Everybody knows that a correlation between two variables doesn’t *imply* a causal connection between them. But it’s often pretty tempting to think so, especially if the correlation is a really strong one. I mean, there must be *some* reason for the correlation, right?* Conversely, the complete absence of a correlation between two variables doesn’t *imply* the absence of a causal connection between them. But again, it sure is suggestive, isn’t it? I mean, if there was any sort of causal connection between those two variables that was strong enough to be worth worrying about, you’d probably see *some* sort of correlation, right?

For instance, let’s say you’re studying changes in the abundance of some species over time. And let’s say that abundance just bounces around more or less randomly. There are no cycles or any other obvious temporal pattern, and no long-term increasing or declining trend. And let’s say that you find a really strong correlation between abundance fluctuations and some weather variable–maybe abundance goes up in wet years and down in dry ones or something. Whereas past densities don’t really explain these fluctuations. So while correlation doesn’t *imply* causation, it sure looks like weather is what matters for population dynamics, right? Further, the data strongly suggest that density dependence is at most weak and quite possibly absent entirely, right? Because after all, if population density really mattered much then surely environmental factors wouldn’t explain so much of the variation in the data, and past densities would explain a lot, right?

*Wrong.* Indeed, not just wrong but *maximally *wrong. The very *opposite* of true. In a world with negative density dependence (aka “negative feedback”, “stabilizing forces”, “return tendency”, and other terms), correlation is not just an unreliable or imperfect guide to causation but a positively *misleading* guide. The data described above suggest a world in which density dependence is *strong*, not weak (Don’t believe me? Read Ziebarth et al. 2010)

In a world with negative feedback, correlations among variables are not a reliable guide to causation. Indeed, they’re often positively misleading. The best way to explain why is with an analogy from economics, where the same error often gets made. The analogy is known as “Milton Friedman’s thermostat”, after the economist who suggested it in a famous paper. Here’s a very clear version of the analogy, from an old post by economist Nick Rowe:

If a house has a good thermostat, we should observe a strong negative correlation between the amount of oil burned in the furnace (M), and the outside temperature (V). But we should observe no correlation between the amount of oil burned in the furnace (M) and the inside temperature (P). And we should observe no correlation between the outside temperature (V) and the inside temperature (P). An econometrician, observing the data, concludes that the amount of oil burned had no effect on the inside temperature. Neither did the outside temperature. The only effect of burning oil seemed to be that it reduced the outside temperature. An increase in M will cause a decline in V, and have no effect on P. A second econometrician, observing the same data, concludes that causality runs in the opposite direction. The only effect of an increase in outside temperature is to reduce the amount of oil burned. An increase in V will cause a decline in M, and have no effect on P. But both agree that M and V are irrelevant for P. They switch off the furnace, and stop wasting their money on oil.

The mistake I’m criticizing here–misinterpreting correlations, and lack of correlations, among variables as evidence for or against causality when those variables are affected by density-dependent feedbacks–isn’t at all hypothetical, nor is it restricted to economics. Indeed, it’s a classic mistake in population ecology. Andrewartha and Birch reasoned more or less as in my hypothetical example above in their famous 1954 paper on thrips, work that provided much of the motivation for the entire “density independent” school of thought in population ecology. Ziebarth et al. 2010 provide a really clear formal explanation of this mistake, and a modern test for density dependence that avoids it.

Note as well that you cannot avoid this mistake simply by looking at partial correlations among variables rather than raw correlations. Multiple regression, even sophisticated extensions of it like structural equation modeling, doesn’t make this problem vanish. Nick Rowe has a very clear explanation as to why in another old post.

Nor does the mistake here depend on the “thermostat” being perfect, or on the absence of stochasticity. Again, see that second old post of Nick’s for explanation.

