Thursday, June 14, 2018

Notes from Frontiers in Biophysics conference in Paros, episode 1 (pilot): Where's the beef in biophysics?

Long blog post hiatus, which is a story for another time. For now, I’m reporting from what was a very small conference on the Frontiers of Biophysics from Paros, a Greek island in the Aegean, organized by Steve Quake and Rob Phillips. The goals of the conference were two-fold:
  1. Identify big picture goals and issues in biophysics, and
  2. Consider ways to alleviate suffering and further human health.
Regarding the latter, I should say at the outset that this conference was very generously supported by Steve through the foundation he has established in memory of his mother-in-law Eleftheria Peiou, who sounds like she was a wonderful woman, and suffered through various discomforts in the medical system, which was the inspiration behind trying to reduce human suffering. I actually found this directive quite inspiring, and I’ve personally been wondering what I could do in that vein in my lab. I also wonder whether the time is right for a series of small Manhattan Projects on various topics so identified. But perhaps I’ll leave that for a later post.

Anyway, it was a VERY interesting meeting in general, and so I think I’m going to split this discussion up based on themes across a couple different blog posts, probably over the course of the next week or two. Here are some topics I’ll write about:

Exactly what is all this cell type stuff about

Exactly what do we mean by mechanism

I need a coach

What are some Manhattan Projects in biology/medicine

Maybe some others

So the conference started with everyone introducing themselves and their interests (research and otherwise) in a 5 minute lightning talk, time strictly enforced. First off, can I just say, what a thoughtful group of folks! It is clear that everyone came prepared to think outside their own narrow interests, which is very refreshing.

The next thing I noticed a lot of was a lot of hand-wringing about what exactly we mean by biophysics, which is what I’ll talk about for the rest of this blog post. (Please keep in mind that this is very much an opinionated take and does not necessarily reflect that of the conferees.) To me, basically, biophysics, as seemingly defined at this meeting, as a whole needs a pretty fundamental rebranding. Raise your hand if biophysics means one of the following to you:
  1. Lipid rafts
  2. Ion channels
  3. A bunch of old dudes trying to convince each other how smart they are (sorry, cheap shot intended for all physicists) ;)
If you have not raised your hand yet, then perhaps you’re one of the lonely self-proclaimed “systems biologists” out there, a largely self-identified group that has become very scattered since around 2000. What is the history of this group of people? Here’s a brief (and probably offensive, sorry) view of molecular biology. Up until the 80s, maybe 90s, molecular biology had an amazing run, working out the genetic code, signaling, aspects of gene regulation, and countless other things I’m forgetting. This culminated in the “gene-jock” era in which researchers could relate a mutation to a phenotype in mechanistic detail (this is like the Cell golden era I blogged about earlier). Since that era, well… not so much progress, if you ask me—I’m still firmly of the opinion that there haven’t really been any big conceptual breakthroughs in 20-30 years, except Yamanaka, although one could argue whether that’s more engineering. I think this is basically the end of the one-gene-one-phenotype era. As it became clear that progress would require the consideration of multiple variables, it also became clear that a more quantitative approach would be good. For ease of storytelling, let’s put this date around 2000, when a fork in the road emerged. One path was the birth of genomics and a more model-free statistical approach to biology, one which has come to dominate a lot of the headlines now; more on that later. The other was “systems biology”, characterized by an influx of quantitative people (including many physicists) into molecular biology, with the aim of building a quantitative mechanistic model of the cell. I would say this field had its heyday from around 2000-2010 (“Hey look Ma, I put GFP on a reporter construct and put error bars on my graph and published it in Nature!”), after which folks from this group have scattered towards more genomics-type work or have moved towards more biological applications. I think that this version of "systems biology" most accurately describes most of the attendees at the meeting, many of whom came from single molecule biophysics.

