Land-use change interacts with climate to determine elevational species redistribution

Climate change is driving global species redistribution with profound social and economic impacts. However, species movement is largely constrained by habitat availability and connectivity, of which the interaction effects with climate change remain largely unknown. Here we examine published data on 1464 elevational range shifts from 43 study sites to assess the confounding effect of land-use change on climate-driven species redistribution. We show that baseline forest cover and recent forest cover change are critical predictors in determining the magnitude of elevational range shifts. Forest loss positively interacts with baseline temperature conditions, such that forest loss in warmer regions tends to accelerate species’ upslope movement. Consequently, not only climate but also habitat loss stressors and, importantly, their synergistic effects matter in forecasting species elevational redistribution, especially in the tropics where both stressors will increase the risk of net lowland biotic attrition.

I was excited to read the paper by Guo and colleagues as I also work on climate and land -use change interactions on biodiversity and agree that very few empirical studies have looked into interacting effects between climate change and land-use change on the magnitude and direction of species range shifts. I commend the authors on tackling such a thoughtful paper, but I have a few questions and suggestions for the authors which are important for the modelling and interpretation of the results: 1) The study size is limited by sample size -only 29 studies included and only 18 of these are determined actual forest ecosystems (>25% forest cover). Not all studies are from mountainous country (e.g. Breeding bird species in NY; Zuzkerberg et al. (2009)) so the ti tle of the paper should be rethought -might be more appropriate to say elevational range shifts or elevational species redistribution.
2) Were studies weighted by the number of species included? E.g. Zuckerberg et al. (2009) included 129 bird species in their analysis whereas Rowe et al. (2009) only studied 25 small mammal species. If no, why not?
3) Why weren't the other models reported in Table 1 of the supplementary material? This is essential for understanding how much better the candidate models e xplain the data relative to other models.
4) The relationship between C C R and average shift rate was not tested in the sensitivity analysis with only the forest ecosystem sites (n = 18) due to small sample size. The authors therefore really need to downplay this interaction or reanalyze with a larger dataset as it is currently not convincing. Note that forest loss and forest cover coefficients were also no longer positive with the +/ -95% C I (Supp. Fig. 4). This should be mentioned in the 'Sensitivity Ana lysis' section of the paper.

