Soil Carbon–Water Trade-Off Relationships and Driving Mechanisms in Different Forest Types on the Yunnan Plateau, China

Round 1

Reviewer 1 Report (Previous Reviewer 3)

Comments and Suggestions for Authors

1. I don't understand what 136.81–256.79%, etc. means in the abstract. Please clarify.

2.  units for RMSD should be reported.

all my former comments were fixed.

Author Response

Comment 1: I don't understand what 136.81–256.79%, etc. means in the abstract. Please clarify.

Response 1：

Thank you for pointing this out. The percentages in the abstract denote relative changes compared with sloping rainfed farmland (SRF). Specifically, we calculated percentage change as(mean value in a given forest type – mean value in SRF) / mean value in SRF × 100%. Accordingly, SOCS in broadleaf plantations was 136.81%–256.79% higher than SRF, and SOCS in conifer plantations was 44.13%–166.57% higher than SRF. Likewise, the +36.6% for SWS in Alnus cremastogyne forest (ACF) means a 36.6% increase relative to SRF.

For clarity, we have revised the abstract to explicitly state the reference baseline and the meaning of the percentages (see revised sentences below).

“Results indicate that within the 0–60 cm soil layer, relative to sloping rainfed farmland, the most pronounced increases in SOCS occurred in the secondary evergreen broadleaf forest restored for 23 years and the zonal broadleaf plantation (Alnus cremastogyne forest) restored for 20 years, with gains of 274.44% and 256.79%, respectively. These were followed by the mixed conifer–broadleaf forest restored for 35 years (+166.57%) and the non-zonal broadleaf plantation (Acacia dealbata forest) restored for 19 years (+136.81%). By contrast, Pinus yunnanensis stands—representing conifer plantations—exhibited smaller SOCS increases of 105.32%, 101.34%, and 44.13% after 60, 22, and 9 years of restoration, respectively, which were significantly lower than those of the younger broadleaf plantations or secondary forests. Vegetation restoration had limited effects on SWS; only ACF showed a significant increase(36.60%).”

Comment 1: units for RMSD should be reported.

Response 1：

Thank you for the suggestion. In our analysis, RMSD is unitless (dimensionless) because both variables—SOC content and SWC—were min–max normalized to [0,1] prior to calculation. After standardization, RMSD represents the Euclidean distance of each SOC–SWC point from the 1:1 line and therefore has no physical units. We have made this explicit at its first mention in the Methods section.

Reviewer 2 Report (Previous Reviewer 1)

Comments and Suggestions for Authors

Dear Authors,

Please find my recommendations for "Soil carbon–water trade‑off relationships and driving mechanisms in different forest types on the Yunnan Plateau, China" manuscript in the next:

1. I recommend for authors that in introduction to better introduce the "soil water storage" term. The terminology, in my opinion, is imprecise and and could induce confusion among readers. The authors should specify whether they refer to gravimetric water content, volumetric water content, plant-available water capacity, or field capacity, as these represent distinct hydrological parameters with different ecological implications
2. L40-42: Please be specific because terms as "qualities" is vague. I recommend it replace with a more precise biogeochemical descriptors 
3. In my opinion the authors should better highlight the knowledge gaps by identifying and presenting specific research deficiencies in current literature. The authors should better highlight why understanding SOCS-SWS relationships is a central scientific challenge. They should present for readers why this coupling is more critical than other biogeochemical interactions or ecosystem processes
4. Also I suggest for authors to better discuss the spatial heterogeneity, temporal dynamics, or methodological challenges in quantifying soil carbon-water interactions, which are fundamental in forest biogeochemistry research
5. For experimental design I recommend for authors to better present how they accounted the site-specific edaphic conditions, microclimate variations, and management history differences which could influence SOCS and SWS independently of forest type (please consider the previous information measurements not just those measured as a results of sampling campaign)
6. L144: Why only one sampling time period? In my opinion this cannot capture seasonal variability in soil water dynamics or account for inter-annual precipitation variations that significantly influence both SOCS and SWS measurements
7. For PLS please better justify the selection of latent constructs or provide theoretical rationale for the proposed causal pathways. For me the grouping of variables into "litter," "soil structure," and "soil chemistry" constructs lacks empirical validation through confirmatory factor analysis. Also for multicollinearity treatment the removing of variables with Spearman's |r| > 0.8 is an arbitrary threshold that may eliminate ecologically meaningful relationships in my view. It would be better if the authors employ variance inflation factor (VIF) analysis or principal component regression for more rigorous multicollinearity assessment
8. Please present all the software involved in results obtaining (section 2. Materials and methods)
9. If possible please ensure volumetric or mass-based equivalents for meaningful interpretation (SOC/SWS)
10. L341: Please check and verify this section. The factors shaping SOCS and SWS analysis shows concerning issues in my opinion: suspiciously high path coefficient (β = 0.98) suggesting overfitting, inconsistent confidence intervals contradicting significance levels, and unexplained GoF values (0.75, 0.72) lacking benchmark comparisons to justify model adequacy
11. L416-418: Please verify this statement as increased micro-aggregation typically enhances soil porosity and water retention capacity through improved pore size distribution, not the reverse
12. Please better sustain the attribution of age-related changes in SOCS and SWS to reduced density, lower physiological water demand and gradual improvement in soil structure to sustain the mechanism, otherwise it seems as a speculative interpretation beyond  observational data
13. In my opinion  RMSD measures deviation magnitude but does not inherently quantify ecological trade-offs or their intensity. Please better consider or sustain
14. Thee authors acknowledge geographic limitations but not enough address the temporal constraints, seasonal variability, or the space-for-time substitution assumptions that  limit the conclusions
15. Please consider in the discussion section to better integrate the relevant data from available literature to establish more comparative/criticist discussions. Also, please pay attention for conclusion and reconsider after improvements

Author Response

Comment 1:I recommend for authors that in introduction to better introduce the "soil water storage" term. The terminology, in my opinion, is imprecise and and could induce confusion among readers. The authors should specify whether they refer to gravimetric water content, volumetric water content, plant-available water capacity, or field capacity, as these represent distinct hydrological parameters with different ecological implications

Response 1：

Thank you for the valuable suggestion. We agree that the term “soil water storage” (SWS) requires a precise definition. In this study, SWS specifically refers to the depth-equivalent amount of water stored in the soil profile at the time of sampling (unit: mm); it is neither plant-available water capacity nor field capacity. We compute SWS from volumetric water content (θᵥ), which is derived from gravimetric soil water content (SWC) measured by oven-drying aluminum-box samples at 105 °C to constant mass and then converting using bulk density (BD). To eliminate ambiguity, we have revised the Methods to define SWS explicitly, distinguish it from field capacity and plant-available water capacity, and clarify the measurement and conversion steps. Specifically, Section 2.4 details the measurement of soil water content: “The aluminum box samples were oven-dried at 105°C until constant weight to determine the soil water content(SWC, %).”

In Section 2.5, we specify the definition and calculation method: “In this study, we use soil water storage (SWS) to denote the depth-equivalent quantity of water contained in the soil profile at sampling (mm). SWS is distinct from plant-available water capacity and field capacity; instead, it reflects the instantaneous amount of water present, computed from volumetric water content integrated over depth[8].”

Our previous calculation used volumetric water content directly; this is equivalent to the current formulation that uses the product of gravimetric water content and bulk density. It is important to note that, although the SWS computed here represents an instantaneous water stock, our methodological emphasis is on comparisons among forest types rather than on long-term dynamics within each type, i.e.: “To avoid bias arising from instantaneous soil-moisture conditions and to better capture the inherent soil-water retention capacity of different forest types, all field sampling was scheduled in May, i.e., at the end of the dry season immediately before the onset of the monsoon. At this time soils typically reach their lowest moisture after a prolonged dry period, thereby maximizing inter-type con-trasts in water status. Notably, May also coincides with the pre-monsoon peak of litter accumulation (LA), which facilitates the capture of maximum litter-layer biomass and the most pronounced differences in soil-moisture conditions among forest types.”

 

Comment 2: L40-42: Please be specific because terms as "qualities" is vague. I recommend it replace with a more precise biogeochemical descriptors

Response 2：

Thank you for this helpful suggestion. We agree that “qualities” is imprecise. Accordingly, we removed the term and replaced it with specific biogeochemical phrasing that identifies the governing processes. The revised sentences in the Introduction (L40–42) now read:

“Soil organic carbon (SOC), the largest carbon pool in terrestrial ecosystems[1], plays a pivotal role in mitigating global climate change and buffering ecosystems against extreme events such as heatwaves and droughts[2]. Soil moisture regulates the availability and cycling of carbon and nitrogen and microbial activity, thereby directly influencing plant growth and governing the dynamics of ecosystem productivity[3–5]. Elucidating the coupling within the soil carbon–water system not only helps optimize the balance between reducing water consumption and enhancing carbon sequestration capacity, but is also essential for strengthening ecosystem services and advancing sustainable forest management.”

These changes remove the vague term and explicitly point to nutrient availability and cycling, microbial activity, plant growth, and productivity dynamics as the relevant biogeochemical descriptors. No other uses of “qualities” remain in the manuscript.

Comment 3.1: In my opinion the authors should better highlight the knowledge gaps by identifying and presenting specific research deficiencies in current literature.

Response 3.1：

We sincerely thank the reviewer for this insightful suggestion. We have now substantially revised the Introduction to explicitly identify and articulate specific knowledge gaps in current literature, with a focus on three key research deficiencies:

• Context-dependent uncertainties in soil carbon-water trade-offs (Introduction, paragraph 2).

We emphasize that current literature fails to provide a predictive understanding of when and why vegetation restoration leads to synergies versus trade-offs between SOCS and SWS. By synthesizing contradictory findings across studies (e.g., synergies in surface layers vs. trade-offs in deep soils; temporal evolution from trade-offs to synergies with stand age), we demonstrate that the carbon-water relationship is not universal but contingent upon climate, species traits, restoration duration, and soil depth. This contextual complexity reveals a fundamental knowledge gap in predicting outcomes under specific ecological conditions.

• Overlooked mechanistic pathways(Introduction, paragraph 3).

We argue that existing studies have predominantly focused on phenomenological correlations between SOCS and SWS while neglecting key mechanistic drivers. Specifically, we identify the litter-soil interface and aggregate stability as critical but understudied mediators. By explaining how litter traits regulate both hydrological processes (infiltration, evaporation) and carbon transformation pathways (through aggregate formation and physical protection), we highlight a fundamental gap in understanding the biological and physical mechanisms that couple carbon and water dynamics.

