Ecologists, especially community ecologists, are always looking for ways to infer process from pattern, cause from effect. Ideally, they’d like some way to do this that:
- Is based on previously-collected or easily-obtained observational data
- Is “off the shelf”, meaning that it can be implemented in a routine, “crank the handle” way, without the need for much customization or even thought from the user.
- Can be used in any system
Examples of previously- or currently-prominent ways to infer process from pattern in ecology include:
- randomization of species x site matrices to infer interspecific competition
- plotting coexisting species onto a phylogeny to infer contemporary coexistence mechanisms
- plotting local vs. regional species richness to infer whether local communities are closed to invasion, or whether local species richness and composition is just a random draw from the regional “species pool”
- using the shape of the species-abundance distribution to infer whether communities have neutral dynamics
- using ordination to infer the process dominating metacommunity dynamics
- the use of power law distributions of movement lengths to infer whether foraging animals follow Levy walks
- using body size ratios of co-occurring species to test for limiting similarity
- attractor reconstruction and convergent cross-mapping
The above approaches to inferring process from pattern all have something in common: none of them work, either in theory or practice. Which leads to the my question:
Has any widely applicable “off the shelf” method to infer process from pattern in ecology ever worked? Can anyone name one?
It doesn’t count if a method is merely “suggestive”. “Suggestive” is cheap; just eyeballing your data is suggestive! It doesn’t count if a method is potentially useful when combined with many other lines of evidence, because then those other lines of evidence are doing most of the work. And it doesn’t count if a method isn’t “off the shelf”. For instance, “develop and parameterize a dynamical model of your study system and then validate it with independent data” isn’t an “off the shelf” method. I’m talking about methods that were sold and used as a powerful way to cut through the complexity of ecology and provide a rigorous yet easy-to-follow path from pattern to process.
Another way to pose the question is to ask: what would have to be the case for a method based solely on observational data to allow more-or-less reliable inferences about underlying causal processes? Is it likely that any such method exists in ecology? If it did, is it possible that it would be off-the-shelf, broadly-applicable, and yet powerful? Based on the example of successful observation-based sciences like astronomy, which I’ve discussed previously, I doubt that any such method exists in ecology.
Note that I do think there are cases outside the physical sciences where such methods exist. I’m thinking of methods like the HKA test and its derivatives, used to test for selection in population and evolutionary genetics just based on gene sequence data (here is a brief review). Notably, much as with the case of astronomy, this is a case where we can write down a more or less complete list of the underlying processes that affect the observational data of interest, where we have a rigorous, quantitative theory of how those processes will affect the observed data, and (crucially) where different processes (here, selection vs. drift) are predicted to affect the data in quite different ways, leaving quite different “signatures”. In contrast, one common failing of putative methods for inferring process from pattern in ecology is that many processes or combinations of processes produce the same pattern.
My hope with this post is to raise the bar for any future proposal to infer process from pattern in ecology. Any such proposed method should have to meet a very high burden of proof that it works before it is widely adopted.
Note: The above is an edited and retitled version of a post that first ran in 2012. Sorry for the rerun. Meg, Brian, and I are all busy right now.
Dynamic Ecology 
My paper on inferring species interactions (http://biorxiv.org/content/early/2015/11/26/018861), which is coming out in Ecology soon, shows that:
1) “randomization of species x site matrices to infer interspecific competition” is less effective than using correlation coefficients
2) partial correlation coefficients (e.g. from linear regression) and logistic regression coefficients actually do a pretty good job of inferring interactions from co-occurrence—even when there are environmental confounders.
Cheers for this David. Had a very quick skim.
Correct me if I’m wrong: it looks like your approach defines competition as a reduction in the probability that species i will occupy a site, given that species j is also there, all else being equal. Which you can then estimate effectively with your Markov approach, because by assumption the data were generated by the same model that you’re estimating.
I confess I’m not sure if I’d call that an inference of process from pattern. Without wanting to get too philosophical about what constitutes a “process”, I’m curious whether your approach would still work if the data were generated by some other model. Say, a stochastic spatial Lotka-Volterra competition model (an arbitrary choice, obviously). Would the “competition” parameters that your approach estimates map onto the parameters of the Lotka-Volterra model?
Your summary of my definition of competition is correct. The various versions of the paper on biorxiv and (soon) in Ecology show a fair amount of robustness in terms of both the simulation method (presence-absence versus abundance, population dynamic time series versus Gibbs sampling) and in terms of the model used to infer competition (various kinds of partial correlation coefficients, GLMs, Markov networks). So I wouldn’t say that the result is trivial. It even works when the data includes a few environmental factors that aren’t modeled. The most recent version that’s on biorxiv actually uses Lotka-Volterra-type dynamics for some of its simulations, and the inference still works.