5)
Why not display the model-averaged coefficients for different taxa type (animal or plant) since 'type' was a parameter in two of the competing models? It would also be valuable to split grassland versus forest dependent species (and maybe tropical) as I suspect that they responded differently to forest cover (%). Forest loss may also be correlated with other variables such as a gain in grassland cover and/or wetlands which could explain higher/faster movements for grassland and wetland dependent species. This additional piece would also probably help to explain the unexplained variance in the models at the species level.
The authors have probably included most data relevant for addressing the research quest ion. However, comparing to the number of predictors, the sample size was nevertheless small and the results may be sensitive to the data. There may exist multicollinearity or indirect effects among predictors. For example, higher forest cover (represented by "C over" in the model) toward the tropics (baseline temperature, "T"), or, as the authors suggested in line 45-47, stronger deforestation ("Loss" in the model) toward the tropics. Indirect effects may occur for average temperature affects the level of forest cover and then buffers species responses. Both of them influence the robustness of multiple regressions and the indirect effect cannot be captured by current analysis setting. The authors could easily check the collinearities of variables. As for the indirect effect, however, the current sample size may still impede meaningful analysis.
The authors also conducted disaggregated analysis, which tried to look at species -specific responses and also increased sample size. However, because of the coarse sp atial resolution of the climate data, a single temperature, identical to the baseline temperature for aggregated analysis, was applied to each species in the site of interest. The constraint made it difficult to test the authors' idea that lowland deforestation and/or forest expansion at highland may interact with climate to affect range shifts. The mismatch between species level response and their corresponding temperature also made the interpretation of baseline temperature ambiguous. The elevational grad ients could easily represent comparable temperature ranges along latitudinal gradients. Assigning an average temperature dramatically reduced the variation to site difference. It was thus not surprising that the disaggregated analysis derived generally similar results from aggregated analysis and unfortunately added limited information.
I had a closer look at the raw data and would like to know more details about the data treatment. As far as I understand, many studies looked at higher part of the elevati onal gradients to avoid impacts of lowland deforestation. For example, Jump et al. (2012) looked at plants at summit areas. Raxworthy et al. (2008) analyzed species distributed higher than about 1400 m.a.s.l. However, in Supplementary Figure 3, the authors seemed to include lower part of the gradient that was outside the focal extent of the original study. I did not check all of them. Please make it clear whether all the forest change profiles corresponded to the study gradients. This is where the authors a rgued not being considered in the previous studies but they might have done.  For Walther et al. (2005), more species than originally reported were included (24 rather than 18). Please clarify if there were criteria to include species.
More than half of the studies focused on plants. As the authors suggested, forest change implied habitat alteration and decreasing buffering effect on animal species under warming. Howeve r, for the plants, the gain and loss of forest may reflect direct population extirpation or increase. Shall we give broadly similar explanations to the underlying mechanisms?
Reviewer #3 (Remarks to the Author): Guo and colleagues follow up on the landmark global study of Lenoir and Svenning (2015), who analysed 1030 elevational range shifts from 29 published studies. Here, the focus is on the impact of baseline forest cover and recent forest cover change (which they assessed using the Global Forest Watch database for post-2000 changes) on these documented range shifts, and on the interaction between these factors and baseline temperature and temperature change (estimated specifically for each study). They analysed the data in two ways-at the study level, and at the species level (while controlling for nested nature of the data).
I should say, first, that reading the Methods (when I finally got them) reassured me that authors had successfully steered clear the many statistical pitfalls that had come to mind as I read the Introduction and the Results. The analysis appears quite sound, and the statistical inferences (given the data -see below) appropriately conservative.
The authors found clear statistical evidence of a synergistic (amplifying) interaction between the forest factors and the climate factors. Few will be at all surprised by this finding, as it has been frequently predicted, but as far as I know this study is the first to offer rigorous evidence.
Less predicable (and thus potentially more important) is their finding that "forest loss positively interacts with baseline temperature conditions such that forest loss in warmer regions tends to accelerate species upslope movements." Unless I am mistaken, this conclusion relies rather heavily on the only three tropical sites among the 29 sites: Hawaii (Volcanoes NP), Borneo (Mt. Kinabalu), and Madagascar. This modest site-level sample size is no fault of the authors-as far as I know, those three studies are the only tropical ones so far available that meet the Lenoir and Svenning's (2015) selection criteria. The authors mention the small number of tropical sites as a limitation of their study (Line 186 ff), but I confess that their reassurance on this point left me scratching my head: "However, because our aim was to investigate the overlooked interaction between climate change and land -use change on species redistribution, instead of drawing a conclusive numerical model, we believe the data used here are suitable." More troubling, perhaps, is that all three tropical sites are large islands, each famous in its own right for endemicity and notorious for its lowland habitat destruction. How this fact might affect the results is not clear, but the potential bias should at least be discussed. For Hawai i and Madagascar (more isolated than Borneo), highland biotas (if memory serves) are believed to have been derived from lowland immigrants, which is surely not the case with most continental sites. (There is an excellent paper on the origins of the Mt. Kinabalu biota, but I can't seem to put my hands on it.) The authors note that "greater elevational distance to the highest mountain summit within the study areas" (Line 168) had an effect on the results, but they do not mention the Massenerhebung effect (see Grubb 1971, McC ain 2005, which may well be relevant to this finding. (Mt. Kinabalu is, in fact, a classic case of this effect.) C onnectivity is (appropriately) mentioned as a critical issue in the Abstract, but not adequately addressed in the body of the paper. Does the Global Forest Watch data somehow take connectivity into account? Assessing connectivity quantitatively for each study area (the novel method of Forrero -Medina et al. 2010, cited by authors,might potentially be applied) may be too much to ask for this study, but it should be discussed. Some smaller things: Fig. 3 a and b. I like the clever way of plotting interactions, but the caption does not make clear that the two panels plot the results for different models, and why they differ. It took me way too long to figure it out from the text.
Line 158. "The fact that warm-adapted tropical species tend to shift more rapidly upslope compared to those in cooler regions could be explained by seasonal temperature stability, i.e. 'mountain pas ses are higher in the tropics' (Janzen 1967; Bonebrake 2013)." I am baffled by this suggestion. Janzen's point was precisely the opposite: in the tropics, elevational shifts (e.g. going up an over a mountain pass) are more challenging than at higher latitudes because species are more narrowly adapted to local (stable) temperature limits.
Line 161. "Alternatively, it could also be partially driven by the shallow temperature gradient across latitudes in the tropics, which makes the other option, elevational shift towards mountain summits, more likely…." It might be more accurate to say, "Alternatively, it could also be partially driven by the shallow temperature gradient across latitudes in the tropics, which makes latitudinal shifts less likely than the other option, elevational shift towards mountain summits." Grubb, P. 1971. Interpretation of the 'Massenerhebung'effect on tropical mountains. Nature 229:44 -45.
Robert K. C olwell University of C onnecticut I was excited to read the paper by Guo and colleagues as I also work on climate and land-use change interactions on biodiversity and agree that very few empirical studies have looked into interacting effects between climate change and land-use change on the magnitude and direction of species range shifts. I commend the authors on tackling such a thoughtful paper, but I have a few questions and suggestions for the authors which are important for the modelling and interpretation of the results: 1) The study size is limited by sample size -only 29 studies included and only 18 of these are determined actual forest ecosystems (>25% forest cover). Not all studies are from mountainous country (e.g. Breeding bird species in NY; Zuzkerberg et al. (2009)) so the title of the paper should be rethought -might be more appropriate to say elevational range shifts or elevational species redistribution. FG et al: Thanks for the suggestion, we changed the title from "montane species redistribution" to "elevational species redistribution". And the sample size has substantially increased to 43 sites with 29 identified as forest systems (major change #1).  Table 2). Furthermore, we believe that the disaggregated (species-level) analysis can well-capture the effects of different sample sizes among studies. Table 1 of the supplementary material? This is essential for understanding how much better the candidate models explain the data relative to other models.

