General Comments

This manuscript investigates the content, molecular composition, and biodegradability of water-soluble organic carbon (WSOC) across a 7.4 m soil profile at the southern boundary of the boreal forest. The authors employ a combination of spectroscopic analyses and laboratory incubations to evaluate depth-resolved changes in WSOC properties and their relation to biodegradability. The study is timely and relevant given the sensitivity of boreal carbon stocks to climate change and permafrost degradation. It contributes valuable data on deep soil carbon dynamics, particularly from a region (southern margin of the boreal forest in Northeast China) that is underrepresented in current literature.

The manuscript is generally well-structured and clearly written, with a sound experimental design and appropriate data analysis. However, a few aspects require clarification or improvement to enhance the manuscript's scientific rigor and presentation. These include a better contextualization of the study’s novelty, clearer methodological justifications, and refinement of certain interpretations to avoid potential overgeneralization.

Specific Comments

Novelty and Contribution:

The manuscript would benefit from a clearer articulation of how this study advances current understanding beyond existing work (e.g., studies from Alaska, Siberia). The novelty lies in deep-profile in situ WSOC characterization at the southern boreal margin—this should be emphasized more explicitly in both the abstract and introduction.

Methodological Justification:

The use of nutrient amendments (NH₄NO₃ and K₂HPO₄) in biodegradability assays should be more critically discussed in the Methods and Discussion sections. While this standardizes microbial activity, it may inflate BWSOC estimates compared to natural field conditions.

The use of extracted microbial inoculum per soil layer could introduce variability due to differential microbial biomass and viability. Were microbial abundance or composition controlled or measured?

Depth Resolution:

The authors group certain depths for discussion (e.g., “upper 2 m” vs. “below 2 m”), but patterns are often non-linear across depths. Consider incorporating a more nuanced, depth-wise interpretation where appropriate (especially for Fig. 6 and Table 2).

The high BWSOC% at 60–180 cm is striking—please clarify if this is a consistent finding or potentially due to sampling or incubation artifacts.

Spectroscopic Interpretation:

The authors use SUVA254 and E250/E365 as proxies for aromaticity and molecular weight, respectively. This is acceptable, but readers would benefit from a brief discussion on their limitations and the role of fluorescence indices (e.g., FI, HIX) that were not used.

Data Interpretation:

The discussion of negative correlations between BWSOC and environmental factors like NH₄⁺, NO₃⁻, and EC is somewhat speculative. The proposed mechanism (e.g., nutrient suppression of microbial degradation) should be more cautiously framed unless further supported.

Clarify whether BWSOC and degradation constants (k) are significantly correlated with SUVA254/E250:E365 using regression statistics.

Conclusions:

The final statements about climate-driven SOC loss extrapolate from WSOC data. It would be more appropriate to caution that WSOC is a proxy for labile SOC, but not equivalent to total SOC vulnerability under field conditions.

Technical Corrections

Abstract: Define "BWSOC" at first use (L16).

L60–61: "in situ conditions" – Specify if this refers to field conditions vs. extracted WSOC.

L194: "formulas ... in Supporting Information" – Ensure these are provided.

Table 2: Units: "g/kg" should be "g kg⁻¹" for consistency; "%" should be "%.

Fig. 2: Axis labels are garbled (e.g., "8-10cm" vs. "0-10cm"). Correct depth labels and ensure variables are clearly defined in the caption.

Fig. 6: Y-axis label "BWSOC (g/kg)" → "BWSOC (g kg⁻¹)".

L263–264: Incomplete sentence ("resulted in very...").

This manuscript provides a useful exploration of water soluble organic carbon from boreal forest soils; the extreme depths of the cores used for the incubation experiments are quite novel and offer a significant contribution to research on soil biochemistry, hydrology, and DOM dynamics overall. However, there are some potential methodological issues that need clarification to properly contextualize the findings. The difference in time between creating the WSOC mixtures for the incubations (4 hours) and the fluorescence intensity analysis (24 hours) creates a margin of error that requires constraining the interpretation of these results more strongly. Additionally, it is difficult to tell if the nutrient addition concentrations are appropriate for each layer given the data available in the manuscript. I believe this manuscript exhibits excellent scientific significance and good scientific and presentation quality. I recommend publication with minor revisions. 

