Asymmetric patterns of soil carbon mineralization during thaw slump recovery: Stable fast-pool size but rebounding decomposition rate

Li, Hanhan; Dai, Tingan; Luo, Danni; Wang, Huan; Xie, Min; Zhang, Yu; Luo, Xuegang

doi:10.5194/egusphere-2026-3656

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https://doi.org/10.5194/egusphere-2026-3656

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09 Jul 2026

| 09 Jul 2026

Status: this preprint is open for discussion and under review for Biogeosciences (BG).

Asymmetric patterns of soil carbon mineralization during thaw slump recovery: Stable fast-pool size but rebounding decomposition rate

Hanhan Li, Tingan Dai, Danni Luo, Huan Wang, Min Xie, Yu Zhang, and Xuegang Luo

Abstract. In areas of thermokarst landslides on the Qinghai-Tibet Plateau, the decline in soil CO₂ emissions over time is accompanied by a decrease in the proportion of active carbon and an increase in the proportion of inert carbon, suggesting that the soil organic carbon pool capacity and its mineralization rate may have changed. The lack of quantitative analysis regarding how actual active carbon pool capacity and mineralization rates regulate CO₂ emissions has led to some uncertainty in CO₂ emission estimates. In light of this, this study utilized a publicly available dataset of a 23-year recovery sequence from thermokarst landslides in the Qilian Mountains. By introducing a dual-pool index model, the cumulative CO₂release process was decoupled into fast-pool capacity (C_0,fast) and fast-pool decomposition rate constant (k_fast), and their driving factors were identified using hierarchical variance decomposition (LMG) and partial least squares structural equation modeling (PLS-SEM). The results indicate that over the 23-year recovery period, C_0,fast did not change significantly, while the turnover rate k_fast rebounded significantly. Furthermore, C_0,fast was primarily driven by total microbial biomass (r = 0.74, p = 0.003), whereas k_fast was influenced by the chemical quality of organic carbon (r = 0.60, p = 0.023). Both LMG and PLS-SEM confirmed that the chemical quality of organic carbon is the primary driver of variation in k_fast (contributing approximately 30 %), while microbial indicators contributed less than 15 %. Furthermore, as the number of recovery years increased, δ¹³C exhibited a significant negative trend (β = −0.761, p < 0.001), and both this trend and the subsequent recovery in pH were significantly correlated with k_fast (r = −0.53 and 0.51, respectively). Soil carbon mineralization during the recovery from thermokarst landslides exhibits an asymmetric pattern characterized by “stable pool capacity and a rebound in mineralization rate.” This finding provides new kinetic evidence for assessing carbon dynamics following permafrost disturbance.

Received: 22 Jun 2026 – Discussion started: 09 Jul 2026

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Hanhan Li, Tingan Dai, Danni Luo, Huan Wang, Min Xie, Yu Zhang, and Xuegang Luo

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RC1:
'Comment on egusphere-2026-3656', Anonymous Referee #1, 04 Aug 2026 reply
Dear editor and authors,
General Comments
Thank you for this interesting manuscript. The manuscript concerns a re-analysis of a dataset recently published in JGR Biogeosciences (https://doi.org/10.1029/2024JG008162). The main novel contribution of this current manuscript concerns the fitting of single and two pool model to the CO2 production during an incubation from Mu et al 2025. The evaluation of turnover time of CO2 produce by thermokarst soils is highly relevant for this journal. However, the manuscript currently falls short on its scientific novelty and quality. Below, I explain this further.
Specific comments
The main finding of the current manuscript describes that the total size of fast carbon does not change along the thaw slump gradient, while its turnover time (kfast) does. The authors state that C0 describes the capacity of the fast/slow carbon. In this decay model, C0 describes the initial decomposition rates during the incubation. Throughout the manuscript the authors use C0 to infer the size (or ‘capacity’) of the carbon pool and state that the size of the carbon does not change, while the actual fresh carbon pool has not been measured. More importantly, the soil along the slum age gradient produce less CO2 over a 189 day incubation than the control. How can the same size of fresh carbon pool produce more CO2? This needs to be discussed. Furthermore, any discussion on the lack of difference in parameters for the slow is currently missing but needs to be added.
Most importantly, the authors do not discuss the results and interpretation of the original publication, which state “We found thaw slumps led to a large loss of labile C, and the resistant C accumulated gradually along the thaw sequence”. In this current manuscript the authors claim the opposite, as discussed above, without discussing the difference in interpretation of the same data. This crucial difference needs to be addressed in order to substantiate their conclusions.
Technical comments
The main results from this manuscript rely on the analysis of the key parameters (C0,fast; kfast; C0,slow; kslow; C0,total) extracted from non-linear model fitting. In its current description, there are multiple biases in the performed ANOVA on those key parameters, that make interpretation of the statistical results unreliable and will need to be further improved.
Unbalanced design -- 24 samples are described in original manuscript but only 23 samples are described in this manuscript (L 266). It is unclear why sample 1-HT2-B1 is missing. It appears to be the case that most of the analyses take parameters value from both samples analyzed using a single pool model or a two-pool in order to have enough samples (L343-346), which do not provide the same output parameters. It is unclear how parameters from the single pool models were included in the ANOVA. The missing data points can cause a unbalanced design is not accounted for.

