Revie of “Wintertime Production and Storage of Methane in Thermokarst Ponds of Subarctic Norway”

Here, Pismeniuk et al. quantified methane storage and emissions from several thermokarst peatland ponds during the ice covered period. By using chronosequences of thermokarst pond formation, they explained the observed rates and distinguished them according to vegetation types. The topic fist very well for Biogeosciences. However, at this stage, the manuscript contains several inaccuracies that need to be addressed. Please see my main comments below.

The primary aim of the study is to quantify methane emissions and storage in ponds over time. I acknowledge the logistical challenges of sampling in remote locations, particularly given the number of ponds included. However, for the study it is necessary statistical strength to talk about ecosystem level replicates. For instance, in the case of pond A8, it is unclear why this very particular case was included. Please provide a stronger justification for its inclusion or consider removing it from the study. Regarding thermokarst formation, your results suggest a promising pattern. However, in several cases there are no replicates. For example, A6 represents a recently formed pond, but no comparative sites are provided, while A3 appears to present a similar issue. Therefore, you need to clearly explain the rationale behind your pond selection.

The protocol for estimating CH4 storage in the ponds is confusing, as it relies on arbitrary or insufficiently justified assumptions when summing the different ice and water layers collected from each pond. It is unclear what you mean by the 5% uncertainty in relation to the headspace method and storage in the water column, please provide a clear explanation and justification. Similarly, the arguments for including uncertainties related to peat are not clearly presented and require clarification. Several methodological sections highlight potential problems with your core sampling procedure and the way the overall balance was calculated. Typically, storage estimates begin from the onset of ice cover and are calculated forward through the ice-covered period. In your study, however, you assume the end of the 2023–2024 ice period based on measurements from the beginning of the 2024–2025 ice period. This reversed logic is highly questionable. Please justify why the study design started in the opposite direction (you acknowledge it in the discussion, but still is not enough to consider a good selection, expand it and use literature to discuss about it). And would recommend to sort it properly, in Figure 2 or Table 2 you are sorting in a way that March measurements are later, which is not the case.

Regarding the sampling campaigns of dissolved gas in water and ice cores measurements, I have several questions. Because, measurements were very limited at the beginning of ice cover in October 2024, and those from September 2024 appear very superficial. Please clarify why dissolved gas samples were collected at only 0.1 m depth in September, and were sampling was conducted (in the center?) of the pond, and why not bottom samples were collected? Please explain the rationale for being selective in October 2024, why were some ponds sampled while others were not? The table showing pond properties is questionable not sampling them, as not all sites were included in the final sampling. Finally, how many samples were collected per site, only one ice core per pond? And water samples per point?

Another critical part is the sampling procedure for dissolved gas and DOC measurements which also requires clarification. For example: (i) How much vacuum was created in the 12 mL vials prior to filling? Why was shaking performed for 5 minutes? This seems excessive, and the friction and hand-warm inside the syringe could have increased the temperature, thereby affecting gas solubility and Henry’s law values. (ii) If acid was added directly into disposable syringes, this could have damaged the syringes and caused leaks. Were syringes replaced for each measurement? Did you check for potential sample interferences or leaks? If not, I strongly recommend verifying this in the laboratory. (iii) Please note that Falcon tubes are known to leach DOC. Did you test whether this influenced your results? Filtration through 0.45 µm is unlikely to remove all bacteria, which could result in DOC depletion if samples were stored for too long. How long were DOC samples stored prior to analysis? (iv) I do not consider your reported CO2 values from dissolved gas samples to be valid, since total inorganic carbon was not determined. Without this measurement, the reported CO2 concentrations cannot be considered representative of the actual conditions in the water (you added acid and no alkalinity was measured), or you need to expand the calculation of Appelo and Postma, 1993. (v) the type of GC detector is not clear, and also you must provide the detection limit for the gases. Also, I do not see the point to include CO2 and N2O in the study since the study is focused on CH4 (N2O is mentioned in the methodology but not used in the results or discussion). (vi) the O2 is not clear how did you measure and which device was used for it. (vii) Again the mixing of the ice samples in the jars was for 1 hour to equilibrate headspace, the remaining oxygen in the ice could be used to oxidize the methane stored in the ice. Still I do not understand why you have such long periods of mixing. 

Figure 2 are showing some error bars, what is this and how they were estimated, it is not clear in the text. Please sort it properly, March at the beginning. Figure 3 is a boxplot, so please add the number of data used to construct them, and the meaning of the whiskers, boxes and lines and circles.

The discussion and conclusion sections are highly repetitive. I recommend condensing them and reformulating after the methodology and results have been corrected or modified in response to my previous comments. In addition, Figure 6 is not sufficiently supported by the results and appears to present data in a casual way. Please rework this figure to ensure that it is consistent with, and properly supported by, your findings.

This is an interesting study that highlights the importance of thermokarst peatland ponds as sources of overwinter methane. Measurements and their uncertainties were carefully conducted and explored with respect to a variety of pond metrics and water and ice characteristics.  The results are comprehensively presented with a fulsome discussion that places these results in context of annual methane budgets and with other circumpolar lakes and ponds.

I only have a few small editorial questions/suggestions:

Line 63. Is it possible that some of these shallow ponds are ephemeral and satellite imagery may show ‘dry’ terrain at certain times of year/different years, which might confound aging?  Either way, I suggest a summary of how the age of ponds was determined be included here in the main text as there appears to be several lines of evidence used for the age evaluation. Additional details such as dates of aerial imagery, etc. could perhaps be given in the Supplemental Materials.

Line 76. Again, it wasn’t immediately clear that ice formation timing was monitored using several methods. Please clarify in the main text.

Line 94. Give some detail about non-thermokarst pond formation processes in this region.

Line 299.  w.e. ?

Line 334.  This statement is unclear without skipping ahead.  Perhaps briefly state here how methane storage in ice is related to thermokarst pond formation age.

Line 378.  Recommend this statement be changed to “the relationship between pond age and bottom flux is not statistically significant (p = 0.07).”

Lines 549-552.  Are these moss mats on the margins of the ponds and not below the water?  If so, how would aerated peat layers or endophytic methanotrophs on the margins of the ponds limit pond bottom fluxes of methane as measured in this study?