The Hamming Test (2013)

In a talk, titled "You and Your Research", the mathematician and computer scientist Richard Hamming describes his time at Bell Labs, and in particular, three questions he asked of some colleagues not in his field:

  1. What are the important problems of your field?
  2. What important problems are you working on?
  3. If what you are doing is not important, and if you don't think it is going to lead to something important, why are you at Bell Labs working on it?

I have often come back to this, particularly at key junctures, to help decide what I should do. More jocularly, they can be summarized as two questions: "What are the important problems in your field" and "Why aren't you working on them?"

What are the important problems of my field

I can remember, as a high schooler, asking my biology teachers, "so if all our cells have the same genome, why aren't all our cells the same?"

Here are a few of the problems that have fascinated me over the last 10 years, all of which have grown out of that simple question of why the same genome doesn't give rise to billions of identical cells:

  • How do cells read out information in the genome to properly differentiate? "A chicken is only an egg's way of making another egg", as Dawkins once pointed out. What that means to me is that somehow, a single embryo (complexed with the world it's developing in) has access to all the information necessary to create an adult version of itself. In the last 30 years or so, we've gradually started to answer mechanistic questions about how this information is actually parsed out of the DNA (among other places)
  • How faithfully can that information be read out? The intracellular environment is not generally as simple as many textbooks draw it, relatively sparse and open. Instead, it's a crowded megalopolis that has millions of active units all jostling around.
  • What happens in development that makes us, as humans, capable of culture?

I think those questions define the core of what I consider to be "my field". That's not to say that there aren't other interesting questions out there, but I think that if we can answer those questions sufficiently well, I'd be just as happy to pack up my Science and go home.

 

There are a number of questions that are naturally linked to these questions. For instance, if we really understood how our cells read out the genetic code, it should be possible to understand how our cells age or respond to stressors and disease. Furthermore, these questions build upon each other&emdash;knowing what the genome codes for ought to help us understand why what the human genome codes for is different than what the chimpanzee, Neanderthal, or other primate genomes code for.

Am I working on them

I'd like to think that fully answering any one of these questions will keep me quite busy for my whole career, even with the accelerating pace of science. Because of that, I have to triage:

Reading out information: This is where my current work lies. I think this is where the technology exists to make the most rapid progress, although it's also a much larger question than we can currently hope to address completely.

Faithfulness of readout: This is one of those fields I've been watching for a while, and am constantly amazed at what lots of very smart people are finding out. In some ways, it seems more tractable than the previous problem, but I'm also not sure that the field is one where I can make as big a difference as where I am now. That said, I often spend time thinking about ways I might jump in, or potentially merge the questions with what I'm already doing

Human distinctiveness: This is the big one, and I'm staying well clear of it. I don't think we are particularly close to providing meaningful answers to many parts of this question, and where we are, the techniques are probably better off being refined in model systems.

What are the best ways of answering those questions

While this wasn't one of Hamming's questions, I think it's worth bearing in mind, and possibly laying out some of the potential answers. After all, it seems unlikely that an angel will descend from the heavens bearing scrolls with a complete textbook on development.

Without going too deeply into the philosophical underpinnings of concepts like biological "design" or determinacy, it's been a driving principle in my career that if you can simply see what all the parts of a system are doing, it's comparatively straightforward to understand what the output will be, and why the system is set up the way that it is.

Of course, even if it were possible to collect all that data, making sense of all of it at once is beyond us at the moment. Nearly every experiment we do can be thought of as some kind of slice through the multidimensional space that is all of knowledge. For instance, taking a picture of something gives two dimensions in real space, but also takes only a small slice of the space of colors (unless your camera sees all wavelengths from radio to gamma rays).

Most of the work I've done in my time in graduate school is, in one way or another, developing methods to "see" what's going on with better resolution, breadth, or both as compared to pre-existing methods. I don't pretend that anything I've done is the be-all-end-all experiment of its kind, but they're all about pushing boundaries.

Other experiments I'd like to do in the future involve taking advantage of the fact that nature has already explored many possible configurations of systems for producing a given outcome. In fact, I'd even invoke Gell-Mann's Totalitarian Principle from Quantum Mechanics: "Anything that is not forbidden is required". It's not literally true, but nevertheless probably enlightening to look at a great range of evolutionary solutions to a problem, and then attempt to divine the rules and restrictions which produce a given outcome. Additionally, there's a long thread of experiments that show that these solutions are not mutually exclusive&emdash;just because a particular enhancer architecture was chosen in one species, there's often no reason a completely different one would lead to the exact same result.

I am, of course, always willing to listen to new approaches. My thoughts on what is feasible and likely productive are based on the current technologies and results, but it's always possible that something will come out of left field, or that someone will demonstrate something really cool using a technique I had written off as impractical.

Conclusions

I can't make this a list of what everyone should work on forever. "Interesting" is inherently subjective, and there are lots of fascinating subjects that I see at seminars and conferences and think, "gee, that's really cool." Occasionally, I see people trying to answer what I consider to be the wrong question, but much more often, it's just that they're going after a different question. That's why this current evaluation is more of a snapshot of what I'm concerned with right now (December of 2013). I will periodically make a new version of this as my interests evolve, grow, and shift.