Apparent Soil Carbon and Nitrogen Stocks in the Mediterranean Forest Ecosystem over a Six-Year Post-Fire Chronosequence

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

General comments

The manuscript entitled “Soil carbon and nitrogen pools in the Mediterranean forest ecosystem over a six-year post-fire chronosequence” addresses an important topic related to post-fire soil recovery in Mediterranean forests. The study presents valuable field data collected over multiple years and has the potential to contribute to the understanding of soil C and N dynamics following wildfire. However, the manuscript still requires substantial revisions before it can be considered for publication. The experimental design and sampling strategy need to be better described and justified, several interpretations in the Discussion are overly speculative and not fully supported by the data, and the conclusions should better reflect the limitations of the study. In addition, there are several issues related to clarity, organization, and scientific writing that should be addressed. Specific comments and suggestions are provided below.

 

 

Abstract

L22: “Mediterranean ecosystems are fire-prone”, why? Please explain in detail.

L27: Make it clearer that “covered by shrubs and trees” are two treatments tested within one of the effects.

L28: Add the month in which the fire occurred.

L29: Expand the abbreviation WC.

 

 

Introduction

The Introduction provides appropriate background but requires better focus and organization. Some statements need stronger justification, methodological information should be removed, and the rationale linking the literature, knowledge gap, objectives, and hypotheses should be strengthened.

 

L49-53: The abbreviations for C and N should be defined upon their first appearance. Furthermore, what else changes besides C and N in the soil? If the study focuses solely on soil, this should be stated, including the effect on soil fauna.

L53-66: I agree with the statements, but what vegetation parameters support this? Number of plants/density, species richness, abundance, what others? This should be detailed, as the text only mentions the effect but does not explain the cause.

L67-69: Okay, note that this has a major influence on temporal variability.

L88-89: Remove this sentence, as it belongs in the methodology section, not the introduction.

L93-97: Remove this paragraph. The first sentence can be moved to the hypotheses section, but the second should not be included.

 

 

Material and Methods

General comments:

Overall, The Materials and Methods section require clarification and additional detail to ensure reproducibility. The experimental design, sampling strategy, and sample processing are not sufficiently described, and several methodological choices need better justification. Some information should be reorganized to improve the logical flow of the section.

 

Specific comments:

L100-101: Add the geographic location of the study.

L101-103: The authors should report exact data regarding the area affected by the wildfire, as well as the park’s total area.

L103-107: This is very important information, but it should be summarized and supplemented with ecological data regarding species richness, abundance, etc.

L107-109: The study methodology is not appropriate. Remove.

L112-119: I understand that collecting samples at the same location would be most appropriate. Therefore, the authors should better explain the procedure adopted to ensure that similar samples were collected across the sampled locations on different dates. The experimental design is described in this paragraph and should be made clearer to the reader, as it is confusing. Improve.

In addition, did the authors collect any data on tree growth? Diameter, height, volume, biomass? These data will show the effect of soil changes on plant growth after the fire. I suggest that they be presented.

L120-121: Specify the sampling layer as 0–10 cm in depth, not just the top layer. Furthermore, the authors should explain why they chose only the surface layer and not other subsurface layers.

L121-124: So there were 5 simple samples, which yielded 1 sample per area? What was the number of replicates? 12 per land cover type? The authors should provide details.

L126: Remove “Upon arrival.”

L139-140: Provide details on the procedures used for analyzing intact soil samples for BD.

L140: Triplicate of how many samples? Specify the total number of samples included in the analyses.

L151-153: What are the differences in vegetation cover (shrubs versus trees) within each sampling period? Provide details.

L159-162: This information should be added immediately after your data processing, after line 150.

 

 

Results

L167-218: The presentation of results in Fig. 1 is excessively long and should be shortened and simplified.

This new presentation should be condensed into a single paragraph. It should not be too long, so that the reader can easily access all the information. Use the figure to support this presentation.

The reference “(Fig. 1)” should appear only at the end of the first sentence.

L191-194: Revise the presentation of units, such as “g m⁻²,” in this paragraph and throughout the manuscript, as in lines 207–210.

L224: Revise “Figg.”

 

 

 

 

Discussion

The discussion is well-grounded in the literature; however, it contains an excess of mechanistic interpretations that have not been experimentally evaluated. It is recommended to limit the conclusions to the results obtained and to make it clear when certain explanations represent only plausible hypotheses, avoiding extrapolations beyond the data produced by the study.

 

L242-245: The explanation that the increase in C and N stocks occurred due to the rapid mineralization of organic matter is speculative. The study did not assess mineralization processes or microbial activity. It is recommended to use more cautious language.

L245-261: The authors correctly discuss the influence of soil density on C and N stocks. However, this limitation should be explored in greater depth, addressing the potential bias in stock estimates when calculated at a fixed depth without correction for equivalent soil mass.

L264-275: The claim that trees exhibited greater C accumulation and that this reflects structural and functional differences in vegetation lacks experimental support. The study did not assess vegetation attributes (biomass, litter production, growth, or floristic composition) that would support this interpretation.

L273-279: The discussion regarding nutrient stabilization, microbial reorganization, and organic matter quality is highly speculative, as these variables were not measured. It is recommended that these interpretations be reformulated in a more hypothetical tone.

L283-292: The explanation for N dynamics is based on processes that occurred between 1 and 3 months after the fire. However, the first sampling was conducted approximately 22 months after the fire. This discussion should be better contextualized or shortened, as it goes beyond the period actually evaluated.

L294-311: Although the authors suggest differences between trees and shrubs in terms of C accumulation, these interpretations are speculative. Information on biomass, litter production, tree survival, or vegetation regeneration would be necessary to support these claims.

L313-328: The discussion of the C:N ratio contains inconsistencies. The authors state that C stocks declined more rapidly than N stocks after the fire, yet the results show an increase in stocks over the monitoring period. It is recommended that this interpretation be revised to avoid contradictions with the presented results.

L321-328: The influence of litter quality on the C:N ratio is plausible but was not evaluated in this study. It is recommended that this explanation be presented as a hypothesis rather than a conclusion.

L330-346: The explanations for changes in soil pH and moisture are consistent with the literature, but they remain inferences. Since ash, water repellency, and vegetation cover were not evaluated, it is recommended to use more cautious wording (“may be related,” “possibly associated”).

 

 

Conclusion

This section is too long and should be shortened by 50%.

My concerns are as follows:

The authors should avoid interpretations that go beyond the results obtained. The statement that soils can “maintain or even increase” C and N stocks should be presented with greater caution, considering that the observed increase may be related to changes in soil density and that the study was conducted in a single area.

The study’s limitations were correctly acknowledged; however, it should be noted that the sites sampled before and after the fire were not exactly the same, which limits causal inferences regarding the effect of fire.

It is suggested that a practical implication of the results be included, indicating how this information can contribute to the monitoring or management of fire-prone Mediterranean ecosystems, thereby strengthening the applied relevance of the study.

Future directions could be more specific, indicating which biological, vegetation, or functional parameters should be incorporated into future studies to better understand the mechanisms of soil recovery after fire.

 

 

Figures:

Figure 1: On the x-axis, show only the time effect: pre, short, medium, and long fire effect.

On the y-axis, the font size of the variable labels should be increased so that the reader can see them clearly.

Inside panel “a,” icons should be added to represent the colors (violet and green) of the different vegetation types (shrubs and trees).

This simplifies the visualization of the information in the figure.

What is the sample size used to calculate the means? This should be indicated in the figure’s legend.

 

Figure 2 and 3: These can be combined.

 

 

Comments for author File: Comments.pdf

Author Response

Reviewer 1

The manuscript entitled “Soil carbon and nitrogen pools in the Mediterranean forest ecosystem over a six-year post-fire chronosequence” addresses an important topic related to post-fire soil recovery in Mediterranean forests. The study presents valuable field data collected over multiple years and has the potential to contribute to the understanding of soil C and N dynamics following wildfire. However, the manuscript still requires substantial revisions before it can be considered for publication. The experimental design and sampling strategy need to be better described and justified, several interpretations in the Discussion are overly speculative and not fully supported by the data, and the conclusions should better reflect the limitations of the study. In addition, there are several issues related to clarity, organization, and scientific writing that should be addressed. Specific comments and suggestions are provided below.

The authors thank the reviewer for the valuable comments and suggestions that have improved the manuscript.

Abstract

L22: “Mediterranean ecosystems are fire-prone”, why? Please explain in detail.

Done (L. 22-23)

L27: Make it clearer that “covered by shrubs and trees” are two treatments tested within one of the effects.

Done (L. 28)

L28: Add the month in which the fire occurred.

Done (L. 26)

L29: Expand the abbreviation WC.

Done (L. 29)

Introduction

The Introduction provides appropriate background but requires better focus and organization. Some statements need stronger justification, methodological information should be removed, and the rationale linking the literature, knowledge gap, objectives, and hypotheses should be strengthened.

L49-53: The abbreviations for C and N should be defined upon their first appearance. Furthermore, what else changes besides C and N in the soil? If the study focuses solely on soil, this should be stated, including the effect on soil fauna.

