Funding the LTEE—past, present, and future: Questions from Jeremy Fox about the LTEE, part 4

This is the 4th installment in my responses to Jeremy Fox’s questions about the long-term evolution experiment (LTEE) with E. coli. This response addresses his 5th and 6th questions, which are copied below.

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  • 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?

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Past.  All in all, I’ve been very fortunate with funding for my research. My first attempt to get the LTEE funded was rejected, but around that time I received a Presidential Young Investigator Award from the National Science Foundation (NSF) that gave me considerable freedom to pursue the research directions that most interested me. Various grants have supported the LTEE since then including, for the past 10 years, an NSF LTREB grant (LTREB stands for long-term research in environmental biology).  LTREB grants are very small, but mine provides core support to keep the lines going.  Other funds are required to do anything more than some basic quality control and assays. My professorship at MSU—named after John Hannah, who was president of MSU for 28 years, about the duration of the LTEE!—has provided discretionary funds that have been invaluable, allowing us to explore new scientific directions and techniques as they become interesting and available, without requiring us to first secure funding. And the graduate students and postdocs in my group have been very talented, and they’ve often been awarded fellowships that fund the essential brain-power and hard work that has made the LTEE so successful.

Present.  I take proposal writing very seriously, always emphasizing both the overarching questions that have been with the LTEE since it began and the specific aims that arise from new discoveries and technical advances. One always has to make the case for why a particular project, individual, or team merits support. So I wouldn’t say it has gotten easier to get funding, especially given the decline in funding rates. But I do sense that reviewers have, on balance, become increasingly excited by the LTEE project over the years, as it has borne a lot of fruit. In fact, the NSF program officer has told me that the LTREB grant will be funded again for the next 5 years. During the pre-proposal phase (yes, a pre-proposal was required for a project that has run for over a quarter century!), the panel summary called the LTEE “this community’s Hubble Telescope.” Now that was certainly gratifying!

Future.  The big challenge going forward will be to secure funds that will allow the LTEE to continue after I’m gone. Many colleagues have told me that the LTEE must continue, and I agree. (I’m not planning on retiring anytime soon, but I think it’s wise to hand off a project sooner rather than wait to the last hour.) I like to call the LTEE the experiment that keeps on giving, so the challenge is to find a way to make that happen.

I realize that not every scientist will have the same good fortune that I’ve had. Indeed, by continuing “someone else’s experiment” a young scientist might even be viewed by some as unoriginal and thus unworthy of the privileges of tenure and funding. To overcome that stigma, I’d like to secure funds to ensure that, not only can the LTEE continue, but that its continuation is rewarding rather than burdensome to future scientists. After all, it comes with its own inherent challenges—including the fact that the populations are tended every day as well as management of the ever-growing collection of frozen samples.

My thinking is that each successive scientist responsible for the LTEE would, ideally, be young enough that he or she could direct the project for 25 years or so, but senior enough to have been promoted and tenured based on his or her independent achievements in a relevant field (evolutionary biology, genomics, microbiology, etc.). Thus, the LTEE would likely continue in parallel with that person’s other research, rather than requiring his or her full effort, just like my team has conducted other research in addition to the LTEE. The goal, then, is provide the future project leaders with the benefits of continuing the LTEE while relieving them of the most onerous burdens.

So as I’ve said before, “If you know anyone who would like to endow a million-year experiment, have them get in touch with me.”

[This picture shows the Hubble Space Telescope. It was taken on a servicing mission in 1997, and it comes from the NASA website.]

Hubble Telescope

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Happy 27th birthday to the LTEE!

The title says it all:  today is the 27th birthday of the long-term evolution experiment (LTEE) with E. coli.

Well, the title doesn’t really say everything. I also want to give thanks to the many people—not to mention the trillions of bacteria—who have made it possible for the LTEE to keep on going and giving.

