A model system is one that has features which make it a particularly good system in which to address whatever question the investigator has posed. That can be for a couple of reasons. One is that the system has features that make it easy to collect needed data. For instance, that’s why small organisms with short generation times are a good model system for long-term studies of population dynamics. Another is that there’s lots of relevant background knowledge, on which you can build in order to ask questions that couldn’t be asked without that background knowledge. For instance, Drosophila melanogaster is a model system for modern-day genetics and genomics not just because they’re easily and quickly reared in large numbers, but because Thomas Hunt Morgan used them to study inheritance over a century ago. Morgan’s work was built on by others, who couldn’t have done their work had Morgan not done his. And others built on that work to do work that they couldn’t otherwise have done, and so on. Perhaps the most powerful model systems are those that are good for asking many different sorts of questions, so that the answers to those questions can be linked together.
Of course, if you’re going to work in a model system, you’re obliged to first decide what question you want to ask, and then choose the model system that lets you answer that question. Or, if you insist on choosing your model system first, you’re obliged to restrict yourself to asking only those questions for which your chosen system is a good model system. For instance, protist microcosms aren’t a good model system for most questions to do with individual behavior, because protists don’t have much in the way of behavior and because it’s difficult to mark and track individuals.
That question-first, system-second approach is how I operate. It’s how workers in other fields operate. Developmental biology, genetics, and other fields of sub-organismal biology all are famous for their laser-like focus on a relatively small number of model systems. But it’s mostly not how ecologists operate. And before you say, “Well, ecologists can’t do that because ecology is all about variability and uniqueness,” you should recognize that our sister discipline of evolutionary ecology, which is just as concerned with variability as we are, increasingly focuses on “field model organisms” like threespine stickleback and anoles.
So ecologists could focus on model systems–but we mostly choose not to. Instead, what ecologists seem to do far too often for my taste is pick their system, then pick a question that in principle it would be interesting to address in that system, then cast about for some way to address that question in that system–often a partial, limited, flawed, or highly-indirect way. After all, if you choose your system first, how likely is it that that system will just so happen to be a good model system for whatever question you subsequently chose? And if pressed on this by some contrarian like me, ecologists too often respond by saying that their approach isn’t perfect but they’re doing the best they can within the constraints imposed by their system.
Which, as I’ve pointed out before, is like tying your own shoelaces together and then saying that it’s only feasible to walk slowly.
Look, there certainly are good reasons to choose one’s study system first. For instance, if there’s some rare species or threatened ecosystem that policymakers have decided ought to be conserved, then we have no choice but to go study that system as best we can. Or maybe it’s a question that’s only relevant in that system, so if we want to study that question we have no choice but to work in that system (although in that case, one might ask why you insist on trying to answer that question, rather than a more tractable question that could be asked in some other system) Or maybe it’s a question that’s only ever been asked in one sort of system, and for comparative purposes it’s really important for us to have some information from a contrasting system, even if that contrasting system makes it very difficult to get an answer. But if you’re doing system-first research for whatever reason, I think it is incumbent upon you to be up front about that. Don’t write or speak as if you’re doing question-first research, and then defend the quality of the answers you get by saying they’re the best answers you could get in your system.
Now before you say it, yes, focusing on model systems has a drawback: systems which make it easy or feasible to ask certain questions may provide a non-random sample of the answers to those questions. For instance, bacteria are a model system for experimental evolution, in large part because of their extremely short generation times. But bacteria also are asexual and have massive population sizes, and experiments on them tend to begin with no standing genetic variation. All of which might cause bacterial evolution experiments to provide results that aren’t representative of what would happen in sexual organisms with smaller population sizes and standing genetic variation. I suspect this argument is why so many ecologists are so reluctant to focus on model systems. “But that model system isn’t at all like my system! In my system, things might be different!” In response, I’d make three points.
First, in your system things might not be different. Just because a system has features that make it a good one for addressing some specific question doesn’t necessarily mean that the answers it provides will be biased. For instance, Thomas Hunt Morgan chose Drosophila melanogaster in part because it’s easy to rear lots of them–but why should that make Drosophila melanogaster any more or less likely than any other organism to exhibit Mendelian inheritance (a topic Morgan set out to study)?
Second, the putatively-unrepresentative features of model systems often can be manipulated, and so turned into testable hypotheses. For instance, you say protist microcosms are an unrepresentative model system in which to study population dynamics because they’re closed to immigration and emigration? Fine, open them up and test how immigration and emigration matter.
