A signal of competitive dominance in mid-latitude herbaceous plant communities

Understanding the main determinants of species coexistence across space and time is a central question in ecology. However, ecologists still know little about the scales and conditions at which biotic interactions matter and how these interact with the environment to structure species assemblages. Here we use recent theoretical developments to analyse plant distribution and trait data across Europe and find that plant height clustering is related to both evapotranspiration (ET) and gross primary productivity. This clustering is a signal of interspecies competition between plants, which is most evident in mid-latitude ecoregions, where conditions for growth (reflected in actual ET rates and gross primary productivities) are optimal. Away from this optimum, climate severity probably overrides the effect of competition, or other interactions become increasingly important. Our approach bridges the gap between species-rich competition theories and large-scale species distribution data analysis.


Recommendation?
Major revision is needed (please make suggestions in comments)

Comments to the Author(s)
As noted in my emails to the editor, I reviewed this paper in February at Ecology Letters. Because the paper has not been substantively changed since that review, I am re-submitting the same review text that I provided at Ecology Letters.

Summary:
The study uses a competition model, in which competitive hierarchy is related to maximum plant height, to explain variation in the fraction of regional diversity which is found at smaller scales across a large number of sites in and around Europe. These results are used to support the hypothesis that joint impacts of temperature and water availability on species trait syndromes and competitive hierarchies are primary drivers of local diversity in the region.
General Comments: First off, let me say that I think that this is wonderfully elegant, simple, and tractable model. I also applaud you for applying mechanistic insight about the underlying traits in your model to structure how species are assumed to interact -i.e. by focusing on asymmetrical effects of height differences, rather than just average trait distance, as is often done in other trait-based studies. Additionally, I think that the overall pattern that you identify -i.e. significant increases in traitbased clustering at mid-latitudes -is quite interesting and convincing. Taken together, I think that this paper demonstrates some very interesting patterns, and includes a plausible, semimechanistic explanation of why that pattern might exist.
Nevertheless, I have a number of major concerns about how the model is presented and interpreted. In particular, I think that there are a number of very strong assumptions in this model that are either not tested or well-supported, or for which the ramifications of breaking those assumptions are not explored. And, indeed, in many cases, I think there is quite a bit of evidence suggesting that these assumptions are not met in real-world systems (including many papers that you cite). Although you note some of these potential problems near the end of the discussion, as far as I can tell, there is not much included in this paper to demonstrate that your results are robust to these concerns, nor is it clear what kinds of biases might appear as a result of these confounding processes. In order for the paper to be more convincing to me, I think that it would require a major restructuring that more closely focused on identifying and quantitatively testing these assumptions.
1. Maximum height as the primary competitive indicator First and foremost, I think that focusing on height as the primary (and only?) indicator of competitive hierarchy is not well supported by existing literature on herbaceous plant competition. In my detailed comments below, I include a number of specific citations that discuss other putative influential processes and traits that are potentially independent of height -e.g. herbivore resistance, mineral resource requirements, and eco-evolutionary history. Although I am not generally opposed to applying a simplified model with a small number of traits (and, as I said above, although I very much appreciate the simplicity of your model, and the mechanistic insight that it uses to model height-based interactions), I think that a lot more text and analyses would need to be devoted to justifying and testing this strong, central assumption.
Additionally, I worry that using "maximum height" taken from a general database of plant traits is potentially problematic. First, maximum values are strongly influenced by sample size -thus, plants that have been sampled many times (e.g. common species) will almost always have greater maximum height values than those that have only been sampled a few times (e.g. rare species).
Thus, I would generally suggest using a quantile-based matric (e.g. 95th percentile height), as this value tends to be a bit more robust to sample size.
Morover, as you note in the text, height is an enormously plastic trait. At the very least, the fact that different species in the database are likely to have been measured under different conditions will add substantial observation error to the analyses. Moreover, it is very likely to also add bias. For example, in my own work with these databases, I have found that because weedy species tend to occur and be measured disproportionally in ruderal areas, they also tend to have significantly higher reported heights than non-weedy species -despite the fact that the relationship is typically reversed at the site level. Ideally, height data should be standardised based on differences in measurement conditions among sites -although this is rarely possible in practice. At the very least, I would strongly urge an analysis of some subset of the data where heights have been measured under standardised conditions, in order to demonstrate that your reported results remain unchanged.
2. Effects of the regional species pool As far as I understand it, the regional species pool is taken directly from observations (i.e. it is not an emergent result of the model, but rather is an input that is subsequently used to model local diversity). At the very least, I think it would be worth discussing in a bit more detail what kind of limitations this might have for your results -e.g. much of the literature on evolutionary biogeography would argue that once the regional pool has been assembled, the local composition is more or less pre-ordained, and local interactions have very impact on outcomes. Again, you note some of these concerns briefly in the end of the discussion, but as far as I can tell, you do not include justifications that would explain why these concerns do not apply to your model. If possible, I would suggest trying to test the effects of the regional pool on your results. For example, to what extent do the clustering patterns that you identify arise as a general response to the climate gradients you are studying, regardless of the size and composition of the regional pool? Apologies if I am missing a part of the analysis that does this already -I know that the randomization routine that you apply does a good job of identifying significant trait clustering, but I'm not sure that this quite gets at the question that I am asking here.
3. Concepts of "ideal" growth conditions I would suggest being a bit more careful about how you discuss "ideal" conditions for plants. It is true that many herbaceous plants grow "best" when water availability is high, and temperatures do not drop too low. But, these patterns are by no means unimodal, nor are they universal. For example, environments that are too wet can lead plants to drown if their roots are saturated, and can cause early mortality and fast turnover due to, e.g. fungal infections. Likewise, high night time temperatures can lead to increases in respiration rates, thereby reducing overall growth. A good source that discusses many of these relationships is Lambers & Oliveira (2020), or other earlier additions. I think it would be a good idea to discuss your results in light of these more nuanced effects of climate on plant growth, rather than focusing on the "optima" that you discuss currently.
