Review Reports

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Reviewer Report for Manuscript ID: Conservation-3945817

Summary of the manuscript

The study examines winter bat mortality in Bulgaria and the demographic structure of deceased individuals from one of Europe’s largest bat colonies. It addresses a critical aspect of bat ecology and provides valuable information on population dynamics, seasonal mortality patterns, and potential conservation concerns. The study combines long-term monitoring data with demographic analyses, offering important insights into chiropteran ecology and wildlife conservation. Overall, the manuscript presents a well-structured dataset and thoughtful analysis. However, several aspects of the study require clarification and improvement before the manuscript can be considered for publication.

Evaluation of the methodology, analyses, and conclusions

Major comments

The monitoring period (1 December to 31 March, 2003–2023) and the sampled habitat gradient along the 2.5 km tunnel are adequate to support robust conclusions. However, the relatively small number of carcass samples collected over February–March 2022 (n = 40) may be seen as a limitation. Clearly explaining the rationale for sampling only 40 individuals within this one-year period, either in the Materials and Methods or the Discussion, would help address potential concerns regarding the study’s robustness.

The Discussion section provides clear interpretations of the results. However, it could be strengthened by adding an additional paragraph that highlights the broader implications of the findings, acknowledges the study limitations, and suggests priorities for future research to further enhance the impact and relevance of the study.

The Conclusions section presently reads more as a set of suggestions rather than a synthesis of the main outcomes of the study. It should be restructured to align with the essential elements of a strong conclusion, summarizing key findings, emphasizing their scientific significance, and providing a concise reflection on the study’s overall contribution to the field.

Specific comments

L10 The term “K-selected species” is quite technical for an abstract. Consider briefly defining or contextualizing it upon first mention (e.g., species characterized by slower growth, lower reproductive rates, and greater competitive ability) to improve clarity and accessibility for a broader readership.

L136–L143 All species names should be italicized to maintain proper scientific formatting and consistency with taxonomic conventions.

Figs. 1, 3, and 4 Please standardize the font size across all figures, ensuring it is at least 8 pt for readability.

English language and clarity

The English could be improved to more clearly express the research.

Ethical considerations

No ethical concerns related to the experimental procedures or data collection. There is no indication of undisclosed conflicts of interest or plagiarism. However, I recommend that the authors address the concerns regarding clarity. Addressing this issue is essential to enhance the scientific rigor, coherence, and reproducibility of the manuscript before it can proceed further in the review process.

Constructive feedback for the authors and areas for improvement

1. Provide a clear rationale for sampling.
2. Expand the Discussion to include broader ecological and conservation implications, study limitations, and priorities for future research.
3. Restructure the Conclusions to summarize key findings, emphasize scientific significance, and reflect on the study’s overall contribution.
4. Define technical terms when first mentioned in the Abstract for clarity.
5. Italicize all species names to comply with scientific formatting conventions.
6. Improve English throughout the manuscript for clarity, conciseness, and readability.

Comments on the Quality of English Language

The English could be improved to more clearly express the research.

Author Response

We sincerely thank the reviewer for their thoughtful, constructive, and detailed feedback. Their suggestions have greatly helped us improve the clarity, structure, and scientific rigor of the manuscript. We have addressed each point carefully, and our responses to all comments are provided below.

Comment 1: The monitoring period (1 December to 31 March, 2003–2023) and the sampled habitat gradient along the 2.5 km tunnel are adequate to support robust conclusions. However, the relatively small number of carcass samples collected over February–March 2022 (n = 40) may be seen as a limitation. Clearly explaining the rationale for sampling only 40 individuals within this one-year period, either in the Materials and Methods or the Discussion, would help address potential concerns regarding the study’s robustness.

Response 1: Thank you for this important comment, which helped us clarify the missing six samples. We have now specified that six carcasses were excluded due to poor preservation or missing teeth, resulting in a final sample size of 34. Carcasses were collected opportunistically, based solely on what was naturally present, and no animals were captured or euthanised for this study. Therefore, the sample size reflects the number of carcasses that were visible and accessible during the survey period, rather than a predefined or targeted sampling effort.

Comment 2: The Discussion section provides clear interpretations of the results. However, it could be strengthened by adding an additional paragraph that highlights the broader implications of the findings, acknowledges the study limitations, and suggests priorities for future research to further enhance the impact and relevance of the study.

Response 2: Thank you for this comment. We agree that highlighting broader implications, limitations, and future research priorities is essential. These aspects are already addressed in the Discussion (lines 246–260), which is intentionally structured around our main conclusion — that winter bat mortality remains poorly quantified due to non-standardised monitoring and a lack of systematic carcass recovery. Throughout this section, we emphasise that the key barrier to advancing knowledge is not a lack of biological relevance, but a lack of comparable and standardized mortality data, and we outline clear recommendations to address this. We therefore did not add a new paragraph but believe these points are sufficiently covered.

Comment 3: The Conclusions section presently reads more as a set of suggestions rather than a synthesis of the main outcomes of the study. It should be restructured to align with the essential elements of a strong conclusion, summarizing key findings, emphasizing their scientific significance, and providing a concise reflection on the study’s overall contribution to the field.

Response 3: Thank you for this comment. We agree that the Conclusions should prioritise the main outcomes and scientific contribution of the study. We have now revised the Conclusions section to clearly summarise the key findings, including (i) that substantial winter mortality events are rare but likely under-detected, (ii) that younger Miniopterus schreibersii represent the most affected age group, indicating early-life mortality as an important demographic filter, and (iii) that detection bias driven by site-specific carcass persistence limits current mortality estimates. The revised text now emphasises the study’s contribution to understanding winter bat mortality and frames the knowledge gaps as core findings, rather than suggestions.

Comment 4: L10 The term “K-selected species” is quite technical for an abstract. Consider briefly defining or contextualizing it upon first mention (e.g., species characterized by slower growth, lower reproductive rates, and greater competitive ability) to improve clarity and accessibility for a broader readership.

Response 4: Thank you for this suggestion. We agree that the term K-selected species may be overly technical in an abstract. We have revised the sentence to improve clarity and accessibility by using more widely understood terminology. The updated sentence now reads: “Understanding the drivers of population dynamics in long-lived, slow-reproducing species such as bats is critical for conservation, particularly during vulnerable life-history stages like hibernation.”

Comment 5: L136–L143 All species names should be italicized to maintain proper scientific formatting and consistency with taxonomic conventions.

Response 5: Thank you for noting this. We have now ensured that all species names in the manuscript are italicised.

Comment 6: Figs. 1, 3, and 4 Please standardize the font size across all figures, ensuring it is at least 8 pt for readability.

Response 6: Thank you for this suggestion. We have standardised the font size across Figs. 1, 3, and 4, ensuring that all text is now at least 8 pt for improved readability and consistency.

Comment 7:No ethical concerns related to the experimental procedures or data collection. There is no indication of undisclosed conflicts of interest or plagiarism. However, I recommend that the authors address the concerns regarding clarity. Addressing this issue is essential to enhance the scientific rigor, coherence, and reproducibility of the manuscript before it can proceed further in the review process.