Data distribution -- While the authors clearly report that some of the extracted kfast values reach the upper limit in their robustness test. The number of samples that reached upper limit should be mentioned in the results section. Furthermore, if 20% of the data is on the upper limit set in the non-linear model it is highly unlikely that the kfast data was normally distributed, while this was not shown in the methods nor results, but becomes apparent in Figure S3. This means that assumptions of the performed ANOVA are likely not met.

Model fitting -- It also unclear to me how the authors choose upper and lower limits to the non-linear model fitting. It is clear that the upper limits affect the output of the ANOVA. The authors selectively describe that the P-value for the effect of Year since collapse remains significant (L 171 - 173), while the changes in effect sizes are not shown nor are the changes in P-value for the effect of soil Depth discussed (Table S14).

Uncertainty on the extracted parameters – The uncertainty on the estimated parameters in the individual non-linear model are neglected in further interpretation. A bootstrapping method to show a lack of effect on the subsequent statistical analysis of these estimate parameters should be used to justify this approach.

Nested design -- Last, the ANOVA model used in this manuscript is unjustified as it does not account for the nested effect occurring from sampling top and bottom soils from the same cores.

Furthermore, I am also concerned about the analysis and interpretation of the data. For example;
Small difference in 13C of the OM are interpreted as an additional plant carbon input(L 528), without providing and source appointment to backup this claim nor showing an plant data to support such inputs.

Increase of pH from 7 to 8 is interpreted as better abiotic environment (L 528), while the references used show that microbial decomposition is higher at a neutral pH.

It is unclear why PLS-SEM does not account for a path between chemistry and microbial biomass or include other parameters.

As it stands, I do not see fit for publication of this manuscript for Biogeosciences. Below I state more line comments that need addressed for this manuscript.

Minor comments
The authors speak of recovery from the thaw slump event throughout the manuscript. However, the photos in the original manuscript show clear physical disturbance even 23 years after the occurrence of the thaw slump event, so it is unclear if recovery is ongoing or achieved at these sites. Furthermore, it is unclear what type of recovery is then meant. For example, no description of the plant height or composition is given. The original publication rather speaks of a evolution.
The presented pearson correlations highly overlap with the original manuscript, thereby do not provide new data and should be removed.
The authors should explain in the introduction what is meant by active carbon. Which physical/chemical parameters determine whether carbon is active?

Line comments
Thermal melting, it could also concern thawing in the case of most permafrost features.

“the capacity of the active carbon pool” is undefined up until this point in the introduction. This makes it impossible for the reader to understand what the authors mean. It seems to me that it implies either the turnover rate of the decomposition rate or proportion of the pool that can be mineralized. Please clarify.

The double use of term plots for both the different sites (ctrl vs thermokarst) as well the individual replicate plots at each site is confusing. Please change plot on L 129 to site or another synonym.

such interpretation should be located in the discussion and needs a reference.

290 please change “land-use” into an adequate term to describe the thaw slump age gradient
This reference does not concerns thaw slump recovery. Please adjust phrasing to present the study accurately.

The PLS-SEM is designed to only show correlations with A/O ratio or microbial biomass. This means A/O ratio is the only drivers thaw could be shown to correlate with change in kfast in this statistical model. Please adjust phrasing.

405 “In the late stages of recovery, the continuous production and selective preservation of microbial residues can enhance alkyl carbon signals;” This is speculation and not shown in the reference. Please remove or adjust sentence accordingly.
Please describe what data from these references show a that mineral weather led to a change in pH.

As shown in the references Rousk et al. 2010; Sinsabaugh et al. 2008, microbial abundance and activity is rather higher at pH 7 than pH 8.

“exhibits a positive effect” Please rephrase. On what does OC quality have a positive effect?

Figure 1. Labels on axes are hard to read. Colours are not explained.
Figure 2. Error bars and mean points need to be explained
Notes S1. “whereas the effects of soil depth and their interaction were not significant (Table S4).” Please update this text to reflect the P-values shown in Table S14, where it shows a significant effect.