The authors thank the Reviewer for the observation. Carbon and nitrogen are now defined at their first occurrence in the Introduction. They also have expanded the text to acknowledge that fire can affect not only soil C and N, but also physical, chemical, and biological soil properties, including microbial communities and soil fauna. Finally, we clarified in the objectives that the present study focused on soil physicochemical properties and that soil fauna was not directly investigated. (L. 30; 91-92)

L53-66: I agree with the statements, but what vegetation parameters support this? Number of plants/density, species richness, abundance, what others? This should be detailed, as the text only mentions the effect but does not explain the cause.

The authors thank the Reviewer for the suggestion. They have expanded this section to identify the main vegetation attributes that can influence post-fire soil C and N dynamics. As these parameters were not directly measured in the present study, the authors now explicitly state that vegetation cover was used only as a broad site category and avoid attributing the observed soil patterns to specific vegetation mechanisms. (L. 119-121)

L67-69: Okay, note that this has a major influence on temporal variability.

The authors thank the Reviewer for the suggestion. The Introduction now explicitly acknowledges that post-fire trajectories may be strongly influenced by interannual climatic variability. (L. 71-77; 85-87)

L88-89: Remove this sentence, as it belongs in the methodology section, not the introduction.

Done.

L93-97: Remove this paragraph. The first sentence can be moved to the hypotheses section, but the second should not be included.

The authors thank the Reviewer for the suggestion, and they have removed the paragraph.

Material and Methods

General comments:

Overall, The Materials and Methods section require clarification and additional detail to ensure reproducibility. The experimental design, sampling strategy, and sample processing are not sufficiently described, and several methodological choices need better justification. Some information should be reorganized to improve the logical flow of the section.

Specific comments:

L100-101: Add the geographic location of the study.

Done (L. 109)

L101-103: The authors should report exact data regarding the area affected by the wildfire, as well as the park’s total area.

The authors have added some details about the area of the Park affected by fire; however, as they did not measure directly the surface park, they have added a reference reporting that. (L. 109; 132)

L103-107: This is very important information, but it should be summarized and supplemented with ecological data regarding species richness, abundance, etc.

The authors thank the Reviewer for the observation. Unfortunately, quantitative pre-fire vegetation data, including species richness, plant density, abundance, and percentage cover, were not collected as part of the original survey and are therefore unavailable. The authors have summarized the description of the pre-fire vegetation and added some limitations. (L. 137-144)

L107-109: The study methodology is not appropriate. Remove.

The authors thank the Reviewer for the observation. The authors recognize that previous surveys was not specifically designed to provide a quantitative assessment of vegetation composition and the statement has been removed. (L. 147-158)

L112-119: I understand that collecting samples at the same location would be most appropriate. Therefore, the authors should better explain the procedure adopted to ensure that similar samples were collected across the sampled locations on different dates. The experimental design is described in this paragraph and should be made clearer to the reader, as it is confusing. Improve.

In addition, did the authors collect any data on tree growth? Diameter, height, volume, biomass? These data will show the effect of soil changes on plant growth after the fire. I suggest that they be presented.

The authors thank the Reviewer for the comment. The authors have revised the paragraph to clarify how spatial comparability was maintained across sampling campaigns. (L. 137-144)

L120-121: Specify the sampling layer as 0–10 cm in depth, not just the top layer. Furthermore, the authors should explain why they chose only the surface layer and not other subsurface layers.

The authors thank the Reviewer for the comment. The authors have modified the material and method section to better clarify the choice of the layer. (L. 147-158)

L121-124: So there were 5 simple samples, which yielded 1 sample per area? What was the number of replicates? 12 per land cover type? The authors should provide details.

The authors thank the Reviewer for the comment. The authors have modified the material and method section to better clarify the sampling design. (L. 147-158)

L126: Remove “Upon arrival.”

Done.

L139-140: Provide details on the procedures used for analyzing intact soil samples for BD.

The authors thank the Reviewer for the comment. They have expanded the Materials and Methods to describe the procedure used to determine bulk density from intact soil cores. (L. 196-204)

L140: Triplicate of how many samples? Specify the total number of samples included in the analyses.

The authors have specified that the analyses included 24 independent composite samples per sampling campaign (12 per vegetation-cover category), for a total of 144 composite samples across the six sampling periods. Each composite sample was analyzed in three technical replicates, which were averaged before statistical analysis. (L. 147-158)

L151-153: What are the differences in vegetation cover (shrubs versus trees) within each sampling period? Provide details.

The authors thank the Reviewer for the comment. Vegetation cover was not quantified using percentage cover, plant density, or biomass measurements. Sites were assigned to two broad physiognomic categories at each sampling period: tree-covered sites were characterized by the presence of an evident tree canopy, whereas shrub-covered sites were predominantly occupied by shrub and herbaceous vegetation and lacked a prevailing tree canopy.

L159-162: This information should be added immediately after your data processing, after line 150.

The authors thank the reviewer for the comment, and they have changed the statistical section according to the Reviewer requests.

Results

L167-218: The presentation of results in Fig. 1 is excessively long and should be shortened and simplified.

This new presentation should be condensed into a single paragraph. It should not be too long, so that the reader can easily access all the information. Use the figure to support this presentation.

The reference “(Fig. 1)” should appear only at the end of the first sentence.

 

The result section has been shortened as requested.

 

L191-194: Revise the presentation of units, such as “g m⁻²,” in this paragraph and throughout the manuscript, as in lines 207–210.

Done.

L224: Revise “Figg.”

Done.

Discussion

The discussion is well-grounded in the literature; however, it contains an excess of mechanistic interpretations that have not been experimentally evaluated. It is recommended to limit the conclusions to the results obtained and to make it clear when certain explanations represent only plausible hypotheses, avoiding extrapolations beyond the data produced by the study.

L242-245: The explanation that the increase in C and N stocks occurred due to the rapid mineralization of organic matter is speculative. The study did not assess mineralization processes or microbial activity. It is recommended to use more cautious language.

L245-261: The authors correctly discuss the influence of soil density on C and N stocks. However, this limitation should be explored in greater depth, addressing the potential bias in stock estimates when calculated at a fixed depth without correction for equivalent soil mass.

L264-275: The claim that trees exhibited greater C accumulation and that this reflects structural and functional differences in vegetation lacks experimental support. The study did not assess vegetation attributes (biomass, litter production, growth, or floristic composition) that would support this interpretation.

L273-279: The discussion regarding nutrient stabilization, microbial reorganization, and organic matter quality is highly speculative, as these variables were not measured. It is recommended that these interpretations be reformulated in a more hypothetical tone.

L283-292: The explanation for N dynamics is based on processes that occurred between 1 and 3 months after the fire. However, the first sampling was conducted approximately 22 months after the fire. This discussion should be better contextualized or shortened, as it goes beyond the period actually evaluated.

L294-311: Although the authors suggest differences between trees and shrubs in terms of C accumulation, these interpretations are speculative. Information on biomass, litter production, tree survival, or vegetation regeneration would be necessary to support these claims.

L313-328: The discussion of the C:N ratio contains inconsistencies. The authors state that C stocks declined more rapidly than N stocks after the fire, yet the results show an increase in stocks over the monitoring period. It is recommended that this interpretation be revised to avoid contradictions with the presented results.

L321-328: The influence of litter quality on the C:N ratio is plausible but was not evaluated in this study. It is recommended that this explanation be presented as a hypothesis rather than a conclusion.

L330-346: The explanations for changes in soil pH and moisture are consistent with the literature, but they remain inferences. Since ash, water repellency, and vegetation cover were not evaluated, it is recommended to use more cautious wording (“may be related,” “possibly associated”).

The Discussion section has been completely changed, some speculation have been removed, and other have been better explained.

Conclusion

This section is too long and should be shortened by 50%.

My concerns are as follows:

The authors should avoid interpretations that go beyond the results obtained. The statement that soils can “maintain or even increase” C and N stocks should be presented with greater caution, considering that the observed increase may be related to changes in soil density and that the study was conducted in a single area.

The study’s limitations were correctly acknowledged; however, it should be noted that the sites sampled before and after the fire were not exactly the same, which limits causal inferences regarding the effect of fire.

It is suggested that a practical implication of the results be included, indicating how this information can contribute to the monitoring or management of fire-prone Mediterranean ecosystems, thereby strengthening the applied relevance of the study.

Future directions could be more specific, indicating which biological, vegetation, or functional parameters should be incorporated into future studies to better understand the mechanisms of soil recovery after fire.

The conclusion section has been completely changed according to the new results and discussion.

Figures:

Figure 1: On the x-axis, show only the time effect: pre, short, medium, and long fire effect.

On the y-axis, the font size of the variable labels should be increased so that the reader can see them clearly.

Inside panel “a,” icons should be added to represent the colors (violet and green) of the different vegetation types (shrubs and trees).

This simplifies the visualization of the information in the figure.

What is the sample size used to calculate the means? This should be indicated in the figure’s legend.

Figure 2 and 3: These can be combined.

The figures have been modified according to the request of the Reviewers.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

The paper presents results of a fire impact assessment on soil properties. The paper is well-structured and well-written. What caught my eye was the lack of illustrations and tables. If the latter is not too significant, then adding a map with the research object and photographs of the area (before and after the fire) would significantly improve the article.

Below are my suggestions and comments.