Response 7: Thank you for this comment. We have now expanded the Ethical Considerations section to improve clarity and transparency. We added the following statement to the manuscript:

“Institutional Review Board Statement: The bat survey was conducted following all relevant ethical guidelines to ensure minimal disturbance to the animals and their environment. Carcasses were collected under a permit issued by the Bulgarian Biodiversity Act (No 830/19.09.2020), which authorizes the collection of deceased individuals for scientific research purposes and for inclusion in museum collections. Ethical review and approval were waived for this study due to compliance with the national legal framework (Bulgarian Biodiversity Act, Articles 49(1) and 58(1)), which governs the handling of protected species for scientific purposes under official permit.”

We believe this revision clearly outlines the legal and ethical framework under which the work was conducted and addresses the reviewer’s concern.

Comments 8: Constructive feedback for the authors and areas for improvement

1. Provide a clear rationale for sampling.
2. Expand the Discussion to include broader ecological and conservation implications, study limitations, and priorities for future research.
3. Restructure the Conclusions to summarize key findings, emphasize scientific significance, and reflect on the study’s overall contribution.
4. Define technical terms when first mentioned in the Abstract for clarity.
5. Italicize all species names to comply with scientific formatting conventions.
6. Improve English throughout the manuscript for clarity, conciseness, and readability.

 

Comments on the Quality of English Language

The English could be improved to more clearly express the research.

Response 8: Thank you for the recommendations.
We have now addressed each point individually in the manuscript and in our detailed point-by-point responses. Furthermore, the entire manuscript has been revised for clarity, grammar, and readability. Final language improvements and proofreading were completed with the assistance of a native English speaker (Ms Ian Bradley), and we believe the revised version is now substantially clearer and more concise.

Reviewer 2 Report

Comments and Suggestions for Authors

This manuscript assembles winter bat‐mortality observations from >109 Bulgarian hibernacula (1991–2023) to describe where and when unusual mortality events occur, explores “hibernation preferences” (altitude, temperature, humidity) across species, and presents an age profile of Miniopterus schreibersii carcasses from the large Parnicite colony following winter 2022 events. Its strongest contributions are the consolidation of disparate monitoring records into a single descriptive baseline for Bulgaria, the explicit acknowledgement of detection/effort heterogeneity and scavenger bias in caves, and the attempt to pair national collation with a worked demographic vignette using dentine layers. Together these provide a useful starting point for standardized surveillance and hypothesis generation in a region with historically patchy reporting.

As framed, however, the central construct that organises the paper, what qualifies as a mortality “event”, is unstable across sections, and this instability propagates into every claim about rarity and distribution. The Abstract defines “significant die-offs” as more than 30 individuals from at least three species, the Methods operationalise unusual mortality events as more than seven individuals following Fritze and Puechmaille, Figure 3 labels UMEs as “>7 carcasses,” and the Discussion returns to “mass die-offs” exceeding 30 individuals. Because the threshold governs case inclusion, these shifts blur the paper’s core question and make the frequency statements non-comparable across the text. There is a need to adopt a single, literature-anchored definition and recalculate all tallies and figures accordingly before broader interpretation can be persuasive.

A related structural issue is the tension between the national scope promised and the evidence ultimately analysed. The Methods highlight more than 109 sites visited over three decades, yet the empirical backbone of the narrative concentrates on a small subset of frequently visited caves, with survey periodicity varying markedly among sites. Table 1 documents this heterogeneity which by itself warrants effort standardisation before inferring spatial patterns or site specificity. As presented, counts are not expressed as rates and do not include effort or colony-size offsets, so apparent differences among sites and years may be sampling artefacts. For a conservation journal readership, the results would be far more interpretable if mortality were reported as effort-adjusted rates and modelled with site and year as random effects.

The paper also reaches for causal language without yet providing the necessary analytical bridge. The Discussion links the concentration of events to the prolonged cold snaps of winter 2012 and situates this within a broader European context, but no temperature anomaly series, microclimate time series, or formal models are brought to bear. If the argument is that extreme winters drive die-offs, then integrating weather or microclimate covariates into effort- and size-adjusted models is the natural next step.

On reproducibility and transparency, the narrative sends mixed signals. The Methods state that the backbone dataset is openly available via GBIF and that data management and statistical analyses were performed in R, suggesting a replicable workflow. The Data Availability Statement, however, indicates that raw survey data are available only upon request.

The demographic case study is a valuable idea yet presently over-interpreted. Forty carcasses were collected from the water surface at Parnicite, thirty-four were aged, and the age distribution is described as skewing young. Because carcasses came from water, recovery is likely biased toward individuals that float or persist; the six unanalyzed specimens are not explained. The Introduction presents dentine increments as a robust method, while the Discussion acknowledges uncertainty due to line clarity, non-annual increments, and under- or over-counting. Given these constraints, the case would be stronger if ages were analysed in coarse classes (first-year versus older), inter-observer agreement were reported explicitly, and any claim of “younger predominance” were framed as a descriptive pattern rather than evidence of differential vulnerability. Ideally, the authors would pair carcass ages with an independent reference before advancing demographic interpretations.

Finally, some presentation choices undermine confidence in cross-species comparisons and should be corrected in any revision. The “hibernation preferences” figure does not explain how species-level means were computed across mixed roosts and uneven visit schedules, nor does it define the categorical “humidity type,” and the legend  seems to contain a taxonomic code mismatch.

Specific comments:

• Abstract. The event threshold “significant die-offs (>30 individuals from at least three species)” conflicts with the UME definition used elsewhere and with Fig. 3. Please pick one threshold and harmonize the entire manuscript and calculations

• Materials & Methods—Hibernacula survey. You define UMEs; >7 individuals yet note that “systematic recording was inconsistent.” Given the uneven survey periodicity in Table 1, present mortality as effort-standardized rates and specify the planned model structure rather than only stating that analyses were “performed in R.” 

• Table 1 (Survey effort). The strong variation in visit frequency among key caves demands effort correction before comparing sites/years; please include an effort table per site × year and use it quantitatively

• Results/Figure 3. The caption states “UMEs, >7 carcasses”, which is inconsistent with the “mass die-offs >30” language in the Discussion. Harmonize definitions and re-tabulate event counts if necessary

• Results. You report that the majority of UMEs were concentrated in winter 2012. Move beyond narrative by testing this against anomaly data (regional temperatures, cave microclimate) in a GLMM with site/year random effects and effort/colony-size offsets. 

• Figure 4 (Hibernacula preferences). The legend contains a taxonomic/code mismatch (“Rhip = Nyctalus noctula”). Correct species codes and define “humidity type.” Also specify how means were computed across mixed-species roosts and unequal sampling (per-visit vs per-site vs per-species weighting). 

• Parnicite case study (Methods/Results). You state a colony size of ~53,468 and that 40 carcasses were collected from water, of which 34 were aged. Please justify the six exclusions, quantify recovery bias from water surfaces, and scale counts to proportional mortality with uncertainty. Consider reporting ages in coarse classes with inter-observer agreement.