I viewed this meeting as a good opportunity to maybe take score and see how well our community has done. I think Steve put it pretty concisely when he said “So, where’s the beef?” I.e., it's been a while, and so what does our little systems biology corner of the world have to show for itself in the world of biology more broadly? Steve posed the question at dinner: “What are the top 10 contributions from biophysics that have made it to textbook-level biology canon?” I think we came up with two: Hodgkin and Huxley’s model of action potentials, gene expression “noise”, and Luria and Delbrück’s work on genetic heritability (and maybe kinetic proofreading; other suggestions more than welcome!). Ouch. So one big goal of the meeting was to identify where biophysics might go to actually deliver on the promise and excitement of the early 2000s. Note: Rob had a long list of examples of cool contributions, but none of them has gotten a lot of traction with biologists.

I’ll report more on some specific ideas for the future later, but for now, here’s my personal take on part of the issue. With the influx of physicists came an influx of physics ideas. And I think this historical baggage mostly distracts from the problems we might try to solve (Stephan Grill made this point as well, that we need something fundamentally new ways of thinking about problems). This baggage from physics is I think a problem both strategically and tactically. At the most navel-gazy level, I feel like discussions of “Are we going to have Newton’s laws for biology” and “What is going to be the hydrogen atom of the cell” and “What level of description should we be looking at” never really went anywhere and feel utterly stale at this point. On a more practical level, one issue I see is trying to map quantitative problems that come up in biology back to solved problems in physics, like the renormalization group or Hamiltonian dynamics or what have you. Now, I’m definitely not qualified to get into the details of these constructs and their potential utility, but I can say that we’ve had physicists who are qualified for some time now, and I think I agree with Steve: where’s the beef?

I think I agree with Stephan that perhaps we as a community perhaps need to take stock of what it is that we value about the physics part of biophysics and then maybe jettison the rest. To me, the things I value about physics are quantitative rigor and the level of predictive power that goes with it (more on that in blog post on mechanism). I love talking to folks who have a sense for the numbers, and can spot when an argument doesn’t make quantitative sense. Steve also mentioned something that I think is a nice way to come up with fruitful problems, which is looking at existing data through a quantitative lens to be able to find paradoxes in current qualitative thinking. To me, these are important ways in which we can contribute, and I believe will have a broader impact in the biological community (and indeed already has through the work of a number of “former” systems biologists).

To me, all this raises a question that I tried to bring up at the meeting but that didn’t really gain much traction in our discussions, which is how do we define and build our community? So far, it’s been mostly defined by what it is not: well, we’re quantitative, but not genomics; we’re like regular biology, but not really; we’re… just not this and that. Personally, I think our community could benefit from a strong positive vision of what sort of science we represent. And I think we need to make this vision connect with biology. Rob made the point, which is certainly valid, that maybe we don’t need to care about what biologists think about our work. I think there’s room for that, but I feel like building a movement would require more than us just engaging in our own curiosities.

Which of course begs the question of why we would need to have a “movement” anyway. I think there’s a few lessons to learn from our genomics colleagues, who I think have done a much better job of creating a movement. I think there are two main benefits. One is attracting talent to the field and building a “school of thought”. The other is attracting funding and so forth. Genomics has done both of these extremely well. There are dangers as well. Sometimes genomics folks sound more like advocates than scientists, and it’s important to keep science grounded in data. Still, overall, I think there are huge benefits. Currently, our field is a bunch of little fiefdoms, and like it or not, building things bigger than any one person involves a political dimension.

So how do we define this field? One theme of the conference that came up repeatedly was the idea of Hilbert Problems, which for those who don’t know, is a list of open math problems set out in 1900 by David Hilbert, and they were very influential. Can we perhaps build a field around a set of grand challenges? I find that idea very appealing. Although I think that given that I’ve increasingly come to think of biology as engineering instead of science, I wonder if maybe phrasing these questions instead in engineering terms would be better, sort of like a bunch of biomedical Manhattan Projects. I’ll talk about some ideas we came up with in a later blog post.