Third, and most importantly: Would you rather have a good answer to the question of interest (even an answer that might not generalize to all study systems), or no good answer? Isn’t some good answer, in some system, better than no good answer at all? Because that’s the choice you’re faced with when choosing between model systems and non-model systems to address any question of interest. Given the choice between a good answer from a model system, and a mediocre or crappy answer from a non-model system, I know which one I’d choose.*
I want to conclude on a positive note, by emphasizing the tremendous opportunities that ecologists are missing by not focusing more on model systems. Remember, one reason why model systems are model systems is because of cumulative accumulation of knowledge. The more you know about a system, the more, and more quantitative, and more sophisticated, and more difficult questions you can ask. Especially in model systems that are good models for more than one sort of question. Lately on this blog we’ve been talking a lot (and will be talking further) about the challenges of “scaling up” and “scaling down” in ecology. Well, the best model systems are ones in which it’s easy to work at multiple scales, thereby making it possible to link from one scale to another.
So what are, or should be, the big model systems in ecology? Systems in which we can easily and cheaply conduct measurements and manipulations on individuals, populations, communities, and ecosystems? Systems we can work with both in the field, and in the lab? Systems with relatively fast dynamics? Involving an organism about which we already know a lot, about everything from its genome sequence, to its individual physiology and life history, to its behavior, to its population dynamics, to its interactions with other organisms, to its biogeography, to its role in energy flow and material cycling? What do you think, class? Any ideas?
Meg: [raises hand] Oooh, I know, I know!
Me: [ignores her because she’s always first to raise her hand] C’mon, someone else. What’s the first system that comes to mind when you try to think of the ideal model system for ecology?
Meg: [half-stands up, raises hand so high she’s at risk of pulling a muscle]
Me: [sighs] Ok, Meg?
Me: Yes. There’s no need to shout, but yes.
Yes, as my dynamic colleague Meg can no doubt attest, Daphnia, and the ponds they live in, are perhaps the ultimate model system for ecology, for all the reasons listed above. I do think some ecologists (including here at Calgary) are starting to treat Daphnia the way geneticists and evolutionary biologists treat Drosophila melanogaster. Which is awesome–they should keep doing that! They’re setting a great example for the rest of us.
Of course, ecology can’t live by one model system alone. Here are some other possibilities:
How about freshwater algae? (Oh, sorry Chris, didn’t see your hand up, were you about to suggest them?) As Chris can attest, we know an awful lot about their physiology, growth, reproduction, resource use, population dynamics, and biogeography, and about interspecific variation in all those things. We probably have, or could obtain without too much difficulty, genome sequences for many of them. They have fast generation times. They’re easy to grow and manipulate in the lab. They’re even of interest for biofuel production, so there’s an applied angle too. And while we can’t easily manipulate them directly in nature, we certainly can and do manipulate lots of biotic and abiotic factors that affect them. And of course, they’re consumed by Daphnia, making the two of them together a model predator-prey system.
Other ideas for key model systems on which ecologists ought to focus more? There’s the aforementioned evolutionary ecology models, threespine stickleback and anoles, of course. How about Arabidopsis? We don’t know tons about its field ecology yet–but that should be easy to rectify. Maybe aphids and their host plants and parasitoids? Maybe bacteria and phage? Bacteria and phage are great for asking questions at the interface of ecology and evolution, and already a model system in genetics and evolution. They would mostly be a lab-based model system for now, but I’m starting to see cool work coming out on their field ecology. Note that I would not suggest “protist microcosms”. They’re fabulous–but for too limited a range of questions to serve as a model system for a large body of ecologists, or for a large chunk of ecology (or maybe I’m just saying that in order to keep y’all from crowding into my system and competing with me).
So what do you think? Aren’t you a little bit sick of working your butt off to get partial, limited, flawed answers to our biggest questions? Wouldn’t you rather work your butt off and get a really complete, definitive answer for once? C’mon, take the plunge–start working in a model system! I’ll bet Meg will even send you a few Daphnia cultures to get you started. 😉
*Well, in an ideal world with no opportunity costs, I’d rather have both answers. I’d rather have as much relevant information as possible from as many systems as possible, including both good information from model systems and much-less-good-but-hopefully-better-than-nothing information from non-model systems. But of course, opportunity costs are ever-present.
