Review of “Pathways of CH4 formation and emission in the subsaline reed wetland of Lake Neusiedl”

Here, Baur et al. continued the extensive research previously conducted by this scientific group in a reed wetland located at a lake in Austria, the title argue that they were focusing on understanding CH4 formation pathways. Although the title attempts to encompass this complex objective, I believe the methodology employed does not fully address such broad scenarios. Instead, I recommend emphasizing diel variations across different seasons rather than the overall CH4 formation processes in the studied ecosystem. I mention this because you are inferring CH4 pathways without performing an appropriate experimental analysis. Microbial assessments combined with isotopic measurements from emissions alone might not be sufficient to clearly identify these pathways. For robust conclusions, incubation experiments using substrates or more detailed analyses would be necessary. I am currently providing general comments on the manuscript, in the next review round, I will likely offer more detailed feedback. At this stage, however, I think the manuscript needs substantial improvement.

Firstly, the Introduction appears poorly organized. Although I understand you might be addressing topics similar to those from previous manuscripts, here the Introduction is brief and omits important details. Regarding isotope information, please ensure that you clearly describe and contextualize isotopic methods and their relevance in terms of diel variations, and their respective emission. Additionally, having paragraphs consisting of only one sentence is inadequate, please expand or combine such sentences with relevant information to provide greater clarity. Several process definitions are merely mentioned but insufficiently explained. For example, you need to clearly introduce the effects of sulfate and oxygen availability on sediments, as well as their potential impacts on CH4 emissions. Not all variations in CH4 emissions can be explained by oxidation alone; rather, the microbial community may also utilize alternative substrates for respiration. This aspect is currently missing and should be addressed explicitly in the Introduction.

Secondly, I understand that the methodology was adopted from previous studies, however, you need to briefly include specific details about your own methods. For example:

(i) Please include, either as an appendix or supplementary material, information about the observed flux determined using the chambers and the Picarro analyzer, clearly indicating instances when data were too erratic. Additionally, specify the Picarro measurement mode and the frequency of data acquisition. For isotope analyses, clarify how long measurements were stabilized before recording values, as well as the measurement uncertainties (I remember it is necessary like 6 min to confirm the isotopic value).

(ii) Table 1 currently provides limited information; please add the sample sizes corresponding to the reported uncertainties. Also, I am curious about how you obtained ebullition data during periods of very low water levels, particularly in summer when this emission pathway appears most prominent in your results. Furthermore, I am surprised by the high chlorophyll-a values observed in winter, are you certain these measurements represent chlorophyll-a and not turbidity caused by shallow water levels? Lastly, regarding the laboratory-analyzed samples (although not clearly described), could you clarify if the reported standard deviations for sulfate, TOC, and chlorophyll-a resulted from temporal sampling conducted over a 24-hour period?

(iii) Ebullition measurements using bubble traps appear highly biased due to the short deployment duration. Given that ebullition is a very stochastic process, it is possible that significant emissions were missed simply because the traps were placed away from emission hotspots. I understand the difficulty involved, as this is one of the major challenges when studying ebullition. In previous studies, you deployed bubble traps for longer periods, however, the focus on diel variations in this study limited that possibility. Do you think a single measurement day per season provides sufficient data to establish a representative ebullition pattern? Looking into the data I would not discard as the main source of emission. The soil chambers faced several issues related to ebullition (as you commented in the method section), suggesting that significant amounts of CH4 accumulated in the surface sediments, which may have been missed due to the short deployment time of the bubble traps (in this case absence of water, but still emission). Given this limitation, why did you not consider using the ebullition events detected by the Picarro analyzer for fluxes to determine other sources of CH4? With proper data management, you could potentially quantify ebullition as part of the total CH4 flux using these measurements.

Thirdly, the presented results represent measurements performed over just 1 day per season. I understand this limitation, it is because you were also collecting data on additional topics, which have been integrated into other published manuscripts. Although you made a substantial effort to collect this data, some results may still be significantly biased due to the short sampling period, particularly for ebullition as previously mentioned. But also, plant-mediated emissions are not fully isolated, as total emissions originating from sources external to the plants could have contributed. The figures require additional information, as it is currently difficult to interpret the origin of the presented data. For instance, in Figure 2, it's unclear what each data point represent, are these individual measurements or average? If they represent average values, please clearly indicate this and the uncertainties. Additionally, if a polynomial function has been applied, specify its order. However, I question whether using a polynomial fit is appropriate in this context; please clearly justify its application as a fit rather than presenting the raw temporal data directly. Also what is the point to fit to this polynomial? Regarding Figure 3, the source of the data is unclear, and I am particularly interested in understanding why these results differ substantially from those previously published in your earlier manuscript in Baur et al. (2024, DOI: 10.1016/j.scitotenv.2023.169112). There is no clear oxidation pattern in Figure C. So you need to expand the information about it. Does this figure include all isotopic signature data from Figures A and B in the four points? Additionally, could you clarify at what value is used during the Picarro measurements?

The authors assessed four pathways of CH4 fluxes (vegetation-mediated, soil- and water-air diffusion, and ebullition), pathways of methanogenesis (acetoclastic, hydrogenotrophic, and methyltrophic), microbial communities, and sediment physical and chemical properties in a subsaline reed-dominated temperate wetland. CH4 fluxes were measured over 24-hour periods 4 times over one year covering all four seasons (spring, summer, fall, winter). Only vegetation-mediated CH4 flux was measured in all 4 seasons.

The abstract implies that the research results contribute to reducing uncertainty in estimates of CH4 emissions from wetlands and improving wetland greenhouse gas modeling. However, the link between the research results and their significance needs clarification in the main text. Specifically, how can the results improve models, and what important knowledge gaps do they fill? Discussion of the results of sediment physical and chemical property analysis is absent and should be added. The authors should also define the term “subsaline” and clarify the significance of the wetland type studied. This is particularly important for convincing non-specialists of the research impact.

I also have some concerns regarding the research design using punctual 24-hour assessments of fluxes over four seasons, which may not adequately capture within-season temporal variation in fluxes, particularly ebullition. Furthermore, the authors were unable to measure all four fluxes in all four seasons, with the exception of vegetation-mediated CH4 emissions. Further justification of 24-hour monitoring periods and comparison of flux pathways across seasons is needed. Is there potential for bias in the seasonal measurements given the short duration of monitoring periods? How does the research address the need to “incorporate all emission pathways across all seasons” (Line 39) and investigate “diel patterns of each available emission pathway during all season” (Lines 53 – 54)? Please address these questions in the main text of the manuscript.

If the authors are willing to address these issues, I’m happy to review a revised version of the manuscript in further detail.