Reply
Citation: https://doi.org/10.5194/egusphere-2026-3656-RC1
- AC1:
  'Reply on RC1', Hanhan Li, 11 Aug 2026 reply
  Responses to General Comments：
  We sincerely thank the reviewers for their thorough and constructive review of this manuscript. We are very pleased that the reviewers recognized the high relevance of the topic, “Assessing the CO₂ turnover time in thermal karst soils,” to this journal. We fully accept the criticisms regarding the manuscript’s current shortcomings in scientific novelty and quality, and we regard them as important guidance for refining this study. We believe these revisions will significantly enhance the academic contribution of this manuscript. We are committed to implementing these changes, and below we provide a point-by-point response to your valuable comments.
  Responses to specific comments：
  We would like to thank the reviewers for their critical and constructive comments, which have helped us clarify the interpretation of our model results and enhance the rigor of the paper. Below, we respond to each point in turn.
  Clarification Regarding the Term “C_0,fast” and the Cumulative CO₂ Release Paradox
  
  Thank you for your comments; we apologize for any confusion this may have caused. First, we agree that more precise terminology is needed for C_0,fast. C_0,fast is a parameter derived from fitting the cumulative CO₂ curve during the cultivation period; it represents the potential mineralizable capacity of the fast pool under controlled cultivation conditions, rather than a direct measurement of the actual fresh carbon pool in the field. We will revise the statement to read: “C_0,fast did not undergo a significant change.” Second, regarding the apparent paradox of “why a seemingly stable fast carbon pool capacity is accompanied by a decrease in cumulative CO₂ release,” this should be understood in terms of the dynamic equilibrium of C_0,fast, which reflects the depletion of readily degradable carbon early on and the subsequent continuous replenishment of carbon sources. The key point here is that these compensatory inputs are primarily dominated by chemically complex, recalcitrant substrates. As these substrates are gradually degraded by microorganisms, they release soluble metabolites or microbial residues with relatively fast turnover rates. In the dual-pool model fitting, these products are kinetically classified as fast-pool components; however, functionally, they differ from the readily available polysaccharides commonly found in soil prior to disturbance. Therefore, although C_0,fast is maintained, the average activity and mineralization efficiency per unit of carbon have decreased.
  Missing Discussion of Slow-Catalyst Parameters
  
  Thank you for your comments and suggestions. We will address the lack of significant differences in the slow-catalyst parameters (C₀_,_slow, and k_slow) in our revised manuscript.
  Explanation of the Apparent Contradiction with the Results of Mu et al. (2024)
  
  We thank the reviewer for pointing out the potential contradiction between our findings and those of Mu et al. (2024), and we apologize for any confusion this may have caused. We would like to clarify here that the two studies are not contradictory but rather represent complementary interpretations of the same recovery sequence from different perspectives. Mu et al. (2024) used physical fractionation and static chemical analysis methods, such as ¹³C NMR, to reveal the compositional evolution of the soil carbon pool during the recovery of a thermal karst landslide: the content of particulate organic carbon (POC) decreased with the duration of recovery, while inert carbon fractions (such as mineral-associated organic carbon, MAOC, and alkyl carbon) gradually accumulated. Our study does not dispute this trend in the transformation of the static carbon pool. Instead, by performing kinetic decoupling of the cumulative CO₂ release curve using a two-compartment exponential model, we provide two key insights from the perspective of carbon turnover dynamics. (i) The absence of significant changes in C_0,fast indicates that, although the original readily degradable carbon was largely lost after the landslide as revealed by kinetic fitting, the fast pool did not disappear as a result. Instead, the composition of the fast pool underwent a qualitative shift during the recovery process, with the lost readily degradable carbon being replaced by new components. While these new components are indeed more “stubborn” than the original active carbon, they still exhibit a significantly faster turnover under cultivation conditions compared to the inert carbon in the slow pool; therefore, the model classifies them as the “fast pool.” (ii) The significant rebound in k_fast reveals the recovery dynamics of the fast pool’s turnover rate. In the early post-landslide period (years 1-12), k_fast remained suppressed; by year 23, k_fast had recovered significantly, reaching or even slightly exceeding the control level. This does not imply that the decomposition rate has returned to its pre-landslide state, but rather indicates that microbial mineralization is gradually recovering, even though the substrate is no longer the original high-quality organic carbon but rather a substitute active carbon with more refractory chemical properties. Mu et al. (2024) addressed the questions of “what the carbon pool is and how it changes,” while we used C_0,fast and k_fast to further address the questions of “whether the carbon pool’s turnover rate has recovered and whether its capacity has changed accordingly.” We will integrate these perspectives into the Discussion section of the revised manuscript.
  Responses to Technical comments：
  Thank you for your technical suggestions. We have clarified and revised the text in response to your questions and recommendations, and these improvements have effectively strengthened the reliability of our statistical inferences. Below, we address each point individually.
  Clarification Regarding Missing Samples and Total Sample Size
  