• Geographical bias in study systems(Introduction, paragraph 4).

We document a severe imbalance in research focus: while arid/semiarid regions (e.g., Loess Plateau) have been extensively studied, humid subtropical mountain systems remain largely overlooked. We demonstrate that this geographical bias limits the generalizability of existing frameworks, as humid systems feature distinct ecological contexts (e.g., highly weathered soils, seasonal rainfall, fragmented topography) that may yield different carbon-water interactions. By quantifying the scarcity of studies in these regions despite their ecological significance, we reveal a critical geographical knowledge gap.

Through this three-pronged approach, we systematically identify both theoretical gaps (in mechanistic understanding) and empirical gaps (in geographical representation) that currently limit predictive capability in managing carbon-water interactions during vegetation restoration.

Comment 3.2:The authors should better highlight why understanding SOCS-SWS relationships is a central scientific challenge. They should present for readers why this coupling is more critical than other biogeochemical interactions or ecosystem processes.

Response 3.2：

We thank the reviewer for raising this important point. In response, we have significantly strengthened our argument for why understanding SOCS-SWS coupling represents a central scientific challenge in ecosystem science. Rather than treating carbon and water as separate cycles, we now emphasize their profound interdependence through both mechanistic linkages and functional consequences (Introduction, paragraph 1).

We first establish the exceptional magnitude of both pools—noting that SOC constitutes the largest terrestrial carbon stock (3.3 times larger than the atmospheric pool) while soil water fundamentally regulates all biogeochemical activity. We then highlight why their coupling is uniquely consequential: unlike unidirectional relationships, SOC and water engage in continuous bidirectional feedback where carbon accumulation modifies soil structure and water retention, while moisture availability simultaneously controls carbon inputs, transformation, and stabilization.

This interdependence becomes particularly critical because it underlies multiple ecosystem services simultaneously—from climate regulation and carbon sequestration to drought resilience and productivity. The central scientific challenge emerges from the fact that optimizing one service (e.g., carbon sequestration through afforestation) often jeopardizes another (e.g., water provisioning), especially under climate change. We reinforce this by citing evidence from drylands where carbon-focused restoration has inadvertently compromised water security and long-term ecosystem function. By demonstrating how SOCS-SWS coupling sits at the nexus of multiple critical processes and trade-offs, we position its understanding as more integrative and societally urgent than studying isolated biogeochemical cycles. This framing justifies why deciphering this particular coupling—rather than other interactions—is indispensable for achieving sustainable ecosystem management in a changing climate.

 

Comment 4: Also I suggest for authors to better discuss the spatial heterogeneity, temporal dynamics, or methodological challenges in quantifying soil carbon-water interactions, which are fundamental in forest biogeochemistry research.

 

Response4：

We thank the reviewer for this insightful suggestion. In response to your comment, we have substantially enhanced our discussion of spatial heterogeneity, temporal dynamics, and methodological considerations in quantifying soil carbon-water interactions throughout our manuscript.

Specifically, in the revised Introduction (Section 2), we have added new content addressing spatiotemporal dimensions of carbon-water relationships. We now discuss how topographic position creates spatial heterogeneity in soil moisture and organic matter distribution, with footslopes typically accumulating more water and carbon while showing weaker trade-offs compared to upper slopes [19]. We further address vertical heterogeneity through the soil profile, noting that land-use changes often exert stronger impacts on deep soil carbon-water interactions [20]. Regarding temporal dynamics, we highlight how stand maturation can modify carbon-water relationships, potentially alleviating early-stage trade-offs. For instance, while severe deep-layer moisture deficits were observed initially in Robinia pseudoacacia plantations on the Loess Plateau, some recovery of deep soil moisture occurred after 30 years of restoration [21]. Additionally, we note that the correlation between SWS and SOCS tends to weaken with increasing restoration duration [15].

Methodologically, we have strengthened our justification for using Root Mean Square Deviation (RMSD) as an appropriate metric for quantifying carbon-water trade-offs. As explained in Section 5 of our Introduction, RMSD provides a simple, dimensionless distance measure that is robust to nonlinear responses. By normalizing both SOCS and SWS to a 0-1 range and calculating the Euclidean distance of each sample point from the ideal 1:1 line in two-dimensional space, RMSD effectively captures the degree of deviation from perfect coordination between carbon and water benefits. The aggregation of these distances at the sample level through root mean square calculation provides a comprehensive measure of trade-off magnitude, with smaller values indicating more coordinated coupling and larger values suggesting more pronounced trade-offs. This approach has been widely validated as an effective indicator for analyzing balance between different ecosystem services and has been extensively applied in ecological management, landscape planning, and decision-making contexts [17,42,43].

 

Comment 5: For experimental design I recommend for authors to better present how they accounted the site-specific edaphic conditions, microclimate variations, and management history differences which could influence SOCS and SWS independently of forest type (please consider the previous information measurements not just those measured as a results of sampling campaign).

Response 5：

We appreciate the reviewer’s concern. In the revised manuscript we removed the space-for-time assumption and reframed the study as a cross-sectional comparison among representative forest types, with sloping rainfed farmland (SRF) as the reference. Our sampling design and analyses explicitly address site-specific edaphic conditions, microclimatic variation, and management history as follows.

First, plot selection minimized background heterogeneity by locating plots within the same geomorphic context and parent material wherever possible and by constraining elevation and slope ranges within each forest type. We recorded terrain variables (elevation, slope, aspect) and soil texture to represent site edaphic and topographic context. Second, we quantified the independent effects of forest type and soil depth using partial correlation and linear mixed-effects models (LMMs). The partial correlations (Figs. S3–S4) show that, after controlling for terrain and texture, litter traits, aggregate stability, and soil chemistry remain significant correlates of SOCS, whereas, after controlling for forest type, terrain and texture no longer explain SOCS/SWS or C–W. The LMMs (Table 1) include soil depth as a fixed effect and site as a random intercept, which absorbs unmeasured site-level heterogeneity, including microclimatic idiosyncrasies and legacy effects. Third, we acknowledge in Section 4.4 that strong forest-type and depth signals can mask residual terrain/texture influences and we explicitly flag SWS sensitivity to topography, outlining the need for future designs that couple stand type with topographic strata.

We believe these revisions have strengthened the discussion of our experimental design and its limitations regarding site-specific factors.

 

Comment 6: L144: Why only one sampling time period? In my opinion this cannot capture seasonal variability in soil water dynamics or account for inter-annual precipitation variations that significantly influence both SOCS and SWS measurements. 

Response 6：

We sincerely thank the reviewer for raising this important point regarding sampling design. We fully agree that multiple sampling time points would be ideal for capturing the full range of seasonal and interannual variability in soil moisture dynamics. However, as this study aims primarily to compare the inherent soil-water retention capacity and carbon sequestration potential across different forest restoration types (rather than to document their complete temporal dynamics), we strategically conducted the sampling during a specific critical period to maximize the comparability of our results. 

Specifically, to avoid bias arising from instantaneous soil-moisture conditions and to better capture the inherent soil-water retention capacity of different forest types, all field sampling was scheduled in May, i.e., at the end of the dry season immediately before the onset of the monsoon. At this time soils typically reach their lowest moisture after a prolonged dry period, thereby maximizing inter-type contrasts in water status. Notably, May also coincides with the pre-monsoon peak of litter accumulation (LA), which facilitates the capture of maximum litter-layer biomass and the most pronounced differences in soil-moisture conditions among forest types.

This approach ensures that the observed differences in SWS and SOCS are primarily driven by the inherent properties of the forest types (e.g., vegetation composition, soil structure, litter input) rather than short-term meteorological fluctuations. We have now explicitly stated this rationale in the revised Methods section to enhance clarity. We acknowledge that our single-time-point design cannot address seasonal or interannual variations, which indeed represent an important direction for future research. Thank you again for this insightful comment.

Comment 7: For PLS please better justify the selection of latent constructs or provide theoretical rationale for the proposed causal pathways. For me the grouping of variables into "litter," "soil structure," and "soil chemistry" constructs lacks empirical validation through confirmatory factor analysis. Also for multicollinearity treatment the removing of variables with Spearman's |r| > 0.8 is an arbitrary threshold that may eliminate ecologically meaningful relationships in my view. It would be better if the authors employ variance inflation factor (VIF) analysis or principal component regression for more rigorous multicollinearity assessment. 

Response 7：

We are deeply grateful to the reviewer for these insightful and constructive comments, which have significantly helped us improve the analytical rigor of our manuscript. We have thoroughly considered both points and implemented major revisions to our statistical approach accordingly. Please find our point-by-point response below.

1. Theoretical Rationale and Empirical Validation of Constructs:

We sincerely thank the reviewer for raising this important point. The theoretical rationale underpinning the proposed relationships between environmental factors and the soil carbon-water nexus was indeed outlined in the introduction (please refer to the third paragraph of the introduction in the original submission). To reiterate, we hypothesized that the litter layer, as a critical interface, governs coupled carbon-water dynamics by influencing water infiltration, evaporation, and serving as the primary source of soil organic carbon. Furthermore, the processes of litter decomposition and subsequent formation of soil aggregates were theorized to form a mechanistic framework linking plant inputs to the physical protection of carbon and the retention of water.

In our initial analysis, we assessed the convergent validity and internal consistency reliability of the reflective constructs, which met the statistical thresholds. However, in direct response to the reviewer's valid critique regarding the lack of empirical validation (specifically, discriminant validity), we conducted further diagnostic tests. These new tests revealed issues with discriminant validity, particularly between the 'litter matrix' and 'soil chemistry' constructs, confirming the reviewer's concern.

2. Revision of Analytical Strategy:

Given the issues with discriminant validity, combined with considerations of our sample size and model complexity, we agreed with the reviewer that the PLS-PM approach was not the most robust for our data. Consequently, we have made a significant revision to our manuscript: we have entirely removed the PLS-PM and variance decomposition analysis.

Instead, we have adopted a more straightforward and statistically robust suite of analyses:

One-way ANOVA combined with LSD post-hoc tests (now explicitly stating the use of the agricolae package) to determine the significance of differences in SOCS, SWS, and trade-off intensity across forest types and soil depths.