So thank you to all of the students, postdocs, and colleagues with whom I’ve collaborated on this project. There are too many to list here, but you will find their names on the papers that have come from the LTEE. I’ll call out just two, on this occasion, for special thanks. Dom Schneider has been an amazingly talented and generous collaborator for so many years—in fact, our first co-authored paper on the LTEE dates back to 1999. And Neerja Hajela has worked with me for 20 years now, and she is the most organized, dedicated, and all-around wonderful technician and lab manager that one could ever have.

Special thanks, too, to Madeleine Lenski, who has tolerated my long-term affair with the LTEE, and who wisely advised me to keep it going on one or two occasions when I was looking in other directions.

[The image below shows the abstract from the first paper on the LTEE, which appeared in The American Naturalist in 1991. It is reproduced here under the doctrine of fair use.  Some of the conclusions have changed a bit as the LTEE has had more time and we’ve gathered more data—that’s science!]

Abstract 1991 LTEE

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The LTEE as meta-experiment: Questions from Jeremy Fox about the LTEE, part 3

This is the 3rd installment in my responses to Jeremy Fox’s questions about the LTEE (my lab’s long-term evolution experiment with E. coli), which he asked at the Dynamic Ecology blog. This response addresses his 2nd and 7th questions, which I’ve copied below. I like all of Jeremy’s questions, but I especially like his 2nd one because it forced me—and many readers, I hope—to think carefully about what experiments are and why we do them.

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  • 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…?
  • 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. 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?

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You’re certainly right, Jeremy, that experiments in the fields of ecology and evolutionary biology typically have two or more treatments. But it’s not an essential part of the definition of an experiment that it has that sort of structure. It would have been nice, perhaps, if the LTEE did have two or more environments and/or two or more ancestors, as you suggest—in fact, we’ve run several of those types of experiments over the years in my lab, and I’ll mention a few of them below.

The reason I didn’t do that with the LTEE, though, was because one of my core motivating questions (see part 2 of my response) concerned the repeatability of evolutionary dynamics across replicate populations. That’s a question about the trajectory of variances over time, which is challenging statistically because estimates of variances have large uncertainties. So if the LTEE had two treatments, I might have been able to say something meaningful about the differences between them, but I would have had less power to say anything about the among-replicate variances for either treatment. In other words, with respect to that motivating question, going from 12 replicate populations down to 6 replicates would have been risky.

It certainly would be nice to have more total populations, say, 24 or even more; and nowadays many labs use 96-well plates for evolution experiments, with each well a replicate population and liquid-handling robots to automate the transfers. When I started the LTEE, though, we worked with flasks (albeit small ones); 12 may not seem like too many, but when we run the competition assays to measure fitness, we then have replicate assays for each population and we analyze multiple generations simultaneously, so the students and postdocs running these assays are handling many dozens or even hundreds of flasks.

The LTEE as a meta-experiment

Stepping back a bit, I’d like to suggest that the LTEE is a sort of meta-experiment, to coin a term. (This idea echoes the question where you suggested that the LTEE has itself become a model system.) By “meta” I mean the LTEE transcends—goes above and beyond—what one usually considers an experiment because the LTEE enables experimentation at several levels.

Level 1: The LTEE as an experiment

First, it is an experiment in the sense that it set out to measure, under defined conditions and with replication, certain specific quantities, such as fitness trajectories. It may not be typical in having a single treatment, but the temporal dimension coupled with being able to analyze multiple time points simultaneously—that is, the “time travel” enabled by the frozen samples across the generations, including the use of the ancestral strain as an internal control in fitness assays—functions in much the same way from an analysis standpoint.

