Thank you for taking the time to review our study with very insightful and constructive comments. Here are our answers to the specific comments highlighted by R1:

1. Did you include control incubations without brackish water? If not, I would suggest this for the next incubation study as the comparison would strengthen the interpretation of the brackish water effect and sulfate inhibition hypothesis.

We agree with R1 that controlling for addition of brackish water is difficult and a limitation of our study. However, the solution to understanding brackish water addition is not as trivial as adding control incubations without brackish water. First, many sediments are dry when sampled. When these are put under anaerobic conditions, the results are, expectedly, zero activity of methanogens. One solution to this is to add water to the sediment in order to at least have aqueous water-saturated pore spaces in all incubations. One solution to this is to add distilled water to incubations. Distilled water incubations have indeed been added in the next set of incubations studies from our group. However we must also stress that a comparison between distilled water incubations and brackish water incubations is not a tool that will solve all the shortcomings of our study by revealing the role of brackish water. Incubations are sensitive experiments subject to a unique set of conditions. While brackish water addition is an environmentally relevant process that occurs on the Arctic coast, under no circumstance is addition of distilled water something that would occur in the environment and all conclusions from these should be taken very cautiously. For example, I would not think that we could calculate the effect of brackish water addition by substracting our brackish water incubations results from our “control” incubations. It could get complicated...and potentially completely wrong, very quickly. However, to frame our results as carefully as possible we did respond to this comment by modifying in the current manuscript by comparingincubation studies without addition of brackish water that were performed near Tuktoyaktuk (Lapham et al., 2020) and compared qualitatively to our results . We expanded the discussion to mention that distilled water studies could show marked differences from brackish water incubations. 

2. I am missing a discussion on methane oxidation since in the ocean a large percentage of the produced CH4 is oxidised before reaching the atmosphere. 

We will add a few sentences in the discussion part where we discuss oxidation in permafrost soils. One thing that needs to be made clear however is that methane dynamics in the ocean seafloor are not at all related to the processes producing methane in our coastal sites. Methane produced in the seafloor is produced below the sulfate-methane transition zone, often many meters or even tens of meters below the sediment water interface. This methane diffuses upwards through the sulfate-methane transition zone where it is oxidized by specialized anerobic methane oxidizers that exist in consortia that can take decades to develop. This is not the case in our coastal sites where the dynamic nature of the soils or sediment mean that stratified zones such as those seen in the seafloor are not well defined and stable. We have therefore refrained from directly comparing these in the study. Here are proposed modification to enhance the discussion directly related to methane oxidation in the context of our study:

Line 475. The calculated total active layer methane production rates (T) from TP and RP do not take into account aerobic and anaerobic oxidation of CH4, which will most likely reduce fluxes of CH₄ from these sites. Studies and models of Arctic soils emissions have highlighted that aerobic methanotrophy could consume more than half of the CH₄ produced in soils, greatly limiting surface emissions (Oh et al., 2020; Zheng et al., 2018). Furthermore, AOM has been shown to play an important role in attenuating CH₄ production in soils and sediments (Segarra et al., 2013; Winkel et al., 2019) but AOM did not appear to influence significantly CH₄ production in incubations with thermokarst lake sediments (Lotem et al., 2023) While AOM represents a major sink for CH₄ in marine sediments (Knittel and Boetius, 2009; Reeburgh, 2007) the very different nature of our coastal sites from methane dynamics in the seafloor means that further work will be needed to understand the role of AOM in coastal environments.

3. Consider discussing the seasonality or temporal dynamics of coastal CH₄ production, even if only conceptually. 

Thank you for this suggestion. We will add a discussion on seasonal CH₄ production in the introduction to increase the clarity that our study evaluates CH4 dynamics during open-water season. Here is the suggested modification text:

Line 60. During growing season, where atmospheric temperatures allows for active layer to thaw and vegetation to grow, hydrological conditions in polygons play a pivotal role in shaping the pathways of OM decomposition and consequently influence the resulting CO₂ and CH₄ production. Well drained oxic conditions allow microbes to decompose OM rapidly, leading to the production of CO₂ (Jones et al., 2020). Conversely, water saturation restricts oxygen availability, promoting anaerobic respiration and fermentation, thus inducing both CO₂ and CH₄ production (Lipson et al., 2012; Turetsky et al., 2008). Thus, coastal changes during open-water season can swiftly alter water saturation conditions in polygons, in many cases significantly enhancing fermentation and CH4 production (Elberling et al., 2013; Holm et al., 66 2020; Treat et al., 2015).

