Review Reports

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Please find my detailed comments in the attached file Review_coasts-4348302.pdf

Comments for author File: Comments.pdf

Author Response

Comment 1. The manuscript is based on a valuable long-term dataset, but its novelty should be clarified more explicitly. A recent broader study by the same authors (Scarton et al. 2026, Ref [8]) appears to have analysed wintering waterbirds in the Venice Lagoon over the same period, using similar IWC data, macro-areas, species/guild trends and CTI. At present, the manuscript only briefly refers to the importance of the lagoon for wintering waterbirds (lines 41-43), but it does not clearly explain why a separate wader-focused analysis is needed. The Introduction should better justify the taxonomic focus on waders, and the Discussion should explicitly state what this analysis reveals that was not evident from the broader waterbird study. In particular, the authors should clarify whether waders show different spatial, functional or thermal patterns compared with the whole wintering waterbird assemblage.

Response 1. We agree with the reviewer. In the original version, the relationship between the present wader-focused analysis and our previous broader waterbird paper was not sufficiently explicit. We have now revised the Introduction to clarify why a separate analysis of waders is warranted. We explain that waders form a more ecologically coherent group than the whole waterbird assemblage, because they are strongly linked to intertidal habitats, benthic prey availability and high-tide roosting sites. This taxonomic focus allows us to address questions that could not be fully resolved in the broader waterbird analysis, particularly the influence of Dunlin dominance, the robustness of compositional change after excluding the dominant species, and the sensitivity of CTI to abundance structure. We also revised the Discussion to state more clearly what this study adds. The revised text emphasizes that the wader-focused analysis reveals: (i) significant compositional turnover despite persistent dominance by Dunlin; (ii) no evidence of increasing dominance or declining evenness, contrary to our initial interpretation; (iii) a spatial pattern towards the Open lagoon that is largely Dunlin-driven; and (iv) a weak abundance-weighted CTI signal that is not supported by presence–absence CTI and is not robust to the exclusion of Dunlin.

Comment 2. The manuscript states that community structure changed markedly, but this conclusion is currently based mainly on univariate descriptors, such as total abundance, species richness, Shannon diversity and Jaccard similarity. These metrics are useful, but they do not show whether the assemblage changed as a whole or whether the observed pattern  was mainly driven by the increasing dominance of Dunlin. This is particularly important because the manuscript also reports an increase in the open lagoon and a decline in fish farms, but it remains unclear whether these spatial patterns reflect a broad  distribution 
of the assemblage, a Dunlin-driven pattern, or changes in particular guilds. Jaccard similarity may miss changes in relative abundance because it is based only on presence–absence, while Shannon diversity may decline simply because one species becomes dominant. I therefore recommend adding an abundance-based multivariate analysis, such as NMDS  or PCoA based on Bray–Curtis dissimilarity, to examine differences in species composition among time periods. Years could be grouped into periods, and the analysis could be performed both including and excluding Dunlin. A PERMANOVA could then be used to test whether assemblage composition differs among periods. If species-by-year-by-macro-area data are available, the same approach could also test whether differences among periods vary across spatial classes, such as open lagoon, fish farms, minor wetlands and the littoral strip.As a related point, Bray–Curtis is mentioned in the Methods [line 203], but I could not 
find the corresponding results in the text.

Response 2. We agree and have added the requested multivariate analyses. We performed Principal Coordinates Analysis (PCoA) based on Bray–Curtis dissimilarities calculated from square-root-transformed annual species abundances. The analyses were carried out both including all species and excluding Dunlin, in order to test whether compositional change persisted after removing the dominant species. Years were grouped a priori into three approximately decadal periods: 1993–2002, 2003–2012 and 2013–2022. We also added one-way PERMANOVA with 9,999 permutations to test whether assemblage composition differed among periods. Pairwise PERMANOVA comparisons among periods were inspected as post-hoc exploratory tests. The revised Results report that the pattern was significant both when all species were included and when Dunlin was excluded. We also added a new PCoA figure showing the ordination of years by period, with separate panels including and excluding Dunlin. This new analysis substantially changed and strengthened the interpretation. We now conclude that the assemblage underwent significant compositional reorganization, and that this pattern was not solely attributable to changes in Dunlin abundance. At the same time, we no longer interpret the results as evidence of progressive structural simplification.

Comment 3.Figure 2 currently appears to show mainly total abundance, but this is difficult to interpret given the verwhelming dominance of Dunlin. To better support the statement that the assemblage is increasing but becoming structurally simplified, I suggest showing total abundance both including and excluding Dunlin (or alternatively using a stacked abundance plot). It would also be useful to show temporal changes in species richness, Shannon diversity/evenness and the annual proportion of Dunlin. Also, an explicit dominance metric, such as the Berger–Parker index, or Pielou’s evenness index, would make the pattern of increasing dominance more transparent. These additions could be incorporated into panels of Figure 2 or presented as a closely related supplementary figure.