• Ageing method. The Introduction frames dentine layers as “robust,” whereas the Discussion details substantial uncertainty (non-annual increments, ring merging, under/over-counts). Align these sections by tempering Intro claims and/or adding a validation subset (replicate teeth, known-age checks, or epigenetic benchmarks).

• Reference list. The bibliography includes duplicated entries for Brunet-Rossinni & Austad (2004) and order references alphabetically

Author Response

Comment 1: As framed, however, the central construct that organises the paper, what qualifies as a mortality “event”, is unstable across sections, and this instability propagates into every claim about rarity and distribution. The Abstract defines “significant die-offs” as more than 30 individuals from at least three species, the Methods operationalise unusual mortality events as more than seven individuals following Fritze and Puechmaille, Figure 3 labels UMEs as “>7 carcasses,” and the Discussion returns to “mass die-offs” exceeding 30 individuals. Because the threshold governs case inclusion, these shifts blur the paper’s core question and make the frequency statements non-comparable across the text. There is a need to adopt a single, literature-anchored definition and recalculate all tallies and figures accordingly before broader interpretation can be persuasive.

Response 1: Thank you for this important observation. We agree that the definition of a mortality “event” must be consistent throughout the manuscript to avoid ambiguity and ensure comparability. We have now adopted a single, literature-anchored definition based on Fritze & Puechmaille (2023), which defines Unusual Mortality Events (UMEs) as occurrences involving ≥7 carcasses. This threshold is biologically meaningful and alredy used in bat mortality assessments.

Accordingly: The Abstract, Methods, Results, and Discussion have all been revised to consistently use ≥7 individuals as the definition of a mortality event. References to “significant die-offs” and “mass die-offs (>30 individuals)” have been removed or rephrased for consistency. Figures and tables (including Figure 3) have been updated to reflect this unified definition. We thank the reviewer for highlighting this point — the manuscript is now clearer, conceptually consistent, and better aligned with current literature.

 

Comment 2: A related structural issue is the tension between the national scope promised and the evidence ultimately analysed. The Methods highlight more than 109 sites visited over three decades, yet the empirical backbone of the narrative concentrates on a small subset of frequently visited caves, with survey periodicity varying markedly among sites. Table 1 documents this heterogeneity which by itself warrants effort standardisation before inferring spatial patterns or site specificity. As presented, counts are not expressed as rates and do not include effort or colony-size offsets, so apparent differences among sites and years may be sampling artefacts. For a conservation journal readership, the results would be far more interpretable if mortality were reported as effort-adjusted rates and modelled with site and year as random effects.

Response 2: We thank the reviewer for this important methodological observation. We agree that effort-adjusted mortality rates and site/year modelling would strengthen inference if the underlying data were collected within a standardized and consistent monitoring framework. However, this study specifically highlights that such a framework has not yet existed for long-term winter bat monitoring in Bulgaria.

Systematic national monitoring of bats began only around 1997, coinciding with the start of sustained bat research in the country. Prior to this, data originated exclusively from individual scientific projects. Even after 1997, monitoring has not been conducted annually and has remained highly dependent on project-based funding, researcher availability, and volunteer capacity, rather than a coordinated long-term survey design. As a result, survey effort, detection probability, and site coverage vary strongly among years, and absence of counts often reflects lack of survey effort rather than lack of mortality or bats.

The higher temporal coverage for a subset of caves reflects their recognised importance: these sites are among the most significant bat hibernacula in Europe, and were therefore prioritised for monitoring whenever funding or field personnel were available. Thus, uneven sampling intensity is not a bias in site selection, but a consequence of conservation prioritisation under resource limitations.

Given these constraints, we conclude that converting counts into standardised mortality rates or fitting site/year mixed-effects models would require assumptions that cannot be justified with the existing data structure and would risk producing highly speculative results. Instead, we now explicitly clarify in the manuscript that:

• data heterogeneity precludes reliable effort-standardised modelling at present,
  
  
• comparisons across sites or years must be interpreted cautiously,
  
  
• and the absence of standardised effort itself represents a key finding that underpins our main recommendation — the urgent need for harmonised national mortality monitoring protocols.
  
  

We believe this framing appropriately reflects both the limitations and the conservation relevance of the dataset, while reinforcing the core contribution of our study: identifying the gaps that must be addressed to enable robust demographic modelling in the future.

 

Comment 3: The paper also reaches for causal language without yet providing the necessary analytical bridge. The Discussion links the concentration of events to the prolonged cold snaps of winter 2012 and situates this within a broader European context, but no temperature anomaly series, microclimate time series, or formal models are brought to bear. If the argument is that extreme winters drive die-offs, then integrating weather or microclimate covariates into effort- and size-adjusted models is the natural next step.

Response 3: Thank you for this important and constructive comment. The possibility that extreme winter conditions, particularly prolonged cold snaps, may contribute to mortality was raised early on as a working hypothesis, including within the field monitoring reports collected during the mortality events themselves. These observations suggested cold stress as a potential driver. However, we currently lack temporally matched, high-resolution microclimate or weather records for the key mortality years (2012 and 2022). Mortality events are also extremely sparse and irregularly recorded across sites, which precludes a statistically robust or causal analysis at this stage. Under these limitations, any formal model would be highly speculative. To provide some environmental context for this response, we extracted ERA5 reanalysis temperature data for each cave entrance and examined cold-snap frequency. This figure is included only for the reviewer’s reference and is not part of the revised manuscript. The ERA5 data show that similarly severe or colder winters occurred in other years without recorded mortality, indicating that a direct quantitative link cannot be meaningfully established with the current dataset. 

 

We fully agree with the reviewer that integrating weather and microclimate covariates into effort- and size-adjusted mortality models is the logical next step. This remains a clear goal for future work, once continuous microclimate monitoring and systematic mortality records become available. We appreciate the reviewer’s suggestion and have emphasised this point in the revised Discussion as an important future research direction.

Comment 4: On reproducibility and transparency, the narrative sends mixed signals. The Methods state that the backbone dataset is openly available via GBIF and that data management and statistical analyses were performed in R, suggesting a replicable workflow. The Data Availability Statement, however, indicates that raw survey data are available only upon request.

Response 4: We appreciate the reviewer’s comment. To enhance transparency, we have added a supplementary dataset that includes all winter monitoring records used in this study, complementing the GBIF backbone dataset and enabling full reproducibility of the analyses.

Comment 5: The demographic case study is a valuable idea yet presently over-interpreted. Forty carcasses were collected from the water surface at Parnicite, thirty-four were aged, and the age distribution is described as skewing young. Because carcasses came from water, recovery is likely biased toward individuals that float or persist; the six unanalyzed specimens are not explained. The Introduction presents dentine increments as a robust method, while the Discussion acknowledges uncertainty due to line clarity, non-annual increments, and under- or over-counting. Given these constraints, the case would be stronger if ages were analysed in coarse classes (first-year versus older), inter-observer agreement were reported explicitly, and any claim of “younger predominance” were framed as a descriptive pattern rather than evidence of differential vulnerability. Ideally, the authors would pair carcass ages with an independent reference before advancing demographic interpretations.

