We thank the reviewer for his constructive and thoughtful comments. We will address the comments (in bolded italics) below.

General Comments

The authors present an interesting and valuable dataset showing temporal and spatial patterns of mire methane flux and its ¹³C signature. They aimed to disentangle the relative importance of methanotrophy vs methanogenesis as well as the availability of substrates for methanogenesis for explaining temporal and spatial variability hypotheses.in their data. Secondary goals were to describe the methane associated prokaryotic community and compare the mire-level ¹³C signature from upscaled measurements (using their chambers and a land cover map for the mire derived from a previous study) to nocturnal boundary layer measurements. While the data itself are useful, and the upscaled ¹³C method successful, there are substantial issues. Primarily that the data presented are insufficient to fully test their hypotheses.

The analysis and interpretation of our δ¹³C data does indeed indicate that this data cannot fully solve the question between the hypotheses. We may have expressed some conclusions too strongly, and not stated the caveats of these results clearly enough. We will reformulate our discussion, as also discussed below in detail, to take the uncertainties and complexities better into account. However, in our opinion the hypotheses, as presented after the Introduction, do offer a useful framework for data analysis and interpretation.

Spatial (HS1 and HS2):

HS1 proposes that variation (in methane flux and ¹³C signature) is due to spatial changes in methane consumption, while HS2 proposes variation is due to spatial shifts from hydrogenotrophic to acetoclastic methane production.

These are not mutually exclusive, which is not inherently an issue, although they are treated as such in the study. Without information on the spatial distribution of methanotrophs or the respective groups of methanogens (or their substrates) or well-constrained values for the expected ¹³C signatures from individual processes, any conclusions on their relative contribution to the data is conjecture.

As the reviewer states, the two hypotheses on spatial variation are not mutually exclusive and they are not intended to be such, as is implied e.g. by the discussion of behavior of the data from chamber 3. However, their purpose is to act as useful simplifications to help analyzing and interpretation of the data. We agree that the presentation of the hypotheses should stress the non-exclusitivity better, and we will modify the revised manuscript to include a case where either of the two processes of HS1 and HS2 dominates. Following this “zero-hypothesis”, no systematic relation between δ¹³C and methane emission rate would be found. We will also re-title the “hypotheses” chapter as “Hypothetical framework”, and in general make the role of the presented hypotheses as simplifications to aid data interpretation clearer.

We do not agree that all conclusions on the contribution of certain processes to the variation in δ¹³C and methane emission rate (F_CH4) are just conjecture, as the data goes some way into refuting some hypotheses. What we state is that the observation of positive correlation between δ¹³C and F_CH4 does show that it is unlikely that methanotrophy would be the dominant cause of the spatial variation in F_CH4.

Temporal (HT1 – HT3)

HT1 states that temporal variation (in methane flux and ¹³C signature) is driven by temperature. HT2 proposes temporal shifts from hydrogenotrophic to acetoclastic methane production. HT3 wisely combines them and proposes there will be a time lag between temperature and production of substrate (presumably of acetate) in the ecosystem that produces a hysteretic out and back arc in the data.

The presence of HT3 resolves the issue of exclusivity there, however the issue of being able to ascribe 13C signature changes to changes in microbial processes without any constraining values or direct measurement of those processes remains. Additionally, although the evidence from their data is evenly split between a temperature-driven response (see point clouds in Figure 9) and a response indicative of hysteresis, they conclude that HT3 is supported.

Also here, as in temporal hypotheses, the different hypotheses are simplifications designed to aid the analysis and interpretation of the data. It is true that we do not have data on temporal development of the microbial communities. As this would have required larger resources this is out of the scope of this study. The central aim of this study is to analyze the spatial and temporal variations of δ¹³C and CH₄ emission rate, to find out which hypotheses they may refute or corroborate.

The chambers from which no hysteretic behavior of δ¹³C-F_CH4 relation is observed are those with low methane emission. Thus, the random uncertainty of the measurements leads to a larger relative noise in the data, which can mask any relatively hysteretic behavior in these chambers. Therefore, we conclude that the hysteretic behavior is evident in the high-flux locations which dominate the mire-scale CH₄ emission, and its δ¹³C value. We will add the above interpretation to the revised manuscript.

We agree that with our data we cannot distinguish e.g. possible shifts between hydrogenotrophic and acetoclastic methanogenesis on one hand and changes in the energetics of hydrogenotrophic methanotrophy on the other hand. Thus, we will modify the revised manuscript to make the terminology clearer.