Response 3. We agree and have completely revised Figure 2. The new Figure 2 is a multi-panel figure showing: (a) total abundance including and excluding Dunlin; (b) species richness; (c) Shannon diversity and Pielou’s evenness; and (d) Dunlin proportion and Berger–Parker dominance. We also added the corresponding analyses to the Results. These new results led us to revise the original interpretation. Although the assemblage remained highly dominated by Dunlin throughout the study period, dominance did not increase over time. Instead, species richness, Shannon diversity and Pielou’s evenness increased, while Berger–Parker dominance and the annual proportional contribution of Dunlin declined slightly but significantly. We therefore removed the original conclusion that the assemblage was becoming progressively structurally simplified and replaced it with a more nuanced interpretation: the assemblage increased in abundance and was compositionally reorganized, while remaining strongly influenced by persistent Dunlin dominance.

Comment 4. The interpretation of the CTI analysis should be more cautious. Although CTI increases significantly, this result is not robust after removing Dunlin, suggesting that the apparent thermal signal may be strongly influenced by dominance structure rather than reflecting a broad community-wide shift towards species with higher thermal affinities. I recommend reporting both abundance-weighted CTI and presence–absence CTI. This would distinguish a change in the thermal composition of individuals from a change in the thermal composition of the species list. A leave-one-species-out sensitivity analysis would also help identify whether the CTI trend is driven mainly by Dunlin or by several species.
Finally, the authors should explain the biological magnitude of the CTI slope. The reported slope of 0.033 yr⁻¹ is statistically significant, but it is not clear whether this represents a small or large change relative to the range of STI values among the analysed species.

Response 4. We fully agree. We have revised both the Methods and Results and substantially changed the interpretation of CTI. In addition to the original abundance-weighted CTI, we now report presence–absence CTI, CTI excluding Dunlin, presence–absence CTI excluding Dunlin, and a leave-one-species-out sensitivity analysis.The revised Results show that the abundance-weighted CTI increased significantly, but the magnitude of the increase was weak relative to the range of STI values among the analysed species. Moreover, the trend was not robust to the exclusion of Dunlin. In contrast, the presence–absence CTI declined over time, indicating that the thermal composition of the species list did not show the same signal as the thermal composition of individuals.The leave-one-species-out analysis further confirmed that the abundance-weighted CTI trend was strongly influenced by a few species. Removal of Dunlin made the CTI trend non-significant, and removal of Pied Avocet also strongly reduced the trend. We therefore revised the Abstract, Results and Discussion to state that the CTI signal is weak, dominance-sensitive and should not be interpreted as clear evidence of community-wide thermophilization.

Comment 5. The source and calculation of STI values should be clarified. The manuscript states that STI values were derived from published datasets based on the intersection of species distribution maps with long-term climatic data, but it is unclear whether the values in Table S1 were taken directly from previous datasets or recalculated by the authors. If they 
were taken from published sources, the source of each STI value should be specified. If they were recalculated, the Methods should describe the distribution maps, climate data and spatial procedure used. This is important because the CTI analysis depends directly on the STI values assigned to individual species.

Response 5. We agree that the original text was insufficiently explicit. We have clarified the Methods to state that STI values were derived from published datasets based on the intersection of species distribution maps with long-term climatic data. We specify that STI values correspond to mean January temperature across the non-breeding distribution of each species and that the climatic baseline used in the source datasets was 1950–2000. We also indicate where STI values are reported in the  Supplementary Material. We did not recalculate STI values independently in this study; rather, we used published STI values and applied them to the Venice Lagoon annual species abundance data to calculate CTI. This clarification has been added to improve reproducibility.

Comment 6. The TRIM outputs should be reported more transparently. The Methods state that, for each analytical unit, the authors estimated (i) annual indices relative to a reference year, (ii) overall log-linear trends and (iii) TRIM trend classifications. However, it is not clear where (i) was reported, what the reference year was, and whether uncertainty estimates, such as standard errors or confidence intervals, are available for the annual indices and overall trends.The reporting of trend analyses is not fully consistent across the manuscript. In some parts of the Results, trends are reported as annual percentage changes from TRIM, whereas in the spatial analyses and climatology the authors report r and p values. This makes it unclear whether all trends were estimated using the same log-linear Poisson approach, or whether some analyses, particularly the spatial ones, were based on standard linear regression. The authors should clarify which statistical model was used for each type of trend analysis and report the results in a more consistent way. The distinction between “stable” and “uncertain” TRIM classifications should be explained in the Methods. Some classifications in Table 1 may appear counterintuitive; for example, an estimated annual change of 11.8% is classified as a “moderate increase”, whereas 9% is classified as a “strong increase”. The authors should clarify the standard TRIM classification rules, including whether classifications depend not only on the 
estimated slope but also on its uncertainty.

