the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 13 Oct 2026
Snow-rich conditions coincide with higher CO2 saturation, while CH4 is generally oversaturated and N2O near equilibrium in alpine sub-Arctic headwaters
Abstract. Headwater streams and lakes exchange greenhouse gases with the atmosphere, but how their gas saturation varies between years with contrasting snow conditions remains poorly understood in cold regions. Groundwater discharge may contribute to this variability by transporting dissolved greenhouse gases to surface waters. At an alpine sub-Arctic site in Norway, we sampled streams, lakes, groundwater and snow in summer 2020 and 2021. We measured carbon dioxide (CO₂), methane (CH₄) and nitrous oxide (N₂O) in surface waters and groundwater to calculate saturation relative to atmospheric equilibrium. A Bayesian mixing model estimated groundwater contributions from water chemistry, and separate regression models assessed their relationships with gas saturation. Our results show that 2020 was an extremely snow-rich year, with the longest snow-cover duration in the 21-year satellite record, whereas snow-cover duration in 2021 was close to the long-term average. CO₂ saturation was higher in 2020 than in 2021, both overall (medians 306 % and 221 %) and at most sites sampled in both years. Higher aquatic CO₂ saturation coincided with reduced terrestrial carbon uptake reported for 2020 in the companion study by Pirk et al. (2023). Median CH₄ saturation exceeded atmospheric equilibrium in both years (320 % and 198 %). CH₄ saturation differed among surface-water sources in 2021. N₂O medians were near equilibrium (109 % and 110 %), with no differences detected among surface-water sources. CO₂ saturation tended to increase with estimated groundwater contribution after accounting for year and surface-water source. However, after accounting for uncertainty in the groundwater estimates, no statistically significant relationship was detected for any of the three gases. Estimated groundwater contributions tended to be higher in 2021, when CO₂ saturation was lower. The clearest between-year contrast was observed for CO₂, whereas CH₄ and N₂O showed no consistent directional change. Multi-year observations linking snow conditions, hydrological pathways and direct gas fluxes are needed to distinguish transport from biological processing and atmospheric exchange.
- Preprint
(12661 KB) - Metadata XML
- BibTeX
- EndNote
Status: open (until 29 Nov 2026)
- RC1: 'Comment on egusphere-2026-5723', Anonymous Referee #1, 20 Oct 2026 reply
Viewed
| HTML | XML | Total | BibTeX | EndNote | |
|---|---|---|---|---|---|
| 304 | 101 | 37 | 442 | 32 | 37 |
- HTML: 304
- PDF: 101
- XML: 37
- Total: 442
- BibTeX: 32
- EndNote: 37
Viewed (geographical distribution)
| Country | # | Views | % |
|---|
| Total: | 0 |
| HTML: | 0 |
| PDF: | 0 |
| XML: | 0 |
- 1
Manuscript summary
The present manuscript by Popp et al. provides a field study on dissolved carbon dioxide (CO2), methane (CH4) and nitrous oxide (N2O) saturation and several solutes, in surface waters and groundwater in a Norwegian arctic-alpine watershed during two occasions (years) with contrasting snow conditions, which was supported by satellite time series data. A mixing model was applied to estimate groundwater contribution to streams and lakes, and its correlation with the dissolved gas saturation. Results show general supersaturation of CO2 and CH4, and atmospheric equilibrium for N2O. Among all gases, only CO2 differed between years, with elevated levels during the snow-rich year. Groundwater contributions were overall low and did not correlate significantly with gas saturation.
Overall assessment
The manuscript addresses an important knowledge gap in aquatic biogeochemistry: While the importance of inland waters as significant sources of greenhouse gases has become well established, the sources and drivers of these dynamics remain poorly understood, especially in remote high latitude / high elevation systems. The manuscript provides important data and insights to fill this gap. The comparison of years with distinct snow regimes is particularly valuable. While the surface water data on dissolved gas concentrations appears robust to address the research question, the groundwater data is rather poorly resolved in space, which may limit the conclusions drawn, unless a convincing discussion is added on the representativity of the selected groundwater well (see general comment below).
Overall, the manuscript appears relatively well written and most display items appear appropriate and well-designed. However, I noticed some redundancy, gaps in the logical flow, and occasional weak connections between the results and the discussion. These issues could be addressed through restructuring, clarification, and/or the inclusion of additional relevant literature (see detailed comments below).
Below, I list a number of suggestions on how a few major and minor issues could possibly be addressed:
General Comments
(1) Introduction – I experienced key information to be scattered across the introduction and suggest restructuring to keep text concise and avoid redundancy: Firstly, the importance of groundwater is mentioned in L. 27 in context of carbon export, and in L. 33/34 in context of N2O export, but then groundwater carbon export is mentioned again in L. 37. I believe could be resolved by moving the section on groundwater discharge effect on C export to freshwaters (L. 37-40) to the first paragraph. Secondly, the lack of knowledge on freshwater greenhouse gas cycling in cold-region environments is mentioned in multiple paragraphs (L. 35-36, L. 38-40, L. 41-48). I would suggest merging these scattered statements into one paragraph.