 

Abstract: It’s clear and shows the paper summary well.

Just one suggestion here is to define what “WC” here (water content abbreviation) means.

 

Introduction

41-42. This statement is ambiguous, in my opinion. While for ecosystems it exerts an overall positive effect (I guess you mean vegetation), what about organisms and animals? So, please consider making it much clearer.

43-46. It would be nice to report fire frequency or dynamics in this region. Has the frequency of fires increased in recent years/decades?

Line 82. The dot is missing. Please check.

 

Materials and Methods

So, the article undoubtedly will benefit from a map with the position of the study area and photos of locations. Please add that as a separate figure. You can see an example here: 10.1134/S1064229319120044.

112-124. Please highlight how many samples were collected in total.

 

Results

This section is concise, but at the same time it clearly reported the main results.

Fig. 1. I don’t see letters of significant difference for the plot of Corg.

It also would be nice to discuss a high Corg variability under the UB_T site, comparing with other locations.

221. The WC abbreviation was already mentioned. Please check this point throughout the text.

 

Discussion

The discussion well explains the mechanisms of changing in soil parameters.

While authors consider 22 months after a fire as a short term, in my opinion it is not really short, as almost two years passed. Anyway, don't mind that because many papers do the same. So, in this direction I would recommend to discuss the instant (1-2 months) fire impact on soil.

248-249. Under citation (#38), please indicate the location within this sentence for better understanding and comparison by readers.

Author Response

Reviewer 2

Comments and Suggestions for Authors

The paper presents results of a fire impact assessment on soil properties. The paper is well-structured and well-written. What caught my eye was the lack of illustrations and tables. If the latter is not too significant, then adding a map with the research object and photographs of the area (before and after the fire) would significantly improve the article.

The Authors thank the Reviewer for the suggestion and they added a table describing the different sampled sites and a supplementary figure (Figure S1) with some photographs of the area before and after fire.

Below are my suggestions and comments.

Abstract: It’s clear and shows the paper summary well.

Just one suggestion here is to define what “WC” here (water content abbreviation) means.

The Authors according the Reviewer have better explained the definition of WC. (L. 29)

Introduction

41-42. This statement is ambiguous, in my opinion. While for ecosystems it exerts an overall positive effect (I guess you mean vegetation), what about organisms and animals? So, please consider making it much clearer.

The Authors clarified the point suggested by the Reviewer adding more information on the positive effects of fire on flora and fauna in the Mediterranean area. (L. 45-46)

43-46. It would be nice to report fire frequency or dynamics in this region. Has the frequency of fires increased in recent years/decades?

The Authors thank the Reviewer and have added more detailed information about the fragility of the Mediterranean ecosystems caused by fire. (L. 47-51)

Line 82. The dot is missing. Please check.

Done.

 

Materials and Methods

So, the article undoubtedly will benefit from a map with the position of the study area and photos of locations. Please add that as a separate figure. You can see an example here: 10.1134/S1064229319120044.

The Authors have added Figure S1 with photographs of study sites.

112-124. Please highlight how many samples were collected in total.

The authors thank the Reviewer for this comment and they have added more details about soil sampling and number of samples in the new version of the manuscript. (L. 147-158)

 

Results

This section is concise, but at the same time it clearly reported the main results.

Fig. 1. I don’t see letters of significant difference for the plot of Corg.

The statistical analyses have been repeated, youo can find the correct statistics in the new version fo the manuscript, in the figure 1.

It also would be nice to discuss a high Corg variability under the UB_T site, comparing with other locations.

The discussion has totally changed, you can find the modifications in the new version of the manuscript.

The WC abbreviation was already mentioned. Please check this point throughout the text.

Done.

Discussion

The discussion well explains the mechanisms of changing in soil parameters.

While authors consider 22 months after a fire as a short term, in my opinion it is not really short, as almost two years passed. Anyway, don't mind that because many papers do the same. So, in this direction I would recommend to discuss the instant (1-2 months) fire impact on soil.

The Authors thank the Reviewer for suggestion and they have modified the discussion section.

248-249. Under citation (#38), please indicate the location within this sentence for better understanding and comparison by readers.

The authors have modified the discussion to better clarify the comparison.

Reviewer 3 Report

Comments and Suggestions for Authors

Dear Authors,

Please find listed below my recommendations for "Soil carbon and nitrogen pools in the Mediterranean forest ecosystem over a six-year post-fire chronosequence":

1. Please consider to better justify the chronosequence approach. The manuscript relies on a space-for-time substitution (comparing distinct plots sampled at different post-fire intervals rather than a true longitudinal design), but this is a well-known limitation of chronosequence studies and it should be better considered for acknowledgment
2. I think that the hypothesis formulation should be much better considered, especially H2, as it predicts a short-term decrease followed by medium-term recovery, all this in the condition that the introduction already cites literature showing highly variable, context-dependent, and sometimes opposite (increase vs. decrease) patterns at short and long term. In my opinion as written the H is not logically derived from the cited evidence and looks more as a simplification imposed post hoc
3. L117-119: In my opinion the statement as the post-fire sampling are not from the same locations due to vegetation alteration is the major confounds "time since fire" with spatial heterogeneity, undermining the causal inference of the entire pool dynamics used throughout the manuscript
4. L120-121: In my opinion using a constant 10 cm depth across highly variable bulk density conditions can materially bias mass-based pool estimates. I think that correction (e.g., equivalent soil mass approach) should be considered
5. L138: Same here, I have few concern here, I saw that he pool calculation assumes constant sampling depth, but bulk density itself changed significantly with fire (an increase according to L187–189) but this for me means that pool increases are partly a mathematical artifact of compaction rather than true nutrient accumulation
6. Please ensure statistical consistency - see case of pH (once is reported as median in other part as mean which is inconsistent with the stated use of non-parametric tests in MM)
7. Please ensure consistency in C pools reporting in the text
8. L206-208: "slightly decreased" how was this tested? Please better ensure consistency in statistical metrics reporting and the text narrative 
9. I think that the manuscript should better evidence the formal time × cover interaction test results
10. L285-288: I recommend a more careful consideration in discussions, here the manuscript invoke volatilization (1–3 months) and mineralization/uptake dynamics (1–2 years) as explanations for N pool changes, but there are no data at those specific intervals were actually collected (sampling was at 22, 34, 46 months - L114-115). Actually these mechanisms are asserted from external literature (extensive citation as 5,46,43,47,48) and are not demonstrated by the study's own measurements...
11. L294-296: This statement is a bit strange for me because the manuscript describe different behavior of nutrient storage between trees and shrubs immediately after stating that no significant difference was found between covers, for me this as it is written is more  a direct rhetorical overstatement of a null statistical result
12. I recommend a better consideration of the discussions section and integration of related representative manuscripts available from the literature. Also studies limitation should be better consider in the end of discussion
13. The conclusion should be shorten and adequately reconsidered after performed corrections

Author Response

Reviewer 3

Dear Authors,

Please find listed below my recommendations for "Soil carbon and nitrogen pools in the Mediterranean forest ecosystem over a six-year post-fire chronosequence":

1. Please consider to better justify the chronosequence approach. The manuscript relies on a space-for-time substitution (comparing distinct plots sampled at different post-fire intervals rather than a true longitudinal design), but this is a well-known limitation of chronosequence studies and it should be better considered for acknowledgment

The Authors agree with the Reviewer and have added a more details about the sampling design, and some limitations in discussion and conclusion section.

1. I think that the hypothesis formulation should be much better considered, especially H2, as it predicts a short-term decrease followed by medium-term recovery, all this in the condition that the introduction already cites literature showing highly variable, context-dependent, and sometimes opposite (increase vs. decrease) patterns at short and long term. In my opinion as written the H is not logically derived from the cited evidence and looks more as a simplification imposed post hoc

      The Authors thank the Reviewer for the comment and they have modified the hypothesis in the new version of the manuscript. (L. 91-104)

1. L117-119: In my opinion the statement as the post-fire sampling are not from the same locations due to vegetation alteration is the major confounds "time since fire" with spatial heterogeneity, undermining the causal inference of the entire pool dynamics used throughout the manuscript

The Authors have better clarified the site choice in material and method section.

1. L120-121: In my opinion using a constant 10 cm depth across highly variable bulk density conditions can materially bias mass-based pool estimates. I think that correction (e.g., equivalent soil mass approach) should be considered

The authors agree that comparisons based on a fixed soil depth may be affected by differences in bulk density and sampled soil mass, and that an equivalent soil mass approach would generally provide more robust stock estimates. The authors have considered this correction; however, only the 0–10 cm layer was sampled, without an underlying layer from which the additional or excluded soil mass and its C and N concentrations could be estimated. Therefore, a rigorous equivalent-soil-mass correction could not be performed retrospectively. The authors have retained the fixed-depth calculations but now consistently define them as “apparent fixed-depth stocks”. The authors have also added this limitation to the Methods, Discussion, and Conclusions and removed interpretations of these values as direct evidence of C or N accumulation or sequestration.

