So you want to do "experimental evolution"

Rich Lenski and his lab are getting a lot of well deserved publicity lately because they have published yet another awesome paper from their long term evolution experiment (LTEE). The success of the LTEE has no doubt sparked a bunch of researchers out there to go "hmm...I can do that!". I'm guessing that I was in third grade or so when Rich started the LTEE, and I have only been tangentially associated with the Lenski research lineage (who in my own experience are as smart and helpful as their mentor), but I've set up long-ish term lab passage experiments a couple of different times with different systems. There are a few things I've learned along the way that I think would be helpful to share with others jumping into the experimental evolution game, and hence this post. Please feel free to add suggestions to this list, or to contact me off-blog if you'd like to talk shop. The best tribute I can have for Rich is to provide as much help for the community as he and his students have for me over the years. I say this every time, but thank you very much!

1. Let the question guide your experiment.  We all have our favorite microbes (OFM), and the reaction that I've seen time and time again is to want to perform an evolution experiment with OFM just to see what would happen. I can assure you that OFM will evolve and adapt to passage conditions and will do so quickly, but what does this really tell you? My first piece of advice colors everything from here on out, and it's to focus on finding a question to ask and only then find the best microbial system to work with. E. coli works great for understanding general evolutionary principles, and in fact one of the most important questions to ask yourself should be "why not do this with E. coli?", but this would be a terrible system to study sporulation. Find the question that excites you and then find the system, it's easy enough to set one up if you know what to look for.

2. Once you've got the system, make sure you can measure fitness. A major piece of the LTEE is the ability to compare phenotypes and genotypes of cells from one generation vs. all others. For any evolution experiment to work, however, you need to be able to demonstrate that that evolution takes place. Competitive fitness assays are just one way to do this, but they are a very powerful test because they enable direct comparisons between strains. In order to carry out competitive fitness experiments, you need to be able to distinguish two strains from one another within a single culture under conditions that closely approximate passage. Rich's experiment directly competes strains that differ in arabinose utilization (Ara+/Ara-), which under the correct plating conditions enables you to visualize different strains by color (red/white). In many cases, such a simple phenotypic comparison isn't easily accomplished. In my first stab at an evolution experiment I was investigating the effect of natural transformation in Helicobacter pylori. Out of necessity, I designed my competitive fitness experiments slightly different than Lenski's because I was using antibiotic markers. Instead of directly competing evolved strains against each other, I would compete evolved strains vs. an ancestral "control" strain which was doubly marked with kanamycin and chloramphenicol. This isn't quite as elegant as I'd like, but I wanted to avoid confounding my evolution results with compensation for these phenotypic markers (in Rich's case, he spent a lot of time demonstrating that the Ara marker is a neutral change under his passage conditions, this often isn't the case for antibiotic resistance). At first I simply tried to plate out the same competition onto non-selective media and kan/cam media, but found that the variance in ratio of evolved/control strains was way too high to be reliable for fitness estimates. For instance, in some cases there would be more colonies on the kan/cam plates than on the non-selective media. To get around this issue and control for such plating variance, I decided to first plate the competition out on non-selective media and then to replica plate to the kan/cam selective conditions. This change allowed me to actually measure fitness using antibiotic markers and all was happy and good for the time being.  It completely sucked to replica plate everything, but it was the only way to get reliable numbers.

3. Carefully think about your passage conditions.  When you are performing a passage experiment, EVERYTHING MATTERS. Are you going to passage under batch culture conditions where there are such things as lag/log/stationary phase, are you going to passage in a chemostat, are you going to passage in vivo, etc...? Every change you make to your passage conditions can affect the results in subtle or not so subtle ways as selection will operate differently under different conditions. If you are passaging in vivo (mouse, plants, whatever), how do you control interactions between other microbes and your targets of interest or sample your focal microbe for freezing? Even the way that you passage your microbes in vivo can change selection pressures. For instance, motility will be a target of selection if you simply place your microbes on a plant leaf and select for infection BUT if you inoculate a leaf with a syringe (bypassing the need for microbes to invade), motility likely doesn't matter at all for infection and my guess is that you'll quickly get amotile mutants. Along these lines, always try to set up cultures using defined media even if you aren't quite sure that all components are necessary (plus, if you carry out LTEE long enough, cool things happen with the "unnecessary components"). With my H. pylori cultures, applicable to passage experiments with many pathogenic microbes, I was forced to use media which contained fetal bovine serum (FBS). The problem here is that every batch of FBS is different because every calf is different! I no doubt missed out on some fine scale evolutionary events simply because my H. pylori populations adapted to growth in different batches of FBS. LB is a little bit better, but remember that a major component of LB is actually yeast extract which can differ significantly from batch to batch and company to company. Something else to keep in mind is that LB media and other types of rich media provide a wider range of niches than defined media which can promote crazy scenarios of dependence between microbes (such as acetate cross-feeding).

