Preprint

Dear Authors,

Thank you for your comprehensive revisions to incorporate the comments and suggestions offered by three reviewers.

One of the three reviewers has kindly provided a second referee report, as copied below. I agree with the reviewer on the improved structure and clarity of the manuscript. However, the reviewer also noted that you could further improve the interpretation of some important results while reducing the complexity shown in the long title and the large number of tables and figures. In addition, I would like to draw your attention to editorial details, including
- Some mismatch between the clean and track-changes versions, such as “and XX% of total annual emissions” (L 33, track-changes version)
- Reference format: capitalized titles (e.g., DelSontoro et al.)
- Inconsistent table format (Tables 1-4) and some corrections required for Table 1 (indicate the number of sites under “Spatial coverage”) Table 3 (use the same unit for the three N species), and Table 4 (indicate significance levels and remove “20” if it is a typo).

Your manuscript can be published after a careful revision to address the reviewer comments and editorial errors. I would like to ask you to submit your revised manuscript together your responses as instructed in the author guidelines.

The author's response in case of "minor" or "major" revisions must be submitted as one separate *.pdf file (indicating page and line numbers), structured in a clear and easy-to-follow sequence: (1) comments from referees/public, (2) author's response, and (3) author's changes in manuscript. Regarding author's changes, a marked-up manuscript version (track changes in Word, latexdiff in LaTeX) converted into *.pdf and combined with the author's response should be provided.

Sincerely,

Ji-Hyung Park
Associate Editor, Biogeosciences

General comments The revised version of the manuscript has a much better quality compared to the previous one. The structure and clarity have particularly improved. Authors have clearly put a lot of effort in responding to the comments, and their responses are overall satisfactory. However, I would like to point out few additional comments below that should be resolved before publication:

The title could be drastically reduced. Here is a suggestion: ‘Temporal trends in methane emissions from a small eutrophic reservoir: the key role of spring burst’.

While the number of figures and tables was reduced from the previous version, it is still quite high for a standard article. Thus, some of the tables and figures can easily be moved to the supplementary section (ex: Table 1 and Figure 6). Also, in Figure 8, combining the panels for shallow and deep sites would make the message more obvious and reduce the number of figure panels.

The interpretation of the results is problematic in some cases, either due to sentence formulation or to lack of evidence from the results of the study:
• Line 447-448: the suggestion to assume zero wintertime methane flux from all temperate reservoirs based only on the results from this one studied temperate system is very unreasonable.
• Line 464: ‘in contrast to the earlier assessment of age and latitude as the main drivers’. While productivity was recently identified as a methane driver, it does not mean at all that age and latitude are less important drivers.
• Line 510-511: the sentence is presented as a definite conclusion, however, alloOC and autoOC were not measured in this study, so the interpretation of this result should be presented as a potential explanation rather than a fact. Also it is not clear to which results exactly the authors refer to when saying that FCH4 was more stable (not visible in Fig 2).
• Line 514-517: ‘However…(Eqn 7)’ the phrasing of these two sentences suggest that there is no existing literature on the climatic drivers of methane flux, except the relation with productivity. This makes little sense and I suggest removing the sentences completely.
• Line 517-520: the results from the comparison with the predictive model contrast with the observed ones (higher observed fluxes in 2018 despite the lower mean chla), they do not align like the sentence suggests. Please reformulate to clarify the interpretation here. • Lines 566-568: I don’t understand how the authors come to the conclusion that system productivity is a more important predictor of methane compared to latitude since they studied only one system thus one latitude. Besides, latitude was previously used in the literature as a proxy for temperature for predicting methane. In their study, the authors find sediment temperature to be the best predictor of methane flux, not productivity. Thus, their interpretation of the most important driver is contradictory.

