No pervasive relationship between species size and local abundance trends

Although there is some evidence that larger species could be more prone to population declines, the potential role of size traits in determining changes in community composition has been underexplored in global-scale analyses. Here, we combine a large cross-taxon assemblage time series database (BioTIME) with multiple trait databases to show that there is no clear correlation within communities between size traits and changes in abundance over time, suggesting that there is no consistent tendency for larger species to be doing proportionally better or worse than smaller species at local scales.

Dear Dr Terry, Your Brief Communication, "No pervasive size trend in global community dynamics" has now been seen by three reviewers. You will see from their comments copied below that while they find your work of potential interest, they have raised quite serious concerns that must be addressed.
In particular, Reviewers 1 and 3 highlight substantial issues with the rank-based analytical approach. We feel that the conclusions are not strong enough at this stage to warrant publication in Nature Ecology & Evolution, and it appears that an overhaul of the analyses would be necessary to make the results more robust. Although we will consider a revised manuscript, please know we are unlikely to send it back to the reviewers unless all of their concerns are thoroughly addressed.
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Reviewer expertise: I wonder if one might target assemblages where absolute changes are actually occurring (other ones might add noise). The question could be respecified as "are changes in assemblages due to a disproportionate decline of large bodied species"? Was there a relation with magnitude of turnover?
Do you predict larger bodied species to have more positive or negative relations (I thought negative, right? larger bodies, greater decline in rank). I ask because Fig 1(iv) shows a positive relation. I also notice that most of the mean tau values were positive (albeit most non-significant). Is this expected? the authors state that they generated 100 randomized tau values for each assemblage (although in Fig 2, they indicate they used 50 randomizations), and then performed two-sample t-tests to see whether the real mean differed from the null. It is not clear how this was done -was a t-test conducted for each of the 100 sets of randomizations? Which t-test was used in this case? or was the mean t-value used? Regardless, applying two sample t-tests to simulated (randomized) sets, treating them as if they were real data, probably isn't the best approach, given the arbitrary nature of how many simulated sets one generates. Instead, why not run 1000 or 10000 randomized sets, calculate tau and just see whether the empirical tau is greater or less than 95% of the sets? I think it is more powerful. I also wonder if power is lost, treating each assemblage as a single data point, and whether formal meta-analytic procedures might be possible. Finally, why are 2-tailed tests used? You have a clear expectation of larger body sizes declining more.