4. In my opinion, you are using the term "active layer" also for unfrozen zones beneath water bodies, which are referred to as "taliks" (for example, at the Harbour site). This should be expressed more precisely throughout the manuscript. 

Correct, we will modify for pondlets, troughs and harbour site.

Line 15: I agree in general that the processes of erosion and subsidence on carbon emissions are understudied but I would be careful with the wording here. There are some publications e.g. Tanski et al., 2019 measuring C release caused by erosion. 

We agree that carbon release by erosion has been the subject of many studies. However, we also think that the fate of carbon in system that will be subject to subsidence are understudied.  We will modify the text to make make it clear that erosion and subsidence are two different processes that affect coastal. Here is a suggested edit:

 In Arctic regions where coastal sediments contain permafrost, global climate change drives processes such as erosion and subsidence. The contribution of these processes to carbon emissions, especially from ground subsidence, are still uncertain.

Line 42: For a more concrete statement, could you give examples for rapid environmental changes? 

Here’s the sentence at line 42: “Inputs and outputs of the Arctic carbon biogeochemical cycle are known to be reshaped by rapid environmental changes (Couture et al., 2018).” We would prefer to keep the sentence as is because we think naming all environmental changes would lengthen and divert from the main focus of the paper. We name a few of those rapid environmental changes at line 35 with references to literature.

However, to respond directly to your comment what we mean by rapid environmental changes are permafrost thaw, sea ice decline, sea level rise, coastal erosion, land subsidence, changes in hydrology and river discharge, warming temperatures, higher frequency in storm events and shifts in vegetation and land cover to name a few more examples.

Line 55: I like this figure which represents your study sites. In my mind it would fit better in section 2.1. Consider moving. 

We will move to section 2.1 but keep the reference to this figure in the introduction as we believe it gives a simple visualization of polygonal ground to the reader.

Line 71: A reference from an Arctic study would fit better here. 

We understand the reviewer’s point. However, we prefer to retain the reference to coastal environments from the Brittany coast (France), as it provides valuable background context on carbon biogeochemistry from a well-studied system. Our intention here is to illustrate general biogeochemical processes in coastal environments rather than to focus specifically on Arctic systems. Substituting this reference with one from the Arctic would, in our view, shift the focus away from the broader conceptual framework we aimed to establish in this section.

Line 114 – Figure 2: For a better orientation please add a dot for Tuktoyaktuk or add to the description that the Harbour is located in Tuktoyaktuk. Further I strongly recommend to add detail maps of the individual study sites (eg. high resolution satellite images where the coring locations are marked) to get a better understanding of the landscape and the exact sampling positions. 

Thank you for the suggestion. We’ll add that the Harbour is located in Tuktoyaktuk in the description and we’ll also add high-res satellite images of our study sites in the final manuscript.

Line 118: I like the clear explanation on why you chose the sampling sites. 

Line 125: Please add a range of the core lengths. 

Yes, good point. The final manuscript will be updated to indicate that the cores collected with the UWITEC gravity corer were approximately 25 cm in length.

Line 132: In figure 1 pondlets are labeled as thaw ponds. For consistency I would recommend to use the same terms. You could also label each core and refer to that in the text. 

Yes, we’ll correct it in the figure. Thank you.

Line 141: If I’m not mistaken you are using the terms profile and core equally but they represent different approaches. I guess from a trough you collected a core? Please explain and/or revise the manuscript accordingly. It would be helpful to have profile/ core pictures and some additional information such as a brief description and profile depth /core length for all sites. Especially for the profiles numbered with 10 a detail map would be ideal to get an understanding of the location and the environment. 

