Determinants of carbon release from the active layer and permafrost deposits on the Tibetan Plateau

The sign and magnitude of permafrost carbon (C)-climate feedback are highly uncertain due to the limited understanding of the decomposability of thawing permafrost and relevant mechanistic controls over C release. Here, by combining aerobic incubation with biomarker analysis and a three-pool model, we reveal that C quality (represented by a higher amount of fast cycling C but a lower amount of recalcitrant C compounds) and normalized CO2–C release in permafrost deposits were similar or even higher than those in the active layer, demonstrating a high vulnerability of C in Tibetan upland permafrost. We also illustrate that C quality exerts the most control over CO2–C release from the active layer, whereas soil microbial abundance is more directly associated with CO2–C release after permafrost thaw. Taken together, our findings highlight the importance of incorporating microbial properties into Earth System Models when predicting permafrost C dynamics under a changing environment.

Introduction is very long compared to the other sections. But it introduces the reader well into the topic permafrost, reviews the scientific literature, and introduces the study area. The last part (starting L151) of the introduction reads like a second abstract, as it in includes a description of the applied methods and hypotheses which are some hidden main conclusions here. I would recommend shortening this part and rephrasing the 2 hypotheses in research questions or aims/objectives.
There is no explicit conclusions section which could be added to /rephrased at the end of the paper In conclusion I am missing partially the logical connections of the paragraphs and the central idea of the paper. Therefore, I am proposing a rejection of NCOMMS-16-03963 in this form.
The single results are of substantial importance and a much needed update on permafrost carbon quality and GHG production, but it needs major revisions and is potentially more suitable to a specialist science journal (in view of the incremental advance reported) than to a general science journal.
Detailed comments: L1: I propose a shorter title: Put just "Carbon dioxide..." instead of "different determinants of CO2..." L2: alpine or mountain permafrost? L21: words used in the title are not necessary to be in the keywords as well. Change "permafrost" to e.g. organic matter L32: I would avoid starting the manuscript with the word "despite" L35: Here and the rest of the manuscript: fluxes instead of effluxes? (and emission instead of production? L38: Please delete the "then" L40 and following: avoid the term "permafrost layer". Active layer is a defined scientific term, but permafrost is composed of very heterogeneous and different layers. Use e.g. permafrost deposits instead. Besides, I would define active layer and permafrost here (very shortly).
L45: inherent decomposability is a very elegant description for the main text, but in the abstract I would name it like "quality for future decomposition" to reach the broader audience L48: Do you mean AL with surface soils? L50: Please change depth to deposits L58: Please change deemed to e.g. was found to be ... or just "is" L59: What do you mean by "large fraction"? L61: Please change "Empirical" to "In-situ hawing experiments" L71: There are some recent model studies including more realistic approaches like including incubation data (Koven et al. http://dx.doi.org/10.1098(Koven et al. /rsta.2014 or Thermokarst processes (which are likely not that relevant to Tibetan plateau due to less ice in PF; Schneider von Deimling 2015 http://dx.doi.org/10.5194/bg-12-3469-2015) L72: Please change "detangling" to a more precise word or description.
L115: This is not only well known; this is the definition of permafrost. Please delete first part of this phrase and add an AL definition like "seasonally unfrozen surface layer" to the next sentence. L121: Please change "input" to "incorporated" L122: Please change "derived" to e.g. "freeze-locked" L123: Moreover, material from the AL enters the PF if sedimentation occurs, and the AL depth stays constant L133: Please delete "Last but not least" L143: I am not sure if I really understand the point how uplift and geological age influences the input of organic matter and its quality. Please add an explaining sentence here.
L152-159: Please delete the part "Five... productions." This feels like a second abstract and used methods should not be included in the introduction.
L159: "We aim to quantify (1) the vulnerability...Tibetan plateau, and (2) determine controlling factors of CO2 production." sound better to me as 2 hypotheses, which are hidden conclusion here (and not objective hypotheses written down before data interpretation. L222: Please justify the chosen 80-day duration of your incubations here and in the methods. The problem of such short durations is that we are far from curve saturation. The reader could extrapolate this in his mind and will end up in definitively to high numbers if he/she is not familiar with incubations. L231: Please CO2 production instead of "it" here L246: How could a microbial community have negative effects on CO2 production, as the microbes produce it? I thing you talk about a high/low proxy here, right? Please be more precise here. L255: Please describe what you mean by "less interacted" L262-263: This is an interpretation of your results, which belongs into the discussion section. L267: Please specify which king of means you are describing here: median, arithmetic... L269: I recommend to avoid phrases like "As expected", "It is well known", "to the best of our knowledge" etc.
L274: You are discussing the lowland permafrost and Tibetan permafrost qualities here. Please add 1-2 sentences discussing the expected C quantity and bring this together in a kind of climate warming risk assessment for lowland compared to Tibetan plateaus permafrost.
L287: When you are discussion age, please integrate you date (radiocarbon) to the results L290: Please be precise here and use the name of the region instead of "this" here.
L295: What are the influences of geological age (young) and glaciation on the organic matter quality and microbial community and thus on CO2 production? L300: Please change sizes to fractions L302: Please rephrase this sentence and delete "or even more so, than..." You could say that PF is at least as labile as AL... L302: Change to active layer deposits. L304: Why are you discussing here just 3 of you 5 sites? Are the other 2 not underlining this interpretation? Please add a sentence on the other sites here as well L340: Please give a reference for the circumpolar date. Especially for the 72 CN ration, which seems to be very high to me? L346-347: I think you mention this point here the 5th or 6th time. Please avoid repetitions L371: This "First..." sentence is highly speculative, as you are comparing 5 sites to a huge database of the arctic region.
L379: You are saying here that your 2 significant proxies are suitable "across permafrost zones". But in the text you highlight the difference of Tibetan permafrost and the lowland permafrost. Like vegetation, uplift, geologically young, glaciers... Please be consistent! L369 -382: I recommend using Conclusions instead of "Implications" to use this signifier word here.
Moreover I would integrate the quantity discussion here as well L486: Please introduce the reader into the aim of your decomposition modelling here L533; please rephrase "data manipulation" L708: Put AL and PF directly behind the words here and delete it at the end of the caption L709: Please change soil layers to deposit types L710: change "lines ending from the box" to whiskers L712: are the dots defined as outlier or included into the calculations? L717-718: change "inside box plot" to included boxplots Tables: • Please add a "sample number" column to every data table!
• name the sites • define abbreviations, as the tables should be understood without reading the text • When you use std: do you assume Gaussian distribution. In L507 you mentioned that you had to transform your data. Is a "normality" assumption justifiable her?   Table S1 • These are impressive ranges in the AL depth. Why? This should be included into the results! Table S2 • YY and CMH have huge SOC contents. Please include this in your results and discussion, especially concerning representativeness of the sites.

Reviewer #3 (Remarks to the Author):
Each of these points is addressed in the review text below, and the reference letter is noted in parentheses following the point. Overall review: The study examined drivers of CO2 production from permafrost regions of the Tibetan Plateau, and found generally higher CO2 production per unit C from permafrost compared to active layer soils, and that the drivers of CO2 production varied between active layer and permafrost (A). The study is of interest because there is limited understanding of the drivers of soil organic matter (SOM) decomposition from permafrost regions, particularly the Tibetan Plateau (B). A strength of the study is the combination of lab incubations with biomarker analysis, three-pool modeling, and structure equation modeling. I have two concerns, which are with the statistical analysis (D) and the discussion of results (H). First, it appears as if the ANOVA was treated as a completely randomized design, which it doesn't appear to be from the description of the sampling method. Second, I think the discussion falls short of explaining the observed patterns and differences among sites and soil depths. I am left wondering, WHY there were the observed differences that were presented in the paper. Although there may not be one clear answer, I think the discussion needs to delve deeper into the literature and to suggest processes that explain the observed results. I have a few minor questions about methodology, noted below (C). Overall, I think the conclusions are robust (E), the experiment was well-conducted (F), and the manuscript appropriately credits previous work (G).

Specific comments
Lines 113-122: I think the introduction should provide more process-level explanation as to why you would expect to see these differences between the active layer and permafrost. For example, I would suggest including some discussion of the mechanism of permafrost formation and impacts on the quality of frozen SOC.
Lines 146-147: It's not directly clear from the text how glacial history would make C more vulnerable on the Tibetan Plateau than in the arctic.
Lines 159-163: From the information presented in the Introduction, it's not obvious why you would hypothesize higher decomposability of permafrost v. active layer SOC, or the different proposed controls. I realize these are hypotheses, but I think the Introduction should be set up to provide the reader with some support for these hypotheses.
Discussion: I think the manuscript is missing discussion of WHY there are differences in inherent lability between active layer and permafrost soils, and why this varies across sites. Without this, it's difficult to get a clear message from the results.
Results, line 246: It's unclear what you mean by 'soil microbial community had a direct negative effect.." SEM model: It seems somewhat circular to include the carbon pool sizes in the prediction of CO2 production, since CO2 production was used to predict the pool sizes.
Lines 203-204: there wasn't exactly a consistent pattern in F/B across sites-it was lower in PF at CMH, and at 2 sites there seemed to be high variation.
Data analysis/Statistics: The statistical analysis needs clarification. The text and Table 4 suggests that this experiment was treated as a completely randomized design. However, as I understand the experiment, cores are nested in site, and (assuming active layer and permafrost samples came from the same cores rather than randomly sampled amongst cores) depth should be nested in core. It's not clear what MS was used as the error term, but from table 4, it was the same for each variable and interaction.
Lines 267-269: First the sentence says that CO2 production from permafrost was 169, then it says it was 223? That should be clarified.
Lines 287-295: In thinking about SOC lability in permafrost, it seems like a key driver is the level of SOM decomposition prior to freezing, in large part a function of the pattern of permafrost formation. How does this differ in the TP compared to Arctic?
Lines 397: was %C reported in results?
Line 465: The jars were sealed with an airtight lid? Was the environment anaerobic between sampling? If so, this seems like it may be a problem, especially for microbial community analyses.
Line 486, 3 pool model: Can you comment on the duration of the incubation in terms of the 3-pool model. That is, is 88 days a long enough timeframe to estimate these 3 pools? 83: Here and throughout: 'microbial community': should this be microbial community structure, composition, abundance? 103-104: 'long-term permafrost C loss' does this mean C mineralization after the permafrost thawed? If so, then by definition, long-term loss has to be correlated with slower cycling pools. Or, does this mean that the C that is frozen in permafrost is not labile (e.g., versus a fast cycling pool that only remains as SOC because it is frozen).

Responses to Reviewer #1
[Comment] This paper shows that the microbial and organic matter quality characteristics of the permafrost layer are different from the active layer, perhaps making it more vulnerable to climate change. Although it is well known that the two soil environments are different in a number of ways, the novelty of this result is the relative importance of the microbial community compared to abiotic and organic matter quality factors in soil decomposition processes, particularly for a region that generally lacks these studies. As such, the results should be of interest to soil carbon and permafrost modelers and, perhaps as the authors suggest, to the earth system modeling community. Although the paper is well written and fairly complete, I have concerns regarding the following 1) the SEM and 2) missing discussion about factors important to soil decomposition that were not included in this study (e.g. localized anaerobic conditions and the insulation effect of the organic matter layer). Some additional points that should be considered are also listed.
[Response] We are very grateful to the reviewer for the insightful comments on our manuscript! Following the reviewer's comments, we have re-constructed the structure equation modeling (SEM) by using the log-transformed moisture data instead of the raw data to consider the non-linear factor within the model. We have also discussed the anaerobic condition and other abiotic and biotic influences (i.e., insulation effect of organic layer) on permafrost vulnerability. These comments enabled us to have a deeper thinking on data analyses and results interpretation, and thus guided us to have a thorough revision on the MS. We feel that the revised MS has been greatly improved.
Thank you! Detailed modifications please see our responses to the following comments.