Anyway, more in the coming days/weeks…


  1. Thanks for reviving this amazing forum, it has been deeply missed! In thinking along these lines, I am always humbled by James Bonner's own 'blog post' (in 1960!) with the [original?] definition of the field of 'systems biology'. It's a short read, and fantastically prescient.

    To add to your list, another iconic example of (what I think of as) a systems biology discovery is Berg and Von Hippel's observation that diffusion-mediated 3D search time vastly under-predicts actual communication time in intracellular signalling. There has been significant work subsequent to this recognition (e.g., proof that transcription factors and polymerase spend at least some time in 1D-walks), but it's not clear to me that we (as a community) have satisfactorily reconciled this paradox. Maybe this is one of the new biologically inspired Hilbert problems?

    Looking forward to your next posts as you elaborate on the echoes of this amazing conference!

    1. Oooh, that's a great Hilbert problem!! Love that stuff, and yes, I think it has at least made some impact on more traditional biological thinking.

  2. Hi Arjun,

    I wrote an editorial last month that was my opening foray into this conversation ( I would love feedback about it-- I may be on to something, I may be wrong, but the important thing is knowing and evolving my thinking. I care so much about this community and this science. I hope that comes through.

    1. P.S. Thoughts specific to your post are forthcoming... :)

    2. This was a really great editorial. Thanks, Quincey!

    3. Very interesting read, Quincey! I have also wondered about absolute units in biology for some time. I was convinced by their power—then Yoav Gilad challenged me to name instances where they are more useful than a fold change. There are cases, but fewer than you might imagine. I wonder if this is because fundamental mathematical structures like in a math model are typically mostly revealed via non-dimensionalization (i.e., taking ratios of things until all the units cancel), and the fundamental parameters are dimensionless ones, like the Reynold's number. In biology, the most natural non-dimensionalization we use is to somehow normalize a number, which is basically… fold change!

      Anyway, lot more thoughts on this topic in a coming blog post on mechanism.

  3. Such a great and thought-provoking piece. Thanks!

    What, if anything, are the truly new theoretical tools that have been developed to tackle biological problems? I've been thinking about this lately. While I still don't really understand this stuff, it seems like the various non-equilibrium results from the Jeremy Englands of the world are at least pointing in that direction. What I especially liked from the famous 2013 England paper ( was that in the middle he explicitly acknowledged that everything he had discussed up to that point did not specifically describe a biological system. It could be anything dissipating heat, being out of equilibrium, etc. Then he moved on to show what is special about a simple (lol) biological system.

    Looking forward to your future posts on this stuff!

  4. I like the idea of a positive definition. In my opinion, one aspect of the definition should include discovering principles governing emerging behaviour. That is very hard.

    It is hard because (i) the linear models that have been so useful for simple physical systems may have limited utility for biological systems and (ii) because of dearth of good data. Yeah, I know we swim in oceans of undigested data, but I would argue that most data are uninterpretable because of poor (sometimes lacking) experimental designs or lots of noise, confounding and/or missing variables and so on.

    I discussed my ideas for dealing with both (i) and (ii) at the HMS theory lunch last month, and I am going to write it up as soon as a get a minute for that. Your post is a great inspiration for writing it up. I look forward to the continuation of this discussion!

  5. I don't understand the focus on labels, definitions, and boundaries around fields. (Okay, to be frank, I find it vaguely off-putting.) My suspicion is such demarcations are often in truth more motivated by social factors than intellectual ones. Obviously we need to use shorthand to describe what we do, but meticulous grouping seems unnecessary. In grant applications and talk introductions, I've been described as a mathematical biologist, evolutionary biologist, systems biologist, statistical ecologist, epidemiologist, complex systems scientist, immunologist, and more, and it's all fine, because my work involves all those things. Fields and methods are porous. Let's be specific about problems and particular approaches involved in each project without encouraging tribalism.