  We appreciate the reviewer’s comments and apologize for any confusion this may have caused. The original in vitro experimental dataset (Mu & Mu, 2025) included a total of 24 soil samples. However, one of these samples, 1-HT2-B2 (Year 12, subsoil, replicate 2), had no cumulative CO₂ release records in the publicly available dataset; this sample may have been lost during the incubation process or was not measured. Consequently, this sample could not be included in any model fitting from the outset. This represents a limitation in the availability of the original research data itself, rather than a subjective decision made during our analysis. All analyses were based on the 23 samples with complete cumulative mineralization curves. Furthermore, among the 23 samples with valid data, one sample (1-HT3-A1, 23-year topsoil) had fewer than four valid observation points (data missing after day 69), making it impossible to reliably estimate the two-tank model (which requires at least four observation points for its four parameters). Therefore, this sample was fitted using only a single-tank model, with both the fast-tank and slow-tank parameters set to missing. Ultimately, 22 samples were successfully fitted to the two-tank model and used for the analysis of all fast- and slow-tank parameters (C_0,fast, k_fast, C_0,slow, k_slow). The single-pool sample was retained solely for the analysis of total pool parameters (C_0,totaland k_total), as these parameters are available in both the single-pool and dual-pool models. This was not explicitly stated in the original manuscript due to an oversight on our part; we will clarify this in the Methods section of the revised manuscript.
  Regarding the Inclusion of Single-Pool Model Parameters in Analysis of Variance and the Handling of Unbalanced Designs
  
  We appreciate the reviewer’s comments and apologize for any confusion this may have caused. The mixed use of single-pool and dual-pool models may lead to design imbalance. We clarify this as follows: In the main analysis of the fast/slow pool parameters (C_0,fast, k_fast, C_0,slow, k_slow) in the manuscript, only 22 dual-pool samples were used. This is because, among the 23 valid samples, one sample (1-HT3-A1) had fewer than four valid observations (fewer than the number of parameters in the dual-pool model) and could only be fitted using a single-pool model; consequently, neither its fast-pool nor slow-pool parameters could be obtained. Therefore, the analysis of the fast- and slow-pool parameters was based on the 22 samples for which the dual-pool model was successfully fitted, and there was no mixing of single-pool and dual-pool parameters in the calculations. Second, the main analysis of the total reservoir parameters (C_0,totaland k_total) utilized all 23 samples, as both single-reservoir and dual-reservoir models can output total reservoir parameters. Furthermore, to verify whether the inclusion of the single-pool sample mentioned above would affect the conclusions, we conducted an additional sensitivity analysis: we excluded the data related to that single-pool sample from the total-pool parameter analysis, retained only the 22 dual-pool samples, and re-ran relevant analyses such as ANOVA, LMG hierarchical decomposition, and PLS SEM. The results showed that the inclusion or exclusion of the single-pool sample in the analysis of C_0,totaland k_total did not affect any of the core conclusions of this study (SI Table S15).
  Data Distribution and ANOVA Assumptions
  
  Thank you for your comments and suggestions. We fully agree that ANOVA assumptions should be tested when data are non-normal, and we will include the following clarification in the revised manuscript: Among the 22 valid dual-pool samples, k_fast values for 3 samples reached the upper limit of the dual-pool model (1.0 d^-1), accounting for 13.6% of the total sample size. Based on the reviewer’s suggestion, we performed Shapiro-Wilk normality tests on the kinetic parameters. The results showed that all parameters deviated significantly from a normal distribution (p < 0.05), suggesting that the normality assumption of ANOVA may not be fully satisfied for these parameters. We subsequently conducted a Kruskal-Wallis nonparametric test, the results of which showed a significant cross-over with those of the ANOVA: k_fast was significant in the ANOVA (F₃,₁₄ = 5.11, p = 0.013), but did not reach the significance threshold in the Kruskal–Wallis test (H = 6.28, p = 0.099); whereas C_0,fast was not significant in the ANOVA (p = 0.056) but was significant in the Kruskal-Wallis test (H = 8.29, p = 0.041); The other parameters (C_0,total, C_0,slow, k_slow) were not significant in either test. Although the p for k_fast in the nonparametric test was slightly higher than 0.05, it remained at a relatively low level, and Tukey’s HSD post hoc comparisons under the ANOVA framework confirmed that k_fast for the 23-year treatment was significantly higher than that of the other treatments (23 years vs. 1 year: p = 0.006; 23 years vs. 12 years: p = 0.029; 23 years vs. control: p = 0.014). C_0,fast was significant in the nonparametric test, further confirming that a treatment effect is indeed present in the data and is not driven by the assumption of a single method.
  Selection of Upper and Lower Limits in Model Fitting and Their Impact on ANOVA
  