Line 71: typo? Believe “object” should be “objective”

Line 101: citation for the gravimetric soil moisture method if possible. 

Line 104-106: Was the soil oven dried before combustion? 

Lines 107-110, 139-144: Could you clarify the difference between WSOC and WEOM (incubation time of extractions) for readers? Why were EEMs the only analysis conducted on the WEOM? Are there any data available from the WEOM extractions on C/N or anything else? It’s quite possible the longer incubation time for these extractions would result in a different composition of leachate from the four hour incubated samples, and so the EEMs may not be wholly comparable to parameters collected in the WSOC samples. The justification for this is important for contextualizing results like those of lines 220-222. It is possible the fluorescence intensity of these areas may not translate to the availability of these classes of compounds in the experimental incubation solutions. The degradability of WSOC in layers 60-180 shown in table 2 is well supported by the results shown in figure 3. I suspect this is largely due to the results shown by the EEMs analysis (figure 5), which appear to show larger ratios of fulvic acid to humic acid, but this again needs to be further contextualized given the differences in preparation between the incubations and the samples used for the EEMs. I find these data to correlate well and be quite convincing despite the preparation discrepancy, so my suggestion is to provide justification for the difference and briefly discuss the possibility for error in the conclusions rather than to exclude data generated from the EEMs. 

Line 126, 225, 257, 274, 348 and figure 9: typo in SUVA254. Please check throughout. 

The introduction section does not adequately connect to the methods section. What is the purpose of preparing microbial inocula (lines 159-168)? Was the inocula from a given soil layer simply returned to the same soil layer’s WSOC, or was there a cross-inoculated treatment? Could you please provide a stronger transition between the introduction and the purpose of these inocula (i.e.; the role of microbes in WSOC turnover and section 3.3 of the results). Given the interesting results presented in figure 9 between soil moisture and most of the measured variables, I think a background discussion on factors influencing microbial metabolism is warranted. 

Lines 179-180: This method doesn’t necessarily standardize nutrient availability. The starting concentration of C:N:P in each layer could result in oversaturation in a given incubation; especially given the fairly high nutrient concentrations in the top 10 cm (Figure 1). In fact, at least for C:N ratios, it looks like the top 60 cm are all above redfield ratio. This makes sense given the manuscript’s findings in lines 216-219. Given that the concentrations of nutrient solutions in lines 169 and onwards are in molarity and the concentrations of C and N in the starting soils (Figure 1) are in mg/kg, it’s not easy to confirm if these amendment ratios are appropriate for the ambient C:N:P of each layer’s WSOC incubations. Given that these depths also exhibited relatively lower BWSOC % than other layers (figure 6), it raises the question of possible saturation. However, the optical data provide support for the conclusion that the findings are related to the soil OC and not a methodological issue. Thus, I suggest either demonstrating the amendments were in appropriate concentrations or further constraining the conclusions section to account for a margin of error. 

 Is there data available for the starting C, N, and P concentrations at Day 0, either in molarity or in mg/L? A table of these values might be an appropriate addition. A brief discussion of the data as potential rather than actual rates (lines 326-333) is presented but could be bolstered by a discussion of the above issue. 

In section 3.3., could you please clarify terms like “deeper soils” and “upper layers.” “Deep soils” can refer to layers as shallow as 50 cm depending on the experimental application. Given the impressive core depths used in these incubations, defining terms like “deep” somewhere in the methods section could help clarify these results. Otherwise, perhaps change terms like “upper layers” to specific depth increments like 0-60 cm, where appropriate. 

Line 277: I suggest changing “other environmental factors” to “other physicochemical parameters” or similar for clarity. “Environmental factors” traditionally invokes things like precipitation, land cover, etc., rather than soil nutrient concentrations or EC. Possibly suggest a similar change in lines 344-351.