Response 6. We agree. We have revised the Methods to clarify the distinction between TRIM analyses and linear regression analyses. TRIM was used for count-based time series, namely total abundance, species-level counts and eco-functional guild totals. These variables represent annual count series and are suitable for log-linear trend modelling with TRIM, which accounts for missing values, overdispersion and serial correlation. By contrast, community metrics, annual macro-area proportions and CTI values were not analysed with TRIM because they are aggregate, derived or proportional metrics rather than raw count series. Their temporal patterns were assessed using linear regression models with year as a continuous predictor. This distinction is now explicitly stated in the Methods. We also revised Table 1 to report TRIM results more transparently, including annual percentage change, standard error, p-value, number of winters and TRIM classification. In the Methods, we added an explanation of the distinction between “stable” and “uncertain” according to standard TRIM classification rules: a trend is classified as stable only when the confidence interval around the multiplicative slope is sufficiently narrow and remains within the predefined stability interval, whereas uncertain trends have confidence intervals too wide to assign a reliable direction or stability class. We now explicitly state that TRIM classifications depend not only on the estimated slope but also on its uncertainty.

Comment 7.I suggest replacing Figure 3 (and perhaps merging it with Figure 2 as an additional panel), with a stacked bar plot showing the annual abundance of the selected species, excluding Dunlin, whose contribution should already be clear from other panels in Figure 2. This would provide a clearer overview of the relative contributions of the other main species through time and help readers see whether changes are shared across species or concentrated in a few taxa. The detailed species-specific plots currently shown in the panels of Figure 3 could be moved to the Supplementary Information. I would also encourage the authors to include a multivariate figure, such as an NMDS or PCoA ordination, to visualize differences in species composition among time periods and spatial classes.

Response 7. We have revised the figure set in response to this comment. The revised Figure 2 now summarizes the main abundance, richness, diversity, evenness and dominance patterns, including total abundance with and without Dunlin. We added a new PCoA figure (Figure 3) showing differences in assemblage composition among periods, both including and excluding Dunlin. This directly addresses the reviewer’s request for a multivariate figure. We retained a species-level figure for the main species and a focused figure for Eurasian Oystercatcher and Ruddy Turnstone, because these species provide useful examples of formerly scarce taxa that increased markedly during the study period. However, the emphasis of the Results has been shifted away from species-specific plots and towards the new community-level, dominance and multivariate analyses.

Comment 8. Several reporting and terminology issues should be corrected for clarity. First, species names are not used consistently throughout the manuscript, figures and tables. In some places, species are referred to by their common names, whereas elsewhere scientific names are used. This should be standardized. At first mention, both the common name 
and the full scientific name should be given, including for Dunlin in the Abstract; thereafter, one naming convention should be used consistently.Second,the phrase “between consecutive winters” should be revised where 2020 and 2022 are compared despite the absence of data for 2021; “consecutive sampled winters” or “successive winters with available data” would be more accurate. 

Response 8. We have revised species nomenclature throughout the manuscript. At first mention, common and scientific names are now provided, including Dunlin Calidris alpina in the Abstract. Species names follow the updated English and scientific nomenclature adopted in the Supplementary Material.

 Additional changes In addition to the specific changes requested by the reviewer, we revised the title to better reflect the new interpretation of the manuscript. The original title referred to “dominance patterns, habitat shifts and weak thermal signals”; the revised title is “Long-term changes (1993–2022) in wintering waders of the largest Mediterranean coastal lagoon: compositional reorganization, dominance effects and weak thermal signals.” This avoids overemphasizing habitat shifts and better reflects the revised conclusion that spatial patterns were largely Dunlin-driven.We also revised the Abstract, Results and Discussion to remove or qualify statements that were not sufficiently supported by the original analyses. In particular, we no longer conclude that the assemblage became progressively structurally simplified, nor do we interpret the spatial redistribution as a generalized habitat shift of the whole assemblage. Instead, we emphasize compositional reorganization, persistent but non-increasing dominance, and dominance-sensitive spatial and thermal indicators.

 

Reviewer 2 Report

Comments and Suggestions for Authors

Title: Long-term changes (1993–2022) in wintering waders of the largest Mediterranean coastal lagoon: dominance patterns, habitat shifts and weak thermal signals

 

General Comments

The manuscript asks a relevant question: how has the wintering wader assemblage of the Venice Lagoon changed over three decades? The study combines abundance trends, community structure, functional guilds, CTI, and spatial distribution across macro-areas. The introduction is generally logical, and the study system is important.

