Data interpretation and integration:

There seems to be some missed opportunities with regards to the data currently in the manuscript and the data available in the literature.

I was very excited to read this manuscript, anticipating the novel use and interpretation of the time series data. Having three sampling points over a twenty-year time period across different parent materials and vegetation types *with* statistical replication (3 pits per site) is quite a unique and powerful dataset! I was disappointed to see no results from the time series featured in the abstract, and no simple modeling exercises to parse the bulk C into pools with associated mean residence times (or system ages, or transit times, etc.). The paper cites the Baisden et al. (2013) paper but does not utilize the simple spreadsheet model available in the supplementary materials of that work. It seems that at least in the surface soils, the respiration and bulk radiocarbon data could be combined to yield some insight into partitioning and turnover of C in these soils. I understand that more complex modeling exercises are beyond the scope of what the authors are trying to convey. However, given that the paper is focused on the influence of mineralogy and climate on decadally cycling C, it seems appropriate to try to explore how the size and turnover of that pool varies across the sites.

There appears to be a much larger dataset from previously published work that could be used to inform the interpretations of the current dataset. There is density fraction data from Rasmussen et al. (2018). I’m extremely curious to know how the radiocarbon value of the respired CO2 compares to the radiocarbon value of the free/light fraction. I’m also curious to know how the respiration rates of the bulk soils compared to the respiration rates of the soils with the litter manipulations (Rasmussen et al., 2008).

Incubation data:

Figure S2 caption states that the soils were incubated from 4-40 days. Why would the soils be incubated for different time periods when the data presented is a flux measurement (CO2 respired per day)? Varying the length of the incubation would have a strong influence on the total amount of C respired and the associated radiocarbon measurement. I supposed some soils were incubated for a longer time period in order to collect enough CO2 for a radiocarbon measurement. If this is the case, the potential artifacts of this approach need to be explicitly discussed. For example, if a soil is respiring at a lower rate, it might imply that the “labile” pool is much smaller. Continuing to incubate this soil for a longer time period would potentially allow for the decomposition of less readily available C, causing the radiocarbon value to be skewed to a more depleted value.

The proposed source and interpretation of the laboratory-respired C is inconsistent in the manuscript. In the methods and results section, the pool of respired C is described as being transient and representative of “…the majority of C leaving the soil via heterotrophic respiration (Lines77-79).” The text in this section of the paper strongly implies that the radiocarbon value of the CO₂ captured during incubation reflects the radiocarbon value of C being respired in the field, specifically that which is cycling on a decadal scale. However, in the discussion, when explaining depleted radiocarbon values of CO₂ from subsurface granite soils, the laboratory-respired CO₂ is described as being sourced from persistent stabilized pools (lines 434-438). Here, the incubation conditions are described as alleviating constraints on decomposition, allowing for decomposition of C which is stabilized under field conditions. Similarly, in the results section, some respiration data was excluded from analysis due to unexpectedly depleted values resulting from “… disturbance of the soil during sample extraction and preparation (lines 363-365).” No doubt these statements imply a high degree of complexity associated with the interpretation of incubation radiocarbon data. It may be necessary to delve into more of this complexity and the philosophical justifications behind one interpretation or another.

Short-range-order mineral abundance as an explanatory variable:

One of the main findings of this work is the dependence of soil C concentration/stock and radiocarbon abundance on the abundance of oxalate-extractable metals. The manuscript also features the lack of correlation between soil C variables and crystalline oxyhydroxide phases.

The acronyms PCM (poorly crystalline metal oxides) and CRM (crystalline metal oxides) are introduced. Because the manuscript relies so heavily on the relative abundance of these two pools of extractable metals, it is important to be specific and accurate about what they represent. Almost all of the minerals that are selectively dissolved are more accurately described as hydroxides and oxyhydroxides rather than oxides. The term PCM includes pyrophosphate-extractable pools of Fe and Al, which are amorphous (not poorly crystalline). Truly using the short-range-order pool of Fe and Al rather than the oxalate-extractable pool would necessitate the subtraction of the pyrophosphate numbers from the oxalate numbers. Similarly, the CRM value excludes Al from crystalline hydroxide phases since Al is not redox soluble. Including Al phases in one pool (PCM) while excluding them from the other (CRM) negates the true comparison of the explanatory power of these mineral pools.

In a more general sense, testing the explanatory power of extractable metals for C characteristics in these soils does not seem to be novel. See results from previous work:

From the abstract of Rasmussen et al. (2005): “We found highly significant, positive correlations between Al-humus complexes, SRO Al minerals, and total C content.”

From the abstract of Rasmussen et al. (2008): “This study corroborates the varied response in soil C mineralization by parent material and highlights how the soil mineral assemblage and litter type may interact to control conifer forest soil C response to climate change.”