(2) I believe that the discussion on the mechanisms underlying the differences in CO2 saturation between the snow-rich and normal year could be improved:
(2.1) The authors argue that “the larger snowpack, lower evapotranspiration, and more extensive flowing stream network may have maintained hydrological connectivity and enhanced the lateral transport of soil-respired CO2 and organic carbon to surface waters. Conversely, the drier stream network and longer snow-free period in 2021 may have reduced terrestrial carbon delivery and allowed greater biological CO2 uptake.” (L. 299-301).
Can you clarify, how this argumentation fits together with the generally low groundwater fraction contributing to surface waters, being somewhat higher in snow-poor year 2021 (Fig. 5), and the low correlation between groundwater fraction and surface water CO2 saturation (Fig. 6)? If elevated soil carbon inputs where important to explain the elevated surface water CO2 in snow rich years, one might expect this mechanism to require higher groundwater fractions and / or correlations between groundwater fraction and surface water CO2 saturation. The discussion might become clearer if it distinguishes surface- and sub-surface runoff, and absolute loads vs. relative contributions / fractions (extending / clarifying the discussion in L. 321-323).
(2.2) The authors highlight the coincidence of elevated surface water CO2 concentrations with lower terrestrial carbon uptake (L. 296-298). I think this should be discussed in more mechanistic detail and set more into context of literature. I believe that the discussion could benefit from elaborating on the concept of supply vs. transport limitation of carbon export to freshwaters. If lateral carbon transport is increased in snow rich 2020, but terrestrial carbon uptake (and hence potential supply) is reduced, would this imply that carbon supply to freshwaters is transport limited? In addition, insights from other studies performed at different spatiotemporal scales could provide further context: In a boreal forest catchment, lateral C export is higher during years with higher precipitation and cloud cover, when terrestrial C uptake was reduced ( https://doi.org/10.1021/ez500169j ), broadly in line with the findings in the present manuscript. Globally, a larger proportion of catchment productivity is routed into inland waters at higher discharge ( https://doi.org/10.1073/pnas.2106322119 ). In contrast, lakes in temperate catchments with higher productivity had higher CO2 emissions ( https://doi.org/10.1038/nclimate1748 ).
(3) Extending the discussion of the assumptions underlying the end-member mixing model may improve the paper:
(3.1) Groundwater and snow were used as end-members in the mixing model (L. 133). This analysis is, however, limited to only one sample per year from a single groundwater well. How representative is the sample for the water that would enter the studied lakes and streams, given possible spatial variation, as shown in e.g. https://doi.org/10.1016/j.jhydrol.2010.03.017 ? Given the large environmental gradients that the sampled surface waters span, should one not expect variability in groundwater composition across study sites? Lots of efforts is put into uncertainty analysis of groundwater contribution estimates, but a major source of uncertainty (spatial variability) is not accounted for.
(3.2) Furthermore, how about rainwater as an additional potential end member of the water entering streams and lakes? Why was it excluded here? How could the simplifications in the end-member mixing model have affected the results?
(4) Water samples analyzed for dissolved gas concentrations were acidified to convert dissolved carbonate species to CO2. However, dissolved CO2 would need to be back-calculated to in-situ pH conditions, accounting for the post-sampling acidification effect, to correctly represent ambient conditions. I cannot find any information on whether or how this was done. Please provide this information or help me finding it. Also, please indicate the volume of HCl added to the samples, and how it was added (in the syringe before shaking; L. 121?).
(5) A recurring feature of the Discussion is the emphasis on study limitations, particularly those related to variables or outcomes that were not measured. While I appreciate the authors’ transparency regarding these limitations, I believe the Discussion could be more concise if the limitations were consolidated in Section 4.3 to avoid repetition. I would also encourage the authors to discuss the strengths and contributions of the study more confidently. As currently written, the repeated emphasis on limitations gives the impression that the findings are largely uncertain or insufficient to support any meaningful conclusions, which may understate the value of the study’s results.
Specific comments
L. 46. I think that the point that remote cold regions are difficult to work in can be made convincingly even without pointing to the difficulties during the COVID-19 pandemic, which were not specific to these regions and could be experienced across the globe.
L. 59. Please clarify “focused on particular gas-delivery pathways”
L. 107. Samples of snowpack and melted glacial ice are mentioned here, but I cannot find any results / data (besides in the dataset). Can this be added (e.g. to supplement) to provide context and assure consistency?
L. 109. Please clarify “Gas measurements from snow and ice did not yield meaningful analyses”. Where there any technical difficulties in measuring the gas content?
L. 113. Please provide details on the sampling points, especially in the lakes. Where in the lakes were samples taken (at the shore, as suggested by Fig. 1?) Near-shore conditions may differ from offshore conditions. How may this have impacted results? At what depth was the sample taken?
L. 114. Please provide further details on the groundwater well. At what depth was the water intake? What was the lithology at the intake and how representative is it for the groundwater entering the studied surface waters?
