Biology needs a Grothendieck (or at least a Hilbert)

By: Tony Kulesa

Recently passed away last month is the storied mathematician Alexander Grothendieck, who, in between his early quest to personally assassinate Hitler and his later (asc)descension into anarchist hermitdom, amassed a Christ-like following of mathematicians to rebuild entire fields of mathematics into a single theory of sublime generality, starting with the definition of a point.

Steven Landsburg gives a fitting layman’s description of Grothendieck’s profoundly powerful approach to mathematics:

“Imagine a clockmaker, who somehow has been oblivious all his life to many of the simple rules of physics. One day he accidentally drops a clock, which, to his surprise, falls to the ground. Curious, he tries it again—this time on purpose. He drops another clock. It falls to the ground. And another.

Well, this is a wondrous thing indeed. What is it about clocks, he wonders, that makes them fall to the ground? He had thought he’d understood quite a bit about the workings of clocks, but apparently he doesn’t understand them quite as well as he thought he did, because he’s quite unable to explain this whole falling thing. So he plunges himself into a deeper study of the minutiae of gears, springs and winding mechanisms, looking for the key feature that causes clocks to fall.

It should go without saying that our clockmaker is on the wrong track. A better strategy, for this problem anyway, would be to forget all about the inner workings of clocks and ask “What else falls when you drop it?”. A little observation will then reveal that the answer is “pretty much everything”, or better yet “everything that’s heavier than air”. Armed with this knowledge, our clockmaker is poised to discover something about the laws of gravity.

In other words, [Grothendieck’s] philosophy was this: If a phenomenon seems hard to explain, it’s because you haven’t fully understood how general it is. Once you figure out how general it is, the explanation will stare you in the face.”

To me, this analogy begs the question, what would have happened had the Isaac Newton of the apple-falling legend been one of today’s molecular biologists? Rather than writing down a new theory of gravity, would he have been looking for the genetic mutations that lead to the apple’s fall from its tree branch (armed with a tree farm, apple collecting robots, and a MiSeq, all on the NIH’s tab)?

What, as Landsburg puts it, is staring us in the face if we could just figure out how to ask the right question? In simple concepts like the definition of a point, Grothendieck saw the potential to build entirely new ways of thinking about geometry that turned long outstanding problems into obvious truths. What would a person like Grothendieck make of the basic axioms from which we build biology? Perhaps there are alternative ways of thinking about the basic building blocks, a gene, an enzyme, an organism, a species, that freshly reinterpret their functions in a way that would reinvent our field.

There are likely many reasons why Grothendieck was able to do what he did for mathematics, but many that knew him suggest the most significant to be his courage. Not only is it tremendously risky to spend years trying to reinvent existing fields, but its also lonely, and surely he would not have achieved anywhere near as much without the support of his peers. There are some biologists that come to mind, indeed even in our own department, who have voiced or even dedicated bodies of work to theoretically “out-there” ideas, and are widely dismissed by their colleagues. In light of Grothendieck’s triumph in mathematics, maybe we shouldn’t so quickly dismiss wild theories, but embrace and encourage them.


Steven Landsburg’s piece on Grothendieck:


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  1. I almost done reading an 800-page ecology textbook. (A labmate and I decided we should know about ecology.) Ecologists are always looking for general principles. We agree on a few: there are more species as you go toward the equator, ecosystems usually have no more than five trophic levels, and the number of species increases exponentially with area surveyed. A different general principle, which I don’t think most ecologists would agree with, is that the unifying principle of ecology is complication. Every system is different, and the general principles are either unsatisfying broad (e.g., chemistry, energy, things eating each other, etc.) or bizarrely narrow (like the trophic levels thing).

    In short, we might already know the general principles of biology. They are chemistry and physics. Everything left is complication, robots, and GWAS. This is hyperbole, but I think it’s more likely than the other side of this false dichotomy, where we can somehow derive the immunology of the alpaca from some Unified Equation of Biology.

    • Perhaps a fun poll question: what are the general principles of biology?

      My hunch would be that the answer might differ, depending on who you ask. I’m even torn about what I would like to say. Do I favor principles in metabolic regulation? Or the cell cycle? Evolutionary theory?

      Scott: I would think that there are many general phenomena that we don’t yet understand. Or am I not thinking generally enough?

      I also am unsure whether Tony meant that such generalities are how we “redefine” fields (perhaps Tony can clarify?). Maybe it’s that an artifact of the clock metaphor?