Now this is the part of the post where I should list some recent examples of this mistake in ecology, thereby demonstrating that it’s a zombie idea (a longstanding, widespread mistake that should be dead, but isn’t). And I am indeed suspicious that this zombie is widespread outside of population ecology (I think it’s mostly been killed off within population ecology). For instance, I suspect that attempts like that of Cottenie (2005) to use variance partitioning to determine the causes of metacommunity structure are making this mistake.** Given that there’s intra- and interspecific density dependence within sites, I doubt that you can reliably infer the causes of metacommunity structure just by looking for statistical associations between environmental and geographic variables, and species abundances. Basically, anytime someone is just using correlations, partial correlations, variance partitioning, multiple regression, structural equation modeling, or related statistical methods to try to infer how causality works in a density-dependent dynamical system, there’s a decent chance that they’re forgetting about “Milton Friedman’s thermostat” and falling prey to basically the same zombie idea that once victimized Andrewartha and Birch. But just off the top of my head, I’m not thinking of any demonstrations from outside of population ecology of people making precisely this mistake. Which perhaps just means that there are some unrecognized examples of this zombies out there, waiting to be slain. Maybe commenters can identify some examples.

There are of course approaches for inferring causality from observational data on dynamical systems that work reasonably reliably under appropriate circumstances. But the ones with which I’m familiar mostly take as their starting point the fact that you’re dealing with a dynamical system that may well have density dependent dynamics.

*Actually, no, but that’s a topic for another post.

**Approaches like that of Cottenie (2005) also have other serious problems (Gilbert and Bennett 2010).

This post is particularly sobering for me as a paleoecologist– we analyze precisely the same sorts of data (and in similar ways) that you describe here (namely, time series of relative abundances related to various environmental variables). Although, historically, these relationships aren’t always even quantified, but are truly correlational– i.e., inferred from qualitative wiggle-matching.

So, how do you avoid it, particularly in systems (like paleoenvironmental reconstructions) where you have limited kinds of data at your disposal?

Yes, now that you’ve reminded me of it, paleoecology definitely is an area in which this zombie is alive and well!

What to do about it? Well, one thing to do is just to be aware of the zombie, and make others aware of it! I’m curious: is this zombie recognized in the paleoecology literature? Because it is quite a distinct problem from things like data quality–Milton Friedman’s thermostat is nothing to do with only having limited, biased, or error-filled data. According to Nick Rowe, econometricians need constant reminding about Milton Friedman’s thermostat. If the same is true in paleoecology, you should consider writing a paper on it! Seriously–generate some simulated data from some simple density-dependent stochastic model and analyze them using standard methods in order to illustrate the problem, and then write a cautionary paper for a paleo journal. Sounds like it could be an easy, and valuable, paper to me.

Another thing to do is to be more conservative and literal in the inferences you draw from your correlation-based statistics. It would’ve been perfectly fine for Andrewartha and Birch to conclude that “year to year fluctuations in thrip abundance are driven by weather fluctuations”. That’s literally what the statistics show. It’s when you make the apparently-small-but-in-fact-huge leap from saying that to saying things like “thrip dynamics are density independent” or “weather, not density, is what matters for thrip dynamics” that they fell prey to the zombie.

Another thing to do is to conduct simulation studies to see if you can find reliable signatures of density dependence that would show up in paleo data. I’m guessing that standard tests for density dependence that modern population ecologists use mostly won’t work well with paleo data, except perhaps with the very highest-quality paleo time series data, but you could try some of them and see. Maybe someone’s already done this? I seem to recall that there’s a guy at the Smithsonian who had a paper in Evolution not too long ago doing some simple descriptive time series analyses on various paleo data sets, asking what fraction of datasets are best described by different classes of time series model. My fellow dynamic ecologist Brian may have some advice here, I believe he has at least one paper applying population- and community-ecology-style stats to paleo data.

I had a really well thought out reply that got zapped into the mists of cyberspace when I tried to log in with wordpress. Regardless, I think that paleoecology generally assumes density independence for a number of reasons. First, the temporal resolution of paleoecological data is usually on multidecadal scales that limit our ability to see individual, rather than population level responses, this is further compounded in pollen data since pollen percentages are not coeval with the proportions of their parent species. At best we get probabilistic proportions for the parent vegetation. Obviously, we still get very interesting and exciting questions to ask and think about, but there is an underlying assumption that at the scales we think on there is general density independence. I think we can look at the thermostat example, paleoecologists can figure out how much oil was burned in a city each year because we can estimate that from particulate deposition, and we can know some mean annual temperature, but we can’t get probes into individual houses. Or something like that.

@downwithtime:

Sorry, but just having data at a coarse temporal resolution emphatically does not justify assuming density independence. Maybe I need to do a separate post on this. If the underlying dynamics are density dependent on timescales shorter than the sampling interval, then the observed (sampled) dynamics will perhaps look rather different than they would if sampled on a finer interval. And it might well be difficult or impossible to accurately and precisely estimate the true strength of density dependence from the observed data. But the observed dynamics absolutely will NOT look as if they were generated by an underlying density independent process.