Minor points:
The authors binned widespread species into 10km grid cells. I wonder if this causes issues of nonindependence.
The authors attribute the positive relation for amniote studies to anthropogenic dispersal limitations (affects smaller bodies animals more). Could the authors explain this more? Is anthropogenic dispersal limitations increasing during the time periods of the studies?
Reviewer #2 (Remarks to the Author): The manuscript: "No pervasive size trend in global community dynamics" investigates whether there is a global trend of decline in species body size. For that, the relationship between size traits and changes in abundance rank over time is analysed for several assemblages worldwide.
The study is well designed and make use of the BioTime database and several trait databases. The text is concise and well written and the figures and supporting materials are informative. The authors did a good job discussing the caveats of using such databases and performing such large-scale analyses. The conclusions are supported by the results and, in my opinion, the manuscript is of potential interest to the readers of this journal.
I appreciate that the authors explicitly mention that insects are not included in the analysis. I recommend to also discuss bias in the distribution of data across realms: are freshwater assemblages included in the study? This is relevant to the scope of the manuscript, as freshwater megafauna is reported as declining globally, see e.g. He, F., Zarfl, C., Bremerich, V., David, J. N., Hogan, Z., Kalinkat, G., ... & Jähnig, S. C. (2019). The global decline of freshwater megafauna. Global change biology, 25(11), 3883-3892.
From Extended Data Figure 1, it seems that the majority of time series are less than 20-years long. It could be that the decline or extinction of large-bodied species happened before the beginning of the time series. In that case, the time series cannot track the changes in size:ranks relationships. I recommend to discuss this issue.
Here some additional comments: Line 16: delete "is". Line 119: The caption of figure 2 says that "Blue density plots show the distribution of 50 randomisations". I wonder why 50 randomizations and not 100, as 100 were used to create the null distribution according to lines 47 and 185.
Line 177, "very small β values": Can you please define what "very small" means?
Lines 189-194: From Extended Data Figure 1, it seems that there are a few outliers in the raw data and skewed distributions. Were the explanatory variables transformed?
Reviewer #3 (Remarks to the Author): This study assesses whether temporal species turnover in community time series results in functional changes related to species size. This is an interesting and relevant question because numerous studies have pointed out size-related vulnerability to anthropogenic threats, and other have concluded that communities will be increasingly dominated by small species. I think this can be an important contribution with potentially interesting results. However, overall I felt a bit dissatisfied with the study. My main concerns relate to the analyses and hypotheses. 1) I don't think using ranks is a good idea. Using ranks makes the analysis quite insensitive to changes, and does not focus on changes per se but rather to reversals in species relative abundances. A species can remain stable and another may be declining, but in a matter of 15 years or so the rank will likely remain stable. Take a simplistic example of a community with two species, a mouse and a tiger. If the tiger decreases or increases while the mouse remain stable you won't see any change in the ranks, as the tiger will always be rarer than the mouse. Similarly, if the mouse decreases and the tiger increases, the rank will also remain invariant as these two species differ by orders of magnitude in their population density. So at present, I'm not convinced by the conclusions made by the authors. I see two possible options. One would consist in a linear model with abundance as dependent variable and body mass and time as predictors. The interaction between the two should inform on size-related changes. In such a model you could also include a number of potentially confounding variables (e.g. those assessed in Fig. 1 in extended data), which would make results more robust to these factors than a simple visual inspection. Obviously this requires some thinking about random intercepts/slopes etc.. A second option I can think of, is focusing on some community weighted average of body size and how this changes over time. You can still analyse this using a linear model.
2) The authors start by explaining that studies focusing on time-series have observed species turnover, and others have claimed different trends for species with different sizes. This is true, however, most of the literature on this (at least the one I know) relates to endothermic vertebrates, and here the authors analyse several different taxa including plants. I'd like to see more space dedicated to what is known or not known, how this knowledge is taxonomically biased, and so what can we expect from these results. Also note that even within taxa, authors have pointed out different size-trends (e.g. Ripple et al. 2017PNAS, or Santini et al. 2021 Ecol Lett cited in the text). Currently the paper jumps into the methods and results too soon, I think the authors need to dig deeper in the literature and provide an overview of what is known and could be expected. 11-12: This comes a bit out of the blue in the abstract, both because specifically focused on body size (but it starts refering to traits in general), and because of the expectation small and large may do better/worse. Perhaps an introductory sentence on common perception/previous studies is worth adding on this L. 19-20: See also González-Suárez, M., Gómez, A., & Revilla, E. (2013). Which intrinsic traits predict vulnerability to extinction depends on the actual threatening processes. Ecosphere, 4(6), 1-16. For how vertebrates body mass relates to extinction risk (note that here they conclude both small and large are at higher risk for different reasons).
