms you and I possess, but for an unusual purpose. And that means that you and I have a power that is just as amazing, but we don’t notice it because it is being used as intended. In fact, it is probably a lot more amazing than the pi calculation, because you can be sure the autistic pi calculating man has no mechanisms in him designed by evolution for that, and so probably his pi calculations are klunky compared to what they would be if evolution had selected us to be pi calculators. Autistic savants are neat because they give us a window into just how powerful all our brains are, a power we can’t see because it is too close to home.

While we’re on the topic of big picture- As society becomes increasingly technologically advanced, our evolutionary pressures change.  What do you think is the next major trait to evolve in or out of the human body as a result of these new pressures?

Ha. One thing I do discuss in The Vision Revolution along these lines is our forward-facing eyes. I have argued and provided support for the new hypothesis that forward-facing eyes evolved to optimize our view in leafy forests. We are no longer in leafy forests, and the benefit of forward-facing eyes is now a handicap. Our world’s occlusions are the size of trash cans and cars, not leaves; and the distance between our eyes is way too low to get the benefit that occurs in forests for us. So, we’d be better optimized now if we had sideways-facing eyes, and so perhaps if you freeze yourself and unfreeze yourself in a million years, your progeny will have rabbit eyes, and everyone will laugh at the forward-eyed freak.

Feeling like we have a connection to a bigger picture is something many of us crave to stay motivated when things are tough in lab.  However, those ties can often be loose at best.  Do you have any advice for basic researchers trying to engage the big picture questions while managing the details of everyday research?

I actually have a book proposal written for a book after the next one, called ALOOF: How Not Giving a Damn Maximizes Your Creativity. The ideas that will be in that book, if it happens at all, have come out of my attempts to become more reflective about how to gear one’s head to optimize one’s chance at getting the next big idea. The idea of remaining aloof has multiple facets, and I’ll mention just one, something that is also part of a longer piece I wrote at my blog. This sense of “aloof” is the most similar to the usual sense, concerning social groups. The advice is to avoid getting too deeply involved in the conference communities in your field. By showing up to them regularly, one cannot help but to begin becoming part of that community. One soon wants to become a big shot in that field, and to impress the current big shots. One wants to stick it to that guy or gal who reviewed your work unkindly. One wants to solve this or that problem, because the community respects that kind of problem. Soon you’re poo-pooing the questions tackled by other fields, and soon you have accepted loads of premises that everyone in the field accepts, and you don’t even realize you have accepted any premises. It is a kind of natural social brainwashing that our brains can’t help but do. And they like to do it. My rule has always been to not go to conferences, unless specifically invited. There are plenty of ways to keep up with the literature without having to go to conferences. What one misses by avoiding conferences, though, are the contacts that can be useful in getting a job and so on. But I’d argue that the damaged creativity is a greater loss. I figured I’d take the hit of not having the best suite of contacts, thereby not locally optimizing, but have a greater chance of globally optimizing my scientific career.

It’s not uncommon to feel vulnerable immediately after publishing a paper – What if people can’t reproduce the work?  What if someone else demonstrates the exact opposite?  What if we completely overlooked the most logical interpretation of the data?  When publishing theoretical results, where the findings may be impossible to prove with current methods, is this feeling amplified?  Or is debate assumed, welcomed and even intended?

I don’t publish theoretical results, by the way. I publish theory, but always with new data to support them. There are bored physicists who sometimes publish biology theory without any data in physics journals, but no one in the biological sciences tends to pay attention. I would have 100 times as many “great” theory papers if I didn’t have to get data! That would be fun! But, no, you must have new data that tests your big theory.

What makes a theorist a theorist is not whether or not they have to test their hypothesis. They must. Theorists are theorists because they specialize in the construction of rigorous, broad, and testable hypotheses.

So, no, I don’t think the feeling is amplified, not, at least, on the basis of a difference on the empirical side. There is, though, perhaps a difference in that, if I’m lucky, I’m overturning a theory or implicit presumption that’s been around for a long, long time. Often the prior theory was based on little or no evidence, but has simply become accepted wisdom; it can take some effort to overturn “what everyone knows”.

Do we, as basic researchers, limit ourselves by focusing too much on the data when trying to generate creative hypotheses?

Certainly one wants to focus on the existing data as a guide to one’s theory. But one shouldn’t just go out and start collecting data without a good theory or suite of theories in hand.  One’s intuitions are often that one should just collect “all the data,” and worry about the theory later. But that’s a bad approach. There’s infinitely much data one can collect, and so you can collect all you want, and still find that you haven’t collected the right type for the theory that you later realize you want to test.

If you could make one change that you think would make science a better career, what would it be?

There are precious few mechanisms that directly encourage non-incremental creative scientific work. The typical hard-nosed measures of success in academics – number of publications, money from grants, and even letters from colleagues – don’t take this into account. Ultimately, if you are successful at non-incremental creative scientific work, you will be appreciated, but not in the ways that are reflected in the traditional accounting system. And, most importantly, the reason you went into science was, presumably, to do something non-incrementally creative, so it pays – for a life well-lived – to aim for it!

Your new book shifts to another one of our senses-  hearing.  Give us a teaser…

My next book is not really about hearing, per se, but it does end up touching upon speech comprehension and music, both obviously in the auditory domain. The general point of the book – titled Harnessed: How Language and Music Mimicked Nature and Transformed Ape to Man – is that the language and music that we cherish so much as distinguishing us from the apes is not innate. Nor can we do these things because we’re terribly smart universal learning machines. We can process speech and make sense of music because cultural evolution has shaped speech and music to be just right for our auditory system. And the trick culture uses to get these things into our thick non-linguistic and non-musical skulls is to make them sound “like nature”. In the current book – The Vision Revolution – I take this approach to explaining the origins of writing (in Chapter 4): written language has shaped itself to look like natural scenes, and thereby harnesses our object-recognition visual system for a new task for which it never evolved. For speech, the story concerns auditory event recognition, and for music the story concerns auditory recognition of conspecifics. But I’ll have to leave the details for later.

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Mark Changizi is an evolutionary neurobiologist and assistant professor in the Department of Cognitive Science at Rensselaer Polytechnic Institute aiming to grasp the ultimate foundations underlying why we think, feel and see as we do. His research focuses on “why” questions, and he has made important discoveries such as on why we see in color, why we see illusions, why we have forward-facing eyes, why letters are shaped as they are, why the brain is organized as it is, why animals have as many limbs and fingers as they do, and why the dictionary is organized as it is.  His articles have been covered in news venues such as the New York Times, Wall Street Journal, Newsweek and Wired. He has written two books, THE VISION REVOLUTION (Benbella, 2009) and THE BRAIN FROM 25,000 FEET (Kluwer, 2003). He is currently wrapping up his third book, HARNESSED: How Language and Music Mimicked Nature and Transformed Ape to Man.