What is your dilution factor going to be each passage? Even though effective population sizes are calculated based on harmonic means, differences in dilution can change evolutionary dynamics within cultures. Passage to densely and your cultures will spend more time at stationary phase than if you passage less densely (unless you time things perfectly). I always try to find the dilution scheme that allows me to catch ancestral populations just after they've started to hit stationary phase at some multiple of 24 hours. For H. pylori a 1:50 dilution achieved this every other day, for Pseudomonas stutzeri (in my experiment) a 1:1000 dilution achieves this every other day. I can't emphasize this enough, for your own sanity you want to design the conditions so that you can come in and passage at regular intervals!

4. How will you archive your populations? Another powerful characteristic of the LTEE is the ability to freeze populations to create a "fossil record". Carefully consider how frequently you want to freeze, and how much of a population you will freeze. The answers here will depend on the hypothesis you are testing. For frequency, consider that frozen cultures take up space that your PI can't allocate to other projects. One of my graduate school advisors still (maybe) has my H. pylori populations frozen down in her freezer (Sorry Karen! We're BSL2 now and I can finally take them off your hands!) even though she is not working with these lines anymore. As the generations pile up, you have to allocate more and more space. As for how much of the population you'd like to freeze, just remember that unless you freeze the whole culture you will be losing some of the population. This doesn't necessarily matter for high frequency genotypes but it does for the low frequency variants. Think of this as a good example of human influenced genetic drift just like an actual passage.

5. Catastrophes will happen. You can have the best planned experiment in the world, but that doesn't prevent your lab mates from "accidentally" (shifty eyes) knocking over your cultures. Before you start, make a plan for what happens if you lose a passage or if your freezer melts. For me, I always keep the previous passage in the fridge until the next passage is complete. Sure, it's a slightly different selection pressure than constant passage...but so is going into the freezer stocks. Also remember that catastrophes happen to everyone, even Rich Lenski, and it's a part of science. It sucks at the time, but exhale and move on. Trust me, you'll be much happier in the end.

6. Can you tell if you've cross-contaminated your experimental lines? Trust me again on this, cross contamination happens so figure out ways to identify it. I always try and alternate between pipetting and passaging phenotypically different strains. For H. pylori this meant having one set of strains be kanamycin resistant while the other set was not (had to perform an extra experiment after the fact to control for this difference). However, I was able to spot one instance where one of the lines had a low frequency of kanamycin resistant colonies. In the final analysis I threw out this line, which is why there are only 5 competent lineages in my Evolution paper. You might say "well Dave, I'm not that sloppy in the lab". That could be a very true statement, but I guarantee that if you run the experiment long enough you will have other people perform the passages. People make mistakes when they aren't as invested, haven't designed the experiments, and are reading from a written protocol. They don't mean to, but it's a fact of life.

7. Be curious. I suppose this works for every single experiment ever done...but curiosity is one of the most important characteristics for research. You will grow to love your cultures, to see them flourish and change. If you understand what to expect from your cultures, you can identify interesting yet unexpected events. Know what to look for and note any changes from this search image. That's where you find really cool results.

Should I go to Grad School?

Given I live in a desert which -- for the most part -- lacks colorful deciduous trees, the one way that I know it's fall is a flurry of activity concerning grad school applications. Since I teach an upper division core class for microbiology majors, I often get questions from students about what to do after undergrad. The first thing I tell them is this: The one burning memory that I have from graduate school is from sometime in the spring of 2004. It was my third year and I distinctly remember getting hit with the combination of relationship problems (long distance girlfriend and I finally broke up) and the 3rd year grad school treat of having a bunch of experiments with no hope of any successful results. Everything was so confusing. It was 2am, I was in the lab on a Saturday, the only car in any of the parking lots outside was my own, what the hell was I doing with my life? I sat there on the floor of the lab and cried. Seriously...even went fetal position a couple of times. With the perspective I have now, and looking back on all of my 5 years in graduate school, I can honestly say that getting a PhD sucked. It was a slog, a war of attrition. There were so many times I wanted to quit...BUT it was also one of the greatest experiences in my life. I don't regret any moment of it, and would do it again and again and not change a thing.