Level 2: The LTEE as a generator of new questions and experiments to answer them

Second, the LTEE has generated a number of new questions and hypotheses that are themselves amenable to structurally independent follow-on experiments. Let me give two examples. We observed fairly early on that several populations had evolved changes in their DNA metabolism and repair that caused their mutation rates to increase by roughly 100-fold (Sniegowski et al. 1997). Such “mutator” mutations can arise by hitchhiking, albeit only occasionally and stochastically, with beneficial mutations that they cause (Lenski 2004, see pp. 246-251). It wasn’t clear, though, whether they would necessarily increase the rate of fitness improvement, given the large populations and correspondingly large potential supply of beneficial mutations in the LTEE. So we designed a separate, shorter-duration experiment with some 48 populations where we varied the mutation rate, population size, and initial fitness of the founding ancestor, and assessed the resulting fitness gains over 1,000 generations (de Visser et al. 1999).

Another case is the “replay” experiments that Zachary Blount ran after one lineage evolved the ability to grow on citrate in the presence of oxygen, which E. coli generally cannot do (Blount et al. 2008). Zack ran thousands of populations that started from genotypes isolated at different times from the population that eventually evolved this new function, in order to test whether it could have arisen at any time by an appropriate mutation or, alternatively, whether it required first evolving a “potentiated” genetic background, or context, in which the “actualizing” mutation would then confer the citrate-using phenotype.

In both of these examples, the subsequent experiments, though separate and distinct from the LTEE, nonetheless emerged from the LTEE. That is, the questions and hypotheses tested in these later experiments were motivated by observations we had made in the LTEE itself.

Level 3: The LTEE-derived strains as useful ancestors for a variety of experiments meant to address existing questions

The third level of the meta-experiment involves questions that arise outside of the LTEE, but for which the LTEE generates a set of materials—specifically, strains—that are especially useful for experiments to address those questions. Again, I’ll give a couple of examples.

Many ecologists, physiologists, and others are interested in studying adaptation to specific environmental factors—such as resource availability, temperature, etc.—as well as examining possible tradeoffs associated with adaptation to those factors. One difficulty, though, is that by moving organisms from nature into the lab and allowing them to evolve under, say, different temperature regimes, adaptation to the shared features of the lab environments may well outweigh adaptation to the specific variable of interest. If so, that would interfere with one’s ability to identify the mutations and adaptations most relevant to the factor of interest, and it could also obscure tradeoffs that might be important if populations were already well adapted to the other aspects of the environment. With these considerations in mind, Albert Bennett and I took a strain from the LTEE that had evolved in and adapted to those conditions—the resources, pH, absence of predators, etc.—and we used it as the ancestor for a new evolution experiment where 6 replicate populations evolved under each of 4 different thermal regimes: 32C, 37C (the same as in the LTEE), 42C, and daily alternations between 32C and 42C (Bennett et al. 1992, Bennett and Lenski 1993). In that way, we could focus attention on temperature-specific adaptations, which were Al’s main interest, rather than having such changes overwhelmed by adaptation to the lab environment.

My second example where LTEE-derived strains were ancestors for an experiment meant to address an extrinsic question is one of an abstract nature. In this study, we quantitatively partitioned the effects of adaptation, history, and chance on phenotypic evolution by founding 3 replicate populations from 12 different ancestors—each one a genotype sampled from a different one of the LTEE populations—and we then let these 36 populations evolve in a new environment, where we changed the identity of the limiting nutrient (Travisano et al. 1995). By measuring the fitness of the 12 ancestors and 36 derived lines in the changed environment, we were able to disentangle and quantify the relative contributions of adaptation, history, and chance to the observed outcomes (see figure below). That is, adaptation measured the mean tendency for fitness to increase, history reflected the effect of the different starting genotypes on the fitness achieved, and chance the variation in the resulting fitness among the replicates that started from the same ancestor.

Sniegowski, P. D., P. J. Gerrish, and R. E. Lenski. 1997. Evolution of high mutation rates in experimental populations of Escherichia coli. Nature 387:703-705.

Lenski, R. E. 2004. Phenotypic and genomic evolution during a 20,000-generation experiment with the bacterium Escherichia coli. Plant Breeding Reviews 24:225-265.

De Visser, J. A. G. M., C. W. Zeyl, P. J. Gerrish, J. L. Blanchard, and R. E. Lenski. 1999. Diminishing returns from mutation supply rate in asexual populations. Science 283:404-406.

