Musings from astrophysics to ecology

Can more research make a difference ?

Fly looking like a bee on a violet geranium flower

In the context of explaining my transition into ecological research, I am regularly facing questions / comments from both scientists and non-scientists, as to whether engaging in scientific research aiming at understanding the ecological or climate crises we are facing is (still) an effective and timely thing to do to address these crises. This post attempts to offer a nuanced, multifaceted view on this difficult question, involving not just scientific considerations but also human psychology, epistemology and politics

First of all, I have had multiple exchanges recently as to which of science vs. political engagement is the most important/effective in the current context. My answer is: both. This in my view is a false dichotomy, it doesn’t need to, and shouldn’t be an exclusive choice. Besides, we are all different people with different personalities, cultures, sensitivies and neural connections, and it is up to each of us, who are not mere robot-scientists but also concerned citizens with an independent political mind like anyone else (something some hardcore activists tend to think we do not have), to decide on a personal basis how we can best contribute. I have already dedicated a whole blog entry to why I personally mostly chose the “research way” so far. Tl;dr: research is where I currently feel I can have the biggest effect personally, and where my personality feels at home. The latter, incidentally, is not really up for discussion, unless one is interested in challenging and criticizing how other people’s brains are wired, which I don’t think has any particular merit.

With this caveat and particular point out of the way, there are a bunch of interesting points worth discussing on the role of scientific research in times of crises. Colleagues familiar with these matters will excuse my possible blind angles: I am always eager to learn, so drop a comment if you would like to point out something substantial that I may be missing. That will make me, and possibly some of my readership, smarter.

There is (and has been for quite a long time now) a mainstream, official (institutional) science policy discourse advocating for “more (interdisciplinary) science to face the ongoing crises”. I can see how this kind of discourse can be frustrating when it is not followed by any truly transformative action from research institutions. I often hear words like “silos”, “ivory towers” etc. to describe what is going on in practice. This discourse can also appear as simple wishful thinking (if not plain institutional greenwashing) considering that there is no rocksolid guarantee that knowing more about the environmental problems at hand is going to be of any help to solve them (more on this later). It is also possible to view this as a disingenuous, calculating way to get funding for one’s usual academic niches to keep doing more of the same. Finally, it is also perhaps a political convenience to put the burden of solving the ongoing crises on scientists (and blame the messenger when the broader society fails to do so), while to lowest order significant political action is likely the most important thing we need in the short term.

All of these are I think legimitate concerns about the political and scientific systems, that I largely share. This being said, things are degrading fast on the environmental side, and some of the changes we are already scientifically aware of, and whose consequences we are starting to witness at an increasing pace, are already baked in our future as a result of our past actions, and irreversible on human timescales. In this context, we must do all we can to mitigate and attenuate the bad stuff in in the near future, in a manner that is both efficient and respectful of nature and the environment itself. And achieving this goal requires (not exclusively, but irreducibly) doing rock-solid scientific research to develop a robust understanding of how extremely complex systems like ecosystems work in conjunction with their environment (whether it is the climate, or the human footprint on natural habitats), in order to design effective attenuation measures. The good news on this front is that ecological conservation action is already working overall, but it needs to be significantly scaled up and has a lot of potential for improvement.

In this context then, advocating that “we need more science” is not just a question of refining our knowledge of an already known problem in our ivory tower, while the world outside burns. As a matter of fact, effectively diagnosing, and knowing how a problem originates is not necessarily enough to figure out how to best mitigate it in a highly constrained socio-political environment (i.e. we can not necessarily revert the path already taken and need to find alternative paths to minimize the damage). Achieving such a goal requires its own specific fundamental scientific basis. And, on this front, a lot more can and should arguably be done.

The promise of a new generation

A few days ago, my attention was brought to an interesting perspective article in PNAS, “Developing a predictive science of the biosphere requires the integration of scientific cultures”, which precisely starts from the observation above. The argument the authors make is that, in biology and ecological sciences, there has traditionally been a larger separation between different scientific research cultures than in other, more mature fields like physics, and that this has hampered progress with finding scientific solutions to the problems we need to solve. The three “cultures” at hand, to make things simple, are: documenting and collecting stuff; detailed “hands-on” modelling using the maximum of data available to reproduce observed patterns and empirically predict stuff, not necessarily with a focus on causal attribution (think machine learning and AI, these days); and theoretical phenomenology (simplifying and conceptualizing how things work in more mechanistic effective terms). The authors call these three scientific cultures the variance, exactitude and coarse-grained cultures, respectively, and argue that to identify good scientific solutions to mitigate the crises at hand from an effective environmental action point of view, an effective synthesis of the three is required. They also stress that this is more of an epistemological issue than a problem with lack of interdisciplinarity (see beginning of this post).

