Looking up

I have spent the summer reading scientific articles and books I had put aside in springtime. The highlight of this period has not been reading ecology, but rather the recent book “Computing the climate: how we know what we know about climate change” by Steve Easterbrook. Indeed, the book has given me plenty of food for thought regarding how to approach (or not) modelling work in ecology, including my own. Let’s go down this rabbit hole!

First of all, let me state that Steve’s book is a highly accessible and enjoyable equations-free must-read for anyone interested in post-second world war science. Even people already familiar with climate science will learn a lot from it, and those less familiar will learn even more. In particular, fellow scientists and teachers reading this, please go read the book ! Even if you are not a climate scientist, it will provide you with everything you need to have informed, and much needed discussions with the broader society about climate change and how we have come to know what’s going on with the climate — and to debunk the massive disinformation and falsehoods still peddled around on this subject.

What I want to write about today, however, is not the climate science itself, but rather the specific thoughts about ecological modelling that the focus of this book on how climate modelling was born, developed, and how it is done today, has inspired me.

Climate science is, at this point, one if not the most advanced field across all of complex system sciences in terms of computational modelling (by complex system science, I mean the study of large systems with many interacting components and degrees of freedom, whose whole cannot be described as just the sum of its parts). Why and how it came to this position is the story of Steve’s book. The point most relevant to our discussion is that, despite the underlying complexity of the problem at hand, climate modelling has become a highly predictive and hyper-professional coordinated activity with no equivalent on Earth, either in public research or in the private sector. Each major model is maintained and developed in a collaborative way by hundreds of experts gathered from all parts of natural sciences, engineering, and computer sciences.

Interestingly, climate modelling didn’t start at all with the big goals we have in mind today, such as assessing precisely for the IPCC the degree of global warming associated with an increase of CO2 in the atmosphere (IPCC did not exist after the war and it isn’t until the end of the 1970s that climate became a serious matter of political conversation). Rather it started after the second world war as a bunch of audacious, exploratory computational and experimental physics projects run by a few physics and computer science pioneers. Back then, climate was not even the focus at all, and weather forecasting was not the main motivation for doing it either — forecasting was done through highly empirical methods at the time and atmospheric dynamics modelling did not become conducive to precise forecasting until many years after the first models appeared. At the inception of all this, it wasn’t even clear and even less guaranteed, considering the intrinsic complexity of the equations describing the climate in theory, that even simplistic atmospheric dynamics models could be run on a computer faster than real time.

Now, we all know the importance that weather, climate and atmospheric dynamics modelling and forecasting has taken in recent years, and it is easy to rationalize a posteriori the development of this science in the current political and societal crisis context. While many of these developments were clearly driven by the issue of understanding CO2-driven climate change, not all of them were, by far, and it was not obvious at all either that initially disparate research in atmospheric science, oceanography, glaciology, chemistry, etc. could some day lead to a successful integrated modelling of many of the relevant processes playing a critical role in shaping our climate.

Which brings me to the following question: given the ecological emergency we are facing, would some large-scale, integrated modelling like this be possible, relevant, and desirable in ecology ?

Having studied several aspects of the field (e.g. community ecology, population dynamics, conservation biology & evolutionary ecology) for almost two years now, and coming from a field where complex computational dynamical modelling has also become a very big thing (think e.g. simulations of the evolution of the large-scale structure of the Universe including the effects of small-scale physical processes), I would argue that in principle, there is no absolute reason why the modelling of the biosphere, and how it is affected by climate change and human activities, can not reach a similar degree of maturity and integration of complexity as climate science has. In fact, ecology today is in a much better state than climate science was in the 1950s, in terms of available technology, empirical knowledge, data, and instrumentation. Would a similar integrated modelling effort be worthy ? In both absolute intellectual and practical terms, probably yes, and in fact I suspect that more integrated efforts to make predictive global ecosystem models are going to be ramped up in the near future. Some parts of CNRS, for instance, are in the process of being reorganized to become a “biodiversity research agency” (much of that is political “greenwashing” posturing, but there are also some significants shifts of perspective happening underground among several of CNRS institutes, to develop along these lines).

So, let’s assume something like that is possible, and worthy of pursuit for its own sake. An important question then is why would we need that specifically, and what would we do with it ? Today, it is easy to see why climate science has become what it is: we live in a climate emergency and need tools to understand it precisely and to navigate the climate future, with its increased risks and extremes. On paper, it would be nice to have similarly accurate and powerful multi-scale (in time and space), multi-science (evolutionary, behavioural, networks/populations, physics, chemistry, maths, computer science etc.) integrated ecological modelling tools at global, regional, and local scales to forecast, manage, and find ways to possibly mitigate the ecological crises we are also living in.