Response 5: We thank the reviewer for this thoughtful comment and for highlighting potential sources of bias in carcass recovery. In this case, we consider it unlikely that the location of carcasses (collected from the water surface) introduced a demographic bias. The affected colony at Parnicite is extremely compact (see photo below), occupying a single chamber with no known spatial segregation by age class, and carcasses were recovered from directly beneath the main roosting cluster. Under these conditions, differences in buoyancy or persistence are unlikely to have systematically affected age composition. The six specimens that could not be aged were too decomposed to yield reliable dentine readings and were therefore excluded to avoid misclassification. We have clarified this information in the revised Methods. Going further with the comment, we thank the reviewer for this constructive and insightful idea. We fully agree that presenting ages in defined classes provides a clearer and more transparent framework given the limitations of dentine increment interpretation. In the revised version, we have reanalysed the data using four biologically meaningful age categories—juvenile, subadult, adult, and advanced adult—which reflect distinct stages of behavioural experience and physiological preparedness for hibernation. This approach strengthens the demographic interpretation while avoiding over-reliance on fine-scale age estimates. We have also clarified in the text that age distributions are presented descriptively rather than as evidence of differential vulnerability. We appreciate the reviewer’s suggestion, which has substantially improved both the clarity and biological relevance of the analysis.

Comment 6: Finally, some presentation choices undermine confidence in cross-species comparisons and should be corrected in any revision. The “hibernation preferences” figure does not explain how species-level means were computed across mixed roosts and uneven visit schedules, nor does it define the categorical “humidity type,” and the legend  seems to contain a taxonomic code mismatch.

Response 6: We agree that the original description of Figure 4 needed clarification. We have now (i) explained in the Methods and Figure legend that values in Figure 4A–C are based on roost-level means per species–roost combination (one point per species per roost, so mixed roosts contribute separate observations for each species under shared microclimate), (ii) defined the three categorical “humidity types” (Dry, Humid, Wet) based on field assessments of condensation and free water, and (iii) corrected the legend to use consistent taxonomic group labels, explicitly stating that Myotis myotis and M. blythii were combined as Myotis myotis/blythii and Rhinolophus euryale, R. mehelyi and R. blasii as Rhinolophus media.

Specific comments:

Comment 7: Abstract. The event threshold “significant die-offs (>30 individuals from at least three species)” conflicts with the UME definition used elsewhere and with Fig. 3. Please pick one threshold and harmonize the entire manuscript and calculations
Response 7: Thank you for pointing this out. We have now adopted a single, literature-based definition of Unusual Mortality Events (UMEs) following Fritze & Puechmaille (2023), i.e. events with ≥7 carcasses. The Abstract, Methods, Results, Discussion, and Figure 3 (including all tallies) have been revised accordingly, and all references to “significant die-offs” or “mass die-offs (>30 individuals)” have been removed or rephrased to maintain full consistency.

Comment 8: Materials & Methods—Hibernacula survey. You define UMEs; >7 individuals yet note that “systematic recording was inconsistent.” Given the uneven survey periodicity in Table 1, present mortality as effort-standardized rates and specify the planned model structure rather than only stating that analyses were “performed in R.”  

Response 8: We agree that effort-standardised mortality rates and explicit model structures would be ideal under a standardised monitoring design. However, as clarified in the revised Methods, survey effort and site coverage were highly uneven and driven by project availability rather than a fixed sampling scheme, meaning that absences often reflect no survey rather than no mortality. Under these conditions, converting counts to formal rates or fitting effort- and colony-size–offset models would require assumptions we cannot justify. We have therefore (i) explicitly described these limitations in the Methods, (ii) stated that our comparisons are descriptive and exploratory, and (iii) emphasised that the absence of standardised effort itself is a key result motivating our recommendation for harmonised national monitoring.

Comment 9: Table 1 (Survey effort). The strong variation in visit frequency among key caves demands effort correction before comparing sites/years; please include an effort table per site × year and use it quantitatively
Response 9: We have expanded the survey effort information by adding a supplementary table that lists, for each site × year, whether winter surveys were conducted and how many visits occurred. As noted above, the strong heterogeneity and gaps in effort preclude robust quantitative effort-correction or rate modelling. We therefore use this table to transparently document effort patterns and explicitly caution readers that among-site and among-year comparisons are exploratory and should be interpreted in light of these constraints.

Comment 10: Results/Figure 3. The caption states “UMEs, >7 carcasses”, which is inconsistent with the “mass die-offs >30” language in the Discussion. Harmonize definitions and re-tabulate event counts if necessary

Response 10:  We have harmonised the definition of mortality events across the entire manuscript using the ≥7-carcass UME threshold. Figure 3 and its caption have been updated accordingly, and all event counts have been recalculated under this unified definition. The Discussion no longer uses the “mass die-offs >30” wording but refers consistently to UMEs as defined in the Methods.

Comment 11:Results. You report that the majority of UMEs were concentrated in winter 2012. Move beyond narrative by testing this against anomaly data (regional temperatures, cave microclimate) in a GLMM with site/year random effects and effort/colony-size offsets. 

Response 11: We fully agree that linking UMEs to temperature anomalies via formal models is the logical next step. However, we currently lack continuous microclimate records for the caves and have only sparse, irregular mortality detections across sites and years, making effort- and size-adjusted GLMMs statistically unstable and highly assumption-dependent. We have therefore refrained from fitting such models and instead now explicitly frame the 2012 concentration as a descriptive pattern. In the revised Discussion, we highlight the integration of weather and microclimate covariates into effort- and size-adjusted mortality models as a key priority for future work once appropriate data become available.

Comment 12: Figure 4 (Hibernacula preferences). The legend contains a taxonomic/code mismatch (“Rhip = Nyctalus noctula”). Correct species codes and define “humidity type.” Also specify how means were computed across mixed-species roosts and unequal sampling (per-visit vs per-site vs per-species weighting). 

Response 12: We appreciate this comment. In the revised Figure 4 and legend, we have (i) corrected the taxonomic code mismatch and use consistent species group labels throughout, explicitly stating that Myotis myotis and M. blythii were combined as Myotis myotis/blythii and Rhinolophus euryale, R. mehelyi and R. blasii as Rhinolophus media; (ii) defined “humidity type” (Dry, Humid, Wet) based on field assessments of condensation and free water; and (iii) clarified that values in panels A–C are based on roost-level means per species–roost combination (one point per species per roost, so mixed roosts contribute separate observations under shared microclimate). This procedure is also described in the Methods.

Comment 13: Parnicite case study (Methods/Results). You state a colony size of ~53,468 and that 40 carcasses were collected from water, of which 34 were aged. Please justify the six exclusions, quantify recovery bias from water surfaces, and scale counts to proportional mortality with uncertainty. Consider reporting ages in coarse classes with inter-observer agreement.