Regarding process from pattern, I guess it depends on what you’d call “process.” On one level, your Lotka-Volterra parameters would also be phenomenological (in the sense that they depend in complex ways on a large number of behavioral and physiological issues). It’s certainly common for people use the phrase “process from pattern” to describe what they’ve supposedly accomplished when they try to infer competition from co-occurrence. The main difference is that essentially none of the null models that dominate this literature even attempt to control for other species.
I guess my first cut answer would be that your set of restrictions are overly stringent for any method to be able to meet them: you’re asking too much and I don’t know that any proposed analytical method has ever promised such great things.
“Another way to pose the question is to ask: what would have to be the case for a method based solely on observational data to allow more-or-less reliable inferences about underlying causal processes?”
This seems to me more tractable. I think there are two basic criteria: (1) the system would have to be relatively simple, as characterized by very few cause and effect relationships and without major feedbacks and loops, time delays, and other problems, and characterized by variables that are readily measurable with as little uncertainty and bias as possible, and/or (2) the use of opportunistic (“natural”) experiments, in which one has “treatments” of important variables that vary independently of each other. Preferably, both of these criteria would be met.
However, stepping back a bit to give an even more general and thus nearly useless answer, I’m a big proponent of basic statistical concepts/methods that allow for important, albeit general, inferences as to what’s driving a system. A simple and classic example would be the examination of values of an important response variable, across sample units, to see how well it follows a Poisson expectation, addressing the question of whether the driving processes of interest, across those units, are explainable by homogeneity or not. Yes, highly general, but to me, important information.
should read: “explainable by *process* homogeneity or not”
“you’re asking too much”
It’s not me who’s asking too much–it’s the people who’ve proposed and used these methods.
Yes, sorry. Though I don’t know the details of any case.
Convergent cross mapping seems promising. What don’t you like about it?
That it fails badly. It’s not at all robust to violations of its very strong assumptions: https://arxiv.org/abs/1601.00716
Thanks for that paper, this will be very helpful for me. I had tried implementing CCM but was getting ambiguous answers.
At some level I do think you need to delve in to the philosophy of what constitutes a cause or a process to answer this question in a satisfactory way. If community composition changes in a similar way with elevation on 50 different mountains (as it often does), then elevation falls somewhere on the causal pathway to predicting community composition. Easily applied method, widely applicable. Have we learned something about process or mechanism? I’ll guess you would say no: we want to figure out if it’s temperature or soil properties or whatever. But even then, you can ask _why_ composition varies with temperature (i.e., still not at mechanism to someone’s satisfaction). The point is that you can always dig one step deeper on _why_. People have their particular level at which they’re satisfied and willing to declare the process revealed, while others don’t care about that level (they hang out a level higher) or won’t be satisfied until things go a level deeper.
Populations geneticists got lucky with so much DNA that codes for nothing, giving them an internal neutral benchmark. If all mutations were potentially under selection, they’d be in the same position as ecologists. Or, alternatively, you could say our method of repeated composition-environment changes rejects neutral theory to the same degree that pop-gen tests can.
I was hoping you’d chime in Mark, and was expecting that this was the example you’d raise. I’m halfway through your book already, so my internal Mark Vellend emulator is already pretty finely tuned. 🙂
I agree with you that species composition-environment correlations are indeed an off the shelf, broadly-applicable, powerful way to demonstrate what you (and I) would call “selection”, thereby rejecting a neutral (selection-free) world.
I’d only add that one reason that works is that the process of interest–selection–is a high-level process. I think an underrated argument for focusing on high level processes is that it by cutting down radically on the number of candidate processes you *may* be able to create a 1:1 mapping of process to pattern. Thus allowing you to reliably infer pattern from process. If the only candidate processes are the high-level “big four” of evolution, or their ecological analogues (drift, selection, migration, mutation), you’ve got a fighting chance of inferring process from pattern (maybe, depending on the details–species abundance distributions of course look the same whether or not there’s any selection). But if you define your candidate processes at a lower level, then you’re almost surely screwed.
Population ecology provides an example. There are features of population dynamics that you just cannot get except via density dependence. So if those features are there, you’ve definitely got density-dependence. Density-dependence is of course a high level process that can arise from all sorts of lower-level processes. The lower down you go, the more difficult it is to come by patterns that are diagnostic of particular processes. Or at least, the same patterns that are diagnostic of high-level processes are very unlikely to be useful for diagnosis of lower-level processes (e.g., different low-level sources of density-dependence in a focal species). For instance, attempts to diagnose, say, predator-prey cycles vs. tri-trophic cycles vs. prey-resource cycles just from features of prey population dynamics haven’t been very convincing, I don’t think.