[Comment] Comments about SEM
One of the weaknesses of SEM is the ability to handle non-linear affects such as the relationship you show between Soil Moisture and CO2 in Fig 3. Is this nonlinearity assumed to be linear in the SEM (Fig 4)? If so, its effect on CO2 will not as high as it should. Was Soil Moisture log-transformed? Do the authors think that the effect of Soil Moisture could be too low?
[Response] Very good comment! Following the reviewer's comments, we have re-constructed the SEM by following two steps: First, we re-examined the relationships between cumulative CO 2 production and a variety of variables for the two depths, because the SEMs were constructed for active layer and permafrost deposits separately (also following reviewer #2's suggestion). We found that non-linear relationships existed between CO 2 production and soil moisture (for both depths), abundance of cutin, suberin and lignin-derived component (only for active layer), abundance of fungal and actinomycete PLFAs (only for permafrost deposits) (Table R1). Second, we conducted the data transformation to consider the non-linear factor in the SEMs. To be specific, for soil moisture, we used the log-transformed data instead of raw data to re-construct the SEM. For relative abundance of cutin, suberin and lignin-derived compounds, they were only three indicators in the matrix (C:N, lignin-, cutin-, suberin-derived compounds and different C pool sizes) representing C recalcitrance. Considering that these variables were closely correlated, we used principal components analysis (PCA) to create multivariate functional index to represent C recalcitrance and only the first principal component (PCA1) was used to construct the SEM. After that, we found that the PCA1 for C recalcitrance in active layer was linearly correlated to the CO 2 production (Fig. R1a). Similarly, the abundance of fungal and actinomycete PLFAs were also subjected to a PCA before performing SEM. The PCA1 for microbial abundance in permafrost deposits was also linearly correlated to CO 2 production (Fig. R1b). Thus, we used the PCA1 for C recalcitrance and microbial abundance directly to construct the SEM.

Fig. R1
Linear relationship between cumulative CO 2 production and PCA1 for carbon recalcitrance in active layer (a) and PCA1 for microbial abundance in permafrost deposits (b).
We would like to mention that the moisture that we used in previous SEM analysis, referred in particular to the moisture during the incubation. Given that good drainage and aeration in most sampling sites (Gao et al., 1985;, we focused on the aerobic C production in this study. Thus, soil moisture of each sample was controlled to 60% of water holding capacity (WHC) during the incubation. Following the reviewer's comments, to consider the causality between soil moisture and pH, we have used the soil moisture in the field instead of that during the incubation to indirect impact on cumulative CO 2 production through its long-term effects on soil pH and soil carbon quality (Fig. R2). The revised SEM showed that the standardized indirect effects of moisture on CO 2 production for active layer and permafrost deposit were -0.81 and -0.80, respectively ( Fig.   R3), being the most important indirect predictor for C loss.

Fig. R2
Effects of soil moisture, pH, microbial community and carbon recalcitrance on the cumulative CO 2 production from active layer (a) and permafrost deposits (b [Response] Very good comment! We would like to mention that the moisture that we used in previous SEM analysis, referred in particular to the moisture during the incubation. It has been widely reported that soils across most of the Tibetan Plateau have reasonably good drainage and aeration (Gao et al., 1985;. Due to this point, this study was designed to focus on the aerobic C production through controlling the soil moisture of each sample to 60% of water holding capacity (WHC) during the incubation. Thus, this soil moisture during the incubation is not assumed to have causality with soil pH.
Following the reviewer's comments, to consider the causality between soil moisture and pH, we have used the soil moisture in the field instead of that during the incubation to reconstruct the SEM in the revised MS. We have also changed the double-headed arrow to a single-headed arrow from soil moisture to pH. Given that explicit environmental setting during the incubation, soil moisture measured in the field could only have indirect impact on cumulative CO 2 production through its long-term effects on soil pH, soil carbon quality and soil microbial communities. Thus we deleted the single-headed arrow from soil moisture to cumulative CO 2 production. Moreover, following the reviewer's comments, we have used an arched double arrow to represent covariance between related variables in the revised MS. The revised priori model was showed in Fig  [Comment] In Figure 4, I suggest reversing the sign of the path from Inherent Decomposability to CO2 Production so that it is POSITIVE. It is confusing as it is currently depicted because if you translate the structure literally the path means "higher decomposability causes lower CO2", which isn't the case. Fortunately, reversing the signs should not alter your SEM results.
[Response] Sorry for the confusing expression. In the SEMs, the sign of each path is based on the standardized path coefficients. For example, the standardized path coefficients from the PCA1 for carbon quality to CO 2 production is -0.97 and -0.35 for active layer and permafrost deposits, respectively ( Fig. R2, Page 6 in this response letter), thus the sign are negative for the two depths. As depicted by the symbol "↑" in the SEMs (Fig. R2, Page 6 in this response letter), these negative relationships are mainly attributed to the positive correlation between PCA1 and racalcitrant C components (i.e., cutin-, suberin-derived compounds, lignin cinnamyl unit compounds). In other words, the PCA1 for carbon quality could be better represented by "carbon recalcitrance".
Therefore, to avoid confusion, we changed the "inherent decomposability" to "carbon recalcitrance" in the revised SEMs. Thanks for your understanding!

[Comment] Comments about other biotic factors
The authors claim that they are not concerned with anaerobic decomposition because soils in the area tend to be freely drained. Yet, anaerobic processes seem to be occurring, else why would an increase in Soil Moisture result in a decrease in CO2 (Fig 3 and 4)? An emerging topic in permafrost soils is that CO2 production is driven by local soil moisture conditions Xue et al. 2016). It would be interesting for the authors to address this question along with their ideas about the role local drainage plays in the Tibetan Plateau.
[Response] Very good comment! We would like to mention that the negative correlation between soil moisture and normalized CO 2 production observed in our study was not resulted from anaerobic processes. Instead, this result could be ascribed to the indirect effect of soil moisture on CO 2 production. To be specific, there was a positive relationship between soil moisture and carbon recalcitrance (Fig. R2, Page 6 in this response letter). As depicted in the SEMs, an increase in soil moisture would result in a higher carbon recalcitrance, which subsequently leads to a decrease in normalized CO 2 production. This negative correlation was also proved in a recent study, which was conducted along a 4,000-km-long transect of natural grassland and shrubland in Chile and the Antarctic Peninsula (Doetterl et al., 2015). They found that higher C content (positively correlated to soil moisture) were characterized by less microbial available SOC and lower rates of normalized CO 2 production (Doetterl et al., 2015). Moreover, soil moisture could also have indirect impacts on CO 2 production through its negative effects on pH, indirectly decrease the microbial abundance, and subsequently exerted negative impact on C loss (Fig. R2, Page 6 in this response letter).
It has been acknowledged that soils across most of the Tibetan Plateau have reasonably good drainage and aeration (Gao et al., 1985;. Due to this point, this study was designed to focus on the aerobic C production through controlling the soil moisture of each sample to 60% of water holding capacity (WHC) during the incubation. This soil moisture condition has been demonstrated to be the optimal water content for microbial activity for permafrost (neither constrained by oxygen nor water availability) (Rodionow et al., 2006;Wang et al., 2010).
Additionally, amber jars were flushed periodically with synthetic air (20% O 2 , 80% N 2 ) when the headspace CO 2 concentrations reached over 1000 ppm to minimize buildup of CO 2 and prevent the anaerobic environment. These experiment settings have been widely used in previous incubation studies (Rodionow et al., 2006;Wang et al., 2010;.
Therefore, the anaerobic processes did not occur in our incubation experiment.
Despite the anaerobic decomposition has not occurred in our incubation experiment, local drainage conditions is still of great importance to predict future vulnerability of permafrost after thawing Lawrence et al., 2015;Natali et al., 2015;Xue et al., 2016). Thus, following the reviewer's comments, we have added a paragraph to discuss the anaerobic condition on permafrost vulnerability and the role of local drainage on the Tibetan Plateau in Discussion section (Page 20, line 417-427) as follows: "In addition to C quality and microbial abundance highlighted in our laboratory observations, other various environmental controls such as drainage condition and soil surface conditions could also have both direct and indirect impacts on permafrost C loss.
Following permafrost thaw, flooding and the development of anaerobic conditions (thermokarst) is common in lowland and peatlands (Treat et al., 2014;Lawrence et al., 2015). The poor drainage condition with low oxygen availability in these regions can significantly constrain the release of CO 2 , but increase CH 4 emissions (Waldrop et al., 2010;Xue et al., 2016). In contrast, in upland areas, similar to our sampling sites, soil drying is expected to accompany permafrost degradation as a result of increased drainage in response to deepening of the water table . Therefore, local drainage condition across the [Response] Very good comment! Following the reviewer's comment, we have added one short paragraph to discuss the insulation effect of organic layer on permafrost vulnerability in Discussion section as follows: "Additionally, the stability of permafrost is also largely controlled by the surface condition such as organic layer thickness (OLT), which insulates the deep soil from variations in air temperature (Tarnocai et al., 2004;Schuur et al., 2008;Johnson et al., 2013). This insulation effect of OLT was suggested to negatively correlate with the active layer depth, acting as one of the most important factors with respect to thaw-depth variability for a continuous permafrost zone (Mazhitova et al., 2004). Different from the thick organic layer in high-latitude permafrost regions, Tibetan permafrost has barely organic layer due to its dry climate . The lack of insulation effect of organic layer in Tibetan permafrost was demonstrated to be the main reason for larger magnitude of active layer thickness change in recent years . Therefore, different OLT in permafrost regions may largely influence the subsurface temperature and control the subsequent permafrost C decomposition on a regional scale." (Page 20-21, line 428-438).
It should be noted that the Tibetan permafrost has barely organic layer due to its dry climate and good drainage condition (Gao et al., 1985). Consequently, the insulation effects could not explain the differences among the 5 sampling sites in Tibetan permafrost. Nevertheless, the difference in the organic layer between high-latitudes and Tibetan Plateau is presumed to be one reason for the higher lability of Tibetan permafrost. In the revised MS, instead of using insulation effect to explain the differences among our five sampling sites, we added more discussions about the potential reasons for lability differences among sites in Discussion section (Page 15-17, line 319-348) as follows: "Less chemical recalcitrant components in permafrost deposits contributed to the higher CO 2 production in YY, HSX and WQ. The observed relatively high C lability for permafrost deposits in these sites could be attributed to syngenetic permafrost formation through aeolian, alluvial and colluvial sedimentation (frozen preservation of plant remains in the Quaternary) Jin et al., 2007;, and cryoturbation (mix undecomposed labile SOC into deeper soils) (Ping et al., 2008;Schuur et al., 2008;Repo et al., 2009). This explanation was further proved by the relic periglacial phenomena and vertical permafrost distribution pattern revealed by boreholes near these sampling sites (Jin et al., 2007). Besides these SOC quality difference, interaction of abiotic factors and microbial communities may also result in the variation of CO 2 production with depth.
For instance, higher soil pH in permafrost deposits of the three sites (Supplementary Table S2) was positively correlated with the abundance of fungi and actinomycete, which were assumed to accelerate the subsequent recalcitrant C decomposition (Högberg et al., 2007;Waldrop et al., 2010) By contrast, similar carbon quality between active layer and permafrost deposits in CMH and KLSK samples could be induced by the climatic changes associated with glacial/interglacial cycle (Froese et al., 2008;Grosse et al., 2011). Two buried permafrost tables separating by a talik was found in borehole near CMH site, suggesting that significant decaying of the permafrost deposits may have been occurred during the Holocene Thermal maximum. In other words, the upper epigenetic permafrost near CMH site was newly formed during the Little Ice Age (Jin et al., 2007;Grosse et al., 2011). Moreover, mineral absorption may also decrease the lability of permafrost C in these two sites. The deeper permafrost deposits are presumed to be more protected against degradation by the association of SOC with minerals in organomineral associations (Mueller et al., 2015). This mineral absorption has been demonstrated to increase with soil C content, and result in lower normalized rate of respiration in soils with high carbon content (Doetterl et al., 2015). Consistent with this assumption, higher clay and silt content as well as SOC concentration in permafrost deposits compared with active layer were observed for both sites (Supplementary Table S2 [Response] Very good comment! Bulk density samples were not available for deep cores due to practical constraints. To obtain bulk density for pedon samples derived from boreholes, we sampled 51 natural soil vertical sections at the same depths as the boreholes from 17 sites using a standard container with 100 cm 3 in volume. We then developed an empirical relationship between measured bulk density and the related SOC concentration derived from the 51 natural soil profiles ( Fig. R5) to predict bulk density for deep cores (Strauss et al., 2013;. Following the reviewer's suggestion, we have added the predicted bulk density into the Table S2 in revised MS. Thanks for your understanding!

