Questions for Rich Lenski about his amazing Long Term Evolution Experiment (UPDATEDx4)

This year, for the 30th year in a row, the University of Calgary will be celebrating Darwin Day with an invited seminar by a top evolutionary biologist.* We’re very excited to have the Rich Lenski as our speaker this year.**

Rich has done lots of great stuff, but he’s most famous for his long-term evolution experiment (LTEE) with E. coli, which has been running for almost 27 years and over 60,000 generations. Rich has a series of blog posts summarizing the key results. I’m not an evolutionary biologist, and I’m biased because I’m a microcosm guy, but whatever–I think the LTEE is the world’s greatest evolution experiment.

I think it’s really interesting not just for the scientific results themselves, but also as a case study of how to do science. I have a whole bunch of questions I want to ask Rich about the LTEE, and I doubt I’ll get the chance to actually ask them all. So I thought I’d share them here; maybe he’ll stop by and answer them! And even if he doesn’t, they’re interesting questions for everyone to think about. They touch on issues relevant to anyone who’s ever had to decide “What scientific question should I ask and how should I go about answering it?”

  • When you first started the LTEE, did you consider it to be a low risk or high risk experiment? Because I could see arguing both ways. In some ways, it’s low risk, because one can imagine lots of different possible outcomes, all of which would be interesting if they occurred. But in other ways, it’s high risk–I imagine that many of the interesting outcomes (including those that actually occurred!) would’ve seemed unlikely, if indeed they’d even occurred to you at all. Or did you not worry much about the range of possible outcomes because the experiment was basically a lottery ticket? “This’ll be cheap and not much work, let’s just do it and see what happens. Something really cool might happen, but if it turns out boring that’s ok because it wasn’t a big investment.”
  • Is the LTEE actually an experiment, and wouldn’t it have been even better if it was? It’s just one “treatment”–12 replicates of a single set of conditions. Wouldn’t it have been even more interesting to have, say, two treatments? Two different culture conditions, two different founding genotypes, two different founding species…?
  • Following on from the previous question: Have you ever considered adding an experimental treatment to the LTEE? There’s precedent for it; think of how treatments were added to the Park Grass experiment after it had been running for a long time. Of course, maybe this isn’t a real question, since you could always go back and use frozen samples to start whatever new experiments you wanted, without having to change the design of the LTEE.
  • How have you maintained funding for the LTEE over the years, and how hard has it been? The difficulty of sustaining funding for long term work is a common complaint in ecology, and I’m guessing in evolution as well. And of course, if people think that they won’t be able to sustain funding for a long-term project, they’re less likely to start one in the first place. At best, they’ll try to do it by piggybacking short-term studies (or short-term rationales) on the long-term work, so that the long-term work can be sustained via a series of short-term grants. When you first proposed the LTEE to NSF or whoever, presumably you didn’t say “I propose to set up 12 replicate lines of bacteria, keep them going for decades, and see what happens”. And when you went back for your first (or second, or third…) renewal, presumably you still didn’t say “a bunch of cool stuff has happened already, so please give me more money to keep it going, just to see if anything else cool happens.”
  • Related to the previous question: Has it become easier to get funding to keep it going as you’ve gone along? Has it gotten to the point where the experiment (and you?) is widely seen as an “institution”? So that rather than needing to justify it anew every few years, people are basically eager to hand you money to keep it going, no questions asked?
  • What’s the role of chance vs. determinism in allowing you to keep the experiment going? If you “rewound the tape of life” and repeated the experiment, do you think it would’ve lasted as long as it has? For instance, I could easily imagine that in a replay of the experiment, no citrate-using line or other gain of a complex function arises during the first, say, 40,000 generations. Possibly leading you to cut off the experiment because nothing new seems to be happening. Or possibly leading funding agencies to cut you off because you haven’t had any exciting new results in a while and they think the experiment has run its course.
  • How much has your ability to keep learning new things from the LTEE depended on events in the experiment itself (evolution of citrate use, evolution of elevated mutation rates, etc.), vs. events external to the LTEE like improving gene sequencing technologies that let us ask questions that weren’t feasible to ask before? In other words, is the previous question based on the false premise that it’s only what happens within the LTEE itself that dictates whether it’s worth it to keep it going?
  • Is the LTEE itself now a “model system”? Model systems in biology–systems in which it’s tractable to ask a given question–often are systems that we know a lot about. We can leverage that background knowledge to ask questions that otherwise wouldn’t be tractable. E. coli of course is a model organism for many purposes, because we know so much about it. But is the LTEE itself now a model system?
  • Has anyone tried to copy or build on the LTEE? This kind of gets back to the questions about experimental treatments. Has anyone tried the LTEE again with a different starting genotype? With a different species (say, a sexually-reproducing yeast)? With a mix of species rather than just one (eco-evolutionary dynamics!)? With different culture conditions (say, with a mineral nutrient rather than C being limiting, or a temporally-varying rather than constant environment)? Given that the basic experiment is relatively cheap and easy (right?), I’d think that a follow-up to the LTEE would be ripe for a NutNet-type approach. A massive distributed experiment, maybe with each participating lab running one replicate of each of a bunch of treatments.
  • You’ve said that there was a time when you were thinking of stopping the LTEE and switching to working on evolution of digital organisms. Why?  And looking back, do you think the idea of stopping the LTEE was reasonable at the time? After all, what’s reasonable ex ante isn’t the same as what looks reasonable ex post. Hindsight is 20-20 vision and all that. Just because it now seems crazy that you ever thought of stopping the LTEE doesn’t mean it was crazy back then. And could you see yourself ever stopping it now, or handing it off to someone else so that you can finally go do that digital evolution work or whatever?
  • Are there results from the LTEE that in your eyes are underrated (or overrated!) by others? I think one of the more underrated results from the LTEE is the evolution of long-term stable coexistence of different mutants derived from the same ancestor. Although not indefinite coexistence–if I recall correctly, one of the coexisting lines eventually evolved so as to exclude the other, rather than the lines evolving so as to further stabilize coexistence (as I think many ecologists might’ve expected). I think ecologists interested in eco-evolutionary dynamics should be taking more notice of this and other results from experimental evolution. Conversely, in your blog post summarizing the major results of the LTEE, one of them was simply the result that the bacteria do indeed exhibit evolution via natural selection. Surely that result is totally expected and so not very interesting, at least not to an evolutionary biologist? And yes, it’s a “textbook” example of evolution by natural selection, but didn’t we already have a lot of those?
  • Do you ever run into objections to the “artificiality” or “unrealism” of the LTEE? There’s a school of thought in ecology that’s skeptical of the value of microcosm experiments, seeing them as a pointless distraction at best and as positively misleading at worst, because they’re “unnatural”. (This school of thought is wrong, of course.) It’s my impression as an outsider that such skepticism doesn’t exist to the same extent in evolutionary biology. Perhaps because evolutionary biology has such a long history of experimental work in the lab (think of Drosophila experiments from many decades ago)? Or at least, that objections to microcosm experiments like the LTEE refer to specific features of the experiment like the large population sizes and asexuality of bacteria? Such specific objections necessarily are limited in scope–they’re not blanket objections to microcosms as an approach, they just identify the limited domain over which the results are generalizable. And they can in many cases be turned into testable hypotheses, say by repeating the experiment with smaller population sizes or a sexually-reproducing organism.