4. Discussion of Chesson's theory Lastly -a minor point, but much of the abstract and introduction focuses on Chesson's coexistence theory. But, I am not sure that your analyses draw very heavily on this literature or concept -rather, it tests a much or common hypothesis related to how functional traits and competitive forcing are related. As I discuss below, these concepts has been explored using Chesson's theory, but it is by no means a major component of it (his theory, rather, focuses on partitioning different kinds of impacts on species invasion rates when rare). Moreover, I think that the empirical evidence supporting the link between his theory and the functional trait literature are weak at best. I would suggest either removing this discussion from your manuscript, or making the link with Chesson's theoretical models clearer.
Specific Comments: 17-20: I am not so sure that there is strong evidence that functional trait clustering corresponds to fitness differences (or for that matter, to niche differences, or to coexistence in general). It is true that Kraft et al. (2015) demonstrate such a relationship in one system, but their model is also unable to explain realised local coexistence at their site -Although they attribute this to spatial heterogeneity, an equally good explanation is that their model simply didn't fit the data very well, and that that the realised values for niche and fitness differences are therefore not very meaningful. I know of very little evidence for the correlation between trait clustering and Chesson's metrics outside of this paper (or other papers that directly use the same dataset and model) -and, several papers (e.g. Letten et al. 2017) seem to suggest that no such relationship should be expected at all. And, to the best of my understanding, the Mayfield & Levine paper is primarily a perspectives piece, and does not offer much empirical proof for the hypothesized relationship. Do you have any more general evidence to support this statement, and this general framework? 20-22: I agree with this statement -although I suspect many macroecologists would disagree. E.g. the Ricklefs (2008) paper you cite in the discussion rather energetically argues that large-scale diversity is driven by geography and evolutionary history, and that local species interactions are largely irrelevant. I think that this perspective might be worth discussing here in more detail. 31-32: "within the limits of structural stability": What do you mean by this? I.e. does this refer to physical stability of the plant (e.g. tree vs. grass growth forms), or to "structural stability" in the mathematical sense? 35-43: How much evidence is there in these sites that competitive hierarchy is determined primarily via traits related to height, rather than, e.g. competition for soil mineral resources? Is there a strong reason to believe that height is a better indicator of competitive interactions than any other trait in these systems? 53-58: Based on your other papers, my understanding is that in this model, competitive interactions are highly asymmetrical and follow a strict competitive hierarchy. While I agree that this structure will generally lead to a decline in local coexistence with stronger average competitive interaction strength, I do not believe that this result must be general -e.g. if the strict competitive hierarchy is removed, or if a trade-off is present (e.g. if species with lower competitive hierarchy also tend to have higher carrying capacity). This isn't necessarily a problem, nor does it mean that your model isn't useful, but I would be careful to point out that the negative relationship between realised coexistence and average competitive intensity is largely a tautological result of the model structure, rather than a general relationship that must appear in all systems.
113-115: Can you explain this a bit more ecologically? I.e. is there a biological reason that the log differences are more meaningful than differences in linear space? 127-128: "Larger plants capture more resources": Again, I don't think that this is necessarily true. For example, in a system that is nitrogen limited, smaller plants often have much higher tissue nitrogen concentrations, and ultimate take up more total nitrogen, than do larger plants (e.g. small herbs vs. tall grasses). Similarly, competitive ability for water can be inversely related to size, specifically because larger plants with larger leaves often lose more water to transpiration, and therefore require higher soil water concentrations to persist. In both of these cases, I think that the problem is exacerbated because you use height (e.g. rather that total above-+ belowground biomass) as your size index. Your argument is potentially a bit more correct for light competition, though again, it will depend on how biomass is distributed as a function of height.
In any case, I don't think that one can axiomatically use this statement to justify that evolution should favour taller plants as the primary mechanism of resource competitive ability. 151-155: Does the model consider the possibility of variable immigration rates, and variable carrying capacities, among species? If not, how would fitting the model to data with variables rates and capacities influence the parameter estimates? 161-167: A minor point, but it seems like this is a 2-tailed test? In this case, I think that the "classic" way of testing at alpha = 0.05 would be to use the 2.5% and 97.5% quartiles as the reference states, such that the combined probability of the lower plus upper tails equals 5%. Apologies if I am missing something. 184-185; 194-198: Again, I am not sure that it is correct to state that evapotranspiration is known to be the primary indicator of environmental constraints on plant growth at large scales. Others have posited, e.g. herbivore-based controls (Borer et al. 2014), soil chemistry-based controls (Laliberte et al. 2014), or biogeographic/evolutionary controls (Ricklefs 2008;McKenna et al. 2009).
I think you are probably correct that a rough correlation between growth rate and evapotranspiration rates exists, and that this correlation is a good general indicator for growth rate, all else being equal. But, there is a huge amount of residual variance that isn't captured by these trends, which makes it difficult to label certain conditions as being "optimal" for plant growth. For example, even "optimal" radiation, water availability, and temperatures can lead to declines in growth -e.g. due to high covariance with herbivore or fungal abundance. 242-243: I'm not sure I agree with this statement -Given, as you say, that one of the defining aspects of a community is that species can interact, it seems important that they should be studied at scales within which interactions are possible. E.g. if a study fails to find significant evidence for species interactions at a 50x50 km2 scale, that hardly means that species interactions are irrelevant to community structure -it just means that if there are significant effects, they occur at scales that are too small to be captured within the grain used by the study.
Just as a simple example: Both Typha and Arrhenatherum can easily exist in the same 50x50km2 grid cell, but they will almost certainly never interact at local scales, simply because they cannot grow under the same conditions. In other words, co-occurrence at one scale cannot necessarily be taken as evidence of co-occurrence at smaller scales. 257-258: This seems to be the first section where you suggest that the correspondence between height and competitive ability that you assume may not hold -But, you don't discuss how breaking this assumption might alter your results. At the very least, I would suggest including a somewhat longer justification of why you think that your results demonstrate that height does indeed universally correspond with competitive hierarchy, and discuss what your results would have looked like had this assumption not been met. 274-276: I'm not totally sure that this is correct -e.g. the Tilman results that you cite generally suggest the existence of some kind of limiting similarity in competitive abilities, which would lead to disaggregation of traits. The legend says that panel (d) shows "Correlation between mean gross primary productivity (GPP) and mean annual ET", but the figure shows ET on both axes.