Response 13: We thank the reviewer for these suggestions. In the revised Methods, we now state that six carcasses were excluded because decomposition or damage prevented reliable dentine readings. We discuss potential recovery bias from water surfaces and explain that, given the extremely compact, single-chamber colony with no known spatial age segregation, we consider systematic demographic bias in floating carcasses unlikely. We now present mortality at Parnicite as a minimum proportional mortality relative to the estimated colony size and report binomial confidence intervals in the Results. Following the reviewer’s recommendation, ages are analysed in four broad classes (juvenile, subadult, adult, advanced adult), and we emphasise that age patterns are interpreted descriptively rather than as definitive evidence of differential vulnerability.

Comment 14: Ageing method. The Introduction frames dentine layers as “robust,” whereas the Discussion details substantial uncertainty (non-annual increments, ring merging, under/over-counts). Align these sections by tempering Intro claims and/or adding a validation subset (replicate teeth, known-age checks, or epigenetic benchmarks).

Response 14: We agree that the Introduction overstated the robustness of dentine increment ageing. We have revised the wording to describe dentine layers as a widely used but imperfect method, explicitly noting known sources of uncertainty and referring forward to the methodological caveats discussed later. We do not currently have an independent validation dataset (e.g. known-age individuals or epigenetic benchmarks), and we now state this explicitly. Throughout the Results and Discussion, we have toned down causal language and stress that age estimates and age-structure patterns should be interpreted cautiously.

Comment 15: Reference list. The bibliography includes duplicated entries for Brunet-Rossinni & Austad (2004) and order references alphabetically

Response 15: Thank you for noting this. The duplicate entries have now been removed. Regarding the order of references, the manuscript uses numbered in-text citations, and according to standard journal formatting, this requires the reference list to appear in numerical order, not alphabetical order. We therefore retained numerical ordering in the bibliography, following the journal’s citation style guidelines. We hope the reviewer agrees, and we remain happy to adjust if the editorial office requires otherwise.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

All comments have been addressed, and now the manuscript is in good shape. I recommend acceptance for publication.

Author Response

Comment: All comments have been addressed, and the manuscript is now in good shape. Acceptance is recommended.
Response: We are very pleased that the reviewer is satisfied with the revised manuscript, and we are grateful for his thoughtful and constructive contributions throughout the review process.

Reviewer 2 Report

Comments and Suggestions for Authors

The revised manuscript shows that the authors have taken the earlier review seriously and have made genuine progress on several central issues. The adoption of a literature-sound definition of an Unusual Mortality Event, the explicit acknowledgement of the opportunistic nature of the monitoring data, the more treatment of the 2012 cold winter, and the re-framing of the Parnicite case study as a minimum, descriptive demographic snapshot all move the paper in the right direction. Conceptually, the response letter is thoughtful and the main scientific concerns have been heard. Unfortunately, the manuscript in its present form does not yet fully embody these improvements, both because many structural problems remain and because several important claims are still insufficiently supported by the relevant literature.

As previously noted, the core issue of definitional consistency is not fully resolved in the text. While the Methods and the updated caption for Figure 3 correctly implement the ≥7-carcass UME threshold, the Abstract and parts of the Discussion still contain hybrid formulations that juxtapose remnants of the former “>30 individuals from at least three species” definition with the new terminology, and even give conflicting numbers of sites and species. This muddles what should be a clean conceptual pivot and will confuse readers about what is actually being counted. The same lack of follow-through affects other sections as the Methods still repeat information on data management, with two different versions of the R software and awkward, stitched sentences, then the Discussion paragraphs around winter 2012 are contined  half-deleted clauses and duplicated linkers. The section numbering is corrupted, and two different captions for Figure 4 appear consecutively, one of them still containing the original taxonomic mismatch and vague references to “humidity type”. These artefacts give the impression of an unfinished draft and, more importantly, make it unnecessarily hard to follow the logic of what is otherwise a useful dataset.

Against this background, the treatment of the literature also needs attention. In several places the manuscript puts considerable interpretative weight on statements that are currently unsupported or only weakly referenced. The early part of the Introduction, where you frame winter mortality in long-lived, K-selected bats as a key demographic bottleneck and hint at cumulative pressures from climate, land-use change and infrastructure, should be more firmly anchored in the substantial bat-ecology and road-ecology literature, as several of your central arguments concern the long-term persistence of bat populations and the limited ability of small, isolated colonies to recover from repeated die-offs, directly connecting anthropogenic pressures to population viability in bats. ( e.g., doi: https://doi.org/10.1016/j.scitotenv.2023.161705 ; https://doi.org/10.1111/mam.12064). Likewise, when you present national-scale winter monitoring as patchy, project-driven and lacking standardization, it would be appropriate to reference existing European monitoring frameworks and UME concepts, rather than leaving the reader to infer that this situation is unique to Bulgaria. Later, in the Discussion, several important claims about the demographic consequences of repeated winter die-offs in small populations, the interaction between severe winters and other anthropogenic stressors, and the likely lag between demographic and genetic signals are articulated as general truths but only lightly sourced. These are precisely the sections where you could draw more systematically on the growing literature on climate-linked die-offs, demographic buffering in bats, and time-lags in genetic responses to barriers.

There are other points where additional referencing would strengthen the argument without overburdening the text. The section in which you describe national monitoring as beginning around 1997 and being historically opportunistic could be linked to documentation of the Bulgarian bat-research context or to broader discussions of opportunistic versus standardized biodiversity monitoring. In the Conclusions, where you present winter mortality events as “sentinel” phenomena that highlight both the vulnerability of bat populations and the gaps in national monitoring, it would be valuable to anchor this language in the existing UME or sentinel-species literature. These additions need not be exhaustive, but they would shift several important paragraphs from plausible but impressionistic narrative to properly referenced scientific argument.

Returning to the structural issues, my overall impression remains that the scientific core of the paper is sound and that the responses to review are, in substance, acceptable. However, the text still contains extensive traces of uncleaned track changes, duplicated and contradictory formulations, inconsistent terminology, and an unfinished reference list (including duplicated entries and manual renumbering artifacts). These problems are sufficiently pervasive that they obscure the message, and they are compounded by the under-use of key references and the complete omission of a highly pertinent recent study. I would therefore encourage the authors to undertake a further round of revision that is less about new analyses and more about cleaning the prose, enforcing consistency in definitions and figure captions, harmonizing section numbering and references, and, crucially, reinforcing the main interpretative steps with a more systematic and up-to-date engagement with the literature.

Comments on the Quality of English Language

Sufficient

Author Response

We thank the reviewer sincerely for the detailed, constructive, and insightful comments. The manuscript has been substantially improved as a result. We also acknowledge the structural issues present in the earlier draft and have now thoroughly addressed them throughout.

Comment 1: The revised manuscript shows progress, but improvements are not fully embodied because structural problems remain and several claims are insufficiently supported by the literature.
Response 1: We appreciate this assessment. In this revision, we performed a full structural clean-up, corrected all inconsistencies, removed incomplete edits and duplicated phrases, and substantially strengthened the literature base so that all key interpretative statements are now properly supported.