*We also do other fun stuff to celebrate the day, using it as a way to build camaraderie among faculty, grad students, and undergrads.

**And by “very excited” I mean “I have undergrads squealing with sincere delight when I announce details of the talk in my classes.” And the talk isn’t until Feb. 6; I’m hoping my students don’t implode with anticipation before then! So Rich, if you’re reading this, the general mood here is that Christmas is coming, and you’re Santa Claus. No pressure. 🙂

UPDATE: Santa Claus Rich Lenski responds!:

UPDATEx2: And immediately is given reason to regret opening his big mouth! 🙂

Laura’s gotten the ball rolling, let’s push it down the hill and turn it into a giant snowball of peer pressure!:

Dynamic Ecology: luring visiting speakers into writing books since 2015! 🙂

UPDATEx3: Rich now has a post up at his blog answering my first question. Thanks Rich!

UPDATEx4: And now he’s answered my second question. The short version of his answer:


19 thoughts on “Questions for Rich Lenski about his amazing Long Term Evolution Experiment (UPDATEDx4)

  1. These are fantastic questions! Maybe we can entice him to answer one per month, in exchange for… maybe he can tell us. But I really want to know the answers. The questions about the early hypotheses and experimental design are especially interesting. It’s funny how important and interesting some experiments can be without adhering to the traditional hypothesis-testing structures–or perhaps I’m also ignorant of some key parts of the early papers.