Of course, even with lower level processes you could try to cut down the numbers by just arbitrarily lumping lower level processes together. Say, “resource competition” vs. “all other stuff that is not resource competition”. But off the top of my head I’m having trouble of thinking of cases in which that sort of arbitrary lumping is helpful. Cases in which it has the desired effect of creating a 1:1 mapping of process to pattern (e.g., patterns that, say, resource competition could generate, but that “other stuff” could not).
Just to stir the pot (because I should be writing a grant) …
Why does population dynamics always get to cloak itself so strongly in mechanism. Much of population dynamics is a bunch of phenomenological parameters fittable only by curve fitting (alpha especially but also K & r) applied to a 2nd order approximation (i.e .a quadratic taylor series) aka Lotka-Volterra equations.
Meanwhile, macroecology fits a species area relationship, often gets much tighter fits and even has some theories about when z should be 0.25 or when z should be 1.0 and yet is declared mechanism-free
Harumph! 🙂
Because “mechanism” and “fit” are two different things.
That was too easy–c’mon ask me a hard one! 🙂
In seriousness, this may get back to your old post on schools of thought. In the comment thread on that post I think we decided that “population processes” was a school of thought, but the opposing school was hard to define.
A tentative suggestion: the “population process” school might be better called the “bucket model” school. It’s people who think in terms of dynamical models–state variables (“buckets”), and the inflows and outflows that cause the values of those state variables to either go up or down. So yes, populations are one example (dN/dt=B-D+I-E). But so for instance is species richness in a simple island biogeography model (dS/dt=cP(1-S/P)-eS). You use those dynamical models to derive predictions about the values of the state variables. But in a sense, that’s secondary–your assumptions are all about the input and output rates. The flows, not the stocks.
Continuing with that line of thought, here’s an opening bid for the defining characteristic of the alternative school: the regression school. The school of thought that thinks in terms of Y=F(X), where Y is some dependent variable and X is some vector of predictor variables. So not dS/dt=[inputs-outputs], but S=cA^z.
Am I on the right track? Does any of these ring true to you?
I think the distinction between a focus on stocks vs flows is helpful and potentially illuminating.
But what I’m not following is why population dynamics is not essentially regression? How is r measured? By regression of populations vs. time in an unlimited growth scenario. How is K measured? By fitting a timeseries via regression. How is alpha measured? By fitting a two-species timeseries.
Why do we fit the L-V? Because the linear goes to zero or infinity and is useless so we add the simplest possible extension.
Why is that a mechansitic model and not a regression model? Or in other words, given the data, a statistician would likely use difference equations instead of difference equations but likely declare the exact same model as a reasonable fit.
Now if you drop to lower level process like resource competition instead of L-V competition, it is a (slightly) different discussion. But I see L-V in a lot of very recent, very big papers.
“But what I’m not following is why population dynamics is not essentially regression? How is r measured? By regression of populations vs. time in an unlimited growth scenario. How is K measured? By fitting a timeseries via regression. How is alpha measured? By fitting a two-species timeseries.”
I see “world view” and “how I obtain the parameter estimates needed to apply my worldview to some particular bit of the world” as two separate things. I guess I don’t see how the fact that a regression is somehow involved in parameterizing a model makes the model “essentially regression”.
Yes, absolutely, as Mark noted, the parameters of any ecological model can always be thought of as phenomenological higher-level summaries of lower-level processes. That’s obviously true for the L-V model. But it’s still true for, say, a resource competition model. For instance, the conversion efficiency parameter in such a model is a phenomenological summary of the hugely complicated physiology of digestion, assimilation, etc.
So I think the L-V model specifically may loom a bit too large in your thinking about the population process school. As I say, if you’re thinking in terms of bucket models, I think you’re one of us, even if there are some specific bucket models you don’t like for whatever reason. If you don’t like L-V models, that’s fine. For my part, I don’t like ratio-dependent predator-prey models. But in general, I’m still a bucket model guy. That’s how I like to think about the world.
So when I think about competition in a simple way, I don’t think of species i causing species j to go extinct or causing species j’s abundance to decline, even though what I ultimately care about is indeed the effect of species i on species j’s abundance or persistence. Rather, I think of species i as causing species j’s *per-capita growth rate to decline*, with knock-on consequences for species j’s abundance. Crucially, I think the whole point of having the bucket model is to work out those knock-on consequences. Rather than trying to skip a step, as it were, and go straight from “abundance of species i” to “abundance of species j” via some sort of regression of abundance of j on abundance of i.