  We appreciate the reviewers’ comments and apologize for any confusion caused regarding the basis for our selection of upper and lower limits and the comprehensiveness of our sensitivity analysis. We have provided the following clarification and revisions: The decomposition rate constants for activated carbon pools reported in the literature are generally low. Schädel et al. (2014), based on a three-pool model inversion of circumpolar Arctic permafrost, reported that the turnover time for the fast pool at 5°C was 0.21-0.48 years, corresponding to k_fast ≈ 0.005-0.013 d^-1; Paul et al. (2006) also indicated, based on measurements of temperate agricultural soils, that the k values for the activated carbon pool range from 0.007 to 0.03 d^-1. In this study, the upper limit of k_fast was set at 1.0 d^-1, which is higher than the values reported in the aforementioned literature, primarily based on the following three considerations: First, differences in sample properties. The low k_fast values reported in the literature mostly originate from old permafrost that has undergone long-term decomposition or highly stable agricultural soils, where the easily decomposable components have been largely depleted. In contrast, the samples in this study were collected from fresh permafrost exposed by a thermal karst landslide on the Qinghai-Tibet Plateau; the organic matter had not undergone sufficient decomposition. Chemical analysis revealed high O-alkyl C content and a low C/N ratio (Mu et al., 2024), indicating a high proportion of active carbon and a decomposition rate that may be significantly faster than that of mature soils reported in the literature. Reserving sufficient parameter space for such highly active samples is a necessary prerequisite for avoiding artificial suppression of data variability. Second, avoid statistical bias caused by artificial truncation. In nonlinear fitting, overly tight upper limits can cause parameter estimates to be forcibly truncated, distorting differences between groups. In this study, the measured median k_fast was approximately 0.3 d^-1, with a maximum of approximately 0.8 d^-1; only 13% of the samples reached the upper limit of 1.0 d^-1, and even after relaxing the upper limit, the k_fast values for these samples did not increase indefinitely, indicating that 1.0 d^-1 is sufficient to accommodate the natural variability of the data. If the upper limit were lowered to near the mean value reported in the literature (e.g., 0.1 d^-1), the k_fast values for most samples would be truncated at the same threshold, and the analysis of variance would reflect model constraints rather than biological differences. Third, sensitivity analysis indicates that the upper limit does not alter the core conclusions. We systematically varied the upper limit of k_fast within the range of 0.5-5.0 d^-1 and repeated all fittings and analyses of variance. The results show that, under all upper limits, the main effect of recovery duration on k_fast remained significant (p = 0.003-0.028). This indicates that the core conclusions are insensitive to the choice of upper limit, and the setting of 1.0 d^-1 is robust and verifiable. Finally, we will include in the revised manuscript the information requested by the reviewers regarding the variation in effect sizes and the p-values for the depth effect.
  Schädel C, Schuur EAG, Bracho R, Elberling B, Knoblauch C, Lee H, Luo Y, Shaver GR, Turetsky MR (2014) Circumpolar assessment of permafrost C quality and its vulnerability over time using long-term incubation data. Glob Change Biol, 20: 641-652. https://doi.org/10.1111/gcb.12417
  Paul EA, Morris SJ, Conant RT, Plante AF (2006) Does the Acid Hydrolysis–Incubation Method Measure Meaningful Soil Organic Carbon Pools?.Proceedings - Soil Science Society of America, 70:1023-1035. https://doi.org/10.2136/sssaj2005.0103.
  Uncertainty in Parameter Estimates
  
  Thank you for your comments and suggestions. We have added a section on parameter uncertainty via Bootstrap analysis to the revised manuscript: The current results of the parameter uncertainty Bootstrap analysis (n = 5000) show that, after accounting for the residual errors from the dual-library model fit for each sample, the median ANOVA p-value for k_fast based on recovery years is 0.090, with a 95% confidence interval of [0.001, 0.679]. Across all Bootstrap iterations, approximately 36.6% yielded significant results with p < 0.05. Although this proportion does not exceed half, it is far higher than the expected significance rate of 5% in the absence of an effect, indicating that the year effect maintains a low p-value level under most parameter perturbations. It should be noted that the Bootstrap method only conveys uncertainty in the curve-fitting process, whereas the core conclusions of this study were cross-validated by multiple statistical methods: mixed models (p = 0.003), Tukey HSD post hoc comparisons (p < 0.05), a large effect size (Cohen’s d > 1.4), sensitivity analysis of parameter upper bounds (p < 0.05 for all upper bounds), and the PLS-SEM permutation test (p = 0.005) all consistently support the significant effect of recovery duration on k_fast. Therefore, the Bootstrap results can be interpreted, to some extent, as reinforcing the robustness of our conclusions.
  Nested Design
  
  We thank the reviewers for pointing out that the original one-way ANOVA did not account for the nested structure of topsoil and subsoil samples from the same sampling point. This was indeed an oversight in our initial manuscript. In subsequent revisions, we plan to address this issue by following these steps: We identified 12 independent plots based on sample numbers as random-effects factors and reanalyzed all kinetic parameters using a linear mixed model (LMM). The fixed effects were years of recovery, soil layers, and their interaction, while the random intercept was the plot. For the key parameter k_fast, the mixed-model results showed that the main effect of years of recovery remained significant (C(Years) [T.23 years]: coefficient = 0.589, z = 2.95, p = 0.003), consistent with the conclusions of the ordinary ANOVA. The depth effect for other parameters (e.g., C_0,fast) was also more significant in the mixed model (p = 0.001). The results of the adjusted mixed model will be presented in the Results section of the main text and in the appendix tables; the identification of the nested structure and the process of constructing the mixed model will also be described in detail in the Methods section.
  Respond to data analysis and interpretation：
  Thank you for your detailed comments on the analysis and interpretation of the data; they are crucial in helping us further clarify the logic behind our data analysis, refine the boundaries of our inferences, and improve the interpretation of our model. Regarding the issues you raised, our responses are as follows:
  Regarding the inference linking minor δ¹³C differences to plant carbon input
  