Spelling and Grammar:
Decision letter (RSOS-201361.R0) The editorial office reopened on 4 January 2021. We are working hard to catch up after the festive break. If you need advice or an extension to a deadline, please do not hesitate to let us know --we will continue to be as flexible as possible to accommodate the changing COVID situation. We wish you a happy New Year, and hope 2021 proves to be a better year for everyone.

Dear Dr Capitan
The Editors assigned to your paper RSOS-201361 "A signal of competitive dominance in midlatitude herbaceous plant communities" have now received comments from reviewers and would like you to revise the paper in accordance with the reviewer comments and any comments from the Editors. Please note this decision does not guarantee eventual acceptance.
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Summary:
The study uses a competition model, in which competitive hierarchy is related to maximum plant height, to explain variation in the fraction of regional diversity which is found at smaller scales across a large number of sites in and around Europe. These results are used to support the hypothesis that joint impacts of temperature and water availability on species trait syndromes and competitive hierarchies are primary drivers of local diversity in the region.
General Comments: First off, let me say that I think that this is wonderfully elegant, simple, and tractable model. I also applaud you for applying mechanistic insight about the underlying traits in your model to structure how species are assumed to interact -i.e. by focusing on asymmetrical effects of height differences, rather than just average trait distance, as is often done in other trait-based studies. Additionally, I think that the overall pattern that you identify -i.e. significant increases in traitbased clustering at mid-latitudes -is quite interesting and convincing. Taken together, I think that this paper demonstrates some very interesting patterns, and includes a plausible, semimechanistic explanation of why that pattern might exist.
Nevertheless, I have a number of major concerns about how the model is presented and interpreted. In particular, I think that there are a number of very strong assumptions in this model that are either not tested or well-supported, or for which the ramifications of breaking those assumptions are not explored. And, indeed, in many cases, I think there is quite a bit of evidence suggesting that these assumptions are not met in real-world systems (including many papers that you cite). Although you note some of these potential problems near the end of the discussion, as far as I can tell, there is not much included in this paper to demonstrate that your results are robust to these concerns, nor is it clear what kinds of biases might appear as a result of these confounding processes. In order for the paper to be more convincing to me, I think that it would require a major restructuring that more closely focused on identifying and quantitatively testing these assumptions.

Maximum height as the primary competitive indicator
First and foremost, I think that focusing on height as the primary (and only?) indicator of competitive hierarchy is not well supported by existing literature on herbaceous plant competition. In my detailed comments below, I include a number of specific citations that discuss other putative influential processes and traits that are potentially independent of height -e.g. herbivore resistance, mineral resource requirements, and eco-evolutionary history. Although I am not generally opposed to applying a simplified model with a small number of traits (and, as I said above, although I very much appreciate the simplicity of your model, and the mechanistic insight that it uses to model height-based interactions), I think that a lot more text and analyses would need to be devoted to justifying and testing this strong, central assumption.
Additionally, I worry that using "maximum height" taken from a general database of plant traits is potentially problematic. First, maximum values are strongly influenced by sample size -thus, plants that have been sampled many times (e.g. common species) will almost always have greater maximum height values than those that have only been sampled a few times (e.g. rare species). Thus, I would generally suggest using a quantile-based matric (e.g. 95th percentile height), as this value tends to be a bit more robust to sample size.
Morover, as you note in the text, height is an enormously plastic trait. At the very least, the fact that different species in the database are likely to have been measured under different conditions will add substantial observation error to the analyses. Moreover, it is very likely to also add bias. For example, in my own work with these databases, I have found that because weedy species tend to occur and be measured disproportionally in ruderal areas, they also tend to have significantly higher reported heights than non-weedy species -despite the fact that the relationship is typically reversed at the site level. Ideally, height data should be standardised based on differences in measurement conditions among sites -although this is rarely possible in practice. At the very least, I would strongly urge an analysis of some subset of the data where heights have been measured under standardised conditions, in order to demonstrate that your reported results remain unchanged.
2. Effects of the regional species pool As far as I understand it, the regional species pool is taken directly from observations (i.e. it is not an emergent result of the model, but rather is an input that is subsequently used to model local diversity). At the very least, I think it would be worth discussing in a bit more detail what kind of limitations this might have for your results -e.g. much of the literature on evolutionary biogeography would argue that once the regional pool has been assembled, the local composition is more or less pre-ordained, and local interactions have very impact on outcomes. Again, you note some of these concerns briefly in the end of the discussion, but as far as I can tell, you do not include justifications that would explain why these concerns do not apply to your model. If possible, I would suggest trying to test the effects of the regional pool on your results. For example, to what extent do the clustering patterns that you identify arise as a general response to the climate gradients you are studying, regardless of the size and composition of the regional pool? Apologies if I am missing a part of the analysis that does this already -I know that the randomization routine that you apply does a good job of identifying significant trait clustering, but I'm not sure that this quite gets at the question that I am asking here.
3. Concepts of "ideal" growth conditions I would suggest being a bit more careful about how you discuss "ideal" conditions for plants. It is true that many herbaceous plants grow "best" when water availability is high, and temperatures do not drop too low. But, these patterns are by no means unimodal, nor are they universal. For example, environments that are too wet can lead plants to drown if their roots are saturated, and can cause early mortality and fast turnover due to, e.g. fungal infections. Likewise, high night time temperatures can lead to increases in respiration rates, thereby reducing overall growth. A good source that discusses many of these relationships is Lambers & Oliveira (2020), or other earlier additions. I think it would be a good idea to discuss your results in light of these more nuanced effects of climate on plant growth, rather than focusing on the "optima" that you discuss currently.