Here the authors projected community changes into the future for birds and mammals In general, you here are assessing entire communities, but as far as I know the literature on body-size related trends is mostly on mammals, and secondarily on vertebrates. The expectation for entire communities or different taxa needs to be better grounded in the literature Line 50: positive relationship between body mass and "positive/negative"(?) trends? Line 53: "predict" is a big word. I can imagine they do not predict them, but did they influence them? Did you find any relationship even if weak? It would really help to add a loess fit on top of the scatterplots for better interpretation (but see my comment above on the need of a more robust way to account for these factors on the results). Also, it seems to me that some variables may benefit from transformation, e.g. species richness Line 62-63: Is the direction of these changes consistent? Or no consistent pattern is observed? 65-67: Density is strongly negatively related to body mass, so habitat area is a bigger issue for large than small species Line 70-71: Sometime the description/interpretation of the results is hard to follow, here and elsewhere I suggest explaining the pattern in words rather than referring to t and its statistical distribution.
90: This should be "meta-analyses", not "metanalyses" . Note, however, that most of these analyses are not proper meta-analyses in sensu strictu, just statistical analyses Fig. 1 What are the coloured lines in b? It is a bit confusing, I'd only show the points. Also, include symbol legend in the figure for simplicity 139: Honestly, I would not trust the GBIF backbone taxonomy, gbif is full of misspelled names, synonyms, subspecies treated or not treated as species, etc. Why not using catalogue of life in taxize? Fig. 2 It may help to add % >0 for better interpretation Line 218: I miss a rationale for it. Why do we need a null model? Why should we expect null model to deviate from no change?
One final point to take in consideration. The time series are, in most cases, quite short to detect such a trend. We may be able to detect changes in species with rapid life histories, but are we capable of detecting changes in species with slow life histories (the large ones)? This is something that is worth discussing and perhaps take into account in the analysis if possible Author Rebuttal to Initial comments Decision Letter, first revision: 24th September 2021 *Please ensure you delete the link to your author homepage in this e-mail if you wish to forward it to your co-authors.
Dear Dr Terry, Your manuscript entitled "No pervasive size trend in global community dynamics." has now been seen again by the three reviewers, whose comments are attached. You will see that while Reviewers 1 and 2 now endorse publication, Reviewer 3 continues to raise some concerns about the analyses. We would like to see this comment addressed before we can reach a final decision regarding publication. Although the reviewer does not mention this, we wondered if analyses of simulated data could be used to explore the contingency of the results on the range of body sizes in the data.
We therefore invite you to revise your manuscript taking into account all reviewer and editor comments. Please highlight all changes in the manuscript text file.
We are committed to providing a fair and constructive peer-review process. Do not hesitate to contact us if there are specific requests from the reviewers that you believe are technically impossible or unlikely to yield a meaningful outcome.
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We hope to receive your revised manuscript within four to eight weeks. If you cannot send it within this time, please let us know. We will be happy to consider your revision so long as nothing similar has been accepted for publication at Nature Ecology & Evolution or published elsewhere. Nature Ecology & Evolution is committed to improving transparency in authorship. As part of our efforts in this direction, we are now requesting that all authors identified as 'corresponding author' on published papers create and link their Open Researcher and Contributor Identifier (ORCID) with their account on the Manuscript Tracking System (MTS), prior to acceptance. ORCID helps the scientific community achieve unambiguous attribution of all scholarly contributions. You can create and link your ORCID from the home page of the MTS by clicking on 'Modify my Springer Nature account'. For more information please visit please visit <a href="http://www.springernature.com/orcid">www.springernature.com/orcid</a>. Please do not hesitate to contact me if you have any questions or would like to discuss these revisions further.
We look forward to seeing the revised manuscript and thank you for the opportunity to review your work.