There’s a subtext here which maybe I ought to bring out into the open. Ecology is hard, and so ecologists are always on the lookout for “shortcuts” that make it easy. Like, say, the idea that you can infer something about contemporary coexistence mechanisms just from plotting coexisting species on a phylogeny, or the idea that you can detect effects of competition on species distributions just by randomizing a species x sites matrix, or the idea that you can infer something about the strength of local species interactions by plotting local vs. regional species richness. In this post, together with various previous ones, I’m implicitly arguing that, if you want your life as an ecologist to be easy (well, as easy as possible), you should quit choosing your system first, and then casting about for some putative shortcut to ask the questions you want to ask. Because those shortcuts generally aren’t shortcuts, they’re actually dead ends. Instead, you should choose your question first, and then choose a model system that makes it easy to answer that question in a *direct* way, without resort to putative shortcuts.
There’s also a second subtext here. Because ecology is hard, ecologists are either not much bothered by, or are very quick to excuse, the flaws and limitations of their putative shortcuts. Because ecology is hard, ecologists not only are very quick to look for shortcuts, they’re very slow to admit that those shortcuts are actually dead ends. Maybe we’re so used to thinking of ecology as hard that at some level we don’t expect our shortcuts to be all that short, or even to get us all the way to our destination, and so aren’t too bothered when the kid in the back seat (that’d be me) starts whining “Are we there yet?!” (causing the ecologists driving the car to yell: “We’ll get there when we get there!”) 😉 This post is trying to break ecologists out of that mindset, by arguing that, in appropriately chosen model systems, ecology is *not* hard (or if you like, the *right* way to make ecology easy is to work in a model system)
Probably should’ve taken a cue from Brian and titled this post “Ecological masochism?” 😉
Well we use periphyton (freshwater attached algae) there are a lot of unexplored possibilities because of its resemblance with terrestrial vegetal systems. It has a close relationship with bacteria (nutrient recycling) and there are small invertebrates and protist that live within (herbivores and predators). So is beautiful because you have everything. And also we work with two species of amphipods (Hyallela) that also feed on periphyton.
Following the first Hamming rule (http://bit.ly/t6nwTD) we are destined to success.
This post reminded me of my search for a PhD system. I wanted to study conflicting selection by mutualists and antagonists on floral traits (a remaining question in floral evolution is whether selection on floral traits is mostly due to pollinators or not). So I had my question and the expectation that pollinators and pre-dispersal seed predators would be likely organisms find conflicting selection, if it exists. I choose to work in the genus Penstemon in part because it was as close to a model system as I could get to address my question (there is a bunch of folks working on various pollination and evolutionary questions in the genus and I found pre-dispersal seed predators in the species growing close to campus). So off I went to study conflicting selection and ended up with a cheeky subtitle to my defence talk “What I learned while trying to study conflicting selection on floral traits”. I didn’t see conflicting selection because the seed predators weren’t ever driving selection on the traits I measured. Damage was variable and they probably do care about plant-traits but not the ones I looked at. So in a round about way, I did answer that selection on flowers was mostly due to pollinators but it isn’t very satisfying because I wasn’t able to figure out what the seed predators were up to. So they’ve just been reduced to a line in the methods of papers with another focus. I have some new data this year, so maybe…but I’m not expecting anything new and it wasn’t the reason I was collecting the data. It just goes to show that you can try to choose a ‘model’ system to answer questions but it doesn’t ensure success. Maybe I should have been working on daphnia!
Interesting. I was at a working group where this claim got debated over beers just a month ago (I recall Andrew Hendry, Jessica Hellmann and Paul Leadley in the thick of this discussion)
I essentially agree. Ecology gives too much license to the “ooh – my organism is cute – I want to go commune with it and I’ll find a way to do research to pay for it” impulse. We might be further along as a field if we had the bloodless detachment from our study systems as, say, physicists do from electrons. Physicists do get excited about electrons but its all in the knowing, not just in the coexisting.
That said, two thoughts:
1) My first graduate school interview somebody told me there are questions people who pick their question then find the system to answer it (as you advocate) and there are systems people who just stay with one system their whole career and follow it where it takes them. Now while the follow your system approach can devolve into the “I love my system” approach, it can also lead to good science. That’s how evolution got Anoles and sticklebacks to begin with. It perhaps requires a great deal of rigor to make the “follow my system” work, but it can.
