There are different kinds of mystery. Subatomic particles are almost illogically tiny, so we can only figure out what’s happening with big machines, long-term data, ingenious experiments, and a bunch of logical inferences. Because science is hard, then there are some simple facts about the world that we don’t know. For instance, the cause of gravity. It’s a mystery, but we have a specific question that we’re trying to answer, even if we don’t know the direction from which the answer will emerge.
We are missing fundamental facts at the foundation of physics. As Donald Rumsfeld would say, there are known unknowns. We know that there are certain things that we don’t know about physics, and are working to know them.
Ecology has a different kind of mystery. I don’t think we have big conceptual known unknowns. At least, I haven’t really heard anybody articulate them. Our big questions are, “I really want to understand X.” And X is something that we partially understand already, which needs lots of new information and ideas to understand more completely. We don’t have known unknowns, per se, we just have known partially-knowns.
The big questions that we have at the moment, are not a matter of discovering a straightforward mathematical relationship or generalized fact. At least, not one that we’re actively seeking, like the cause of gravity.
We have oodles of unknown unknowns in ecology — history has shown that we’ll have our socks blown off by finding out something when we weren’t even looking for it. But whenever physicists find out the cause of gravity, they will be in the process of looking for it. Even if the discovery is from a serendipitous unexpected find. Ecologists have a lot to learn from big ideas and big approaches like metabolic and species-energy theories, paleoecological models, Maximum Entropy Modeling, and other contemporary questions and approaches. And many that have yet to be developed. But this work is important in the revelation of details for pending questions, and those pending questions are about finding more complete answers, not hidden answers. These approaches are contributing to known partially-knowns.
The next big discovery in ecology is something that we, as a scientific community, won’t see until it’s quickly approaching us from the horizon. We don’t have a radar for the big questions off in the distance. At least, not any that we discuss on a regular basis.
This is particularly true for macroecology, the sprawling effort to figure out what governs patterns of organismal abundance and species richness across large spatial scales. These patterns involve energy, temperature, nutrients, metabolism, interaction networks, the earth’s history, and a lot more. It’s as complex as you choose to make it. The more complex you make things, the more you can explain. (That’s just a fact of statistics.) If you’re not an ecologist, you might not appreciate that there are government-funded centers dedicated to macroecological questions.
Ecology, at least most of the time, takes for granted what an “organism” is and what “species” are (though what constitutes individual organisms and species are, themselves, slippery issues). The challenge in ecology is to detect generalized patterns among individual organisms and species, what causes those generalized patterns, and to predict relationships.
Are you trying to explain species richness — how many species there are? If so, then at the global scale, there are only two things that matter:
- Speciation: When new species emerge.
Extinction: On a consistent but irregularly frequent basis, some species stop existing.
The number of species on this planet is governed by those two variables. Speciation and Extinction. That’s it. Nothing else. They’re not easy to measure, but there you have it. It couldn’t be more simple conceptually, even if it is a total bear to measure.
Planetary species richness isn’t an ecological question, per se. It’s an evolutionary question. As an ecologist, I’m not so excited about the nitty gritty of evolutionary questions (notwithstanding their centrality to biology). As I look at species richness as an evolutionary issue, I get less interested. (That’s just me and my academic predilections.)
Of course, species richness is indeed an ecological phenomenon, because we are interested in what happens at the subplanetary level. Ecologists want to know how, where, when, and — mechanistically — why some species occur in some places and not in other places.
When people are working to figure out these patterns of species richness, they sometimes get lost in the weeds of the details. As a result, sometimes the most obvious fact is presented as a research finding.
For example, a brand new paper in a peer-reviewed journal has the title: “Higher speciation and lower extinction rates influence mammal diversity gradients in Asia.” Here’s another one: “Faster speciation and reduced extinction in the tropics contribute to the mammalian latitudinal diversity gradient.”
You’ve gotta be kidding me.
To me, those titles read like: “Water can exist in different phases: solid, liquid and gas.” Or, “Zoologists observe that mammals have fur,” or perhaps “Activity in the brain influences behavior.”
Of course places that have more species have a combination of higher speciation rates and lower extinction rates! (Yes, measuring it isn’t necessarily easy. And, it’s mathematically possible for that not to be the case but still have that kind of richness gradient. Evidence for extinction rates acoss richness gradients isn’t as good as for speciation rates*. But, still. I think you see where I’m coming from.)
When you’re trying to figure out how many species are in a certain location — or look at multiple locations, perhaps along a gradient, it gets a little more complex. In addition to (1) speciation and (2) extinction, there are really two (and half) more variables that are fundamental to predicting species richness at the subcontinental scale.
- Species geographic range.
4 and a half. The range * scale interaction.
If you think of species occupancy of a certain location as a pixel, then the size of the pixel can really change what the range map looks like. If you look at a map of Birds of North America, then ranges are just big amoeba shapes on a broad scale. But if you were to create a very fine-scale map, then there are occupied canyons, empty bushes, and other microhabitats where organisms occur and don’t occur. For example, in the rainforest where I work, there are some species that (apparently) only occupy the clay banks of streams and not much anywhere else. They might have a very big coarse range map. But on the fine spatial scale, they will only be occupying a small part of a coarse range map.
Wait, did I say it gets a little more complex? I meant a lot more complex.
At the broadest scales, with just a few variables, we can predict species richness pretty well. (We can argue about the mechanisms causing those relationships, but those arguments won’t be settled with data. That’s a whole ‘nother problem.) But as spatial scale gets smaller, it falls apart. Down to the square meter — the scale at which I most often sample — our level of predictability is total crap. Even if I have lots of information at hand about several square meters directly adjacent to one another, I won’t have much ability to predict the species richness inside each of them.