FG: We appreciate the suggestion and have included the details of each of the candidate models in the main text (see the new version of Table 2).
4) The relationship between CCR and average shift rate was not tested in the sensitivity analysis with only the forest ecosystem sites (n = 18) due to small sample size. The authors therefore really need to downplay this interaction or reanalyze with a larger dataset as it is currently not convincing. Note that forest loss and forest cover coefficients were also no longer positive with the +/-95% CI (Supp. Fig. 4). This should be mentioned in the 'Sensitivity Analysis' section of the paper.
FG: With the increased sample size (major change #1), we are now able to run the same model selection process in the sensitivity analysis, and the results are largely consistent with the full dataset (see Supplementary Table 6 and Supplementary Fig.2).

5)
Why not display the model-averaged coefficients for different taxa type (animal or plant) since 'type' was a parameter in two of the competing models? It would also be valuable to split grassland versus forest dependent species (and maybe tropical) as I suspect that they responded differently to forest cover (%). Forest loss may also be correlated with other variables such as a gain in grassland cover and/or wetlands which could explain higher/faster movements for grassland and wetland dependent species. This additional piece would also probably help to explain the unexplained variance in the models at the species level.
FG: In the updated results, taxa type (plants vs. animals) had a weak effect at the aggregated level (cf. site level) and was not consistently significant in the candidate models listed in Table  1. For that reason, we decided not to show this result in the main text but as a Supplementary Figure (see the new Supplementary Fig. 1). We now discuss this weak effect in the main text but caution in reading too much into this effect (see lines 102-108 in the revised version). Regarding our analyses at the species level, taxa type (plants vs. animals) is not an important predictor (appeared in 1 out of 13 competing models) with a confidence interval straddling 0. Therefore, it is more appropriate to focus on the important and significant variables common among our candidate models. We understand the consideration for differentiating grassland and forest dependent species, but it is very difficult to apply a consistent classification criterion for the 2798 data points that cover a wide range of taxa. To address this concern, we ran the sensitivity analysis by restricting to forest systems only (assuming that species living in these areas are mostly forest dependent or forest specialists), and the consistent results further confirmed the robustness of the findings.