Comment 2: Definitional consistency of UMEs is not resolved; the Abstract and parts of the Discussion still mix the former definition (“>30 individuals from at least three species”) with the new ≥7-carcass threshold, including conflicting site and species counts.
Response 2: The UME definition is now fully consistent across the entire manuscript. All remaining traces of the former definition were removed from the Abstract, Discussion, and other sections. Conflicting numbers have been corrected so that all text and figures now match the ≥7-carcass threshold.

Comment 3: Methods still contain repeated information on data management, references to two different versions of R, and awkward, stitched sentences.
Response 3: The Methods section was completely revised. All redundant information was removed, both R versions consolidated into one accurate reference, and all awkward or fragmented sentences rewritten for clarity and consistency.

Comment 4: Discussion paragraphs around winter 2012 contain half-deleted clauses and duplicated linkers.
Response 4: These paragraphs have been rewritten in full. All partial edits and duplicated transitions have been removed, and the description of winter 2012 is now coherent and complete.

Comment 5: Section numbering is corrupted, and two captions for Figure 4 appear consecutively, one containing a taxonomic mismatch and unclear “humidity type” terminology.
Response 5: Section numbering has been corrected throughout. The Figure 4 captions were merged into a single accurate version, the taxonomy corrected, and vague microclimate terms replaced with precise descriptors.

Comment 6: Several statements are insufficiently referenced; the Introduction needs stronger grounding in bat ecology and road ecology, particularly regarding demographic bottlenecks and cumulative pressures.
Response 6: We expanded the Introduction with the specific references suggested by the reviewer and additional key works on bat life history, demographic sensitivity, and cumulative anthropogenic pressures. This section is now fully supported by current literature.

Comment 7: Claims about national-scale winter monitoring being patchy should reference European monitoring frameworks and UME concepts.
Response 7: We added references to relevant European monitoring frameworks, including EUROBATS, and clarified that historical reliance on opportunistic winter counts is a broader European issue, not unique to Bulgaria.

Comment 8: In the Discussion, claims about repeated winter die-offs, interactions with anthropogenic stressors, and demographic–genetic time-lags are expressed as general truths but lightly sourced.
Response 8: These sections have been strengthened with additional literature. We added citations on demographic buffering, climate-linked die-offs, cumulative stressors, and demographic–genetic time-lags. We also added a dedicated paragraph on demographic vs. genetic lag effects, with new references.

Comment 9: Additional referencing could strengthen the section on the history of Bulgarian bat monitoring and on opportunistic versus standardised biodiversity monitoring.
Response 9: We have incorporated targeted literature that contextualises the historical development of Bulgarian monitoring within broader discussions of opportunistic versus standardised monitoring, improving the grounding of this section.

Comment 10: The Conclusions present winter mortality events as “sentinel” phenomena but require supporting references from UME or sentinel-species literature.
Response 10: We added appropriate references and clarified this argument in the Discussion and Conclusions. The text now anchors the “sentinel” concept in established literature.

Comment 11: The manuscript still contains uncleaned track changes, duplicated formulations, inconsistent terminology, and an unfinished reference list with duplicates and renumbering errors.
Response 11: We carried out a thorough, line-by-line editorial revision. All track-change remnants were removed, terminology harmonised, duplicates eliminated, and the reference list fully corrected and reformatted.

Comment 12: A further revision is encouraged to focus on consistency, prose cleaning, figure caption accuracy, numbering harmonisation, and engagement with up-to-date literature.
Response 12: We followed this recommendation closely. All figure captions and numbering have been corrected, terminology standardised, prose cleaned throughout, and literature engagement strengthened. The revised manuscript now fully reflects the improvements requested.

Round 3

Reviewer 2 Report

Comments and Suggestions for Authors

In this revised version the authors have engaged with the first-round reviews and the manuscript is appreciably clearer and more transparent than the previous version. Nevertheless, a number of structural issues remain, many of them directly linked to points I raised earlier, and these continue to weaken the coherence of the narrative and the strength of the inferences that the reader is invited to draw. My comments below focus on whether the core concerns of my previous review have been substantively addressed and on how the overall structure could be improved.

With respect to the central organising concept of the paper, what qualifies as an “event”, the situation has improved but is not yet fully satisfactory. Within the main text, Methods and Discussion, the authors now adopt a consistent threshold of more than seven carcasses for Unusual Mortality Events, explicitly referencing Fritze and Puechmaille and removing the earlier “mass die-offs >30 individuals” language. This responds directly to my concern about shifting definitions across sections and brings most of the manuscript into alignment. However, the Abstract still describes UMEs as “>7 individuals from at least five species” , introducing a species-richness criterion that is neither justified in the text nor used elsewhere in the analysis. Because the Abstract frames the study for the reader and summarises the tallies, this inconsistency reopens precisely the ambiguity that motivated my original comment. I would strongly encourage the authors to harmonise the Abstract with the Methods and either drop the “five species” condition or, if they truly intend to use it, recalibrate the event counts accordingly and explain the rationale.

A second, more global structural issue concerns the relationship among the three analytical components, notably the national tally of winter mortality events, the roost-level analysis of hibernation preferences, and the Parnicite age-structure case study. The title already signals that the paper is, in effect, built around two pillars  (winter mortality and a demographic study) but the body of the manuscript adds a third, quasi-independent piece on species’ hibernacula preferences. In the Introduction, the authors now state that they “investigate how hibernation preferences may be related to mortality risk” and that this, together with the age structure, will provide insight into the demographic consequences of winter mortality. In the Results and Discussion, however, the hibernation-preference section is purely descriptive, with roost temperature, altitude and water regime and compared among species, and the authors conclude that most bats favour humid caves at lower altitudes, but there is no analysis that actually relates these variables to the occurrence or intensity of mortality events. Indeed, UMEs and non-UME sites are never formally contrasted. The reader is thus left with three interesting analyses that do not fully cohere into a single argument about “drivers of winter mortality”. To make the structure more honest and persuasive, the authors should either provide at least a simple comparison of roost characteristics between mortality and non-mortality sites, or they should explicitly present the roost-preference section as a side result not intended to quantify mortality risk. At present, the aims over-promise and the subsequent sections under-deliver, which creates a structural tension.

The Materials and Methods section is much more detailed than before and now includes the GBIF data source, the Bulgarian Cave Database classification for water regime, and a clear description of species groupings. This is very welcome. Yet the organisation of this section still makes it hard for the reader to see how the different datasets map onto the three strands of analysis. The Hibernacula survey subsection mixes data-source description, ecological variables, species grouping and an extended reflection on effort heterogeneity and European context in a single long passage. The statistical procedures for national UME tallies, roost preferences and age structure are all compressed into a single paragraph in 2.4, even though the Results are naturally organised around those three themes. From a structural perspective, I believe it would be clearer to separate data description from interpretation in 2.1, and to structure 2.4 into distinct paragraphs that mirror the three analyses. Here at first, UMEs tallied and mapped, then roost preferences were summaries and test, and third, age classes and demographic indices computation. Doing so would also make the response to my earlier methodological comments much more transparent.