Blount, Z. D., C. Z. Borland, and R. E. Lenski. 2008. Historical contingency and the evolution of a key innovation in an experimental population of Escherichia coli. Proc. Natl. Acad. Sci. USA 105:7899-7906.

Bennett, A. F., R. E. Lenski, and J. E. Mittler. 1992. Evolutionary adaptation to temperature. I. Fitness responses of Escherichia coli to changes in its thermal environment. Evolution 46:16-30.

Bennett, A. F., and R. E. Lenski. 1993. Evolutionary adaptation to temperature. II. Thermal niches of experimental lines of Escherichia coli. Evolution 47:1-12.

Travisano, M., J. A. Mongold, A. F. Bennett, and R. E. Lenski. 1995. Experimental tests of the roles of adaptation, chance, and history in evolution. Science 267:87-90.

[The figure below appeared in Science (Travisano et al. 1995), and it is reproduced here under the doctrine of fair use.]

Adaptation, chance, history image

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Science Communication: Where Does the Problem Lie?

When concerns arise about the public’s understanding of science—say, on the efficacy of vaccines vs. their risks—I see many articles, tweets, etc., bemoaning poor scientific communication.

Communication involves multiple parties and several steps. The science must be published, discussed widely, explained openly, and eventually stated in terms that non-specialists can understand. It also must be heard—and not merely heard, but fairly considered, carefully weighed, and then accepted, rejected, or put on hold by the intended receiver.

That’s not all, of course. There are generally intermediaries—including teachers, reporters, doctors, business interests, politicians, religious leaders, and others—who must also convey the scientific information, but who may block, change, confuse, or distort the message either accidently or deliberately.

And none of this is a one-way flow of information. There are multiple voices, and there are feedbacks as questions are asked, answered in new words or with new evidence, and so on.

So it’s a complex problem, too complicated for a poll to shed much light. And of course, a poll here will get a highly non-random sample—mostly scientists, students, and others with an interest in science.

But perhaps some professional pollster or organization interested in the communication of science can develop a proper poll along these lines (with information about a respondents’ professions, ages, affiliations, etc.), and with proposals about how to improve the situation at the various roadblocks. (Or maybe similar polls already exist. Please feel free to suggest useful references in the comments.) It might also be interesting to run the same poll except with prompts about different issues such as vaccinations, global change, and evolution.

So here’s the poll:

If you had to say, which one of the following groups shoulders the greatest blame, and thus has the greatest room for improvement, when it comes to the problems of communicating science?

  • Scientists
  • Professional intermediaries such as teachers, reporters, and doctors
  • Other intermediaries such as businesses, politicians, and religious leaders
  • The public

[The image below is from the British Council / BBC World Service site on teaching English. It is shown here under the doctrine of fair use.]

Communication

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Questions from Jeremy Fox about the LTEE, part 2

This is part 2, I guess, of my response to Jeremy Fox from his questions about the LTEE over at the Dynamic Ecology blog.

It’s not an answer to his 2nd question, but it’s a partial answer to the first part of his 3rd question? (Have I got you confused already? Me, too.) Well anyhow, Jeremy asked:

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  • Did the LTEE have any hypotheses initially, and if so, how were you going to test them? This question probably just reflects laziness on my part, not having gone back and read the first publications arising from the LTEE, sorry. :-) I ask because, with just one treatment and no quantitative a priori model of how the experiment should turn out, it’s not clear to me how it initially could’ve been framed as a hypothesis test. For instance, I don’t see how to frame it as a test of any hypothesis about the interplay of chance and determinism in evolution. It’s hard to imagine getting any result besides some mixture of the two, and there’s no “control” or a priori theoretical expectation to compare that mixture to. Am I being dense here? (in addition to being lazy…)

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Short answer: Yes, the LTEE had many hypotheses, some pretty clear and explicit, some less so. (What, did you think I was swimming completely naked?)