  Thank you for your comments and suggestions. We acknowledge that we did not directly measure the δ¹³C of plant tissues, nor did we perform source apportionment. However, the observed trend of δ¹³C shifting toward negative values along the recovery sequence is consistent with theoretical expectations for rhizosphere sediments. Werth & Kuzyakov (2010) provided a comprehensive review of ¹³C fractionation at the root–microbial–soil interface, noting that CO₂ from C3 plant root respiration is approximately -2.1 ± 2.2‰ poorer in ¹³C than root tissue, and that microbial processing further alters the ¹³C signature of SOM (microbial biomass in C3 soils is enriched by +1.2 ± 2.6‰ relative to SOM). These fractionation patterns indicate that even minor inputs of fresh plant-derived carbon can leave a detectable isotopic fingerprint in SOM. Although the magnitude of the changes in this study is small and does not constitute conclusive proof, it provides supportive, indirect evidence for vegetation restoration replenishing the fast pool. We will adjust the wording in the revised manuscript to explicitly frame the δ¹³C trend as an “observation that raises a hypothesis” rather than conclusive evidence.
  Werth M, Kuzyakov Y (2010) ¹³C fractionation at the root–microorganisms–soil interface: A review and outlook for partitioning studies. Soil Biology & Biochemistry, 42:1372-1384. https://doi.org/10.1016/j.soilbio.2010.04.009.
  Interpretation of the pH increase from 7 to 8 and improvements in the abiotic environment
  
  Thank you for your comments and suggestions. We agree that microbial decomposition typically reaches its optimum under near-neutral pH conditions. However, in the specific context of this thermokarst sequence, the key lies in the trajectory of pH recovery rather than its absolute value. In the early stages of the landslide, the exposure of deep, acidic parent material caused a sharp drop in surface soil pH (from ~7.5 to ~6.8), which constituted significant acid stress for microorganisms. The subsequent rebound to ~7.8–8.0 essentially represented relief and recovery from this state of stress. Although a pH of 8.0 may be slightly above the optimal range for certain acidophilic microbial groups, compared to the acidified state following the landslide, this alkalization trend likely optimized the overall physicochemical environment by enhancing the availability of nutrients such as phosphorus. Furthermore, our PLS-SEM model also confirmed a significant positive effect of pH on k_fast (β = 0.515, p = 0.041). This suggests that, within the specific study interval, the process of recovery toward neutral values was a key factor in promoting the restoration of decomposition function. We will clarify this important distinction between “pH recovery” and “optimal pH” in the revised manuscript.
  Regarding the Specification of the PLS-SEM Model Structure
  
  Thank you for your comments; we apologize for any confusion this may have caused. Regarding the reviewer’s concern about the path between chemical and microbial biomass, we clarify as follows: In the baseline PLS-SEM model, the path between organic carbon chemical quality and microbial biomass was specified from the outset (Fig. 4) and was not omitted. The standardized coefficient for this path is 0.920, but it did not reach statistical significance (Bootstrap p = 0.094), indicating that, under the data conditions of this study, the direct effect of organic carbon chemical quality on total microbial biomass is not yet significant; however, this does not affect the significant direct effect of organic carbon chemical quality on k_fast. Regarding concerns about “whether other parameters were included,” we specifically constructed an extended PLS-SEM model in addition to the main model, incorporating soil organic carbon stable isotope (δ¹³C) and pH as latent variables (SI Table S10). The results showed that both δ¹³C and pH had significant path effects on k_fast (path coefficients of -0.572 and 0.515, respectively; p < 0.05). Environmental variables such as soil moisture and texture were not included in the final structural equation model to avoid overparameterization, as they exhibited weak correlations with k_fast (|r| < 0.36) and showed no significant differences across treatments. We will discuss this point more explicitly in the revised manuscript.
  Responses to Minor comments：
  We thank the reviewers for raising these critical questions, as their comments have helped significantly improve the accuracy and clarity of the manuscript.
  Regarding Terminology, Novelty of Data, and Definition of Basic Concepts
  