2) I think genetics, and even to some extent evolution, have it easier. Genes in Drosophila work pretty much the same as genes in humans (as do evolutionary principles). However, while – as you know – I am a fan of microcosm work, there are limits to how much Daphnia will tell us about trees. There are even a lot of limits on what Arabidopsis can tell us ecologically about trees. Thus we need a tree “model system” – and that starts to be an oxymoron – how can you call something with a generation time of 100 years a model system? Can we let Anoles stand in for all vertebrates? maybe to some degree. In our over beer discussion of this, I think we decided we would need about 50 model systems in ecology. Not quite as satisfying as the 3 or 4 in genetics or evolution, but still a big step up from where we are today.
A few more candidate “model systems”
Center for Tropical Studies Forest plots (e.g. BCI)
Grasslands have nice properties of temporal and spatial scale (as an aside I wonder if one would classify Tilman’s Cedar Creek as a “follow the system” or pick the system to answer the question?)
Serengeti (we’ve studied the heck out of this place)
Eastern decidious forest trees and understory (argubably the most studied ecosystem not coincidentally because it is the most densely populated)
I’m having a hard time thinking of animals that are candidates – we ecologists seem to be very diffuse in our coverage of the animal kingdom.
Writing this list – it strikes me that places are model systems in ecology as much as specific organisms (which makes sense to the extent ecology is a field rather than lab oriented science)
Anyway – a very thought provoking post. Thanks.
“Ecology gives too much license to the “ooh – my organism is cute – I want to go commune with it and I’ll find a way to do research to pay for it” impulse.”
Wow, I carefully avoided putting it that way in the post! Nice to have somebody else besides me going a little overboard around here for once! 🙂
Re: your point 1, I don’t know that evolutionary ecology ended up with anoles and sticklebacks as model systems entirely through a system-first approach. At least not system-first in the sense of “I’m picking this system because I want to commune with lizards/fish and I’ll figure out some sort of research to do on them”. For instance, threespine stickleback species pairs in postglacial BC lakes are kind of a “best of both worlds” situation. It’s a case of an intriguing pattern in a particular system (hey, how did these very young lakes each end up with a pair of stickleback species, one benthic, one limnetic) that also happens to be a nice model system for studying the processes that gave rise to that pattern (stickleback are small, manipulable, breedable in the lab, etc.)
Your point 2 sounds like an elaboration on my passing remark that one reason to take a system-first approach is comparative: because ecology is variable, it’s often important for us to ask the same question in a range of systems, even if that question is difficult to address in some of those systems. I agree with that point.
Your list of suggested model systems is very good.
Re: Dave Tilman’s grassland work at Cedar Creek, you’d have to ask Dave, but I think it’s a mix of system-first and question-first. Grassland plants are a good model system for asking questions about resource competition and coexistence–but not quite as good as the algae in chemostats that Dave began his career on. I’m speculating here, but my guess is that Dave moved to grasslands because he needed to convince people that his ideas about resource competition mattered for “real” organisms in “the real world”. So he moved to a terrestrial field system to have a contrast with the algae–but he picked the terrestrial field system best-suited to asking the questions he wanted to ask (and a terrestrial field system quite likely to reveal an important role for resource competition–the soil at Cedar Creek is really sandy and nutrient-poor, which puts a big premium on nitrogen acquisition and retention by plants). Again, I’m speculating on this, and one can certainly imagine various other system-based and question-based reasons for Dave moving from algae to grasslands.
Now that you have so helpfully singled out my most outrageous statement 😉 I feel a need to clarify …
1) I am not claiming all ecology is done from that motive
2) I am not claiming I am immune to it – my easiest career path would have been to become an econometrician and I would have made a lot more money, but I find a walk in the woods too compelling to pass up.
But I stand by my claim that it is real and present.
Economists and social scientists regularly have to deal with the fact that they are essentially studying themselves and thus need to be on guard for/deal with unavoidable biases.
Ecologists don’t study ourselves per se, but we study something we are coevolved with and which is wired into the more basal parts of our brain. I think it is a fact of life we are less objective than say a geologist or physicist. The best thing to do with such situations is to discuss them and not avoid them. And I think your post highlights a case where perhaps this bias impedes progress and I don’t think it will change unless we pull out into the light of day the reason why (phew – do I now sound suitably academic on the topic while saying the same thing!?)
One more comment, on the number of model systems needed in ecology vs. other fields. I agree that we’ll need more model systems in ecology in order for them to collectively cover all the big questions we want to ask. But I do think there’s such a thing as too many. It’s a matter of opportunity costs–money and effort put into developing system X into the 51st model system in ecology might be better spent taking advantage of existing model systems.
