Kleber et al. continue their exciting work on CH₄ release associated with glacier retreat in Svalbard. This paper focuses on the catchment of a small valley glacier in central Svalbard and its groundwater springs (investigated previously) and meltwater stream network. The authors found high CH₄ concentrations in both the springs and the glacial river and estimate a total of 1 t of CH₄ emissions from the catchment, two thirds of which are flushed from the glacier bed by the meltwater.

The paper is well written and brings interesting new data on a highly timely issue of CH₄ release in a rapidly deglaciating Arctic region and a careful mass balance-based estimate of potential CH₄ emissions from the catchment.

My main criticism is the lack of stable isotope data on the CH₄ from the meltwater samples, which makes the interpretation of the CH₄ source(s) and so the governing mechanism(s) (see line 59) of the emissions difficult. The claim that “small valley glaciers like Vallåkrabreen can be a substantial source of methane, challenging previous theories that subglacial methane is largely produced microbially in the anoxic environment beneath large ice sheets” (l. 440-441) makes little sense, since if the CH₄ is thermogenic (which seems likely given its high concentration and the expected low bioavailable OC content in the subglacial environment) the glacier itself (or rather its ecosystem) is not the source but rather its meltwater acts as a mobiliser/carrier, and the comparison of Vallåkrabreen and Leverett Glacier and their catchment sizes (l. 291-294) is beside the point. This is not to question the importance of the results – I think it’s great to see that a broader approach to glacier retreat as a landscape-scale process is necessary to fully understand its climate feedback potential – but it should be emphasised or made explicit in the text.

The true focus and novelty of the study should also be made clearer in the (last paragraph of the) introduction – at the moment it’s quite drowned.

Minor comments

l. 33 Subglacial C stores have also been estimated to be significant (Wadham et al 2019 Nat Comms) and should be mentioned.

l. 41-42 Vinsova et al. (2022 Glob Biogeochem Cycles) provide an overview of Arctic subglacial OC and its potential microbial degradation and could be mentioned.

l. 102 What was “sufficiently high CH₄ concentration” in this case?

Fig 2 Is there any correlation between Q and CH₄?

I also recommend the authors fix the inconsistencies in tense (past vs. present) and voice (passive vs. active) throughout the text for a better reading experience.

Review af Kleber et al. Proglacial methane emissions driven by meltwater and groundwater flushing in a high Arctic glacial catchment

Thanks for an interesting and well written paper with nice figures. I think it is a great study with sound methods, solid results and adequate interpretations. I fully acknowledge the challenge of collecting the type of data you included in the paper and you are well aware of the limitations. Because you do the upscaling for the catchment over the meltseason and claim the Vallåkrabreen is a hotspot, you also need to compare it with other CH4 emitting sites at Svalbard as a minimum and secondly from the broader Arctic. My estimation of the area-normalized flux shows that maybe the valley is not a larger hotspot per area than moist tundra in Svalbard. However, that does not mean that these glacial methane emissions are not important for the CH4 budget of Svalbard. I think these reflections are missing from your manuscript and should be included.

Below are detailed comments

Abstract

Line 11: I would suggest an alternative formulation: “Glacial groundwater is a conduit of geologic methane released in front of retreating glaciers on Svalbard…” so as not to provide the indication that CH4 is produced in the meltwater itself as you conclude yourself later.

Line 13: It is misleading here that you mention “two summers” as the reader gets the impression that you monitored the emission and gauging over two summers when it was actually only one summer you did these measurements. I suggest that you revise the formulation here and also in line 16 to specify that the emission estimate was only for 2021.

Line 17: “catchment”? Do you refer to the 20 km2 or the groundwater catchment which is maybe bigger as this would include the glacial groundwater. If possible I would normalize to the area as well, so that metric is presented up front.

Line 18-19: Notion of proglacial areas as hotspots. This is only valid if you compare it to CH4 emissions from other CH4 sources in Svalbard and/or other Arctic CH4 emitting hotspots, such as thermokarst or Arctic wetlands. Here it would help to have the emission rates normalized per area.

Line 21-22: Technically, the glacial meltwater is not the source of the methane. This must be the geologic methane as you mention in the first line. I would rather write something like: “glacial melt rivers may be growing emission points/areas of subglacial CH4 across other rapidly warming regions of the Arctic.” So as not suggest CH4 is produced in the meltwater, which to date have not been shown.

Introduction

Line 24-25: This is a claim that I guess is the backdrop for many papers on Arctic CH4, but it is overstated and should be avoided in my opinion. According to the latest global assessment of the CH4 budget in Saunois et al. 2020 (https://doi.org/10.5194/essd-12-1561-2020) in Table 6 (page 1597) of global natural CH4 emissions in 2017 above 60°N is 16 (top down) and 31 (bottom up) Tg CH4 y-1. This is 7 and 10% respectively of the global CH4 emission from natural sources (60°N to 90°S) where the southern hemisphere CH4 emission is mainly from terrestrial sources and globally tropical wetlands is by far the most important source of CH4 and will continue to be as emissions are also increasing from these regions under climate warming. I would delete the sentence and focus the introduction with the second sentence in line 25-27 changing it to something like: “In recent decades, seasonal and climatic controls on methane emissions from climate sensitive Arctic systems, such as wetlands, permafrost and geological seeps, have been observed…” In this way it becomes evident that it is really the climate sensitivity that is at the heart of your story here and not the Arctic budget which you cannot say anything about. 