Fig. R5
The relationship between measure bulk density and related SOC concentration.
[Comment] lines 287-295. The way I read this: 'the Tibetan Plateau is geologically old with old soil carbon, which decomposes more slowly', but this contradicts the last sentence. Consider re-wording.
[Response] Thanks for the comments. Following the comments from Reviewer #2, we have deleted those arguments related to soil carbon age on the Tibetan Plateau since we do not have radiocarbon evidence on soil age. Instead, we added more discussions about the effects of ice content and organic layer on the CO 2 production in the revised MS (Page 7-8, line 140-146).

[Comment] A. Summary of the key results
The manuscript NCOMMS-16-03963 aims to quantify the CO2 production by using aerobic incubation [Response] We are very grateful to the reviewer for his/her insightful comments on our manuscript! These comments enabled us to have a deeper thinking on methods interpretation, and thus guided us to have a thorough revision on the MS. We feel that the revised MS is greatly improved. Thank you!
We are sorry that we did not clarify why we used a three-pool decomposition model in this study, which leads to your confusion. We would like to mention that this study was designed to: (1) identify C quality differences between active layer and permafrost deposits; and (2) determine controls of CO 2 production for both active layer and permafrost deposits after thaw. To achieve these objectives, we included three types of proxies (soil C:N ratio, relative abundance of SOM components derived from biomarker analysis and pool sizes for C fractions derived from the model) to quantify C quality. In other words, in this study, a three-pool model was only used to estimate pool size for C fractions with different turnover times, which was then used as one proxy for SOC quality. These pool sizes for different C fractions were frequently used to quantify the SOC quality in previous laboratory incubations . These three types of proxies are expected to provide more comprehensive information on SOC quality. We have clearly mentioned these points in the Method section of the revised MS (Page 25-26, line 540-552). BTW, we would like to mention that the novelty of this study is not reflected in the modeling part (i.e., modeling the fate of permafrost C), rather than the other parts (i.e., evaluating the relative importance of the microbial community, organic matter quality and abiotic factors in soil C decomposition processes) stated by the other two reviewers. As the other two reviewers pointed out, "Reviewer #1: The novelty of this result is the relative importance of the microbial community compared to abiotic and organic matter quality factors in soil decomposition processes, particularly for a region that generally lacks these studies. Therefore, our findings not only could be of interest to the permafrost community, but also could attract the readership in both ecology community and earth science community (see details in Page 20-21 of this response letter).
Despite predicting C loss under warming scenario is not the focus of this study, following the reviewer's comment, we added a short paragraph to discuss the potential C loss from the Tibetan Plateau under different warming scenario in the Discussion section of the revised MS (Page 13-14, line 274-282) as follows: "It has been suggested that permafrost would degrade between 19~25% (RCP4.5) to 48~63% (RCP8.5) from the current extent by 2100 (Schuur et al., 2013). Moreover, a recent evaluation has demonstrated that Tibetan permafrost stores about 15.31 Pg C within top 3 meters . By combining these with an average aerobic C loss of 45.4% for the same timeframe (assuming soils would be thawed for only 4 months per year for the next 85 years till 2100 and stay at a constant temperature of 5 o C) , we generated a rough warming risk assessment across the Tibetan Plateau. Within the next 85 years, between 1.32~1.74 Pg C (RCP4.5) to 3.34~4.38 Pg C (RCP8.5) could be released to the atmosphere as CO 2 from the Tibetan Plateau (Schuur et al., 2013)". Thanks for your understanding!

[Comment] C. Data & methodology: validity of approach, quality of data, quality of presentation
The methodical approach is impressing. Unfortunately, I am missing the central idea and logical connection of the numerous methods. Anyway, there are not many studies combining incubations and organic biogeochemistry and also the statistics look to be carried out carefully and well.
[Response] Thanks for the reviewer's insightful comments. We are sorry that we did not clarify the connection of the various methods in the previous version of the MS. To avoid this confusion, here we would like to explain why we used different approaches to address two central questions. As mentioned above, the main objectives of this study were (1) to identify C quality differences between active layer and permafrost deposits; and (2) to determine controls of CO 2 production for both active layer and permafrost deposits after thaw. To achieve these objectives, we included three types of proxies (soil C:N ratio, relative abundance of SOM components derived from biomarker analysis and pool sizes for C fractions derived from the model) to quantify C quality. To be specific, soil C:N ratio is a traditional but indirect proxy for SOC quality (Strauss et al., 2015). By contrast, biomarker analysis is a molecular-level method that provide an unparalleled insight into SOC chemical composition, being one of the most direct methods to examine the SOC quality (Feng & Simpson, 2011). In biomarker analysis, the relative abundance of the recalcitrant compounds was used as one direct proxy for SOC quality. At the meantime, pool sizes for C fractions with different turnover time (range from less than a year to hundreds or thousands of years) estimated from soil C decomposition model have also been interpreted as another proxy for SOC quality . It is easily understood that, in this study, elemental analysis, SOM biomarker analysis and three-pool model were jointly used to obtain three types of proxies for SOC quality. These three types of proxies are expected to provide more comprehensive information on SOC quality. After obtaining the SOC quality, we combined these variables with environmental factors (i.e. soil moisture, pH) and microbial abundance variables (i.e., fungal PLFAs, actinomycete PLFAs, microbial PLFAs) together to explore the relative importance of these factors in soil decomposition processes (response variable: cumulative CO 2 production derived from laboratory incubation) by constructing structure equation modeling (SEM). permafrost deposits in this study. We included three types of proxies (soil C:N ratio, relative abundance of SOM components derived from biomarker analysis and pool sizes for C fractions derived from a three-pool model) to quantify C quality. After obtaining the SOC quality, we combined these variables with environmental factors (i.e., soil moisture, pH) and microbial abundance variables (i.e. fungal PLFAs, actinomycete PLFAs, microbial PLFAs) together to explore the relative importance of these factors in regulating carbon loss by constructing structure equation modeling (SEM). [Response] Very good comments! We acknowledge that five sampling sites cannot fully represent the total Tibetan permafrost. We would also like to mention that we didn't aim to represent all the Tibetan permafrost in this study whereas to examine whether the controls of C decomposition in active layer and permafrost deposits after thaw are similar or not. To answer this question, we think that using five typical sampling sites is adequate for the following reasons: First, all these sampling sites were located in typical Tibetan permafrost zone with altitude above 4000 m (Fig. R7). It has been widely accepted that the zones of permafrost on the Tibetan Plateau are delineated as follows:

[Comment]
(i) mountain permafrost in the Altun-Qilian Mountains; (ii) seasonally frozen ground in the Qaidam

Basin; (iii) continuous permafrost in the northern part of the southern Qinghai and northern Tibet
Plateau; (iv) discontinuous permafrost in the southern part of the northern Tibet Plateau; (v) mountain permafrost in the Himalayas; and (vi) sporadic and patchy mountain permafrost on the eastern peripheries of the QTP (Zhou et al., 2000;Jin et al., 2011). Our five sampling sites were located within the third type of permafrost zone, which is the largest part of the continuous alpine permafrost on the plateau. In this typical permafrost region, the Xidatan-Amdo transect and the Gonghe-Qingshuihe transect were usually selected for long-term permafrost monitoring by geocryologists and permafrost engineers due to their typical permafrost characteristics and easy access (Jin et al., 2007;Jin et al., 2011;Cheng & Jin, 2012). Our five sampling sites located along these two typical transect. To be specific, YY, CMH, HSX and WQ located near Huashixia Permafrost Research Station, which is around Gonghe-Qingshuihe transect, while KLSK located near the Cryosphere Research Station on the Qinghai Tibet Plateau (CRSQTP) near Xidatan, which is at the northern border of the Xidatan-Amdo transect (Jin et al., 2011). In addition to permafrost feature, the grassland types in these five sampling sites are also typical on the Tibetan Plateau including swamp meadow, alpine meadow and alpine steppe (Fig. R8). Therefore, these five sites located within typical permafrost zone with typical ecosystem types on the Tibetan Plateau. We have clearly mentioned these points in the Method section of the revised MS (Page 22, line 459-470).