Why did I stay with graduate school? I had other options, I was a decently compensated intern at a pharmaceutical company all throughout undergrad and had gotten offers to remain on but turned them down. The 9 to 5 life and a daily routine wasn't for me. Sure I was turning down a good job, but I knew deep down that I'd be much more happy as a university researcher. I just always knew that I got bored with routines, with dealing with the same problems over and over again. Industry jobs seemed like scenes from the movie Groundhog day (I'm not entirely right or wrong about this). It seemed as though a job in academia would bring different challenges every day (and it certainly does). I wanted to be challenged, constantly, always from different angles. I knew that that kind of changing landscape of problems is what satisfies my brain.

It was during my time as an intern that I realized I really enjoyed asking questions, finding out how the world worked. I knew I didn't want to go to medical school, and graduate school just seemed like a good way to continue learning about the world. I remember being amazed that I could actually get paid (not a lot by comparison to other things, but enough) to go to school!!! I still can't believe that there are actual jobs that pay me to learn about the world and share what I learn with others. During my first of second year in grad school, my view of life solidified completely. It was at this point that one of the experiments I had thought of and designed actually worked. There I was, the only person at that moment in time that knew a new fact about how the world worked. It was thrilling, it was addictive...there is simply nothing like the rush you get when you get new experimental results. Sure, the paper that came of this experiment was pretty niche, but I was hooked. It's a combination of all of those feelings that helped me stay the research course even when things looked so incredibly bleak.

So should you go to grad school? It's definitely not for everyone, and as I say above, it really really sucks sometimes. It's simply a personal decision that I can only provide one perspective on. Every department and lab is different, and it's up to you to find a place to thrive. You have to find ways to motivate yourself to keep putting one foot in front of the other, to continue performing experiments even though 95% of them fail. Starting in grad school -- and continuing throughout academic careers -- you are surrounded by rejection. Rejection is never fun or easy, but over time it becomes easier to deal with.

I didn't think I'd make a ton of money with a PhD, I didn't even know if I'd eventually have a job. To this point there are a couple of things I can say now that I didn't know before 1) it's much easier to get an industry job with a BS or Masters than a PhD (companies can hire people and train them the way they want) and 2) it's easy to start out as a Masters student (or PhD) and upgrade to Phd (or downgrade to Masters) so your path isn't set the moment you start grad school. I didn't know what I wanted to do with my PhD when I started grad school (in the beginning I didn't think I'd actually be good enough at research to be a PI), but I knew that I enjoyed learning. My love of learning kept me motivated.

You don't finish grad school, you survive grad school. Your job as a graduate student is to make mistakes and to learn how to avoid making mistakes in the future. Your job as a graduate student is to consume every possible piece of information you can and learn to filter out good from bad. Grades really shouldn't matter to you anymore (in fact, if you can, take every class Pass/Fail). Classes are there not to prove that you can get an A, but to give you an opportunity to truly internalize relevant information. As a grad student you are much more likely to figure out some very small thing about the world that only a handful of people really care about, and that leaves your mom to question why you aren't a REAL doctor, than you are of actually making difference to human health. That's OK, it's all about building a foundation for the future wherever that may lead.

Looking back, there is one extra unexpected bonus that made graduate school worthwhile. Apart from the rush of science and research, grad school happened at a time in my life when I was truly becoming who I actually am as a person. I had moved across the country from NY to Oregon, and had started a life completely on my own away from the training wheels that undergrad life can bring. Some of my best friends to this day are people from my grad school cohort. People who were always up for a beer or pizza, people who shared similar experiences to me growing up as a bit of a science nerd. People from all walks of life, with very different perspectives, who nonetheless all found ourselves diving headfirst into research. I would be a very different person if I did something other than graduate school, because that was the moment in time when I really ventured out from the nest.

Grad school is one of the most difficult things I've ever done, and it's not for everyone, but for me it was completely worth it.

Replication and Studies of Host-Pathogen Relationships

There has been a buzz around the interwebs (and on actual paper too, so I guess it must be real!) lately about how difficult it can be to replicate published results. Much of the popular press has focused on a couple of articles from The Economist called "How Science Goes Wrong" and "Trouble at the Lab". There have also been a variety of well thought out posts from the likes of Jerry Coyne, Ian Dworkin, Chris Waters among others.

Some of the chatter has been along the lines of "BUT...REPLICATION IS A PILLAR OF THE SCIENTIFIC METHOD. THERE IS A SERIOUS PROBLEM IF MOST STUDIES CAN'T BE REPLICATED. WASTE OF THE MONEYZ!!! GRUMBLE GRUMBLE..."