Medium answer that will be fleshed out in later responses: Before we get to specific hypotheses—those formal, testable suppositions and predictions—I like to begin with general questions about how and why things are they way they are. So, what were the questions the LTEE originally set out to answer? (I emphasize “originally” because new or substantially refined questions have arisen over the course of the project, as we’ve answered some questions, made new observations, framed new questions, etc.)

What follows below are three overarching sets of questions that I hoped, long ago, the LTEE could answer, at least in the context of the simple flask-world that it encompassed. I present all three sets of questions  in some of my talks about the LTEE. However, in my talks to broad public audiences – like my Darwin Day talk at the University of Calgary next week – I focus especially on the third set of questions – about the repeatability of evolution – because I think it is the most interesting to people who are not necessarily evolutionary biologists or even scientists, but who are curious about the world in which we live.

Motivating questions for the LTEE

A few more thoughts: The first set of questions, about the dynamics of adaptation, include ones where I had clear  expectations that were testable in a fairly standard hypothesis-driven framework. For example, I was pretty sure we would see the rate of fitness improvement decelerate over time (and it has), and I was also pretty sure we’d see a quasi-step-like dynamic to the early fitness increases (and we did). Nonetheless, these analyses have yielded surprises as well, including evidence (and my new strong conviction) that fitness can increase indefinitely, and essentially without limit, even in a constant environment. In regards to the second set of questions, about the dynamics of genome evolution and their coupling to phenotypic changes–I’m sure these were part of my original thinking, but I will readily admit that I had almost no idea how I would answer them. Hope sprung eternal, I guess; fortunately, wonderful collaborators—like the molecular microbiologist Dom Schneider—and brand new technologies—wow, sequencing entire genomes—saved the LTEE.

 

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Questions from Jeremy Fox about the LTEE, part 1

Over at the Dynamic Ecology blog, Jeremy Fox asked me some interesting questions about the history, philosophy, and science of the E. coli long-term evolution experiment. Perhaps mistakenly—in terms of time management, not my interest!—I agreed to try to answer them … though over what time frame, I’m not sure. Anyhow, here is Jeremy’s first question followed by my (very) short and (too) long answers.

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  • 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.”

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The short answer: Life was good, and I wasn’t thinking about risk. Or as they say about investing: it’s better to be lucky than smart!

The long, non-linear* answer: I’d already had success with some shorter duration, more traditionally designed experiments (e.g., Lenski, 1988), and so it wasn’t a total shot in the dark—that is, I knew the LTEE would yield data. I also knew, though, that it was an unusually abstract, open-ended, and non-traditional experiment, and that it might not appeal to some people for those reasons. But I loved (and still do) the seemingly simple (but in reality complex) questions, issues, and hypotheses that motivated the LTEE.

I never thought of the LTEE project as a “lottery ticket”, but some follow-up work that grew out of it had that feel.** And, oddly enough, there was one lottery-ticket aspect of the research early on, although that reflected a lack of preparation rather than a well-conceived feature.***

Maybe I was overly confident, but I’d also say that I was pretty sure the outcomes—whatever they might be—would be “cool.” The questions were intriguing, and there hadn’t been many, if any, previous attempts to answer them quite so directly. Data would be forthcoming, and even if the results weren’t definitive, I felt there would be some interest in trying to interpret whatever data emerged.**** Plus, I knew enough about what would happen—based on the experiments I had already done—that I was confident that the data and analyses would be informative with respect to at least some of my questions. Also, the use of microbes to study evolution in action was still uncommon, so the novelty of the approach would ensure some interest among my colleagues—although let me emphasize that Lin Chao, Dan Dykhuizen, Barry Hall, and Bruce Levin, among others, had already demonstrated the power of using microbes for experimental studies of evolutionary questions.*****