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Reviewers' comments: Reviewer #1 (Remarks to the Author): The authors have adequately addressed my concerns, and I believe that the interpretation of the results is sound (and is interesting). I agree with their presentation of multiple metrics of change (including keeping the ranked version in the extended material), and that the results are robust to these choices. I also agree with the secondary, species-based analysis. Finally, although this was not addressing one of my explicit comments, I liked that they kept their interpretation of significance of the amniotes more cautious and did not over interpret it. Overall, I think the authors have done a good job.
Reviewer #2 (Remarks to the Author): The authors did a good job in reviewing the manuscript. The new analytical approaches make the manuscript stronger. I have only a few minor comments. The reference to Figure  In the first revision, me, and the other two referees had similar concerns on the sensitivity of the rank analysis to changes. The authors have argued that even if this is true in principle, this is unlikely in practice and that the conclusions do not change when using different approaches. That other approaches lead to similar results is re-assuring, but in a way it is potentially concerning. I made a simplistic and extreme example in my previous comment (tigers and mice), and authors argued that that was indeed extreme and there's no similar case in their dataset, as most time series focus on particular guilds such as lizards or song birds. I find this very concerning, as the results are likely heavily dependent on the variability of taxa included in each time series. I expect that sizerelated trends are only visible if the community data includes very large and very small species, but not if the data only include similar-sized species. Is there any relationship between size-trait range (or better, 95% of the distribution) with the trend observed?
Please note that I revised the pdf with track-changes, so the line numbers below correspond to that pdf document.
One general comment: The author often refer to "traits" in general, e.g. "relative trait rank within an assemblage". However, as all traits are size traits, I suggest repeating "size traits" all the times to avoid confusion.
Also, the authors indeed argued that their methodological options are limited due to gaps in the data, however I am still confused on how authors dealt with incomplete data, and would like to see this better explained in the text. L. 68-69: The authors should also discuss how representative the biotime is taxonomically. Most of the time series do not include large vertebrate species, which are those on which much of this sizedependent threat literature has been developed l. 96 I think "spatial, temporal and TAXONOMIC BIAS" would be more appropriate than "limitations" L 110: I think this is the first time you mention 3 approaches. Above you only say you repeat the analysis using different transformations and cite the SI.
L. 248: I am not sure I understand this. At least 5 times the species occur in the time series? i.e. observed at 5 time steps? Please clarify. Also, as this is based on a continuous value, why not using that value directly instead of binarizing into winner and looser which degrades the information into a threshold-dependent binary outcome?
Extended Data Table 1: Revise sentence "There was no consistent drivers.." I am not sure how to interpret the table. What I find confusing is the response variable. From the text (l. 62) is seems like you use the correlation coefficient, but here it seems you use a trait variable? Please clarify.
Extended data Table 4: I find hard to understand this: "relationship between the relative trait rank within an assemblage and the assignment to either 'winner' or 'loser' categories". Please clarify. In general, I think it would be really useful if you could elaborate more on some part of the methods in a dedicated section of the SI, especially the different approaches to assess trends. I would only provide Extended Data Table 6 as a csv table, not also in the pdf ********************END******************** Author Rebuttal, first revision: Reviewer #1 (Remarks to the Author): The authors have adequately addressed my concerns, and I believe that the interpretation of the results is sound (and is interesting). I agree with their presentation of multiple metrics of change (including keeping the ranked version in the extended material), and that the results are robust to these choices. I also agree with the secondary, species-based analysis. Finally, although this was not addressing one of my explicit comments, I liked that they kept their interpretation of significance of the amniotes more cautious and did not over interpret it. Overall, I think the authors have done a good job.
Our thanks to the reviewer for the supportive comments. We very much agree that a cautious interpretation of the results is essential.