Partial correlation analysis (using the ppcor package) to disentangle the independent relationships between soil carbon storage, water storage, their trade-off intensity, and environmental factors, while controlling for key covariates (e.g., soil texture, topography).

We believe this revised approach provides clearer, more defensible, and easily interpretable results that directly address our research questions without the aforementioned methodological complexities.

3. Multicollinearity Assessment:

We appreciate the reviewer's suggestion for a more rigorous approach to multicollinearity. The |r| > 0.8 threshold was initially employed to retain ecologically meaningful variables that might be moderately correlated but still important, a common practice in ecological studies. In line with the reviewer's recommendation, we have now performed a Variance Inflation Factor (VIF) analysis for all environmental indicators included in our correlation and partial correlation analyses.

We are pleased to report that all VIF values were below the conservative threshold of 10. Specifically, only two variables (LDI and TN) had VIF values between 5 and 10, indicating moderate but acceptable levels of multicollinearity that do not adversely affect the stability of our interpretations. This new analysis confirms that our selected variables are suitable for the correlation-based analyses presented in the revised manuscript.

Once again, we extend our sincere thanks to the reviewer for their expert comments, which have greatly enhanced the quality and clarity of our work. We hope our detailed responses and substantial revisions are now satisfactory.

Comment 8: Please present all the software involved in results obtaining (section 2. Materials and methods)

Response 8：

We sincerely thank the reviewer for this valuable comment. We fully agree that transparency in statistical methods is crucial for reproducibility. As suggested, we have now explicitly detailed all software and R packages used for each statistical analysis in the revised "2.4. Statistical analysis" section.

The specific additions are as follows:

The nortest package was used for the Kolmogorov–Smirnov test to assess data normality.

The car package was used for Levene’s test to assess the homogeneity of variances.

The stats and agricolae packages were used for one-way ANOVA and the LSD post-hoc comparisons, respectively.

The lme4 package was employed to construct linear mixed-effects models (LMEs), which are the core of our analysis, allowing us to control for unmeasured plot-level variability by specifying plot as a random effect.

The ppcor package was used for partial correlation analysis to disentangle the independent relationships between key variables after controlling for confounding factors.

This comprehensive overview ensures that our analytical workflow is fully transparent and reproducible. We thank the reviewer for prompting us to improve the clarity of our methodology.

Comment 9: If possible please ensure volumetric or mass-based equivalents for meaningful interpretation (SOC/SWS)

Response 9：

Thank you for the suggestion. Because most comparative studies report soil water storage (SWS) as depth-equivalent water in millimetres (mm), we retain mm as the primary reporting unit to ensure cross-study comparability. We clarify this in the Methods and throughout the manuscript. Note that RMSD analyses use min–max–standardized values and are therefore unitless.

Comment 10: L341: Please check and verify this section. The factors shaping SOCS and SWS analysis shows concerning issues in my opinion: suspiciously high path coefficient (β = 0.98) suggesting overfitting, inconsistent confidence intervals contradicting significance levels, and unexplained GoF values (0.75, 0.72) lacking benchmark comparisons to justify model adequacy. 

Response 10：

We sincerely thank the reviewer for their meticulous examination and raising these critical points, which provided us with an opportunity to thoroughly re-evaluate our analytical approach. We agree that the initial PLS-SEM results presented in this section warranted further scrutiny.

The reviewer correctly identified that the high standardized path coefficients (e.g., β = 0.98) can be a cause for concern, often indicative of potential multicollinearity among predictor variables. We acknowledge that while such high coefficients do not necessarily denote a statistical error or overfitting within the PLS-SEM framework—and are indeed reported in published ecological literature (e.g., https://doi.org/10.1002/ldr.5495；https://doi.org/10.1016/j.scitotenv.2023.165557；https://doi.org/10.1016/j.gecco.2025.e03725)—they can complicate the interpretation of individual variable contributions. Furthermore, we appreciate the reviewer's point regarding the Goodness-of-Fit (GoF) index. Although values > 0.60 are sometimes used as a rule-of-thumb for adequate global model fit in PLS-SEM, the metric has been criticized and is increasingly deprecated in favor of more robust diagnostic criteria. We regret not providing clearer benchmarks for these values in our original manuscript.

The reviewer's concerns, particularly when considered alongside those raised in Comment 7, convinced us that the PLS-SEM approach, while valuable, might not be the most transparent or defensible method for our dataset and readership. Therefore, in direct response to this comment, we have taken the significant step of removing the entire PLS-SEM analysis from the revised manuscript.

To address the core research question—identifying the factors shaping SOCS and SWS—we have replaced the PLS-SEM with a more conventional and robust set of statistical analyses, the results of which are now presented in the revised Section 2.6 and visualized in new figures. We employ Linear Mixed-Effects Models (LMEs) to rigorously assess the influence of forest type, soil depth, and their interaction, while controlling for spatial heterogeneity using plot as a random effect. We use partial correlation analysis to disentangle the complex interrelationships between key soil properties, carbon, and water storage after accounting for the influence of covariates.

We are confident that this revised analytical strategy eliminates the concerns regarding overfitting, provides easily interpretable and statistically solid results (including confidence intervals), and offers a clearer, more direct answer to our research questions. We believe the manuscript is greatly improved as a result of the reviewer's insightful feedback.

Comment 11: L416-418: Please verify this statement as increased micro-aggregation typically enhances soil porosity and water retention capacity through improved pore size distribution, not the reverse 

Response 11：

We thank the reviewer for this insightful comment. We agree that increased micro-aggregation generally enhances soil porosity and water retention by improving pore size distribution. Upon careful re-examination of our data and the relevant literature, we have revised our interpretation to more accurately reflect the specific context of our findings.

The amended statement now reads:

“Although structural improvement is typically associated with synergistic increases in SOCS and SWS [68], this study observed that these two variables did not always change synchronously, and significant differences were found among forest types (Fig. 3, Fig. S2). One possible explanation is that litter input increased the proportion of large aggregates (> 2 mm) and aggregate stability [64], yet under these specific conditions, it may have concurrently reduced the abundance of micro-aggregates and capillary porosity, potentially diminishing soil water retention capacity to some extent.”

We have incorporated terms such as “one possible explanation” and “may” to appropriately qualify the proposed mechanism and avoid overgeneralization. Thank you again for prompting this important clarification.

 

Comment 12: Please better sustain the attribution of age-related changes in SOCS and SWS to reduced density, lower physiological water demand and gradual improvement in soil structure to sustain the mechanism, otherwise it seems as a speculative interpretation beyond  observational data 

Response 12：

We thank the reviewer for this important point about attribution. In the revised manuscript, we first clarify that across all forest types, stand age has no significant effect on SOCS and SWS, whereas a positive age effect is observed only within coniferous stands (Section 4.1, para. 2). To avoid over-interpretation beyond observational evidence, we have toned down causal language and now present the mechanisms as plausible explanations supported by our limited data and literature. Specifically, we note that (i) early afforestation stages are characterized by strong soil disturbance/erosion and low inputs from litter and roots, which commonly lead to lower SOCS in young stands [56]; and (ii) with stand development, litter accumulation increases, as indicated by rising IWAR and ESC values in our dataset (Fig. S1), together with potentially lower soil-respiration losses [57], which together can facilitate SOCS accrual.

For SWS, we emphasize that soil water is critical for tree growth [4], especially in the water-limited Central Yunnan region. In our study, SWS in Pinus yunnanensis stands increases with age, a pattern that differs from the age-related declines reported for apple orchards on the Loess Plateau [21] and Korean pine forests [43]. We interpret this difference as being consistent with the age-related increase in vegetation/canopy cover observed in our sites (Table S1), which likely reduces direct solar radiation and soil evaporation while enhancing canopy interception and rainfall infiltration. By contrast, studies reporting declining SWS with age often involve low canopy cover, excess deep-root water uptake, and/or persistent drought conditions [21].

Importantly, because reduced stand density, lower physiological water demand, and gradual improvement in soil structure were not directly measured in our dataset, we do not claim them as definitive causes. Instead, we explicitly frame them as possible contributors that are consistent with the observed patterns and the literature, and we mark such statements with qualifying terms (e.g., “may,” “likely,” “plausibly mediated by…”). These revisions are now incorporated in Section 4.1, paragraph 2 (Fig. S1; Table S1) and are highlighted in the manuscript.

 

Comment 13: In my opinion  RMSD measures deviation magnitude but does not inherently quantify ecological trade-offs or their intensity. Please better consider or sustain

Response 13：

We sincerely thank the reviewer for this insightful comment, which allows us to better clarify the ecological rationale behind our choice of metric. We agree that the Root-Mean-Square Deviation (RMSD) is, at its core, a measure of deviation. However, as applied in our study and in a well-established body of literature on ecosystem service trade-offs, it has been effectively used to operationalize and quantify the intensity of a trade-off.

The key ecological interpretation lies in the reference point against which the deviation is measured. In our methodology, we do not simply calculate deviation from a mean; we specifically calculate the deviation of each observation (a soil sample) from the 1:1 ideal line in a standardized carbon-water space. This is a critical distinction.

A point lying on the 1:1 line represents a state of perfect balance or synergy, where a system delivers equally high (or low) levels of both carbon storage and water retention.

The Euclidean distance from this line directly quantifies the degree of imbalance. A larger distance indicates a stronger deviation from this balanced state, which we interpret as a more intense trade-off (where one service is high at the expense of the other) or a more intense synergy (where both are low). The RMSD then aggregates this across all samples to give a population-level measure of trade-off intensity.

As we now explicitly state in the revised introduction (final paragraph), this approach is not novel to our study but is a recognized and robust method in sustainability science. It has been widely used to quantify the balance between various ecosystem service pairs (e.g., carbon storage vs. water yield, biodiversity vs. agricultural production) because it is simple, dimensionless, and robust to non-linear responses [17,42,43]. It effectively translates the complex concept of a "trade-off" into a quantifiable geometric distance.

We have added these clarifications and key references to the manuscript to better sustain our analytical choice. We fully agree with the reviewer that future research could develop even more nuanced metrics, and we have now included a sentence to that effect. However, we believe the RMSD approach provides a transparent, reproducible, and ecologically meaningful measure for the purposes of our study.

Comment 14: Thee authors acknowledge geographic limitations but not enough address the temporal constraints, seasonal variability, or the space-for-time substitution assumptions that  limit the conclusions 

Response 14：

We sincerely thank the reviewer for raising this important point regarding the temporal dimension and sampling design. We fully agree that multiple sampling time points are essential to fully capture seasonal and interannual variations in soil moisture dynamics. In response to this comment, we have revised the manuscript to more explicitly acknowledge the temporal limitations of our study and to further clarify the rationale behind our sampling strategy.