The cores refer to the samples taken with the UWITEC gravity corer in the harbour. All soil samples were profiles. For troughs, we obtained a profile from the sides of the trough (water-saturated soil). We will add pictures of collected profiles and cores with their length as well as high-res satellite images. In the methods section, lines 123 to 129, we differentiate between cores and profiles, stating that cores were taken in the Harbour and profiles were collected from TP and RP sites. However, we acknowledge that in the abstract, line 22, we did not differentiate as a matter of being more concise. Here’s the suggested edit for the abstract, line 22:

To better constrain CH₄ production dynamics along the land to ocean continuum, sediment cores were collected from nearshore marine sediments and soil profiles from the active layer of the coastal (intertidal) zone and inland soils.

Line 183-186: Do I understand correctly that the gas concentration measurements were not continuous throughout the entire 339-day period? Was the final measurement on day 339? What do you mean by back calculating? Were the CH₄ production rates calculated solely from the linear accumulation observed during the first 16 weeks? 

We have fixed the wording to remove the word backcalculated as this is not what was meant. What we meant was that the rates were calculated from the linear accumulation observed during the incubations. The final measurement was on day 339. We were not able to measure gas concentrations in the incubations the first few weeks.

Line 217: I am no expert on stable methane isotopy 

That’s ok! We thank you for your constructive comments!

Line 238-244 (Figure 3): I like your figures but to me the graphs in plot c and d are hard to distinguish, especially 10A and 10C. Think of adjusting the colours. All information needed is written in the figure caption but I think the legend could be improved by adding some more information such as location name. You are talking about the active layer at the harbour site. Do you really mean active layer or rather talik? Below waterbodies the unfrozen layer usually is called talik. 

We’ll add specific location name in the legends of the graph. We have fixed the wording throughout the manuscript. When the samples were taken from perennially thawing and freezing sites, these are now referred to as active layer. Sites (such as in the ocean) where samples were taken that do not freeze and thaw perennially, are referred to as talik.

Line 266 (Figure 4): Add to the caption that the error bars are the grey lines. To me the error bars miss the end point marking but if you note in the caption that the grey lines are the error bars, it’s clear. 

Good point, we’ll add that the error bars are the grey lines in the caption, thank you.

Line 303 (Figure 6): I suggest to relocate some of the information given in the caption to the figure itself, such as “acetoclastic” and “hydrogenotrophic methanogenesis” you also could add "permafrost" to panel b. Please label the vertical line. This makes it easier for the reader to understand your figure. 

Thank you for pointing this out. We’ll label the vertical line and add permafrost to panel b. However, we wish to keep the theroretical explanation of acetoclastic vs hydrogenotrophic methanogenesis in the figure caption as it’s not a discussion point or a result.

Line 342: In general, it is true that long-term sulfate input is inhibiting methanogenesis, but there are field studies which show that low sulfate concentrations or recent inundation is either not impacting or even promoting methanogenesis. Please distinguish this statement and incorporate more recent findings. For example, Yang et al., 2023 (https://onlinelibrary.wiley.com/doi/10.1111/gcb.16649); Jenrich et al., 2024 (https://onlinelibrary.wiley.com/doi/abs/10.1002/ppp.2251) and Jenrich et al., 2025 (https://bg.copernicus.org/articles/22/2069/2025/). 

Thank you for this input, we’ll add nuance with more recent findings. Thank you for providing literature on the matter. Here are the suggested edits at line 342:

This hypothesis is also consistent with field observations; organic matter mineralization in brackish wetlands is consistently dominated by bacterial sulfate reduction (Bridgham et al., 2013; Torres-Alvarado et al., 2005) where little to no CH₄ emissions are observed (Pönisch et al., 2022; Petersen et al., 2023; Kroeger et al., 2017). However, it’s important to note that recent field studies show that recent inundation and low sulfate concentrations in coastal permafrost-affected soils does not impact methanogenesis (Jenrich et al., 2025; Jenrich et al., 2024; Yang et al., 2023).

Line 355: You could add Yang et al., 2023 as an example for thermokarst lagoons which are a transition zone from terrestrial to marine environments. 

Thank you, very relevant, we’ll add that reference to thermokarst ponds.

Line 414-417: Very cool finding! I agree with that. In a recent study I also found that CH4 and CO2 production is highest during the first stages of land-sea transition and that CH4 production decreases with increasing marine influence. 

Awesome, we are glad that our findings align!

Line 456: Great to see that in situ flux measurements and incubation results are in line. 