Certainly, that’s the way cell biologists and developmental biologists think. In those fields, if you apply for a grant to develop organism X into a new model system, you’ll often get strong pushback asking you why you’re not just asking the questions you want to ask in C. elegans or zebrafish or whatever. The attitude is very much that “We already have enough model systems, you’re going to have to work hard to convince us that it’s worth trying to develop any new ones.” But somehow, I doubt that many ecological grant applicants have ever been told “That’s a great question, but you should ask it in some other system.”
The rocky intertidal is another good example of an ecological model system, albeit only for a limited range of questions. And desert annual plants are a model system for studies of Chessonian (i.e. modern) coexistence theory, not just because they’re easy to manipulate in the relevant ways, but also because their life histories are well-described by discrete-time mathematical models that are easy to analyze in a Chessonian way.
It’s actually not too hard to come up with ecological systems that are models for a limited range of questions. Much harder to come up with ones like Daphnia and the ponds they live in, which are models for a wide range of questions.
As for animal model systems, besides the suggestions in the post, like Brian I’m struggling to name any, even for a limited range of questions. Animals are mostly hard to work with, perhaps unless they’re small and naturally confined to ponds. For instance, amphibian larvae were once a model system for studies of competition and predation. (My supervisor Peter Morin did a lot of that work, before deciding that he really wanted to ask questions about how species interactions affect population dynamics, prompting his move to protist microcosms. A fine example of choosing your system to fit your question) Trying to think of something terrestrial…How about granivorous desert rodents? Model systems for studies of foraging behavior, and people have done long term experiments on them to look at competition and coexistence. Is that a system lots more people should be taking up?
Great post and comments! As a first year PhD student, I’m thinking about this exact question for realz. I am struggling with the “but animals are cute”, or more specifically, “but mammalian carnivores are awesome!”, issue. I’m happy to hear a shout out for granivorous desert rodents, but can anyone think of a terrestrial carnivore model system? Think of this as your opportunity to help shape the future of ecology 🙂
I’m starting to think (in agreement with Brian) that a place may be a more interesting system than an individual organism. Or maybe by interesting I mean easier to tackle.
Sorry, can’t think of any terrestrial mammalian carnivore that’s a good model system, even for questions about terrestrial mammalian carnivores. The only exceptions might be specific populations that have been intensively studied for a long time. Wolves on Isle Royale, or lions in the Serengeti. Maybe Yellowstone wolves and bears.
Which gets to your comment about places as model systems. All the “model places” are places that happen to have been intensively studied for a long time. It’s that cumulative long term knowledge that makes them model systems now. Permanent forest plots like BCI, the Serengeti, LTER sites, etc. Basically, if you study a non-model system hard enough for long enough, it eventually becomes a model system.
Interesting. I, too, am of the Question Then System philosophy. Where I diverge from you here (and it wouldn’t be fun if I didn’t) would be in the idea of a limited number of model systems. A limited number of model systems means, by definition, a limited number of questions we can ask.
Now, you may be intimating that we should focus on systems where most basic ecological questions can be easily asked and answered. (maybe). I would argue that you are therefore privileging questions regarding basic ecological theory, and not those that address how basic theory is made manifest in real-world conditions – i.e., questions of applied ecology and natural history.
Indeed, if you don’t confront simple findings gleaned from model systems with data from the more complex world in non-model systems, that parameter that may be 0 in your model system, and hence you have rejected as being important, may come back with a vengeance. The trick, though, is to chose a system that, again, allows you to ask whether the results from your model system are worth a hill of beans in the more complex world, of if there is something that they, too miss.
So, question first. Then system. But remember that clean simple model systems may limit not only questions, but also answers.
Not sure I can say much in reply that I didn’t say in the post or other comments. Yes, if you have reason to think that the answers you get from your model system will be affected by the very features that make that system a model system, then you need to be aware of that. And yes, if the answer to a question is likely to vary among systems, then ideally (for comparative purposes) you’d like to have both a good answer from a model system, and less-good answers from non-model systems.
My post is explicitly not about applied questions or natural history questions, which by their nature are tied to specific systems. As I said in the post, with those sorts of questions you have no choice about the study system. Your only choice is whether or not to pursue the question at all. None of which has anything to do with model vs. non-model systems, save that it’s incumbent on you not to fool yourself into thinking that you’re doing anything other than system-first research.