L. 118. Consider mentioning the anions and cations here, as this becomes relevant in L. 141-142
L. 120. Ar and N2 were measured but not presented in the paper. Why? In fact, Ar could be used to normalize dissolved greenhouse gas concentrations to isolate metabolic and physical processes ( https://doi.org/10.1007/s10533-015-0154-8 ), which may overcome a limitation mentioned in the present manuscript (L. 263-264, L. 339-344).
L. 125. How was barometric pressure measured/calculated for each site? What elevation gradient was covered in the study? Accurate pressure measurements may affect pCO2 assessments in alpine freshwaters (see https://doi.org/10.1016/j.jhydrol.2026.136633 )
L. 163. It would be good to clarify the term “groundwater relationships” used here. What is related to what?
L. 179. I would clarify up front that mixed-effects models were used. This may also help readers better understand the “grouping term” analysis (L. 180).
L. 229-230. Does the statement “the contribution of groundwater to lakes and streams varies depending on the catchment and year” hold if the large mixing-model uncertainties were taken into account? From Figure 6, it seems that these uncertainties are of similar magnitude as the variability between years and across most sites shown in Figure 5. Statistical support for this statement would make this and other related statements in the discussion on groundwater contributions varying in space and time (L. 319-320) more convincing.
L. 249. Clarify “a common response” … to what? Do you mean a common response to different snow conditions among years?
L. 261. “net uptake” would be more accurate, to reflect that metabolism effect on CO2 concentration is the net balance between gross primary production and ecosystem respiration
L. 261-264. In the first sentence, metabolism and weathering are mentioned, but in the second, it is metabolism and gas-exchange rates. This inconsistency is slightly confusing to me. All three processes could be relevant but were not measured. Can you rephrase the statement to reflect this?
L. 265-269. The connection between results and this discussion on glaciers as CO2 and CH4 suppliers appears unclear. How does this discussion relate to the results where the glaciated and non-glaciated valley sites are compared?
L. 270-280. High CH4 concentrations should be a result of the net balance of high production and / or low consumption. Similar to the discussion on CO2 (L. 256-264), I think the discussion would benefit from not only bringing up CH4 sources, but also CH4 sinks (e.g. oxidation).
L. 281-287. Similarly to the previous comment on CH4, only N2O sources are mentioned here, but what are the potential sinks of N2O?
L. 293-295. This statement could be supported by https://doi.org/10.1029/2025GL120340
L. 305-310. Can the assessment of snow effects on CH4 be set into literature context (as done for N2O in L. 312-314)?
L. 326 Please clarify “this difference”
L. 341-342. Can the statement on gas exchange velocity be related more directly to the results? For example, could the snow rich year have led to higher stream discharge, which in turn resulted in higher gas exchange (e.g. https://doi.org/10.1002/lol2.70003 ), which may have moderated between-year differences in gas concentrations?
L. 344-345. CH4 ebullition is mentioned as an unaccounted flux pathway. Indeed, CH4 ebullition may be a significant pathway in certain arctic/alpine streams draining large organic matter stocks (e.g. https://doi.org/10.6073/pasta/d04ae85f579c60a5b751749a46f9b77b ). The discussion may benefit from a very brief clarification on how likely ebullition could be in the study systems, for example by providing context on stream morphometry and organic matter stocks.
L. 354-369. The Conclusion section reads like a repetition of the results section. Can the authors go beyond restating results and synthesize implications of their results?
L. 394-395 The headspace method may give erroneous results if the shift in the carbonate equilibrium during shaking is not accurately accounted for, especially when headspace-to-water ratio is rather large and for samples close to or below atmospheric equilibrium, as might be the case for some samples here ( https://doi.org/10.5194/bg-18-1619-2021 ). Please assess this source of error and account for it, if appropriate.
L. 395-397. Since pH is so important for the carbonate equilibrium calculation, it would be good to provide data on pH in the manuscript (not just in the dataset).
L. 395-397. Given the relatively high Calcium concentrations in the bedrock (L. 82) and surface waters (Fig. E1c), one may wonder how much calcium interferes in the carbonate equilibrium reactions and may affect pCO2 due to the formation of e.g. CaCO30, CaHCO3+ and CaOH+, which seems to be disregarded here (L. 395-397). In fact, at pH <8 as is the case here, the effect is small, and this could be mentioned (see e.g. https://doi.org/10.1007/s002160050832 ).
Figure 3 and 4: What is the reasoning behind highlighting median values in Figure 4, given that they are already shown in Figure 3? This information seems redundant and I believe that Figure 3 would be enough to convey the message. Then, redundancy in L. 222-226 could also be removed.
Figure 6 Why is the relationship between groundwater fraction and gas saturation only shown for CO2, but not for CH4 and N2O? For consistency and transparency, I would suggest adding figures for the other gases, potentially in the appendix.
Figure E1. I was a bit confused to see inconsistent horizontal axis labelling in panel d), relative to a-c. For consistency, can the same categories be used across all panels, and “NA” added above “g-lake” in d)?
Dataset
I reviewed the dataset and it appears to look fine. However, I couldn’t find any clarification of the table headers/symbols/abbreviations. Please help me find it or add it if it is missing.