Line 468-474: I like the comparison and reasoning, and I agree that Arctic soils represent an important source of CH₄. However, to strengthen the argument on a global scale, it would be helpful to include a size comparison between Arctic coastal wetlands and tropical coastal wetlands. 

Yes, thank you for the relevant idea. Here are the suggested edits that will be inserted at lines 468-474:

CH₄ emissions and production within areas of coastal influence thus appear of similar magnitude. By comparison, mangrove forests, which are a major global source of CH₄ but a very different environment from coastal Arctic polygon terrain, had average CH₄ fluxes to the atmosphere of 0.3 +/- 0.1 mmol m^-2 d^-1 (Rosentreter et al., 2018). In another study, the average measured CH₄ flux from a Yangtze Estuary (China) tidal salt marsh, with a subtropical monsoon climate, was 2.4 mmol m^-2 d^-1 (Li et al., 2021). These reported values are similar to our study as well as other studies in the region. At a global scale, tropical coastal wetlands are dominated by mangroves, occupying ~147,000 km². By contrast, Arctic wetlands as a whole cover ~3.5 million km² (Wortington et al., 2024). Even if only a small fraction of these Arctic wetlands occurs within coastal zones, their total areal extent remains comparable to the total mangrove area (Wortington et al., 2024). This global scale view adds to the notion that Arctic coasts are an important source of CH₄ that warrant further investigation.

494: I like the upscaling approach to show the impact of sea water inundation on a bigger landscape scale. 

This is also an exercise we enjoyed doing!

We thank R2 to have taken the time to review our study. Here are our answers to the comments pointed out.

1. No control experiment without brackish water addition was set up, making it impossible to clarify the specific impact of brackish water itself on methane production (e.g., whether there is a promoting effect). Additionally, no experimental groups with different sulfate concentration gradients were established, which weakens the persuasiveness of the key conclusions of this study.

We appreciate the reviewer’s comment and agree that control incubations without brackish water addition, as well as experiments with defined sulfate gradients, would have strengthened the study. This has been pointed out by the two reviewer and has been addressed. We agree that these “control” treatments were not included in our experimental design. To partially address this gap, we compared our results with those from a previous incubation study on Tuktoyaktuk soils (Lapham et al., 2020), where no brackish water addition was applied. This provides a useful point of reference, although we acknowledge that it is not a direct control within our dataset. We have revised the manuscript to more clearly acknowledge this limitation and to emphasize that our conclusions regarding the role of brackish water and sulfate should be viewed in this comparative and exploratory context.

Text to add to manuscript at line 325: We note that our experimental design did not include parallel incubations without brackish water or with sulfate concentration gradients; therefore, our interpretation relies in part on comparison with previous incubations of Tuktoyaktuk soils conducted without brackish water addition (Lapham et al., 2020), and should be regarded as exploratory rather than definitive.

This being said, we are unsure of how useful control incubations would be or how we would use them to gain additional information. I would like to refer you to the discussion we wrote to a similar point made by R1. Here are the main points pasted below:

We agree with R1 that controlling for addition of brackish water is difficult and a limitation of our study. However, the solution to understanding brackish water addition is not as trivial as adding control incubations without brackish water. First, many sediments are dry when sampled. When these are put under anaerobic conditions, the results are, expectedly, zero activity of methanogens but this is not relevant because we simply have dry material. One solution to this is to add water to the sediment in order to at least have aqueous water-saturated pore spaces in all incubations. Adding distilled water to incubations does this. Distilled water incubations have indeed been added in the next set of incubations studies from our group. However we must also stress that a comparison between distilled water incubations and brackish water incubations is not a tool that will solve all the shortcomings of our study by revealing the role of brackish water. Incubations are sensitive experiments subject to a unique set of conditions. While brackish water addition is an environmentally relevant process that occurs on the Arctic coast, under no circumstance is addition of distilled water something that would occur in the environment and all conclusions from these should be taken very cautiously. For example, I would not think that we could calculate the effect of brackish water addition by substracting our brackish water incubations results from our “control” incubations. It could get complicated...and potentially completely wrong, very quickly. However, to frame our results as carefully as possible we did respond to this comment my modifying in the current manuscript by comparing incubation studies without addition of brackish water that were performed near Tuktoyaktuk (Lapham et al., 2020) and compared qualitatively to our results . We expanded the discussion to mention that distilled water studies could show marked differences from brackish water incubations.