FG: Added, thanks.
Pg 5, Line 84 -the variables of the best fitted model should be stated here. Table 2.

FG: The variables (with detailed effect size and significance level) are now listed in
Reviewer #2 (Remarks to the Author): The authors looked at confounding effects of forest cover change on climate-driven range shifts across elevational gradients by compiling and re-analyzing published data. I think it is a much needed work even though studies focusing on climate-driven redistribution should have tried their best to exclude confounding factors, particularly habitat change, in the original design. In reality, it is challenging and not feasible for many studies. Thus, evaluating the interacting effects is a very nice attempt and provides insights into the widely reported biological responses under climate change.
After reading through the manuscript carefully, I think, generally, the authors analyzed the data appropriately given the question to address and data available so far. The discussion and conclusion followed logically and coherently. They also made it clear about the limitation of the study. However, I am not yet fully convinced by the interpretation of the results because of the constraints of multiple regressions, given the small sample size and some data treatment issues.

FG:
We would like to thank referee #2 for her/his valuable comments. We have now significantly (almost doubled) increased our sample size (major change #1) and checked for data collinearity (major change #3). See detailed responses to specific comments below.
The authors have probably included most data relevant for addressing the research question. However, comparing to the number of predictors, the sample size was nevertheless small and the results may be sensitive to the data. There may exist multicollinearity or indirect effects among predictors. For example, higher forest cover (represented by "Cover" in the model) toward the tropics (baseline temperature, "T"), or, as the authors suggested in line 45-47, stronger deforestation ("Loss" in the model) toward the tropics. Indirect effects may occur for average temperature affects the level of forest cover and then buffers species responses. Both of them influence the robustness of multiple regressions and the indirect effect cannot be captured by current analysis setting. The authors could easily check the collinearities of variables. As for the indirect effect, however, the current sample size may still impede meaningful analysis.
FG: Our results are further strengthened by increasing the sample size to 43 (site-level) and 2798 (species-level) which is a very important improvement compared with the initial submission. We would like to thank again referee #2 for mentioning that issue as it pushed us to improve and consolidate our work. We also appreciate the thoughts on multicollinearity and have used the variance inflation factor (VIF) and applied a conservative cut-off threshold of 2 to address this potential problem. The variable "Gain" was thus removed in the specieslevel analysis due to its high VIF value, while all other variables have VIF values below the threshold and with low correlation coefficients (see the new Supplementary Tables 4-5). Therefore, we believe our results are robust to data collinearity.
The authors also conducted disaggregated analysis, which tried to look at species-specific responses and also increased sample size. However, because of the coarse spatial resolution of the climate data, a single temperature, identical to the baseline temperature for aggregated analysis, was applied to each species in the site of interest. The constraint made it difficult to test the authors' idea that lowland deforestation and/or forest expansion at highland may interact with climate to affect range shifts. The mismatch between species level response and their corresponding temperature also made the interpretation of baseline temperature ambiguous. The elevational gradients could easily represent comparable temperature ranges along latitudinal gradients. Assigning an average temperature dramatically reduced the variation to site difference. It was thus not surprising that the disaggregated analysis derived generally similar results from aggregated analysis and unfortunately added limited information.
FG: Thanks for pointing out this issue. We have now replaced our temperature data using the newly published high resolution CHELSA dataset and hence are able to calculate fine-scale temperature for each 10-m elevation band as we did for the forest data (major change #2). We believe that by doing so, the aggregated and disaggregated analyses are more independent from each other. That we still find contributing effects from both habitat and climate variables in determining species range shifts in both analyses strongly supports our main argument for considering both drivers.
I had a closer look at the raw data and would like to know more details about the data treatment. As far as I understand, many studies looked at higher part of the elevational gradients to avoid impacts of lowland deforestation.  Figure 3, the authors seemed to include lower part of the gradient that was outside the focal extent of the original study. I did not check all of them. Please make it clear whether all the forest change profiles corresponded to the study gradients. This is where the authors argued not being considered in the previous studies but they might have done. More than half of the studies focused on plants. As the authors suggested, forest change implied habitat alteration and decreasing buffering effect on animal species under warming. However, for the plants, the gain and loss of forest may reflect direct population extirpation or increase. Shall we give broadly similar explanations to the underlying mechanisms? FG: Thanks for pointing out the alternative mechanism, we have now included it in the manuscript. However, the main scope of this study is not to test specific mechanisms but to assess the confounding impacts of climate and land-use change. And the fact that we did not find a significant difference between taxa at the species level, although a weak but nonsystematic effect was detected at the site level, suggests that the impacts of both factors are independent of taxa type (animals vs. plants).