Reviewer #2 (Remarks to the Author):
The authors did a good job in reviewing the manuscript. The new analytical approaches make the manuscript stronger. I have only a few minor comments.
Our thanks to the reviewer for the positive and constructive comments. Thank you for the spot. We think it is makes marginally more sense for the maps to come before the main results plot (although both are to some extent 'results'). We have introduced an earlier reference to figure 1 to keep the ordering sensible. Indeed -we have adjusted. This was a relic of our previous draft.
Line 173, "Data not from adults was discarded": this is stated also at line 170. This is true; however, the first reference refers to quantitative body size measurements, while the second refers to the qualitative traits. While we could probably find a way to phrase it once to cover both categories, it would likely be longer and more convoluted than our current formulation

Reviewer #3 (Remarks to the Author):
In the first revision, me, and the other two referees had similar concerns on the sensitivity of the rank analysis to changes. The authors have argued that even if this is true in principle, this is unlikely in practice and that the conclusions do not change when using different approaches. This is an interesting point, distinct to the points discussed around the previous version of the manuscript. Like all cross-study comparative analyses, there is a balance to be struck between comparing like-with-like and also having a sufficient range to detect signals through noise. To continue the analogy further, a comparison of a restricted set of mice might span a very small size range that would be hard to relate to trends. On the flip-side, comparing tigers with mice is also likely to be heavily influenced by other drivers. Most ideally for the questions we want to address, a scale roughly of 'rodents' would probably hit the sweet spot. To some extent we do have to trust that the original compilers of the data contained in BioTIME made reasonable choices of the scale of data, that they do indeed represent meaningful communities. The BioTIME dataset is specifically curated for the analysis of communities, and has been subject to much discussion and analysis, so we believe this is a reasonable assumption.
To address the possibility that trait-ranges have a driving influence on our results, we have looked into the data and do not find any particular cause for concern and have incorporated the results into the manuscript.
For this analysis, for each assemblage we took the difference between the log10(minimum) and log10(maximum) values of traits for the species that were actually used in the analyses (i.e. excluding very transient species that were filtered out as described in the main text). Clearly there is a very large number of ways to describe the spread of traits in each community, but this seemed the most direct. We looked at how this relates to our tau metric (for multi-site studies we took an average trait range, so each dot represents a single study-trait combination).
Contrary to the reviewer's expectation, there is no obvious problematic trend in the divergences from zero and the trait range. Most assemblages showed ranges of about 1-2, (i.e. a 10-fold to 100-fold size range) Note that some traits are lengths and some are masses -lengths showed a smaller range (as would be expected based on the number of dimensions involved).
We repeated the analysis excluding the 5% largest and 5% smallest species, and the results were very similar: To address this in the manuscript, we have added this metric of 'trait range' as an additional predictor into SI Fig2, alongside the other potential factors such as time-series length and number of species (L61, L221). We have split the figure into two parts because the sub-facets were getting too small. Because the results were so similar, we only included the 'untrimmed' trait range.
We have added a sentence to the main text making our assumptions on this explicit (L95-96). Additionally, we have added some extra explanation about what a BioTIME 'study' constitutes (L28), and added summary statistics of the trait range to the main text (L42-43).
Please note that I revised the pdf with track-changes, so the line numbers below correspond to that pdf document.
One general comment: The author often refer to "traits" in general, e.g. "relative trait rank within an assemblage". However, as all traits are size traits, I suggest repeating "size traits" all the times to avoid confusion. This is a good idea -we have gone through the manuscript and clarified this in a number of places where we present our methods and results.
Also, the authors indeed argued that their methodological options are limited due to gaps in the data, however I am still confused on how authors dealt with incomplete data, and would like to see this better explained in the text.
We assume here that the reviewer is referring to incomplete trait data here, based on their reference to the methodological constraints. Trait data could be missing in a number of different ways, but the main issues were the cases where the species naming within BioTIME may not be relatable to trait data bases, or that the species did not have trait data listed.
Our approach to incomplete alignment between the trait data and the population data was quite straightforward -we did not attempt to infer or impute any missing data and focussed on the correlation between the trait values and the population responses ( ) across the species that we had data for. A possible source of confusion here is that we linked the trait data before doing the final rounds of filtering described in the methods (L186-191), so that our dataset would of the maximum use to other future users.
Where we do not have trait data, it is excluded from the calculation of the Kendall rank correlation coefficient between the trait in question and . In the method for calculating that we include in the main text, each species is looked at in isolation, so the analysis proceeds as if those species were removed.
In the case of the population rank-change approach to calculating , the counts of species that do not have trait data are included in the calculation of . We considered this one of the advantages of the rank-abundance approach. However, the species without trait data cannot be considered in the trait-β correlation.
We have adjusted the main text (L47) and the methods section (L201) to make this more clear.

L 54: several?
We presume that the suggestion is to replace: 'Certain' individual studies showed significant relationships… . It wouldn't be a big change either way, but we don't consider the number sufficient to be labelled as 'several'.

Line 62: See my comment above on the potential influence of size range in the community values.
We have added trait range as an additional tested co-predictor at this location, as we discuss above.

L. 68-69: The authors should also discuss how representative the biotime is taxonomically. Most of the time series do not include large vertebrate species, which are those on which much of this size-dependent threat literature has been developed
We have added extra text highlighting the lack of large-vertebrate coverage in the BioTIME database [L68-69]. We agree it is important to make crystal clear that our manuscript is not focussed on the threats faced by large-vertebrate apex species. There are important distinctions between the conservation-orientated threat literature (which as the reviewer points out is primarily large and charismatic vertebrate focussed) and broader community ecology questions.
However, in terms of BioTIME's representiveness, large vertebrate species are a tiny fraction of global biodiversity (despite being a fraction with distinctive functional roles). Some would argue that BioTIME is biased towards vertebrates, not against them, although this is mostly towards small ones. l. 96 I think "spatial, temporal and TAXONOMIC BIAS" would be more appropriate than "limitations" We would agree that taxonomic biases within BioTIME are a significant issue, but the taxonomic biases could not be detected by the tests we refer to there. We discuss taxonomic unevenness and biases later in the paragraph. The difference is largely semantic, however at that point in the manuscript we discuss issues such as shortness of timeseries or the number of species which we feel are 'limitations' (due to the scale of data), rather than 'biases' (due to unbalanced sampling) in the data -although they might have the potential to cause biases in the results.