As noted in our response to Comment 6, the primary objective of this study was to compare the inherent soil water retention capacity and carbon sequestration potential across different forest restoration types, rather than to document their complete temporal dynamics. To maximize comparability and minimize the influence of transient meteorological conditions, all field sampling was strategically conducted in May (at the end of the dry season before the monsoon onset). During this period, soil moisture typically reaches its seasonal minimum after a prolonged dry spell, thereby maximizing the contrast in water status among different forest types. Additionally, May coincides with the pre-monsoon peak in litter accumulation, enabling us to capture peak litter biomass and the most pronounced differences in soil moisture conditions across forest types. This approach ensures that the observed differences in soil water storage (SWS) and soil organic carbon storage (SOCS) are primarily attributable to the inherent properties of the forest types (e.g., vegetation composition, soil structure, litter input) rather than short-term weather fluctuations. We have clarified this rationale in the revised Methods section. We explicitly acknowledge that the single-time-point design cannot reflect seasonal or interannual dynamics, and these aspects represent important directions for future research. As emphasized in the final paragraph of Section 4.3: "Future studies should focus on the long-term dynamics and seasonal variations of soil carbon–water relationships across different plant communities, particularly by integrating root distribution, water-use strategies, and microbial functional processes. Such work is crucial to unveil the driving mechanisms behind carbon–water couplings and to inform the restoration and sustainable management of degraded ecosystems."

Regarding the space-for-time substitution assumption that may limit conclusions, we have removed this hypothesis based on our actual sampling design. We have shifted the focus from emphasizing the impact of vegetation restoration on soil carbon–water coupling to studying the distribution, trade-offs, and influencing factors of soil carbon and water across typical forest types. Using partial correlation analysis and mixed-effects models, we confirmed the effects of forest type and soil depth on SOCS and SWS (Fig. 4 and Table 1). However, based on the results of partial correlation analysis (Figs. S3 and S4), in Section 4.4 of the Discussion, we also highlight that the significant effects of forest type and soil depth on SOCS and SWS in this study may have overshadowed the potential effects of topography and soil texture (Fig. 4, Figs. S3, S4; Table 1). Although previous studies have reported significant effects of elevation, slope, and indirectly resulting climatic differences on both parameters [11], in our study area, the low relief amplitude and minimal slope variation (Fig. 1) result in insignificant climatic differentiation. Thus, the variations in SOCS and SWS are primarily driven by forest type and soil depth (Table 1). Although significant correlations were observed between SWS and topography/soil texture without considering background differences (Fig. S3), after controlling for forest type or topographical and textural covariates, significant correlations were only found between SWS and SOCS as well as soil C/N ratio in the 40–60 cm soil layer (Fig. 4). This indicates that SWS is interactively regulated by multiple factors [11]. However, after accounting for the interactive effects of forest type and soil depth, the influences of topography and soil texture on SWS were not significant (Table 1), suggesting that forest type and soil depth exert stronger effects on SWS than topographic and edaphic factors. Nevertheless, the sensitivity of SWS spatial distribution to topographic variations should not be overlooked [19]. Future studies should be conducted to determine optimal community-topography configuration patterns for suitable vegetation restoration in the Yunnan Plateau and similar ecoregions.

We are grateful to the reviewer for this constructive suggestion, which has helped us improve the clarity and methodological rigor of the manuscript.

 

Comment 15: Please consider in the discussion section to better integrate the relevant data from available literature to establish more comparative/criticist discussions. Also, please pay attention for conclusion and reconsider after improvements

Response 15：

We sincerely thank the reviewer for these insightful suggestions. We have thoroughly revised the Discussion and Conclusion sections to better integrate comparative and critical perspectives from the literature and to ensure our conclusions are well-supported by the enhanced analysis. Key improvements made:

In Sections 4.1 and 4.2, we expanded the discussion on the effects of forest type and soil depth on SOCS and SWS by incorporating relevant comparative data from recent literature. This includes a more critical examination of how litter quality and soil properties—shaped by forest community characteristics—drive the observed differences in carbon sequestration and water retention across restoration types.

In Section 4.3, we strengthened the discussion on the direction and strength of soil carbon–water coupling, placing our findings within the broader context of existing mechanistic frameworks and highlighting both consistencies and discrepancies with previous studies.

In Section 4.4, we further addressed uncertainties surrounding SWS influences. While Table 1 indicates that terrain and soil texture did not exhibit significant effects on SWS after accounting for forest type and soil depth, we nevertheless emphasize that these factors should not be disregarded. We explicitly call for future research to determine optimal community-topography configurations for vegetation restoration across the Yunnan Plateau and similar ecoregions.

In the Conclusion, we refined our final takeaways to more clearly articulate data-supported practical implications. Specifically, we highlight that—based on trade-off analysis and partial correlation results—restoration practices in water-limited regions like the study area should prioritize low-water-use, high-litter-quality broadleaved or mixed forests. These communities enhance aggregate stability and moderate soil organic nitrogen levels, thus promoting carbon–water synergy in surface soils, mitigating trade-offs in intermediate layers, and preventing excessive water consumption in deep soils. We conclude by outlining future research priorities aimed at unraveling the interactions between litter quality, soil properties, and carbon–water trade-offs across diverse forest types under varying site conditions.

We believe these revisions have significantly improved the depth, critical perspective, and practical relevance of our discussion and conclusions. Thank you again for these valuable comments.

Reviewer 3 Report (New Reviewer)

Comments and Suggestions for Authors

Revision report 
Journal: Forests (ISSN 1999-4907)
Manuscript ID: forests-3827161
Type: Article
Title: Soil carbon–water trade‑off relationships and driving mechanisms in different forest types on the Yunnan Plateau, China.
General Comments
This manuscript investigates the interactions between soil organic carbon storage (SOCS) and soil water storage (SWS) under different forest restoration types on the Yunnan Plateau, China. By combining field measurements with structural equation modeling, the study evaluates trade-offs and synergies between SOCS and SWS, while also examining the roles of litter traits, soil chemical attributes, and soil structural properties. The topic is relevant and timely, addressing pressing questions related to ecosystem restoration, carbon–water coupling, and sustainable forest management.
Title, Abstract, and Keywords
1.    The title and abstract clearly present the scope of the study and its main findings.
2.    The keywords could be optimized to improve indexing. For instance, avoid repeating terms already present in the title, since those are already indexed.
3.    It would be beneficial to clarify the study’s hypotheses in the abstract, ensuring that readers understand the research framework from the outset.
Introduction
Overall, the introduction is solid in terms of literature review and scientific framing. The authors clearly identify the knowledge gap and formulate testable hypotheses. However, the flow and clarity could be improved to enhance readability.
4.    L51–52: The use of “Conversely” when citing Chen et al. is not accurate. A more precise wording would be “More specifically, Chen et al. reported that …
5.    The paragraph discussing deep-rooted plantations should be clarified. A simplified causal chain would help readers follow the logic: deep roots → higher water consumption → dry soil layers → reduced sustainability of SOC retention and ecosystem stability.
6.    The sentence “with carbon loss further driving continuous water depletion” is confusing. It would be clearer to frame this as a feedback loop: less water → less carbon → even less water retained.
Results and Discussion
7.    The results are robust and supported by solid statistical evidence, which provides confidence in the reliability of the findings. The discussion is comprehensive, offering rich mechanistic insights and establishing clear connections with the relevant scientific literature.
8.    Given the large number of variables examined, it would be highly beneficial to include a conceptual schematic diagram that integrates the relationships tested in this study while also highlighting hypothetical interactions and areas that remain to be explored in future research. This would enhance clarity and provide readers with a more accessible overview of the study’s contributions and research gaps.
Overall Recommendation: Major revisions. The manuscript presents valuable data and relevant insights, but several sections require clarification, improved readability, and additional synthesis (e.g., a conceptual diagram). Addressing these revisions will significantly strengthen the clarity, robustness, and impact of the study.

Sincerely,

Comments on the Quality of English Language

The English language is clear and professional, but certain sections would benefit from minor polishing to improve readability and flow. In particular, some sentences in the introduction and discussion are overly long and complex, which could be simplified for better clarity

Author Response

Comment 1: The title and abstract clearly present the scope of the study and its main findings. 

Response 1：

We thank the reviewer for affirming the clarity of our title and abstract. In light of this comment, we did not modify the title. To ensure consistency with the main text revised in response to other comments, we made targeted refinements to the abstract, without altering the study’s content or conclusions.

 

Comment 2: The keywords could be optimized to improve indexing. For instance, avoid repeating terms already present in the title, since those are already indexed. 

Response 2：

We appreciate the reviewer’s suggestion on optimizing the keywords to improve indexing. In response, we revised the keywords to emphasize key variables and processes while reducing overlap with the title. The updated keywords are: soil organic carbon; soil water storage; carbon–water trade-offs; vegetation restoration; Central Yunnan Plateau. We retained “carbon–water trade-offs” and “Central Yunnan Plateau” as domain-defining terms to facilitate topic- and region-specific retrieval across databases, while the remaining terms broaden discoverability.

 

Comment 3: It would be beneficial to clarify the study’s hypotheses in the abstract, ensuring that readers understand the research framework from the outset. 

Response 3：

We thank the reviewer for this constructive suggestion. To clarify the research framework from the outset, we have explicitly stated the study’s hypotheses in the abstract (third sentence) and defined all acronyms at first mention. The added sentence reads:

“We hypothesize that, relative to SRF, both SOCS and SWS increase across forest types; however, the direction and strength of the SOCS–SWS trade-off differ among plant communities and are regulated by litter traits and soil structural properties.”

These changes improve clarity without altering the study design or conclusions.

 

 

Comment 4: Overall, the introduction is solid in terms of literature review and scientific framing. The authors clearly identify the knowledge gap and formulate testable hypotheses. However, the flow and clarity could be improved to enhance readability. 

Response 1：

We appreciate the reviewer’s positive assessment of our introduction and the helpful suggestion to improve flow and clarity. Accordingly, we rewrote the first half of Paragraph 2 in the Introduction to (i) foreground the overall uncertainty and context dependence of soil carbon–water responses to vegetation restoration/land-use change, and then (ii) present the literature in a two-strand structure:

Synergy strand (surface/early stages): studies reporting concurrent increases in soil water and topsoil SOCS due to moisture-enhanced organic matter accumulation and microbial processes, and noting that carbon losses can, in turn, reduce soil moisture (refs [9–11]).