Reviewer #3 (Remarks to the Author):
Guo and colleagues follow up on the landmark global study of Lenoir and Svenning (2015), who analysed 1030 elevational range shifts from 29 published studies. Here, the focus is on the impact of baseline forest cover and recent forest cover change (which they assessed using the Global Forest Watch database for post-2000 changes) on these documented range shifts, and on the interaction between these factors and baseline temperature and temperature change (estimated specifically for each study). They analysed the data in two ways-at the study level, and at the species level (while controlling for nested nature of the data).
I should say, first, that reading the Methods (when I finally got them) reassured me that authors had successfully steered clear the many statistical pitfalls that had come to mind as I read the Introduction and the Results. The analysis appears quite sound, and the statistical inferences (given the data-see below) appropriately conservative.
The authors found clear statistical evidence of a synergistic (amplifying) interaction between the forest factors and the climate factors. Few will be at all surprised by this finding, as it has been frequently predicted, but as far as I know this study is the first to offer rigorous evidence.
Less predicable (and thus potentially more important) is their finding that "forest loss positively interacts with baseline temperature conditions such that forest loss in warmer regions tends to accelerate species upslope movements." Unless I am mistaken, this conclusion relies rather heavily on the only three tropical sites among the 29 sites: Hawaii (Volcanoes NP), Borneo (Mt. Kinabalu), and Madagascar. This modest site-level sample size is no fault of the authors-as far as I know, those three studies are the only tropical ones so far available that meet the Lenoir and Svenning's (2015) selection criteria. The authors mention the small number of tropical sites as a limitation of their study (Line 186 ff), but I confess that their reassurance on this point left me scratching my head: "However, because our aim was to investigate the overlooked interaction between climate change and land-use change on species redistribution, instead of drawing a conclusive numerical model, we believe the data used here are suitable." FG: We would like to thank Robert K. Colwell for the very positive feedback on our initial work and for his insightful comments that helped us improve the quality of our work. As now explained in major change #1, we updated the Lenoir and Svenning (2015) dataset by adding a fairly large number of studies all published between 2014 to 2017 and have substantially increased the sample size, especially with 6 additional studies in the tropics (e.g. Asia, Central America and South America: see the updated version of Figure 2 which shows the improvement in spatial coverage with this updated dataset). Therefore, we believe that the interaction term that we still find between forest loss and baseline temperature is strong and coherent. We are very happy about this new and enhanced dataset that offers a consolidated overview of elevational range shifts thanks to the very recent reports from the tropics.
More troubling, perhaps, is that all three tropical sites are large islands, each famous in its own right for endemicity and notorious for its lowland habitat destruction. How this fact might affect the results is not clear, but the potential bias should at least be discussed. For Hawaii and Madagascar (more isolated than Borneo), highland biotas (if memory serves) are believed to have been derived from lowland immigrants, which is surely not the case with most continental sites. (There is an excellent paper on the origins of the Mt. Kinabalu biota, but I can't seem to put my hands on it.) FG: Thanks for pointing out the tropical island bias. We have now included this point in our discussion. Note, however, that by including more continental sites in the tropics we have attempted to correct for this sampling bias, to some extent. In addition, we also think that the forest cover baseline in year 2000 could reflect historical habitat destruction across elevations whereas the recent shift recorded over the past few decades should be comparable across tropical and continental sites.
The authors note that "greater elevational distance to the highest mountain summit within the study areas" (Line 168) had an effect on the results, but they do not mention the Massenerhebung effect (see Grubb 1971, McCain 2005, which may well be relevant to this finding. (Mt. Kinabalu is, in fact, a classic case of this effect.)