L 110: I think this is the first time you mention 3 approaches. Above you only say you repeat the analysis using different transformations and cite the SI.
Thank you for the spot. We have smoothed this out and added a pointer the results figure in SI. Yes -that is correct. We have clarified the text (L225). The key point is that we only tested those species that were observed at least 5 times -the total time series could be longer (e.g 8,4,2,0,3,0,1).

Also, as this is based on a continuous value, why not using that value directly instead of binarizing into winner and looser which degrades the information into a threshold-dependent binary outcome?
We are extracting a measure in the confidence in trends here, not simply the slope as such, in order to provide a complimentary analysis to the main results. While we could use the p-value as some kind of continuous response, this does not feel particularly natural and would introduce additional distracting considerations. Yes -the response variable is our 'τ'. We conduct separate analyses for each trait category. The table contains the model coefficient estimates for the effect of each possible driver on tau.
We have revised the table caption text to make this more clear: **Extended Data Table 1** Full statistical results from lLinear model analysis of putative study-level drivers predictors of size trait -population trend correlations ( ). We tested each Each trait separately, except (apart from 'Qualitative body size', for which there were too few studies for a meaningful test.) was tested independently and Nno corrections were made to the reported values for multiple comparisons. There were was no consistent drivers -while certain relationships between possible predictor variables were identified as significant at p<0.05 (highlighted in bold), these were not consistent across the set of traits and had low explanatory power (adjusted-2) in all cases except Fish (as discussed in the main text). Table 4: I find hard to understand this: "relationship between the relative trait rank within an assemblage and the assignment to either 'winner' or 'loser' categories". Please clarify. In general, I think it would be really useful if you could elaborate more on some part of the methods in a dedicated section of the SI, especially the different approaches to assess trends.

Extended data
We have re-written this caption (below) to simplify the sentence structure and split the table to make it even more clear that there are two separate sets of tests being conducted. There is not much more complicated here than a series of weighted logistic regressions, that are described in the main text methods. **Extended Data Table 4** Results from logistic regressions seeking to determine if Statistical results demonstrating the lack of a significant relationship between the relative trait rank within an assemblage and predicts the likelihood of an identifiable population level trend. Separate analyses were carried out for assignment to either 'winner' andor 'loser' categories. Each test was a logistic regression, weighted by the reciprocal of the number of cells within a study that include the species. Coefficient estimates are shown on the transformed scale. Separate models were fit for each trait and direction of trend, and no corrections were made for multiple comparisons. Table 6

as a csv table, not also in the pdf
We previously included the large table to fulfil the requirement to directly link back to the original data providers within BioTIME. However, we agree that it was very unwieldly. To improve matters, we have greatly reduced the number of columns in the SI table, and just point out the information available in the code supplement. This has also allowed us to include data citations in a better form, and is in better keeping with other papers in this journal that have used the BioTIME dataset.

Decision Letter, second revision:
18th October 2021 Dear Dr. Terry, Thank you for submitting your revised manuscript "No pervasive size trend in global community dynamics." (NATECOLEVOL-210513641B). It has now been seen again by Reviewer 3, whose are below. The reviewers find that the paper has improved in revision, and therefore we'll be happy in principle to publish it in Nature Ecology & Evolution, pending minor revisions to add further caveats in line with the reviewer's requests, and to comply with our editorial and formatting guidelines.
If the current version of your manuscript is in a PDF format, please email us a copy of the file in an editable format (Microsoft Word or LaTex)--we can not proceed with PDFs at this stage.
We are now performing detailed checks on your paper and will send you a checklist detailing our editorial and formatting requirements in about a week. Please do not upload the final materials and make any revisions until you receive this additional information from us.
Thank you again for your interest in Nature Ecology & Evolution. Please do not hesitate to contact me if you have any questions.