Specific comments
• Line 19: ‘arenot’ add space
• Line 62: remove ‘by phytoplankton’ as this is not the only hypothesized pathway for CH4 production in surface waters.
• Line 64-65: the term ‘surface mixed layer CH4’ is confusing, reformulate the sentence. • Line 74: not sure what you mean by ‘stochastic systems’
• Line 237: ‘They surveys’ should be ‘The surveys’?
• Line 349: ‘FCH4’ the CH4 should be subscript
• Line 413-416 and 426-428: these sentences belong in the discussion section rather than the results.
• Line 443 and line 451: ‘Deemer et al.’ the reference lacks the date
• Line 466: representative of what? Please rephrase this sentence.
• Line 479 and 482: replace ‘*’ by ‘x’
• Line 512-514: these two sentences are very unclear • Line 547: ‘wefocus’ add a space

RC1: 'Comment on bg-2021-36', Anonymous Referee #1, 12 Mar 2021

AC1: 'Reply on RC1', Sarah Waldo, 27 Apr 2021

Thank you for your thoughtful comments that were echoed by the other referees and will improve the revised manuscript. Please see attached document for the response to all RC.

Citation: https://doi.org/10.5194/bg-2021-36-AC1

RC2: 'Comment on bg-2021-36', Anonymous Referee #2, 24 Mar 2021

General Comments

I agree with reviewer #1 on the high potential of this well conducted study on CH4 emissions from a temperate eutrophic reservoir which includes 2 years of continuous monitoring of total CH4 emissions by eddy covariance (EC) and gap-filling with ANN and ebullition with automated bubble traps at shallow and deep sites and six extensive field surveys during which diffusion (floating chambers) and ebullition (manual bubble traps) were measured at more than 10 sites. The interpretation on the spatial and temporal variability of CH4 emissions can be done on the basis of meteorology (Rainfall, temp, atmospheric pressure), energy balance (H, LE), hydrodynamics (Brunt-vaisala Freq, temp profiles), hydrology (water inputs, water levels) and biogeochemistry (O2, Chloa).

Major comments

My first major comment is about the result section which does not depict the whole dataset. Indeed, only CH4 fluxes are described but not correctly (see below).

Information on meteorology and hydrology would be very welcomed. Description of the energy balance, thermal stratification and its spatial variability, vertical biogeochemical stratification (O2, CH4…) and their spatial variability and chlorophyll a data and its spatial variability are required

For CH4 emissions, I would recommend to separately describe ebullition (funnels, bubble traps), diffusion (floating chambers) and total emissions from EC. As a matter of fact, I wonder whether the gap-filling is not already a kind of interpretation as the gap-filling is based on the covariation of the fluxes with other variables when EC data are available. Therefore, it has to be decided by the authors to keep it in the result section or move it to the discussion. Independently of where the gap-filled fluxes are described (results or interpretation), it would be very informative for the reader to have information on the validated fluxes (“real data”) and on the EC fluxes after gap filling for comparison.

The second major comment is related to the absence of information regarding the calculation of total emissions from the reservoir. A critical discussion on the comparison of the different type of measurements is required in order to determine the adequate methodology to combine them for a robust estimation of total emissions. We currently ignore whether the emission factor given in the manuscript is an average of all measurements, whether it is only based on EC… Did the author take into account the bathymetry for the extrapolation of ebullition from the reservoir since ebullition at deep sites is lower than at shallow sites?

Minor comments

-Throughout the manuscript: Does “Static pressure” depict atmospheric pressure or the sum of atmospheric and hydrostatic pressure?

-Did the author explore the role of hydrostatic pressure (water level and their variations) on CH4 emissions?

-Did the authors attempt to decipher diffusive fluxes and ebullition from the EC dataset (at least when they have concomitant surface concentrations and or chamber measurements with EC measurements)?

As the manuscript require substantial rewriting/reorganization in order to properly present the dataset and better focus on key results in the discussion no detail comments are provided.

Citation: https://doi.org/10.5194/bg-2021-36-RC2

AC1: 'Reply on RC1', Sarah Waldo, 27 Apr 2021

Thank you for your thoughtful comments that were echoed by the other referees and will improve the revised manuscript. Please see attached document for the response to all RC.