The paper’s strongest contribution is the finding that abundance increase does not necessarily mean ecological stability, because total numbers are heavily driven by dominant species. That is a useful message.

But the manuscript currently suffers from four main problems:

1. Some key claims are not statistically demonstrated. For example, “structural simplification” is repeatedly claimed, but there is no formal trend test for Shannon diversity, evenness, dominance, or beta-diversity.
2. Spatial “habitat shift” is under-analysed
   The paper reports an increase in open lagoon abundance and a decline in fish farms, but does not fully separate true redistribution from changes in total abundance, detectability, survey conditions, or habitat availability.
3. The CTI section is promising but incomplete
   The authors correctly show that the CTI trend disappears after excluding Dunlin, but they stop too early. They need a fuller species-contribution analysis.
4. There may be overlap with a closely related previous publication by the same authors
   The reference list includes a 2026 Diversity paper on wintering waterbirds in the Venice Lagoon from 1993–2022, with trends, spatial patterns, and management issues. The authors must clearly explain what is genuinely new here.

Major comments

1. The novelty must be clarified because the dataset appears already published

This is the biggest editorial risk. The manuscript cites a recent paper by Scarton et al. titled “Wintering Waterbirds in the Venice Lagoon, Years 1993–2022: Trends, Spatial Patterns and Management Issues”. The current manuscript also uses the Venice Lagoon 1993–2022 wintering waterbird dataset and discusses trends, spatial patterns, and management implications. That creates a serious question: what is new here? The authors need a direct statement in the Introduction or Methods explaining the difference between the previous article and this manuscript.

2. “Structural simplification” is an important claim but not properly quantified

The abstract says the community changed markedly, with increasing dominance and reduced evenness. The Discussion also states that the assemblage is increasingly abundant but structurally simplified. This is plausible, but the analysis does not fully support it yet.

The manuscript reports that Shannon diversity ranged from approximately 0.3 to 1.17 and those lower values occurred in years with high abundance. But this is descriptive. There is no formal trend test for Shannon diversity, Pielou’s evenness, Berger-Parker dominance index, Simpson dominance, Proportion of total abundance represented by Dunlin, Temporal beta-diversity

3. The CTI analysis is good but incomplete

The CTI analysis is one of the most interesting parts of the manuscript. The authors calculate CTI using species-specific STI values and then repeat the analysis excluding Dunlin. The result is important: CTI increases significantly when all species are included, but the trend becomes non-significant after Dunlin is removed.  

4. The spatial analysis is too simple for the claim of habitat shift

The manuscript reports that the open lagoon supported most waders, averaging 71% of individuals, while fish farms accounted for 26%. It also reports a strong increase in the open lagoon and a significant decline in fish farms. This is interesting, but the interpretation “shift towards natural tidal habitats” needs more support.

At present, the analysis appears to use simple temporal trends in counts by macro-area. That is not enough to prove redistribution. The authors should analyze proportional use of macro-areas through time, not only raw abundance. If total abundance increased, open lagoon counts may rise simply because the whole population increased. Also, the authors should be careful with wording. The IWC counts are high-tide or rising-tide counts intended to maximize detection of roosting birds. Therefore, the data may reflect roosting distribution as much as foraging habitat use. The manuscript currently discusses open lagoon as “foraging habitat” too confidently.

5. The statistical methods need strengthening

The methods state that species-level trends were estimated using TRIM, with correction for overdispersion and serial correlation. That is appropriate for count monitoring data. But other analyses are handled weeklies. Temporal trends in climate variables, total abundance, and CTI were assessed using linear regression. This is too basic for a 30-year ecological time series.

The authors do not necessarily need very complex models, but they should at least test residual autocorrelation and report confidence intervals. For abundance, TRIM or a generalized model is more appropriate than simple linear regression.

6. Species-level trend table needs confidence intervals

Table 1 reports annual change, trend category, and p-value for 19 species. This is not enough.

For a serious trend paper, the table should include: annual multiplicative slope or annual percentage change, standard error, 95% confidence interval, p-value, TRIM classification, number of years observed and total abundance or mean annual abundance.

7. The Methods acknowledge detectability problems but do not solve them

The authors honestly acknowledge many limitations: imperfect detectability, observer variation, weather, water level, estimation errors in large flocks, and habitat/species-specific detectability. This is good. But the manuscript then largely proceeds as if these uncertainties do not affect the interpretation.

8. The heading “Climate and Sea Level Trends” is misleading

Section 3.1 is titled Climate and Sea Level Trends, but the text only reports winter temperature. Sea level is not analyzed in the Results. Either add actual sea-level analysis or remove “Sea Level” from the heading. This is a simple but important fix.