While the dataset is strong, its strength is mainly in describing spatial and temporal variation in methane flux and signature. If data are available from the site on the ¹³C signature of soil C, this might be enough to draw conclusions on microbial processes based on assumptions regarding fractionation rates. Otherwise, the framing of the study should shift to focus on its strengths; I can imagine an analysis of hotspots and hot moments, and/or the relationship between fluxes, vegetative cover, and water depth.

This description of spatial and temporal variation of δ¹³C and its covariation with CH₄ emission rate are the central themes of this study. The different hypotheses, presented in the beginning, are to be treated as useful simplifications to be used as framework for data interpretation. We will emphasis this on the revised version of the manuscript.

We choose to present the hypotheses right after the introduction as separate chapter, as they influence not only interpretation of the data, but also analysis. The other option would be to present a more vague hypotheses in the end of the introduction, with more detail (incl. Figures) in the Discussion.  

We are not sure what exactly you mean with “hotspots” and “hot moments”. If they are to mean times and locations with considerably higher emission rate that in the near-by spatio-temporal environment, we do not really observe such events or locations (see Figures S1 and S2). What we observe is more like a continuum, with gradual changes overlaid by some variation.

We feel that an analysis of CH₄ emission rates in relation with vegetation cover and water depth would not be very novel as it has been conducted in many previous studies. Also, this data set has rather limited spatial coverage (six chambers) due to the instrumental requirement of isotope Keeling-plot approach that leads to 30 min chamber closure time.

Specific comments:

Additionally, there are a few issues that are reducing the clarity of the authors’ message. One is the use of the phrase “trophic status”, which is used in the manuscript to indicate both seasonal build-up of plant-derived carbon as well as the metabolic pathway of methanogenic archaea. Neither of these is likely the default interpretation that readers will be using when they first encounter the phrase. Distinct phrases should be used (and explained on first use) for these two phenomena and the link between them should be made explicit.

We agree that the terminology here is somewhat confusing. We used the term “trophic status” in the same as in Hornibrook and Bowes, 2007 and Hornibrook 2009 (both cited in the manuscript). We imply that the trophic status ( = quality and quantity of available substrates) has an effect on the metabolic pathway. Furthermore, we discussed in places exclusively on shifts between acetoclastic hydrogenotrophic methanogenesis but did not mention the changes in energetics of the hydrogenotrophic methanogenesis, which can facilitate similar relations. “Substrate availability”, both in quantity and quality (acetate vs CO₂/H₂), may be a better term than “trophic status” or “trophic level” in our analysis. Thus, we will revise the terminology and discussion, for them to be more exact.

Another issue is the description of the Keeling plot method, which currently leaves the reader to put together that the mixing ratio is based on the up-scaled land cover values, unless my interpretation is widely off-base (see L168 & 219). Please clarify this.

The Keeling-plot method itself does not need up-scaled land cover values. In the Keeling plot method, the best fit line between d13C and inverse of the CH4 mixing ratio (Χ) is extrapolated to 1/Χ=0, as explained in the manuscript (lines 190-198). This is done separately for each chamber closure in chamber approach, and for each night in the nocturnal boundary-layer approach.

The land cover values are used in upscaling the chamber δ¹³C values (Eq. 2) to represent the whole mire, and for comparison with NBL-A method.

Finally, the formatting for different taxonomic levels is none-standard and inconsistent throughout the manuscript.

We are not sure what the reviewer means by his comment. Is it that we need to italicize all the taxonomic levels or only the genus level and below?

Technical corrections:

66 Replace “mires’ with “wetlands”, as this statement applies to all wetlands ecosystems, rather than mires specifically

Yes, this is a good suggestion as it makes the sentence more general.

71 This implies the phase-change fractionation leads to biological (or kinetic) fraction, which is not true. It would be more accurate to describe biotic and abiotic fraction processes as just that, two separate chemical phenomena

Maybe this sentence is not exact enough. We did not refer to phase-changes here. We will reformulate the sentence.

74 Introduce the reader to what makes a mire ecosystem distinct from other wetland types here

In short, mires are wetlands with active peat formations. This definition of mires will added to the text.

93 Alternative to what?

Alternative to each other.

175 Is this plot within the chamber itself or around the chamber?

With plot we mean the surface inside the chamber itself.

189 Define RMSE

Yes, this will be defined.

207-214 unit formatting, “spectrometer”

Thank you for noticing this. These will be corrected.

239 Totally fine to use gDNA as shorthand for “genomic DNA”, but it should be defined on first use.

Yes, this will be defined.