From the abstract of Rasmussen et al. (2018): “Results indicated that short-range order mineral phases were the dominant factors accounting for the variation in soil carbon content and residence time.”

Climate as a categorical variable:

Using climate as a categorical variable does not appear to be appropriate. Vegetation is covarying with climate, and this strongly influences C stocks and turnover. This fact is acknowledged in Rasmussen et al. (2018) where the categorical variables are parent material and ecosystem instead of parent material and climate. This fact is further driven home by the Rasmussen et al. (2008) paper where differences in litter chemistry between vegetation types were so large that they had significant explanatory power for variance in soil respiration. It is also possible that NPP and/or above- vs. below-ground C allocation might vary between “warm”, “cool”, and “cold” sites. There’s also the issue of differences in fire regime across the different ecosystems (Rasmussen et al., 2018). Perhaps the fact that temperature had no explanatory power as a continuous variable is actually a more interesting result? What if litter chemistry and mineralogy were important and climate was not? Wouldn’t this be an interesting finding to explore?

Minor line-by-line comments:

Line 10: The results associated with the repeated sampling do not seem to be highlighted anywhere in the abstract.

Line 16: Could it be that climate was highly significant as a categorical variable because as a categorical variable it encompasses all the other variation across sites? How is using climate as a categorical variable different than using site as a categorical variable? Statistically, the tests would be identical, but the interpretation of the result would be very different.

Line 21: The acronym PCM? Has the convention changed from using "short range order" to "poorly crystalline metal" (SRO has been swapped for PCM)?

Line 38-39: “… insight into the relevant time scales associated with these key soil forming factors.” Something doesn't quite work with the meaning of this sentence. Is "time scales" referring to the fact that temperature changes much faster than the SRO mineral content of the soil?

Line 53: The sorptive capacity of minerals is dependent on many things in addition to the density of hydroxyl groups. Perhaps modify the first part of this sentence to be more general and then highlight the especially strong bonding associated with ligand exchange?

Line 65: You might specify that the bomb-derived radiocarbon is the tracer.

Line 72: Would it be appropriate to cite Graven's or Sierra's paper on the decline of the bomb curve here? I think it might be important to point your readers to additional information on this specific point, as many soil scientists are unaware of this fact.

Lines 77-79: The phrasing here might need a little clarification. Some might argue that the majority of the C leaving the soil via heterotrophic respiration under field conditions would likely have a similar radiocarbon value as that year's atmosphere (See figure 9 of Phillips et al., 2013;  full reference given below). Some might additionally argue that the C respired in a laboratory incubation is not the same pool of C respired under field conditions, and that the radiocarbon value of lab-respired C is some metric of the mean age of the C that may be more available for decomposition under conditions of disturbance.

Lines 141-142: “Samples were collected from the A horizon only in 2001, and from both the A and B horizons in 2009 and 2019.” This does not seem correct according to the associated publications, or the data presented in this paper.

Lines 150-151: “We omitted the 2009 samples from the incubation experiment to save on time and analysis costs, and because sample material was only available from a single profile at each site.” Doesn't this strongly effect your ability to examine the dynamics of this "decadally cycling pool"? Also, it looks like there were three pits sampled in 2009 according to Rasmussen et al., 2018?

Line 176: Here you switch to SRO, then back to PCM below.

Line 184: “… the difference of dithionite-citrate extractable Fe and ammonium-oxalate extractable Fe as a proxy for CRM abundance.” This obviously is excluding gibbsite, which cannot be quantified with selective dissolution... wouldn't the andesite and/or granite soils contain gibbsite in some quantity? Is that important in the context of the influence of crystalline oxides on SOM?

Lines 196-197: “…values of Δ14C < 0 indicate radioactive decay of 14C, which has a half-life of 5730 years.” Samples with values <0 per mil can still have bomb C in them. Also, all radiocarbon values reflect some level of radioactive decay. Maybe just emphasize that higher values indicate faster cycling, with values above zero confirming the incorporation of significant amounts of bomb C, implying decadal cycling?

Equations 1-4: How are these random error terms constrained and/or defined?

Line 257: “… substantial variation in SOC concentration between 2001, 2009, and 2019 in the surface mineral layers.” Were the samples taken during the same month/season across the years? Were there significantly different drought conditions, el nino, atmospheric river events, fire, etc. across the years?

Lines 362-364: This seems a bit of a "throw away" explanation for these outlier values. These samples wouldn't have been any more or less disturbed during sampling than the others, would they? I think it's fine to exclude strong outliers (how else can you possible do statistics on systems with such high variance?), but it seems like a more process-based or mechanistic explanation could be found given all the ancillary data and the high level of expertise of the author team.

