Review of RSPB-2022-1428 “Functional traits trade-offs define plant population stability worldwide” by Conti et al.

The paper presents an analysis of the potential effect of the intraspecific variability in multiple traits on population stability using the TRY and LOTVS datasets. The main conclusions are that the variation in several traits seem to present significant associations with species persistence in communities, most notably leaf dry matter content (LDMC), seed mass and specific leaf area (SLA). Overall, the study appears as methodologically sound and its main findings are intriguing. However, analyses fail to account for the potential effects of co-ancestry and obviate important factors of plant population dynamics such as life history strategies. Therefore, the reader comes away wondering to what extent the results are robust and to what extent they are the manifestation of the many important, unaccounted variables.
For instance, by failing to factor in evolutionary similarity, the authors might be omitting some crucial, hidden element. Maybe taxa with similarly high LDMC or seed mass tend to be evolutionarily similar (e.g., they belong in the same order or family). Plants from this hypothetical group could share other important traits that are ultimately the ones responsible (at least in part) for the population stability of the corresponding species. The effects of co-ancestry are multi-dimensional and might affect traits that are latent in the present models and that have to be accounted for somehow.
Notwithstanding the potentially confounding effects of shared evolutionary history, there are some traits that are not considered which would appear as rather meaningful, such as plant size or life history. For instance, perennials are expected to be less sensitive to population fluctuations in the short term (as the authors explain for the case of trees). Why is this not incorporated in the models? It is easy to hypothesise some of the effects this might have. For instance, annuals are more likely to rely on small, dormant seeds to ensure population stability by seed-banking. Consequently, the effects attributed to seed size (or other specific traits) might be the manifestation of different life-history strategies, which need to be explicitly considered.
The omission of woody taxa (by the by, why omit trees but not shrubs?) albeit maybe justified, might have created some bias in the results that needs to be addressed. The dataset is limited to either understory vegetation (which has its own peculiar ecology) or grasslands (or are shrublands considered) which again, have some particularities. How is this expected to influence results? Are any of the traits particularly linked to any of these two (or any other) biome/vegetation type? Moreover, there is (almost) not data from tropical vegetation. How is this expected to affect the findings? Cold the described patterns be only relevant for temperate environments?
In summary, this is a potentially interesting work, but the analyses need to be revised using more detailed models and the writing needs to be enriched both conceptually and factually.

Minor comments
Title
- The dataset is not strictly global. Big swaths of the globe are omitted. Please change the title to reflect this fact.
Introduction
- The Introduction does not cover recent literature well enough. From the more theoretical, conceptual point of view, there is a fair amount of papers that have used eco-evolutionary dynamics to investigate the role of functional traits in community assembly and maintenance. The predictions and and ideas of some of these works could likely enrich the present manuscript. A couple that the authors might find relevant are:
-Villa-Martín et al. (2016) Eco-evolutionary Model of Rapid Phenotypic Diversification in Species-Rich Communities. PLOS Computational Biology 12 (10): e1005139.
-Faster et al. (2016) Multitrait successional forest dynamics enable diverse competitive coexistence. PNAS 114 (13) E2719-E2728.
Maybe because of this limited coverage of the theoretical literature, the claims that results confirm theoretical predictions are somewhat unconvincing. The authors need to provide a more exhaustive canvassing of evolutionary models and present the ones they see as most appropriate in a more detailed and systematic fashion.
Some empirical works that should at least be kept in consideration have also been omitted. One that seems rather relevant is:
Mayfield, M. M. et al. (2010) What does species richness tell us about functional trait diversity? Predictions and evidence for responses of species and functional trait diversity to land-use change. Glob. Ecol. Biogeogr. 19, 423–431.

Materials & Methods
- A description for the characteristics of the LOTVS dataset needs to be provided. Distribution of the plots, ecological and vegetation characteristics, etc.
- Some cursory explanation for the rationale behind trait selection would be useful
- It is unclear what the authors mean by a “skewed distribution” of data. Non-normal? Not satisfying the criteria of parametric models? Please clarify.
- The authors should at least provide a brief explanation of why they chose not to use a meta-analytical approach. It seems that it could have been a useful framework to find the size of the effect of each trait on population stability through time.

Second review of RSPB-2023-0344 “Functional traits trade-offs define plant population stability across different biomes” by Conti et al.
The authors have made a clear effort to incorporate reviewers’ comments. However, several shortcomings, some of them raised previously, remain.
The first one, already pointed out, is that the explanatory power of the models is very low. This is a central result that needs to be put forward very explicitly and mentioned in the Abstract. Otherwise, readers might be misguided about the actual amount of variation that the models described here represent.
This lack of explanatory power could be related to the traits that are not accounted for. Even if the phylogenetic correction might control for some of those, others might not have a strong phylogenetic signal and therefore they need to be considered independently of the phylogeny, at least conceptually. For instance, frameworks such as r/K or Grime’s C-S-R rely heavily on the idea of dispersal to explain the differences between strategies (i.e., r-strategists or ruderals produce a large amount of easily dispersed progeny that can colonize new patches). In the case of plants, dispersal has an additional temporal dimension mediated by seed dormancy. However, the authors do not seem to have considered the effect that either of these processes (seed dispersal and dormancy) might have on population stability. This omission needs to be addressed.
Another major limitation of the manuscript is its handling of what the authors have called “categorical traits”, some of which merit more careful analysis. For instance, looking at Fig. S1 and Fig. S5, one cannot but wonder about the explanatory power of life-history alone. The difference between annuals and non-annuals is clearly major. This needs to be clearly addressed. The authors need to present the models for this and other "categorical" traits in a manner analogous Table 1, so the reader can judge fit across models.
In summary, although he paper is still a remarkable effort, the results are unconvincing.
Minor comments
Abstract
-The authors need to reflect the low explanatory power of their models explicitly so as to not misrepresent their findings.
-L. 171: Why use the mean CV and not the median?
-L. 192-198: This explanation of the statistical analyses and phylogenetic correction is very deficient. It would be impossible to reproduce any of the analyses with the information provided.
-L. 240: What do the authors mean by a “dramatic” change in statistical results?
-L. 347-348: “This is an indication…” This passage is probably wrong. Including more (or other) variables will increase the explanatory power of the models. The researcher only needs to identify the relevant ones…
-Table 1 and figure 1 seem to be quite redundant. Maybe the relevant information of Fig. 1 could be incorporated into the table? Alternatively, maybe use the figure as a more detailed representation of the data, in the vein of Fig. s1.
Fig. S1: Please provide the explanatory power of these models.

The authors have addressed all the concerns raised previously.
However, they insist in that the explanatory power of their models is "relatively" small. Please avoid the adverb: any model that explains less that 10% of the variation in the response variable has very poor explanatory power.
Also, they should revise the text and eliminate all qualifications not supported by the quantitative results (e.g., what do they mean by "tremendous" in line 363?).