It’s kinda funny that we can predict species richness across continents, but not a square meter in the backyard.
One explanation for this is the interaction between range and scale, and how it’s confounded by sampling effort. Most species are rare, and especially when working in a species-rich location, you won’t find all of them. So if we’re trying to know area that we can’t sample in its entirety, then we can only make estimates. And once you start estimating, then you can’t deal with specific information about each species, and you can only make models. And that’s where you throw your hands up when you realize that you don’t have a high level of predictability. Or you open up a big well-funded center and do lots of modeling.
To understand richness, we’ve got to consistently think about four things: speciation, extinction, range, and scale. Those are the things that are critical variables that need to be part of any generalized explanation for richness gradients. These four variables deal with the generation and loss of diversity, where it occurs, and how we measure it. If you’re not thinking about these variables, then you won’t really have a good understanding about how things are the way the are. If you have a model to explain richness that doesn’t explicitly or implicitly incorporate these parameters, then the model isn’t really an attempt to account for reality.
But here’s the problem with the attempt to find a generalized understanding of richness: each one of those four things is okay to work with on its own, but when you build in more than one of things, it’s a monster. And that’s just for a single biological taxon, and things often vary among taxa. While you need to account for speciation, extinction, range and scale, it doesn’t seem quite reasonable to try.
To an ecologist, speciation, extinction, range and scale are necessarily not the mechanisms, but the things that you need to account for in order to understand causal factors at sub-planetary scales. This is where metabolic rates, temperature, body size scaling, insolation, precipitation, seasonality, soil respiration and nutrient limitation (among everything else) matter.
Ultimately, what we are measuring are emergent phenomena of emergent phenomena of emergent phenomena. For example, when we measure that a particular tree occurs in a particular place, it had to start growing there. To grow from that location, it needed to have its seed arrive at some place, and experience the conditions for germination and withstand myriad forces that might have prevented it from reaching adulthood. The reason a tree lives somewhere is because of the nutrients and microbes in the soil, the temperature in the air, if the herbivores were hungry for it or not, the presence of a trampling hoof, and so many other things.
Once you start scrutinizing very fine spatial scales, hap and hazard overwhelm the powers of prediction.
I would guess that climate scientists can imagine if they measure five thousand different things at very fine resolutions, and have the computing power that reaches just beyond the limits of our imagination, that an accurate model of the climate might be possible. But for organisms? It would have to be even more complex. It’d have to model all of the brains of individuals that make decisions affecting the distributions of other organisms. We can’t even reliably predict if a rat will turn right or left in a maze, much less precisely where it will cache a seed.
In The Hitchhiker’s Guide to the Galaxy, Douglas Adams proposed that the Earth itself was a complex computer designed to find the the identity of a question with a very simple known answer. I think that’s the way we need to think as ecologists. We might even have the answer, but we don’t know the question we want to ask.
This is why so much of contemporary macroecology drives me frickin’ nuts. Because so many people want to propose a big explanatory model, make some big theory, when we know a priori that these models and theories won’t be able to create a generalized explanation as is often purported. Nearly all new papers are pegged to specific theories, when the information in those papers would be so much more helpful if it wasn’t pegged to an ephemeral concept that we’ll move past within the next decade or two. Okay, there is a new pattern, or a new understanding of pattern. Does this really have to be a test of a theory?
When nearly all new papers come out, we get some new information that helps increase the predictive power of existing concepts. We will get variables that supplement or replace other variables, providing new explanatory power. We can attempt to describe a mechanism as a TLA**, but these mechanisms are not providing mechanistic explanations of what happens, but are simply doing a better job at finding correlates of observed patterns. For example, knowing the scaling relationships associated with metabolic rates of organisms might help explain macroecological patterns. Even if that is true, and even if the metabolic theory of ecology has some universalities, then what we see are emergent patterns based on biological constraints. Not a new generalized mechanism. (Unless you think that emergent patterns based on biological constraints constitutes a mechanism, which if you want to define a mechanism that way, um, go on ahead and do so.)
Why do plants and animals — and microbes — occur where they do and fail to occur where they don’t? Science isn’t equipped to answer this as a why, we are looking at how this happens. And the more we look at this carefully, we’ll be able to explain even more.
Some macroecologists might be seeking to stumble on a grand new explanation, that mechanistically explains things better than the hodgepodge of correlates and theories we’re working with at the moment. These are the folks who hold out hope for a unknown unknown.
Other macroecologists might imagine that new information will serve to fill in the gaps of knowledge, and because species distributions are emergent phenomena of many haphazard processes, we will get better predictability and hone our ideas, but we won’t have a grandiose explanation that radically departs from what we have now. These are the folks who are working on the known partially-knowns.
I imagine most macroecologists would feel that they couldn’t be pigeonholed into either simplistic description.
I am prepared to be surprised by great new discoveries or realizations. I don’t know if there is an unknown unknown, but given the history of knowledge, that’s the most parsimonious possibility. How can there not be unknown unknowns? (In hindsight, natural selection is quite obvious, but a couple hundred years ago, it wasn’t something that people knew or understood.) Maybe some big grand simple explanation is out there. We don’t have the big known unknown like physicists have gravity. What so exciting is that we, as a community, know that we’ll be surprised when the topic of the next big discovery arrives.
In the meantime, could we stop trying to pitch incremental advances as grandiose explanations?
If you’re reading this and you are unsatisfied with my lack of nuance, then I can understand where you’re coming from. I happen to think these issues are experiencing too much nuance, and stepping away from minutia might help someone see things in a fresh light and generate new questions.
*A thoughtful (but not new) paper that deals with the details, derived from these fundamentals, is Mittelbach et al. 2007. It’s a good primer.
** Three Letter Acronyms