    • I agree! A group of grad students and I are currently reading through the Garland and Rose experimental evolution book. The grad students were universally surprised that anyone would have ever doubted that experimental evolution would work and be observable in the lab on short timescales. When we were discussing it, I brought up the LTEE and how, while it seems like such an obvious experiment now, that’s only because Rich thought to do it and it was so tremendously successful.


        Great point. Hindsight is 20-20. That’s kind of the implicit theme of my questions–it wasn’t *obvious* at the start that this was a great idea for an experiment, or even a particularly good idea! So was it a good idea at the time, but for some non-obvious reason? Was it a lottery ticket that turned out to be a winner? Or what?

    • @Sarah Cobey:

      “It’s funny how important and interesting some experiments can be without adhering to the traditional hypothesis-testing structures”

      That’s a really interesting comment. Perhaps it’s because, to have an experiment that really stands out from the crowd, it has to be unconventional in *some* way. And trade-offs are ubiquitous, so to get an experiment that’s unconventional in some way, you have to sacrifice some conventional virtues, such as a traditional hypothesis-testing structure (or “replication”, or whatever).

      Of course, this doesn’t mean that everybody should seek to do unconventional experiments! Because of course, lots of unconventional experiments that sacrifice some conventional virtues turn out boring or uninterpretable or just weird.

      Which raises the question of how you decide when to be unconventional. And whether some people are better at it than others. Is Rich Lenski good, or lucky? (Presumably, the answer is “yes”.)

  2. And another question, which I’ll share: Would *any* evolution experiment that runs sufficiently long *necessarily* turn out to be a great experiment? Or at least quite likely turn out to be a great experiment? And if so, how do we fund more of them? And how do we decide which ones to fund (since after all, by assumption they’d *all* be great experiments!)? And what’s “sufficiently long”? (Opening bid: “sufficiently long” means “at least 10 times more generations than any previous evolution experiment with these or relevantly-similar organisms”).

    • Hmmm, are you allowing for the possibility that the only experiments that would be allowed to run that long would be ones that seem promising in the early stages? There could be strong selection bias in the experiments themselves!

      • No, I’m imagining a case with no selection bias: every experiment just runs for a really long time, even if early on the results don’t seem promising. Is it the case that P(really interesting results) goes to 1 for sufficiently long experiments?

  3. My guess for “Has it become easier to get funding to keep it going as you’ve gone along?” is harder. From what I’ve seen of long-term experiments, these days you typically have to come up with a brilliant novel idea on why to keep it running every 3-5 years. That’s my necessarily recent observation, by the way, since I’m a recent ecologist. I understand that it used to be easier to get funding for so-far-successful long-term research. (U.S. bias.)

    • I can only offer anecdotes here. I seem to recall Jim Brown writing back in the 90s that he’d found it easier to get funding to keep his long term desert granivore experiments at Portal going than to get funding for macroecological work. But that doesn’t directly get at your question, because maybe Jim just found it relatively easier to come up with new rationales for the Portal experiment every 3-5 years.

      I can say based on very recent personal experience as a co-PI that the NSF long-term research program is a little oddly structured. I can sort of understand why it’s structured the way it is–it’s basically funding constraints. But in practice, it means that you apparently have to have a very specific amount of data already collected, and a very specific justification for collecting *exactly* 10 more years of data. Basically, you need a big question that you can’t answer at all with your current data or a few more years of data, but that you can definitely answer with 10 more years of data. A quite oddly narrow window to try to hit. N=1 here, obviously, so your mileage may vary.

  4. Pingback: Questions from Jeremy Fox about the LTEE, part 1 | Telliamed Revisited

  5. Pingback: Questions from Jeremy Fox about the LTEE, part 2 | Telliamed Revisited

  6. Pingback: The LTEE as meta-experiment: Questions from Jeremy Fox about the LTEE, part 3 | Telliamed Revisited

  7. Pingback: Funding the LTEE—past, present, and future: Questions from Jeremy Fox about the LTEE, part 4 | Telliamed Revisited

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