268 Spatial and temporal fluxes/signatures as well? This is unclear because of the lack of a separate statistical analysis section

No, this refers to genetic analysis. The fluxes and isotopic signatures are analyzed with MatLab.

Figure 8 takes up a lot of space it is, without providing a lot of information. The 10 day periods could be further collapsed into 4 blocks throughout the growing season, perhaps with a trend line. Or a subset of representative panels could be shown and the remainder moved to a supplement.

You are right that this takes a lot of space. The suggestion to move the full figure to Supplement and to have a subset in main text is good and we will follow this.

374 Is this mire nearby, how different is the climate/vegetation? Some quantitative context for the comparison would be helpful. Also, is an overlap of one methanogenic genus meaningful? It seems likely be mere chance.

The Abisko-Stordalen mire is in Northern Sweden and thus very different in its climate. We have discussed these differences in lines 376-380. We can add coordinates to Abisko-Stordalen to make the geographic difference more obvious. Our statement is a bit misleading, as we observed the same genera of hydrogenotrophic methanogens and the same genus to be dominant. We found this similarity in spite of geographic and climatic difference interesting to warrant mentioning.

The thank for the positive and constructive comments. We address the comments (in bolded italics) in detail below.

General comments

The study by Rinne et al. investigates CH4 emission rates and d13C-CH4 values, and the community structure of methanogenic and methanotrophic communities in a poor fen in southwest Sweden. It is one the most detailed investigation to date pairing high temporal resolution upscaled d13C-CH4 values with integrated d13C values of CH4 flux sampled from nocturnal boundary-layer accumulation. The key findings locally are that: (i) the observed spatial and temporal differences in d13C values of CH4 emissions vary systematically in response to environmental conditions, (ii) the spatial range of values (~15 permil) is larger than temporal variations and appears to be governed by differences in substrate and moisture levels within the peatland that can be identified by vegetation assemblages that can be delineated via remote sensing, and (iii) metagenomic analysis indicates that methanogenic communities within the peatland are diverse and capable of adapting to changes in substrate supply and environmental conditions. I support publication of this work with minor revision.

I recommend that the authors explore further in the Discussion section the implications of their measured d13C values for isotope-weighted global CH4 budgets. The measured d13C values (~ -81 to -79 permil) of CH4 emissions from the site are significantly more negative than d13C values typically attributed to global and northern wetlands (e.g., -58‰; Mikaloff-Fletcher et al., 2004a,b; -58‰, Bousquet et al., 2006; -59‰, Monteil et al., 2011;). Similar to Fisher et al. (2017), this study presents further compelling evidence for a need to adjust d13C values attributed to CH4 emissions from northern peatlands.

We originally did not go into this discussion, as after all our measurements present only one mire ecosystem. Thus, we felt that it may not have wider implications in this context. However, with this encouragement, we will put our mire-scale δ¹³C values into perspective of d13C values observed in other mires in the revised version of the manuscript. The δ¹³C values observed at Mycklemossen mire are are indeed in the lower end of those observed in mire ecosystems also in light of some recent reviews (e.g. Menoud et al., 2022).

Specific comments

Manuscript title: ‘…variation of d13C values of methane…’

This was actually one of the title alternatives we were considering for the initial submission. It is probably slightly more accurate. We will modify the revised version of the manuscript accordingly.

Line 13 – ‘…offer clues…’?

Thank you for spotting this typo. It will be corrected.

Line 76-77 and elsewhere. Replacing terms such as ‘isotopically lighter CH4’ with more specific language would eliminate the need for clarifying statements in parentheses. For example (lines 75-76) could be written as ‘ … hydrogenotrophic methanogenesis typically produced CH4 that is 13C-depleted relative to CH4 generated from acetoclastic methanogenesis.’

We will edit the text as suggested here.

Line 108: ‘reflect differences in CH4 production due to differences in substrate availability for methanogenesis.”

In the original sentence we referred to differences in the trophic status that encompasses both quantity and quality of available substrates. The suggested change makes the sentence simpler, and mostly conveys the same content. We will change the sentence accordingly.

Line 110 and elsewhere: ‘methanotrophy prefers 12C, leaving more 13C to the emitted CH4” =‘Enzymatic reactions associated with methanotroph metabolism consume 12CH4 preferentially, resulting in 13C-enrichment of residual CH4.’

Yes, the suggested sentence is clearer and we will make a change accordingly.