I now recall that I tried to get at this in a very badly written old post that just confused people: https://dynamicecology.wordpress.com/2012/06/08/ecology-is-mostly-not-like-billiards-but-lots-of-people-think-it-is/ What I called “billiard ball thinking” in that old post is what I’m calling the “statistical prediction” school now. The idea of predicting or explaining one state variable directly in terms of another state variable, rather than via a dynamical model in which state variables affect one another’s input and output rates.
p.s. I bet you’re a fan of, say, macroevolutionary models that specify (possibly diversity-dependent) rates of speciation and extinction. Which if so makes you a bucket model person too, because those are (stochastic) bucket models. 🙂
Reading through all this and mulling it over some more, my conclusion is that it’s not particularly the math/stat method that should be the focal point of the question, but rather the study design more generally–that is, just exactly how the data were collected in the first place. That’s going to determine what you can infer regarding likelihoods/ML of driving process(es). If I see tree growth rates decline as I ascend a series of mountains, and can only employ observational data (per the restrictions given in the post), then I’m going to have collect growth rate data in a series of locations designed specifically to create a natural experiment in which I know, quantitatively, the variation in various possible explanatory drivers. Thus e.g. I collect growth rate data very systematically on slopes with differing solar radiation loads, different latitudes, continentality, local P shadowing, elevation, and etc, allowing me to distinguish between the effects of solar absorption, ambient T, CO2 partial pressure, parent material and whatever else is potentially important. The analytical method is pretty irrelevant, assuming basic quantitative skills–it will be some fairly basic tool given to us by statisticians long ago.
Short version: the nature of the data used in a study are far more important than the analytical method.
@Jeremy – continuing the thread down here.
So there is an interesting discussion to be had about whether we should study dN/dt or N – I think to preempt it goes like I say “I’m ultimately interested in absolute level of N and dN/dt hasn’t proved that informative about N” and you say something like “there is not really a science of N – mechanism is at dN/dt”.
I’m also happy to agree that say the MacArthur-TIlman model of resource competition or the Holt model of apparent competition is more mechanistic than L-V. But I’m going to stick to L-V for a minute because an awful lot of basic and applied ecology centers around L-V and single species quadratic models like logistic or near relative Ricker. So in that context, and leaving N vs dN/dt aside, assuming for the moment its dN/dt is the topic of discussion:
I can write:
1) dN1/dt=rN1(K-a12N2-N1)/K but it is competition only because your (and most) definition of competition is 1/N1 dN1/dt has a negative partial derivative with respec to N2
or
2) dS/dA=czA^(z-1) (the less common form of the species area but it is used in any number of papers, and given S=0 at A=0 this is more or less 1-1 to with S=cA^z and say this a study of how species increase with area.
Both the quadratic functional form of 1 and the power law of 2 are picked because they’re simple, not because they’re capturing some deep mechanism (although a lot more ink has been shed on the functional form of #2 than #1)
So why is #1 mechanistic and #2 mechanism free?
Because #1 is a bucket model and #2 isn’t. #2 has no state variables with input and output rates. dS/dt=[immigration and/or speciation rate as a function of area] – [extinction rate as a function of area] would be a bucket model. Obviously one that could be pretty phenomenological and L-V like, or pretty mechanistic, depending on how exactly you filled in those brackets.
This is an interesting and useful discussion for me, I’m learning something about your thinking I didn’t know. And presumably, you’re not alone in thinking as you do about this. But I get the sense that we’re puzzling each other, and I’m not sure how to fix that. You’re not “getting” why anyone would see the distinction between (say) dS/dt and dS/dA as worth caring about. And I’m not getting how you could possibly not get it!
I will keep mulling it over. Meanwhile, maybe someone else can step in and hopefully keep the conversation going in a productive direction.
[goes to the door, calls] “Meg? Can you come in here for a minute?” 🙂
I agree this is very educational and fun! I think this issue has lurked behind most of the relatively small areas of disagreement we have had over the years.
OK – I understand your meaning of bucket model a little better. I call them accounting models in a draft chapter of my book. Dollars in the bank can only change by adding dollars or removing dollars. Whatever the language it is a time derivative alternative to the conservation of X laws in physics (but unlike conservation laws “matter” can be created – e.g. interest rates or birth – and destroyed). And I agree ecology works better with bucket/accounting models than conservation models.