Line 27-31: Here your text seems to directly link the potentially rising CH4 emissions from a warming Arctic to the observed temperature increase in the Arctic. I am not a climate scientist but that much I know, is that the temperature increase in the Arctic is related to the global circulation system and not local emissions of methane. Please rewrite so as not to allude to this wrong claim. Also the paper Rantanen et al. 2022 does not mention CH4 in their paper as a cause for this rapid warming.

Line 41-63: I think this section is nicely written and frames your story well. However, you mention that CH4 have two subglacial sources, either from overridden organic carbon or geological sources. It is not clear from the text whether your study also considers subglacial CH4 derived from organic carbon at the bed in relation to the geological methane, but you only consider geological methane. The partitioning between these two sources in the specific setting of Svalbard is highly interesting, but you do not have the measurements to provide qualified assessments of this partitioning.

Methods

Figure 1 is very nice!

Line 80-82: What was the reason to sample here, where you have a mix of the subglacial and supraglacial waters, effectively diluting the subglacial waters? I could imagine that you over the season will have differing degrees of dilution due to different meltwater volumes from the two rivers. What are your thoughts on how this water source mixing may influence your interpretation of the CH4(aq) concentration results? I assume you did not have means to partition the flows from the two rivers? You already discuss the dilution of subglacial waters in the discussion, but you could get an idea if you compared water volumes with concentrations.

Line 101-104: The described methodology is somewhat unclear. The G2201-i systems I am familiar with runs on a flow rate of 40 mL min-1. Your vials contain maximum 20 mL, but you only added 4 mL N2 headspace (according to your Nat Geo 2023 paper) so did you dilute your samples or run the sample through the inlet for a short period? 4 mL would is equivalent to 6 seconds of flow at 40 mL min-1 which is by far too little to saturate the tubes and cavity and hence the reading will not be trustworthy, so you must have done something else, but you do not tell what. It would be good to provide more details as they are not provided in your Nat Geo 2023 paper either, as others working with small sample volumes would benefit from knowing what you did. As it is written now it is impossible to replicate your method due missing information.

Line 105-108: I think it is not adequate to refer the reader to another publication for your methodology. Most of your readers are not familiar at all with the “float” method for groundwater discharge and you do not even refer the reader to the right chapter in this long report of 106 pages. You may even have had to adopt the method for your specific location and this is needed to be described. I am not suggesting an exhaustive paragraph, but at least few lines of text describing the main principle of the method referring to the right chapter in the report.

Line 112: Which brand was the flourometer? I assume it is very important to calibrate the flourometer prior to these measurements and how was this achieved?

Line 121-123: Did you not measure the isotope composition of this ebullition methane? At least it is not mentioned, but quite useful in comparison to the dissolved CH4 you also run on this machine. The difference could possibly highlight transformation of the CH4, such as oxidation?

Line 129: Flux calculation. Could you not say that Ca could in fact be any point downstream of place of Cin and the flux is therefore instead the total flux between upstream of that measurement point to Cin? This is a more general formulation and you can avoid that rather uncertain assumption that Ca has to attain a value of 4 nM.

Line 147 – 148: I am not convinced that linear interpolation is suitable here. You measure every 2-5 days, but the runoff varies over diurnal cycles. This has also been demonstrated in Lamarche-Gagnon et al. 2019 where the CH4(aq) concentration is linked to meltwater volume, with lower concentrations during high flow (dilution from supraglacial melt) and higher concentrations during low flow (less dilution). So dependent on when you sample your water during the hydrograph you can either end up overestimating or underestimating concentrations in between samplings with interpolation. If there is no relation between discharge and CH4(aq) there is no other way than linear interpolation with all the uncertainties that follow. However, did you investigate whether there was a relation, for example regressing CH4(aq) downstream and Q (Figure 2)? And if so, would it not be more correct to make a discharge-weighted concentration to interpolate between discrete samples? I acknowledge that you have relatively few discrete samples, so there may not be a clear relationship also because your concentrations are relatively stable. In the end the uncertainty is likely the same as you also do a lot of assumptions with the linear interpolation. Anyways, it would good to hear your thoughts on this and your arguments and I would suggest you add your comments on the uncertainty of the chosen approach in the discussion.

Line 164-170: Here you mention the discharge and methane concentration outside the gauging period, but you do not say why the periods start and end at 26^th of May and end 6^th of October, respectively.

Results

Figure 2: I would add “2021” after “Day of year” to make it clear that you only estimated emissions during one year

Line 173 – 178: In figure 2 you use day of year which is good, but make sure also to mention that in the text, so it is easier for the reader to follow.

Line 176-178: I think this text is not needed as it basically is the figure caption to figure 2. So I suggest to delete.