Fig. R7
A map of soil sampling locations with site names shown next to the closed red circles. Second, both the difficulty in field sampling and high cost of laboratory analysis (SOM biomarker and PLFA biomarker) constrained our sample size. It has been reported that the Tibetan alpine permafrost is generally characterized by the thick active layer (generally more than 2.4 m) (Pang et al., 2009) as a consequence of the arid climate, high evaporation, and lack of insulation effect of organic layer Yang et al., 2010). This thick active layer on the Tibetan Plateau largely increases the difficulty of permafrost deposit sampling. Moreover, the cost of deep pedon sampling, SOM biomarker and PLFA biomarker are also pretty high. Similarly, these difficulties and budget limits have also been the great challenges met by researchers who focus on high-latitude permafrost. Consequently, they also used limited sampling sites, ranged from 2 to 6 sites to explore the controls on permafrost decomposition after thaw in previous incubation studies (Wagner et al., 2007;Waldrop et al., 2010;Song et al., 2014;Treat et al., 2014). [Response] Thank you for the comments. As mentioned above, we have tried our best to obtain these typical Tibetan samples (total sample size equals to 30 = 5 sites × 2 depths × 3 replicated cores per site), and we believe that these samples are adequate to answer our questions. Definitely, future studies with large sample sizes are necessary to explore the vulnerability of Tibetan permafrost under continuous warming.
Our conclusions could be summarized as the following two points: (1) Carbon vulnerability in permafrost deposits was similar or even higher than that in active layer soils; (2) Carbon quality was most crucial for active layer carbon emission, whereas soil microbial abundance was more important for permafrost carbon loss after thaw. We would like to emphasize that these findings not only could be of interest to the permafrost community, but also could attract the readership among both ecology community and earth science community. To be specific, among ecology community, especially in climate change community, scientists pay close attention to the sign and magnitude of carbon-climate feedback (Davidson & Janssens, 2006;Heimann & Reichstein, 2008). Given that permafrost is the single largest component of terrestrial C pool (Hugelius et al., 2014), conversion of just a fraction of this frozen carbon pool into the greenhouse gases could accelerate the rate of future climate warming . Owing to the vital importance of permafrost in climate change science, Nature publishing group present a Specials Archive including a selection of overview articles and primary research from Nature, Nature Climate Change, Nature Geoscience, Nature Reviews Microbiology and Nature Communications over the past two years (http://www.nature.com/nature/focus/permafrost/index.html?WT.mc_id=BAN_ NATURE_1504_WCPERMFROST_PORTFOLIO). These articles highlighted the urgent need of understanding the decomposability of thawing permafrost (Conclusion 1) and relevant mechanistic controls (Conclusion 2) over C loss . Therefore, our findings are important for accurate evaluation on the direction and strength of C-climate feedback, which could also attract the readership from climate change community.
Additionally, among earth science community, scientists have a keen interest in understanding the persistence mechanism of deep soil carbon, which still remains obscure in previous studies (Fontaine et al., 2007;Schmidt et al., 2011). Carbon recalcitrance, physical protection by soil aggregate and mineral absorption and the absence of fresh organic carbon are presumed to be three mechanisms for long mean residence time (MRT) of deep soil carbon (Mikutta et al., 2006;Fontaine et al., 2007;Schmidt et al., 2011). Our finding (Conclusion 2) revealed that microbial abundance was more important than carbon chemistry in controlling the fate of deep soil carbon, at least in Tibetan permafrost region. Therefore, this finding could improve the knowledge of the persistence mechanism of deep soil carbon.
Last but not least, as the other two reviewers pointed out, our study has novelty in both scientific findings and research methods. [Response] Very good comment! By referring to the published papers, we have changed the "inherent decomposability" to "carbon quality". Following the reviewer's comments, we have deleted the last part of the introduction and rephrased the main objectives as following "The main objectives of this study were to (1) identify C quality differences between active layer and permafrost deposits; and (2) determine controls of CO 2 production for both active layer and permafrost deposits after thaw" (Page 8, line 154-156).
[Comment] There is no explicit conclusions section which could be added to /rephrased at the end of the paper.
[Response] Following the reviewer's comments, we have rephrased the Conclusion section of the revised MS (Page 21-22, line 440-456).
[Comment] In conclusion I am missing partially the logical connections of the paragraphs and the central idea of the paper. Therefore, I am proposing a rejection of NCOMMS-16-03963 in this form.
The single results are of substantial importance and a much needed update on permafrost carbon quality and GHG production, but it needs major revisions and is potentially more suitable to a specialist science journal (in view of the incremental advance reported) than to a general science journal.
[Response] Thanks again for the reviewer's insightful comments. Your comments enabled us to have a deeper thinking on methods interpretation, and thus guided us to have a thorough revision on the MS. As mentioned above, we have reorganized the Method section and added a supplementary figure (Fig. R6, Page 17 in this response letter) to elaborate the relationships among various methods. We have also added this elaboration in the Result section to provide a more coherent body of our work (Page 8-9, line 159-168). By accounting for these comments received, we feel that the revised MS has been greatly improved. Hopefully, the reviewer will be satisfied with our revised version but we are happy to make any additional changes that you think necessary. Thank you! Our conclusions could be summarized as the following two points: (1) Carbon vulnerability in permafrost deposits was similar or even higher than that in active layer soils; (2) Carbon quality was most crucial for active layer carbon emission, whereas soil microbial abundance was more important for permafrost C loss after thaw. We would like to emphasize that these findings not only could be of interest to the permafrost community, but also could attract the readership in both ecology community and earth science community. To be specific, in ecology community, especially among climate change community, scientists pay close attention to the sign and magnitude of carbonclimate feedback (Davidson & Janssens, 2006;Heimann & Reichstein, 2008). Given that permafrost is the single largest component of terrestrial C pool (Hugelius et al., 2014), conversion of just a fraction of this frozen carbon pool into the greenhouse gases could increase the rate of future climate change . Owing to the vital importance of permafrost in climate change science, Nature publishing group present a Specials Archive including a selection of overview articles and primary research from Nature, Nature Climate Change, Nature Geoscience, Nature Reviews Microbiology and Nature Communications over the past two years (http://www. nature.com/nature/focus/permafrost/index.html?WT.mc_id=BAN_NATURE_1504_WCPERMFROST_ PORTFOLIO). These articles highlighted the urgent need of understanding the decomposability of thawing permafrost (Conclusion 1) and relevant mechanistic controls (Conclusion 2) over C loss . Therefore, our findings are important for accurate evaluation on the direction and strength of C-climate feedback, which could also attract the readership in climate change community.
Additionally, among earth science community, scientists have a keen interest in understanding the persistence mechanism of deep soil carbon, which still remains obscure in previous studies (Fontaine et al., 2007;Schmidt et al., 2011). Carbon recalcitrance, physical protection by soil aggregate and mineral absorption and the absence of fresh organic carbon are presumed to be three mechanisms for long mean residence time (MRT) of deep soil carbon (Mikutta et al., 2006;Fontaine et al., 2007;Schmidt et al., 2011). Our finding (Conclusion 2) revealed that microbial abundance was more important than carbon chemistry in controlling the fate of deep soil carbon, at least in Tibetan permafrost region. Therefore, this finding could improve the knowledge of the persistence mechanism of deep soil carbon.
Last but not least, as the other two reviewers pointed out, our study has novelty in both scientific findings and research methods. [Response] We would like to mention that our main objective is to determine controls of CO 2 production for both active layer and permafrost deposits after thaw. As the reviewer #1 pointed out: "the novelty of this result is the relative importance of the microbial community compared to abiotic and organic matter quality factors in soil decomposition processes, particularly for a region that generally lacks these studies". Due to this point, we think that "Different determinants of CO 2 " in the title could present our finding directly. We have shorted the title as "Different determinants of CO 2 production from active layer and permafrost deposit on the Tibetan Plateau". Thanks for your understanding!
[Response] Good comment! There were various terminologies to describe the elevationally controlled permafrost, such as alpine permafrost (Zhao et al., 2004;Jin et al., 2007), mountain permafrost (Yang et al., 2010), plateau permafrost (Jin et al., 2000), altitudinal permafrost (Tully et al., 2013) and elevational permafrost (Tripolskaja et al., 2013). These terminologies are synonymous with each other. In this study, we used alpine permafrost because this term was more frequently used in previous studies (Fig. R9). Thanks for your understanding! [Comment] L21: words used in the title are not necessary to be in the keywords as well. Change "permafrost" to e.g. organic matter [Response] Done as suggested.
[Comment] L32: I would avoid starting the manuscript with the word "despite" [Response] Good comment! We have revised the sentence to "Permafrost plays an important role in global carbon (C) cycle. However, model predictions of permafrost C emissions and its feedback to climate warming are highly uncertain due to the lack of mechanistic understanding of controls over permafrost C turnover." [Comment] L35: Here and the rest of the manuscript: fluxes instead of effluxes? (and emission instead of production? [Response] We have changed "effluxes" to "fluxes" in revised MS. Additionally, we have checked the usage of word "emission" and "production" in all published permafrost incubation studies. We found that both two words could be used but we still use "production" instead of "emission" because "production" was more frequently used in previous studies (production: 62% vs. emission: 38%) (Fig. R10). Thanks for your understanding!

Fig. R10
Pie chart for incubation studies in permafrost region using word "production" and "emission" in manuscript title (Total sample size: n = 16).
[Comment] L40 and following: avoid the term "permafrost layer". Active layer is a defined scientific term, but permafrost is composed of very heterogeneous and different layers. Use e.g. permafrost deposits instead. Besides, I would define active layer and permafrost here (very shortly).
[Response] Good comment! Following the reviewer's suggestion, we have changed "permafrost layer" to "permafrost deposits", and have added a brief definition of active layer here and a brief definition of permafrost in the Introduction section of the revised MS (Page 2, line 41).
[Comment] L45: inherent decomposability is a very elegant description for the main text, but in the abstract I would name it like "quality for future decomposition" to reach the broader audience [Response] Very good comment! By referring to the published papers, we have changed the "inherent decomposability" to "carbon quality" (Page 2, line 44)..
[Comment] L48: Do you mean AL with surface soils?
[Response] We have changed the "surface soils" to "active layer soils" in revised MS.
[Comment] L50: Please change depth to deposits [Response] Done as suggested.
[Comment] L58: Please change deemed to e.g. was found to be ... or just "is" [Response] Done as suggested.
[Comment] L59: What do you mean by "large fraction"?
[Response] We have deleted the "large" in the revised MS.
[Comment] L71: There are some recent model studies including more realistic approaches like including incubation data    -12-3469-2015) [Response] Thank you for providing these valuable references. We have included these two references in the revised MS (Page 4, line 67-70).
[Comment] L72: Please change "detangling" to a more precise word or description.
[Response] We have changed the sentence to "These model predictions further highlight the importance of understanding the decomposability of thawing permafrost and relevant mechanistic controls over C loss".
[Comment] L115: This is not only well known; this is the definition of permafrost. Please delete first part of this phrase and add an AL definition like "seasonally unfrozen surface layer" to the next sentence.
[Response] Very good comment! Done as suggested.
[Comment] L143: I am not sure if I really understand the point how uplift and geological age influences the input of organic matter and its quality. Please add an explaining sentence here.
[Response] Very good comment! We have deleted those arguments related to geological age on the Tibetan Plateau since we do not have radiocarbon evidence. Instead, we added more discussions about the effects of ice content and organic laryer on the CO 2 production in the revised MS (Page 7-8, line 140-146).
[Comment] L152-159: Please delete the part "Five... productions." This feels like a second abstract and used methods should not be included in the introduction.
[Response] Done as suggested.
[Comment] L159: "We aim to quantify (1) the vulnerability...Tibetan plateau, and (2) determine controlling factors of CO2 production." sound better to me as 2 hypotheses, which are hidden conclusion here (and not objective hypotheses written down before data interpretation.
[Response] Very good comment! Done as suggested.
[Comment] L169: Please introduce abbreviations while using them for the first time (CMH) [Response] Done as suggested. [ where R(t) is the CO 2 -C emission rate at time t (mg C g -1 SOC d -1 ), C tot is the initial soil SOC content (i.e., 1000 mg C g -1 SOC), f 1 and f 2 are the fractions of fast and slow pools, k 1 , k 2 , k 3 are the decay rates of fast, slow and passive pools, respectively (Supplementary Table S5). In this soil C decomposition model, C tot and R(t) are measured quantities. The five parameters (i.e., f 1 , f 2 , k 1 , k 2 and k 3 ) were determined by a Markov Chain Monte Carlo (MCMC) approach .
Briefly, the approach was based on Bayes' theorem: where the posterior probability density function P(θ|Z) was obtained from the prior uniform probability density function P(θ) and the likelihood function P(Z|θ). It was assumed that the observed and modeled values followed a multivariate Gaussian distribution with a zero mean: where Z i (t) and X i (t) are the observed and modeled CO 2 -C emission rates, and σ i (t) is the standard deviation of measurements. A Markov Chain Monte Carlo (MCMC) technique, Metropolis-Hastings (M-H) algorithm, was used to construct P(θ|Z) of parameters (Metropolis et al., 1953;Hastings, 1970).
[Comment] L199: Please change the word respects here [Response] We have change the word "respects" to "aspect".
[Comment] L218: Please change the percentages to factors like 400% into 4 times more (if I understand this right) [Response] Good suggestion! We have rephrased the sentences as follows "Specifically, the normalized cumulative CO 2 production was significantly higher in permafrost deposits compared with active layer at YY, HSX and WQ (Fig. 2). The largest difference between depths was observed in WQ samples, where CO 2 production from permafrost deposit was 5 times higher than that from active layer (Fig. 2d)" (Page 11, line 223-226).
[Comment] L222: Please justify the chosen 80-day duration of your incubations here and in the methods. The problem of such short durations is that we are far from curve saturation. The reader could extrapolate this in his mind and will end up in definitively to high numbers if he/she is not familiar with incubations.
[Response] Very good comment! As mentioned above, the main objective of this study is to determine controls of CO 2 production for active layer and permafrost deposits after thaw but not to quantify long-term CO 2 production from thawing permafrost landscapes . To achieve this objective, short-term incubations are usually used to explore the potential mechanisms of permafrost decompositions once soils thaw (Wagner et al., 2007;Waldrop et al., 2010;Treat et al., 2014). Thus we think that 80-day incubation is appropriate for this study. We have added these points in the Method section of the revised MS (Page 24-25, line 511-517 [Response] Sorry for the mistake. We have revised the sentences to "Soil microbial abundance had direct positive effects on the cumulative CO 2 production, whereas pH and C recalcitrance had direct negative effects on cumulative CO 2 production in active layer." in the revised MS (Page 12, line 245-247).