Trade-off strand (deep layers/plantation types): evidence that deep-rooted plantations or orchards (e.g., Robinia pseudoacacia, apple) increase SOC while depleting deep soil water and forming persistent dry layers; we also summarize cases of long-term natural succession and cropland conversion that constrain SOC gains via moisture declines, as well as instances of minor effects (refs [12–18]).

 

Comment 5: L51–52: The use of “Conversely” when citing Chen et al. is not accurate. A more precise wording would be “More specifically, Chen et al. reported that …

Response 5：

We sincerely thank the reviewer for this insightful comment. We agree that the use of the word "Conversely" may have oversimplified the nuanced relationship reported by Chen et al. and that their findings should be more precisely contextualized within the broader literature. We now delimit the conditions under which synergy is observed (early restoration stages or surface soils) and avoid implying a direct contradiction. The revised sentence reads:

“On the one hand, some studies have observed synergistic improvements during the early stages of restoration or in surface soils, whereby higher moisture promotes organic matter accumulation and microbial processes, thereby increasing topsoil soil organic carbon storage (SOCS) [9–11], whereas losses of soil carbon can also reduce soil moisture [12].”

We intentionally do not single out Chen et al. in this sentence; instead, we frame the literature to emphasize scenario-specificity and then proceed to the depth- and vegetation-type–dependent evidence in subsequent sentences. These changes improve precision and readability.

 

Comment 6: The paragraph discussing deep-rooted plantations should be clarified. A simplified causal chain would help readers follow the logic: deep roots → higher water consumption → dry soil layers → reduced sustainability of SOC retention and ecosystem stability.

Response 6：

We thank the reviewer for suggesting a clearer presentation of the mechanism for deep-rooted plantations. In the revised Introduction, we front-load a simplified causal chain to guide readers through the logic—deep roots → higher water consumption → dry soil layers → reduced sustainability of SOC retention and ecosystem stability—and then summarize the supporting evidence. Specifically, we now state that deep-rooted plantations or orchards (e.g., Robinia pseudoacacia, apple) often enhance carbon accumulation while markedly depleting deep soil water and forming persistent dry layers, thus exhibiting a characteristic carbon–water trade-off [13–15]. We further note that long-term natural succession can similarly increase SOC while drawing down soil moisture [16], and that conversion of sloping cropland to orchards or forests frequently causes pronounced soil-moisture declines that constrain SOC gains [17,18]. These revisions improve the mechanistic clarity and reading flow without altering our conclusions.

 

Comment 7: The sentence “with carbon loss further driving continuous water depletion” is confusing. It would be clearer to frame this as a feedback loop: less water → less carbon → even less water retained.

Response 7：

We appreciate the reviewer’s suggestion to frame the mechanism as a feedback loop. In the revised manuscript, we removed the ambiguous clause (“with carbon loss further driving continuous water depletion”) and recast the argument to highlight a reinforcing feedback—less water → constrained SOC accrual (less carbon) → even less water retained. Concretely, we now state:

“Long-term natural succession may increase SOCS but is often accompanied by declines in soil moisture, thereby constraining the long-term gains in SOCS[16]. Similarly, converting sloping cropland to orchards or forests often causes substantial reductions in soil moisture, resulting in only limited increases in SOCS[17,18]. Some studies have also reported that, in certain contexts, land-use change has no significant effect on either SOCS or SWS[11].”

These changes improve mechanistic clarity and readability while preserving our conclusions.

 

Comment 8: Given the large number of variables examined, it would be highly beneficial to include a conceptual schematic diagram that integrates the relationships tested in this study while also highlighting hypothetical interactions and areas that remain to be explored in future research. This would enhance clarity and provide readers with a more accessible overview of the study’s contributions and research gaps. 

Response 8：

We thank the reviewer for this excellent suggestion. We completely agree that a conceptual schematic diagram would be a valuable addition to synthesize the complex relationships examined in this study and to highlight potential interactions and future research directions. We acknowledge that such a figure would greatly enhance the clarity and accessibility of our work for readers.

We  carefully considered this addition; however, because the relationships examined are context-dependent across forest types and soil depths, a single diagram would risk over-simplifying key pathways and potentially misrepresenting site-specific mechanisms. To preserve accuracy and clarity, we instead keep the synthesis in the textual framework (Introduction and Discussion), where we delineate the tested relationships and uncertainties in greater nuance. If the editor deems a schematic essential, we would be happy to prepare a concise version for the Supplementary Material at a later stage.

Round 2

Reviewer 2 Report (Previous Reviewer 1)

Comments and Suggestions for Authors

Dear Authors,

Thank you very much considering my recommendations and improving your manuscript. Reading carefully the manuscript I have noticed that there are few things that should be considered in discussions section. Please find them listed below.

1. L390: In my opinion the claim that broadleaf forests show significant increases in SOCS at 20-40 cm and 40-60 cm is oposite  established pedogenic processes. In my opinion without controlling for bioturbation, illuviation, or cryoturbation, this depth distribution pattern cannot be attributed solely to forest type. Please improve formulation
2. L392-395: In my opinion the authors should also consider here that their results could differ also due to potential confounding variables such as stand density, management history, or soil parent material - all these could explain the discrepancy
3. In next, I think that attribution of lower SOCS in conifer plantations solely to high lignin content and low decomposition rate without considering mycorrhizal associations could be a mistake. Up to my knowledge the coniferous species predominantly form ectomycorrhizal relationships that can actually enhance soil carbon stabilization through different pathways than the arbuscular mycorrhizal networks typical of broadleaf species. I recommend for authors to consider that in their discussion senction
4. L447-450: In my opinion this statement should be well sustained including also enough temporal precedence data
5. L461-469: This statement should be better sustained by priming effect measurements or microbial biomass data. Otherwise it should be reconsidered/reformulated

Author Response

Comment 1: L390: In my opinion the claim that broadleaf forests show significant increases in SOCS at 20-40 cm and 40-60 cm is oposite  established pedogenic processes. In my opinion without controlling for bioturbation, illuviation, or cryoturbation, this depth distribution pattern cannot be attributed solely to forest type. Please improve formulation. 

Response 1：

We sincerely thank the reviewer for this insightful comment. We agree that the observed pattern of SOCS accumulation in deeper soil layers (20–40 cm and 40–60 cm) under broadleaf forests appears unusual when considered in isolation from comparative context, as it seemingly contrasts with established pedogenic processes. As the reviewer rightly pointed out, such depth distributions could indeed be influenced by processes including bioturbation, illuviation, or cryoturbation, and should not be attributed solely to forest type without adequate justification.

In response to this comment, we have revised the relevant sentence in the manuscript to clarify that the comparison is made against the short-rotation forest (SRF) baseline, not that broadleaf forests inherently accumulate more SOC at depth in an absolute sense. The original phrasing may have implied a general property of broadleaf forests rather than a relative difference compared to a degraded land use type.

Revised Manuscript Text:

"Notably, compared to SRF, broadleaf forests exhibited significant increases in SOCS not only in the surface layer but also at 20–40 cm and 40–60 cm depths (Figure 2a). This depth distribution pattern differs from many earlier reports in which organic carbon accumulation was predominantly concentrated in the 0–20 cm surface layer[49,50]."

This reformulation emphasizes that the observed deeper SOCS accumulation is a relative increase compared to SRF—which exhibits very low carbon stocks across all depths—rather than an absolute deviation from typical pedogenic expectations. We agree with the reviewer that the processes they mentioned could influence depth distribution, and in the discussion, we have expanded our consideration of these factors (Lines 410–418). However, the strong contrast with SRF suggests that forest type, through its influence on litter quality, root distribution, and microbial community, can still play a significant role in shaping vertical SOCS patterns, even after accounting for other background pedogenic processes.

We believe this revised formulation is more precise and thank the reviewer again for helping us improve the clarity of our argument.

 

Comment 2: L392-395: In my opinion the authors should also consider here that their results could differ also due to potential confounding variables such as stand density, management history, or soil parent material - all these could explain the discrepancy. 

Response 2：

We thank the reviewer for raising this important point. We fully concur that confounding variables such as stand density, management history, and soil parent material could potentially contribute to the differences in SOCS observed among forest types.

While these factors may exert some influence (as partially reflected in Table S1), our statistical analyses were designed to clarify the dominant role of forest type. Specifically, partial correlation analysis (controlling for other confounding factors or conditional on forest type, see Figures 4, S3, and S4) and mixed-effects models (incorporating confounding factors, specifically topography and texture, as random effects; see Table 1) consistently identified forest type as a primary and significant driver of SOCS variation.

Therefore, we propose that the observed pattern is most likely attributable to the intrinsic properties of coniferous litter. As reported, coniferous litter typically decomposes more slowly than broadleaf litter (Figure S1), likely due to its higher lignin content, which may inhibit microbial breakdown and the subsequent transfer of carbon into mineral soils[51]. In response to the reviewer’s comment, we have refined the relevant statements in the manuscript to reflect a more cautious interpretation and have explicitly acknowledged the potential influence of the confounding factors noted by the reviewer. The revised text now reads:

“This distribution pattern may be partly influenced by confounding site and stand attributes (Table S1); however, results from partial correlation analysis (Figures 4, S3, S4) and mixed-effects models (Table 1) indicate that forest type remains the dominant factor governing SOCS variation. Thus, we speculate that this pattern may be associated with the properties of coniferous litter, which—compared to broadleaf litter—generally exhibits higher lignin content, slower decomposition rates (Figure S1), and consequently, constrained microbial breakdown and carbon transfer into mineral soils[51].”

 

Comment 3: In next, I think that attribution of lower SOCS in conifer plantations solely to high lignin content and low decomposition rate without considering mycorrhizal associations could be a mistake. Up to my knowledge the coniferous species predominantly form ectomycorrhizal relationships that can actually enhance soil carbon stabilization through different pathways than the arbuscular mycorrhizal networks typical of broadleaf species. I recommend for authors to consider that in their discussion senction. 