Line 113 – awkward sentence; ‘less 13C depleted CH4’ = ‘13C-enriched CH4’ or ‘CH4 having more positive d13C values’.

Yes, “less ¹³C depleted” is somewhat like a double negation. However, especially “CH₄ having more positive δ¹³C values” can be also confusing as the δ¹³C values are still negative. “higher δ¹³C values” could be simple and straightforward.

Line 121 – In this context ‘substrate supply’ rather than ‘trophic status’ perhaps would more accurately describe the environmental variable impacting CH4 emission rates.

We used trophic status as used in e,g, Hornibrook and Bowes, 2007, and Hornibrook 2009, although the term in the latter is “trophic level”. “Substrate supply” or “substrate availability” can indeed be better in this context.

Furthermore, our sentence, “…the seasonal cycle of the CH4 emission rate is due to the changes in trophic status, i.e. between acetoclastic-dominated (AM) and hydrogenotrophic-dominated (HM) methanogenesis.” implies only changes between acetoclastic and hydrogenotrophic pathways, while also changes in energetics of hydrogenotrophic methanogenesis can work in the same way. Thus, we will change this sentence to reflect this reasoning.

Line 163 – remove capitalization ‘polymethyl…’

We will do this.

Lines 203-205 – How was the CRDS calibrated in the field for concentration and stable isotope measurements?

We took parallel samples from chamber closures and run these with IRMS, as explained in the next paragraph. We also occasionally have run standard gas to check the concentration measurement.

Lines 231-233 – Data from chamber 3 are not mentioned?

As there is very little data from chamber 3, and its contribution would be low due to small fluxes. We did not include it to the upscaling calculation. We will mention this explicitly in the revised version of the manuscript.

Line 276 – ‘…seems to be quite similar…’ If this is an important point, perhaps employ a statistical comparison?

This is actually not an important point for this study, just an interesting observation. Thus, we will remove this from the revised version of the manuscript, as it may confuse a reader.

Line 304 – ‘there were hardly any data’

Thank you for spotting this. We will correct it.

References

Menoud, M., van der Veen, C., Lowry, D., Fernandez, J. M., Bakkaloglu, S., France, J. L., Fisher, R. E., Maazallahi, H., Stanisavljević, M., Nęcki, J., Vinkovic, K., Łakomiec, P., Rinne, J., Korbeń, P., Schmidt, M., Defratyka, S., Yver-Kwok, C., Andersen, T., Chen, H., and Röckmann, T.: Global inventory of the stable isotopic composition of methane surface emissions, augmented by new measurements in Europe, Earth Syst. Sci. Data Discuss. [preprint], https://doi.org/10.5194/essd-2022-30, in review, 2022.

Bousquet, P., Ciais, P., Miller, J.B., Dlugokencky, E.J., Hauglustaine, D.A., Prigent, C., Van der Werf, G.R., Peylin, P., Brunke, E.G., Carouge, C., Langenfelds, R.L., Lathiere, J., Papa, F., Ramonet, M., Schmidt, M., Steele, L.P., Tyler, S.C. and White, J. (2006) Contribution of anthropogenic and natural sources to atmospheric methane variability. Nature 443, 439-443.

Fisher, R. E., France, J. L., Lowry, D., Lanoisellé, M., Brownlow, R., Pyle, J. A., et al. (2017). Measurement of the 13C isotopic signature of methane emissions from northern European wetlands. Global Biogeochemical Cycles, 31, 605–623.

Mikaloff Fletcher, S. E., Tans, P. P., Bruhwiler, L. M., Miller, J. B., and Heimann, M. (2004a). CH4 sources estimated from atmospheric observations of CH4 and its 13C/12C isotopic ratios: 1. Inverse modeling of source processes. Global Biogeochem. Cy. 18:GB4004, doi:10.1029/2004GB002223.

Mikaloff Fletcher, S. E., Tans, P. P., Bruhwiler, L. M., Miller, J. B., and Heimann, M. (2004b). CH4 sources estimated from atmospheric observations of CH4 and its 13C/12C isotopic ratios: 2. Inverse modeling of CH4 fluxes from geographical regions. Global Biogeochem. Cy. 18:GB4005, doi:10.1029/2004GB002224.

Monteil, G., Houweling, S., Dlugockenky, E. J., Maenhout, G., Vaughn, B. H., White, J. W. C., and Rockmann, T. (2011). Interpreting methane variations in the past two decades using measurements of CH4 mixing ratio and isotopic composition, Atmos. Chem. Phys., 11, 9141–9153.