Preach it, Jeremy! I’m glad you’re spreading the gospel of Daphnia. 😉
Seriously: I don’t know where I fall on the system-first vs. question-first spectrum. Since I’ve been working on Daphnia since I was an undergrad, you could certainly make the argument that I am a system-first person. But I have tried working with other systems, but keep coming back to Daphnia since I think they work best for the questions I’m interested in, which is more question-first. One problem I have with people suggesting that people be purely question-first: if one is not really familiar with a study system, it is possible to make silly mistakes or not take things into account that are really important (but not initially obvious), or to waste a lot of time spinning one’s wheels trying to do simple things, just from a lack of knowledge. So, as with most things, I end up falling in the middle, and think it’s important to have a system you know well, but also to make sure it’s well-suited to the questions you’re tackling.
To get more specific: My lab has recently begun working with an a new parasite, Pasteuria ramosa. This has been the subject of lots of work by Dieter Ebert, Tom Little, and their labs, so it’s not a totally new system, but we’re pairing it with a different host than they have, and it’s not a parasite I had worked on before. I felt the need to switch to this system in part because I wanted to work on questions related to parasite evolution, which was something I couldn’t do with our yeast parasite system (since it shows surprisingly little variation). But I wasn’t having such an easy go of getting infections going in the lab — it was enough to do some work, but progress was slow. Then I hired Stuart Auld as my postdoc. Stu came from Tom’s lab, and had tons of experience with Pasteuria. When he showed up, he pointed out that Pasteuria spores stick to the walls of centrifuge tubes, and so they need to be ground with an automated pestle for a long time. This is a seemingly trivial detail (and, as far as I know, has not been included in the methods of publications), but makes a big difference in the ability to carry out infections, and to quantify parasite fitness. We had been inadvertently throwing away huge numbers of spores, since they were stuck to the walls of the tubes without us realizing it.
Time to go stretch to deal with that pulled muscle. You really shouldn’t have made me wait so long. 😉
Yeah, as I said in the post, question-first science can look like system-first science if you’re always asking questions that can be asked in a particular system. That describes me with microcosms. I’m a question-first person–but for the most part, protist microcosms are the right system in which to ask those questions, so I always end up working in that system. I do think there are people who don’t get that. In my old post defending microcosms, I noted Steve Carpenter’s complaint about people treating microcosms as an end in themselves. I think what Steve forgot is that a frequently-employed means to an end is still just a means to an end. I ride the bus to work every day, but I don’t ride the bus for its own sake, it’s just the best way for me to get to work. Similarly, just because I work a lot in microcosms, or you work a lot with Daphnia, doesn’t mean we *only* care about those systems for their own sake.
Little tricks that don’t ever make it into the Methods sections of papers could be a whole post. We microcosmologists definitely have our little tricks. And our key bits of background knowledge, passed down verbally from microcosmologist to microcosmologist but never revealed to the uninitiated. I just had a student from another university come visit my lab for a few days to learn the tricks and the lore. He’d been trying and failing to repeat some classic protist microcosm work that, for seemingly trivial technical reasons that only we protist microcosm folks know about, is extraordinarily difficult to duplicate.
Jeez, how could I forget flour beetles as a model system for population ecology?! Again, a model system for only a rather narrow range of questions, but still–what a model!
I’m an applied ecologist so I’m not entirely convinced by your model system argument. That said, since you’re casting about for animal model systems, and if you’re willing to scale-up, Gypsy moth, larch budmoth, and spruce budworm are three excellent ‘model systems’ for landscape-scale population dynamics.
Having just spent a week down at my field site, I’ll put in a shout out for desert rodents. Rodents are really a model system already for population ecology and used to be one in the 60s, 70s, 80s for community ecology. Why? You can get high numbers and species richnesses with “relatively” (for vertebrates) little effort. Many of them have been well studied and thus we already know a lot about their natural history, you can track individuals, they operate at workable spatial scales that allow you to ask both local community and more regional questions, they can have strong impacts on plant communities and nutrient cycling, mouse genetics are well studied and becoming more so and, well, I could go on. You might argue I’m biased since they are what I work on, but I actually started graduate school wanting to work on a different system and I drifted to desert rodents because they are a great model system.
We should remember in this discussion of model systems that model systems arise from a combination of the characteristics of the system and a long history of work that makes them tractable to work with and interpret results from. Someone’s special system/taxa today might be our best model system for answering a new set of questions tomorrow. Would the BCI 50 ha plot be a model system today if Hubbell, Condit, and Foster hadn’t put so much work into it and given the rest of us a baseline for being able to use and understand that system?