Why isn’t S a state variable? It is called so in the macroecological literature. And why is dt in the denominator inherently more mechanistic than dA or dS or dT (temperature) or dN in the denominator? It is true that dS/dA doesn’t have outputs (you can’t lose species as you expand area) but, you certainly are “inputting” species into the “richness bucket” as you go across area presumably by increasing # habitats, etc. Indeed nearly all the thinking about species area relationships have been about what affects the rate at which you encounter new species as you walk along a transect – aka beta diversity – dispersal limitation, new habitats, simple sample effects from increasing number of individuals, at large scales new climates etc. It is a very rate-oriented discussion (although again because S=0/A=0 is fixed rate and bucket fill volume are 1-1 in this case). And indeed a number of people have pointed out that species-area and beta diversity are two sides of the same coin and beta diversity is an inherently derivative-like operation.
I guess I would argue mechanism is more about how much detail you go into about your bucket filling/empty rules (e.g. how mechanistic you get about birth rates in a population model – gestation times, temperature effects, food effects, body size effects, resource accumulation rates and their conversion efficiencies through anabolism and catabolism to new biomass, etc), not whether the bucket filling rule is dN/dt or dS/dA. So since L-V is lets swap a quadratic term in because linear doesn’t work, and lets take the bucket filling parameter, call it “births”, and it fit it by curvefitting is NOT very mechanistic. Simply being dN/dt (or dX/dt) does not mechanism make. That strikes me as a very temporal-biased perspective.
And just to further hypothetical it. What if I look at species-time relationships? Now I am writing dS/dt (not the MacArthur Wilson colonization-extinction dynamic version but the stand in one place and count the species I see over the years version). That is, as many papers have shown, very analogous to dS/dA and it has dt in the denominator.
“dS/dt=[immigration and/or speciation rate as a function of area] – [extinction rate as a function of area] would be a bucket model.”
I think you meant to write “dS/dA = …” right? The relevance being that your point is about the importance of specifically tracking the contributors to an observed response variable, not whether ispace, vs time, is the denominators of the rate process. And I would agree, that is the central point–whether or not one is tracking the known or hypothesized contributors to a process.
@Jim:
I meant dS/dt. No typo.
@Brian,
Still mulling over my response to your most recent comment, but in the meantime wanted to start a new thread by asking you a question: So, what (if anything!) do you think is the common thread uniting my post’s examples? Would you agree with me that they’re all failures or dead ends, and that the shared reason is because they were all attempts to infer process from pattern?
Yes – I definitely agree that your original point about trying to infer process from pattern fits snugly into a hole in the human brain that makes it very tempting but very likely to go astray (like AIC). And I strongly agree with all of your examples (although I don’t know enough about Levi walks or convergent cross-mapping to have informed opinions on those two). And I’ve led the charge on a few of those, especially the idea that an SAD shape can imply process. You left off distribution of traits (under vs overdispersed in a community) to infer process but I would firmly add that one too.
To me this goes back to Cohen’s idea that there are always an infinite number of ways to generate the same pattern. So pattern can’t point strongly to process. Some sort of measurement across a perturbation and prediction about what should happen is necessary. Ideally experimental but observational/natural experiment is perfectly acceptable if necessary.
Its what counts as a process, raised by Mark and Jim in the comments, that got me thinking along this line. We clearly have very different views on this. After all, I’ve argued that MaxEnt and the Central Limit theorem may be a process (http://onlinelibrary.wiley.com/doi/10.1111/j.1600-0706.2009.17771.x/abstract) and I’m pretty sure you disagree! But lets save that debate for another day and stick to dN/dt vs dS/dA. And to the latter, I would argue that in a species area relationship conversation:
1) observing that z often equals 0.25 and then post hoc coming up with an explanation is weak evidence for that process (which is hammered home because there must be at least half a dozen such explanations that have been produced and they’re all different)
2) Making a novel bold prediction about z (e.g. it must increase with scale above a certain threshold in area because of the arrangement of species ranges) is a stronger test.
3) Finding an experiment or observation of perturbation across a mechanism (e.g. rate of habitat variation across space) is an even stronger test.
This gets back to Jim’s point which I very much agree with that it is the inferential context that matters.
But none of that makes dS/dA less mechanistic (=process containing or process informing) than dN/dt.
Just to expand. Isn’t the whole point of dy/dx is rate of change of y with x. Or if I’m a statistician the covariance of y with x. Doesn’t this align to my #3 as “perturbation” as being the key way to isolate/demonstrate mechanism. So any derivative (rate of change) that is explained is indicative of mechanism and sets up tests of mechanism.
Which doesn’t solve my problem that I am more interested in the level of the state variable (e.g. S) than its rate of change.
Brian, it seems to me that Cohen’s point about infinite explanations for any pattern gets at the key issue about inferring process – that process can never be inferred from pattern alone. But that also goes for manipulative experiments. The data from a controlled experiment still simply describe a pattern – what gives them power is that the experimental design allows us to escape the ‘infinite explanations’ problem. The strong assumption that the only difference between treatment and controls is/are the manipulated variable(s)is what allows causal attribution to be made.