Discussion of Chesson's theory
Lastly -a minor point, but much of the abstract and introduction focuses on Chesson's coexistence theory. But, I am not sure that your analyses draw very heavily on this literature or concept -rather, it tests a much or common hypothesis related to how functional traits and competitive forcing are related. As I discuss below, these concepts has been explored using Chesson's theory, but it is by no means a major component of it (his theory, rather, focuses on partitioning different kinds of impacts on species invasion rates when rare). Moreover, I think that the empirical evidence supporting the link between his theory and the functional trait literature are weak at best. I would suggest either removing this discussion from your manuscript, or making the link with Chesson's theoretical models clearer.
Specific Comments: 17-20: I am not so sure that there is strong evidence that functional trait clustering corresponds to fitness differences (or for that matter, to niche differences, or to coexistence in general). It is true that Kraft et al. (2015) demonstrate such a relationship in one system, but their model is also unable to explain realised local coexistence at their site -Although they attribute this to spatial heterogeneity, an equally good explanation is that their model simply didn't fit the data very well, and that that the realised values for niche and fitness differences are therefore not very meaningful. I know of very little evidence for the correlation between trait clustering and Chesson's metrics outside of this paper (or other papers that directly use the same dataset and model) -and, several papers (e.g. Letten et al. 2017) seem to suggest that no such relationship should be expected at all. And, to the best of my understanding, the Mayfield & Levine paper is primarily a perspectives piece, and does not offer much empirical proof for the hypothesized relationship. Do you have any more general evidence to support this statement, and this general framework? 20-22: I agree with this statement -although I suspect many macroecologists would disagree. E.g. the Ricklefs (2008) paper you cite in the discussion rather energetically argues that large-scale diversity is driven by geography and evolutionary history, and that local species interactions are largely irrelevant. I think that this perspective might be worth discussing here in more detail. 31-32: "within the limits of structural stability": What do you mean by this? I.e. does this refer to physical stability of the plant (e.g. tree vs. grass growth forms), or to "structural stability" in the mathematical sense? 35-43: How much evidence is there in these sites that competitive hierarchy is determined primarily via traits related to height, rather than, e.g. competition for soil mineral resources? Is there a strong reason to believe that height is a better indicator of competitive interactions than any other trait in these systems? 53-58: Based on your other papers, my understanding is that in this model, competitive interactions are highly asymmetrical and follow a strict competitive hierarchy. While I agree that this structure will generally lead to a decline in local coexistence with stronger average competitive interaction strength, I do not believe that this result must be general -e.g. if the strict competitive hierarchy is removed, or if a trade-off is present (e.g. if species with lower competitive hierarchy also tend to have higher carrying capacity). This isn't necessarily a problem, nor does it mean that your model isn't useful, but I would be careful to point out that the negative relationship between realised coexistence and average competitive intensity is largely a tautological result of the model structure, rather than a general relationship that must appear in all systems.
113-115: Can you explain this a bit more ecologically? I.e. is there a biological reason that the log differences are more meaningful than differences in linear space? 127-128: "Larger plants capture more resources": Again, I don't think that this is necessarily true. For example, in a system that is nitrogen limited, smaller plants often have much higher tissue nitrogen concentrations, and ultimate take up more total nitrogen, than do larger plants (e.g. small herbs vs. tall grasses). Similarly, competitive ability for water can be inversely related to size, specifically because larger plants with larger leaves often lose more water to transpiration, and therefore require higher soil water concentrations to persist. In both of these cases, I think that the problem is exacerbated because you use height (e.g. rather that total above-+ belowground biomass) as your size index. Your argument is potentially a bit more correct for light competition, though again, it will depend on how biomass is distributed as a function of height. In any case, I don't think that one can axiomatically use this statement to justify that evolution should favour taller plants as the primary mechanism of resource competitive ability. 151-155: Does the model consider the possibility of variable immigration rates, and variable carrying capacities, among species? If not, how would fitting the model to data with variables rates and capacities influence the parameter estimates? 161-167: A minor point, but it seems like this is a 2-tailed test? In this case, I think that the "classic" way of testing at alpha = 0.05 would be to use the 2.5% and 97.5% quartiles as the reference states, such that the combined probability of the lower plus upper tails equals 5%. Apologies if I am missing something. 184-185; 194-198: Again, I am not sure that it is correct to state that evapotranspiration is known to be the primary indicator of environmental constraints on plant growth at large scales. Others have posited, e.g. herbivore-based controls (Borer et al. 2014), soil chemistry-based controls (Laliberte et al. 2014), or biogeographic/evolutionary controls (Ricklefs 2008;McKenna et al. 2009). I think you are probably correct that a rough correlation between growth rate and evapotranspiration rates exists, and that this correlation is a good general indicator for growth rate, all else being equal. But, there is a huge amount of residual variance that isn't captured by these trends, which makes it difficult to label certain conditions as being "optimal" for plant growth. For example, even "optimal" radiation, water availability, and temperatures can lead to declines in growth -e.g. due to high covariance with herbivore or fungal abundance. 242-243: I'm not sure I agree with this statement -Given, as you say, that one of the defining aspects of a community is that species can interact, it seems important that they should be studied at scales within which interactions are possible. E.g. if a study fails to find significant evidence for species interactions at a 50x50 km2 scale, that hardly means that species interactions are irrelevant to community structure -it just means that if there are significant effects, they occur at scales that are too small to be captured within the grain used by the study.
Just as a simple example: Both Typha and Arrhenatherum can easily exist in the same 50x50km2 grid cell, but they will almost certainly never interact at local scales, simply because they cannot grow under the same conditions. In other words, co-occurrence at one scale cannot necessarily be taken as evidence of co-occurrence at smaller scales. 257-258: This seems to be the first section where you suggest that the correspondence between height and competitive ability that you assume may not hold -But, you don't discuss how breaking this assumption might alter your results. At the very least, I would suggest including a somewhat longer justification of why you think that your results demonstrate that height does indeed universally correspond with competitive hierarchy, and discuss what your results would have looked like had this assumption not been met. 274-276: I'm not totally sure that this is correct -e.g. the Tilman results that you cite generally suggest the existence of some kind of limiting similarity in competitive abilities, which would lead to disaggregation of traits.