The mistake here is a conceptual one, not empirical. It’s not a matter of having or not having data on the “amount of oil burned”, or data at the level of “individual houses”, or whatever.

I absolutely don’t mean to pick on you here. But the mistake here is a REALLY common one among biogeographers, macroecologists, and paleoecologists in my experience, and it really bugs me. Thinking that, because you only have data on “large” spatial or temporal scales, or because there’s some sort of large-scale signal or pattern in the data, that processes that operate on “small” scales will not generate a signal in your observed data. That somehow, “small scale” processes just “average out” or “aren’t strong enough to matter” at the large scale. For instance, that because plants only compete with neighboring plants, competition doesn’t matter at large scales. Sorry to get on a soapbox, but that is 100% dead wrong. See our recent posts on scaling up, and older posts on why current ecology doesn’t erase the signal of historical biogeography. The right way to think about it is as follows (to take the plant competition example again): every plant everywhere competes, all the time, so competition matters at even the largest spatial and temporal scales.

Again, this mini-rant isn’t aimed at you at all, sorry for taking a passing remark of yours as an excuse to bring this up. In my defense, I can only say that this mistake is closely related to the mistake in the post.

.

Sorry Jeremy, but you’ve just sunk an entire subdiscipline: invasion biology.

You sunk my

~~battleship~~subdiscipline!Wow! Thanks Jeremy!

I want to see if I (roughly) understand this. Because I think that the ecologists’ thermostat problem is slightly different from the economists’ version, but if I can understand your version I think we can in turn learn from you.

Let A(t) be abundance (population?) at time t. Let W(t) be weather at time t. e(t) is some unobserved random shock.

Here are two competing theories:

1. A(t) = A(t-1) + W(t) + e(t)

Theory 1 has no Malthusian steady state. Abundance follows a random walk (maybe with drift).

2. A(t) = bW(t) + (1-b)A(t-1) + e(t) where 0<b<1

Theory 2 has a Malthusian steady state, that depends on weather, (in steady state, A=W), and it approaches that steady state over time. The bigger is b, the faster it approaches the steady state. That's the feedback. It's a thermostat theory, where b measures the speed at which the thermostat works.

We don't know which theory is true. So we attach a weight w to theory 2, and (1-w) to theory 1. 0<w<1. The combined theory (which nests both theories as special cases) is:

3. A(t) = [(1-w)+w(1-b)]A(t-1) + [(1-w)+wb]W(t) + e(t)

Which simplifies to:

3' A(t) = [1-wb]A(t-1) + [1-w(1-b)]W(t) + e(t)

We estimate a regression:

4. A(t) = BA(t-1) + CW(t) + e(t)

We know that B is an estimate of [1-wb] and C is an estimate of [1-w(1-b)].

The estimate for C will be non-zero whichever theory is true. A small estimate for B tells that w is large, which means we should put MORE weight on the second/Malthusian/thermostat theory. In the limit, as w and b both approach one, which means the thermostat theory is true and the thermostat works very quickly, we should expect to see lagged abundance explain nothing (B=0). The weather (which is like a hand that changes the thermostat setting) explains everything.

Is that roughly right?

Yes, you’ve got the right idea, Nick. The typical ecological model would be specified slightly differently, but that’s details (for which interested readers can consult Ziebarth et al.). You’ve definitely got the gist. Thanks for filling in some details that I was too lazy to provide.🙂

And yes Nick, I think you’re right that the mistake ecologists make isn’t exactly the same as forgetting about Milton Friedman’s thermostat, but I thought it was close enough to go with it.

Thanks Jeremy.

It’s very close. Because some of our thermostats work with lags too. It takes time for the Bank of Canada to notice that inflation has risen above the 2% target, and it takes more time for tighter monetary policy to bring inflation back down to target. (But the Bank of Canada sometimes has foresight.) If the Bank of Canada is doing its thermostat job right, you should observe zero correlation between current inflation and lagged inflation, if the lag is longer than the lag in the thermostat. (At what you call “coarse data resolution” and what we call “low frequency data” you should see zero correlation, if it’s coarse/low enough.)