But does that mean that process can never be inferred from observational data? Judea Pearl wouldn’t say so. And I think he would point to structural equation modelling as a technique that could work. That with enough information, the covariance among variables can make the ‘infinite explanations’ problem much more manageable. I haven’t used the technique enough to know how well this works on the ground. But Judea Pearl’s work on causality certainly seems to have developed a strong conceptual framework for inferring process from observational data. Jeff
I fully agree (I think I even said it somewhere in all the copious Brian-Jeremy comments) that you can infer process with observational data. Also the experiment observation axis is much more of a continuum than the dichotomy we present it to be. If anybody’s ever looked at Koch’s postulates for what is required to prove a microbe causes a disease that is a way tougher “experiment” than anything an ecologist would do.
Not to repeat a post from a couple of weeks ago, but I think testing a priori predictions vs post hoc is important, testing multiple predictions is important, etc. Observation vs. experiment is just one factor and not the be-all, end-all.
Behold the near-real-time influence of Dynamic Ecology! 🙂
Can’t accuse this comment thread of shying away from deep questions 🙂 – you are probably tired by now but I will nevertheless add a few thoughts:
1) I do agree with Mark’s / Dave’s comment about having to be more precise about the meaning of “process”, “mechanism”, “infer”, “causal” etc. If an SDM infers the correct environmental niche, does in infer a process or not? Some say yes, some say no, but the disagreement is entirely about the meaning of “process”.
2) @Brian: I do think d/dt is special. Causality implies a time-direction, so first-principle mechanistic models will have to be temporal. Models such as dS/dA are likely describing a secondary pattern rather than a primary mechanism (but again, depends on what you call mechanism / process). Side note 1: “state variable” usually refers to variables of a dynamic system, which would imply time-dependence, see https://en.wikipedia.org/wiki/State_variable / Side note 2: of course, dS/dA can be a “processes” when connected with a dt, as in PDEs for d^2S/dx/dt
3) 2 being said, there are certainly many dynamic model that have highly unrealistic and phenomenological submodels, in particular in population modeling. Which raises the question if they deserve to be called “mechanistic”, or more mechanistic than an SDM that does identify the causal niche axes.
4) Can we infer processes from patterns? Sure we can. Darwin inferred evolution from observations without having made an experiment. But it’s hard. And there will be some margin for error. If something is hard, you will always have people tell you there is an easy way. But most of those “shortcuts” don’t work, as pointed out by the post. I think the main problem is that lots of processes are intertwined (e.g. dispersal / history always creeps in), so you will ultimately need methods that are a lot more complex if you want reliable inferences out of the box.
All very good points.
Re: your #3, worth mentioning Simon Wood’s idea of “partially specified” models here. Also called “semi-parametric” or even “semi-mechanistic” models. The basic idea is that dN/dt = F(N, other stuff), and you estimate some portion of the form of F() from data using a smoothing spline rather than assuming a particular functional form. For instance, you might leave the functional response in a predator-prey model unspecified (because you don’t know enough to specify it), and estimate it by fitting a spline to data from a bunch of feeding rate trials at different prey densities.
Edit: oh, and since Steve Ellner was just visiting Calgary, I have to give a shout-out to integral projection models. As with partially specified models, I definitely consider them process-based bucket models–even though some of the process rates are described by nonparametric regressions estimated from data (e.g., of fecundity and/or survival probability on body size).
Jeremy – I am confused about your partially specified models and what you think of them. Surely dN/dt=spline is a statistical model, not a process model?
@Brian:
I’d say it’s still a process model, but perhaps only barely. I’m happy to agree with you, Mark, and Florian that, within the broad category of process models (aka bucket models), there are more and less phenomenological/statistical ones. Things like the L-V model and partially specified models are towards the phenomenological/statistical end (well, depending on how much and what sort of biology your partially-specified model specifies). Though like Florian, I do think there’s something special about dt, even if the model is literally just something like dN/dt=N*(spline function of N)
Florian – thanks for dropping by. Its never too late to comment on DE!
I agree with most of what you said, but I’m going to take issue with your point #2 (probably surprising no one). And I’m going to take issue on two levels.