1. L138: Same here, I have few concern here, I saw that he pool calculation assumes constant sampling depth, but bulk density itself changed significantly with fire (an increase according to L187–189) but this for me means that pool increases are partly a mathematical artifact of compaction rather than true nutrient accumulation

The authors agree that variation in bulk density can influence fixed-depth stock estimates and that an apparent increase in a stock does not necessarily represent true nutrient accumulation. However, after reanalysing the data with the mixed model requested by the reviewers, bulk density did not differ significantly. Given the fixed-depth calculation and the observational sampling design, we no longer interpret this difference as true N accumulation. The Results, Discussion, and Conclusions have been revised accordingly.

1. Please ensure statistical consistency - see case of pH (once is reported as median in other part as mean which is inconsistent with the stated use of non-parametric tests in MM)

The Authors thank the Reviewer. The statistical analyses were repeated, and you can find the correct results in the new version of the manuscript (Figure 1).

1. Please ensure consistency in C pools reporting in the text

The Authors have re-calculated the stock of N and C and they have corrected the Discussion section.

8. L206-208: "slightly decreased" how was this tested? Please better ensure consistency in statistical metrics reporting and the text narrative 

This section has been completely modified.

1. I think that the manuscript should better evidence the formal time × cover interaction test results

The authors have performed a mixed model to test the interation between time and vegetation. The methods and results has been modified consistently.

1. L285-288: I recommend a more careful consideration in discussions, here the manuscript invoke volatilization (1–3 months) and mineralization/uptake dynamics (1–2 years) as explanations for N pool changes, but there are no data at those specific intervals were actually collected (sampling was at 22, 34, 46 months - L114-115). Actually these mechanisms are asserted from external literature (extensive citation as 5,46,43,47,48) and are not demonstrated by the study's own measurements...

The Authors have modified the Discussion and have deleted the speculation throughout the manuscript.

1. L294-296: This statement is a bit strange for me because the manuscript describe different behavior of nutrient storage between trees and shrubs immediately after stating that no significant difference was found between covers, for me this as it is written is more a direct rhetorical overstatement of a null statistical result

After doing the linear mixed model with interaction, statistical results have changed and the claim bout the different behaviour of nutrients under different vegetation cover have been deleted.

1. I recommend a better consideration of the discussions section and integration of related representative manuscripts available from the literature. Also studies limitation should be better consider in the end of discussion

The Authors have added in the Discussion and conclusion sections several limintation about the present study.  

1. The conclusion should be shorten and adequately reconsidered after performed corrections

The Authors thank the Reviewer and they completely rewritten Conclusions section according to the Reviewer’s suggestion.

 

 

Reviewer 4 Report

Comments and Suggestions for Authors

Dear Authors, 
Comments on the manuscript can be found in the attached file.

Comments for author File: Comments.pdf

Author Response

Reviewer 4

The manuscript addresses an important issue: changes in carbon and nitrogen pools in volcanic soils following a Mediterranean forest fire. The greatest strength of the study is the availability of data from before the fire and from several post-fire surveys, potentially covering a period of around six years.

The authors thank the reviewer for the valuable comments and suggestions that have improved the manuscript.

However, in its current form, I would not consider the conclusions to be sufficiently substantiated. The most serious issues concern: the contradictory chronology of the experiment; the lack of parallel, fire-unaffected control areas; changes in sampling locations; likely erroneous units for C and N stocks; failure to account for changes in soil mass when comparing stocks; statistical analysis unsuitable for the experimental design; unwarranted causal conclusions; an unclear relationship with numerous previous publications from the same area; and numerous inconsistencies between the abstract, results and discussion. Please note the following observations:

 

Lines	Meaning	Comment
27–28, 114–115	Critical	The dates and number of months are mathematically impossible. Following the fire in 2017, spring 2019 may correspond to approximately 22 months, but spring 2021 is approximately 46 months, not 34, and spring 2023 is approximately 70 months, not 46. At the same time, in lines 250, 262 and 366, the authors refer to six years. The chronology must be corrected throughout the work. The authors thank the Reviewer for the comment, and they have corrected the date. (L. 124-132)
101	Serious	June 2017 is given as the date of the fire. The main phase of the fire on Vesuvius is documented for 9–12 July 2017 by NASA and Copernicus. The authors should specify the exact eruption and the date relating to its area.   The authors thank the Reviewer for the comment, and they have corrected the date. (L. 109)
112–119	Critical	The post-fire areas did not correspond to the pre-fire areas. This means that the differences may result from spatial heterogeneity rather than from the fire or the recovery time. This is not a classic longitudinal study of the same sites.   The authors agree that the study is not a classical longitudinal assessment based on repeated measurements of identical permanent plots. The authors have clarified the sampling design, explicitly acknowledged this limitation, and revised the manuscript to avoid attributing the observed differences exclusively to fire or post-fire recovery time. (L. 137-144)
112–119	Critical	There is a lack of parallel, unburned control areas studied in 2019, 2021 and 2023. The effect of the fire is therefore completely confounded with the effects of the year, precipitation, temperature, succession, land-use changes and location.   The authors thank the Reviewer for the comment. No parallel unburned sites were sampled; therefore, differences between the pre-fire baseline and the post-fire campaigns cannot be attributed exclusively to the wildfire. The authors have explicitly acknowledged this limitation throughout the revised manuscript and replaced causal statements concerning fire effects and recovery with observational language describing differences among pre- and post-fire sampling periods.
112–119, 141–150	Critical	It is unclear whether the 24 pre-fire plots were sampled repeatedly between 2015 and 2017, or whether new plots were selected each year. It is not stated whether the same 24 plots were resampled in subsequent campaigns following the fire. Without this information, it is impossible to determine the experimental unit or the number of independent observations.   The authors thank the Reviewer for the correction. The same 24 sites—12 under shrub cover and 12 under tree cover—were repeatedly sampled during the annual pre-fire surveys conducted from 2015 to 2017. Most of these sites were also resampled during the post-fire campaigns of 2019, 2021, and 2023. Only 5 sites were relocated slightly because wildfire-induced vegetation changes prevented their continued classification within the original vegetation-cover category. The authors have modified the sampling design to improve clarity. (L. 124-132)
136–138	Critical	The stock equation does not include units or a conversion factor. With BD in g cm⁻³, depth in cm and concentration in %, the correct form is: stock (g m⁻²) = BD × depth × concentration (%) × 100.   The authors thank the Reviewer for identifying the missing units and conversion factor. The authors revised the equations and specified all units explicitly. Soil organic carbon and total N stocks are now expressed in Mg ha⁻¹ rather than g m⁻².
136–138, 191–210	Critical	The values given are likely to have the wrong units. For the soil beneath the shrubs before the fire: 0.46 g cm⁻³ × 10 cm × 0.33% N × 100 gives approx. 152 g N m⁻², not 2.59 g m⁻². The value 2.59 would be more likely to be Mg ha⁻¹. Similarly, 44.6 for C looks more like Mg ha⁻¹ than g m⁻². All calculations need to be verified against the source data.   The authors thank the Reviewer for highlighting the error. Re-examination of the original calculations showed that the values had been assigned incorrect units and that the stock calculations required revision. The authors have recalculated bulk density for each sample from its oven-dry soil mass and the corresponding core volume. Soil organic carbon and total N stocks were then recalculated from the measured concentrations, bulk density, and sampling depth. The corresponding values in the dataset, statistical analyses, Figure 1, Results, Discussion, and Conclusions have been replaced. Because the recalculated stocks differed substantially from the original values, all statistical tests concerning SOC and total N stocks were repeated, and statements that were no longer supported by the revised analyses were removed or modified.
136–140, 245–261	Critical	Stocks were compared at a constant depth despite a nearly twofold change in bulk density. In such a situation, an increase in ‘stocks’ may result from a greater soil mass in the 0–10 cm layer, rather than from the accumulation of the element. It is recommended to recalculate using the equivalent soil mass (ESM) method. This issue has been discussed in detail by Wendt and Hauser.   The authors thank the Reviewer for raising this important methodological issue. The Reviewer’s concern was based on the bulk-density values and stock calculations reported in the previous version, which suggested an approximately twofold increase in bulk density and significant increases in C and N stocks. The revised results no longer show significant differences in bulk density among sampling periods, either under trees (Kruskal–Wallis, P = 0.992) or under shrubs (Kruskal–Wallis, P = 0.109). Therefore, the previous apparent increase in SOC stock and its interpretation as C accumulation have been removed. Because the study included only one sampled soil layer and no additional soil from beneath the sampled depth, a rigorous equivalent-soil-mass correction could not be performed retrospectively without extrapolating C and N concentrations beyond the sampled material. The authors therefore retained the fixed-depth stocks, explicitly reported for the 0–10 cm layer, and avoided interpreting their temporal variation as evidence of C or N accumulation or sequestration.
127–138	Serious	It is unclear whether the ‘C pool’ was calculated from total C or from Corg. If calculated from total C, it must not be automatically interpreted as a stock of organic matter or as organic carbon sequestration.   The authors thank the reviewer for highlighting this ambiguity. . In the revised manuscript, all C-stock calculations were performed using the measured organic C concentration (Corg), rather than total C. The variable is now consistently termed “soil organic carbon stock” (SOC stock) and is expressed as Mg C ha⁻¹ throughout the manuscript. (L. 184-195; 205-209)
139–140	Serious	Bulk density was determined after drying at 75°C. The standard ISO 11272 core method specifies drying at 105°C to constant weight. A temperature of 75°C may overestimate the dry soil mass if water remains in the soil. Any deviation requires justification and validation. ISO 11272.   The authors thank the reviewer for the correction, and they apologize for the error. They have corrected the correct temperature in the soil analysis section. (L. 196-204)
141–162	Critical	The tests used do not correspond to the ‘time × vegetation’ factorial design. Separate Kruskal–Wallis tests for trees and shrubs do not test for interactions. A model is required that takes into account time, vegetation type, their interaction, site structure and any repeated measurements.   The authors thank the Reviewer for identifying this limitation in the original statistical analysis. The authors replaced the separate Kruskal–Wallis and Wilcoxon tests with factorial linear mixed-effects models. Sampling period, vegetation type, and their interaction were included as fixed effects, while site identity was included as a random intercept to account for repeated observations from the same site. Type III Wald chi-square tests with sum-to-zero contrasts were used to evaluate the fixed effects. Response variables were transformed where required based on model diagnostics. cFigure 1, its caption, the Statistical Analysis section, and the Results and Discussion have been revised accordingly.
154–162	Serious	It is not stated whether the variables were standardised prior to PCA. When using pH, water content, percentage concentrations and unit resources simultaneously, standardisation is essential.   In the new version of the manuscript, the authors performed a new PCA standardizing the variables, and they have modified the material and method section accordingly. (L. 232-238)
154–162	Serious	The PCA/PERMANOVA analysis simultaneously included C and N concentrations, the C:N ratio, bulk density, and resources calculated from the same concentrations and BD. This results in mathematical redundancy and artificially amplifies the significance of the axes related to C, N and BD.   The authors agree with the Reviewer that the original selection of variables introduced mathematical redundancy. The authors have therefore repeated the PCA using only directly measured soil properties: pH, WC, Corg concentration, total N concentration, and BD. The PCA, its figure, and the corresponding Methods and Results have been replaced accordingly.
159–162	Serious	Bray–Curtis is typical for data on the composition/abundance of biological communities, and its selection for standardised physicochemical properties requires justification. No data transformations, number of permutations, permutation constraints, pseudo-F, R² or PERMDISP test are reported. PERMANOVA may confound differences in centroid positions with differences in variance – see Warton et al. and Anderson.   The authors thank the Reviewer for this methodological observation. The authors agree that the use of Bray–Curtis dissimilarities was not adequately justified for the standardised continuous physicochemical variables considered in this study. After reconsidering the nature of the variables and the partially repeated and unbalanced sampling design, the authors have removed the PERMANOVA from the revised manuscript.
171–179	Serious	The figure caption refers to the Wilcoxon test, which is not described in the methodology. It is also unclear whether a correction for multiple comparisons between cover types was applied.   The authors have changed the statistical analyses, performing an LMM followed by a Holm-Sidak post hoc.
171–179	Moderate	The caption ‘median, minimum and maximum’ probably does not accurately describe a classic box plot, which usually shows the median, quartiles and whiskers. All elements of the plot must be defined, and the sample size (n) and the method of presenting outliers must be specified.   The authors have modified the figure caption according to the suggestion of the Reviewer.
191–210	Serious	The C and N results are implausibly low for the 0–10 cm mineral layer if they are indeed expressed in g m⁻². It is essential to provide a data table, the formula with units, and a sample calculation.   The authors thank the Reviewer for highlighting this inconsistency. The authors agree that the values reported in the previous version were implausibly low when interpreted as g m⁻². Re-examination of the source data showed that the stock units had been incorrectly reported and the calculations have been revised according to the equation reported in the Methods.
219–238	Serious	The PCA and PERMANOVA results are incomplete. The table of loadings, eigenvalues, the full PERMANOVA table, R², pseudo-F, the number of permutations, the results of pairwise comparisons and the P-value corrections are missing.   The authors have added a table with eigenvalues of PCA in the supplementary material, Table S1.
231–233	Serious	The sentence only mentions comparisons of UB with three time points after the fire. It is unclear whether ST–MT, ST–LT and MT–LT were compared.   This analysis have been removed from the manuscript.
238	Editorial error	The placeholder text ‘3.1. Subsection’ has been left in.   The authors have removed the error.
376–377	Editorial error	File not found: ‘Figure S1: title; Table S1: title; Video S1: title’. The supplement has not actually been described.   The authors thank the Reviewer for the correction and they have corrected it.