The authors’ decision not to pursue effort-standardised mortality rates or formal mixed-effects models deserves some comment, as this was a core element of my previous review. In the revised Methods and Discussion, they now explain at length that survey effort was highly uneven, driven by project-based funding and site accessibility, and that absences often reflect missing surveys rather than absence of bats or mortality. On this basis they argue that converting counts to rates or fitting models with effort and colony-size offsets would require untestable assumptions. I appreciate this frank assessment and agree that the heterogeneity is substantial. However, the manuscript still invites readers to interpret counts as if they were rates. For example, the Results state that winter mortality was 'highly species- and site-specific' and that Miniopterus schreibersii experienced the 'most frequent and severe losses' . Without any denominator in terms of total surveys or colony size per site, these statements inevitably blur sampling artefacts with biological patterns. If the authors wish to retain a purely descriptive approach, then the structure of the Results and Discussion should also be clearly and consistently descriptive, avoiding language that implies tested differences in risk. Alternatively, they might explore very simple rate approximations (e.g. carcasses per survey at a given site and year) and present them explicitly as such. At the very least, the opening paragraph of the Results should give the reader a clear denominator (number of roosts, number of winter surveys) so that the rarity of UMEs can be understood in context.

The treatment of climate and the exceptional winter of 2012 illustrates a related structural problem. In my earlier comment, I suggested that if the authors wish to argue that extreme winters drive die-offs, a natural step would be to integrate temperature anomalies or microclimate covariates into effort- and size-adjusted models. They now acknowledge that they lack high-resolution microclimate data and that winters equally or more severe than 2012 occurred without recorded mortality. This is properly noted in the response. In the manuscript, however, the Discussion still moves quite quickly from these caveats to the statement that extreme winters are a likely driver of the observed patterns and that winter 2012 exemplifies this. Since no climatic analysis appears in the Results, the climate narrative remains speculative. 

The Parnicite age-structure case study has been significantly reworked and many of my concrete suggestions have been taken on board. Nevertheless, the main text does not spell out the proportional mortality relative to the estimated colony size, even though both numbers are given, leaving readers to infer the very small absolute fraction of the colony represented by the 34 aged carcasses. In addition, while the Discussion now contains an excellent description of the uncertainties inherent in dentine and cementum ageing and introduces epigenetic clocks as a promising alternative, this cautionary material follows, rather than precedes, a paragraph that states that the age structure of Parnicite, together with external studies, collectively supports early-life mortality as a critical demographic filter in long-lived bats . In other words, the strong demographic conclusion is still presented before the methodological caveats have been fully explained.

In summary, the manuscript has moved in the right direction and several of the earlier weaknesses have been resolved, particularly those relating to the clarity of the roost-preference analysis, data availability and the technical description of the age-determination protocol. The authors’ expanded discussion of monitoring gaps and detection biases is also useful. However, in my opinion the core structural concerns remain only partially addressed. I would therefore recommend a further round of revision focused not so much on adding new analyses, but on tightening the conceptual architecture of the paper, aligning the aims and definitions across sections, moderating claims where the evidence is necessarily descriptive, and rebalancing the Discussion so that methodological limitations are woven directly into the interpretation of results. 

Comments on the Quality of English Language

Sufficient

Author Response

Dear Reviewer,
We sincerely thank you for your thorough and constructive evaluation of our manuscript. Your detailed comments greatly improved the clarity, structure, and interpretative balance of this study. Below, we respond point-by-point and describe all revisions made.

Comment 1: With respect to the central organising concept of the paper, what qualifies as an “event”, the situation has improved but is not yet fully satisfactory. Within the main text, Methods and Discussion, the authors now adopt a consistent threshold of more than seven carcasses for Unusual Mortality Events, explicitly referencing Fritze and Puechmaille and removing the earlier “mass die-offs >30 individuals” language. This responds directly to my concern about shifting definitions across sections and brings most of the manuscript into alignment. However, the Abstract still describes UMEs as “>7 individuals from at least five species” , introducing a species-richness criterion that is neither justified in the text nor used elsewhere in the analysis. Because the Abstract frames the study for the reader and summarises the tallies, this inconsistency reopens precisely the ambiguity that motivated my original comment. I would strongly encourage the authors to harmonise the Abstract with the Methods and either drop the “five species” condition or, if they truly intend to use it, recalibrate the event counts accordingly and explain the rationale.

Response 1: We thank the reviewer for highlighting this inconsistency. We have now harmonised the definition of Unusual Mortality Events throughout the manuscript. The Abstract no longer includes the “five species” criterion; instead, it reports the number of species involved as part of the results, not as part of the definition itself. The definition of UMEs ( >7 individuals, following Fritze & Puechmaille ) is now fully consistent across the Abstract, Methods, Results, and Discussion.

Comment 2: A second, more global structural issue concerns the relationship among the three analytical components, notably the national tally of winter mortality events, the roost-level analysis of hibernation preferences, and the Parnicite age-structure case study. The title already signals that the paper is, in effect, built around two pillars  (winter mortality and a demographic study) but the body of the manuscript adds a third, quasi-independent piece on species’ hibernacula preferences. In the Introduction, the authors now state that they “investigate how hibernation preferences may be related to mortality risk” and that this, together with the age structure, will provide insight into the demographic consequences of winter mortality. In the Results and Discussion, however, the hibernation-preference section is purely descriptive, with roost temperature, altitude and water regime and compared among species, and the authors conclude that most bats favour humid caves at lower altitudes, but there is no analysis that actually relates these variables to the occurrence or intensity of mortality events. Indeed, UMEs and non-UME sites are never formally contrasted. The reader is thus left with three interesting analyses that do not fully cohere into a single argument about “drivers of winter mortality”. To make the structure more honest and persuasive, the authors should either provide at least a simple comparison of roost characteristics between mortality and non-mortality sites, or they should explicitly present the roost-preference section as a side result not intended to quantify mortality risk. At present, the aims over-promise and the subsequent sections under-deliver, which creates a structural tension.

Response 2: We thank the reviewer for this important observation. We have revised the manuscript to clarify the role of the hibernation-preference analysis and to resolve the structural inconsistency identified.

First, in both the Abstract and Introduction, we now explicitly state that the roost-preference analysis is intended to provide ecological context, not to quantify mortality risk. We explain that, due to the very small number of mortality sites and uneven survey coverage, it was not possible to test whether roost characteristics differ between UME and non-UME sites.

Second, we removed any statements implying that hibernation preferences were analysed as predictors of mortality. Instead, we present this section as a descriptive component of the study.

Third, we now emphasise that although this analysis is necessarily descriptive at present, these species-specific environmental preferences will be valuable for future assessments of mortality risk once more systematic mortality data become available. Because one of our aims is to highlight the importance of collecting appropriate winter-mortality data, we believe that documenting baseline hibernation preferences is an essential step toward enabling such analyses in the future.

Finally, we improved the structural flow of the manuscript so that the aims precisely reflect the analyses performed, thereby eliminating the over-promising noted by the reviewer.