FG: Thanks for the suggested references, we have now discussed and incorporated the Massenerhebung effect in the revised text.
Connectivity is (appropriately) mentioned as a critical issue in the Abstract, but not adequately addressed in the body of the paper. Does the Global Forest Watch data somehow take connectivity into account? Assessing connectivity quantitatively for each study area (the novel method of Forrero-Medina et al. 2010, cited by authors, might potentially be applied) may be too much to ask for this study, but it should be discussed.

FG: Indeed, quantitatively assessing forest connectivity would be ideal, yet unfortunately we don't have the actual distribution information (apart from elevation) that Forrero-Medina et
al. 2010 relied on, hence we were not able to use the same method to assess connectivity. However, we believe that the forest cover percentage could represent forest connectivity across elevation, with denser forest better connected than sparse ones, albeit the pure effect of fragmentation per se after controlling for the confounding effect of area loss cannot be tested here due to a lack of data at the global extent.
Some smaller things: Fig. 3 a and b. I like the clever way of plotting interactions, but the caption does not make clear that the two panels plot the results for different models, and why they differ. It took me way too long to figure it out from the text.
FG: Thanks, we have now clarified the figure caption to make it more intuitive. The figure also changed somewhat with the updated dataset.
Line 158. "The fact that warm-adapted tropical species tend to shift more rapidly upslope compared to those in cooler regions could be explained by seasonal temperature stability, i.e. 'mountain passes are higher in the tropics' (Janzen 1967;Bonebrake 2013)." I am baffled by this suggestion. Janzen's point was precisely the opposite: in the tropics, elevational shifts (e.g. going up an over a mountain pass) are more challenging than at higher latitudes because species are more narrowly adapted to local (stable) temperature limits.

FG:
We have clarified the statement to emphasize temperature stability and thermal niches (see lines 147-151 in the revised text).
Line 161. "Alternatively, it could also be partially driven by the shallow temperature gradient across latitudes in the tropics, which makes the other option, elevational shift towards mountain summits, more likely…." It might be more accurate to say, "Alternatively, it could also be partially driven by the shallow temperature gradient across latitudes in the tropics, which makes latitudinal shifts less likely than the other option, elevational shift towards mountain summits." Pg 6 lines 92-94 "We found a consistent positive interaction effect between forest loss and temperature" -but not when the non-forest species were excluded (Supp. Fig. 2). This should be discussed in the discussion.
Pg 8 lines 126-127 "we found strong synergistic effects between baseline temperature and forest cover" -There not strong based on the confidence intervals. The word 'strong' should be reconsidered here.
Pg 9 lines 152-154 "generally positive effects of forest cover on the elevational shift rate" -Not based on the model average coefficients for the species level and when the outcomes were restricted to forest ecosystems only.
Pg 17 lines 342-344 "results were largely consistent" -Except the predictor scale (Loss) was no longer significant (p>0.05) and based on Supp. Fig 2, Temperature and Forest C over coefficient averages are no longer significant (see confidence intervals).
The conclusion of 'strong interactions'  are therefore questionable based on these specific examples listed above.
Nicely done on the reanalysis, but why did you include taxa type as a fixed effect and not as a random intercept? You may not see a difference in the results, but it should at least be tested in your LMM random structure prescreening (pg 15, line s 309-311)... and may explain some of the unexplained variance at the species level.
I missed this during the first review, but where are the residual plots and goodness of fit tests? These are needed for the reviewers to determine the fit of the best fitting models.

