Summary:

Kjær et al. presents an incubation study using soils from permafrost peatlands in northern Norway. The authors collected material from active to mineral layer in a permafrost habitat, and a comparison core from thawed thermokarst soil. The authors used aerobic and anaerobic headspaces in the incubations, at different depths from an inland-to-ocean gradient of permafrost peatland habitats. The first 20 days were sampled multiple times a day and give insights to the microbial activity directly after permafrost material thaws. Each depth group was divided in four with two vials being kept at field moisture, and the other two vials having water added for a slurry mixture. The replicates were further divided so that one vial begins in an aerobic headspace and one vial remains anaerobic for the duration of the incubation. The authors provide rates and cumulative values for the O2, CO2, N2, CH4 and N2O and geochemical data for the soil cores. Stable isotope signature analysis and dissolved organic carbon samples were also taken to supplement the gas production dataset. The main findings of the study were that the three sites had similar patterns by depth in the various parameters measured. Notably, the active layer samples were highly productive in DOC production, a pattern not observed in the post-thaw samples. 

I am enthusiastic about the content of the study, and especially of the high resolution gas measurements. The paper is pertinent and could be of interest to the scientific community with its high resolution gas measurements, and strategic selection of interesting study sites. However, multiple major comments should be considered. 

MAJOR COMMENTS:

The authors clearly state their objectives with the paper, though a hypothesis was not provided. This was reflected further in the paper when the results were more reports of the data and did not prove / disprove what the authors had hypothesized how the various depths would respond to the treatment groups. Some measurements (ie. stable isotope signatures) are reported in the results but not further integrated into the rest of the paper. Further analysis could also be done with the cumulative gas production between coring sites. The novelty of this study lies with its high-resolution measurements, especially the gas production from the first ~20 days; the community could benefit from the quantification of this fast carbon pool that is largely not captured with ex-situ incubations to date. 

I am not entirely convinced that the paper in its current form presents a robust statistical analysis to meet the authors objectives. The largest issue being that there were many treatment groups but no technical replicates. A replicate of n=1 is statistically weak, though the high resolution of the measurements provides some compensation for this. Overall, I think that the site / depth replicates could be binned differently to explore stronger hypotheses that are developed in response to the comment above. T-test’s were performed to determine difference between the geochemical parameters of the sites but further analysis could be done on the gas fluxes than determining if the production rate is exponential or not. 

Important parameters such as the general vegetation of field sites, soil type, and soil bulk density were not reported. These parameters are essential for the comparison of these results to similar experiments, and usability for those looking to use the data for reviews or inputs for earth system models. 

The authors reference the cores being collected on an inland-to-sea gradient. This was mentioned in the introduction and site description but not further discussed. The natural gradient a transect introduces a range of variables (ie. climate, vegetation, etc.) that likely influence the data and could give greater relevance to the patterns seen in this study. It would be of value for the authors to shape their discussion of what research questions they were looking to answer with this gradient when they selected their soil coring locations. 

MINOR COMMENTS:

Line 34: Some grammatical errors, some rephrasing for clarity needed. 

Line 43: Here I would suggest expanding on what has been introduced here. Anaerobic respiration in peatlands is just starting to be understood, and this experiment's high resolution measurements afford a unique opportunity to capture processes that happen right as the material starts to thaw from its frozen state. 

Line 45: Although it could be considered “common knowledge”, I think it's worth briefly elaborating on why CO2, CH4 and carbon cycles are important on a global scale in the introduction. 

Line 50: This is the first mention of the sea / inland dynamic. A paragraph on the variables this natural gradient introduces would improve the paper and better emphasize the importance of the data. Clearly stating which sea or body of water is referenced would make for a more easily readable paper. 

Line 51-52: A brief discussion of why active layer / permafrost layer vary in oxygen availability and potential for degradation would improve paper. Suggested readings, citations. 