[Comment] L255: Please describe what you mean by "less interacted"
[Response] To avoid confusion, we have deleted the word "interacted" in the sentence.
[Comment] L262-263: This is an interpretation of your results, which belongs into the discussion section.
[Response] We have deleted the arguments related to result interpretation in the revised MS.
[Comment] L267: Please specify which king of means you are describing here: median, arithmetic...
[Response] Done as suggested.
[Comment] L269: I recommend to avoid phrases like "As expected", "It is well known", "to the best of our knowledge" etc.
[Response] Good comment! We have deleted all the phrases like that in the revised MS.
[Comment] L274: You are discussing the lowland permafrost and Tibetan permafrost qualities here.

Please add 1-2 sentences discussing the expected C quantity and bring this together in a kind of climate warming risk assessment for lowland compared to Tibetan plateaus permafrost.
[Response] Very good comment! To do this, we bring our estimated C loss together with recent carbon inventory on the Tibetan Plateau in two warming scenarios to predict the potential C loss as follows: "It has been suggested that permafrost would degrade between 19~25% (RCP4.5) to 48~63% (RCP8.5) from the current extent by 2100 (Schuur et al., 2013). Moreover, a recent evaluation has demonstrated that Tibetan permafrost stores about 15.31 Pg C within top 3 meters . By combining these with an average aerobic C loss of 45.4% for the same timeframe (assuming soils would be thawed for only 4 months per year for the next 85 years till 2100 and stay at a constant temperature of 5 o C) , we generated a rough warming risk assessment across the Tibetan Plateau. Within the next 85 years, between 1.32~1.74 Pg C (RCP4.5) to 3.34~4.38 Pg C (RCP8.5) could be released to the atmosphere as CO 2 from the Tibetan Plateau (Schuur et al., 2013)". We have added these points in the revised MS (Page 13-14, line 274-282).
[Comment] L287: When you are discussion age, please integrate you date (radiocarbon) to the results [Response] Very good comment! Given that we do not have radiocarbon evidence, we have deleted those arguments related to geological age on the Tibetan Plateau. Instead, we added more discussions about the effects of ice content and organic layer on the CO 2 production in the revised MS (Page 7-8, line 140-146).
[Comment] L290: Please be precise here and use the name of the region instead of "this" here.

L295: What are the influences of geological age (young) and glaciation on the organic matter quality
and microbial community and thus on CO2 production?
[Response] As mentioned above, we have deleted those arguments related to geological age in the revised MS.

[Comment] L300: Please change sizes to fractions
[Response] Done as suggested.
[Comment] L302: Please rephrase this sentence and delete "or even more so, than..." You could say that PF is at least as labile as AL...
[Response] Done as suggested.
[Response] Done as suggested.

[Comment] L304: Why are you discussing here just 3 of you 5 sites? Are the other 2 not underlining this interpretation? Please add a sentence on the other sites here as well
[Response] Very good comment! Following the Reviewer #3's and your comments, we have added a paragraph to discuss the differences in carbon lability between active layer and permafrost deposits, and also this difference varies across sites in the revised MS (Page 15-17, line 317-348).
[Comment] L340: Please give a reference for the circumpolar date. Especially for the 72 CN ration, which seems to be very high to me?
[Response] Done as suggested. The range of C:N ratio was derived from the synthesis by .

[Comment] L346-347: I think you mention this point here the 5th or 6th time. Please avoid repetitions
[Response] Done as suggested.
[Comment] L371: This "First..." sentence is highly speculative, as you are comparing 5 sites to a huge database of the arctic region.
[Response] Very good comment! We have deleted the comparison between Tibetan and Arctic permafrost. We changed the sentences to "In conclusion, our finding confirms the high C vulnerability in Tibetan alpine permafrost based on the SOC biomarker and CO 2 production in the incubation experiment. The high C vulnerability to warming together with the large C pool size [Comment] L379: You are saying here that your 2 significant proxies are suitable "across permafrost zones". But in the text you highlight the difference of Tibetan permafrost and the lowland permafrost. Like vegetation, uplift, geologically young, glaciers... Please be consistent!
[Response] Very good comment! We have rephrased the sentence as "suggesting that these two variables could be used to predict C loss across alpine permafrost zones under warming scenario".
[Comment] L369 -382: I recommend using Conclusions instead of "Implications" to use this signifier word here. Moreover I would integrate the quantity discussion here as well [Comment] L388: squares?
[Response] Done as suggested. We have changed the sentence to "We collected three replicate cores per site within a 100 m 2 plot".
[Comment] L392: Please describe what you mean with "typical" here. Sound very subjective in this context [Response] To avoid misunderstanding, we deleted the word "typical" here, and added reasons for selecting the two segments as following: According to the position of upper permafrost table, we selected two segments from each sediment core to represent active layer (20-30 cm) and surface permafrost deposit (Supplementary Table S2). The sub-surface soil in activity layer was selected to avoid the surface soil consisting of large amount of live plant materials and prevent any sloughed material or soil contamination during drilling (Waldrop et al., 2010;Roy Chowdhury et al., 2014). The surface permafrost was selected because the deposits at this depth were firstly subjected to thaw under global warming . We have clearly mentioned these points in the Method section of the revised MS (Page 22-23, line 473-479).

[Comment] L392: refer to the AL thicknesses, which you gave in the tables later
[Response] Done as suggested.
[Comment] L399: Why did you not remove the carbonate by HCL and measure the SOC with the same device as the TC?
[Response] Soil organic carbon (SOC) was determined by using the potassium dichromate oxidation method because this is a national standard method in China that has been widely used to determine SOC concentration in previous studies (Nelson & Sommers, 1982;Yang et al., 2008;Yang et al., 2009). To further evaluate the accuracy of this method, surface soil samples from 115 sampling sites on the Tibetan Plateau were selected to determine the SOC concentration by two methods. The results showed that the SOC concentrations derived from wet oxidation method were closely correlated with those determined by an elemental analyzer (Vario EL Ш, Elementar, Germany) (r 2 = 0.98, P < 0.0001) (Fig. R11), indicating that this wet oxidation method is reliable for determining SOC concentration. Thanks for your understanding!

Fig. R11 Correlation between the SOC concentrations determined by two methods.
[Comment] L413: How did you remove the organic matter and carbonates here?
[Response] Soil texture was determined using a particle size analyzer (Malvern Masterizer 2000, UK) after removal of organic matter and carbonates by hydrogen peroxide and hydrochloric acid, respectively.
[Comment] L417-...: Which software did you use to integrate your GC-MS peaks?
[Comment] L452: Please explain the context of PLFA here shortly; living cells incl. intact head group....

[Response]
Following the reviewer's suggestion, we have added some descriptions about the PLFA in the revised MS as follows: Phospholipids are essential membrane components of all living microbes, which will decomposes quickly upon cell death, so the total PLFA biomarkers in a sample represent all living cells (Bossio & Scow, 1998). Moreover, different microbial groups produce specific or signature types of PLFA biomarkers allowing quantification of the important microbial groups and provide direct information about the structure of the active microbial community (Bossio & Scow, 1998) (Page 29-30, line 626-631).

[Comment] L463: Please tell the reader the depth
[Response] Done as suggested.
[Comment] L473: Do you follow a protocol which you should cite here?
[Response] Done as suggested.
[Comment] L484: Please describe the detector and the software you used to measure and integrate your peaks.
[Response] Done as suggested.

[Comment] L486: Please introduce the reader into the aim of your decomposition modelling here
[Response] Very good comment! Following the reviewer's comment, we have added one sentence to introduce our aim of this decomposition model in the revised MS (Page 28, line 599-601).
[Comment] L708: Put AL and PF directly behind the words here and delete it at the end of the caption

[Comment] • I recommend to add a study region figure;
• name the sites; • define abbreviations, as the figures should be understood without reading the text; • Please use an intuitive colour scheme: PF bluish (cold) AL reddish (warm, thawed) [Response] Very good suggestions! Done as suggested.

• Ad confidence interval notches to the boxes
[Response] Done as suggested.

• -5 o C PF light blue; • Boxplots bigger and incl. notches
[Response] Very good suggestions! Done as suggested.
[Comment] Figure 3: • AL and PF trends and models should have been calculated separately; • Change the colour of PF from red to blue; • Add the equations and sample numbers; • Justify the logarithmic model in the context of parsimony (and comparability to the other linear models) [Response] Done as suggested. Following the reviewer #1's suggestion, we re-examined the relationship between cumulative CO 2 production and a variety of variables for the two depths. We found that non-linear relationships exist between CO 2 production and soil moisture (for both depths), abundance of cutin, suberin and lignin-derived component (only for active layer), abundance of fungal and actinomycete PLFAs (only for permafrost deposits) (Table R1, Page 4 in this response letter). Our analysis showed that both logarithmic and linear model could fit the relationship. However, logarithmic model, capturing more variation across the sampling sites, exhibited a better performance with higher r 2 than linear model (Table R1, Page 4 in this response letter). Thus, we used non-linear model to fit the relationship in the revised MS.  Table S1 was the largest range across the three replicate cores for each sampling site. As you can see in the Table R2, there were large variations in active layer thickness between three replicated cores (collected within a 100 m 2 plot) in one swamp meadow site (YY). This variation may be derived from the large spatial heterogeneity in soil characters and water contents within this grassland type (Table S2). Similarly, large spatial heterogeneity in active layer thickness was also reported in high-latitude peatlands (Treat et al., 2014). [Response] Thanks for the reviewer's insightful comments. These comments enabled us to have a deeper thinking on data analyses and results interpretation, and thus guided us to have a thorough revision on the MS. We feel that the revised MS has been greatly improved. Thank you! Following the reviewer's comments, we have re-analyzed our data. We used mixed-effects models to investigate differences in all soil physical, chemical and microbial properties and C pool sizes among site (YY, CMH, HSX, WQ and KLSK) and depth (active layer vs. permafrost deposit), in which site and depth were treated as fixed factor and depth nested in core was treated as random factor.