First, probably without meaning too, you changed the conversation from “mechanism” and “process” to “cause”. “Causality” is in most philosophical treatments a much more restricted concept than mechanism. And indeed the word is primarily used in physics which very much has the time dependency you describe. But in biology, certainly ecology, it is much more common to talk about mechanism. And the word mechanism is not a simple synonym for causality. Indeed biology and mechanism have taken totally different roads than the physics definition of causality. And modern philosophers of biology (e.g. Craver) have equated mechanism with the notion of breaking a phenomenon into component parts (very crudely put). Nothing to do with time. Some philosophers do bring time/causality into mechanism. But it is by no means a universally agreed upon or required feature of the concept mechanism. A lot of biologists invoke mechanism without causality. Or to take an example from a neighboring field of ecology, soil science, take the Jenny equation S = f(cl, o, r, p, t, …). Soil type is a function of climate, organic factors, etc.Now plenty of people will tell you that Jenny’s equation is unsatisfyling vague about precise mechanisms and processes, and I agree. To me this is weakly mechanistic in the same way as the L-V. But nobody feels compelled to model soil development at the level of spatiotemporal PDEs of soil particles. Yet everybody agrees that climate or organic factors are “mechanisms” determining soil type. That’s just how the word mechanism is used.
Second, even if I were to stipulate that you are in theory correct about dt having precedence because of the time ordering of cause, this is highly impractical. Would my theory of species area relationships be better if I could write a partial differential equation of dS/dx dt instead of just dS/dx (using x for x coordinate here instead of A for area). Sure and would it be even better if I could write it as a differential with temperature of other factors (dS/dx dt dT). Sure. But good luck with that approach! The number of fundamentally important partial differential equaiton models in ecology is pretty much limited to diffusion/dispersal and McKendrick-vonForrestor that I can recall. And none of those rank up there in importance with L-V. To be successful in modelling you have to simplify. And if I choose to simplify out the dt and you chose to simplify out the dx or dA some rigid obeisance to a definition of causality that says I can never drop dt but I can drop dx is impractical. First off it more or less dictates that temporal questions are “more scientific” than spatial questions which is not I think a claim anybody wants to make (even though it is an unintentional implicit outcome of a claim of primacy of dt over dA or dx). And I think if you follow this line of argument to its logical conclusion it also suggests that only BACI experimental designs assess causality and spatial replication is invalid for testing. It is entirely unrepresentative of how we do science and unacheivable. Unless we want to say that only changes over time are meaningful. To throw out all changes over space and all changes with some covariate like temperature is unacceptable. And to insist that the study of changes over space are not allowed to simplify out the temporal dimension, but changes over time are allowed to simplify out the spatial dimension is at its ultimate extreme logical conclusion a form of claiming “my science is better than yours”.
My two cents.
Yikes, the distinction between cause and mechanism is one that escapes me even if philosophers have agreed that these are different things – there is no question that I was thinking/using cause and mechanism synonymously. Brian, Is there anywhere in this trail of comments where replacing mechanism with cause would have changed the discussion? And this isn’t a rhetorical question – I’m actually trying to sort out how much I have to think about the distinction.
And even if we are using them interchangeably I’m not convinced by Florian’s statement that “Causality implies a time-direction, so first-principle mechanistic models will have to be temporal.” I see time as important in diagnosing the direction of causality (e.g. does area increase after an increase in species richness or the reverse?) but I wouldn’t have thought that means that models from first principals MUST be temporal. Perhaps time sries would be necessary for confirming the direction of causality – is that the same as saying the model would have to be temporal? Jeff
Hi Jeff – Interesting points.
First – I think it is useful to distinguish the English use of cause vs the physics word “casuality” which has become quite precise (and complex: in space-time you have to refer to light cones to determine what happened “first”). I agree in English we would freely define mechanism as “the things that cause things”. And I agree nobody except science fiction writers with hypothetical time machines can get away suggesting things that happened afterwards caused things before. But causality and the emphasis on temporal precedence as pivotal to the meaning of mechanism has unique to physics and philosophers of physics. Specifically temporal precedence is a necessary but nowhere close to a sufficient condition for “cause” or mechanism. So other features have to be involved in determining what is or isn’t a mechanism. And in biology, not many people have found temporal precedence as a particularly helpful indicator of mechanism.
But if I can expand on what you said, I think it is quite dangerous to hang too much on temporal precedence as the measure of cause in ecology. As you suggest it now means claims of mechanism would really need time series with Before-After-Control designs. And plenty of things in ecology happen nearly simultaneously – turn on a lamp and photosynthetic rate increases very rapidly. Our claim that light was the mechanism rather than the other way around is almost certainly not measured on the preciseness of time measurements that varifies temporal precedence. It is based on what we manipulated and on a conceptual model of light hits chlorophyl/electron chain/rubisco etc. Which fits Cravers description of mechanism. And when you get right down to it is a fundamentally spatial description.
