The manuscript by Mavrovic et al. is a nice investigation on the controls of CO₂ emissions from high latitude soils during the cold season. Although the study is not showing many things that are particularly new, there are a few insights here that I like. And since there’s little data from the cold season in these environments, the data presented in this study is going to quite valuable to a wider audience. Therefore, I think it can be suitable for publication after some adjustments and clarifications.

First of all, one of the main conclusions is that non-growing season fluxes during the zero curtain are controlled by liquid water content, and not by temperature. That’s not particularly surprising since soil temperatures do not vary during the zero curtain period, so other variables should be more important. Likewise, the authors say that liquid water content is less important than soil temperature when liquid water content is low, but that’s pretty much the same thing: it’s a subset of the data where there’s little change in liquid water content. The authors acknowledge these aspects briefly in their results, but it should be discussed more extensively in the discussion. What is the relative importance of liquid water content? Figure 7 suggests that it's responsible for a huge change in the fluxes. 

Otherwise, it’s strange to see so few parameters being part of the random forest analysis. Why weren’t more soil properties, like C:N ratios part of this analysis? Or calculated available pore space? There’s a huge variation in the fluxes, and there are few soil or site-specific differences that are addressed in this manuscript. Other causes for the peaks seen at below-zero temperatures are not discussed, even though it has been discussed in the past that soil-freezeup reduces available pore space, which leads to bursts of greenhouse gases in permafrost environments (see e.g. Mastepanov et al 2013).

Finally, the authors compare their results to those from Natali et al. (2019), and then discuss how their regression is different below and above -5 degrees C. However, both regressions have large uncertainties attached to them, so this difference is most likely non-significant. If you think your result is different, please show that with a statistical test.

Other, minor comments:

The title does not show that these are only soil fluxes. Please add that detail. Also, I would say ‘cold season’ or ‘winter’ rather than ‘non-growing season’ since you clearly measured in the middle of winter.

Page 6, Equation 2: it’s a minor detail but this is only true if there’s no liquid water in the snowpack. Looks like your sites did not experience melt events, so this is probably not an issue. Could be mentioned though.

line 217-218: did you determine average snow density for the snowpack or did you make a profile? I wonder how the density differences between the depth hoar and wind slab affects your calculations.

Line 219-221: why only measure T_soil at such a shallow depth? I would expect respiration to be relatively high across the root zone, and temperatures may differ with depth, affecting your correlations.

Line 223: why only 86%?

Line 241: these are only random errors related to your calculations, assuming that the method is perfect. Which systematic errors may have affected your measurements?

Line 248-249: the uncertainty analysis is not explained well. What is the min-max uncertainty propogation method? Please elaborate, and give a reference.

Line 256-258: this is written a bit strangely. Zero curtain happens at all your sites, you simply were not there to measure it.

Line 354: which lack of measurements between -0.5 and -6? There a few. Or do you mean the number is too low?

Line 362-363: like I mentioned before, this may be due to changes in available porosity. See also Pirk et al. (2015) for how this works with methane fluxes (but same principal holds for CO₂). Other useful papers are Zona et al. (2016) and Raz-Yaseef et al. (2017), who showed similar bursts with eddy covariance. Otherwise, I wonder whether changes in air pressure may have played a role, which may affect the storage in deep snow packs.

Line 425-427: but Natali et al. also had many more datapoints, so their estimate is better constrained. Anyway, I doubt there is a statistically significant difference between the regressions in your two studies.

References

Mastepanov M, Sigsgaard C, Tagesson T, Strom L, Tamstorf M P, Lund M and Christensen T R 2013 Revisiting factors controlling methane emissions from high-Arctic tundra Biogeosciences 10 5139–58

Pirk N, Santos T, Gustafson C, Johansson A J, Tufvesson F, Parmentier F-J W, Mastepanov M and Christensen T R 2015 Methane emission bursts from permafrost environments during autumn freeze-in: new insights from ground penetrating radar Geophysical Research Letters 42 6732–8

Raz-Yaseef N, Torn M S, Wu Y, Billesbach D P, Liljedahl A K, Kneafsey T J, Romanovsky V E, Cook D R and Wullschleger S D 2017 Large CO2 and CH4 emissions from polygonal tundra during spring thaw in northern Alaska Geophysical Research Letters 44 504–13

Zona D, Gioli B, Commane R, Lindaas J, Wofsy S C, Miller C E, Dinardo S J, Dengel S, Sweeney C, Karion A, Chang R Y W, Henderson J M, Murphy P C, Goodrich J P, Moreaux V, Liljedahl A, Watts J D, Kimball J S, Lipson D A and Oechel W C 2016 Cold season emissions dominate the Arctic tundra methane budget Proceedings of the National Academy of Sciences 113 40–5

This manuscript reports data on non-growing season CO2 fluxes from 4 different sites in the Arctic-boreal region. Three sites are Arctic while one site is Boreal. Measurements of CO2 concentrations down through the snowpack were done over two consecutive years. Snow samples were used to infer the diffusion coefficient of the snow in order to calculate CO2 fluxes based on the concentration gradient using Fick’s law of diffusion.