2. The incubation period lasted as long as 339 days, but the MS did not elaborate on how stable experimental conditions (such as temperature fluctuations and substrate consumption) were maintained during this process, which may affect the reliability of the results.

We thank the reviewer for raising this point. We have revised the Methods section (line 177) to more clearly describe the incubation conditions. The incubations were maintained at a constant temperature of 4 °C throughout the entire 339-day period, with no fluctuations. Substrate concentrations were not actively controlled or monitored, aside from repeated measurements of headspace methane. While we acknowledge that substrate depletion may have occurred over the long incubation period, our primary goal was to assess potential methane production under stable temperature conditions, rather than to simulate closed substrate-balanced systems.

3. No determination was made on sulfate reduction rates or related functional genes (such as the *dsrA* gene of desulfovibrio). The coexistence of sulfate reduction and methane production was only inferred from the "smell of sulfide," resulting in insufficiently direct and adequate evidence.

We thank the reviewer for this important comment. We agree that our study did not directly quantify sulfate reduction rates or functional genes (e.g., dsrA) and that the qualitative note of sulfide odor is not a sufficient line of evidence on its own. As stated in the Methods, monitoring sulfate reduction would have required tracer-based rate measurements (e.g., 35S-sulfate assays) or destructive sulfide extraction methods (AVS/CRS), which were beyond the scope of this study and would have required additional expertise, replicates, and instrumentation. Moreover, given the high concentrations of reactive iron minerals in these soils, dissolved sulfide would likely have been scavenged rapidly, complicating direct detection and quantification.

We also note that microbial community characterization (e.g., detection of sulfate-reducing taxa or the dsrA gene) would not by itself demonstrate active sulfate reduction, as the presence of sulfate reducers does not necessarily imply metabolic activity. For this reason, we believe that such measurements, while valuable, would not have provided conclusive evidence in the context of our experimental design.

In light of this, we have revised the manuscript to clarify that the coexistence of methane production and sulfate reduction was not demonstrated directly in our incubations. We now present the sulfide odor as an anecdotal observation only, without attaching mechanistic interpretation or weight to it. We acknowledge this as a limitation and suggest that future studies combining tracer-based sulfate reduction assays and microbial functional gene analyses would be necessary to rigorously test this question.

4. In Figure 6, the correlation analysis between the stable carbon isotope composition of methane and methane production pathways only cites the research of Hornibrook et al. (1997, 2000), without conducting in-depth cross-validation with other data in this paper (such as TOC content and sulfate concentration).

We appreciate the reviewer’s comment. Our interpretation of δ¹³C-CH₄ patterns in relation to methane production pathways was guided by established fractionation frameworks (Hornibrook et al., 1997, 2000). We agree, however, that this discussion could be strengthened by considering other geochemical data from our study. While TOC content and sulfate concentrations were measured, they do not correlate consistently with the isotope values across all landforms and depths in our dataset, making it difficult to validate. We have revised the discussion to explicitly acknowledge this limitation and to clarify that the isotopic evidence is considered in light of but not directly correlated with the broader geochemical context. We also highlight that more systematic integration of isotope data with TOC, sulfate, and microbial measurements will be an important avenue for future work.

5. Regarding the explanation for the high methane production rate in the coastal zone, it is mentioned that "it may be related to the labile organic matter brought by goose feces" in lines 445-446, but there is a lack of direct experimental evidence (such as analytical data on organic matter in goose feces), making this explanation somewhat tenuous.

We agree with R2 that this is anecdotal evidence. We use this in the manuscript to highlight one observation that stood out at this site. However, it cannot be mechanistically linked with the high methane production rates. The heterogenous environment in coastal NWT makes it difficult to pinpoint the reasons for specific observations and anomalies but it is important for us to be able to report the non-quantitative observations that we noted in the field. We also need to take into account that the goal of the study was not to establish correlations between specific local phenomenon like goose feces and methane production rates but this was nonetheless an observation that stood out that we saw pertinent to report. We have adjusted the text to ensure that the reader does not interpret this as a mechanistic relationship.