Thank you for raising the point about just because temporal precedence being a feature of mechanism doesn’t mean it has to be the only valid way to infer mechanism. And so studying rates of accumulation (Jeremy’s bucket models) is by no means the only valid “first principles” way to study mechanism (a point I think Florian acknowledged in his #4 as well). I was trying to say that but said it rather badly.
I think this discussion highlights why we must solve 1) first, because likely 80% of the discussion in this tread is about the meaning of words and not about the ideas / concepts behind them.
That being said – I am struggling with the idea of having a mechanism without cause, and a cause without causality. Are we agreeing that the laws of physics apply for the physical world? If so, I can’t see how causality would be necessary for physics, but not for ecology. Sure, there are static correlations that people colloquially refer to as mechanism or laws, but for all examples I can think of there is a process in the back of one’s head, e.g. dN/dA arises because that there are niches, historical processes, competition and so on.
Btw, afaiks Craver’s definition does not exclude the necessity of causality, it just doesn’t put it in the center of the definition. The Stanford Encyclopedia of Philosophy discusses the different definitions, including Craver’s, and concludes
“Each of these characterizations contains four basic features: (1) a phenomenon, (2) parts, (3) causings, and (4) organization.” http://plato.stanford.edu/entries/science-mechanisms/
Taking a step back from this discussion – I don’t think it’s helpful to chastising ourselves over our lack of “perfect indicators” for processes – few to none of the other scientific disciplines have a device that they can point to a complex system and say: oh, it’s 23% process A, 10% process B etc. Even if it would, it would be a useless info because numbers would change for each spatial and temporal scale. But we can understand the processes and what they do. And I don’t think we are doing so badly in ecology, or do you?
“And I agree nobody except science fiction writers with hypothetical time machines can get away suggesting things that happened afterwards caused things before.”
You would think this would absolutely be the case. But there are, I kid you not, papers in which year t climate variable (usually, annual or seasonal T), to estimate year t -1 tree ring characteristic (usually, width), are considered among a suite of possible candidate models, as evaluated by either p or R squared. Although not common, I have yet to find *any* critical response/ comment on this practice in the TR literature. This is the extreme end of a few really bad analytical practices that raise deep skepticism in that field among some of us outside of it.
Anyway, I agree that temporal sequence is necessary (quite!), but not sufficient, for inferring causation in a complex system. In a simple system though, it can be sufficient, or damn close to it.
I’d have to say that I’m now by no means certain on the various topics involved here, but that the discussion of these (and related) topics is highly important, essential even. We’re clearly not all on the same page in terms of assumptions/beliefs on the philosophy and practice of science, and this cannot but lead to problems.
The only thing I’m really definite on is that I don’t agree, at all, that process/mechanism cannot be inferred from observational data. Inference is always probabilistic–that’s sort of the whole background assumption for maximum likelihood methods. Sure there are often multiple paths to the same endpoint, but they’re not all equal in their likelihoods–that’s the whole point. It’s not hard to demonstrate that simulations employing fundamental statistical models such as binomial, multinomial etc.
I would agree pretty strongly with your point in each of the first and second paragraph.
Have been mulling this over and have one that I think basically meets your criteria: Pritchard et al’s STRUCTURE method/program for assessing population structure from multilocus genetic marker data (http://www.genetics.org/content/155/2/945). Was actually going to suggest this earlier. There are some other, similar methods als, some of which have been incorporated into R packages (e.g. “Geneland”).
I don’t know much about STRUCTURE beyond being aware that it’s a standard tool. As far as I know, it’s a good example. On my admittedly-limited understanding, I think it’s analogous to the HKA test and its derivatives, and to some approaches in astronomy–we have very good background knowledge of the processes that generate the data, and different processes generate quite different patterns, so we can reliably infer process from pattern.
I think one point to make is that a sequential application of a tool may be required to distinguish between alternative hypotheses. For example, with STRUCTURE (and I am going totally off the top of my head here, NOT fully sure I’m right on this), distinguishing between a genetically distinct sub-popln explainable by (1) an immigration event(s), vs. (2) non-random mating (relative to the larger population under study), would require sequential sampling/analysis. And since those two things are hardly minor distinctions, as determinants of popln structure, that’s just what you’d have to do.
I’m not familiar with either the HKA test or w/ astronomy applications, but I agree with your point. That’s why I much like population genetics and heredity–one has a definite theoretical basis for expectations. They’re more tractable and interpret-able from strong first principles than are most other aspects of ecology.
On the downside, I also think that their algorithmic approach is a good example of using complex and ineffecient Bayesian methods when they’re neither needed nor optimal. At least I can’t figure out why they went that route.
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