[Comment]
Similarly, we performed another mixed-effects model to test for differences in cumulative CO 2 production among temperature, soil layer and sampling sites (R package: nlme). As you can see in the result (Fig. R12), re-analysis did not alter our results. The R code for the analysis is presented as production among temperature, soil layer and sampling sites.
Following the reviewer's comments, we have also added more discussions of the reasons for decomposability differences between the two layers and different regions in Discussion Section in the revised MS as follows (Page 15-17, line 317-348): "The variation of C vulnerability with depths in YY, HSX and WQ could be attributed to three aspects: SOC quality, microbial abundance and environmental factors. To be specific, higher SOC quality with less chemical recalcitrant components in permafrost deposits contributed to the higher CO 2 production in YY, HSX and WQ. The observed relatively high C lability for permafrost deposits was supported by previous observations in high-latitudes Waldrop et al., 2010;Treat et al., 2014). It could be attributed to syngenetic permafrost formation through aeolian, alluvial and colluvial sedimentation (frozen preservation of plant remains in the Quaternary) Jin et al., 2007;, and cryoturbation (mix undecomposed labile SOC into deeper soils) (Ping et al., 2008;Schuur et al., 2008;Repo et al., 2009). This explanation was further proved by the relic periglacial phenomena and vertical permafrost distribution pattern revealed by boreholes near these sampling sites (Jin et al., 2007). Besides these SOC quality difference, interaction of abiotic factors and microbial communities may also result in the variation of CO 2 production with depth. For instance, higher soil pH in permafrost deposits of the three sites (Supplementary Table S2) was positively correlated with the abundance of fungi and actinomycete, which were assumed to accelerate the subsequent recalcitrant C decomposition (Högberg et al., 2007;Waldrop et al., 2010).

By contrast, the similar C vulnerability between depth in CMH and KLSK samples could be explained by similar carbon quality and higher mineral protection in permafrost deposits.
Specifically, similar carbon quality revealed by SOM biomarker and C fraction pool sizes in these two sites could be induced by the climatic changes associated with glacial/interglacial cycle (Froese et al., 2008;Grosse et al., 2011). Two buried permafrost tables separating by a talik were found in borehole near CMH site, suggesting that significant decaying of the permafrost deposits may have been occurred during the Holocene Thermal maximum, and the upper permafrost was newly formed during the Little Ice Age (Jin et al., 2007;Grosse et al., 2011). Additionally, mineral absorption may also decrease the lability of permafrost C in these two sites. The deeper permafrost deposits are presumed to be more protected against degradation by the association of SOC with minerals in organomineral associations (Mueller et al., 2015). Mineral absorption has been demonstrated to increase with soil C content recently (Doetterl et al., 2015). Consistent with this assumption, higher SOC concentration in permafrost deposits compared with active layer were observed for both sites (Supplementary Table S2), which was the consequence of abrupt increase in SOC from the upper permafrost table (Supplementary Fig. S4)" (Page 15-17, line 317-348).
[Comment] lines 113-122: I think the introduction should provide more process-level explanation as to why you would expect to see these differences between the active layer and permafrost. For example, I would suggest including some discussion of the mechanism of permafrost formation and impacts on the quality of frozen SOC.
[Response] Very good comment! We have added more explanations for the expected decomposability differences between the two layers in Introduction section as follows: In permafrost region, a unique feature of permafrost-affected soils is that there exists an active layer (seasonally unfrozen surface layer), beyond which summertime warmth is insufficient to thaw the soil . This limit leads to a separation between seasonally thawed and perennially frozen soils and further results in substantial differences in not only SOC quality, but also microbial abundance and soil physicochemical environment (Rumpel et al., 2002;Billings et al., 2015). For example, most SOC in active layer are derived from vegetation inputs with relatively short mean residence time, whereas the lability in permafrost C likely varies according to the rates and timing of C burial, which is in large part a function of the pattern of permafrost formation (Grosse et al., 2011).
It has been suggested that high SOC quality could be expected in permafrost deposits where relatively undecomposed organic matter is preserved through some dominant soil processes, including cryoturbation (mixing of soils by freeze-thaw process) (Ping et al., 2008;Repo et al., 2009) and syngenetic permafrost growth with ongoing sedimentation Zimov et al., 2006;Treat et al., 2014). By contrast, substrate like epigenetic permafrost deposites subjected to repeated freeze/thaw cycles and cryochemical precipitation are likely more recalcitrant (Grosse et al., 2011;Treat et al., 2014;Ping et al., 2015) (Page 6-7, line 110-123).
[ [Response]: Very good comment! As mentioned above, we have added more discussions of the reasons for inherent decomposability differences between the two layers and different regions in Discussion Section in the revised MS as follows (Page15-17 , line 317-348): "The variation of C vulnerability with depths in YY, HSX and WQ could be attributed to three aspects: SOC quality, microbial abundance and environmental factors. To be specific, higher SOC quality with less chemical recalcitrant components in permafrost deposits contributed to the higher CO 2 production in YY, HSX and WQ. The observed relatively high C lability for permafrost deposits was supported by previous observations in high-latitudes Waldrop et al., 2010;Treat et al., 2014). It could be attributed to syngenetic permafrost formation through aeolian, alluvial and colluvial sedimentation (frozen preservation of plant remains in the Quaternary) Jin et al., 2007;, and cryoturbation (mix undecomposed labile SOC into deeper soils) (Ping et al., 2008;Schuur et al., 2008;Repo et al., 2009). This explanation was further proved by the relic periglacial phenomena and vertical permafrost distribution pattern revealed by boreholes near these sampling sites (Jin et al., 2007). Besides these SOC quality difference, interaction of abiotic factors and microbial communities may also result in the variation of CO 2 production with depth. For instance, higher soil pH in permafrost deposits of the three sites (Supplementary Table S2) was positively correlated with the abundance of fungi and actinomycete, which were assumed to accelerate the subsequent recalcitrant C decomposition (Högberg et al., 2007;Waldrop et al., 2010).
By contrast, the similar C vulnerability between depth in CMH and KLSK samples could be explained by similar carbon quality and higher mineral protection in permafrost deposits. Specifically, similar carbon quality revealed by SOM biomarker and C fraction pool sizes in these two sites could be induced by the climatic changes associated with glacial/interglacial cycle (Froese et al., 2008;Grosse et al., 2011). Two buried permafrost tables separating by a talik was found in borehole near CMH site, suggesting that significant decaying of the permafrost deposits may have been occurred during the Holocene Thermal maximum, and the upper permafrost was newly formed during the Little Ice Age (Jin et al., 2007;Grosse et al., 2011). Additionally, mineral absorption may also decrease the lability of permafrost C in these two sites. The deeper permafrost deposits are presumed to be more protected against degradation by the association of SOC with minerals in organomineral associations (Mueller et al., 2015). Mineral absorption has been demonstrated to increase with soil C content recently (Doetterl et al., 2015). Consistent with this assumption, higher SOC concentration in permafrost deposits compared with active layer were observed for both sites (Supplementary Table S2), which was the consequence of abrupt increase in SOC from the upper permafrost table (Supplementary Fig. S4)." (Page 15-17, line 317-348).

[Comment] Results, line 246: It's unclear what you mean by 'soil microbial community had a direct negative effect.."
[Response] Sorry for the mistake. In the revised MS, we have revised the sentences to "Soil microbial abundance had direct positive effects on the cumulative CO 2 production, whereas pH and C recalcitrance had direct negative effects on cumulative CO 2 production in active layer." (Page 12, line 245-247).
[Comment] SEM model: It seems somewhat circular to include the carbon pool sizes in the prediction of CO2 production, since CO2 production was used to predict the pool sizes.
[Response] We would like to mention that this kind of analysis may not induce great uncertainties in SEM analysis because of the following three reasons: First, we used the CO 2 -C emission rate rather than the CO 2 production to predict the pool size (f i )  as follows: where R(t) is the CO 2 -C emission rate at time t (mg C g -1 SOC d -1 ), C tot is the initial soil SOC content (i.e., 1000 mg C g -1 SOC), f 1 and f 2 are the fractions of fast and slow pools, k 1 , k 2 , k 3 are the decay rates of fast, slow and passive pools, respectively. In this soil C decomposition model, C tot and R(t) are measured quantities. The five parameters (i.e., f 1 , f 2 , k 1 , k 2 , k 3 ) are determined by a Markov Chain Monte Carlo (MCMC) approach.
After obtaining the five parameters, the CO 2 production is subsequently calculated as follows: where C cum is the cumulative CO 2 production at time t (mg C g -1 SOC), C cum1, C cum2 and C cum3 are cumulative CO 2 production from fast, slow passive C pools, respectively.
As depicted in the formula, the cumulative CO 2 production (C cum ) depends on the five parameters (f 1 , f 2 , k 1 , k 2 , k 3 ) simultaneously to the specific carbon pool size (f i ). The loose relationship between specific carbon pool sizes and cumulative CO 2 production was further proved by the moderate correlation between the two variables (r 2 ranges from 0.54 to 0.77) (Fig. R13). This moderate correlation does not support the circular assumption since the r 2 for the two circular variables were not very high. In other words, the r 2 for the two circular variables should be very high if the assumption hold true.

Fig. R13
Relationship of cumulative CO 2 production with fast (a) and slow (b) C pool size. Red solid circles represent data points in active layer (n = 15), and blue solid circles represent data points in permafrost deposits (n = 15).
Second, pool sizes of C fraction were only a small part of the matrix (C:N, lignin-, cutin-, suberinderived compounds and different C pool sizes) describing C recalcitrance in the SEM. Since these variables in C recalcitrance group were closely correlated, we used principal components analysis (PCA) analysis to create multivariate functional index to represent C recalcitrance .
The first component (PC1) was then introduced as a new variable into the subsequent SEM analysis.
As depicted in the Table R3, compared with carbon pool size, the PCA1 for C recalcitrance were more correlated with relative abundance of SOM components (i.e., lignin-, cutin-, suberin-derived compounds) in both active layer and permafrost deposits.  Third, our conclusion did not change even if we remove carbon pool sizes in the SEM. As depicted in the Fig. R14, removing the carbon pool size would decrease the standardized direct effects of carbon quality on CO 2 production in certain degree (from -0.97 to -0.67 in active layer; from -0.35 to -0.20 in permafrost deposits). Nevertheless, C quality is still the most important direct predictor of C loss for active layer; Soil microbial abundance also remains to be the most import direct predictor for permafrost deposits. Thanks for your understanding!

Fig. R14
Comparison of standardized direct effects derived from the structural equation modelling before (a) and after (b) removing carbon fraction pool size.

[Comment] lines 203-204: there wasn't exactly a consistent pattern in F/B across sites-it was lower in PF at
CMH, and at 2 sites there seemed to be high variation.
[Response] Following the reviewer's comment, we have re-analyzed the data but the result does not change. The ANOVA result from a mixed effects modeling is presented as below. As the depicted in Fig. R15, the P value for "layer" is 0.03, which indicated a significant depth effect across the 5 sites. We have rephrased the sentences as following: fungal-bacterial ratio (F/B), surrogate for microbial community structure, showed a relatively consistent variation between depths, except for CMH samples. F/B was significantly higher in permafrost deposit than those in active layer (depth effect, P = 0.03) and there was no site × depth interaction (P = 0.63) (Page 10-11, line 209-213).