Recommendation

Major revision

The manuscript has a publishable core. The dataset is valuable: a 30-year International Waterbird Census series from the Venice Lagoon, with 29 annual counts and 28 recorded wader species, excluding 2021 due to COVID-19 restrictions. The central result is interesting: wintering wader abundance increased, but the assemblage became more dominated by a few species, especially Dunlin, while the apparent Community Temperature Index signal became weak once Dunlin was removed.

However, the paper is not yet strong enough for a high-quality ecological journal. The major weakness is not the dataset. The dataset is good. The weakness is the analytical framing and overinterpretation. Several conclusions are stronger than the analyses can support, especially regarding habitat shifts, thermal signals, and “structural simplification.”

Comments for author File: Comments.pdf

Author Response

We thank Reviewer 2 for the detailed and constructive review. We appreciate the reviewer’s positive assessment of the dataset and of the central message of the study. We also agree that several conclusions in the original manuscript were stronger than the analyses could support, particularly regarding structural simplification, spatial redistribution and the CTI signal. In response, we have substantially revised the manuscript, added several new analyses, modified the title, and made the interpretation more cautious throughout the Abstract, Results and Discussion.

Comment 1. The novelty must be clarified because the dataset appears already published. This is the biggest editorial risk. The manuscript cites a recent paper by Scarton et al. titled 2022: Trends, Spatial Patterns and 2022 wintering waterbird dataset and discusses trends, spatial patterns, and management implications. That creates a serious question: what is new here? The authors need a direct statement in the Introduction or Methods explaining the difference between the previous article and this manuscript.  

Response 1.  We agree that this was insufficiently clear in the original submission. We have now revised the Introduction to explicitly distinguish the present study from the previous whole-waterbird paper. The previous paper analysed the entire wintering waterbird assemblage, whereas the present manuscript focuses exclusively on waders as an ecologically coherent group with stronger dependence on intertidal habitats, benthic prey availability and high-tide roosting sites.This narrower taxonomic focus allowed us to address questions that could not be fully resolved in the broader study: whether the increase in wader abundance is accompanied by changes in dominance and evenness; whether compositional reorganization persists after removing the dominant species, Dunlin; whether spatial changes among macro-areas reflect a broad redistribution of the assemblage or are mainly driven by Dunlin; and whether CTI trends represent a community-wide thermal signal or a dominance-sensitive abundance effect. We also revised the Discussion to state explicitly what the present analysis adds: significant compositional turnover despite persistent dominance, no evidence of increasing dominance, a spatial pattern largely driven by Dunlin, and a weak CTI signal that disappears when dominance effects are controlled.

Comment 2. Structural simplification is an important claim but not properly quantified. The abstract says the community changed markedly, with increasing dominance and reduced evenness. The Discussion also states that the assemblage is increasingly abundant but structurally simplified. This is plausible, but the analysis does not fully support it yet. The manuscript reports that Shannon diversity ranged from approximately 0.3 to 1.17 and those lower values occurred in years with high abundance. But this is descriptive. There is no formal trend test for Shannon diversity, , Berger-Parker dominance index, Simpson dominance, Proportion of total abundance represented by Dunlin, Temporal beta-diversity 

Response 2. We agree. The original interpretation of progressive structural simplification was too strong. We have now added formal analyses of species richness, Shannon diversity, Pielou’s evenness, Berger–Parker dominance and Dunlin proportional contribution. We also added abundance-based multivariate analyses using Bray–Curtis dissimilarities and PERMANOVA to assess compositional change among periods. The new results changed our interpretation. Species richness, Shannon diversity and Pielou’s evenness increased significantly over time, while Berger–Parker dominance and the annual proportional contribution of Dunlin declined slightly but significantly. Therefore, the revised manuscript no longer states that the assemblage became progressively structurally simplified. Instead, we now describe the assemblage as highly uneven and strongly dominated by Dunlin, but without evidence of increasing dominance or declining evenness. We also added PCoA and PERMANOVA based on Bray–Curtis dissimilarities to assess abundance-based compositional change among approximately decadal periods. These analyses were performed both including and excluding Dunlin. The results showed significant compositional differences among periods in both cases, indicating that long-term assemblage reorganization was not solely attributable to the dominant species.

Comment 3. The CTI analysis is one of the most interesting parts of the manuscript. The authors calculate CTI using species-specific STI values and then repeat the analysis excluding Dunlin. The result is important: CTI increases significantly when all species are included, but the trend becomes non-significant after Dunlin is removed.   