Respectfully, C hrystal Mantyka-Pringle
Reviewer #2 (Remarks to the Author): The authors have put substantial effort to improve the robustness of the results by increasing sample size to 43 sites and 2798 species. They also applied fine-scale temperature to species specific analysis, making it more independent from site -specific analyses. From the revised results, the authors found generally positive effects of climate (base line temperature) and habitat (forest cover) on range shifts. Importantly, they found synergistic effect between forest loss and baseline temperature on species redistribution in site level analysis, which constituted the main points of this work. Again, I agree it is a very thoughtful paper and here I have only a few questions left: The temporal mismatch between the forest change (2000)(2001)(2002)(2003)(2004)(2005)(2006)(2007)(2008)(2009)(2010)(2011)(2012)(2013)(2014)(2015) and the surveys of species range shifts (over several decades) was worrisome. The starting years of species survey were on average 44-year ahead the beginning of the forest database, and only the last 7 years (average across studies) were covered by the forest data, let alone some studies showed no overlap. The spatial consistency of the Global Forest Watch didn't ease the concern of methodological artefact. However, given data availability, there might be no better solution for this. I would suggest that the authors reveal and emphasize the temporal mismatch in greater detail, so that the readers may judge the results by themselves.
The positive correlation between forest loss and gain was counter-intuitive and raises similar concern about methodological artefact. Is there any particular reason for this phenomenon? If it was forest gain applied to the analysis, would it yield meaningful results to support current argument? I encourage providing different supporting evidence to strengthen current discussion.
The authors raised insightful questions about the opposite impacts of forest loss on species range shifts in warmer and colder regions. There may be post hoc explanations for the findings but in fact, plant extirpation or microclimatic changes following habitat disturbance were not restricted to warmer regions. And fundamentally, why wouldn't forest loss impede range shifts of warm -adapted species, at least in relative sense, comparing to cold adapted species? Given current findings, I guess the authors also need to call attention to the habitat-constrained climate tracking for temperate species.
A minor point about the baseline temperature in the site level analysis -it confounded with the extent of elevational gradient, not simply reflecting tropical or boreal sites. Many low latitude sites yielded similar baseline temperature to cooler regions. In this regard, species level analysis captured the temperature effects better.
For the sensitivity analysis, was the interaction term sensitive to the criteria of forest ecosystem? C urrent criteria, i.e. > 25% forest coverage seemed to be loose. Please also report the details of the interaction term.
Reviewer #3 (Remarks to the Author): In this revision, Guo and colleagues have been exceptionally thorough in responding to reviewers' concerns and suggestions, and impressively enterprising in expanding the basis for their study to additional datasets, making possible additional and more rigorous statistical analyses.
In my earlier review, I had expressed concern about relying on just three tropical sites -all of them islands-to infer the important result that range shifts driven by forest loss are more rapid at low latitudes than in temperate and boreal regions. The authors have now discussed this issue and managed to find a few additional tropical sites.
The assumption made by the authors is that "baseline temperature" is a proxy for latitude, which it certainly can be. But shifts of high elevation tropical species could have a baseline temperature characteristic of boreal regions (3000 m at sea level on the equator corresponds to 50 degrees latitude at sea level). To my dismay, unless I am mistaken, latitude is not tabled for the study sites, although (of course) elevational range is recorded. I suggest adding latitude data to the Supplemental tables, while making clear that "baseline temperature" is not a simple proxy for latitude. Fig. 4. The X-axis labels are too small, and they should be defined in the caption.
Tables 1 and 2. Define the variables in the table caption.
There were many grammatical and usage problems in the main text. Being a compulsive editor, and having identified myself, I took the liberty of correcting them in the Word document, with Track C hanges.
Robert K. C olwell University of C onnecticut