Clymo, R. S., & Hayward, P. M. (1982). The Ecology of Sphagnum. In A. J. E. Smith (Ed.), Bryophyte Ecology (pp. 229–289). Springer Netherlands. https://doi.org/10.1007/978-94-009-5891-3_8

Hodgkins, S. B., Tfaily, M. M., McCalley, C. K., Logan, T. A., Crill, P. M., Saleska, S. R., Rich, V. I., & Chanton, J. P. (2014). Changes in peat chemistry associated with permafrost thaw increase greenhouse gas production. Proceedings of the National Academy of Sciences, 111(16), 5819–5824. https://doi.org/10.1073/pnas.1314641111 

Schädel, C., Beem-Miller, J., Aziz Rad, M., Crow, S. E., Hicks Pries, C. E., Ernakovich, J., Hoyt, A. M., Plante, A., Stoner, S., Treat, C. C., & Sierra, C. A. (2020). Decomposability of soil organic matter over time: The Soil Incubation Database (SIDb, version 1.0) and guidance for incubation procedures. Earth System Science Data, 1511–1524. https://doi.org/10.5194/essd-12-1511-2020 

Line 56: A definition and introduction of thermokarst earlier in the introduction would improve the flow and  better emphasize the importance of the data

Line 60: Consider rephrasing for clarity

Line 80: While the site history on a geologic scale is informative, a description of the modern vegetation at the time of sampling, soil types at each depth, and a broader site introduction is necessary. 

Line 104: How were the layers decided? Visual inspection of the soil horizons, or was there a metric used to delineate a change in the soil core? Example photos of vegetation or soil of sites would be useful in the supplement, if possible. 

Line 179: A brief description of how the authors went from the GC output to their reported units of umol CO2/CH4 g-1 dw-1 and µg g dw-1 225 d-1 using the cited Molstad et al method would increase the reproducibility of the values used in this study and readability of paper. 

Line 190: For the statistics, it is unclear if the peat characteristics applies to the geochemical analysis or the gas chromatography measurements. If the t-test, etc was performed in a statistics program (ie. R, python, etc) it should be stated and the package credited. 

Line 216: Whether or not the gas production is exponential / linear at different timepoints has some value, but the larger question is if the rate of production is different between the treatment groups (slurried or field moisture, aerobic or anaerobic, the inland-to-sea gradient between field sites, and depth groups). Here the study's largest weakness of having no replicates becomes an issue. Its difficult to make assertions about these treatments inducing higher or lower rates of GHG production with one technical replicate per treatment

Line 254: Were the incubations “constantly agitated”? The methods state that the slurry treatment groups were mixed for an hour to disperse the peat, then the peat settled

Line 257: Samples completely under the water line are mostly in an anaerobic environment. I would suspect that the inhibited rate of O2 diffusing into the water would be the limitation, and not the reduced headspace volume. 

Line 265: Table could be moved to Supplement, and values of interest simply discussed in the results.

Line 275: It is likely not that the thawing permafrost was necessarily “stimulated” but rather that the authors are observing a lag phase common in ex-situ incubation studies with permafrost soils. 

Knoblauch, C., Beer, C., Liebner, S., Grigoriev, M. N., & Pfeiffer, E.-M. (2018). Methane production as key to the greenhouse gas budget of thawing permafrost. Nature Climate Change (4), 309–312. https://doi.org/10.1038/s41558-018-0095-z 

Line 279: Same comment as Line 254

Line 305: Same comment as Line 265

Line 314-317: Needs Figure references and more specific language 

Line 324-328: This paragraph would benefit from references to Figures and/or specific references to the data. 

Line 339: The authors imply that the CO2 production from their study is higher than that of another permafrost site using a similar methodology. While this is useful, I would recommend a reassessment of this interpretation. Incubations are useful in their ability to isolate individual ecosystem-scale controls on GHG production; however, they are limited in direct comparisons of the production values as (the authors state in Line 350) there are many discrepancies between incubation studies. 

Line 373: Bringing in the stable isotope results and expanding on what the significance of the different patterns of depletion / enrichment in each site and by depth here would add value to the discussion 

Line 381: I suggest moving Figure S4 into the main body of the manuscript and discussing this dataset more. I would also suggest expanding on how these were analyzed in the methods.

Line 393: For this study (Panneer Salvem et al 2017) and the others used in this discussion, some explanation is needed as to why the authors chose these particular studies to compare their results so closely to the comparison papers results. 

Line 405: There has been significant focus on exponential / non-exponential production rates, but no reason given as to why this is significant to answering a hypothesis or adds value to the study.

Line 408: It is unclear why this high-altitude / high-latitude comparison is being made  

Line 419-420: Same comment as Line 324-328

Line 443: For the conclusion of this paper, the authors should consider framing the study more robustly into the significance of these high resolution measurements into the current state of knowledge on permafrost C dynamics. 

Line 453: Perhaps an earlier mention of these elements (DOC runoff and down-stream ecosystems) if it is the main recommendation of the study. For example, expanding on the statement in Line 400 would achieve this.