Response 1：

We sincerely thank the reviewer for this highly insightful comment. We fully agree that mycorrhizal associations represent a key mechanism mediating soil carbon dynamics and that attributing lower SOCS in conifer plantations solely to litter chemistry (e.g., high lignin content and slow decomposition) represents an oversimplification. Different mycorrhizal types may influence the formation and stabilization of mineral-associated organic carbon through pathways such as root exudation, fungal necromass accumulation, enzymatic activities, and interactions with soil aggregates and minerals.

Current evidence on whether ECM-dominated ecosystems generally store more soil carbon than AM-dominated systems remains context-dependent and mixed (e.g., Wu et al., 2022; Lu et al., 2025). ECM tree species also tend to have lower litter quality (higher C:N) and slower decomposition, which can modify SOM inputs and turnover; our litter trait indicators (Fig. S1) are consistent with this pattern. Meanwhile, AM-dominated communities often exhibit higher tree diversity, and AM versus ECM leaf/root substrates differ in both decomposition rates and environmental sensitivity, potentially shifting the relative contributions of POM and MAOM. Accordingly, in the revised Discussion we continue to treat differences in litter chemistry as an important mediator of SOCS contrasts, while also emphasizing the possibility that ECM systems may contain proportionally more POM than MAOM.

In response to this comment, we have revised the Discussion to incorporate a more balanced and mechanistic interpretation:

“While mycorrhizal associations may also mediate SOCS differences among forest types[52], the typically lower tree diversity and slower litter decomposition in ECM-dominated systems may favor increases in particulate organic matter (POM) rather than mineral-associated organic matter (MAOM)[53]. To better understand soil-carbon dynamics across forest types, further research is needed on how mycorrhizal affiliation influences SOC accumulation.”

 

Comment 4: L447-450: In my opinion this statement should be well sustained including also enough temporal precedence data. 

Response 2：

We thank the reviewer for raising this important point. We agree that temporal precedence data would further strengthen the statement in Lines 447–450. We acknowledge that the original wording may have implied a causal interpretation. However, as our study is based on a space-for-time substitution approach and synchronic measurements, our design does not include longitudinal data that would be needed to definitively establish the directionality of the relationships between soil structural indicators and carbon-water trade-offs. Therefore, we have revised the wording to emphasize correlation rather than causation. The text has been modified as follows:

“In the mid- and deep layers, SOCS is negatively associated with BD and PAD but positively associated with MWD, whereas in the surface layer the associations between soil structural indicators and SOCS are relatively weak. In the 20–40 cm layer, the carbon–water trade-off intensity shows a negative association with TN but a positive association with BD (Fig. 4). This pattern is consistent with findings reported for arid and semi-arid regions[11,13,43].”

 

Comment 5: L461-469: This statement should be better sustained by priming effect measurements or microbial biomass data. Otherwise it should be reconsidered/reformulated

Response 5：

We thank the reviewer for this insightful comment. We agree that direct measurements of priming effects or microbial biomass data would provide stronger support for the mechanistic explanation regarding microbial mining of native SOC. As our study did not include these specific measurements, we have reconsidered and reformulated the corresponding paragraph (Lines 461-469) to present this mechanism more cautiously as a hypothetical scenario rather than a definitive explanation. The revised text now emphasizes the correlation between litter quality and the observed patterns, and frames the microbial mechanism as a potential possibility that requires future validation. We believe this modification aligns the speculation with the available evidence:

“A plausible explanation is that could explain this pattern is that litter inputs increase the proportion and stability of macroaggregates (> 2 mm)[66], but might concurrently reduce microaggregate abundance and capillary porosity in some contexts, thereby potentially limiting plant-available water. Furthermore, the slow decomposition of high-C/N litter could induce nitrogen limitation, which might potentially stimulate microbial communi-ties to utilize more native SOC[63], a process that could intensify water use during carbon sequestration. However, this specific mechanism requires further verification through direct measurements of priming effects and microbial dynamics.”

 

We sincerely thank the reviewers and the editorial team for their meticulous evaluation and valuable, insightful suggestions, which have markedly improved the manuscript’s logical coherence and academic quality and provided important guidance for our re-search.

Reviewer 3 Report (New Reviewer)

Comments and Suggestions for Authors

The authors have substantially improved the presentation of their manuscript and have adequately addressed the main suggestions raised in the previous review. The revised version is clearer, better structured, and provides stronger support for its conclusions.

Sincerely,

Author Response

Dear Reviewer,
We are truly grateful for your kind and encouraging feedback on our revised manuscript. Your recognition of the improvements we've made means a great deal to us.
We've put in significant effort to address the previous suggestions, aiming to present our work in a more comprehensive and coherent manner. Your comment that the revised version is clearer, better structured, and offers stronger support for the conclusions has motivated us even further.
We will continue to refine the manuscript based on any remaining details or potential enhancements that might arise during the publication process. Once again, we appreciate your time and expertise in reviewing our work, and we look forward to seeing it published with the help of your valuable input.
Thank you sincerely.

This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Dear Authors,

Please find below my recommendations for "Divergent soil carbon-water trade-off relationships and underlying mechanisms during vegetation restoration in the Yunnan Plateau" manuscript:

Introduction:

• L43-45: Since this statement is the central theme of this manuscript, it would be advisable for readers to be familiar with the mechanical link between carbon pools and hydrologic processes
• L49-50: The manuscript should be more specific and the statement to be sustained by clear examples/case examples/numerical examples, etc. up to case
• The manuscript present in the abstract the "coupled dynamics of soil organic carbon stocks (SOCS) and soil water storage (SWS)) following subtropical vegetation restoration" as a knowledge gap but the authors after that (starting from L51....) present numerous results resulted from other studies which could become confusing for readers. I recommend to better highlight the identified knowledge gaps instead of being to narrative

Materials and methods:

• L151-159: The manuscript should clarify whether the seven forests selected for study represent actual independent blocks or pseudo-replicated plots extracted from a single slope
• Please better clarify how were considered in this research the forest ages, land-use history, micro-topography, management, etc.  
• Please consider to introduce information about the slop angle, aspect, and lithology
• L187-188: Please justify the selection of this time intervals
• Please clarify if SOC and SWS are sampled to 60 cm (aggregated into 0–20, 20–40, 40–60 cm layers),  and the bulk density (BD) is reported only once per layer and assumed constant within forest types. In my opinion the spatial BD heterogeneity at small scales (<5 m) typically could exceeds 10 %, so in that case the cumulative SOCS error could be underestimated

Results and Discussions:

• L268: The PCA only in a narrative manner states that “PC1 explained 60.9 %” ...., but in my opinion the full eigenvalue table and variable loadings should be provided (at least in supplementary material)
• Phrases such as “markedly lower”/“significant improvement”/“continuous increase” should be accompanied by numerical and statistical metrics
• Please better clarify if the chronosequence sites are edaphically or topographically comparable

Conclusions

In my opinion, statements that certain forest types “markedly enhance nutrient availability” or “support long-term carbon-moisture synergy” are too exaggerated, as long-term processes have not been directly monitored.

Author Response

Response to Reviewer1:

 

Introduction

• L43-45: Since this statement is the central theme of this manuscript, it would be advisable for readers to be familiar with the mechanical link between carbon pools and hydrologic processes

Response:

We thank the reviewer for this constructive suggestion. In the introduction (after the sentence at L43–45), we have added a concise mechanistic summary clarifying how soil organic carbon (SOC) and soil water are coupled through soil structure, pore networks, plant–litter inputs, and microbial processes. The revised passage now reads as follows (added text in bold):

Within forest ecosystems, soil organic carbon storage (SOCS) and soil water storage (SWS) are critical to soil fertility and vegetation productivity [3]. Their magnitudes, qualities, and complex coupling relationships profoundly influence and regulate associated biogeochemical processes and ecosystem functions [4,5].

• L49-50: The manuscript should be more specific and the statement to be sustained by clear examples/case examples/numerical examples, etc. up to case

Response:

We appreciate this helpful suggestion. We have revised the passage at L49–50 to add concrete mechanistic examples, land-use/vegetation cases, and depth-resolved patterns, with supporting citations. Specifically, we now (i) distinguish topsoil (0–20 cm) from subsoil (20–200 cm) responses, (ii) cite deep-rooted plantations (e.g., Robinia pseudoacacia, apple orchards) that increase SOC but deplete soil water and form dry layers, and (iii) provide cases from natural succession and cropland conversions.

• The manuscript present in the abstract the "coupled dynamics of soil organic carbon stocks (SOCS) and soil water storage (SWS)) following subtropical vegetation restoration" as a knowledge gap but the authors after that (starting from L51....) present numerous results resulted from other studies which could become confusing for readers. I recommend to better highlight the identified knowledge gaps instead of being to narrative

Response:

Thank you for this important point. We have revised the Introduction to explicitly delineate the scope of the knowledge gap and to reduce narrative listing. In particular, we now clarify that most empirical evidence summarized from L51 onward is derived from the Chinese Loess Plateau, a semi-arid region with deep loess parent material and distinct hydropedologic regimes. Whether those SOCS–SWS coupling patterns hold under humid subtropical vegetation restoration—typical of the Yunnan Plateau, with higher rainfall, highly weathered soils, and broadleaf/mixed forest trajectories—remains insufficiently tested. We therefore streamlined the literature summary and state that contrasting outcomes likely reflect differences in climate, species selection, restoration age, and soil depth, but that a systematic, depth-resolved comparison across forest types and stand-age gradients in humid subtropical regions is still lacking. Our study is designed to address precisely this gap.

Materials and methods:

• L151-159: The manuscript should clarify whether the seven forests selected for study represent actual independent blocks or pseudo-replicated plots extracted from a single slope

Response:

Thank you for the suggestion. Our plots are independent blocks, not pseudo-replicated subsamples from one slope. As clarified in the Methods, for each forest type we delineated three spatially independent forest patches and established one 20 m × 20 m plot per patch—i.e., plots were not repeated subsamples on the same slope. Within each plot, litter was sampled along upper/middle/lower slope positions. In the analyses, we further controlled residual heterogeneity by standardizing elevation, slope, silt, and clay and including plot identity as a random intercept in the mixed-effects models. These clarifications are now included in the revised Methods text.

• Please better clarify how were considered in this research the forest ages, land-use history, micro-topography, management, etc.  