  Thank you for your comments and suggestions. Regarding the use of the terms “recovery” and “evolution”: We fully agree with the reviewer’s observation: even 23 years after the landslide, the physical landscape of the landslide area remains in a disturbed state, and true landscape restoration often takes hundreds of years. In the original manuscript, we used the term “recovery” specifically to refer to the process of rebuilding biogeochemical functions, rather than to denote a return to the original geological morphology prior to disturbance. To maintain consistency with the terminology used in Mu et al. (2024) and to avoid implying that the ecosystem has fully recovered, we will uniformly replace the term “recovery” used to describe the time series with “post-landslide succession” or adopt the term “evolution” from the original literature in the revised manuscript. Regarding vegetation conditions, we acknowledge that the initial manuscript lacked detailed descriptions of plant height or composition; in subsequent revisions, we will draw upon the vegetation (e.g., Carex, Kobresia) reported by Mu et al. (2024) to support the context of biological colonization.
  Regarding the reproducibility of Pearson correlation coefficients:
  
  We fully agree with the reviewer’s comments. The Pearson correlation analysis in the original manuscript did, to a large extent, replicate the correlations between soil properties reported by Mu et al. (2024), and these findings did not provide additional incremental information for this study. In subsequent revisions, we will retain only the Pearson correlation results related to the newly fitted kinetic parameters (C_0,fast, k_fast, C_0,slow, k_slow), focusing on presenting the relationships between these parameters and the chemical quality of organic carbon and microbial indicators.
  Regarding the definition of “activated carbon”
  
  We thank the reviewer for pointing out the importance of defining this concept. In the context of this paper, “active carbon” does not refer to a specific physical fraction (such as particulate organic carbon, POC) or a particular single chemical substance, but rather constitutes an operational definition. We will clearly define it in the Introduction: active carbon refers to that portion of the carbon pool (C_0,fast) representing the potential for mineralization, as inferred from a two-compartment kinetic model, whose core characteristic is a high turnover rate (k_fast). From a physicochemical perspective, this pool may be heterogeneous, comprising both easily degradable substrates (e.g., O-alkyl carbon) and relatively complex microbial-derived components (e.g., alkyl carbon) that can be enzymatically degraded within specific cultivation time scales. Through this kinetics-based definition of “activity,” this study aims to capture the dynamic characteristics of soil carbon cycling during the post-landslide succession process, which serves as a valuable complement to the static chemical analysis by Mu et al. (2024). We will clearly articulate this distinction in the revised manuscript.
  Responses to Line comments：
  We thank the reviewer for such a thorough review of our manuscript; these comments are crucial for improving the quality of our work. Below are our responses to each point:
  Regarding the term “thermal melting”:
  
  We agree with the reviewer’s point. “Thermal melting” may be ambiguous. We will uniformly revise it throughout the text to “thaw” or “thawing,” following the terminology used in Mu et al. (2024).
  Regarding the definition of “active carbon pool capacity”:
  
  We thank the reviewer for pointing out that the definition of “the capacity of the active carbon pool” in the Introduction was unclear. In this study, this term refers to the size of the active carbon pool that can be mineralized (i.e., the proportion or total amount of mineralizable carbon), rather than its turnover rate. In the revised manuscript, when “active carbon pool capacity” is first mentioned in the Introduction, we will directly provide its physical meaning and model expression, and clearly distinguish it from the “decomposition rate constant,” so that readers can accurately understand these two core concepts before proceeding to the Methods section.
  Regarding the mixed use of the term “Plot”:
  
  We thank the reviewer for pointing out this ambiguity. In the revised manuscript, we will follow your suggestion and change “plot” to “site” on Line 129 to eliminate the ambiguity.
  Regarding the placement of interpretive content and supporting references:
  
  We agree with the reviewer’s comments. We will move some speculative or highly interpretive statements to the Discussion section and add corresponding references to support our arguments.
  Regarding the term “land-use”:
  
  The term “land-use” on line 290 is indeed inappropriate for describing naturally occurring thaw slump sequences. We plan to revise it to “thaw slump age gradient,” as used by Mu et al. (2024), to accurately reflect the research context.
  Regarding the relevance of references to thaw slump recovery:
  
  We thank the reviewer for pointing out the discrepancies in the references. We will carefully examine the context of the relevant references, adjust the wording, and ensure that previous research is accurately presented.
  Regarding the interpretation of the PLS-SEM model:
  
  We agree with the reviewer’s precise interpretation. The PLS-SEM model does indeed primarily reveal a strong association between the A/O ratio and k_fast. We will revise the relevant statements (such as sentences in the “Results” or “Discussion” sections) to avoid implying that the A/O ratio is the sole driving factor. Instead, we will emphasize that “within the framework of this model, the A/O ratio is the most significant variable explaining the variation in k_fast” and acknowledge the limitation that the model does not include all potential factors.
  Speculation regarding the enhancement of alkyl carbon signals by microbial residues:
  