Response 3. We agree and have expanded the CTI section substantially. In addition to the original abundance-weighted CTI, we now report: CTI excluding Dunlin, presence–absence CTI, presence–absence CTI excluding Dunlin, and a leave-one-species-out sensitivity analysis. These additions allowed us to distinguish changes in the thermal composition of individuals from changes in the thermal composition of the species list. The revised Results show that abundance-weighted CTI increased significantly, but the biological magnitude of the increase was weak relative to the range of STI values among the analysed species. Moreover, the trend was not robust to the exclusion of Dunlin. In contrast, presence–absence CTI declined over time, showing that the species list did not shift in the same direction as the abundance-weighted index. The leave-one-species-out analysis further indicated that the CTI trend was strongly influenced by a few species, especially Dunlin and Pied Avocet. We therefore revised the Abstract, Results and Discussion to interpret the CTI signal as weak and dominance-sensitive, rather than as clear evidence of community-wide thermophilization.

Comment 4. The manuscript reports that the open lagoon supported most waders, averaging 71% of individuals, while fish farms accounted for 26%. It also reports a strong increase in the open lagoon and a significant decline in fish farms. This is interesting, but the interpretation "shifts towards natural tifal habitats need more support".  At present, the analysis appears to use simple temporal trends in counts by macro-area. That is not enough to prove redistribution. The authors should analyze proportional use of macro-areas through time, not only raw abundance. If total abundance increased, open lagoon counts may rise simply because the whole population increased. Also, the authors should be careful with wording. The IWC counts are high-tide or rising-tide counts intended to maximize detection of roosting birds. Therefore, the data may reflect roosting distribution as much as foraging habitat use. The manuscript currently discusses open lagoon as "foraging habitat" too confidently.

Response 4. We agree. We have revised the spatial analysis and the interpretation. We now analyse annual macro-area proportions rather than relying only on raw abundance. Proportions were calculated separately for the whole assemblage, for Dunlin alone and for all species excluding Dunlin. This allowed us to test whether changes in macro-area use reflected a broad redistribution of the assemblage or were mainly driven by the dominant species.The revised results show that the proportional contribution of the Open lagoon increased and that of Fish farms decreased when the whole assemblage was analysed. However, this pattern disappeared after excluding Dunlin, while Dunlin alone showed a strong increase in proportional occurrence in the Open lagoon and a decline in Fish farms. We therefore no longer interpret the pattern as a generalized habitat shift of the whole wader assemblage. Instead, we describe it as an apparent spatial redistribution of counted birds that was largely Dunlin-driven. We also revised the Discussion to emphasize the limitations of IWC spatial data. Open lagoon counts were conducted during high or rising tides to maximize detection of roosting birds; therefore, the data describe the distribution of counted birds during standardized winter surveys and cannot fully distinguish foraging habitat use from roosting distribution or detectability. We have consequently replaced stronger wording such as “habitat shift” or “shift towards natural tidal habitats” with more cautious expressions such as “distribution of counted birds among macro-areas” and “proportional occurrence in the Open lagoon”.

Comment 5. The statistical methods need strengthening The methods state that species-level trends were estimated using TRIM, with correction for overdispersion and serial correlation. That is appropriate for count monitoring data. But other 
analyses are handled weeklies. Temporal trends in climate variables, total abundance, and CTI were assessed using linear regression. This is too basic for a 30-year ecological time series. The authors do not necessarily need very complex models, but they should at least test residual autocorrelation and report confidence intervals. For abundance, TRIM or a generalized model is more appropriate than simple linear regression. 

Response 5. We agree that the original Methods were not sufficiently clear. We have now revised the statistical Methods to explicitly distinguish between TRIM analyses and linear regression analyses.TRIM was used for count-based time series, namely total abundance, species-level counts and eco-functional guild totals. These variables are annual count series and are suitable for log-linear trend modelling within the TRIM framework, which accounts for missing values, overdispersion and serial correlation. This revision also addresses the reviewer’s concern about total abundance: total abundance is now reported using TRIM, not as a simple linear regression.Linear regressions were used only for continuous or derived variables, including winter temperature, species richness, diversity and dominance indices, annual macro-area proportions, abundance-weighted CTI and presence–absence CTI. These variables are not raw count series suitable for TRIM, but derived indices or proportions. We now state this distinction explicitly in the Methods.We also report slopes, confidence intervals and p-values for the main linear trends in the Results, and we have made the interpretation more cautious where the underlying variables are derived metrics.

Comment 6. Species-level trend table needs confidence intervals. Table 1 reports annual change, trend category, and p-value for 19 species. This is not enough. For a serious trend paper, the table should include: annual multiplicative slope or annual 
percentage change, standard error, 95% confidence interval, p-value, TRIM classification, number of years observed and total abundance or mean annual abundance.  

Response 6. We have revised Table 1 to improve transparency of TRIM results. The table now reports annual percentage change, standard error, p-value, number of winters in which each species was recorded and TRIM classification. We also added total waders and the three eco-functional guilds to the table, because these count-based series were also analysed with TRIM. We did not include all additional abundance descriptors in the main table to avoid making it excessively wide and difficult to read, but cumulative abundances and annual counts are provided in the Supplementary Material. We also clarified in the Methods that TRIM classifications depend not only on the estimated annual change but also on the uncertainty around the multiplicative slope. This should help explain why some apparently similar annual changes may receive different TRIM classifications.