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Author's Response to Decision Letter for (RSOS-201361.R0)
See Appendix A.

Recommendation?
Major revision is needed (please make suggestions in comments)

Comments to the Author(s)
The authors present a model of competitive dominance that predicts some interesting macroecological patterns, which are then tested against empirical data. The model is elegant in its simplicity and quite compelling. In essence the authors assume vegetation height to be the key indicator of competitive strength and show that, at macro scales, this is related to light and evapotranspiration and find that plant height clustering is most evident in mid-latitude ecoregions, where they assume conditions for growth (reflected in actual evapotranspiration rates and gross primary productivities) are optimal. In effect they build a simple model and show that the pattern predicted by the model is the same as that observed. This is potentially really neat, but I don't think this is really the same as truly validating the model -it just so happens that the patterns are broadly similar, which could be coincidental, or could be that the model is good. The pattern could be explained by other things: e.g. abiotic rather than biotic controls or cause rather than effect . The authors assume mean annual evapotranspiration is a reliable measure of environmental constraints on plant growth. However, while partially related to leaf temperature (and hence net radiation and climate), evapotranspiration is strongly controlled by stomatal conductance (and hence photosynthetic rates) and foliage density (and hence canopy height). It could instead be argued that evapotranspiration rates are predictable from vegetation growth rather than the other way around.
Beyond that it is quite hard to get a sense of this paper. This is partly as it is really hard to follow as most of theoretical grounding presented in another paper, the methods themselves are not detailed enough and don't list all of the datasets used, and the results are a confusing blend of theory, method and actual results. Other potential limitations are that (i) vegetation height is assumed the key (only) indicator of competitive strength, when quite clearly this may not be the case and (ii) it is not clear whether the latitudinal patterns of potential light and water availability presented in Fig 1 come from. Is this PAR or some other measure of light availability, and is it constrained to seasons of plant growth (potentially revealing much higher light levels in the Arctic owing to 24 daylight)?
Most of the above could be handled with a convincing rebuttal, some more nuanced presentation of concepts and with a significant restructuring of the manuscript. I'd suggest restructuring the middle bit as follows: (1) outline the theory, (2) detail patterns predicted by the theory, (3) list the data obtained to test the theory (including all the environmental data) and (4) present the results (i.e. extent to which data support theory).
(2) and (3) could potentially swap order, but really needs to know about the theory before finding out about the data.
In summary, this could be quite a neat paper, but it could also be quite flawed, and I would really need to see a more sensibly structured manuscript before fully passing judgement.

Decision letter (RSOS-201361.R1)
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Reviewer comments to Author: Reviewer: 2 Comments to the Author(s) The authors present a model of competitive dominance that predicts some interesting macroecological patterns, which are then tested against empirical data. The model is elegant in its simplicity and quite compelling. In essence the authors assume vegetation height to be the key indicator of competitive strength and show that, at macro scales, this is related to light and evapotranspiration and find that plant height clustering is most evident in mid-latitude ecoregions, where they assume conditions for growth (reflected in actual evapotranspiration rates and gross primary productivities) are optimal. In effect they build a simple model and show that the pattern predicted by the model is the same as that observed. This is potentially really neat, but I don't think this is really the same as truly validating the model -it just so happens that the patterns are broadly similar, which could be coincidental, or could be that the model is good. The pattern could be explained by other things: e.g. abiotic rather than biotic controls or cause rather than effect . The authors assume mean annual evapotranspiration is a reliable measure of environmental constraints on plant growth. However, while partially related to leaf temperature (and hence net radiation and climate), evapotranspiration is strongly controlled by stomatal conductance (and hence photosynthetic rates) and foliage density (and hence canopy height). It could instead be argued that evapotranspiration rates are predictable from vegetation growth rather than the other way around.
Beyond that it is quite hard to get a sense of this paper. This is partly as it is really hard to follow as most of theoretical grounding presented in another paper, the methods themselves are not detailed enough and don't list all of the datasets used, and the results are a confusing blend of theory, method and actual results. Other potential limitations are that (i) vegetation height is assumed the key (only) indicator of competitive strength, when quite clearly this may not be the case and (ii) it is not clear whether the latitudinal patterns of potential light and water availability presented in Fig 1 come from. Is this PAR or some other measure of light availability, and is it constrained to seasons of plant growth (potentially revealing much higher light levels in the Arctic owing to 24 daylight)?
Most of the above could be handled with a convincing rebuttal, some more nuanced presentation of concepts and with a significant restructuring of the manuscript. I'd suggest restructuring the middle bit as follows: (1) outline the theory, (2) detail patterns predicted by the theory, (3) list the data obtained to test the theory (including all the environmental data) and (4) present the results (i.e. extent to which data support theory). (2) and (3) could potentially swap order, but really needs to know about the theory before finding out about the data.
In summary, this could be quite a neat paper, but it could also be quite flawed, and I would really need to see a more sensibly structured manuscript before fully passing judgement.