While a bit abstract, there is some merit and underlying factual basis in these observations. Even in physics, the distinction between these different cultures exists, and it is a major epistemological issue in astrophysics (what do we call “understanding” there ? Describing what we see ? Fitting stuff ? Theorizing ? ), albeit with much lower odds and real world consequences than in ecological or climate modelling. What I have learned and observed so far on how the ecological research landscape is structured is pretty much in line with this assessment. Some of this may be attributable to cultural and historical reasons, but a good part of the problem undoubtedly stems from the sheer complexity of the systems under study. While physics is complicated, as a physicist already specializing in complex physical systems, it is quite obvious that we are dealing with relatively easy-peasy problems compared to biologists or ecologists. As such, there is no really obvious good or bad way to approach these problems in the first place.

Now, diagnosing the issue with finding solutions is all good but, assuming we are convinced more science is needed to mitigate the ecological crisis, how do we go on to overcome the problem in practice ? How do we go from something like “let’s do a coarse-grained theoretical model of this kind of stuff (waves hand) to understand it”, given a collection of increasingly fine-grained observations and data (point A), to scientifically motivated, actionable recommendations, preferentially rooted in a robust understanding of cause and effect, to mitigate the ecological crisis (point B) ? One of the main risks here, I know all too well from my experience in astro (and also my semi-insider knowledge of fields like fusion science), is that the chain between the starting point (building models) and end points (making robust and useful predictions, recommendations, and taking decisive action) can easily be broken, either because we get lost in the complexity of the system at some stage, face insurmountable technical hurdles, take deadly logical or technical shortcuts that compromise the whole edifice, or because funding or a long-term science policy commitment is lacking, or because the people involved get frustrated by the lack of progress, burn-out, change fields, or get distracted by other things (e.g. responsabilities or working in techno-administrative dystopia), or a mix of everything.

As a theoretician and a newb in ecology, I am not the best-placed person to offer meaningful insights on how to get from point A to point B in ecology (although I did my best in solar physics and other subfields of astro to move towards building better bridges between theory and observation in recent years) but at the very least it is a question and problem that has me thinking a lot at night when it comes to my own future research in ecology. While it is easy to take a path of least resistance and switch problems in research when one gets frustrated, or to get into a self-justifying vicious circle of doing more-of-the-same to justify one’s own existence, without making any further difference after a while, I would like to avoid this kind of pitfall in this new chapter of my career. I certainly do not want to indulge in the luxury of remaining disconnected from the drive that my work makes at least a small positive difference to the real world in the end. This is why I am doing my best to craft a personal research path which, while rooted in the “coarse-grained” theoretical approach most suiting to my physics background, attempts to integrate from its inception both a practical data analysis/usage component and a hands-on component aiming at becoming familiar with practical conservation research. While more than likely not sufficient, the minimal assumption here is that it is at least probably necessary to integrate these different components and approaches from the beginning in one’s own research if it is to make a non-zero difference, however small, in the end. In other words, I have effectively, for more than a year now, tried at my modest level, to turn the abstract synthesis idea of the recent paper discussed earlier into a practical plan. Devising a good research strategy to fullfill non-trivial specific goals is in effect a much harder task than devising a theoretical model, learning a new technique, or analysing a particular dataset. There is no guarantee that any of this is going to work in my case. I may give up at some stage for a variety of reasons (see above), or it may take me (or the broader scientific community, considering we are all facing similar questions) a prohibitively large amount of time to obtain very modest results that won’t necessarily make any difference in the grand scheme of things.

Which brings us back (hopefully slightly more enlightened) to the beginning of this post: can, and will more research make a difference ? Considering the uncertainties at hand, and short timescales on which we need to act, wouldn’t we be better off spending the money currently aimed at research (ecology included) on hands-on, short-term ecological conservation and climate-change mitigation actions ? Will more research actually lead to markedly more effective solutions and positive evolutions than just throwing at the problem all the tools and activism energy we already have ? This question occupies the mind not just of outsiders like me, but also of many environmental scientists who are concerned about the (lack of) impact of their own research. Phasing out of astrophysics to what I personally think is a more urgent area of research, there is certainly some irony in realizing that some of my ecology colleagues are themselves wondering whether doing research in ecology is still a timely and necessary thing to do to address the ongoing ecological crisis.

I don’t have a good answer to such an existential question, and I doubt anyone has. In fact, I have a feeling that it is also somewhat of a false dichotomy, and the only definitive statement I am prepared to make on this issue at this stage is that any definitive, radical take on it is almost certainly wrong. More than ever, we need to inform our decisions and actions by honest scientific doubt, and leave space to accomodate uncertainty and hope. Research is truly unpredictable and full of serendipity. If we manage to get our act together collectively and, importantly, to also motivate and enroll a new generation of young researchers bringing fresh views on old problems, there is a real chance we will be able to make a valuable difference. This opportunity can not be overlooked. What’s more, from a psychological point of view, the hope of discovery and the faith we place in the next generation are not really negotiable when you are a scientist. So, a more relevant question again perhaps is not whether we must go for it, but how we must organize, both as a community and as individuals, to motivate a new generation to get into some of today’s most important research problems, and to maximize the chances that the research we do together makes a difference in the end, with minimal regret if things do not quite go according to plan.

“The thing to do”, by Blue Mitchell

Leave a Reply

Your email address will not be published. Required fields are marked *


Leave a Reply

Your email address will not be published. Required fields are marked *