Lines 394-395: What is the hypothesis associated with this testing the explanatory power of crystalline Fe oxyhydroxides? Given the information in the literature, why would you expect a relationship between crystalline Fe/Al oxyhydroxides and 14C? Wouldn't you expect a relationship between pyrophosphate-extractable Fe/Al and %C and/or 14C given the pH of the soils?

Lines 470-474: This is not the only conclusion that can be reached by the data presented. Indeed, the carbon could be cycling more quickly in the p. pine ecosystems regardless of what mineral surfaces are available to provide sorptive protection, especially since only the suface soils were incubated… also these conclusions seem highly similar to the conclusions of the Rasmussen et al. (2018) paper: “These results suggest a link between the degree of soil weathering and C storage capacity, with a greater divergence in storage capacity and residence time in the Inceptisols, Entisols, and Andisols of the white fir and red fir ecosystems relative to minimal variation in the highly weathered Ultisols and Alfisols of the ponderosa pine ecosystem.”

References:

Baisden, W.T., Parfitt, R.L., Ross, C., Schipper, L.A. and Canessa, S., 2013. Evaluating 50 years of time-series soil radiocarbon data: towards routine calculation of robust C residence times. Biogeochemistry, 112(1), pp.129-137.

Phillips, C.L., McFarlane, K.J., Risk, D. and Desai, A.R., 2013. Biological and physical influences on soil 14 CO 2 seasonal dynamics in a temperate hardwood forest. Biogeosciences, 10(12), pp.7999-8012.

Rasmussen, C., Throckmorton, H., Liles, G., Heckman, K., Meding, S. and Horwath, W.R., 2018. Controls on soil organic carbon partitioning and stabilization in the California Sierra Nevada. Soil Systems, 2(3), p.41.

Rasmussen, C., Southard, R.J. and Horwath, W.R., 2008. Litter type and soil minerals control temperate forest soil carbon response to climate change. Global Change Biology, 14(9), pp.2064-2080.

Rasmussen, C., Torn, M.S. and Southard, R.J., 2005. Mineral assemblage and aggregates control carbon dynamics in a California conifer forest. Soil Science Society of America Journal, 69(6), pp.1711-1721.

The authors present in their manuscript “Soil minerals mediate climatic control of soil C cycling on annual to centennial timescales” a very unique and outstanding data set. This study is a follow up of three former field studies at the same sites and I was excited to read about new insights derived from this well established field studies. The authors present that mineralogy (expressed by metal oxides) is attenuating the climatic effect on SOC cycling and used an extensive 14C dataset of bulk end respired 14C values. The authors conclusion however are not beyond what was reported before from the same sites in the cited studies mainly by Rasmussen et al. in several years. In fact the data interpretation seems to not go beyond the previous knowledge and just supporting the same findings derived from 2001 and 2009 field studies. This is supported by a quite weak discussion. Beside this lack of novelty and missing exploration of more and needed mechanistic understanding of SOC cycling depending on climate and geochemical properties. Rather than supporting very similar results in study compared to the previous studies, the exploration of the sequence from 2001 to 2019 could be the main novelty here.  However, I have some major concerns regarding the comparability of the previous data 2001 and 2009 and the new data 2019. First of all, I had difficulties to follow the authors description of the data source. It is not always clear when the 2001, 2009 of 2019 data is used and how the different years, especially 2001 and 2009, are combined. It should be possible to follow the whole manuscript and data source without the need of the reader to read the other publications published previously by a similar group of authors (e.g. Rasmussen et al. papers).

May main concern is the different sample depth between the study years. Referring to section 2.2 but also effecting than the results. The actual difference in sampling layers in 2019 and the horizon sampling in 2001 and 2009 is not clear and more prove is needed to be sure that there are no substantial differences, which would overlay the reported findings. Given the difference in soil development stage, I can imagine that these can be quite different in terms of A to B horizon transition. After I checked Rasmussen et al (2018b) it is clear that the depth are substantially different. Thus, in the studies form 2001 and 2009 the upper sampling depth was only a few cm of the A horizon. These samples would consequently contain a much larger proportion of SOC that is much more dominated by more modern 14C signals as they are most likely more dominated by fresh inputs compared to 10cm layers which contain a larger proportion of B horizon material and thus older material. It is not clear if and how the authors corrected for this.

The authors applied spline fitting for the soil properties (please clarify which properties and section 2.6). I am not convinced that this solves the issue of 14C pools with depth.

How did the authors deal with the different depth for bulk and respired 14C in Fig. 2? When comparing the individual years in bulk 14C in Fig. 3, how can the authors be sure that the drops in delta14C from 2009 to 2019 are not overlaid by depth differences? For most sites it appears that differences between 2001 and 2009 are much smaller, which are both sampled by horizon and potentially more similar depth (?) and the difference to 2019 is larger. This depth differences are likely to affect the delta14C of respired to a much larger extent. Would depth explain the differences between 2001 (Fig. S3) and 2019 (Fig. 2)?