So what exactly in your mind would it take to falsify the importance of density dependence? Under your scenario, you can have a weak to zero measured effect of prior densities on growth rate and some other variable (in your scenario you found weather, but all you would need to do is posit some arbitrary temporally varying variable you haven’t found yet) and voila – you can claim density dependence is acting.

It seems to me all you’ve shown is that the scenario in the 2nd paragraph could occur under density dependence. You haven’t shown that it is the only possible cause. Indeed, by parsimony, I would have to pick weather having a stronger effect than density dependence (not the same as no density dependence) as the best scenario, barring additional evidence.

I would also need more convincing that paleo data that time-averages over the normal time-frame of population dynamics (say 10-50 generations) is not likely to show signals most strongly of things other than density dependence (e.g. environmental forcing).

Hi Brian,

My hypothetical example is just a paraphrase of Ziebarth et al. 2010 (which Nick’s comment has the basic gist of). Yes, absolutely, you can, using appropriate tests and with good enough data, falsify density dependence (well, I think it would be better to say accurately and precisely estimate the strength of whatever density dependence there is). I just meant to make a different point: you can’t rule out density dependence with inappropriate methods. One such inappropriate method is the Andrewartha and Birch method.

Re: paleo data (or any data), all I’m saying is that you need to understand how your sampling procedure affects your ability to test for whatever features of the dynamics you want to test for. For instance, if time averaging over many generations has a tendency to obscure the signal of density dependence, and you collect and analyze some data and find no signal of density dependence, you cannot then infer that density dependence is absent. That’s not a severe test of density dependence.

I wouldn’t have thought this post would draw any pushback from you, so that probably means I didn’t write it very well. My bad. Maybe I should’ve just said “read Nick’s posts, and Ziebarth et al. 2010, and then think about how they might be relevant outside of population ecology”. Because that’s basically all I wanted to say.

Hi Jeremy – I found it an interesting post. And of course mathematically accurate. I wasn’t necessarily picking on the details. To me it raises very interesting larger issues about how we do inference in ecology. In any ecological systems there are many potential candidates for the main driver of the system. Internal population dynamics is almost always one. So is environmental forcing (which itself unpacks into dozens of hypotheses), Species interactions, (co)evolution, etc. Given that population dynamics of even seemingly simple systems in ecology can produce complex and varied dynamics – in short can produce lots of different outcomes, and equally, given that one can almost always find some environmental variable with decent correlation, and etc, how do we proceed?

I have a default preferred explanation of environmental forcing. And you have a default preferred explanation of population dynamics. But we both know these are just biases, not rigorous science.

I think the framing of your post is very useful. My question of how you would proceed to falsify population dynamics wasn’t meant to be rhetorical or pointed question. Surely you would agree that just because you can demonstrate a scenario where factor X could explain data D doesn’t mean it is necessarily the most likely or correct scenario. As for falsifying environment as the explanation, one effective method is just to wait a few more years. If I haven’t got a variable with a genuine causal relationship and it was just correlated by chance (Freedman’s paradox), then it will break down pretty quickly if I watch 5 or 10 more years.

How does ecology proceed through this morass of many possible explanations, each of which is very often a viable explanation and very hard to falsify. This certainly applies to macroecology – if you read Gaston and Blackburns book- every pattern has 10-15 possible explanations most of which are not prima facie wrong. I think too much of ecology has been done by sticking with one’s preferred default explanation, which is clearly wrong, but it is not obvious to me how one does better?

Putting one’s neck out and making predictions that are strong enough to be clearly wrong is one such, and I will continue pursuing the implications of this in some more postings in the new year.

I think the idea of assigning relative strength or importance of factors (which you also get at by saying you prefer to measure the importance of density dependence rather than falsify it) is another important route forward (e.g. variance partitioning can be one useful tool). It also starts to get towards ideas like Platt’s strong inference or the model comparison idea of Burnham and Anderson but it has a twist in that the goal is not to have one model clear the field of the other models, but rather just to give a priority or weight to each.

Any other ideas?

Hi Brian,

I don’t have a default preferred explanation for population dynamics, didn’t mean to give that impression, sorry. I just object to ruling out or playing down density dependence on the basis of tests that don’t justify that inference, or worse suggest the opposite inference.