  We agree with the reviewer’s comment that the statement on line 405 of the original manuscript was indeed too definitive and went beyond the scope of direct evidence provided by our current data and the cited literature. Based on the theoretical framework of the microbial carbon pump (MCP) proposed by Liang et al. (2017), residues produced by microbial turnover may be selectively preserved through chemical structure or mineral adsorption. In the revised manuscript, we will amend the relevant sentence to a more cautious, speculative statement, such as: “In the late stages of recovery, the continuous production and selective preservation of microbial residues may contribute to the observed enhancement of alkyl carbon signals.”
  Liang C, Schimel JP, Jastrow JD (2017) The importance of anabolism in microbial control over soil carbon storage. Nature Microbiology, 2:17105. https://doi.org/10.1038/nmicrobiol.2017.105.
  Literature support regarding pH changes caused by mineral weathering:
  
  We thank the reviewer for pointing out this critical omission in the literature citations. Upon careful verification, we found that of the two references cited in the original manuscript, Olefeldt et al. (2016) primarily mapped the distribution of thermokarst landscapes in the circumpolar Arctic and estimated carbon stocks, while Walker et al. (2010) focused on exploring the application of chronosequences in ecological succession studies; neither study focused on the geochemical mechanisms of pH recovery following thermokarst landslides. To correct this error and strengthen the foundation of our argument, we have cited literature that is directly based on thermokarst landslides on the Tibetan Plateau and has observed the mechanisms of pH changes (Men et al. 2026; Wang et al. 2023) and have rewritten the relevant paragraphs. Specifically: thermal melting and landslides expose deep-seated acidic parent material, causing a post-disturbance decline in surface soil pH; as the recovery process progresses, the pH gradually rebounds, which is most likely attributable to the combined effects of multiple processes, including the exposure of alkaline parent material, the loss of organic matter, and the migration of soluble salts—accumulated in the low-lying terrain of the landslide area—toward the surface soil through evaporation.
  Wang L, Liu G, Ma P, Cheng Z, Wang Y, Li Y, Wu X (2023) Effects of thaw slump on soil bacterial communities on the Qinghai-Tibet Plateau. Catena, 232: 107342. https://doi.org/10.1016/j.catena.2023.107342.
  Men X, Fu Z, Zeng L, Wang L, Du W, Gao S, Zhang G, Jiang G, Wu Q (2026) Permafrost collapse alters alpine ecosystem development via microtopographic modification on the Qinghai-Tibet Plateau. Catena, 262, 109692. https://doi.org/10.1016/j.catena.2025.109692
  Discussion on microbial activity at pH 7 and pH 8:
  
  We agree with the reviewer’s reference to the core conclusions of Rousk et al. (2010) and Sinsabaugh et al. (2008). We will revise the text to emphasize that the key point of this study is the “recovery process” of pH from the acidified state (~6.8) following the landslide toward alkalinity, rather than asserting that pH = 8 is superior to pH = 7.
  Regarding the ambiguous phrasing “exhibits a positive effect”:
  
  We thank the reviewer for pointing out the ambiguity of this phrasing. The original statement, “organic carbon chemical mass exhibits a positive effect,” did indeed fail to specify the object of that effect. According to the core findings of this study, organic carbon chemical mass—particularly the chemical reorganization process characterized by alkyl carbon accumulation—plays a key driving role in the recovery of k_fast. Therefore, during the subsequent revision process, we rewrote the Conclusions section, replacing the ambiguous “positive effect” with a clear causal statement to clarify that organic carbon mass influences the mineralization process by driving the recovery of k_fast.
  Regarding the axis labels and color legend in Figure 1:
  
  We appreciate the reviewer’s suggestion. In the revised manuscript, we will increase the font size of the axis labels and scale labels in Figure 1 and ensure that the image resolution meets the requirements. Additionally, we will clearly explain the meaning of the color coding in the figure legend.
  Regarding the error bars and mean points in Figure 2:
  
  We will add an explanatory note to the figure legend of Figure 2 to ensure that readers can distinguish between the error bars (SE) and the mean points.
  Regarding the update to Note S1:
  
  We thank the reviewer for carefully identifying this discrepancy in the data. Upon verification of Table S14, we confirm that soil depth and its interaction do indeed have a significant effect. The original text in Note S1 stated, “whereas the effects of soil depth and their interaction were not significant (Table S14).” We will correct this to read: “whereas the effects of soil depth and their interaction were significant (Table S14).” We thank the reviewer for helping us correct this error.
  
  Reply
  
  Citation: https://doi.org/10.5194/egusphere-2026-3656-AC1

Hanhan Li, Tingan Dai, Danni Luo, Huan Wang, Min Xie, Yu Zhang, and Xuegang Luo

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https://doi.org/10.5194/egusphere-2026-3656-supplement

Hanhan Li, Tingan Dai, Danni Luo, Huan Wang, Min Xie, Yu Zhang, and Xuegang Luo

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Short summary

When frozen ground collapses on the Tibetan Plateau, buried carbon is released as CO₂. Scientists expect emissions to fade as easy carbon is consumed. Using a public 23-year recovery dataset from the Qilian Mountains, we found a surprise: the readily available soil carbon pool stayed stable, but its breakdown rate rebounded strongly. This was driven more by fresh plant inputs and improving soil chemistry than returning microbes.


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