Line 184-194: I think it could be good to calculate the average seasonal area normalized flux from the glacier catchment (20 km2) and according to the info you provided the meltseason length is 133 days with a total potential flux of 616 kg CH4 (meltriver contribution only). This is a potential flux of 0.231 mg CH4 m-2 d-1 (616 * 1000 * 1000 mg CH4/20000000 m2/133 days). It may not say a lot, but it is only for servicing the reader so it can be compared to other CH4 emitting systems in the Arctic.

Line 195-196: I think the description of this transect is too short. The results conflicts with your conceptual flux model (equation 1) as it clearly shows that CH4(aq) at the outflow in to the fjord is not at the atmospheric equilibrium (4nM) but instead elevated by one order of magnitude. This in my opinion deserves a comment.

Figure 5: Why do you have GW1 at the two lowest panels and not on top? It is more logic to have GW1 at the top although this is only because they have the numbers 1 and 2.

Line 234-238: Perhaps mention that these numbers are not included in the upscaled emissions.

Line 246: It is not clear what you mean by “groundwater pools”? How do they look and where are they placed in the landscape? What is their formation? Rather unclear and I suggest to add a larger picture than what is shown Fig. S2, perhaps showing the proglacial landscape with these pools.

Discussion

Line 253-257: I agree with this more conservative approach, but your transect measurements clearly show that you do not reach atmospheric equilibrium concentrations in the river and hence the potential flux is more of a theoretic construct, which according to your measurements would be lower than the 616 kg CH4 if you use the measurements with equation 1.

Line 263-271: If you take your transect data into account you are never in the range of reaching the atmospheric equilibrium concentrations along the river. Hence, the mass balance assumption of 4 nM is not met and the difference between Cin and Ca (which could be Cmin) is smaller than if using 4 nM and hence the emission estimate is proportionally lower. I think this deserves a comment.

Line 273-282: This is good and I agree with that concentrations at the upstream are likely lower than at the portal.

Line 291-294: The comparison to Leverett is ok in the sense that glacier size maybe is not so important, but you do not mention that the sources of CH4 are fundamentally different between the two sites which are the cause for the different flux magnitude. The geological source below Vallåkrabreen leads to the proportionally higher flux per area than Leverett and presumably lower oxidation in meltwater, but here all the methane is sourced from microbial productuib where a substantial CH4 oxidation takes place in the subglacial environment and along the flow path below the ice. Hence, it is possible that the CH4 production rate may be much higher than the net CH4 emissons indicate. Also, you mention in line 264-265 that the CH4 is likely unaltered (e.g. oxidized) in the meltwater and perhaps also in the subglacial environment. Thus, Vallåkrabreen and Leverett are very different glacial CH4 emitting systems. This is an interesting reflection and moderates your argument and I think this deserves a comment here.  

Line 328-333: Technically this text belongs in Methods as you describe an approach to partition the loss to CH4 oxidation. So I suggest to move there.

Line 335-354: I think this is results and should be moved accordingly. I like the way you do it here and it seems reasonable, but it is a bit unclear and therefore it would be good to have this important result in the appropriate place of the manuscript. I was thinking of another approach or maybe it is the same? The total potential loss (degassing + oxidation) from GW1 could be calculated using equation 1 where Cin is CH4(aq) at the source and Ca is CH4(aq) at 25 meters multiplied by the groundwater outflow and assuming no water loss along the transect. Then you calculate F from equation 4 where 𝛿13𝐶-CH4,t is the isotopic value at 25 meter and 𝛿13𝐶-CH4,i at the groundwater spring and multiply this with the total loss. Could this not work as well?

Also, in this text you mention that you cannot calculate the contribution of methanotrophy to the loss (line 349), but then you mention this the 14% contribution in line 350. This is very confusing and it seems contradictory, so please revise the text to make it clearer.

Conclusions

Line 454-455: The statement “Our findings highlight that glacier forefields on Svalbard are hotspots for methane emissions” is much stronger if you compare emissions with other known sources of CH4 from Svalbard or the Arctic. See for example this preprint paper with CH4 emissions estimates from moist tundra in Svalbard: https://essopenarchive.org/users/551125/articles/604242-moist-moss-tundra-on-kapp-linne-svalbard-is-a-net-source-of-co2-and-ch4-to-the-atmosphere (the only I could find upfront and I am sure there are others).

In this paper (line 424-431) the total summer (day 160 – 284) CH4 emission is between 0.039 – 0.164 g CH4 m-2, which equals 0.3 – 1.3 mg CH4 m-2 d-1. The estimate I can calculate from your catchment is 1000 kg CH4/20 km2/133 days = 0.38 mg CH4 m-2 d-1 (this figure may be subject to revision as the flux magnitude and catchment sizes are uncertain)

So compared to these preliminary estimates the Vallåkrabreen is as strong a CH4 source per square meter as moist tundra in Svalbard. I agree that with the number of glaciers in Svalbard potentially emitting CH4 they are important for the total CH4 emission for Svalbard, but without an upscaling including other surface types we are still in the dark as to how important it is. This is not your job to do here, but I think you have to mention the comparison, ideally supplemented with more studies of CH4 emissions from wet ecosystems in Svalbard or maybe across the Arctic.