I should also say, in case it’s not obvious, that I had no idea or intention that the experiment would continue for anywhere near as long as it has lasted—nor that it might, I now hope, be running long after I’m gone. I had previously performed some experiments that lasted several hundred generations, and as I saw the dynamics and thought about the math behind the dynamics, I realized that over those time scales I might be seeing the effects of only one or two beneficial mutations as they swept to fixation. That hardly seemed satisfactory for experiments to explore the structure of the fitness landscape. So I decided the experiment should run for 2,000 generations, over which time I expected there would be at least several fixations of beneficial mutations in each population (and I was right), and that would deserve calling it long-term. That would take a little less than a year, given the 100-fold dilution and 6.6 generations of re-growth each day.

Of course, propagating the lines for 2,000 generations was one thing—running the competitions to measure fitness, analyzing the data, writing the paper, responding to reviews, all that took longer. So while the experiment began in February 1988, the first paper (Lenski et al., 1991) was not submitted until August 1989, resubmitted September 1990, accepted that November, and finally published in December 1991. Meanwhile, the LTEE itself continued and the generations ticked by. The baseline work of keeping the populations going is not that onerous—yes, somebody has to attend to the transfers every day, but once a lab team reaches a moderate size, it’s not too hard to arrange. And I lived next to the campus in Irvine, so it wasn’t hard for me to come in on the weekends and holidays … and my wife still loves me, and my kids recognized my face ;>)

You also wondered whether some of the interesting possible and actual outcomes had occurred to me when I started. Definitely not! I had made a strategic decision to make the environment of the LTEE very simple in order to eliminate, or at least reduce, certain complications (especially frequency-dependent interactions and clonal interference). And while I think my planning kept these complications from getting out of hand, the tension between the simplicity of the experimental design and all the complications has definitely been part of its interest. That tension, along with time, the evolutionary potential of the bacteria, and the smart, talented, creative** and hard-working students and colleagues have made the LTEE what I call “the experiment that keeps on giving.”

Footnotes

*Hey, that’s what footnotes are for, right?

**I’ve thought that way about some follow-on work that uses the LTEE lines, but not about the project as a whole. Here are a couple of examples of “lottery tickets” that people suggested to me, and that won big. A former postdoc Paul Sniegowski, now on the faculty at Penn, wanted to know whether the actual mutation rate itself might be evolving in the LTEE populations. Bingo! Several lines evolved hypermutability and so, curiously enough, the first mutations we ever mapped affected the mutation rate itself (Sniegowski et al., 1997). Another example: Dominique Schneider is a molecular microbiologist in Grenoble, and we’ve collaborated for over 15 years. He thought we should look at whether DNA topology—the physical supercoiling inside the cell—might have changed in the LTEE lines. Well, I thought to myself, why would it change? But Dom’s lab will do all the work, so sure, why not look? And it turns out, sure enough, that DNA supercoiling changed repeatedly in the LTEE lines (Crozat et al., 2005), and it even led us to discover a gene not previously known to affect supercoiling (Crozat et al., 2010). There’s a lesson here, by the way—work with people who are smarter, who have different interests, and who have different skills than oneself.

***I actually started two versions of the LTEE—not one experiment with two proper treatments, but two separate experiments that differed in terms of both the starting strain and the environment. Unlike the successful LTEE, I hadn’t done any previous evolution experiments with the other ancestral strain and environment. Anyhow, I soon stopped the other version when the populations evolved a phenotype that made it very difficult to work with them. In brief, the populations evolved to make pinprick-sized colonies that were next-to-impossible to count in the assays we use to measure fitness. Who needed that headache! So, in a way, I guess I had two lottery tickets: I hadn’t done the relevant prior work for one of them, whereas the one that paid off was actually a pretty strategic gamble.

