A couple of weeks ago, I was doomscrolling surfing the r/Science community on Reddit while taking a break when I came across this absolute legend of a paper: Will any crap we put into graphene increase its electrocatalytic effect?

Briefly, these authors were sick of the plethora of graphene-doping papers plaguing the field of material sciences – so much that researchers were publishing a new paper for every combination of elements used to dope graphene to improve its electrocatalytic properties. In comedic fashion, the authors doped graphene with literal crap (guano, aka bird poop) and showed even that could improve its electrocatalytic properties. Unashamedly, the authors trashed the mountain of graphene-doping studies that had no business being in the scientific literature. A hilarious read.

After I was done catching my breath, the paper still stuck in my mind – and not solely because of its comedic effect. In recent years, the number of papers in every scientific field has exploded – ecology included (see my previous post). And in my field, every month I could expect to see at least one new paper claiming, “xxx environmental factor alters yyy plant trait”, or “global change influences plant communities by shifting zzz trait”.

How is that any different from the graphene-doping study above?

Ecologists generally don’t like to predict stuff

Interest in how global change may influence ecosystems and biodiversity has (rightfully) exploded in the past two decades, and ecologists have caught on with the trends by pushing out numerous papers documenting how species’ traits have been altered as environmental conditions vary. For example, Green et al. (2022) explicitly quantified this trend among ecology journals, with over 800 trait-based ecology studies published from 1978-2018. Disappointingly, however, only ~3% of these studies utilized the trends in functional traits they found to predict ecological phenomena beyond the dataset compiled in their original study.

I wrote about the predictive power of ecology in a different post last year, where I lamented about the lack of studies in ecology that actively sought to predict ecological phenomena at any meaningful scale. Perhaps the lack of such papers could be attributed to the weak R² and explanatory power of current models, dissuading researchers from publishing their findings? Alternatively, perhaps predicting the future requires massive data – something that just wasn’t feasible without the abundance of trait-based data that we lacked until only recently? Maybe that was what holding ecologists back from producing prediction-centric research.

While I am glad to see my field so rich in data nowadays, sometimes I wonder whether there are diminishing returns to observing and documenting species’ traits, especially in the absence of a mechanistic framework. I admit I am part of the problem – I have published multiple studies of that nature before (though in my defense, the part of the world where I work in is extremely underrepresented). But now that I am a bit more mature in my research career and am actively pondering my next steps, now I am thinking “is there a better way forward?”

Why observation-centric studies aren’t enough

The abundance of data we have nowadays is both a blessing and a curse. On one hand, trait-based datasets (especially for plants) have exploded in recent years (e.g. see this, and this), and ecologists are now blessed with endless ways to play with new data to test novel hypotheses on how plants respond to their environment, and to one another.

At the same time, because of the sheer volume of data we have at our fingertips, there is also an endless number of hypothesized mechanisms that could explain the trends in our data – and no easy way to tell which ones are actually true. Take for example, this very recent study that looked at how root traits of forest communities shift with respect to eCO₂ in the Amazon. The authors reported an increase in plant specific root length (SRL, a measure of how efficient plants forage for nutrients per unit biomass), root tissue density (RTD, a measure of tissue density and root longevity) and arbuscular mycorrhizal colonization rates (a measure of mutualistic associations with fungi). From these trends, the authors postulated a number of mechanisms to explain their findings:

1. Plants were relying more on mycorrhizae for nutrient foraging.
2. Plants increased SRL to enhance soil exploration and mine organic matter in the soil for nutrients.
3. Plant root longevity was enhanced by the increase in RTD and reduced fine root production, suggesting that plants were replacing their roots less often under eCO₂.

That’s a lot of mechanisms to cover in one study (and I haven’t even listed all of them yet)! Yet, which of these are true? Looking at the same results, one could rightfully criticize:

1. without any measure of plant nutrient uptake or mycorrhizal foraging*, how can we sure that plants actually rely more on mycorrhizae for nutrient uptake (or otherwise)?

*Understandably, both variables are hard to measure in practice. However, this still doesn’t dismiss the point that mycorrhizal colonization rate in roots doesn’t really tell us a lot (if anything at all)

• there is very little evidence that plant root longevity increases with RTD.
• without an additional proxy (e.g. fine root standing stocks, or mortality rate), it is difficult to infer whether plants replaced their roots less often (i.e. a conservative strategy as the authors proposed).

This is not to say this is a bad study – it does provide important evidence that our forests in the Amazon will respond physiologically in some ways to eCO₂. Yet, like many observation-centric studies (or essentially any experimental manipulation study in-situ), without a strong way to narrow down which mechanisms are driving the results, we can only conclude that something is happening — but we aren’t quite sure what.

Inferring mechanisms is way harder, but more insightful

Designing an experiment that can properly elucidate an ecological mechanism is tremendously hard – I would argue more so than any other science. This is because in nature, everything is interlinked, and there are so many confounding factors to account for. Most of the time, one cannot expect to cleanly separate interacting entities to study them individually, such as roots, fungi and soil microbes. That is why in practice, ecologists often rely on proxies that theoretically reflect the mechanisms of interest, such as functional traits.

At the same time, these proxies can only take us so far, before someone starts questioning “is variable xxx really representative of yyy?” To close the chasm between observations and mechanisms requires thinking hard about the limits of our inference before a study is conducted – what can we truly say even if we do get a significant result? Alternatively, another way forward is for ecologists to review and compare past findings to test what differences might explain why two findings/studies don’t agree with each other. The latter, however, requires extensive and deliberate effort by networks of researchers to document, maintain and replicate past experimental setups – no different from how physicists and chemists do lab-based research. With the current economic climate of science, I am not particularly confident the latter will ever bear fruit.

As I mentioned previously, my personal ambition for my work is to produce ecological findings that are predictive, not merely descriptive. A lofty goal perhaps, but if it means slowing down one’s rate of publishing to increase the quality of one’s research output, that’s a worthwhile trade-off in my eyes. And in my humble opinion, we need more ecologists doing the same – focus on crafting simple, well-designed experiments that can clearly tell us something mechanistic, rather than broad studies with elaborate setups that contain an overwhelming number of possible interpretations.