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Reviewer #3 (Remarks to the Author): I've now read the response of the authors and the revised paper. I still think the paper is a good scientific product, although I am still not enthusiastic about the overall conclusion and message. The bottomline of the authors is they trust "that the original compilers of BIOTIME made reasonable choices of the scale of data, that they do indeed represent meaningful communities". First, biologically speaking, those in BioTIME are not communities, but just assemblages of species that have been recorded. Second, the selection of species depends on the data used to estimate animal abundance. For example, in birds or fishes, the same sampling approach is OK to sample "most" species in an area, but this is not true for e.g. mammals, where depending on the group of species we use different techniques. This makes impossible to have e.g. time series of a mammal community. Also, for example, cetaceans are not sampled the same way fishes are sampled, so time series of fish species will unlikely include cetaceans, and yet biologically speaking cetaceans do belong to the same community and we may expect a shift due to anthropogenic effects. An honest discussion of what is a community according to BIOTIME database, and what does this imply for the conclusions, is still lacking from the text. It is great the authors tested the effect of body size range, but one can see most of the data span 2 orders of variation (with the exception of seed mass), while just to give some examples, fishes and mammals span >6 orders of variation in body mass, and birds >4. It is not only a matter of apex predators. Fishes are almost all carnivorous, and the largest mammals and birds are not carnivorous either. Everything in macroecology is scale-dependent, there are many factors that affect community trait shifts that act simultaneously, some are only evident over large value ranges. Provocatively, would we be able to detect the Bergmann's rule you mention within a single country? Probably not.
Overall, I remain to be convinced that traits in communities are overall shifting, or not shifting. Right now the paper sends a strong message that is appealing for big journals like Nat Ecol Evol, but may be detrimental for scientific research.
In conclusion, while the authors know acknowledge this limitation, I think this should be more apparent. Most of the conclusions are made at the beginning of the text, while this important limitation is only briefly mentioned at the end, so won't be noticed by many. My only final comment is to be really transparent on the boundaries within which your conclusions are valid, starting from the abstract or the first part of the paper.

Our ref: NATECOLEVOL-210513641B
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Please use the following link for uploading these materials: [REDACTED] If you have any further questions, please feel free to contact me.