Fig. R15
ANOVA results from a mixed-effects model testing for differences in F/B among soil layer and sampling sites. [Response] Very good comment! Following the reviewer's comments, we have re-analyzed our data. As mentioned above, we have used mixed effects modeling to test for differences in cumulative CO 2 production among temperature, soil layer and sampling sites in which site, depth and temperature were treated as fixed factor and depth nested in core was treated as random factor. (R package: nlme). As you can see in the result (Fig. R12, Page 39 in this response letter), re-analysis did not alter our results. Thus, we undated the results in the Table S4.

[Comment] Data analysis/Statistics: The statistical analysis needs clarification. The text and
[Comment] lines 267-269: First the sentence says that CO2 production from permafrost was 169, then it says it was 223? That should be clarified.
[Response] Thanks for the comment. We have rephrased the sentences to "Arithmetic mean of CO 2 production rate in Tibetan alpine grasslands was approximately 169 ± 35 μg CO 2 -C g -1 SOC d -1 for 80-day laboratory incubation, in which CO 2 production from permafrost deposit was about 223 ± 44 μg CO 2 -C g -1 SOC d -1 ." [Comment] lines 287-295: In thinking about SOC lability in permafrost, it seems like a key driver is the level of SOM decomposition prior to freezing, in large part a function of the pattern of permafrost formation. How does this differ in the TP compared to Arctic?
[Response] Very good comment! We do agree that the level of SOM decomposition prior to freezing could largely influence the SOC lability. As we have mentioned in the Introduction Section, "high SOC quality could occur in permafrost deposits where relatively undecomposed organic matter is preserved through some dominant soil processes, including cryoturbation (mixing of soils by freeze-thaw process) (Ping et al., 2008;Repo et al., 2009) and syngenetic permafrost growth with ongoing sedimentation Zimov et al., 2006;Treat et al., 2014). By contrast, substrate like epigenetic permafrost deposits subjected to repeated freeze/thaw cycles and cryochemical precipitation are likely more recalcitrant (Grosse et al., 2011;Treat et al., 2014;Ping et al., 2015)" (Page 6-7, line 118-123). Particularly, in Alaskan peatland, decomposition stage was demonstrated to have a stronger negative correlation with C flux than depth or thermal state (Treat et al., 2014). In Tibetan permafrost, undecomposed plant roots and stems were also found near our sampling sites (Jin et al., 2007). Nevertheless, we could not compare the degree of decomposition of high-latitude and high-altitude permafrost due to the scanty data for both regions, but see (Treat et al., 2014;Treat et al., 2016). Owing to the importance of SOM decomposition stage in predicting the permafrost vulnerability, Further studies on permafrost decomposition degree and other processes responsible for the permafrost C quality must be undertaken in both high-latitude and Tibetan permafrost zones. We have added these points in the Discussion Section of the revised MS (Page 14-15, line 294-303).
Thanks for your understanding!

[Comment] lines 397: was %C reported in results?
[Response] Sorry for the misleading word. We have deleted the phrase "total C" in the revised MS. All the C reported in the result table are SOC concentration.
[Comment] line 465: The jars were sealed with an airtight lid? Was the environment anaerobic between sampling? If so, this seems like it may be a problem, especially for microbial community analyses.
[Response] Yes, the jars were sealed with an airtight lid. However, all the jars were flushed periodically with synthetic air (20% O 2 , 80% N 2 ) when the headspace CO 2 concentrations reached over 1000 ppm to minimize buildup of CO 2 and prevent the anaerobic environment  . Therefore, we think that this settlement would guarantee the aerobic environment between sampling, and thus would not influence the microbial community.
[Comment] line 486, 3 pool model: Can you comment on the duration of the incubation in terms of the 3-pool model. That is, is 88 days a long enough timeframe to estimate these 3 pools?
[Response] Very good comment! For soils from regions other than permafrost ones, 2-pool model is usually (but not always) good enough to simulate the soil C respiration in incubation studies (e.g., .
For soils from permafrost regions, it is still unclear, though both two-and three-pool models were found to fit equally well with data from a recent synthesis conducted by .
To demonstrate this point, we compared the performance of a two-pool and three-pool C decomposition modeling using all the sample data from our 80-day incubation. Our analysis showed that three-pool and two-pool model have similar AIC (-57.9 vs. -55.6 for three-pool and two-pool model, respectively, Fig. R16), indicating that overfitting did not happen to the three-pool model. By contrast, three-pool model display much better performance in estimating carbon flux rate for our data (r 2 = 0.83 vs. 0.65; RMSE = 0.05 vs. 0.08 for three-pool and two-pool model, respectively, Fig. R16). Taken together, we chose to use the three-pool model as it more accurately describes C dynamics.
Given that our 80-day incubation belongs to short-term incubation, we only used fast and slow C pool size to explain the variations of CO 2 production in both ordinary least square (OLS) regression and SEMs. We have added these points in the Method section of revised MS (Page 28, line 592-601). Thanks for your understanding!

Fig. R16
Comparison of three-pool (a) and two-pool (b) model performance using data from our 80-day incubation experiment.
[Comment] 83: Here and throughout: 'microbial community': should this be microbial community structure, composition, abundance?
[Response] Very good comment! We have revised the "microbial community" to "microbial abundance" here. Also we have specified the microbial community to microbial composition, abundance throughout the MS.
[Comment] 103-104: 'long-term permafrost C loss' does this mean C mineralization after the permafrost thawed? If so, then by definition, long-term loss has to be correlated with slower cycling pools. Or, does this mean that the C that is frozen in permafrost is not labile (e.g., versus a fast cycling pool that only remains as SOC because it is frozen).
[Response] Yes, it means C mineralization after the permafrost thawed. To avoid this confusion, we have rephrased the sentence as "Instead, slow degrading C fractions were found to be the more important for the long-term permafrost C loss after thaw in laboratory incubations (>1 year) (Schädel et al., 2014)" (Page 5-6, line 99-101). Although by definition, long-term C loss could be correlated with slower cycling pools in models, such relationship have not been well illustrated using data from laboratory studies . By presenting the results from , we aim to emphasize the importance of recalcitrant C compounds in controlling CO 2 emissions. Thanks for your understanding!

[Comment] 85-86: Association of high CH4 production with high methanogen abundance does not necessarily mean limitation
[Response] Good comment! We have changed the word "limit" to "affect".
[Response] Done as suggested.
[Comment] 102: change 'to be the dominator for', to 'to be the dominant driver of' [Response] Done as suggested.
[Comment] 113-115: many many studies separate active layer and permafrost samples when using in incubations. I would change the sentence and/or add references [Response] Thanks for the comment. We changed the sentence to "it remains unknown whether controls over soil C loss in active layer and permafrost deposits are different or not".
[Comment] 123-125: I'm confused by this sentence; not sure how to suggest an edit.
[Response] Thanks for the comment. We have deleted the sentence and reorganized the paragraph in the revised MS (Page 6-7, line 115-123).
[Response] Done as suggested.
[Comment] 221: with two times larger XX? Missing a word in this sentence [Response] We have changed it to "with two times more abundant than cutin".

Reviewer #1 (Remarks to the Author):
My comments here focus mostly on how the authors addressed previous comments about the SEM, drainage, and organic layer. Overall the authors did a thorough job of considering each point. It appears the SEM has improved by considering the nonlinear effect of soil moisture. Although this made the resulting SEM diagram look different, the primary conclusions of the paper were not changed.
The authors also added a new paragraph (lines 413 -438) with qualifying statements about the influence of drainage and the organic layer on their results. By recognizing these issues, it gives more confidence that the authors have carefully considered where the interpretation of their results may not apply. This may also help to address the concern mentioned by Reviewer #2 that the heterogeneity of the landscape may not be represented by such a small number of sites, because the results mostly apply to upland soils.
As a side note and for further study, it would interesting to see the same analysis presented for more layers in the soil profile. This may reveal the gradational effects of organic matter quality and microbes with depth and soil temperature (a result more useful to global carbon models), which could strengthen the simpler paired analysis between just one AL and PF of this study.

Reviewer #2 (Remarks to the Author):
Dear authors, Thank you for improving your paper by including the majority of the reviews. Moreover, I want to thank you for your detailed answers on all the reviewers' comments. Especially the additional method figure in the supplement is great for a better understanding of your methodical idea.
The only point I found not satisfying is the answer on my major concern: the sample representativeness. Are 10 samples enough to draw conclusions on the regional scale: 5 sites at 2 depth equals 10 samples; including 3 replicates? In total, you looked at 30 samples. Of course permafrost regions are not easy to access and the logistical effort to get samples is huge, and I am sure that you "have tried your best to obtain these typical Tibetan samples", but it seems to me that a bigger database would be more appropriate. I definitively agree that your story could be of broader interest, but this sample size limits its validity. It is a great first step in the right direction, but potentially not enough for an interdisciplinary high impact journal.
Detailed comments: L1: I agree on your rebuttal on changing the "determinants" in the title. Nevertheless, I would delete the "Different". This would strengthen your point that the determinants are the major novelty of your paper.   Table S2 and S3: Please add the sample number to these tables

Reviewer #4 (Remarks to the Author):
I was asked to check if suggestions made by reviewer 3 were met, I should say most of them, please see below.
I agree the information generated in this work is really important and can be used in many ways, I do not want to elaborate more on this since all reviewers expressed it extensively. Is a great work and it should be published however, few things need to be fixed.
My main concern is on the incubation time more than on the use of a two or three C pools model.
Conclusions and projections of C release due to permafrost thaw from the region in study are made based on the 80 days' incubation, if I understood it correctly. I wonder how precise the estimations of C pools and decay rates can be with such a short incubation time. I suggest to find a data set with a longer incubation time (1 year, at least) and test your C pool models, there are many people with such of data even with similar temperature of incubation. I would like to see more discussion related to the role of the slow decomposing C on total C release from the incubated soils and on projections made.
I strongly recommend to harmonize the use of CO2 production to CO2-C, is not the same thing and I believe authors want to say C released as CO2 (CO2-C) instead of only CO2. This problem is present across the text and figures; it is really confusing in the way as it is now. The same with the terms "production, emissions, loss, accumulation (cumulative)", most likely, all those terms are used to indicate the same "CO2-C release".
Reviewer comment lines 267 -269 not clarified yet, changing to arithmetic did not solve it, I think authors mean 169 for AL and 223 for PF, is that correct?
I think problems on the statistics were fixed as recommended.
Issues on the introduction and a more detailed discussion on mechanisms was also done.

Responses to Reviewer #1
[ [Response] Very good point! We fully agree with the reviewer that more insights could be provided for model developments by examining gradational effects of organic matter quality and microbes with depth and soil temperature. Based on this point, a future study will be designed to explore more layers in more soil profiles so as to gain a complete understanding on the controls over carbon release across Tibetan permafrost regions.