For morethangray: I can think of a couple of mammal systems that probably qualify as model systems for mammalian terrestrial carnivores: Isle Royale, Craig Packard’s lion system, and I think Yellowstone is rapidly reaching that status as well.
Shorter Morgan: what Jeremy said. 😉
Just teasing Morgan, it’s reassuring that someone who actually knows something about mammals has the same thoughts I had. Ditto for how non-model systems can become model systems just by being studied for long enough.
Sorry Jeremy. Still a bit fried from the field. I had interpreted your comment as a question about whether desert rodents might be good, not an endorsement for them….
No worries, it was a tentative endorsement–which I actually made in the hopes of drawing a comment from you!
Looks real interesting, looking forward to reading this one when time allows Jeremy.
Sometime before my Detroit Tigers being to dismantle their NL foe in the World Series preferably.
Heh, every chapter of my dissertation involves strange uses of the model organisms we know and love, including:
-Pitcher plant communities
As a result, talking to hardcore field ecologists about what I do generally elicits an eye-roll or gag motion.
I’m confused on exactly what you mean by the term “model system”. Presumably, the implication is that since it’s a model system, it’s characteristics are generalizable. For theoreticians, the ultimate model system is a computer simulation. Anything done on actual organisms is going to be limited in how generalizable the results therefrom are.
No, a model system isn’t necessarily representative or typical of other systems (which I take it is what you mean by “generalizable”). It’s just a system that has features that make it easy, or as easy as possible, to address the question asked, and to do so in the most direct or effective way possible.
OK, thanks for that clarification Jeremy.
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How do you see this claim:
Just saw it, will be blogging about it in the Friday linkfest post.
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Some wonderful insights here. But it seems an implicit assumption is that the “point” of ecological research is to find out the “answers” (correct underlying dynamics) of ecology as quickly as possible. While this may seem obvious, it is certainly not unequivocally true. While all of us who pursue science as a career (or even pastime) are (I’d say) trying to figure out “objectively correct dynamics/rules” of the world, finding them as fast as possible is not necessarily the goal. Nor is finding “the most important answers” necessarily the goal. (More on this in a moment.) We do what we do for some mixture of drawing personal satisfaction from it, and from finding/thinking it useful. While your points about opportunity cost are well taken, the question for many (especially those far on the side of “I study my system because it’s cute” approach) would be “What would be the point getting better answers to questions in a system I don’t enjoy?” At the extreme, of course, if we were able to determine all the best model systems, should all researchers switch to them even if they no longer enjoyed what they did? Or should they be “obligated” to enjoy the most logical study systems in some way? (Ok, that’s obviously a bit hyperbolic.)
Things, to me, get more complicated when you add the question of “the most important questions”, i.e. “What are the most pressing things to study that will have the largest practical significance?” (Alternatively, that could end in “…that will lead to the greatest increase in our understanding of the world?”, a question that is different in both obvious and subtle ways.) As someone who works with both social and natural science, it increasingly seems to me that the most “important” questions (those most imperative to answer in order to solve real-world problems) lie in the social realm. It is not at all true, of course, that natural science research is not important to solving problems of biodiversity loss, climate change, etc., but rather it does seem to me that the “rate-limiting step” to solving most of these is progress in social change. Indeed, I think the argument could be made that the most effective thing for scientists to do to address these pressing issues would actually to be to get involved directly in attempts at grassroots social change rather than continue researching. In terms of opportunity costs and the urgency of the problems that face us, and the profound need for social mobilization, this may be more effective than all the good science in the world.
So I’ve spun off into rambly-town here, but at heart is a slippery slope, or (as you discussed in your post about salesmanship) a spectrum that can appear to have a concrete division. From a utility point of view, focusing on fewer model systems may generate better ecological knowledge faster. But human utility is drawn from subjective enjoyment as well as (for scientists at least) the accumulation of nominally objective knowledge. So insofar as people enjoy a panoply of systems more than fewer model systems, an argument can be made for continuing as things are. If the argument is net societal utility, then accumulating knowledge faster (or rather, more efficiently) actually is important and represents social opportunity costs, but then taking it farther still, one should reasonably consider the social utility of academic ecology and academic research more broadly. And while I would never argue these are without utility (or haven’t shown their extreme utility in the past!), I would also say few of us have seriously undertaken a study of how “useful” what we do is compared to other professions (and indeed, parameterizing that utility function would be… challenging). But if we’re talking opportunity costs, it is possible that time and resources spent as academic ecologists could be “better spent” as elementary school science teachers, in terms of getting us more quickly to important social changes/fixes.