Response:

Thank you for this suggestion. We have clarified these items in the Methods as follows:

 

Stand ages were obtained from local planting/enrichment records and field verification. For Pinus yunnanensis, we analyzed three age classes—PY9 (young), PY22 (near-mature), and PY60 (mature)—selected for data availability/accessibility and representativeness of the local restoration trajectory. For all plantation forests, the pre-afforestation land use was sloping rainfed farmland (SRF); this information is recorded for each plot. Within each plot, litter sampling was stratified along upper, middle, and lower slope positions. In the statistical analyses, elevation and slope (together with silt and clay) were standardized and included as covariates to control residual topographic/edaphic heterogeneity. Field verification confirmed long-term protection of all plots with no recent anthropogenic management or disturbance (e.g., tending/thinning, fertilization, grazing exclusion, understory clearing, fire), as stated in the Methods (see Table S1).

• Please consider to introduce information about the slop angle, aspect, and lithology

Response:

Thank you for the suggestion. We have added per-plot slope angle (°), aspect, and lithology/parent material in Table S1 (Supplementary Information) and referenced this in the Methods. This clarifies site conditions for all plots.

• L187-188: Please justify the selection of this time intervals

Response:

Thank you for the suggestion. We have clarified our rationale in the Methods. Specifically, the intervals 0.25–24 h were chosen to (i) resolve the fast, early-time adsorption phase with dense sampling ≤2 h, (ii) track the slower approach to near-equilibrium with wider, approximately log-spaced intervals ≥4–24 h, and (iii) include a 24-h endpoint as a practical near-saturation reference, beyond which litter water uptake was observed to remain essentially stable in preliminary trials. The revised text now reads:

“To capture the rapid changes during the initial adsorption phase (≤2 h) and the slower approach to equilibrium at later stages (≥4–24 h)—and given that water uptake remains essentially stable beyond 24 h—oven-dried litter was placed in nylon mesh bags (45 cm × 30 cm) and submerged in water for preset durations of 0.25, 0.5, 1, 2, 4, 6, 8, 12, and 24 h.”

• Please clarify if SOC and SWS are sampled to 60 cm (aggregated into 0–20, 20–40, 40–60 cm layers),  and the bulk density (BD) is reported only once per layer and assumed constant within forest types. In my opinion the spatial BD heterogeneity at small scales (<5 m) typically could exceeds 10 %, so in that case the cumulative SOCS error could be underestimated

Response:

Thank you for this helpful clarification request. We have made the sampling depth and BD treatment explicit in the Methods.

Thank you for the comment. We have clarified in the Methods that SOC and SWS were sampled to 60 cm and analyzed by 0–20, 20–40, and 40–60 cm layers, with 0–60 cm values obtained by summing layer estimates. BD was measured for every plot at each depth layer using undisturbed cores; we did not use a single BD value or assume constancy within forest types. Layer- and plot-specific BD values were used to compute SOCS per layer, which were then summed to 0–60 cm; SWS was computed analogously from layer-specific measurements.

Results and Discussions:

• L268: The PCA only in a narrative manner states that “PC1 explained 60.9 %” ...., but in my opinion the full eigenvalue table and variable loadings should be provided (at least in supplementary material)

Response:

Thank you for the suggestion. In the revised manuscript we have removed the PCA section entirely and deleted the narrative sentence at L268. The current Results no longer rely on PCA, and we have avoided similar narrative-only reporting elsewhere. Our analyses now focus on the pre-specified models (ANOVA/LME, PLS-PM, and multimodel selection with variance decomposition), with full model outputs and statistics provided in the main text.

• Phrases such as “markedly lower”/“significant improvement”/“continuous increase” should be accompanied by numerical and statistical metrics.

Response:

Agreed. We have systematically revised the manuscript to (i) replace qualitative phrases with exact magnitudes (e.g., % change or mean ± SE) and (ii) report corresponding statistics (test used, effect estimate, 95% CI, and P value). Where such metrics were not essential, we removed the subjective wording. These changes have been applied throughout the Results and figure/table captions, and details are provided in the relevant tables/supplement where appropriate.

• Please better clarify if the chronosequence sites are edaphically or topographically comparable

Response:

Thank you for pointing this out. In our design and analyses we took explicit steps to ensure comparability and to control residual differences:

Shared land-use history: except for SF and MF (natural regeneration/enrichment), all forests were established by afforestation on former SRF, providing a common pre-restoration baseline. Consistent sampling window: all plots were sampled in May (late dry season, pre-monsoon) to minimize short-term weather effects and enhance cross-site comparability. Independent blocks with micro-topographic stratification: for each forest type we established one 20 × 20 m plot in each of three spatially independent patches (not repeated subsamples on a single slope); within plots, litter was sampled along upper/middle/lower slope positions. Statistical control of edaphic/topographic background: we standardized elevation, slope, silt, and clay and included them as covariates in the ANOVA/LME; plot identity was specified as a random intercept to account for among-plot heterogeneity and the repeated-measures structure. Path analyses on controlled residuals: for PLS-PM, we first controlled for elevation, slope, silt, and clay in mixed-effects models and then used the residuals as responses, focusing inference on vegetation-related effects. These procedures clarify that, while chronosequence sites cannot be made identical, they are made comparable by design and explicitly controlled in analysis using measured topographic and textural variables already reported in the Methods.

Conclusions

• In my opinion, statements that certain forest types “markedly enhance nutrient availability” or “support long-term carbon-moisture synergy” are too exaggerated, as long-term processes have not been directly monitored.

Response:

Thank you for this important caution. We have removed over-stated wording and avoided any implication of long-term outcomes not directly monitored. Throughout the manuscript we now (i) use measured, time-bounded effects with magnitudes and statistics (e.g., mean ± SE, % change, 95% CI, P), and (ii) replace causal or long-term language with neutral, evidence-based phrasing (e.g., “higher/lower,” “was associated with,” “indicates,” “may suggest”).

Reviewer 2 Report

Comments and Suggestions for Authors

This paper compares soil organic carbon stocks (SOCS) and soil water storage (SWS) in seven difference forest types following restoration of degraded sloping rainfed farmland in Yunnan Plateau, China. This was done by a field sampling campaign in 2019. The authors report on differences in SOCS and SWS among forest stands such as faster litter turnover and stronger hydrological regulation in deciduous forests. The authors report that this study provides new insights into the synergistic regulation mechanisms of soil carbon and water during the restoration of degraded sloping farmland.

The subject of this paper is important and worthy of study. Unfortunately, the main issue here is that “it was assumed that initial soil conditions were homogeneous across all sites, and any changes in SOCS and SWS could be attributed to differences in vegetation type and restoration pathways” (lines 161-162). This is clearly not the case because the data in Table S3 show that state factors such as clay content vary from 8.6% to 24.4%, and sand content varies from 52% to 66% in the 3 stands (sites) and these do not change because of forest type. Because soil texture has an enormous effect on soil carbon storage as well as soil water storage it is impossible to disentangle any effect of forest type – especially when the 7 forest types vary in age from 9 to 60 years old. Many other state factors (slope, elevation (and I assume climate)) that cannot be affected by forest type in as little as 9 years (age of the youngest stand sampled) will also affect SOCS and SWS so the study design cannot test the effect of forest type on SOCS and SWS – which is the goal of this paper. This is not a “space for time” design (line 151) as too many variables differ among sites. I am also not convinced by the “trade-off” figures between SOCS and SWS shown in Figure 5 – I or really understand what they are showing (not really explained in the methods). Isn't this simply showing a lack of a relationship? For example, how is equation 10 derived? What are the minimum or maximum values – values across all sites or are they the mean value of each site or an individual value? All the error bars on Figure 2 are the same size which just adds to my confusion. In Figure 5 there are 9 points per stand type – I have no idea where these points come from (only 3 plots per site?) and what is the arrow showing – which side of the 1:1 line most points are located? Likewise, I have no idea why soil depths below 40 cm are shown when some of these forests are less than 20 years old. Figure 6 shows some very complex relationships (which I can’t really understand given the large number of acronyms), but this is just based on 3 sampling sites in each of the 7 locations (n = 27). The authors need to think about what they are trying to test rather than throwing a range of statistical techniques at a limited dataset.

The only thing this paper can do is to describe the differences in SOCS and SWS among the 8 sites and determine what factors are related to high/low values. However, this is an issue because of the sampling design. For example, the authors report litter thickness – but this is likely affected by age of the stand (see table S2) and the PCA in Figure 2 – so is it age or litter thickness that affects SOCS and SWS. I am not sure how the authors would go about doing this – but I do know that this paper cannot evaluate the effect of forest type on SOCS and SWS.  The paper also suffers from a very limited sampling design – just 3 replicates per forest type (line 164) so there are almost as many variables as samples.

I must unfortunately recommend rejection based on this major issue and suggest that the authors take a different approach to the dataset. The authors should also think about the best way of presenting the data – Figures 2 and 3 need the data in the S2 and S3 tables to be understandable and seeing the actual data are important prior to the statistical analyses. Likewise, the data in S1 are important as they show the forest differ in many ways – not just forest type.

Author Response

Response to Reviewer2:

• The subject of this paper is important and worthy of study. Unfortunately, the main issue here is that “it was assumed that initial soil conditions were homogeneous across all sites, and any changes in SOCS and SWS could be attributed to differences in vegetation type and restoration pathways” (lines 161-162). This is clearly not the case because the data in Table S3 show that state factors such as clay content vary from 8.6% to 24.4%, and sand content varies from 52% to 66% in the 3 stands (sites) and these do not change because of forest type. Because soil texture has an enormous effect on soil carbon storage as well as soil water storage it is impossible to disentangle any effect of forest type – especially when the 7 forest types vary in age from 9 to 60 years old. Many other state factors (slope, elevation (and I assume climate)) that cannot be affected by forest type in as little as 9 years (age of the youngest stand sampled) will also affect SOCS and SWS so the study design cannot test the effect of forest type on SOCS and SWS – which is the goal of this paper. This is not a “space for time” design (line 151) as too many variables differ among sites.

Response:

We appreciate this important point and agree that the statement implying homogeneous initial soils was inappropriate. We have removed that sentence and revised the text to reflect what we actually did: we did not assume edaphic/topographic homogeneity, but measured and controlled key background factors in the analyses.

Text revision (Methods): Deleted: “…it was assumed that initial soil conditions were homogeneous across all sites, and any changes in SOCS and SWS could be attributed to differences in vegetation type and restoration pathways.” Added clarification (already described elsewhere in Methods, now made explicit here):“To minimize background heterogeneity, elevation, slope, silt and clay contents were standardized and included as covariates in all models; plot identity was specified as a random intercept. For pathway analyses (PLS-PM), we first controlled these covariates in mixed-effects models and used the residuals as responses, focusing inference on vegetation-related processes.”