Responses to Reviewer #2
[Comment] Thank you for improving your paper by including the majority of the reviews. Moreover, I want to thank you for your detailed answers on all the reviewers' comments. Especially the additional method figure in the supplement is great for a better understanding of your methodical idea. The only point I found not satisfying is the answer on my major concern: the sample representativeness. Are 10 samples enough to draw conclusions on the regional scale: 5 sites at 2 depth equals 10 samples; including 3 replicates? In total, you looked at 30 samples. Of course permafrost regions are not easy to access and the logistical effort to get samples is huge, and I am sure that you "have tried your best to obtain these typical Tibetan samples", but it seems to me that a bigger database would be more appropriate. I definitively agree that your story could be of broader interest, but this sample size limits its validity. It is a great first step in the right direction, but potentially not enough for an interdisciplinary high impact journal.
[Response] Thanks again for the reviewer's insightful comments! We admit potential limitations of the relatively small sample size. Following the editor's (Dr. Graham Simpkins) suggestion, we explicitly stated the limitations and potential issues of site representativeness in the revised manuscript. To be specific, the limited samples collected from the upland permafrost areas may induce the following uncertainties. First, the limited sample size may lead to uncertainty in predicting future CO 2 -C loss across the Tibetan Plateau.
Although Tibetan permafrost mainly occurs in upland areas with good drainage conditions , flooding has also occurred in some lowland areas (Cotrufo et al., 2013). The poor drainage conditions with low oxygen availability in these lowlands can significantly inhibit the CO 2 -C release Schädel et al., 2016). Consequently, the potential CO 2 -C release estimated in this study likely overestimates the C loss that can be expected under natural conditions across regional scales. Second, the limited sample size may also induce uncertainty in exploring controlling factors that regulate the CO 2 -C release. It has been suggested that anaerobic CO 2 -C release was mostly explained by the environmental controls (e.g., relative water table position) in lowland regions with waterlogged soils (Treat et al., 2015). Hence, the controls over the CO 2 -C released reported in this study mainly applies to   [Response] Thanks for the reviewer's positive comments.
[Comment] My main concern is on the incubation time more than on the use of a two or three C pools model. [Response] Very good comment! Following the reviewer's suggestion, we extracted the data of C flux rate from a long-term incubation (390 days)  to validate the length of incubation. To increase data comparability, only data from 5 o C incubation and similar sampling depth were used. To do this validation, we established another dataset with observations of only first 85-day C flux rate from the same incubation experiment. Then we applied three-pool model to the same sample with different experimental periods separately. The comparison of the mean estimated parameters indicated that the incubation time would barely affect the parameter for the fast C pool (i.e., k 1 and f 1 ) (Table R1). Consequently, C loss from short-term incubation (i.e., 85 days) was little affected by incubation duration for both active layer and permafrost deposits (19.3 vs. 20.4 mg C g -1 SOC for active layer and 28.8 vs. 30.1 mg C g -1 SOC for permafrost deposits). By contrast, incubation time does have some influences on the estimated parameter associated with the slow and passive C pool (i.e., f 2 ) (Table R1). This may lead to a certain degree of uncertainty in longterm projection for C loss (e.g., 194.8 vs. 156.6 mg C g -1 SOC for 10200-day incubation for permafrost deposit). We have added these comparisons in the revised MS (Page 27, line 582-590). b f 1 and f 2 are the fractions of fast and slow pools, k 1 , k 2 , k 3 are the decay rates of fast, slow and passive pools, respectively. We assumed that soils would be thawed for only 4 months per year and stay at a constant temperature of 5 o C. Then 1 year of incubation represents in situ conditions for 3 years. Thus, the next 85 years till 2100 represents incubation for roughly 28.3 years (≈10200 days).
Although incubation time may affect the accuracy of the parameters related to slow degrading C, these uncertainties would not alter our major conclusion (i.e., Carbon quality was most crucial for active layer carbon emission, whereas soil microbial abundance was more important for permafrost carbon loss after thaw) for the following two reasons: First, our conclusion was directly drawn from the SEM analysis, in which the estimated C pool sizes were only a small part of the matrix (C:N, lignin-, cutin-, suberin-derived compounds and different C pool sizes) describing C recalcitrance. As mentioned in the previous version of MS, given that these variables in C recalcitrance group were closely correlated, we conducted principal components analysis (PCA) analysis to create multivariate functional index to represent C recalcitrance . The first component (PC1) was then introduced as a new variable into the subsequent SEM analysis. As depicted in the Table R2, compared with carbon pool size, the PCA1 for C recalcitrance were more correlated with relative abundance of SOM components (i.e., lignin-, cutin-, suberin-derived compounds) in both active layer and permafrost deposits. Hence, compared to the SOM components, C pool sizes estimated from models were less important in the SEM analysis.
Second, our conclusion did not change even if we removed carbon pool sizes in the SEM. As depicted in the Fig. R1, removing the carbon pool size would decrease the standardized direct effects of carbon quality on CO 2 -C release to some degree (from -0.97 to -0.67 in active layer; from -0.35 to -0.20 in permafrost deposits). Nevertheless, C quality was still the most important direct predictor of C loss for active layer, soil microbial abundance also remained to be the most import direct predictor for permafrost deposits. Taken together, incubation time would not alter our conclusions.  Based on the above-mentioned parameter comparisons, we agree with reviewer that the incubation time may induce some uncertainties during the long-term projection of potential C loss under warming scenario. Nevertheless, it should be noted that predicting long-term C loss is not the major aim of this study, which was requested by the Reviewer #2. To be specific, this study mainly aims to determine controls of CO 2 -C release for both active layer and permafrost deposits after thawing), which was not originally designed to predict long-term C loss under warming scenario. In response to the Reviewer #2's comment "predict C loss across permafrost zones under warming scenario should be done for a manuscript for nature communications", we added some discussions the potential C loss from the Tibetan Plateau under different warming scenarios (Page 12, line 241-249). Moreover, as the validation mentioned above, the incubation duration did not affect the estimated C loss from short-term incubation (i.e., 85 days). The estimated CO 2 -C release for 80-day incubation in our study was highly correlated with the measured CO 2 -C release (Fig. R2, r 2 = 0.94, RMSE= 4.67). Taken together, we think that 80-day incubation is appropriate for the major conclusions drawn in this study (i.e., Carbon quality was most crucial for active layer carbon emission, whereas soil microbial abundance was more important for permafrost carbon loss after thaw). Thanks for your understanding! Figure R2. The relationship between estimated cumulative CO 2 -C release and measured cumulative CO 2 -C release from our 80-day incubation.
[ [Response] Very good comments! The C release projection was made as the following two steps: First, we estimated model parameters using Markov Chain Monte Carlo (MCMC) approach (Schädel et al., 2013;. To be specific, we applied the threepool model to each of the 30 soil samples separately at a given incubation temperature as follows: where R(t) is the CO 2 -C emission rate at time t (mg C g -1 SOC d -1 ), C tot is the initial soil SOC content (i.e., 1000 mg C g -1 SOC), f 1 and f 2 are the fractions of the fast and slow pools, and k 1 , k 2 , and k 3 are the decay rates of fast, slow and passive pools, respectively. In this soil C decomposition model, C tot and R(t) are measured quantities. The five parameters (i.e., f 1 , f 2 , k 1 , k 2 and k 3 ) were then determined by a Markov Chain Monte Carlo (MCMC) approach (Schädel et al., 2013;. Before applying MCMC to each sample, the prior parameter range (Supplementary Table 7) was set as widely as possible in the initial model so as to cover the possibility for all the soil samples. It should be noted that the prior range was adjusted a little bit depending on site conditions. For example, owing to the low C emission rate at CMH site, we chose a longer turnover time for the slow and passive C pool (upper limit in Supplementary Table 7) for these soils.
Second, we predicted CO 2 -C release using the parameters generated above. Maximum likelihood estimates (MLEs) were quantified for all the well constrained parameters, the mean values were calculated when parameters were poorly constrained . The final parameters estimated from MCMC (Table R3) were then used to make short-term (80-day) and long-term (10200-day, ~ 85 years in situ until the year 2100) projection of CO 2 -C release for each of the 30 soil samples separately by using the following function: where C cum is the cumulative CO 2 -C release at time t (mg C g -1 SOC).
We would like to mention that those values in the Table S5 in previous MS are the initial range of the five parameters for most sites, not an average for all sites. The prior range was adjusted a little bit depending on site conditions. As you can see from the above descriptions, owing to the low C emission rate at CMH site, we chose a longer turnover time for the slow and passive C pool (upper limit in Supplementary Table 7) for these soils. Nevertheless, to avoid this confusion as the reviewer raised, we have clearly described this point in the revised MS (Page 26-27, line 569-574) and added an explanation of the parameter range for CMH site in the Supplementary  f 1 and f 2 are the fractions of fast and slow pools, k 1 , k 2 , k 3 are decay rates of fast, slow and passive pools, respectively. The interquartile range is presented in square brackets.
[Comment] I would like to see more discussion related to the role of the slow decomposing C on total C release from the incubated soils and on projections made.
[Response] Very good point! Following the reviewer's suggestion, we discussed the slower decomposing C on total C release by analyzing the MRT (Table R4) and the contribution of different C pools to total C release (Table R5). Specifically, we added one paragraph regarding this issue as follows: "As shown by SEM analysis, CO 2 -C release from the active layer was primarily directly determined by C recalcitrance. The determinant role of C recalcitrance observed in this study, together with previous findings in arctic and boreal regions , jointly suggest the vital role of more slowly degrading C in governing SOC turnover in the active layer.
Interestingly, short turnover times for the fast C pool were observed in both the active layer and the permafrost deposits, with an average turnover time of 0.34 years (Supplementary Table 5). The estimated short turnover time for the fast C pool was supported by previous results in high-latitude regions . This small C pool (<1% of total C) (Fig. 1) having a short turnover time indicates that long-term permafrost C degradation will be dominated by more slowly degrading C . To further reveal the role of the more slowly decomposing C on total C release, we analyzed the contribution of different C pools to total C release. The results indicated that, during the entire 80-day incubation, approximately 29.0% and 64.9% of the C released as CO 2 originated from the fast and slow C pools, respectively, whereas only 6.1% of CO 2 -C release originated from the passive C pool (Supplementary Table 6). However, when projected to a 10200-day incubation period (~ 85 years in situ until the year 2100), the contribution of the fast C pool substantially dropped to 2.4%, whereas the contribution of the slow and passive C pools increased to 73.6% and 24.0%, respectively (Supplementary Table 6). Taken together, these results demonstrated a crucial role of more slowly degrading C in long-term permafrost C degradation" (Page 14-15, line 293-312).  [Response] Following the reviewer's suggestion, we harmonized the use of CO 2 production to CO 2 -C release through the revised MS.
[Comment] Reviewer comment lines 267 -269 not clarified yet, changing to arithmetic did not solve it, I think authors mean 169 for AL and 223 for PF, is that correct?
[Response] Sorry for the confusion. 169 ± 35 μg CO 2 -C g -1 SOC d -1 in the previous MS was the arithmetic average of AL and PF. To avoid the confusion, we rephrased the sentence as follows: "Arithmetic mean of CO 2 -C release rate from the active layer and permafrost deposits at these five typical sites on the Tibetan Plateau was approximately 116 ± 27 μg CO 2 -C g -1 SOC d -1 and 223 ± 44 μg CO 2 -C g -1 SOC d -1 for 80-day laboratory incubation, respectively." (Page 11, line 233-236).
[Comment] I think problems on the statistics were fixed as recommended. Issues on the introduction and a more detailed discussion on mechanisms was also done.
[Response] No responses needed.

Reviewer #2 (Remarks to the Author):
Dear authors, Thank you for including the paragraph explaining the small sample size. I agree that your story could be of broader interest, and if the editors of Nature Communucations agree on continuing with your manuscript despite this limited sample size, I am ok with this as well.
Best regards

Reviewer #4 (Remarks to the Author):
Determinants of carbon release from the active layer and permafrost deposits on the Tibetan Plateau. By Leiyi Chen et al.
Authors addressed my concerns in the manuscript. I recommend to have a quick mention on the similarities and differences between soils from the Tibetan Plateau and those from Dutta et al.
Other than that, I recommend to publish it.