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Decision letter (RSOS-201361.R2)
We hope you are keeping well at this difficult and unusual time. We continue to value your support of the journal in these challenging circumstances. If Royal Society Open Science can assist you at all, please don't hesitate to let us know at the email address below.

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36
Plant height is a fundamental trait that reflects the ability of the individual to optimize its own growth within its 37 local biotic environment and regional physical constraints (see Falster & Westoby (2003), Holmgren et al. (1997) 38 and references therein). How plant height adapts to these opposing constraints has been studied in trees (King, 39 1990, Law et al., 1997, Midgley, 2003 and herbaceous plants (Givnish, 1995(Givnish, , 1982. Here we analyzed presence- . By assuming that competition between hetero-specifics is driven by signed 46 height differences, we found a significant positive correlation between the degree of clustering and actual evapo-47 transpiration rates. Across Europe, actual evapotranspiration is lower at more southern latitudes (due to reduced 48 precipitation levels) as well as at more northern latitudes (due to colder temperatures and low levels of sunlight).

49
Herbaceous plant height clustering is significant only over a latitudinal band where environmental constraints to 50 plant growth are weaker, which suggests that the signature of competitive dominance can only be detected in the 51 assemblage patterns of mid-latitude ecoregions.

53
In order to make to make this contribution self-contained, we first provide a summary of the main predictions 54 derived by our suite of models. Recent theoretical approaches have focused on predicting analytically the ex-55 pected fraction of species that survive in competitive scenarios (Serván et al., 2018). A spatially-implicit model 56 of Lotka-Volerra type (Capitán et al., 2020) allowed us to predict on average how many species are expected to 57 survive as a function of mean competitive strengths. We observed that the fraction of extant species p c , which we 58 called "coexistence probability", decays with the average competitive strength ρ as a power law above a certain 59 threshold in competition, and curves for different pool sizes S can be collapsed into the same curve following the 60 mathematical dependence, which was observed numerically and justified analytically (see Capitán et al. (2020)). We showed that the exponent 62 γ is controlled by the immigration rate µ. This is the first prediction of the spatially implicit model.

63
In order to explore the significance of competitive dominance in empirical communities, we applied first ran-64 domization tests to model communities. In this way, we established a second prediction for this model. Null models 65 for community assembly (Chase et al., 2011, Gotelli et al., 2010, Webb et al., 2002   regime is characterized by a low non-dimensional immigration rate (λ = µ/(αK) much lower than 0) -here α 76 stands for the average species growth rate in isolation, and K is the carrying capacity of the environment.

77
The spatially-explicit model incorporates a trade-off between potential growth and alternative mechanisms 78 other than growth that allow shorter individuals to overcome being out-competed by taller plants (see Capitán 79 et al. (2020)). While the latter are better competitors for light, the former allocate more energy in allelopathic 80 compounds (Fig. 1). Height hierarchies alone, as assumed in our spatially-implicit model, lead to the selection of 81 taller plants in species assemblages. In the more realistic spatially-explicit model, species processes take place on 82 a lattice where locally taller plants grow faster than neighbors because they are less shaded, but in the presence of 83 heterospecific neighbors, they are also more prone to die. Computer simulations show that the balance of these two 84 mechanisms can end up selecting plant sizes characterized by an optimal potential height that can be either shifted a region may reveal more information about the underlying assembly processes than the co-occurrence of species 95 at any given location (Ricklefs, 2008). As species are aggregated over lattice cells of increasing size, clustering habitat type based on the WWF Biomes of the World classification (Olson et al., 2001), which defines different 104 ecoregions, i.e., geographically distinct assemblages of species subject to similar environmental conditions. We 105 consider each cell in an ecoregion to represent a species aggregation.

106
Each herbaceous species in an ecoregion was characterized by its maximum stem height H, an eco-morphological 107 trait that relates to several critical functional strategies among plants (Díaz et al., 2015). It represents an optimal 108 trade-off between the gains of accessing light (King, 1990, Law et al., 1997, water and nutrient transport from Mean height values were obtained from the LEDA database (Kleyer et al., 2008) for as many species as there 112 were available in the database. Missing values were taken from (Ordonez et al., 2010)

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For all the species reported in an ecoregion, we formed an empirical competition matrix with pairwise ρ ij signed  In an ecoregion with richness S, a number s k ≤ S of species will form a species assemblage at cell k. The 128 coexistence probability was calculated from data as the average fraction of species that survive per cell, with N C representing the number of cells in the ecoregion. This quantity, together with the distribution of trait 130 differences in cells, was used to compare model predictions with real data. both physical (Craine & Dybzinski, 2013, Falster & Westoby, 2003 and biotic (King, 1990, Law et al., 1997. To 137 explore these opposing constraints, we analyzed plant data in the light of the two community assembly models.