6. The study found significant differences in methane production rates among different landforms (such as high-centered and low-centered polygons), but key environmental factors of various landforms (such as organic matter degradation rate, microbial community composition, and pore water chemical gradients) were not systematically measured. That is, it is unclear whether factors such as hydrological differences caused by landforms (e.g., water saturation), organic matter activity (as indicated by δ¹³C-TOC), or microbial community structure dominate the spatial heterogeneity of methane production.

We thank the reviewer for this insightful comment. We agree that our study did not systematically measure the key environmental drivers (e.g., organic matter degradation rates, microbial community composition, δ¹³C-TOC, pore water geochemistry) that could mechanistically explain the spatial heterogeneity in methane production across landforms. Our primary objective was to quantify and compare methane production potential among contrasting polygonal landforms as a first step toward identifying where hotspots of methane cycling occur. We fully recognize that disentangling the relative influence of hydrology, organic matter activity, and microbial community structure requires a more targeted study design. We have revised the discussion to acknowledge these limitations and to emphasize that future work should integrate these biogeochemical and microbial datasets to better constrain the drivers of methane production variability.

7. In the discussion, the explanation of the mechanism by which sulfate does not inhibit methane production (such as non-competitive methanogenesis and syntrophic methanogenesis) was not analyzed in combination with the specific data of this study, making it relatively general.

That's correct, we give general hypothesizes on what could explain the mechanisms observed in our incubation set, which inferred our first and general hypothesis.

8. For the determination of sulfate and chloride ion concentrations (Method 2.2), it is clearly stated that "only one measurement was performed for each sample." Although stability tests showed a variation rate of < 3%, there is a lack of biological replicates (such as different sampling points of the same landform type), making it impossible to rule out the interference of spatial heterogeneity.

We thank the reviewer for pointing this out. Our discussion of sulfate and methane production mechanisms (e.g., non-competitive and syntrophic methanogenesis) was indeed presented in general terms and not explicitly linked to the data from this study. In our dataset, we observed active methane production even in the presence of measurable sulfate concentrations. However, we did not collect the complementary measurements (e.g., specific microbial functional groups, detailed electron acceptor fluxes) that would allow us to directly test the relative contributions of non-competitive methanogenesis versus syntrophic interactions in our sites. We have revised the text to make this distinction clearer: while our results are consistent with mechanisms reported in other Arctic and sub-Arctic systems, our data do not allow us to resolve the exact pathway. We now emphasize this limitation and suggest that targeted microbiological and isotopic analyses would be necessary in future studies to address the underlying mechanisms.

9. In the stable carbon isotope analysis (δ¹³C-CH₄), only one incubation vial was used for each depth. Although 2-3 instrument replicate measurements were conducted, no biological replicates (such as parallel incubation vials for the same treatment) were set up, making it difficult to distinguish between real differences among samples and experimental errors.

We appreciate this important point. It is correct that only one incubation vial per depth was used for δ¹³C-CH₄ analysis, with 2–3 instrument replicates but without biological replicates. At each depth, we conducted four incubation vials in total, prioritizing robust estimates of methane production rates as the central focus of the study. Ideally, additional incubations per depth would have been performed to allow for biological replication in the isotope analyses as well. However, given logistical and sample constraints, this was not feasible. I will also note here that while methane production rates are quite variable between biological replicates, the carbon isotopes in methane rarely show a correlation with rate within biological replicates. This information was not included in this study but our tests have demonstrated this. We have revised the text to explicitly acknowledge that while the isotope results provide valuable insight into methane cycling processes, they should be interpreted with caution in the absence of biological replication.

10. All figures and tables (such as Figure 4, Figure 5, and Table 1) only display means and standard deviations, without statistical tests (such as t-test and ANOVA) to verify the significance of differences between groups (such as different landform types and different sites).

We thank the reviewer for this comment. We agree that statistical tests can be valuable when differences between groups are subtle. In our dataset, however, most of the differences among landform types and sites are large and clearly exceed the range of variability (as shown by the standard deviations). For this reason, we consider the presentation of means with standard deviations sufficient to convey the magnitude of contrasts, without requiring formal hypothesis testing. Our primary goal was to highlight the pronounced differences in methane production potential and geochemical context across coastal and inland sites. We have added clarification in the methods/discussion to explain this rationale.