Comment 3: The Materials and Methods section is much more detailed than before and now includes the GBIF data source, the Bulgarian Cave Database classification for water regime, and a clear description of species groupings. This is very welcome. Yet the organisation of this section still makes it hard for the reader to see how the different datasets map onto the three strands of analysis. The Hibernacula survey subsection mixes data-source description, ecological variables, species grouping and an extended reflection on effort heterogeneity and European context in a single long passage. The statistical procedures for national UME tallies, roost preferences and age structure are all compressed into a single paragraph in 2.4, even though the Results are naturally organised around those three themes. From a structural perspective, I believe it would be clearer to separate data description from interpretation in 2.1, and to structure 2.4 into distinct paragraphs that mirror the three analyses. Here at first, UMEs were tallied and mapped, then roost preferences were summarised and tested, and third, age classes and demographic indices were computed. Doing so would also make the response to my earlier methodological comments much more transparent.

Response 3: We thank the reviewer for these detailed and constructive suggestions regarding the organisation of the Materials and Methods. In response, we have restructured this section to make the three analytical components clearer and to separate descriptive information from interpretation.

First, we revised subsection 2.1 by renaming it to
“Hibernacula survey and hibernation site characteristics”,
to reflect more accurately that this part of the Methods includes both the long-term monitoring data and the ecological variables (temperature, altitude, water regime) used to summarise species-specific hibernation characteristics. These elements are presented together because they originate from the same monitoring dataset and were collected simultaneously during each winter survey, making them a single, integrated component of the data-collection process. We also removed interpretative sentences concerning survey-effort heterogeneity from this subsection and relocated them to the Discussion, as recommended.

Second, we reorganised subsection 2.4 into three clearly defined analytical components, each now presented under its own heading:

• 2.4.1. Unusual mortality events

• 2.4.2. Species-specific hibernation preferences

• 2.4.3. Age-structure analysis

These new subsections follow the same structure as the Results, making it easier for readers to follow how each dataset maps onto its respective analysis.

Overall, these changes make the Methods section clearer, better aligned with the organisation of the Results, and more transparent with respect to how each dataset contributes to the three strands of analysis.

Comment 4: The authors’ decision not to pursue effort-standardised mortality rates or formal mixed-effects models deserves some comment, as this was a core element of my previous review. In the revised Methods and Discussion, they now explain at length that survey effort was highly uneven, driven by project-based funding and site accessibility, and that absences often reflect missing surveys rather than absence of bats or mortality. On this basis they argue that converting counts to rates or fitting models with effort and colony-size offsets would require untestable assumptions. I appreciate this frank assessment and agree that the heterogeneity is substantial. However, the manuscript still invites readers to interpret counts as if they were rates. For example, the Results state that winter mortality was 'highly species- and site-specific' and that Miniopterus schreibersii experienced the 'most frequent and severe losses' . Without any denominator in terms of total surveys or colony size per site, these statements inevitably blur sampling artefacts with biological patterns. If the authors wish to retain a purely descriptive approach, then the structure of the Results and Discussion should also be clearly and consistently descriptive, avoiding language that implies tested differences in risk. Alternatively, they might explore very simple rate approximations (e.g. carcasses per survey at a given site and year) and present them explicitly as such. At the very least, the opening paragraph of the Results should give the reader a clear denominator (number of roosts, number of winter surveys) so that the rarity of UMEs can be understood in context.

Response 4: We thank the reviewer for raising this important point. First, at the beginning of the Discussion, we now state explicitly that the available data vary greatly in survey frequency across sites and years, and therefore all inferences based on carcass counts should be interpreted descriptively rather than as effort-standardised rates. Second, we removed or rephrased any sentences in the Results and Discussion that could imply tested or quantitative differences in mortality risk among species or sites. The relevant statements now refer to observed patterns only. Third, the methodological explanations relating to uneven effort and its implications were moved from the Methods to the Discussion, where they are now integrated into the interpretation of mortality patterns rather than presented as methodological details. Together, these changes ensure that the manuscript does not unintentionally suggest rate-based or risk-based differences where the data do not support them, and they fully align the interpretation with the descriptive nature of the dataset.

Comment 5: The treatment of climate and the exceptional winter of 2012 illustrates a related structural problem. In my earlier comment, I suggested that if the authors wish to argue that extreme winters drive die-offs, a natural step would be to integrate temperature anomalies or microclimate covariates into effort- and size-adjusted models. They now acknowledge that they lack high-resolution microclimate data and that winters equally or more severe than 2012 occurred without recorded mortality. This is properly noted in the response. In the manuscript, however, the Discussion still moves quite quickly from these caveats to the statement that extreme winters are a likely driver of the observed patterns and that winter 2012 exemplifies this. Since no climatic analysis appears in the Results, the climate narrative remains speculative. 

Response 5: We agree that, in the absence of explicit climatic analyses, statements regarding extreme winters must be presented cautiously and without causal inference. In response, we have substantially moderated the climate-related text in the Discussion. First, we added a clear caveat at the start of the relevant paragraph:
“Because no microclimate or regional climatic indices were incorporated into our analyses, any link between cold anomalies and mortality remains hypothetical.” Second, we revised the concluding sentence of that section to avoid implying a demonstrated causal relationship. The previous phrasing, “Extreme winter conditions are a likely driver…”, has been replaced with: “Extreme winter conditions may contribute to mortality events, but this cannot be confirmed with the available data.” Third, we removed language that suggested a specific explanatory role for the winter of 2012 in the absence of supporting evidence, and we now frame it solely as an example of a year with both severe conditions and observed mortality, without attributing causation. These revisions ensure that all climate-related interpretation is appropriately tentative and consistent with the descriptive scope of the dataset.

Comment 6: The Parnicite age-structure case study has been significantly reworked and many of my concrete suggestions have been taken on board. Nevertheless, the main text does not spell out the proportional mortality relative to the estimated colony size, even though both numbers are given, leaving readers to infer the very small absolute fraction of the colony represented by the 34 aged carcasses. In addition, while the Discussion now contains an excellent description of the uncertainties inherent in dentine and cementum ageing and introduces epigenetic clocks as a promising alternative, this cautionary material follows, rather than precedes, a paragraph that states that the age structure of Parnicite, together with external studies, collectively supports early-life mortality as a critical demographic filter in long-lived bats . In other words, the strong demographic conclusion is still presented before the methodological caveats have been fully explained.

Response 6: We thank the reviewer for these valuable observations. We have revised the manuscript to address both the proportional-mortality clarification and the ordering of the Discussion paragraphs. First, we now explicitly state the proportion that the 34 carcasses represent relative to the estimated colony size. Immediately after reporting the number of analysed carcasses, we added: “The 40 carcasses represent approximately 0.07% of the estimated colony size.” This ensures that readers do not need to infer the proportion and can more clearly contextualise the demographic sample. Second, in the Discussion we have reordered the relevant paragraphs so that the methodological caveats surrounding dentine-ring ageing precede any demographic interpretation. This restructuring ensures that uncertainties in ageing methods are fully presented before the biological conclusions that follow from the age-structure data. To reinforce this flow, we also added the transition phrase:
“With these methodological uncertainties in mind…”
at the start of the interpretative paragraph.

Together, these revisions improve the clarity, transparency, and logical structure of the age-structure section in line with the reviewer’s recommendations.