****I was at UC Irvine when I started the LTEE, and Michael Rose was one of my colleagues there. His work on the evolution of aging—postponed senescence—in fruit flies (e.g., Rose 1984) was an inspiration in terms of the importance and power of long experiments. We also spent a lot of time discussing fitness landscapes, the alternative perspectives of Sewall Wight and R. A. Fisher about the dynamics on those landscapes, and what experiments might tell us. Michael didn’t design, direct, or do the lab work for the first LTEE paper, but he helped me clarify my thinking and write the first paper on the LTEE (Lenski et al., 1991). Perhaps more importantly, his interest in the questions and issues made me realize that other smart people would also be interested.

*****I used to complain, mostly in jest, that “Evolutionary biologists say I’m asking the right questions, but studying the wrong organism, and microbiologists tell me I’m studying the right organism but asking the wrong questions.” I got that sort of response occasionally, but many people from both fields were very interested and encouraging. For example, I remember David Wake telling me, after one of my first talks about the LTEE, how much he liked both the questions and the approach.

References

Lenski, R. E. 1988. Experimental studies of pleiotropy and epistasis in Escherichia coli. II. Compensation for maladaptive pleiotropic effects associated with resistance to virus T4. Evolution 42: 433-440.

Lenski, R. E., M. R. Rose, S. C. Simpson, and S. C. Tadler. 1991. Long-term experimental evolution in Escherichia coli. I. Adaptation and divergence during 2,000 generations. American Naturalist 138:  1315-1341.

Sniegowski, P. D., P. J. Gerrish, and R. E. Lenski. 1997. Evolution of high mutation rates in experimental populations of Escherichia coli. Nature 387: 703-705.

Crozat, E., N. Philippe, R. E. Lenski, J. Geiselmann, and D. Schneider. 2005. Long-term experimental evolution in Escherichia coli. XII. DNA topology as a key target of selection. Genetics 169: 523-532.

Crozat, E., C. Winkworth, J. Gaffé, P. F. Hallin, M. A. Riley, R. E. Lenski, and D. Schneider. 2010. Parallel genetic and phenotypic evolution of DNA superhelicity in experimental populations of Escherichia coli. Molecular Biology and Evolution 27:2113-2128.

Rose, M. R. 1984. Laboratory evolution of postponed senescence in Drosophila melanogaster. Evolution 38: 1004-1010.

 

LTEE flasks repeating

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Putting GMOs on a Tight Leash

Two papers appeared in the latest issue of Natureone from Farren Isaacs’ group and the other from George Church and colleagues—that presented, developed, and demonstrated a strategy for limiting the spread of genetically modified organisms, or GMOs, in the event that they are accidentally released or deliberately applied to the environment.

My Involvement with GMO Discussions in the 1980s

I was actively involved in discussions about environmental applications and field testing of genetically engineered organisms back in the 1980s. As a postdoc in 1984, I had a short letter in Nature where I suggested a containment strategy for an early proposed application of genetically modified “ice-minus” bacteria. Later that year I attended a small meeting on environmental applications of GMOs at the Cold Spring Harbor Laboratory, and a short report was published in the Bulletin of the Ecological Society of America. As faculty member at UC Irvine in 1986, I served as a consultant on a report for the Office of Technology Assessment of the US Congress. I also co-organized and moderated a lively public debate on the benefits and risks of genetically engineered organisms between Jerry Caulder, who was CEO of a biotech company, and the distinguished ecologist Daniel Simberloff, an expert on invasive species.

At that time, one of the arguments—the “excess baggage hypothesis”—for the safety of GMOs was that genetically engineered functions would impose a metabolic burden and thereby reduce the fitness of the organisms, so that they wouldn’t be good competitors in nature. While that argument made some sense as a trend or tendency, it didn’t seem likely that it would apply in every possible case given the potential for new environments and/or compensatory adaptations to favor novel functions. In 1988, I wrote a review for Trends in Ecology & Evolution with a postdoc, Toai Nguyen, on the “Stability of recombinant DNA and its effects on fitness” that made these points.