I also think it’s good to avoid posing density dependence and environmental forcing as opposing alternatives, or even as ends of a continuum. I even think one should avoid asking which is the “most important” or “strongest” or the “main driver” of population dynamics. I have some old posts talking about this. That kind of language simply doesn’t fit how stochastic dynamical systems work. I think it’s much better to think in terms of how to identify, and estimate the parameters of, dynamical models. And to think about precisely which models, with precisely which parameters, are capable of reproducing precisely which features of the observed dynamics.

For instance, as I noted in response to another commenter, in the example in my second paragraph it’s perfectly correct to say that year-to-year fluctuations in abundance reflect weather variation. What’s incorrect is to infer from that that weather variation also explains *other* features of population dynamics, or that *density dependence is zero or near-zero*, or that weather is the “main driver of population dynamics”.

Perhaps it’s time for a post on when it makes sense to ask questions of the form “What’s the most important determinant of X?” Questions of that form make sense in a *much* more limited range of contexts than many ecologists seem to realize.

I think the issue of lots of different (and often non-mutually-exclusive) explanations for a given pattern is a rather different one. Not sure I have much to say that I haven’t said before. Here’s one relevant old post:

https://dynamicecology.wordpress.com/2012/05/31/simplifying-a-complex-overdetermined-world/

I suppose one thing I’d say is that, if there are a bazillion reasons why some pattern might occur, and no good reasons why it wouldn’t, well, maybe there’s your explanation for the pattern right there. The world is that way because it’s hard to see how it could be any other way! I think John Lawton may have made this point in one of his old VftP columns. I grant that that “explanation” might not seem very satisfying. But it wouldn’t entirely dismiss it. Insofar as the world is like this, it’s kind of handy. For instance, Tony Ives and Karen Abbott (?) have a nice EcoLetts paper showing how ARMA models are a very flexible and robust way to fit a very wide range of observed population dynamics. Now, selecting the correct order of density dependence and the correct number of time steps over which to calculate the moving average often is difficult. But for purposes of estimating certain quantities, like the return rate to the stationary state (a very useful measure of “stability”), that doesn’t matter. You can estimate the return rate well even if you select a model with the wrong order of density dependence and/or the wrong moving average period. So if you want to estimate return rates, it’s actually *really useful* that there are many possible ARMA models that might have generated your data–because as long as you settle on *any one* of them, you’ll get a good return rate estimate!

But yes, sometimes you really do need to sort among all the possible explanations for your pattern in order to find the *right* one. One way to do that is to take advantage of the fact that the many different explanations for any one pattern tend to make different predictions about other patterns. So rather than focusing on explaining one pattern at a time (the species-abundance distribution, or linear local-regional richness relationships, or whatever), focus on discriminating among alternative models of how the world might be. I take it that’s what’s your suggesting in referring to Platt’s notion of strong inference, and I know it’s something you’ve recommended to people working on explaining species-abundance distributions.

In other posts I think I’ve said that I’m a “process first” rather than a “pattern first” guy, and this is one reason why. “Pattern first” people too often tend to focus on particular patterns to the exclusion of others, or at least try to explain different patterns one at a time. Even if your ultimate goal is pattern explanation, I think it’s often best to start from a process-first point of view. For instance, if the world was neutral, what would all the consequences of that be? And I mean *all* the consequences, not just for the observed patterns that you most care about explaining, but also for, e.g., the outcomes of manipulative experiments. One powerful way to rule out explanations for some pattern of interest is to test those explanations via an experiment that has nothing to do per se with the pattern–but everything to do with the proposed explanation. For instance, if you manipulate relative abundances and show that species tend to increase when rare and decline when common, you’ve ruled out a neutral world, no matter how well neutral models can fit the species-abundance distribution or species-area curves or whatever (though I suppose you still could have an argument over whether neutral models nonetheless are adequate approximations for some purposes). But unfortunately (alert: potentially-massive overgeneralization ahead), I think an interest in explaining patterns tends to go hand in hand with a preference for doing certain sorts of science, and not doing other sorts. Probably many macroecologists and biogeographers wouldn’t think of themselves as doing macroecology or biogeography, and wouldn’t really enjoy themselves, if they spent their time doing small-scale field experiments rather than data analyses focused directly on the patterns of ultimate interest. I leave it to you to judge if the exceptions to this generalization are sufficiently numerous as to make it an overgeneralization.😉 (And of course, it cuts both ways: process-first people also tend to enjoy doing certain sorts of science, and not enjoy other sorts. Which presumably tends to cause them to have their own blind spots.)