 

Other comments:

 

• Lines 24–25: ‘the research aims’ should be ‘the research aimed’; ‘in a Mediterranean’ is written without a space.

Done.

• Lines 27–28: incorrect number of

The authors have corrected them. (L. 29)

• Lines 29–31: the claim of a ‘progressive increase’ is not true for C under the trees – the stock decreases from 332 to 301 between the medium and long term.

This sentence has been removed according to the new calculations in the manuscript.

 

• Lines 30–31: ‘approximately 5-fold’ does not describe Relative to UB, the increase in N is approximately:
  • 6, 12.8 and 18.7 times under the trees;
  • 6; 11.8 and 14.9 times under the trees.

The authors thank the Reviewer for identifying this numerical inconsistency. The authors agree that the expression “approximately five-fold” did not accurately describe the previously reported changes in total N stock. According to the new calculations performed for the new version of the manuscript, the Abstract, Results, Discussion, and Conclusions have been revised accordingly.

 

• Lines 31–32: the claim that WC increased in the short term contradicts the results under trees, where it fell from 23.9 to 9.27 per cent.

The authors agree with the Reviewer and have deleted the statement in the original Abstract regarding the WC pattern under the two vegetation covers.

 

• Lines 33–35: the conclusion suggests that the effect of time since the fire has been demonstrated, although the layout does not allow for the separation of time, year, space and the fire itself.

The authors agree with the Reviewer that the sampling design does not allow the effects of fire, calendar year, elapsed time, and spatial variation to be separated unequivocally. The post-fire observations were obtained during successive years, and contemporaneous unburnt control sites were not sampled during each post-fire campaign. Therefore, differences among sampling periods cannot be interpreted as causal effects of time since fire alone.

The authors revised the manuscript to describe the results as temporal patterns or associations with sampling period rather than demonstrated effects of time since fire. The authors have also added this limitation to the Discussion and Conclusions and clarified that the observed differences may reflect the combined influence of fire condition, sampling year, elapsed time, and spatial heterogeneity.

 

• Lines 36–37: the keywords are awkward: ‘nutrient storage’, ‘dynamics of C and N’, ‘recovery time’. Better alternatives would include, amongst others, soil carbon stock, soil nitrogen stock, post-fire recovery, Andosols, Mediterranean forest, vegetation

The authors thank the Reviewer for the suggestion, and they have replaced the keywords.

 

The abstract should state explicitly that this is an observational comparison of different sites and campaigns, and that the increase relates to ‘apparent fixed-depth stocks’ until the stocks are recalculated using the equivalent soil mass method.

The authors agree with the Reviewer that the observational nature of the study and the limitations of fixed-depth stock comparisons should be stated explicitly in the Abstract.

Following verification of the source data, all bulk-density, SOC-stock, and total-N-stock values were recalculated. The authors have therefore removed statements referring to C or N accumulation, recovery, or sequestration and now describe the study explicitly as an observational comparison among sites and sampling campaigns. Stock values are consistently described as apparent fixed-depth stocks for the 0–10 cm layer.

A rigorous equivalent-soil-mass correction could not be applied retrospectively because only one soil layer was sampled and no soil was collected beneath the 10 cm sampling depth. An ESM calculation would therefore require extrapolating Corg and total N concentrations to an unsampled soil depth and assuming that their concentrations were uniform beyond the sampled layer. We considered that such an extrapolation would introduce unsupported information. Instead, we retained the corrected fixed-depth stocks, clearly acknowledged their limitations, and avoided interpreting differences as direct evidence of C or N accumulation. Because of the recalculation of several parameters, the abstract results have been changed.

 

The methodology is insufficient: the description of laboratory analyses presents a general outline but does not ensure reproducibility and does not address the issues relating to the field layout.

In the field project – lines 100–123 – the following are missing: coordinates and a map of all sites; elevation above sea level, slope, aspect and distances between sites; site selection criteria; the area represented by a single site; measurement of local fire severity; information on fire management measures: sanitary felling, deadwood removal, afforestation, and erosion control; confirmation as to whether the same plots were sampled in 2019, 2021 and 2023; meteorological data for individual campaigns; information on how the three years’ pre-fire data were combined; justification for grouping different species into the broad categories of ‘trees’ and ‘shrubs’. Particularly problematic is the grouping of soils beneath Quercus ilex, various Pinus species and, potentially, Robinia pseudoacacia into a single ‘trees’ category. These species have different litter composition, rates of litter and decomposition, and impacts on the nitrogen cycle. Without information on species composition and its changes, the ‘trees’ effect is ambiguous.

 

The authors thank the reviewer for the comment. They have added a site-level table reporting permanent site identifier, original field identifier, geographical coordinates in WGS84, elevation, sampling history, broad vegetation cover, and the available information on characteristic plant species. They have clarified that 24 geographical sampling locations were considered. Because some field identifiers changed during the monitoring period and, in some cases, shrub- and tree-covered microsites were located in close proximity, the original identifiers were reconciled using coordinates and field records and linked to permanent site identifiers. The revised Methods and Table 1 now specify which locations were sampled during each campaign.