This depth difference would also influence the mineralogy and PCM and CRM between 2001/2009 and 2019. When I understand correctly, the authors took only the 2001 data for the metal oxide concentrations (e.g. Fig. 5) for both years presented. But the samples from 2019 might contain more metal oxides when containing more B horizon material. The authors could prove this by analyzing only a subset or composites and compare to the other years.

The authors need to provide more prove how the different depth are comparable and that the 14C data can be really compared between the years. At the current state, I am not convinced that the comparison can be made in a way the authors present it.

I also have major concerns regarding the incubation of the soils. The incubation times seem to differ between samples on the range of 4-40 days. It is completely unclear how long which sample was incubated and such huge differences in incubation time question the comparability of the results. Especially for the respired 14C the incubation time will highly effect the SOC pools that are respired and how would this be comparable when the incubation time differs by factor 10 between high and low C samples? The authors should also discuss the effect of incubating the soils from different climate at similar temperature. The authors did assess the maximum respiration and not the real respiration. This needs to be critically discussed and assessed how this would effect the 14C respired.

The authors miss completely to discuss the potential influence of such factors (sample depth and incubation) on the presented results. The authors should rethink limitations of their results and interpretation.

Some specific aspects:

The authors should improve all figures to avoid all the repetitions in legend, axis titles etc.

Line 86: Check citation

Line 124: The authors should reproduce this map for this manuscript. the methods should be clear without looking at other papers.

Line 140:  remove C. Rasmussen as the citation (Rasmussen, 2004) is enough

Line 150: The authors should critically discuss the fact that samples from 2001 were stored for 18 years and that this could influence the incubation results. The authors carefully considered this by pre-incubation for a week and drying the 2019 samples to have the same disturbance. But still the alteration of the 2001 might have been much larger.

Line 157: Was the pre incubation at same temp as the final incubation?

Line 163-165: What is the meaning of incubation each sample to 10000 ppm CO2? How long was the incubation and was it the same for each sample from different years? If not it might not be comparable. In the caption of Fig. S2 it is reported between 4 and 40 days.

The incubation time needs to be the same for every sample to be comparable. Comparing 4 and 40 days is nearly impossible. It is not clear from the manuscript what is compared with each other therefore, I cannot follow if the differences in 14C respired are highly affected by different durations of incubation.

Line 168: It is not clear to me from which year the data comes finally. Fig. 5 shows only 2001 but the analysis were done in 2001 and 2009 but not in 2019. Please be clear which data comes from which study. It can not be expected that the reader reconstructs all the authors research form 2005-2019.

Line 193: The authors should clarify that delta 14C  is corrected for sampling time

Line 203: The depth differences need to be clear.

Line 205 and all stats: Climate and parent material are defined by sites along the gradient. Should sites not be included as a random factor in the models? Otherwise it is only testing between sites.

Line 253-255: Did the BD differ between 2001 and 2009? If yes, how can the authors average here and would this explain much larger errors for the stocks?

Line 253: Why do the authors cite here these references?

Line 264-265: Unclear what the authors mean. andesitic more than basaltic and granite? but thus is not always true, especially for the 2001 data

Line 277: 2009 data should also be in the supplement for comparison

Line301-304: This is not result.

Line 307-308: I am not convinced that depth can be directly compared due to potential much larger input of faster cycling in shallower samples. Thus, could simply the mixing of deeper SOC in the 2019 samples can influence the depleting ind delta14C?

Line 327: Please see comments before regarding depth. This might be much stronger when looking at respired 14C values and 7 of 9 sites showed higher 14C depletion in 2019. Thus more deeper SOC in the sample?

Line 360-364: Rather discussion

Line 388: It should be clear from the methods and figure caption that the data is from the Rasmussen et al (2018) paper. Which needs more clarification

Line 408-411: The start of the discussion is rather introduction and the authors do not support their statements with the literature here.

Line 422-426:  Thus this study just confirmes what was previously found

Line 435: How can the magnitude be the same when days of incubation are different?

Line 482-486: This is only based on temperature discussion. However, it is more and more evident that soil moisture rather than temperature control the warming response of soils The authors discussion is rather incomplete and not supportive enough for this statement. E.g. Zosso, C. U., Ofiti, N. O. E., Soong, J. L., Solly, E. F., Torn, M. S., Huguet, A., Wiesenberg, G. L. B., & Schmidt, M. W. I. (2021). Whole-soil warming decreases abundance and modifies the community structure of microorganisms in the subsoil but not in surface soil. SOIL, 7(2), 477–494. https://doi.org/10.5194/soil-7-477-2021