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Jeremy,

I found your tone and claim to be at odds with one another in this post and could only sort out what you were saying by studying the comments. The tone seem bombastic (sinking subdisciplines and all) and exciting, but the claim turns out to be rather smallish. From my understanding your claim is that trying to infer the PRESENCE of density-dependence from cor(x(t),x(t+1) can be misleading. Period. All the bits about weather is a distraction from that point. As you state earlier in the comments the cor(E(t),x(t+1)) (where E in fluctuating env.) will give you the correct answer. This means that neither paleo ecology or invasion ecology is necessarily sunk if they are looking environmental causes of population fluctuations. This is especially true at the time scales they look at where the dynamics of the population is at a much faster scale than the change in environment, allowing precise tracking by the populations.i.e. dn/dt=r*n(t)(1-n(t))/K(T) if T>>t then n* is approx K(T). Again, as you state, thinking that this suggests the absence of density-dependence wrong-headed. (Do people do that?)

In this post you make the best joke of the year with the comment, “The best way to explain why is with an analogy from economics..”. Hilarious. For my head, that might be one of the worst way to try to explain something. The best way is with a precise mathematical argument. Here is my attempt.

Correlation is a second order (moment) measure, so to find cor(E,x(t+1) we will look at first order approximations to both E and the dynamics of X. Most simple models with density dependence and forcing can be approximated to first order as u(t+1)=u(t)+e(t)-b*u(t), where u=x/mean(x)-1, e=E/mean(E)-1 are perturbations around mean values and b is a constant that depends on the model. For example for the logistic map (i.e. x(t+1)=r(t)x(t)(1-x(t))) b= mean(x)/(1-mean(x), for the Ricker model (i.e. f(x)=a(t)*x(t)*exp(-c*x(t))) b=c*mean(x). In other words, b gives us some information about density dependence.

Now we can look at the covariation of fluctuations of environment with abundance cov(e,u(t+1)=, (where indicates a mean). This is equal to cov(e,u)+var(e)+b*cov(e,u) assuming cov(e,u) is zero (i.e. this years weather is not correlated with this years population) gives cov(e,u(t+1))=var(e). This is obviously positive and if we divide by var(e) to make it a correlation it will equal 1. Here the correlation does not lead us astray.

Next and more interestingly lets look at cov(u(t),u(t+1)).

cov(u(t),u(t+1))==var(u)+cov(e,u)-b*var(u). Again, assuming cov(e,u)=0 gives

cov(u(t),u(t+1)=var(u)(1-b) which shows that the covariance and thus the correlation between x(t) and x(t+1) can be positive, zero, or negative depending of the model and the particular values of the parameters. For example, for the logistic map with r~N(mu,s), cor(u(t),u(t+1) is near zero for mu near 2, positive for 1<mu2.

The understanding here is that for density dependent models, the plot of x(t+1) vs x(t) is either saturating (beverton-holt type) or hump-shaped (ricker, logistic map). The parameters of the model that result in a positive equilibrium on the up-slope of the the hump result in cor(u(t),u(t+1)>0, near the peak then cor(u(t),u(t+1)=0, on the down-slope then cor(u(t),u(t+1)<0

Here is r code to show this.

#####################

#set up pop. vectors

x1=rep(0,200)

x2=rep(0,200)

x3=rep(0,200)

#create fluct. var.

e1<-rnorm(200,1.25,.1)

e2<-rnorm(200,2.0,.1)

e3<-rnorm(200,2.75,.1)

#initial conditions

x1[1]=1-1/(1.25)

x2[1]=1-1/(2)

x3[1]=1-1/(2.75)

#Simulate discrete logistic

for(i in 2:200)x1[i]<-e1[i-1]*x1[i-1]*(1-x1[i-1])

for(i in 2:200)x2[i]<-e2[i-1]*x2[i-1]*(1-x2[i-1])

for(i in 2:200)x3[i]0. For example if we define the strength of density dependence as c in the ricker model (above) we can ask how c affects b and thus cor(x(t),x(t+1) (answer: b is independent of c for c>0 & mean(x) near the equil. x). One thing that is obvious is that if density dependence is absent, then b=0 and cor(x(t),x(t+1)=1, not =0, but cor(x(t),x(t+1)>0 is possible even in the presence of density dependence.