Comment 7. The Methods acknowledge detectability problems but do not solve them The authors honestly acknowledge many limitations: imperfect detectability, observer variation, weather, water level, estimation errors in large flocks, and habitat/species-specific detectability. This is good. But the manuscript then largely proceeds as if these uncertainties do not affect the interpretation. 

Response 7. We agree that the limitations associated with detectability, observer variation, water level, weather and large-flock estimation errors needed to be integrated more clearly into the interpretation. We have therefore expanded both the Methods and Discussion. In the Methods, we now explain that detailed observer-level and survey-condition metadata were not systematically archived for the whole time series, preventing formal modelling of detectability. At the same time, we emphasize that survey design, spatial coverage and counting protocols remained consistent through time within the national IWC framework, supporting the use of the dataset for medium- to long-term trend analyses. In the Discussion, we now explicitly state that IWC data cannot fully separate changes in abundance from changes in detectability, roosting distribution or short-term tidal conditions. This is particularly important for highly gregarious species such as Dunlin and for high-tide or rising-tide counts in the Open lagoon. We therefore interpret the spatial results as changes in the distribution of counted birds among macro-areas, not as direct evidence of foraging habitat selection. 

Comment 8. Section 3.1 is titled Climate and Sea Level Trends, but the text only reports winter temperature. Sea level is not analyzed in the Results. Either add actual sea-from the heading. This is a simple but important fix.

Response 8.  We agree. We have removed “Sea Level” from the heading. The revised heading is now “Climate Trends”. We did not add a sea-level trend analysis because sea level was not one of the variables analysed in the Results. Sea-level rise and tidal-flat deepening are discussed only as broader contextual factors in the Discussion, where we now use cautious wording and avoid presenting them as direct explanatory variables for the observed spatial patterns.

Additional changes. In response to the reviewer’s general concern about overinterpretation, we revised the title and several key conclusions. The original title included “habitat shifts”; the revised title is “Long-term changes (1993–2022) in wintering waders of the largest Mediterranean coastal lagoon: compositional reorganization, dominance effects and weak thermal signals.” This better reflects the revised interpretation. We also revised the Abstract, Results and Discussion to remove or qualify unsupported claims. In particular, we no longer state that the assemblage became progressively structurally simplified, and we no longer interpret the increase in the Open lagoon as a generalized shift towards natural tidal habitats. Instead, the revised conclusion emphasizes abundance increase, persistent but non-increasing Dunlin dominance, significant compositional reorganization, Dunlin-driven spatial patterns and a weak, dominance-sensitive CTI signal.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors have addressed most of my previous major concerns and the manuscript is substantially improved. In particular, the added multivariate analyses, the revised CTI treatment, the new dominance metrics, the analyses performed both with and without Dunlin, and the clearer comparison with the broader waterbird study all strengthen the paper. I recommend minor revision, mainly to resolve remaining small inconsistencies.

 

 

lines 340-344

The CTI formula appears to have a formatting issue in pdf file. In addition, the term S is defined in the text but does not appear in the abundance-weighted CTI formula. Please revise the equation and the accompanying definitions.

 

Lines 393-398

It is unclear why total abundance was analysed using TRIM, whereas total abundance excluding Dunlin was analysed using a linear trend. Since the latter is also a count-based annual time series, please clarify why a different modelling approach was used. In addition, the two trends are reported in different units, annual percentage change for total abundance and individuals yr⁻¹ for the series excluding Dunlin, which makes their magnitudes difficult to compare. Please consider analysing both series using the same approach, or at least reporting the results in comparable units.

 

Figure 2

In Figure 2d, Dunlin proportion and Berger–Parker dominance appear to overlap almost completely. If Dunlin was the most abundant species in every year, these two metrics are mathematically equivalent, because the Berger–Parker index is the proportional abundance of the most abundant species. In that case, plotting both curves may confuse readers. I suggest explicitly stating in the caption/text that Berger–Parker dominance is equivalent to Dunlin proportional abundance because Dunlin was consistently the dominant species.

 

Figure 3

Adding group ellipses to Figure 3 could improve readability, but this is optional. If included, the caption should define what the ellipses represent, and the interpretation should remain based on the PERMANOVA results.

 

Table 1

I noticed that several annual change estimates in revised Table 1 differ from those in the previous version of the manuscript. This may simply reflect recalculation or correction during revision, but it would be helpful if the authors clarified this, especially where the revised values affect the interpretation of species-level or guild-level trends.