As the authors point out, there is still today a lack of data and understanding of what governs CO2 flux rates during the non-growing season in the Arctic. Based on the measurements performed the authors show that soil temperature is the dominant predictor of resulting CO2 fluxes at sub-zero temperatures across sites, whereas during zero-curtain conditions liquid water content becomes the primary predictor of CO2 flux. These two variables dominated also over e.g. vegetation type. This is an interesting result warranting publication. However, some issues should be resolved before the manuscript is ready for publication.

As such, the applied field methodology seems sound and well described except for a few critical details that should be explained further, including how many and in which depths snow samples were done for obtaining information about the snowpack conditions. The authors explain how the snow properties change down through the profile but it is unclear if this is reflected in the snow sampling procedure – e.g. how are changes down through the profile in terms of changes in diffusivity incorporated into the flux calculations. More critically, it is clear that liquid water content was only measure at one site, but unclear if the liquid water content was then estimated at all the other sites except for MM, based on soil temperature and soil properties. It seems to me that this is what was done but it is unclear and this disturbs the overall understanding also of the RF modelling, where there may or may not be missing LWC estimates from 3 of the 4 sites. The authors should clarify explicitly which LWC data were available from all sites for the RF model. If data on LWC were indeed not estimated for the 3 other sites, and therefore missing in the RF modelling, the authors should explain how the RF model handles these missing values and how this affects the interpretation of the RF model result for the importance of LWC when all data are included in the analysis. Except for this lack of clarity, the analyses performed also seems sound.

An important finding reported is the shift from temperature-dependent CO2 fluxes at sub-zero temperatures to liquid-water dependent fluxes at zero curtain conditions. The authors should here also reflect on the potential bias that this was only observed at one of the 4 sites and consequently this result may be affected also by site-specific differences. Particularly because this is also the warmer and boreal site, where the other sites are all arctic.

In general, the authors focus a lot on RMSE of the different models, but reflect less on the other estimated parameters. E.g. the temperature dependency parameter (B) in figure 5 and 6 differ strongly but a discussion of the potential impact of these differences is lacking. I also suggest relating RMSE, e.g. also in the abstract to mean/median or e.g. seasonal fluxes in order to be able to judge the error in more relative terms.

In addition, as a suggestion, the authors could consider if a combined model, taking into account both soil T and LWC at the same time could be even better than the presented alternative models only taking one or the other variable into account. After all, both temperature and liquid water are co-limiting the CO2 fluxes but to different extent in the two temperature regimes. If such a combined model could work for both sub-zero and zero curtain conditions it would be a robust model to use for winter conditions in general in the boreal/arctic region.

Some specific comments:

29-30: Exponential relationship with temperature is expected – but they differ in the two situations. Why do you report only RMSE here? Yes, it indicates that it is a better model but why not a line on what was the effect of liquid water availability (i.e. how was the model characterized)?

119 Is a more natural order of the sections here to switch to have data collection before CO2 flux calculations? Consider the same in the result section.

129 NWT not explained

152 In Jones et al 1999, d[CO2]/dz has the unit of ppmv m-1 and you are shifting from ppmv to g C m-3. Also you do not explain that z is in meters and that is how you get to this unit. Please use one line to explain this.

176 D usually should have the unit of m2 time-1 (often seconds but in your case recalculated to daily). You should state the unit, so that the reader can follow how the resulting unit for FCO2 arises.

189 Did you sample from the top of the snow pack first and pushed the sampling rod deeper? Please explain in detail.

218 How many different snow densities were measured in the different profiles? And how exactly did you sample snow for density estimation? Please give more info on that.

243 – snowpit measurements – more precisely snow density measurements, right? Or do you mean all three (density, porosity, tortuosity?) please clarify.

251 Zero-curtain conditions – it’s a little unclear here whether you are defining this term here – which I believe you are. I suggest rephrasing to “Zero-degree Celsius curtain conditions exist when the soil temperature is around freezing point (0°C) for longer periods of time and a mix…” – and maybe even shortly explain in the abstract too as not all readers will be familiar with this term.

258 It is unclear if you mean that you estimated LWC at all the other sites this way. This is critical to clarify.

281 “…based on a multitude of decision trees”.

298 Since a major part of the uncertainty is related to density, then it is even more important to know exactly how it was sampled.

305: in principle your figure legend symbol indications are not entirely correct, but I see the point. Maybe add to figure text that colors indicate site and symbol type indicate year…

320 But these regimes coincide with regime 1 being the northern sites and regime 2 being MM – seems like a major confounding factor of this cross site analysis, as site-specific conditions may

328 SWE only explained first time a few lines later…

Also – how can you include LWC in a full model across all sites when it was only measured at the MM site? Connected to my question above if you estimated LWC at the other sites with the method described above.

410 Figure 8 – shrubs, not schrubs.

421 confirms not corroborates

445 soil pores not soil porosities

463 availability and quality of labile C

990 Figure A1 + A3: should be ‘shrubs’ – not ‘schrubs’