138
The first one is a spatially-implicit model of Lotka-Volterra type, and the second one is a straightforward spatially- Two predictions from the implicit model tested against data 142 The collapse of curves predicted by Eq. (1) helps eliminate the variability in S, so that empirical coexistence 143 probabilities, which arise from different ecoregion sizes, can be fitted together (Fig. 3). Confirming the first 144 prediction of the spatially-implicit model, we found a significant correlation between the probability of coexistence 145 and the scaled competitive overlap based on empirical data (Fig. 3), indicating that a model driven solely by 146 dominant competitive interactions reliably predicts the average richness of plant communities across ecoregions.

147
In addition, this theoretical prediction allowed an indirect estimation of the relative importanceρ of average inter-148 vs. intraspecific effects: the average ratio of inter-to intraspecific competition strength is about 5% (see Supporting

149
Information, section A for details on the estimation procedure).
where (ρ C ij ) is the submatrix of the ecoregion competition matrix restricted to the species present in the cell.

163
Compared to ecoregion samples, the lower (higher) the empirical community average ρ C is, the higher (lower) 164 is the degree of species clustering in the cell. For each cell we calculated the probability p = Pr( ρ Q ≤ ρ C ) 165 that the the competition average ρ Q randomly-sampled from the pool is smaller than the empirical average. At Testing the second prediction against empirical observations yields a mixed picture. We calculated p-values for 173 randomization tests applied to every cell in each ecoregion, which represent the empirical distribution of p-values 174 (Fig. 4). At the parameter values that make plant data consistent with the first prediction, the spatially-implicit 175 model predicts significant trait clustering. We observe that some ecoregions are consistent with this theoretical 176 expectation. However, other ecoregions clearly do not comply with this prediction. In addition, no ecoregion is 177 consistent with trait overdispersion (Fig. 4). Selecting species in randomization tests according to species dispersal 178 abilities portrays the same picture (results not shown).

179
Ecoregion clustering and actual evapotranspiration rates 180 In order to better quantify the propensity of an ecoregion to exhibit clustering in maximum stem height, we defined 181 a clustering index q for an ecoregion as the fraction of its cells that lie within the 5% range of significant clustering 182 (randomization tests yield p-values smaller than 0.05 for those cells). An ecoregion for which significant clustering 183 is found in most of its cells will tend to score high in the q index. We examined how the clustering index varied 184 across the continent in terms of the geographical location of ecoregion centroids as well as with actual evapotran-185 spiration (Fig. 5). Evapotranspiration maps were obtained from data estimated through remote sensing (Mu et al., .

187
Water availability acts as a factor limiting plant growth at geographical scales (Fig. 1a), and correlates with to be stronger at ecoregions less limited by environmental conditions. As environments become harsher and less 198 optimal for plant growth, these clustering patterns disappear. This is particularly true for the severe climatic con-199 ditions characteristic in the Mediterranean (with erratic rainfall, limited water availability and drought), as well as  (Fig. 6b).

210
Correlations are significant but, in some cases, very weak. These results are consistent with our interpretation in 211 terms of a signal of competitive dominance in mid-latitude ecoregions.

212
Our spatially-explicit model predicts the persistence of trait clustering as species are aggregated at larger spatial Information, section B : ). We conclude that clustering patterns at large scales is an emerging pattern that can be 222 interpreted as a signature of competitive dominance operating at much smaller spatial scales.

317
Further work is required to better relate the average ratio of inter-vs. intraspecific competition, which stabilizes 318 species co-existence, to plant traits, and analyze how this aggregated parameter changes at increasing spatial scales 319 and across taxa.

50
Light and water availability (Fig. 1) impose significant limitations on gross primary productivity which is 51 reflected in actual evapotranspiration rates (Garbulsky et al., 2010). These two resources vary at regional scales, 52 placing strong, sometimes opposing constraints on how tall a plant can growwithin the limits of structural stability.

89
::::::: Species :::::::::: clustering :::::: under ::::::::::: competitive ::::::::::: dominance 90 In order to explore the significance of competitive dominance in empirical communities, we applied first random-91 ization tests to model communities. In this way, we established a second prediction for this model. Null models for 92 community assembly (Chase et al., 2011, Gotelli et al., 2010, Webb et al., 2002 compare the properties of actual 93 communities against random samples of the same size extracted from a species pool (observed diversity at the 94 ecoregion level). This approach assumes that realized communities are built up through the independent arrival of 95 equivalent species from the pool , MacArthur & Wilson, 1967 ::::::::::::::::::::::::::::::::::::: (Alonso et al., 2015, MacArthur & Wilso 96 regardless of species preferences for particular environments or species interactions. Our randomization tests were 97 based on a single statistic, the competitive strength averaged over species present in realized model communities, 98 which were then compared to random samples of the same size drawn from the species pool. The null hypothesis 99 (i.e., empirical communities are built as random assemblages from the ecoregion) can be rejected in both sides of Mean height values were obtained from the LEDA database (Kleyer et al., 2008) for as many species as there 145 were available in the database. Missing values were taken from (Ordonez et al., 2010)

161
In an ecoregion with richness S, a number s k ≤ S of species will form a species assemblage at cell k. The 162 coexistence probability was calculated from data as the average fraction of species that survive per cell, with N C representing the number of cells in the ecoregion. This quantity, together with the distribution of trait 164 differences in cells, was used to compare model predictions with real data.