As a result of my interest in and involvement with these issues, I was asked to serve on two expert panels—one convened by the Ecological Society of America (ESA), the other by the National Research Council (NRC) arm of the National Academy of Sciences—that wrote lengthy reports, both published in 1989. In both reports, the committees tried to emphasize that one needed to consider two different issues. (1) What, if any, were the potential problems that might be caused by the release of particular GMO? (2) In the event that some problem actually did arise, would the GMO (or its engineered genes) survive and possibly spread in the environment? Or would the problem be resolved by halting further applications of the GMO, because they would then simply die off?

(These panels were hard work, but through them I met some great scientists, including Jim Tiedje and Rita Colwell among many others.)

After that extensive involvement with this science-policy issue in the 1980s, my research tended toward more basic questions in the years that followed. Meanwhile, of course, there has remained substantial scientific, commercial, and public interest in the methods and applications of genetic engineering. The two recent papers in Nature reflect the latest efforts to ensure the safety of GMOs by putting them on a tight leash.

My Thoughts on the Recent Papers

I was asked to comment on the Nature papers by Malcolm Ritter, a science reporter for the AP, and he briefly (and accurately) quoted me in a short news piece that appeared yesterday. In light of a question about my thoughts on Twitter, I thought I’d share my full remarks here:

Using genetically modified organisms in the environment raises a couple of intersecting issues. One concerns the effects those organisms have. Of course, GMOs are intended to provide some benefit—say, for bioenergy or agriculture—but in some cases the GMOs might have secondary or unanticipated harmful effects. If these harmful effects occur, and if they outweigh the benefits, then one would like to be able to recall the GMOs from the environment—sort of like recalling cars when some problem is discovered after they’ve been sold. The challenge is that GMOs are organisms, they are alive and can reproduce, and so they won’t necessarily just go away if one stops using them. Over the years, different strategies have been proposed to ensure that GMOs will, in fact, just die off after they’ve done their job, but these strategies have had holes, such as the possibility that evolution might break whatever leash the scientists put on the GMOs so that they could be recalled.

These two papers, though, point the way towards putting GMOs on a very tight leash, one that is meant to be unbreakable, by changing the genetic code of an organism so that its replication becomes dependent on certain synthetic building blocks—amino acids—that aren’t found in nature. So by applying these molecules along with the GMO in some environment, the GMOs can replicate and do their job. But if the synthetic amino acids aren’t supplied, then the GMOs won’t be able to replicate further after they’ve run out, and so that provides a leash that should rein the GMOs in if there is some problem. Of course, there are a lot of technical challenges to pulling this off, because you can’t make the organisms so weak that they can’t do their intended functions.

And of course, extending this approach from microorganisms—the subject of these papers—to crop plants would raise all sorts of additional questions about nutritional value and safety. Those are different issues and not what these papers are about.

Coda: Does this approach ensure containment of a GMO? Probably not. There aren’t many guarantees in life, and evolution has a history (billions of years, in fact) of finding clever solutions that might not occur to engineers and scientists. Does that mean that we should not use GMOs in nature? Not at all. As our ESA and NRC reports of a quarter-century ago stressed, one should consider both the benefits of a particular environmental application of a GMO and its potential harm if something goes wrong. In those cases where the benefits are great, and the potential for harm is very small (both in likelihood and magnitude), then the issues of containment and recall after a release are less critical. But in those instances where the potential risks of some GMO are substantial—either in terms of the likelihood or the magnitude of adverse effects—then every effort must be made to put the GMOs on a tight leash or, absent that, do not proceed with the proposed application.

[The image below is one part of Figure 1 from the Nature paper, titled “Recoded organisms engineered to depend on synthetic amino acids” and authored by Alexis J. Rovner, Adrian D. Haimovich, Spencer R. Katz, Zhe Li, Michael W. Grome, Brandon M. Gassaway, Miriam Amiram, Jaymin R. Patel, Ryan R. Gallagher, Jesse Rinehart and Farren J. Isaacs.  This image is shown here under the doctrine of fair use.]

Portion Fig 1 from Rovner et al, Nature, 2015

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