2) There is nothing provocative here, is there?

I am not sure if this analysis misses or makes your point? Help a guy out.

Sorry if you found the delibrately-provocative tone distracting Don. This post wasn’t aimed at folks like you, who are so familiar with the point being made here that they struggle to see how it could possibly be a point worth making. I leave it to readers to judge whether the point made in the post is large enough to be worth making.

Thank you for providing some technical commentary.

It’s commenters who said I was sinking entire subdisciplines, not me. While mistakes along the lines identified in the post may be more common in some subdisciplines than others, I’m sure this mistake isn’t widespread enough to sink any subdiscipline.

Hi Don,

Apologies for the rather curt initial response, I was in an airport and rushing, probably should’ve just waited.

I agree this isn’t my best-developed post. It’s more of a provocative teaser for Nick’s posts. I’m sorry you don’t like the tone, but having gone back and read the post again I don’t think it’s out of line. I suggest that the tone may seem out of line to you because you’re already familiar with the point made in the post. I can assure you that your pre-existing familiarity with the point of this post puts you in a small minority of readers of this blog.

As for whether the point of this post was important enough to be worth posting on, and writing about in a deliberately-provocative way so as to attract the reader’s attention, all I can say is that I think it was, and at least some readers seem to agree. I note that the substantive point made in the post is one that Ziebarth et al. spend a fair bit of text discussing. Now, I’m not one to invoke proof by authority–it could well be that I, numerous readers, and Ziebarth et al. are all more interested than we should be in a rather minor point. But if so, I don’t think it’s *obvious* that we are.

With respect, if you think the thermostat analogy is a terrible way to explain things (indeed, so obviously terrible as to deserve mockery), and that the long string of equations and R code you provided is the best way to explain things, well, I do wish you’d give me a bit of credit and keep in mind that I have a lot of experience explaining things to a broad audience in a non-technical way, both on this blog and as a professor for many years. I have never claimed to be perfect, and as I said earlier I admit that this post isn’t one of my best developed efforts. But no, my way of explaining things in this post is not laughable–or at least, it’s no more laughable than your notion that lots of readers will read and understand a dry post filled with equations. My post was intended as a deliberately-provocative *starting point*. I would hardly claim that someone who only read this post and nothing else fully understands the issue–but giving readers a full, technical understanding was not my goal.

I hear you, and I like what/how you write, which is why I come back. I think you do good work here.🙂

I agree that analogy can be useful for conveying technical ideas to a general audience. But, the tradeoff is, of course, precision and thus an increase in the probability of your idea being misapplied/misunderstood.

Reading this post and the initial comments made me concerned that your point was being misunderstood in a potentially dangerous way. That is why I felt the need to bring some analytical clarity to the table. It might not be for everyone, but it is there for anybody who wants to go deeper.

The code is meant exactly for those who might not be able to translate your argument to code for themselves. One can click through in R and get a graph that makes the point that Cor(x(t),x(t+1)) is a bad way to judge the presence of density dependence.

As for being deliberately provocative, meh.

Dear Dr. Fox,

I have tried to express some of my thoughts in a blog post since it was too long to serve as a comment: http://www.cottenielab.org/2013/01/variation-decomposition-is-zombie-idea.html

Any comments are of course appreciated, either here as a comment, or as a comment on my blog.

Sincerely,

Karl

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Quote the end of the original post: “**Approaches like that of Cottenie (2005) also have other serious problems (Gilbert and Bennett 2010).”

See Tuomisto, Ruokolainen, Ruokolainen (2012) in Ecography for a description of the causes of the apparently serious problems pointed out by Gilbert and Bennett, and for solutions. The proximate cause of the problem seems to be saturation of dissimilarity measures. I.e., Once communities share no species in common, the dissimilarity is zero, regardless of environmental or spatial distance. Saturated dissimilarities has two potential causes: long environmental gradients and insufficient sampling. There is statistical solution to the first cause, and an empirical solution to the second (sample sufficiently).

Interesting, will have a look. Although I still think there’s a deeper issue here: trying to infer process from pattern, based on unjustified intuitions about what sorts of patterns should be expected to arise from what sorts of underlying processes.

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