195
The collapse of curves predicted by Eq. (1) helps eliminate the variability in S, so that empirical coexistence 196 probabilities, which arise from different ecoregion sizes, can be fitted together (Fig. 3). Confirming the first 197 prediction of the spatially-implicit model, we found a significant correlation between the probability of coexistence 198 and the scaled competitive overlap based on empirical data (Fig. 3), indicating that a model driven solely by 199 dominant competitive interactions reliably predicts the average richness of plant communities across ecoregions.

200
In addition, this theoretical prediction allowed an indirect estimation of the relative importanceρ of average inter-201 vs. intraspecific effects: the average ratio of inter-to intraspecific competition strength is about 5% (see Supporting

202
Information, section A for details on the estimation procedure).

228
Testing the ::: this : second prediction against empirical observations yields a mixed picture. We calculated p-229 values for randomization tests applied to every cell in each ecoregion, which represent the empirical distribution 230 of p-values (Fig. 4). At the parameter values that make plant data consistent with the first prediction, the spatially-231 implicit model predicts significant trait clustering. We observe that some ecoregions are consistent with this 232 theoretical expectation. However, other ecoregions clearly do not comply with this prediction. In addition, no 233 ecoregion is consistent with trait overdispersion (Fig. 4). Selecting species in randomization tests according to 234 species dispersal abilities portrays the same picture (results not shown).

235
Ecoregion clustering and actual evapotranspiration rates

236
In order to better quantify :: We ::::::::: explored ::::::: whether ::::: there :: is :: a :::::::::: geographic :::::: signal ::: in the propensity of an ecoregion to 237 exhibit clustering in maximum stem height. ::::: For : a :::::: better ::::::::::::: quantification, we defined a clustering index q for an 238 ecoregion as the fraction of its cells that lie within the 5% range of significant clustering (randomization tests yield 239 p-values smaller than 0.05 for those cells). An ecoregion for which significant clustering is found in most of its 240 cells will tend to score high in the q index. We examined how the clustering index varied across the continent 241 in terms of the geographical location of ecoregion centroids as well as with actual evapotranspiration (Fig. 5).

242
Evapotranspiration maps were obtained from data estimated through remote sensing (Mu et al., 2011).

263
The spatially-explicit model allows for either the dominance of tall, mid-sized or short plants, as a consequence 264 of the trade-off between investment in either potential growth or alternative mechanisms other than growth (see  (Fig. 6b).

269
Correlations are significant but, in some cases, very weak. These results are consistent with our interpretation in 270 terms of a signal of competitive dominance in mid-latitude ecoregions.

272
Our spatially-explicit model predicts the persistence of trait clustering as species are aggregated at larger spatial 273 scales (much larger than the typical range of species interactions). This is important because real individual plants 274 interact at much lower spatial scales (1 to 1000ha) compared to the spatial resolution of our dataset (grid cell sizes 275 about 50 km). To assess the robustness of our results, we further investigated the effect of aggregation scales 276 on clustering patterns using plant data. In line with the spatially-implicit :::::::::::::: spatially-explicit : model, the analysis 277 of herbaceous plant communities from mid-latitude ecoregions reveals that our results are robust to both up-and 278 down-scaling community sizes (see Fig 6c). Height clustering remains significant in a range of aggregated scales, 279 and extrapolates to smaller areas (under a random placement hypothesis, communities of smaller sizes were built 280 by randomly selecting a number of species as predicted by the empirical species-area relation, see Supporting

281
Information, section B : ). We conclude that clustering patterns at large scales is an emerging pattern that can be 282 interpreted as a signature of competitive dominance operating at much smaller spatial scales.
in species composition and in environment, than the the ecoregion itself. Therefore, in principle, grid cells could 322 be regarded as communities in an operational and relative sense. In addition, we assumed that the European Flora 323 database represents species composition at a steady state, this is, we examined the stationary patterns resulting 324 from eco-evolutionary processes associated to long time scales. Although real individual plants interact at much 325 lower spatial scales, two species from the same ecoregion will eventually interact within a grid cell given enough 326 time. The larger the temporal scale, the larger is the area where two species will have a chance to interact through 327 generations and repeated dispersal events. The scale at which a set of local communities reveal information 328 about underlying assembly processes is very often the regional scale (Diniz-Filho et al., 2009, Olalla-Tárraga & 329 Rodríguez, 2007, Ricklefs, 2015, which has led to the " : "regional community concept" (Ricklefs, 2008(Ricklefs, , 2011. : " 330 :::::::::::::::::::: (Ricklefs, 2008(Ricklefs, , 2011. :

331
It is important to make a clear distinction between actual plant size and the species-level trait, "maximum stem ability (Gaudet & Keddy, 1988, Weiner, 1993, there has been considerably less attention paid to the evolutionary 336 establishment of functional trade-offs between different species-level traits (Adler et al., 2014, Stearns, 1989.

337
The common wisdom that competition favors taller plants may not always hold [for instance, in low-nutrient, 338 competition-intensive, undisturbed habitats, see Tilman & Wedin (1991)]. Our analysis shows that height cluster-339 ing :::: (and :::: not :::::: height ::: per :: se : ) : at middle-range latitudes is a fingerprint of a balance between energy invested in either 340 potential growth or other mechanisms that may help plants overcome competitors. For instance, when competitors 341 are close relatives in dense herbaceous communities, selection may favor the evolution of a low leaf height. In 342 these situations, "for short conspecific herbs to exclude competitors from a highly productive site, they must pos-343 sess alternative mechanisms to overcome competition, such as root competition or allelochemics" (Givnish, 1982).

344
More generally, we :::::: would argue that functional trade-offs tend to evolve in regions of higher primary productivity, 345 where the relative role of biological interactions (competition, parasitism, herbivory) is expected to be higher.