In the revised manuscript we explicitly account for between-site heterogeneity. Our goal is to compare forest types that share a common land-use history while conditioning on measured edaphic and topographic covariates: all plantations were established on former sloping rain-fed farmland (SRF), whereas SF and MF developed through natural regeneration or enrichment planting. All plots were sampled during the same phenological and hydrometeorological window (May, late dry season) to minimize weather-driven variability. We retain the term “space-for-time,” but now state in the Discussion that the observed associations are conditional on measured covariates and reflect a single-season snapshot, rather than proof of site-invariant causal effects or long-term trajectories. Wording in the Results and Discussion has been adjusted to avoid causal over-reach. Rather than assuming comparability, we model edaphic and topographic differences and interpret forest-type contrasts conditionally.

• I am also not convinced by the “trade-off” figures between SOCS and SWS shown in Figure 5 – I or really understand what they are showing (not really explained in the methods). Isn't this simply showing a lack of a relationship? For example, how is equation 10 derived? What are the minimum or maximum values – values across all sites or are they the mean value of each site or an individual value? All the error bars on Figure 2 are the same size which just adds to my confusion. In Figure 5 there are 9 points per stand type – I have no idea where these points come from (only 3 plots per site?) and what is the arrow showing – which side of the 1:1 line most points are located? Likewise, I have no idea why soil depths below 40 cm are shown when some of these forests are less than 20 years old. Figure 6 shows some very complex relationships (which I can’t really understand given the large number of acronyms), but this is just based on 3 sampling sites in each of the 7 locations (n = 27). The authors need to think about what they are trying to test rather than throwing a range of statistical techniques at a limited dataset.

Response:

Equation 10 (explicitly listed in Methods §2.5) provides the root-mean-square deviation (RMSD) between soil organic carbon storage (SOCS) and soil water storage (SWS), calculated according to the evaluation procedure described in reference [4]. For each forest type, the sample size is n=9 (three soil depths × three replicate plots). The axis limits are scaled to the global minimum and maximum observed across all soil depths and all land-use/forest types; this has been noted in the figure caption.

Each stand type has three plots and three soil depths (0–20, 20–40, 40–60 cm). Trade-off panels display the depth-specific mean per plot (3 plots × 3 depths = 9). We have added this note to the Fig. 3 caption and the Sampling subsection.

The error bars in Figure 2 represent standard errors derived from 1,000-iteration bootstrap resampling to quantify model uncertainty. Because some standard errors are very small, the bars may appear to overlap visually, even though their values differ. This description has been streamlined in the latest manuscript.

We acknowledge that Figure 6 in the original manuscript contained an excessive number of abbreviations, which hindered readability. In the revised version we retain abbreviations only for the forest types and the standard soil physicochemical indices, thereby making the figure and accompanying text more concise and accessible. We have also revisited the study objectives and streamlined the statistical analyses to align more closely with those aims.

• The only thing this paper can do is to describe the differences in SOCS and SWS among the 8 sites and determine what factors are related to high/low values. However, this is an issue because of the sampling design. For example, the authors report litter thickness – but this is likely affected by age of the stand (see table S2) and the PCA in Figure 2 – so is it age or litter thickness that affects SOCS and SWS. I am not sure how the authors would go about doing this – but I do know that this paper cannot evaluate the effect of forest type on SOCS and SWS.  The paper also suffers from a very limited sampling design – just 3 replicates per forest type (line 164) so there are almost as many variables as samples. I must unfortunately recommend rejection based on this major issue and suggest that the authors take a different approach to the dataset. The authors should also think about the best way of presenting the data – Figures 2 and 3 need the data in the S2 and S3 tables to be understandable and seeing the actual data are important prior to the statistical analyses. Likewise, the data in S1 are important as they show the forest differ in many ways – not just forest type.

Response:

Thank you for this helpful suggestion. In the revised manuscript we have (i) refocused the narrative on between-site differences in SOCS and SWS and on the factors associated with these differences; (ii) retained the conifer chronosequence (PY9, PY22, PY60) solely to contrast within-conifer ages and conifer vs. broadleaf types; and (iii) streamlined the statistical workflow to match these aims. Specifically:

Model focus. To emphasize the effect of forest type, our final regression analyses use covariate-adjusted responses (residuals after controlling for elevation, slope, silt and clay as specified in the Methods), and then relate these residuals to forest type and the reduced set of explanatory variables. This two-step approach avoids re-introducing topographic/edaphic covariates in the final models while still conditioning on them.

Parsimony and collinearity. We reduced the predictor set to satisfy basic sample-size constraints and to limit multicollinearity (pre-filtering by Spearman |r|>0.8; model parsimony via ΔAIC<2 with model averaging), consistent with the procedures already described.

Scope of materials moved to Supplement. To keep the main text focused, we moved litter and soil-property summaries to the Supplement and removed the PCA section from the Results.

These revisions sharpen the study’s focus on site-level contrasts and clarify how associated factors are assessed, while keeping inference explicitly conditional on measured topographic and textural covariates.

Reviewer 3 Report

Comments and Suggestions for Authors

The paper presents interesting results about mechanisms and relationships between SOC stocks and soil water storage across different forest species. The paper is well-written and structured. However, some clarifications are needed:

 

Abstract:

There are two SOCS abbreviations with different words: stocks and storage. Please, keep just one.

Line 27-28. Ket soil indicators and litter? It's no clear – “key litter”. Please clarify or revise.

Here also specify what are soil indicators.

 

Introduction:

103. Yunnan Plateau (China) – I suggest include the country here.

The last paragraph must clearly indicate the key aim. Probably, sentences from lines 112-115 should be placed above.

 

Materials and Methods:

205-207. It is not clear how many samples were taken from each land use type. Please specify.

235. Check the reference rules for citing papers in the text.

 

Results:

268. PCA analyzes should mentioned in the Materials and Methods part.
269. The text does not disclose the "ESC" abbreviation.
270. PCA, as abbreviation already used.

 

Discussion:

437. PCA, as abbreviation already used.

This section discussed all the results in detail. There are no more comments from my side.

 

Conclusions

608. Yunnan Plateau, China

Author Response

Response to Reviewer3:

Abstract:

• There are two SOCS abbreviations with different words: stocks and storage. Please, keep just one.

Response:

Thank you for pointing out this inconsistency. We apologize for the confusion. In the revised abstract (and throughout the manuscript), we now use a single consistent term for SOCS. We have standardized the phrase to **“soil organic carbon stock (SOCS)”** and removed any alternate usage of “storage” when referring to SOCS. This change ensures consistency in terminology.

• Line 27-28. Ket soil indicators and litter? It's no clear – “key litter”. Please clarify or revise. Here also specify what are soil indicators.

Response:

Thank you for identifying this issue. We have clarified the wording. We also reviewed the manuscript to remove similar ambiguous phrasing and to ensure that the terminology is consistent with the Methods section.

Introduction:

• Line103, Yunnan Plateau (China) – I suggest include the country here.

Response:

Thank you. We have added the country at first mention and ensured consistency thereafter.

• The last paragraph must clearly indicate the key aim. Probably, sentences from lines 112-115 should be placed above.

Response:

Thank you for the advice. We revised the final paragraph to state the study aim explicitly and moved the relevant sentences as suggested. The revised aim now reads:

Revised text: Therefore, to elucidate the carbon–water processes and their key drivers across different forest types on the Yunnan Plateau, China, we compared SOCS and SWS among eight land-use/forest types.

Materials and Methods:

• 205-207. It is not clear how many samples were taken from each land use type. Please specify.

Response:

Thank you for the suggestion. We have made the sample counts explicit in the Methods.

Added text (Methods):

“For each land-use/forest type (n = 8), we established three 20 × 20 m plots (n = 24 plots in total). From each plot, soils were sampled at 0–20, 20–40, and 40–60 cm, yielding 3 plots × 3 depths = 9 layer-specific soil samples per type for each measurement stream (mixed/disturbed soil for chemistry, core/undisturbed soil, and aluminum-box samples), i.e., 8 × 3 × 3 = 72 samples per stream overall. Litter was collected at upper/middle/lower slope positions and composited to one litter sample per plot (thus 3 per type, 21 in total).”

Results:

• Line235 Check the reference rules for citing papers in the text.

Response:

Thank you. We reviewed and corrected all in-text citations to follow the journal’s numeric style. Specifically, we (i) standardized to square-bracketed numbers, (ii) ordered multiple citations ascending and used ranges for consecutive items (e.g., [7–9], not [9,8,7]), (iii) used commas for non-consecutive items (e.g., [6, 12, 21]), and (iv) aligned punctuation and spacing per the guide. At Line 235 and throughout, mixed author–year forms were replaced with the correct numeric format, and the reference list was reordered to match the revised in-text numbering.

• Line268 PCA analyzes should mentioned in the Materials and Methods part.

Line269 The text does not disclose the "ESC" abbreviation.

Line269 PCA, as abbreviation already used.

Response:

Thank you for these notes.

PCA — In the revised manuscript, we have removed the PCA analysis and the related sentence at L268. Consequently, no PCA description is needed in Materials & Methods.

ESC abbreviation — We now spell out ESC at first mention and use the abbreviation consistently thereafter (matching the terminology in the Methods).

PCA abbreviation usage — Any residual use of “PCA” has been deleted with the removal of the analysis; there is no undefined abbreviation remaining.

Discussion:

• Line437 PCA, as abbreviation already used.

Response:

Thank you. In the revised manuscript, the PCA analysis has been removed, and the reference at L437 has been deleted.

• This section discussed all the results in detail. There are no more comments from my side.

Line608 PCA, as abbreviation already used.

Response:

Thank you. In the revised manuscript, the PCA analysis has been removed, and the reference at L437 has been deleted.

We sincerely thank the reviewers for their careful evaluation and valuable suggestions. The revised manuscript now provides clearer methodological descriptions (including sampling independence and covariate control), explicit sample counts and depth coverage, justified sampling windows and experimental intervals, quantified effect reporting, streamlined statistical analyses, and clarified figures and notation, with corresponding updates to the Supplementary Information. We believe these changes strengthen the manuscript’s focus, interpretability, and robustness. All edits are tracked and line-referenced to the current version. We appreciate the opportunity to revise the work and are glad to make any additional changes the editor deems necessary.