At the top of this post I'm hoping to add a slightly more nuanced opinion here, followed by some unpublished results at the bottom to serve as a cautionary tale. I don't really disagree with worries about the state of science. Replication is of the utmost importance for research, and if results aren't robust there must be a way to keep track. Perhaps post pub peer review and comments will fill this particular niche. Experiments now are built on a foundation of experiments and models pioneered over years and decades. If you are interested in getting involved in a new research direction, one of the most important things to do is actually see if you can replicate foundational results in your hands in your own lab. That being said, biology is hard. Replication of single experiments under well controlled conditions can easily be thrown off by Rumsfeldian unknown unknowns. I remember hearing from someone (I want to say it was Paco Moore and that there is a paper somewhere on this which I can't find with quick google searches) that measurement of fitness in the context of Rich Lenski's long term E. coli experiment can be slightly altered by University water quality. In grad school I remember Patrick Phillips describing an experiment with nematodes where the assay would only work for about two weeks a year because the stars and sun and temperature aligned to yield the perfect experimental environment. It turns out that physiology and behavior of living organisms can be extremely sensitive to just about everything if you measure closely enough.

This problem is compounded even more when you are dealing with multiple living organisms, for instance,  when your research area is host-pathogen (host-symbiont, same diff) relationships. I can't speak for anyone that works with animal models, but I can definitely attest that plant immune responses are EXTREMELY sensitive to pretty much every stimulus you can think of. Since plant immune responses are dependent on cross-regulation across multiple hormonal pathways, even the slightest change in some environmental factors can completely shift the likelihood of infection. This is exacerbated by having to grow plants for multiple weeks before you can actually do the experiments, all the time worrying that some random lab malfunction (3am growth chamber overheating anyone?) will render batches of host plants unreliable. Different labs will have different water, soil, temperatures, humidity (low humidity in Tucson is the bane of my lab existence sometimes!), etc...When I started working on P. syringae and plants as a postdoc, I would get very frustrated at my inability to replicate other peoples published experiments. The more time I spent in the lab, the more I realized that that's just the way it is sometimes. Don't get me wrong, there are a variety of other reasons that replication may fail, but when you're crying into your lab notebook at 3am keep in mind that it's incredibly hard to control both the host and pathogen growth in the exact way that the published experiments were performed.

I'm guessing that every PI that works with phytopathogens and plants has a story where there was an interesting phenotype which couldn't be replicated when they moved to a different lab/University. As a postdoc I remember screening through 50 or so very closely related isolates of P. syringae pv. phaseolicola to look for subtle differences in virulence on Green (French) bean. The goal here was to minimize random genomic variability between strains, by choosing very closely related strains, so that I could hopefully quickly pin down genotypic differences underlying interesting phenotypic differences simply by looking at the genomes. Basically GWAS for microbes to use a looser term.  This was one of the experimental directions I started as a postdoc and was hoping to continue as PI in my own lab. One of the most solid results I had was a subtle difference in growth between two strains on French bean cultivar Canadian wonder. Canadian wonder is the universal susceptible cultivar to P. syringae pv. phaseolicola, which basically means that this plant was thought to be highly susceptible to all flavors of this particular pathogen. I had actually found that one strain (Pph 2708) grew 10-fold less than a very closely related strain (Pph 1516) in this cultivar (Fig. 1).

When I did pod inoculations, although the response was somewhat variable, there did seem to be some immune recognition of Pph 2708 compared to other strains (Fig. 2).

You can tell that there is something different in this inoculation because the water soaked halo is smaller for Pph 2708 than other strains, except for the avirulent mutant that lacks a functioning type III secretion system (Pph 1448a hrcC-).

So there it is, I've got two very closely related strains of P. syringae that slightly differ in pathogenicity. I have genome sequences for these (will link when I've stored up the strength to navigate the Genbank submission). There aren't many differences between them, on the order of hundreds of SNPs and tens of gene presence/absence. I had everything set up and ready to go to finish off the story once I got to Tucson and set up shop.

Here's where the problem arises...even though the result is solidly replicated under North Carolina conditions there is no growth difference between Pph 1516 and Pph 2708 in Tucson. A lot of strains I've worked with behave differently here in the desert compared to the land of tobacco and barbecue, and my guess is that it's because there is literally no humidity in the air. Since plant immune responses are linked to abscisic acid I'm guessing that the lack of humidity really annoys them when I take plants out of the growth chamber to perform inoculations. Not necessarily the lack of humidity per se, but the necessary change in humidity that accompanies taking plants out of the growth chamber. Yes, there are ways to Rube-Goldberg my way around this problem, and I have thought about a walk in growth chamber, but truth is other things worked better and I've concentrated on them. On top of that I'm using slightly different soil (what I could get my hands on), it's a different growth chamber, etc...Point is, I have a result that I would not think twice about publishing if only I hadn't tried to replicate this experiment in a different place. This happens a lot.