 

Figure(s) 6

Figure numbering should be checked. The manuscript currently appears to label both the macro-area figure and the CTI figure as Figure 6.

Author Response

Comment 1. The CTI formula appears to have a formatting issue in pdf file. In addition, the term S is defined in the text but does not appear in the abundance-weighted CTI formula. Please revise the equation and the accompanying definitions.

Answer 1. We have revised the formula and the accompanying definitions. The equation now explicitly states that the summation is over i = 1,...,S_y, where S_y is the number of species with available STI values in year y. This removes the formatting ambiguity and ensures consistency between the equation and the text.

Comment 2. It is unclear why total abundance was analysed using TRIM, whereas total abundance excluding Dunlin was analysed using a linear trend. Since the latter is also a count-based annual time series, please clarify why a different modelling approach was used. In addition, the two trends are reported in different units, annual percentage change for total abundance and individuals yr⁻¹ for the series excluding Dunlin, which makes their magnitudes difficult to compare. Please consider analysing both series using the same approach, or at least reporting the results in comparable units.

Answer 2.  We agree. Since total abundance excluding Dunlin is also a count-based annual time series, we re-analysed this series using TRIM, applying the same settings used for total abundance, species-level counts and eco-functional guild totals. The revised text now reports both trends in the same units, as annual percentage change. Total abundance was classified as a moderate increase (+3.5% yr⁻¹), and total abundance excluding Dunlin was also classified as a moderate increase (+6.2% yr⁻¹, p < 0.01). We updated Section 2.4, Section 3.2 and Table 1 accordingly.

Comment 3. In Figure 2d, Dunlin proportion and Berger–Parker dominance appear to overlap almost completely. If Dunlin was the most abundant species in every year, these two metrics are mathematically equivalent, because the Berger–Parker index is the proportional abundance of the most abundant species. In that case, plotting both curves may confuse readers. I suggest explicitly stating in the caption/text that Berger–Parker dominance is equivalent to Dunlin proportional abundance because Dunlin was consistently the dominant species.

Answer 3. We agree. Because Dunlin was the most abundant species in every sampled winter, the Berger–Parker dominance index is mathematically equivalent to Dunlin proportional abundance in this dataset. We now state this explicitly in the Figure 2 caption and in the relevant Results text, to avoid any possible confusion.

Comment 4. Adding group ellipses to Figure 3 could improve readability, but this is optional. If included, the caption should define what the ellipses represent, and the interpretation should remain based on the PERMANOVA results.

Answer 4. We considered this suggestion but chose not to add ellipses, in order to avoid over-emphasizing visual grouping in an ordination plot with a relatively small number of annual points per period. The interpretation remains based on the PERMANOVA results, as recommended by the reviewer.

Comment 5.  I noticed that several annual change estimates in revised Table 1 differ from those in the previous version of the manuscript. This may simply reflect recalculation or correction during revision, but it would be helpful if the authors clarified this, especially where the revised values affect the interpretation of species-level or guild-level trends.

Answer 5. We clarified the issue by ensuring that Table 1 reports the final TRIM results consistently for the dataset used in the revised manuscript, i.e. 1993–2022 excluding 2021, with the species-level analyses restricted to species recorded in at least 10 winters and with the final eco-functional guild assignments. The recalculated values do not alter the main interpretation: increasing trends remain prevalent, three species show moderate declines, one species is stable and five are uncertain. We also added the new TRIM row for total abundance excluding Dunlin, so that this series is reported consistently with total abundance and the guild-level trends.

Comment 6. Figure numbering should be checked. The manuscript currently appears to label both the macro-area figure and the CTI figure as Figure 6.

Answer 6.  Corrected. The macro-area figure remains Figure 6, and the CTI figure has been renumbered as Figure 7.

Reviewer 2 Report

Comments and Suggestions for Authors

The authors have made a substantial effort to address the concerns raised during the previous review. The manuscript has been significantly strengthened through additional analyses, clearer methodological descriptions, and a more balanced interpretation of the results. In particular, the inclusion of community diversity metrics, Bray-Curtis/PERMANOVA analyses, expanded CTI sensitivity analyses, and revised spatial analyses has considerably improved the scientific rigour of the study.

Overall, I appreciate the authors' thorough revision and believe the manuscript is now suitable for publication. 

Author Response

Comment 1. The authors have made a substantial effort to address the concerns raised during the previous review. The manuscript has been significantly strengthened through additional analyses, clearer methodological descriptions, and a more balanced interpretation of the results. In particular, the inclusion of community diversity metrics, Bray-Curtis/PERMANOVA analyses, expanded CTI sensitivity analyses, and revised spatial analyses has considerably improved the scientific rigour of the study. Overall, I appreciate the authors' thorough revision and believe the manuscript is now suitable for publication. 

Answer. We thank Ref. 2 for his kind comment.