This started out so easy to say in my mind… Yikes. Ok, TL;DR: I actually agree with your well-made arguments, but I think adding in personal utility of studying different systems complicates things. Adding net social utility *immensely* complicates things. I think we should move closer to evaluation systems that take some account (or greater account) of opportunity cost and utility, such as the comment about justifying the use of something other than, say, zebrafish in molecular biology. But if we extend that idea further, we may also have to face up to the fact that opportunity cost and utility calculations similarly may not necessarily favor many of our other professional choices–such as choice of profession! I don’t have anything to propose on this as of yet, but I think it’s worth noting.
For those curious, some resources on the need for science in effective policy:
Hagerman, S. M., H. Dowlatabadi, and T. Satterfield. 2010. Observations on drivers and dynamics of environmental policy change: insights from 150 years of forest management in British Columbia. Ecology and Society 15:2. (Open access: http://www.ecologyandsociety.org/vol15/iss1/art2/)
Jasanoff, S., editor. 2004. States of Knowledge: The Co-Production of Science and Social Order. Routledge, London.
Vatn, A. and D. W. Bromley. 1994. Choices without prices without apologies. Journal of Environmental Economics and Management 26:129-148.
Thanks very much for taking the time to make such thoughtful comments. Not sure my response will do your comments justice…
Re: personal satisfaction as a motivation, I’ll admit to slightly mixed feelings. If I’m honest, a big reason I ask the questions I do, in the systems I do, is personal satisfaction. I find it immensely satisfying to ask a question, and get a really clean, clear-cut answer. In an old post on “the best sentences a scientist gets to say,”, I said that one of my favorites was “the error bars are too small to be visible”. Which is something I’ve gotten to say in talks and papers, because of the system I work in. Importantly, that’s not mutually exclusive of–in fact, it goes hand-in-hand with–the fact that I’m working in a model system well-suited to answering the questions I want to ask. I’m also impatient, and so I enjoy working in a system in which the experiments are short by ecological standards (a few months at most). So happily for me, the things that give me the greatest satisfaction in science just so happen to be things that can be done–indeed, are best done–in my chosen model system.
But when this happy sort of circumstance doesn’t apply–and for many ecologists, it doesn’t–then my feelings are more mixed. On the one hand, the only way any science at all–especially fundamental work–is going to get done is if people really love doing it. My implicit assumption in the post is that the alternative to doing ecology in non-model systems is doing ecology in model systems. But in some cases, the alternative might be no ecology at all, since if for whatever reason (lack of funding, whatever) someone isn’t able to work in the system they love, maybe they’ll just go do something else that isn’t ecology (and no one else will get to do more ecology because of that). On the other hand, the fact that you get great personal satisfaction from working in system X doesn’t change the quality of whatever science you conducted. Your personal satisfaction is just that–yours. Others aren’t likely to find the same things satisfying that you find satisfying. If you’re ok with that, that’s fine–to each his own. But if you aren’t ok with that, or can’t afford to be, for instance because you need to get grants in order to afford to do science, then sadly you may have to do science you find less personally satisfying.
Your point about opportunity costs at different levels is absolutely right. Just as there are opportunity costs to doing ecology in non-model systems, there are opportunity costs to doing any sort of ecology–we could be paying for more schoolteachers or cancer researchers or whatever. I have no answer to that. I have no idea how to make these sorts of judgments. These judgments do get made, of course–legislators setting government budgets make such judgments every year. But I know nothing about how it’s done beyond what I read in the news, and know nothing about how it might be done differently. All I can say (as I’ve said in an old post) is that I do think there are good reasons for pursuing fundamental research in a world with pressing applied problems. But how to weigh those reasons up against the reasons for hiring more schoolteachers, or doing more cancer research, or whatever–I have no idea.
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In physics, chemistry, social sciences, economy, nobody and medicine nobody claims that we don’t have money but to study model systems, This happens only in genetics and physiology. Physiologists and geneticists that study Arabidopsis etc. don’t study the organism, they study the cell. In other words, they model the lower level of organization with a model of an upper level of organization. This is the only way model organisms can work. A model for ecosystems would be the higher level of organization, i.e landscape – they did it in Hubbard Brook many years ago, much before blog existed.
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