Advancing plant functional trait science

I struggle at times to understand why we haven’t made much progress in understanding plant functional traits over the past ten years.

As has been well chronicled for over a century, plant functional traits are keys to understanding the evolution of plants, predicting ecosystem response to global change, and interpreting the distribution of species. None of the importance of plant functional traits has changed any time recently.

I would never argue that there has been no progress. For example, Wright et al.’s 2004 Nature paper on the worldwide leaf economic spectrum certainly is a landmark synthesis, but it was largely confirmatory from Reich’s work in the late 90’s. Baraloto’s recent work on the decoupling of leaf and stem economics is a good study that has the potential to be important. At the very least, advances have been sporadic and incremental.

Still, it just doesn’t feel like we’ve learned much in the past ten years about traits.

Regardless of how much advance there has (or hasn’t) been over the past 10 years, why hasn’t there been more?

In some ways I feel like there are a number of Catch-22 chicken-eggs involved in trait research. This isn’t an exhaustive list, but ones that seem to stand out.

• Funding agencies do not fund trait work. Major screening projects just are not funded. Most of the funding has been into syntheses of extant data while new data has largely come from side projects and student work.
• Pot-phobia. I’ve talked about the “pot effect” before and no one would deny that plants can sense their environment. Yet, proposing to grow plants in pots inevitably generates criticism. For example, one proposal review recently included the criticism “The plan to compare plants grown in small pots in growth chambers is questionable, since small pot effects will likely cause artifacts”. The word ‘artifact’ is a dismissively loaded term here. Besides, there is never criticism for the “field effect”—the artifact of growing small plants in an unconstrained soil volume with excess resources. Put briefly, intraspecific variation and plasticity is a bugaboo that can kill broader questions.
• No new conceptual advances to test. There are still exciting untested hypotheses, but there is the perception that the discipline is a bit dead intellectually. CSR has never been modernized while LHS is just three orthogonal traits. Not much new seems to have taken its place. The lack of a exciting toe-hold here hurts.
• Phylogenies are incomplete. It’s hard to describe what a drag on progress this is. Without a robust phylogeny, species and traits cannot be compared evolutionarily. For example, it’s hard to do congeneric comparisons when it can’t be agreed that species belong in the same genera. And to require ecologists to generate phylogenies is an unnecessary requirement that doesn’t promote long-term growth.
• Post-SLA research in a SLA paradigm. The leaf economic spectrum is a great advance, but the common perception to many is that SLA is the central trait of plants. Here’s one comment we received recently on a proposal: “It was odd not to see conventional traits like SLA… included in this work”, even though we had proposed to measure the components of SLA: leaf thickness and tissue density. Put briefly, there is too much uncertainty on whether SLA is a central trait that structures plant evolution and ecology, or whether SLA should R.I.P. for a new generation of metrics.
• The decline of traditional physiological ecology. This one is unquantifiable, but the central importance of physiological ecology to ecology has been diluted. The rise of model organisms and ecosystem ecology/global change biology has at the very least diluted the middle ground that was plant physiological ecology, instead of strengthened it as a discipline. I think there’s been a loss of the perspective that comes from being at the nexus of plant evolution, biogeography, and ecosystem function.

So what to do? I don’t have clear answers here. This post is just a scratchpad for me.  A couple thoughts come to mind.

• We can’t always wait on phylogenies. If a phylogeny doesn’t exist, it is not helpful to insist that ecologists create one or that we wait. Some aspects of the work might later get revised, but functional trait work can be done in advance of the phylogenies. Especially considering how often phylogenies get revised.
• We need model species sets. The rise of model organisms—and the resources devoted to their study—has  been quite amazing. Model organisms in and of themselves do not help us understand plant functional traits too much. They aren’t inherently comparative. I think we need model species sets to complement model organisms. For a broad clade, we need to identify a reasonable number of species that represents a broad set of evolutionary and ecological contrasts. This set then needs to be examined by multiple researchers, just like with model species.
• The pot effect needs to become irrelevant. We will always need to grow plants in containers. We need clear understanding of how containers affect genetic expression and plant functional traits. Direct research is required here.
• We need better theories. All disciplines need buzz. Plant functional trait research doesn’t have it. It needs it.
• We need to measure old traits more, but we also need to develop new traits. SLA and rooting depth isn’t enough to help us understand how plants have been shaped and respond to everything from drought to herbivores.
• We need to encourage breadth in our science. Plants have been shaped and respond to a multitude of environmental factors. You can’t describe an elephant by grabbing its tail, nor by having a number of scientists grabbing individual parts. Some need to try and feel the whole and understand how the parts come together.