Plot-level slope, aspect, meteorological measurements, and detailed records of post-fire management interventions were not available and could not be reconstructed reliably. This limitation is now explicitly acknowledged in the Methods and Discussion. Local fire severity was classified as 3 according to Saulino et al., 2020.

 

In the laboratory analyses (lines 125–140), information is missing regarding: the model of the elemental analyser; sample mass and combustion conditions; the method of C and N calibration; reference materials, recovery, precision and limits of quantification; details of HCl decalcification: soil mass, acid volume, contact time, drying method and control of Corg losses; the definition of C:N: total C/total N or Corg/N; the diameter, height and volume of the rings for BD; the number of independent BD cores per site; corrections for skeletal fragments >2 mm; information on whether the three laboratory determinations were averaged. ‘All laboratory determinations were carried out in triplicate’ refers to technical replicates, not three independent samples. If these were treated as independent statistical observations, this would constitute pseudo-replication. Furthermore, in line 129, the soil:water ratio is specified as v:v; this should normally be given as the ratio of soil mass to water volume (w:v).

The authors thank the Reviewer for identifying the suggestion, and they have expanded the soil analyses section. (L. 163)

Please note the numerical and interpretative inconsistencies:

Lines 29–31 vs 206–210: no continuous increase in C under the trees.

The authors have deleted the wrong sentences.

Lines 30–31 vs 191–210: a fivefold increase does not describe N.

The authors have deleted the wrong sentences.

Lines 31–32 vs 197–198: WC under the trees fell in the short term.

The authors have deleted the wrong sentences.

Lines 167 and 195: in one instance medians are presented, and in another the ‘mean value’, despite the use of non-parametric statistics.

The authors have deleted the wrong sentences.

Lines 183–186: the concentration of N under the shrubs changes relatively little, whilst the N pool increases by as much as a dozen or so times. This suggests that the pool result is largely generated by BD or unit error.

The authors have corrected the error by recalculating BD and stocks.

Lines 191–210: there are no measures of dispersion for any of the medians given.

The authors have corrected the errors.

Lines 231–233: the full PERMANOVA results are missing.

The PERMANOVA analysis was deleted from the paper.

Lines 283–285: the statement that, in the short term, the N stock was ten times greater is inconsistent with the figures – approximately 6.6 times.

The authors have deleted the wrong sentences.

Lines 286–292: the authors describe a decline in N 1–3 months after the fire, although the earliest sample was taken approximately 22 months after the event.

Lines 313–320: the claim that, following a fire, C stocks decline more sharply than N stocks contradicts the authors’ own findings, in which both stocks increase.

Lines 246–247: ‘after an initial increase, then a decrease’ applies at most to C under trees; it does not apply to N or C under shrubs.

The authors have deleted the wrong sentences.

It would be advisable to include a table showing, for each combination of time and cover: the number of independent plots; the median, Q1–Q3 and range; concentrations of Corg, total C and N; BD; C and N stocks; test statistics, exact P-values, adjusted P-values and effect sizes.

The discussion is extensive but largely speculative. The authors repeatedly attribute mechanisms that were not investigated: litter production, mineralisation, stabilisation of organic matter, microbial activity, N fixation, tree resistance and the rate of primary production.

The authors have changed the discussion section according to the new results.

 

The most significant examples include:

Lines 242–245: rapid SOM mineralisation does not automatically explain the increase in total C stock; mineralisation also results in C emissions. Pyrogenic C, litter input, erosion and CO₂ fluxes were not measured.

 

Lines 253–261: the authors correctly note the importance of BD, but this undermines the main conclusion regarding accumulation. The issue should not merely be a caveat in the discussion – it requires recalculation.

Lines 264–279: the description of different trajectories for trees and shrubs is an overinterpretation, as PERMANOVA did not reveal a cover effect, and differences in stock between cover types were not significant.

Lines 274–279: ‘efficient nutrient stabilisation’, ‘microbial reorganisation’ and ‘rapid recovery of organic matter turnover’ were not measured.

Lines 296–312: the amounts of burnt and new litter, as well as biomass production, were not determined.

Lines 302–305: The assertion that the trees were not completely destroyed and therefore continued to produce litter requires field data.

Lines 321–328: differences in the quality of tree and shrub litter are a plausible mechanism, but this study did not measure lignin, cellulose, the C:N ratio of the litter, or the rate of decomposition.

Lines 330–339: It has not been demonstrated that the increase in pH caused N retention. ‘Retention’ and ‘mobility’ have been conflated without explanation, although they are not synonyms.

Lines 340–343: high temperatures were present during the fire, not ‘after the fire’. The statement that the accumulation of organic matter reduced water content is unclear and may contradict the subsequent explanation regarding increased retention.

Lines 344–348: neither canopy regeneration, litter quantity nor crown closure were measured.

 

The discussion could be shortened by around 20–25%, clearly separating: own results → consistency with the literature → possible mechanism → limitations of the interpretation.

All the speculations in the new version of the discussion were removed, and the discussion has been re-adapted according to the new results.

 

Required corrections prior to re-evaluation:

 

1. Correct the date of the fire and all month
2. Present a spatio-temporal diagram of the experiment and the actual
3. Clarify which test conditions were repeated and which were
4. Separate the year effect from the fire effect, or qualify the causal
5. Verify the units and recalculate all C and N
6. Apply the ESM or explicitly define the results as apparent stocks at a constant
7. Determine whether the C stock refers to total C or
8. Analyse the data using a model corresponding to the time × cover system, with a plot effect if the measurements were repeated.
9. Remove mathematically dependent variables from a single PCA/PERMANOVA
10. Make the raw data, R code and complete tables of results
11. Limit the discussion of mechanisms that were not
12. Disclose the relationship between the data and the team’s previous
13. Remove boilerplate text and correct the entire reference list (e.g. entries 1, 34, 35).

In summary, it can be noted that the potential of the time series is considerable, but in its current form, it cannot be concluded that actual fire-induced accumulation of C and N has been demonstrated. The most likely explanation is a combination of changes in soil density, incomparability of sites, the year effect and a problem with stock units.

The authors have corrected the great part of the issues raised by the Reviewer and when they cannot add more details they have explained or inserted as limitations in the manuscript.

 

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors have adequately addressed almost all of the comments raised in the previous review. The manuscript has been substantially improved, particularly regarding the description of the sampling design, methodological details, limitations, and the reduction of speculative interpretations in the Discussion.

I also note that almost all field surveys and sampling campaigns were conducted by the authors themselves, which provides consistency to the dataset and strengthens the study.

Overall, I consider that the authors have satisfactorily addressed my previous concerns, and the manuscript is now suitable for publication.

Author Response

Reviewer 1

The authors have adequately addressed almost all of the comments raised in the previous review. The manuscript has been substantially improved, particularly regarding the description of the sampling design, methodological details, limitations, and the reduction of speculative interpretations in the Discussion.

I also note that almost all field surveys and sampling campaigns were conducted by the authors themselves, which provides consistency to the dataset and strengthens the study.

Overall, I consider that the authors have satisfactorily addressed my previous concerns, and the manuscript is now suitable for publication.

Response: The authors thank the Reviewer for appreciating the new version of the manuscript.

Reviewer 3 Report

Comments and Suggestions for Authors

Dear Authors,

Thank you very much for considering to improve "Soil carbon and nitrogen pools in the Mediterranean forest ecosystem over a six-year post-fire chronosequence". Reading the new version of the manuscript I noticed few aspects that could be considered. Please find these listed as follows: 

1. The methods section needs a better consideration in its formulation. They are too narrative and not contain the relevant technical information that ensure reproducibility - see for example case of GC no info about column, oven oven condition, inlet/detector operation data,.. quality performance parameters, etc. statement as L174-183 do not tell nothing.  Please keep this recommendation with seriosity through all the method section
2. Figure 1 - please verify the significant letters distribution (in my opinion they looks strange)
3. Why the Figure 2 differ comparing with the first version of the manuscript? Dim1 - 33.8 vs 42.8 / Dim2 30.7 vs 22.4
4. In discussions the cited literature should be well integrated and used for debate/comparisons/explanation and not just to enumerated 
5. In my opinion the limitations need to be clearly evidenced as a subsection

Author Response

Dear Authors,

Thank you very much for considering to improve "Soil carbon and nitrogen pools in the Mediterranean forest ecosystem over a six-year post-fire chronosequence". Reading the new version of the manuscript I noticed few aspects that could be considered. Please find these listed as follows: 

1. The methods section needs a better consideration in its formulation. They are too narrative and not contain the relevant technical information that ensure reproducibility - see for example case of GC no info about column, oven oven condition, inlet/detector operation data,.. quality performance parameters, etc. statement as L174-183 do not tell nothing. Please keep this recommendation with seriosity through all the method section

Response: the authors agree that complete instrumental parameters would improve analytical reproducibility and they have expanded the Methods to report all the available information retained in the analytical records, including the analyser model and configuration, sample preparation and mass, capsule type, oxidation temperature, combustion and carrier gases, reduction process, chromatographic separation, detector type, calibration material, quality-control procedure, and analytical precision. The authors also want to clarify that the Flash EA 1112 is a dynamic-combustion elemental analyser with an integrated gas-separation column and thermal conductivity detector, rather than a conventional gas chromatograph with a separate inlet and programmable GC method. Unfortunately, the original instrument method files are no longer available; therefore, parameters that could not be verified, such as exact gas flows, column specifications, detector settings, calibration range, recovery, and quantification limits, were not reconstructed from nominal manufacturer specifications. This limitation is now explicitly stated in the Methods (L. 196-200)

1. Figure 1 - please verify the significant letters distribution (in my opinion they looks strange)

Response: The authors thank the Reviewer for comment. The letters represent Holm-adjusted comparisons among sampling campaigns based on estimated marginal means averaged across vegetation categories. They do not represent separate comparisons for shrubs and trees because no sampling period × vegetation interaction was significant. To avoid ambiguity, the letters have been centred above each pair of shrub and tree boxplots, and the explanation has been clarified in the figure caption.