      It’s a beautiful image (smashing clocks), and a great example of how one might become lost while working towards an answer. But I think the clockmaker’s folly — tinkering with the mechanics of a clock in search of an explanation for gravity — doesn’t necessarily mean that current efforts to elucidate the role of a protein (or species, etc.) cannot make ground-breaking steps in fundamental biology. ( There’s so much about a cell’s inner workings that we don’t know, even for E. coli ! )

      • Aha! Yes, you’ll notice that I alluded to another mathematician in the title: David Hilbert. I was planning on writing another section of this post about him, but then decided against it and forgot to change the title. But… in light of your response let me revisit it.

        In early 20th century, Hilbert centered the field of mathematics on 23 problems essential for the development of further mathematics ( Some of these problems were directly related to establishing a firm foundation for mathematics, e.g. how can we rederive all of math from a small set of axioms that we can all agree are true.

        I’d argue that our field, biology, is in dire need of this kind of discussion. Some might argue that we already know what the outstanding questions are – but let me point out something really important about Hilbert’s questions: in 100% of cases, it is absolutely clear whether a satisfying answer was given. Our “general questions” in biology are almost never poised in a way that makes it clear whether we have answered them or not. So what we need to do is not so much debate what are questions are, as much as decide how to evaluate whether a question has been given adequately answered.

        For example, you say “there’s so much about a cell’s inner workings that we don’t know, even for E. coli!” But how much of that is important ? How do we even evaluate it? In biology there’s almost limitless complexity, so of course there will always be things that we don’t know, but maybe they don’t have a significant effect on the answers to questions that we’re interested in.

    • Thanks for thoughtful response!

      I agree with you that biology is enormously complicated, however do living systems span the entire space generated by iterating the rules of chemistry and physics? If they don’t, then will it ever be possible to predict the boundary? Why not?

      I don’t think I should be able to predicted every detail of the immunology of the alpaca from some unified equation, far from it. But, why can’t I try to describe the evolution of some general properties of immune systems along the evolutionary trajectory of alpacas? As an example, can the human immune system generate antibodies that cover an arbitrarily large fraction of chemical space generated by other biological systems? If yes, can alpacas? If yes, then where along our evolutionary trajectory is an organism’s whose immune system cannot?

    • I’m also going to post my main comment from that discussion:

      Some context behind why I wrote this post: as a researcher and technologist in biology, I’ve realized that it’s unclear the concrete standing questions are.

      >99% of the time, work is justified (and finished) with some application to health and medicine, with little regard for theory building or true understanding of a system. Bringing up this point usually solicits two responses: 1) we don’t have enough data yet 2) there’s little use for theory in biology.

      First, how do we judge what questions are worth asking and researching, vs trivial details? How do we even know whether we understand whether a question has been adequately answered? The current state of research to me often seems like John Searle’s Chinese Room: we just generate a huge dictionary of perturbation-responses and call this “understanding”. This might be effective to find drug targets, but is it real understanding? It might be the first step, but it seems to me that we’re swimming in plenty of data already and it’s worth it to step back and try to figure out what what it is we are actually trying to do. I’m comfortable with the fact that answers to our questions might be a long ways off, but it’s scary that no one seems to care that we don’t even know what the questions are.

      Second, I’d argue biology has historically been very theoretical. We developed a whole quantitative theory of genetics (Fisher, Wright, Haldane, …) before we had identified what a gene actually was. Hell, it was still debated what matter even looked like at that the microscale (where we knew genes must exist)! In the advent of molecular biology, Watson, Crick, Brenner, Gamow, Delbruck, et al, predicted through (some) experiments but mostly reasoning and conjecture much of what was later found to be true about transcription/translation. There are countless other examples of where theory has driven the study of the origin of life, molecular biology, ecology, et cetera. Only recently, when health science started to dominate biological research, did biology become less theoretical and more focused on individual instances of problems.

      tl;dr – What’s most scary is that we don’t even know what the foundational questions are anymore for modern biology. Rather than focusing on clearly stated foundations, the field is guided by the latest trends in glamour journals, which tend to obfuscate questions rather than answer them.

  2. I agree with you on that we shouldn’t so quickly dismiss wild theories, but embrace and encourage them.Only in this way can we have the chance to discover more secrets of the nature.And CD Genomics(a biotech company, always keeps this as its goal, pay much attention to biology research.

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  4. Great post. We see this all the time today – people are too concentrated on one particular issue, whether it be business or personal, that we are shielded from seeing the bigger picture. We all need to take Grothendieck’s word and think in more general terms. This type of thinking will spur curiosity, innovation and growth!

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