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Reviewer #3: Remarks to the Author: I've now read the response of the authors and the revised paper. I still think the paper is a good scientific product, although I am still not enthusiastic about the overall conclusion and message. The bottomline of the authors is they trust "that the original compilers of BIOTIME made reasonable choices of the scale of data, that they do indeed represent meaningful communities". First, biologically speaking, those in BioTIME are not communities, but just assemblages of species that have been recorded. Second, the selection of species depends on the data used to estimate animal abundance. For example, in birds or fishes, the same sampling approach is OK to sample "most" species in an area, but this is not true for e.g. mammals, where depending on the group of species we use different techniques. This makes impossible to have e.g. time series of a mammal community. Also, for example, cetaceans are not sampled the same way fishes are sampled, so time series of fish species will unlikely include cetaceans, and yet biologically speaking cetaceans do belong to the same community and we may expect a shift due to anthropogenic effects. An honest discussion of what is a community according to BIOTIME database, and what does this imply for the conclusions, is still lacking from the text.
It is great the authors tested the effect of body size range, but one can see most of the data span 2 orders of variation (with the exception of seed mass), while just to give some examples, fishes and mammals span >6 orders of variation in body mass, and birds >4. It is not only a matter of apex predators. Fishes are almost all carnivorous, and the largest mammals and birds are not carnivorous either. Everything in macroecology is scale-dependent, there are many factors that affect community trait shifts that act simultaneously, some are only evident over large value ranges. Provocatively, would we be able to detect the Bergmann's rule you mention within a single country? Probably not.
Overall, I remain to be convinced that traits in communities are overall shifting, or not shifting. Right now the paper sends a strong message that is appealing for big journals like Nat Ecol Evol, but may be detrimental for scientific research.
In conclusion, while the authors know acknowledge this limitation, I think this should be more apparent. Most of the conclusions are made at the beginning of the text, while this important limitation is only briefly mentioned at the end, so won't be noticed by many. My only final comment is to be really transparent on the boundaries within which your conclusions are valid, starting from the abstract or the first part of the paper.
I've now read the response of the authors and the revised paper. I still think the paper is a good scientific product, although I am still not enthusiastic about the overall conclusion and message.
We believe the edits we have made can address the reviewer's concerns -indeed we completely agree on the importance of calibrating the strength of the conclusion appropriately. We note that our manuscript is much more circumspect and includes considerably more (both in absolute and proportional terms) discussion about the limitations for the BioTIME database than previous papers that The bottomline of the authors is they trust "that the original compilers of BIOTIME made reasonable choices of the scale of data, that they do indeed represent meaningful communities". First, biologically speaking, those in BioTIME are not communities, but just assemblages of species that have been recorded. Second, the selection of species depends on the data used to estimate animal abundance. For example, in birds or fishes, the same sampling approach is OK to sample "most" species in an area, but this is not true for e.g. mammals, where depending on the group of species we use different techniques. This makes impossible to have e.g. time series of a mammal community. Also, for example, cetaceans are not sampled the same way fishes are sampled, so time series of fish species will unlikely include cetaceans, and yet biologically speaking cetaceans do belong to the same community and we may expect a shift due to anthropogenic effects. An honest discussion of what is a community according to BIOTIME database, and what does this imply for the conclusions, is still lacking from the text.
These are issues that are fundamental to all ecological research -what is a community? Although we would reject the insinuation that have been dishonest in our presentation, we have been happy to add further clarification of what the studies in BioTIME represent. Distinctions between assemblages and communities are real, but the extent of data that the reviewer appears to be requesting here, fully complete communities, would lead to paralysis of progress in ecology. It would not be necessary to have sampled all species in a community to detect size-based determinants in performance, as long as the sampling was not strongly biased in some way.
We are speculating here, but we suspect some of these points are derived through the lens of the macro-ecological studies that attempt to link species traits to their overall global performance, in which circumstance it would be meaningful to attempt to include all mammals or birds. While related, this is a fundamentally different scale and approach to the localised community-level approach we take. Our edits to the abstract are intended to make this distinction more readily apparent.
It is great the authors tested the effect of body size range, but one can see most of the data span 2 orders of variation (with the exception of seed mass), while just to give some examples, fishes and mammals span >6 orders of variation in body mass, and birds >4. It is not only a matter of apex predators. Fishes are almost all carnivorous, and the largest mammals and birds are not carnivorous either.
While there is inevitably room for improvement of the data, we believe that the trait range is sufficient to make meaningful comparisons, and is also enough of a span for it to be reasonable to expect a differences. There is not good evidence of greater influence of traits in those studies that include a wider spread of traits, as we show in our SI. As we discussed in our previous response, it is not clear that it would necessarily be advantageous to have traits spanning 6 orders of magnitude within a single study. Comparing elephants with mice is unlikely to be particularly informative because the scales of their dynamics would be likely be poorly captured in a single study.
Everything in macroecology is scale-dependent, there are many factors that affect community trait shifts that act simultaneously, some are only evident over large value ranges. Provocatively, would we be able to detect the Bergmann's rule you mention within a single country? Probably not. This is certainly true, and indeed a major point about our paper (e.g. our final sentence 'Community responses appear to be considerably more nuanced and localised than previously considered based on theoretical macroecological expectations'). Our results can be seen as a pushback against extrapolating from very large scales (e.g. expectations of climate warming derived from Bergmann's rule) down to the community level, where all sorts of processes are occurring, and which result in a wide variety of size trait-driven and non-size-trait driven responses.
Overall, I remain to be convinced that traits in communities are overall shifting, or not shifting. Right now the paper sends a strong message that is appealing for big journals like Nat Ecol Evol, but may be detrimental for scientific research.
Some scepticism like this is certainly warranted. However, we maintain that our study represents a strong best effort to use the breadth of data that is available. We see our paper as a comprehensive first attempt at investigating this problem and we repeatedly highlight the gaps that remain.
In conclusion, while the authors know acknowledge this limitation, I think this should be more apparent. Most of the conclusions are made at the beginning of the text, while this important limitation is only briefly mentioned at the end, so won't be noticed by many.
My only final comment is to be really transparent on the boundaries within which your conclusions are valid, starting from the abstract or the first part of the paper.
We have added additional discussion of the limitations, and reworked the abstract (as discussed over email) to make the scale of our analyses more clear.

Final Decision Letter:
12th November 2021 Dear Dr Terry, We are pleased to inform you that your Brief Communication entitled "No pervasive relationship between species size and local abundance trends", has now been accepted for publication in Nature Ecology & Evolution.
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