1. Why the Figure 2 differ comparing with the first version of the manuscript? Dim1 - 33.8 vs 42.8 / Dim2 30.7 vs 22.4

Response: The PCA differs from that in the original submission because it was repeated in response to the previous Reviewers’ concerns regarding standardisation and mathematical redundancy. The original PCA included both directly measured variables and derived variables, such as Corg:N and C and N stocks, which gave disproportionate weight to C, N, and BD. In the revised analysis, only directly measured properties—pH, WC, Corg, total N, and BD—were retained, and all variables were centred and scaled to unit variance. Changing the input matrix and its preprocessing necessarily changed the eigenvalues and the percentages of variance explained.

1. In discussions the cited literature should be well integrated and used for debate/comparisons/explanation and not just to enumerated.

Response: The authors thank the Reviewer for the suggestion and they have revised the Discussion to use the literature comparatively rather than as a list of possible mechanisms throughout the paragraph.

1. In my opinion the limitations need to be clearly evidenced as a subsection

Response: The authors thank the Reviewer for the suggestion, and they have added a dedicated subsection entitled “Study limitations” at the end of the Discussion.

Reviewer 4 Report

Comments and Suggestions for Authors

Dear authors,

the attachment contains comments and remarks

Comments for author File: Comments.pdf

Author Response

Reviewer 4

While many issues have been resolved, it is evident that some problems remain unresolved.

The following are of particular significance:

It is evident that the stock equation still contains an erroneous unit, as evidenced in lines 205– 209. The equation that has been derived is as follows:

Stock (g m⁻²) = BD × depth × element concentration (%)

This equation is numerically accurate for a result expressed in Mg ha⁻¹; however, it is not applicable to g m⁻². It is evident that, for a given surface area of 1 m², a factor of 100 is required.

The formula used to calculate the volume of stock is as follows:

stock (g m⁻²) = BD × depth × concentration(%) × 100

However:

The quantity of stock (in milligrams per hectare) is expressed as a function of depth and concentration (in percentage form).

As demonstrated in the results (lines 268–270), the authors utilise the unit Mg ha⁻¹. However, it should be noted that the methodology stipulates the unit g m⁻². The assertion by the authors that the units were corrected "throughout the manuscript" is therefore erroneous. This error is of particular significance, given that the erroneous units were identified as a primary factor contributing to the initial major revision.

Response: The authors thank the Reviewer for the comment, and they have corrected the error. The previous equation combined a numerical expression appropriate for Mg ha⁻¹ with a label in g m⁻². The authors have corrected the equation and now report stocks consistently in Mg ha⁻¹ throughout the manuscript.

 

Ø Unclear number and history of sites — lines 124–158

The text makes reference to 24 sites and 24 samples in each campaign; however, Table 1 contains 27 identifiers: 24 of which are labelled as BF+AF and three of which are labelled as AF.

In their response letter, the authors stated that "only five sites were relocated slightly." The following aspects require further clarification:

- The number of sites that were relocated, i.e. whether three or five sites in total were relocated

- The exact sites that were studied in 2019, 2021 and 2023

- The sites that were replaced

- Whether a site was assigned a new identifier after relocation

- Whether a relocated site was treated as the same site or as a new one in the model

- The actual n for repeated measurements

The designation "BF+AF" is overly generalised. The following columns should be included in the table: As demonstrated in Figure 1, the presence of each sample is clearly indicated for the years 2015, 2016, 2017, 2019, 2021 and 2023.

The Problem of the Three Years Before the Fire in the Statistical Model. The authors report a total of 144 samples. The calculation indicates that 24 sites should be assessed at six time points, thus yielding a total of 144. Concurrently, the model incorporates a mere four levels: BF, ST, MT, LT. This suggests that observations from 2015, 2016, and 2017 were treated collectively as a single BF level. Consequently:

The study encompassed a total of 72 observations, with each subsequent time point following the fire comprising 24 observations. The three distinct calendar years preceding the fire were amalgamated into a single level. The variability observed between the years 2015 and 2017 was incorporated into the within-level error of BF. The authors must elucidate whether they averaged the three-year values for each plot to obtain a single baseline value, or whether they entered all three observations as the same BF level. In the latter case, justification and a sensitivity analysis are required. A valid comparison would be made between a model based on an averaged baseline level and a model using all years. It is evident that the random plot effect has not been adequately substantiated. The model employs the plot identifier as a random intercept; however, the authors concurrently recognize that identical locations were not consistently surveyed. In the event of the relocation of plots, it is imperative that they are not automatically retained as the same repeated measurement object.

Response: The authors thank the Reviewer for identifying the inconsistencies in the description of the sampling design. The authors have re-examined the original sampling records and reconstructed the correspondence among the site identifiers used during the different campaigns. The previous statements referring to 24 sites per campaign, 144 samples, and five slightly relocated sites were inaccurate. After accurate evaluation, the authors had noted a wrong calculation of sites and number of replicates, and now they have corrected the number of sites and replications throughout the manuscript

The analysis-ready dataset comprises 44 site-by-campaign observations representing 27 distinct physical sites. Specifically, nine sites were included in the pre-fire baseline, 11 sites were sampled in 2019, 12 in 2021, and 12 in 2023. Thirteen physical sites were sampled in at least two periods, accounting for 30 observations, whereas 14 sites were represented in only one campaign. Only sites whose correspondence could be verified from the sampling records were assigned the same site identifier across campaigns. Sampling locations that did not correspond to a previously sampled physical site were assigned a new identifier and treated as independent sites in the statistical analysis. Therefore, the previous statement that five sites had been relocated has been removed. The newly sampled sites were not considered formal one-to-one replacements for specific previous sites.

The pre-fire condition was based on nine physical sites sampled during four campaigns conducted between 2015 and 2017. For the primary analysis, the observations from these campaigns were averaged within each physical site and variable, producing one pre-fire baseline value per site. Thus, the pre-fire condition contributed nine, rather than 36, observations to the model. This procedure avoided giving the pre-fire condition disproportionate weight relative to the individual post-fire campaigns and prevented repeated pre-fire measurements from being treated as independent observations.

The mixed-effects models included sampling time, vegetation cover, and their interaction as fixed effects and physical site identity as a random intercept. Consequently, observations from the same verified physical site were treated as repeated measurements, whereas campaign-specific or spatially distinct sites were treated as independent sampling units. The authors have revised Table 1 to indicate the presence of each site in 2015, 2016, 2017, 2019, 2021, and 2023 and have added the actual sample size for every campaign.

 

Furthermore, there is a notable similarity in the coordinates of certain tree and shrub plots, which may be indicative of similar geographical or environmental characteristics. These microplots may be adjacent, and therefore not fully spatially independent. The random effect of the sector/parent location should be considered, or at least the potential for spatial autocorrelation should be discussed.

Response: The authors have corrected the wrong information present in the manuscript, and they have made a new Table 1 presenting the correct sites sampled during the study.

 

The issue of core samples for BD determination is addressed in the following section, which is located between pages 196 and 204. The authors specify a cylinder with an inner diameter of approximately 5 centimetres and a height of 15 centimetres. Concurrently, the resources are calculated for the 0–10 cm layer. The ambiguity arises from the uncertainty surrounding the following aspects:

The cylinder's sampling of soil from a depth of 0–15 cm.

The insertion of the cylinder, which may have been limited to a depth of 10 cm.

The precise volume considered in the equation.

The volume of a cylinder with a diameter of 5 cm is estimated to be approximately:

The volume of 294.5 cubic centimetres is equivalent to a height of 15 centimetres.

The volume of 196.3 cubic centimetres is equivalent to a height of 10 centimetres.

The discrepancy is 50%, and it has the potential to substantially modify the BD and resource estimates. It is incumbent upon the authors to specify the actual core volume and to provide a sample calculation.

Response: The authors thank the reviewer for highlighting the inconsistency about BD measurement. And they have specified in material and method section that the core for the BD measurement was with an height of 15 cm with a volume of about 294 cm^-3(L. 209-219)

 

It is evident that no correction was applied for the skeletal fraction. In the relevant pages, it is stated that stones were excluded during the process of sampling, and no correction was applied for the fraction >2 mm. In the context of shallow, stony volcanic soil, the following implications may be observed:

- A preferential direction of sampling towards areas exhibiting reduced stoniness may be indicated;

- An overestimation of the fine soil fraction resource per unit area may be observed;

- The comparability of sites may be constrained.