Now, I think there’s a major difference with climate science here, and that difference is the gap between the required urgency of action and understanding (e.g., of ecosystem transitions/extinctions) and the current state of the field. Climate science was developed in the second half of the twentieth century and capitalized efficiently on many of these developments in the twenty-first century, in part also driven by the more short-term needs of weather forecasting. I may not have the full picture, but from what I have gathered from my reading and discussions, and my many past interactions and relationships with people and labs in climate science and atmospheric fluid dynamics, I do not think ecological modelling is anywhere near where climate modelling was even twenty years ago. Problem is, the climate emergency and ecological emergency are on the same timescale. Many physics colleagues with whom I have discussed my transition to ecological modelling tell me: “it’s all good and interesting what you are attempting to do, but it’s likely too late anyways to invest in that”. There are many (essentially social) motivations with which I disagree that possibly make them bring up this argument (like ostriches burying their head in the sand), but factually they still may have a point.

This gap is due to many factors, but two of them stand out for me: ecology as a science beyond “naturalism” is a much more recent field than physics and chemistry, and it is intrinsically a more complex science too. Unlike in astro & climate, in ecology scientists do not really know what equations need to be solved, or even if adequate sets of tractable mathematical modelling frameworks exist to describe spatio-temporal dynamical ecological process in a consistent, integrated way. In fact, I was warned about this in no uncertain terms by a few mathematical ecologists right when I stepped in the field, 18 months ago.

In this sense, climate scientists had it “easier” (yes, it is alway easy to find things easy a posteriori !): the definitive equations and laws of thermodynamics and fluid motion have been known since the XIXth century, and you can’t really go wrong with them if you know and have the material capacity to program them on a computer (you do need a computer to solve them though, and to program this computer in highly non-trivial ways, considering the underlying mathematical structure and properties of these equations). Of course, lots of people have already tried to borrow from the field of physics to describe ecological process (something I am also attempting to do, as this is the only thing I know how to do obviously), BUT there is at core nothing like an established set of equations or mathematical description set in stone for something that could be called ecological thermodynamics or out-of-equilibrium ecological dynamics, that looks like the Navier-Stokes equations of Clausius-Clapeyron law. Similarly, there is no definite general set of well-posed equations for eco-evolutionary processes. So where do we start ?

In ecology, any simplified model that fits the purpose of explaining some bit of data or observation is essentially legit today. And that’s all right: as the adage goes, all models are wrong, but some of them are useful ! But, given this, is it even possible to conceive achieving a useful integrated ecosystem model “of everything” on the timescale on which it is needed ? Does it even make sense to think about moonshot-like scientific modelling efforts aiming at building predictive global integrated ecological models in this emergency context ? Are we even clear what it is that we would like these models to answer and assist us with ? On the other hand, if we limit ourselves to a small-scale, reducive and reductionist approach of ecological research, with every group focusing on little bits and problems separately, and without a push to integrate the results in a broader perspective (this is similar to most fields of science, astro included, so no offence intended), is there any hope that this research can have a decisice, positive impact on the future of our planet ?

I do not have definitive answers to these questions of course, and neither should I expect to reach such answers in the future probably. My lack of experience in the field of ecology also likely prevents me from having a realistic global perspective on the whole field at this stage. Still, I find it worthy and in fact mandatory to ask myself, as a small piece of this big gigsaw puzzle, this kind of questions: as a sanity check, to clarify my own aspirations, and to define the role I can have in ecology research. Steve Easterbrook’s book on the history of climate science has certainly turned the knife in the wound in terms of what we as a community, and I, as a member of this community, can realistically hope to achieve in ecology on the relevant timescales.

Still, to end this blog post on a positive note, reading Steve’s book also gave me several reasons for hope and action. First, it is a wonderful achievement that so much has been learned on how our climate works in just 75 years considering the sheer complexity of the climate system, and this should provide hope for anyone working in similarly complex areas of science today. Second, if anything the book shows that climate science could not have progressed as a whole, and have become what it is now, without early exploratory numerical modelling efforts conducted by a handful of people in the 1950s and 1960s. The limitations of computers at the time forced them to think hard to simplify their models to the maximum, starting from well-known, yet untractable (for the time) non-linear partial differential equations hiding very complex phenomena, so as to extract the maximum amount of interesting physics and phenomenology at a minimal technical cost. These scientists were tremendously successful at doing just that and, as simple and limited as their first models were, what they found was essentially all that was needed to lowest order to understand how climate dynamics works. This, in the end, is probably what struck me most in the book.

So let this be the conclusion of this note: it is not impossible that qualitative, and possibly semi-quantitative global progress similar to what has been achieved in climate science can be made in understanding the dynamics of ecosystems in the near-future, if only we manage to keep a central goal in mind: focus on the big, important questions, and don’t miss the forest for the trees. Easier said than done! Because, what is the forest exactly, and what are you going to do with it ?

An interesting associated read on this problem: “Prediction in ecology: promises, obstacles and clarifications”, by V. Maris et al.

“The pressing need for anticipatory predictions should not mean that ecology is doomed to be a weak science. It is precisely by recognizing the difference between anticipatory and corroborative predictions that we allow ecologists to work at different time scales and recognize the value of slowly acquired corroborated knowledge that may in the future build up into a practical science, just as has happened into other areas of knowledge.”