Citation: https://doi.org/10.5194/bg-2021-36-AC1
AC2: 'Reply on RC2', Sarah Waldo, 27 Apr 2021

Thank you for your comments that will improve the revised manuscript. Attached, please find the response to all RC.

Citation: https://doi.org/10.5194/bg-2021-36-AC2

RC3: 'Comment on bg-2021-36', Anonymous Referee #3, 26 Mar 2021

This paper deals with methane emissions in a small temperate eutrophic lake. Emissions were assessed from a variety of measurement techniques (floating chambers, submerged funnels and eddy covariance) together with some environmental parameters (sediment temperature, atmospheric pressure, heat fluxes, met data…) and a neural network (ANN) approach. The paper discusses the links between CH4 fluxes and the biophysical parameters, as well as it provides an analysis of the temporal and spatial variability of those emissions. The subject is of great interest since methane emissions from reservoirs are still poorly studied and constrained at the global scale. There are very few eddy covariance-based studies with long series (2 years) as presented here. As stated before by reviewers #1 and 2, There is no doubt that the data base gathered here is worth publication in the Biogeosciences journal. Some rearrangements would be welcome before publication.

One of the most striking results presented here is the difference between 2017 and 2018 seasonality and cumulated emissions. Unfortunately, though well argued, there are no direct measurements of nutrients and carbon (TOC, DOC, POC, quality of OM) to support these assumptions. Discussion on the diurnal patterns is also a bit disappointing since the results are not unequivocal.

Authors should focus the paper on the main findings which can be supported by the data provided in the paper, and subsequently, present figures might be a little bit too numerous in that perspective of a more focused paper.

The end of the abstract is mentioning "…there is a trade-off in intensive measurement of one water body versus short-term and/or spatially limited measurements in many water bodies", and also "The insights from multi-year, continuous, spatially extensive studies like this one can be used to inform both the study design and emission upscaling from spatially or temporally limited results". These statements are indeed interesting and I wish the paper would give clearer insights and develop more on this matter in the discussion and conclusion.

Rearrangements suggested by Rev 1 and 2 would improve the paper a lot since results and discussion are all mixed together at the moment. I am particularly sensitive to the place devoted to ANN gap-filling and on the way it impacts final emission numbers.

Page 4, line13: How was used time-lapse camera in this study?

Page 4, line 27: there were no u* filtering at EC-S1? If so, you should argue xwhy

Page 5, line 33: more details are needed on the way Akaike information criterion (AIC) was used to determine fitting rate of change in the chambers.

Page 6, line 10-11: vertical profile were done manually, detail procedure( how long for each level)

Page 6, line 30: give more details about:” a probability design that has been shown to reduce uncertainty relative…”

Page 9, line 26: you should give the information that “both quantitative analyses of the relationship between FCH4 and SedT yielded statistically significant results” before implying a link between those two parameters in lines 22-24

Page 11, line 3: I understand that the sandy substrate mention here was brought for recreation use (beach). Is there any point to measure fluxes at the very specific place?

Page 11, lines 23-24: comment on absolute and relative importance of each factor

Page 11, lines 28, 29 and 30: table 3 instead of table 2

Page 13, line 4-5: any assessment of the mentioned transfer?

Page 13, line 21: any nutrients data to support the suggestion mentioned here?

Page 13, line 26-27: any measurement of residence time and output/input of C to support this?

Page 14, line 2: is this consistent with kinetic found by Grasset et al, 2018?

Page 14, line 28: pattern and patterning instead of patter and pattering

Page 15, line 32: detail input parameter of the model used

Page 15, line 33: Del Sontro et al 2018 ref missing or is this Del Sontro et al 2016?

Citation: https://doi.org/10.5194/bg-2021-36-RC3

AC3: 'Reply on RC3', Sarah Waldo, 27 Apr 2021

Thank you for your comments which will improve the quality of the revised manuscript. Please find attached our response to all RC.

Citation: https://doi.org/10.5194/bg-2021-36-AC3

Interactive discussion

Peer review completion