The assertion that no corrections were made does not, in itself, resolve the issue. This should be explicitly acknowledged as a limitation on the resources expressed per unit area.

Response: The authors thank the reviewer for the comment and they agree that merely stating that no correction was applied was insufficient. They have now clarified that the stocks refer to the sampled fine-soil fraction and explicitly acknowledge that the absence of a volumetric coarse-fragment correction may overestimate area-based stocks and constrain comparisons among sites. (L. 217-219)

 

It is evident that the abstract under scrutiny contains unwarranted causal conclusions, as evidenced in lines 31–38. Notwithstanding the authors' assertions, the following contentions persist:

The following statements are made in the study: "Time since fire... impacted soil characteristics"; "Vegetation cover impacted..."; and "The time since fire affects...".

These findings contradict the subsequent admission that there were no parallel unburned controls and that it is impossible to separate time, year, and the impact of the fire.

The abstract should state that:

Soil properties exhibited variation among the sampling campaigns; however, these discrepancies cannot be ascribed exclusively to wildfire or elapsed time, as contemporaneous unburned controls were not available for analysis.

Response: The Abstract has been rewritten to describe differences among sampling campaigns rather than causal effects of wildfire or elapsed time. It now explicitly states that contemporaneous unburnt controls were unavailable and that the observed patterns cannot be attributed exclusively to fire or time since fire. (L. 39-41)

It is evident that the statistical results remain incomplete. As illustrated in Table 2, Wald statistics and P-values are presented; however, the following elements are absent:

- model coefficients;

- confidence intervals;

- effect sizes;

- Box–Cox transformation parameter values;

- information on precisely which variables were transformed;

- model diagnostic results; and

- information on how the EMM values were transformed back.

 

Response: The authors have improved the previous presentation of the statistical results in the new version of the manuscript. Table 2 has been expanded to include degrees of freedom and semi-partial values with confidence intervals for each model term. The authors have also added three supplementary tables reporting: (i) the transformation applied to each response, the corresponding Box–Cox parameter, random-effect variance, ICC, model convergence, singularity and diagnostic statistics (Table S2); (ii) all fixed-effect coefficients with standard errors and 95% confidence intervals (Table S3); and (iii) estimated marginal means on the original response scale, pairwise comparisons, Holm-adjusted P-values and standardised differences (Table S4). They have also clarified that statistical tests were conducted on the model scale and that EMMs and their confidence intervals were returned to the original scale using the inverse Box–Cox transformation.

 

It is imperative to note that a P-value of 0.0000 for Corg:N is not acceptable and should be reported as P < 0.0001, for instance.

Response: Done.

 

The response letter also makes reference to the Holm–Šidák post hoc test, whereas the manuscript on lines 227–228 reports the standard Holm correction. It is imperative that the content is consistent.

It is evident that the complete descriptive data table is not available. The requested table, which should include the following for each combination of campaign and coverage, has not yet been provided:

- actual n;

- median;

- Q1–Q3;

- range;

- Corg, N, and BD;

- SOC and N stocks;

- effect sizes and confidence intervals.

This is particularly necessary given the varying sample sizes at the baseline and post-fire periods. Boxplots should not be considered as a substitute for a descriptive data table.

Response: The authors thank the Reviewer for identifying the inconsistent terminology. “Holm–Šidák” in the previous response letter was an incorrect description. All pairwise P-values were adjusted using the standard sequential Holm procedure. The authors have replaced “Holm–Šidák” with “Holm” throughout the response letter and verified that the terminology is consistent with the Methods, Results, figure captions, and supplementary tables.

The authors have also added a complete descriptive statistics table for every sampling-time x vegetation combination (Table S8).

 

It is evident that the interpretation of the ESM has been rectified to a limited extent. The authors have accurately employed the term "apparent fixed-depth stock" and have generally refrained from interpreting SOC as sequestration. However, on pages 309 to 310, reference is still made to an "increase in N storage", despite the fact that N stock is also dependent on soil mass in the 0–10 cm layer. The absence of statistically significant differences in BD does not provide unequivocal evidence that the effect of soil mass is negligible. A presentation of the soil mass per 1 m²for each date would be advantageous, as would the inclusion of a sensitivity analysis.

Response: The authors thank the reviewer for the correction and have removed the expression “increase in N storage”. The revised text states only that apparent fixed-depth N stock, without interpreting this difference as true nutrient accumulation.

 

The scarcity of raw data and R code is evident.

Lines 413–414 comprise the following:

These are available from the corresponding author upon reasonable request.

It is important to note that the present study does not address the comments regarding the following aspects:

- availability of source data;

- availability of R code;

- availability of BD calculations;

- availability of SOC and N stock calculations; and

- assignment of samples to sites and campaigns.

In the wake of the initial identification of significant unit errors and the subsequent necessity to recalculate the results, the provision of data and code should be considered a prerequisite for further evaluation.

 

Response: The authors have now provided the complete R code used for data verification and statistical analysis. The script includes verification of the apparent fixed-depth SOC and N stocks from BD, elemental concentration, and the 10-cm reference depth; Box–Cox transformations; mixed-effects models; Wald χ² tests; estimated marginal means; Holm-adjusted comparisons; effect sizes; model diagnostics; boxplots; and PCA. It also generates the complete sessionInfo() output. The correspondence between historical sample labels, reconstructed physical-site identifiers, sampling campaigns, and vegetation categories is reported in Table S1. The site-level dataset is subject to third-party data-ownership restrictions and cannot be made publicly available without authorisation from the data owner. This restriction is now explicitly reported in the Data Availability Statement.

 

It is evident that the relationship to the team's previous publications has not been explained. This remains one of the most significant unaddressed comments. The manuscript cites numerous works by the authors in the same field, including references 8, 18, 33, 35, 45, and 50. However, the manuscript does not specify several key points:

- It is unclear whether the same sites were used.

- It is unclear whether the same campaigns were used.

- It is unclear which data were previously published.

- It is unclear which results are entirely new.

- It is unclear whether the 2019 data have already appeared in other studies.

It is imperative that the authors include a table comparing the current manuscript with their previous publications. Absent this condition, the novelty and independence of the dataset remain unestablished.

 

Response: The authors have added Table S9 to the Supplementary Materials. For each relevant publication, the table identifies the study sites, sampling campaigns, variables previously reported, observations shared with the present dataset, and the specific contribution that is new in the present manuscript. We have also added a paragraph to the Methods explicitly acknowledging any reuse of site- and campaign-level observations. The novelty of the present study lies primarily in the integration of multiple pre- and post-fire sampling campaigns within a single analytical framework, the specific focus on Corg and N apparent fixed-depth stocks, and the application of a factorial mixed-effects model accounting for repeated site observations. Thus, the study does not claim that every individual measurement is unpublished; rather, its original contribution derives from the research question, the multi-campaign synthesis, the recalculated stock estimates, and the statistical framework used to evaluate sampling-period and vegetation associations.

 

It is evident that the supplement and bibliography have not been thoroughly revised.

Specifically, pages 392 to 393 persist in displaying only the following content:

Figure S1; Table S1.

It is important to note that no titles were provided, nor was the supplement attached for review. Consequently, the veracity of the table of eigenvalues and PCA loadings cannot be substantiated.

Errors still appear in the bibliography, including:

- inconsistent formatting of titles and journal names

 

Response: The authors thank the Reviewer for highlighting the error. The authors have now prepared and uploaded a complete Supplementary Materials file in which every figure and table is numbered, titled, captioned and cited in the main manuscript.

 

The response letter describes many actual changes but contains several inconsistencies:

- it declares 24 sites and 5 relocations, while the table shows 27 identifiers and 3 AF sites

- it states that all units were converted to Mg ha⁻¹, while the equation still specifies g m⁻²

- it cites Kruskal–Wallis tests for BD, although the manuscript presents an LMM

- it mentions a post hoc Holm–Šidák test, while the PDF specifies a Holm correction

- claims that all causal inferences have been removed, but they remain in the abstract

- claims that all speculation has been removed, while some still remains—though it is now better qualified

Responses are to be prepared once more, this time with a point-by-point approach, with reference to the exact new text and correct line numbers.

The version received demonstrates significant improvement and now has publication potential; however, at this stage, it is recommended that a further targeted round of revisions be undertaken.

The following items are required prior to acceptance:

The first step in the process is the correction of the equation and the units of measurement.

2. A comprehensive elucidation of the 24/27 sites and 3/5 relocations is imperative.

Thirdly, a detailed account is required which elucidates the manner in which the data collected from 2015 to 2017 was utilised.

The fourth point for discussion is the clarification of the BD cores and sample volume.

The fifth step in the process involves the supplementation of model results, effect sizes and descriptive data.

6. The elimination of causal claims from the abstract.

The provision of data and R code is to be undertaken.

The eighth point pertains to the disclosure of data overlap with previous publications.

The ninth item on the agenda is the supplement and the entire bibliography.

Response: The authors have done all the issues raised by the Reviewer in the new version of the manuscript.