Review on the manuscript titled ‘Methane in Zackenberg Valley, NE Greenland: Multidecadal growing season fluxes of a high Arctic

tundra’, submitted for publication in Biogeosciences by Johan Scheller and colleagues.

The presented manuscript summarizes chamber-based methane fluxes from the Zackenberg experimental area in Northeastern Greenland. Multiple experiments have been conducted in this area in the period 1997 to present, which are all being considered, while the paper mainly focuses on a data-rich period 2006-2019. Regarding the evaluation of these long time series, the focus has been placed on interannual variability as well as on the extrapolation of fluxes into 2 separate upscaling domains. As a second focus, the paper introduces a new dataset constraining fluxes within a recently formed erosion gully. Based on these new chamber flux data, the authors present a sensitivity study how future erosion events may change net methane emissions within the study area, and how these disturbance effects can be related to expected increases in methane emissions linked to Arctic warming.

The long-term coverage and high temporal frequency of measurements make the Zackenberg experimental area an outstanding resource when it comes to studying carbon cycle processes within the Arctic. This is particularly the case for methane fluxes. Therefore, a study summarizing the wealth of previously reported methane chamber campaigns into a single time series with uniform format is certainly highly valuable. I find the additional focus on the potential effect of gully erosion on landscape scale methane budgets within degrading Arctic landscapes even more interesting. Taken together, the manuscript has a lot to offer, and these topics are certainly of high interest to the readers of this journal. However, I found the weak structuring of this paper to pose quite a hurdle to follow its core message. Also, the authors miss to quantify and discuss several important sources of uncertainty that are essential for supporting their key messages. Main main points of concern are as follows:

1.) if I understood correctly, the upscaled fluxes are based on spatially distributed measurements from the 2007 campaign presented by Tagesson (2013), and interannual variability derived from the automated chamber (AC) program. The latter only covers parts of the land cover types present in the upscaling areas. So you assume that the IAV in these AC systems is representative for changes in the other components that make up the study area. Given the wealth of chamber campaigns that were conducted in the Zackenberg area over the past decades, it must be possible to evaluate this assumption. If not, how do you estimate the uncertainties associated with this approach? 

2.) Related to item 1.), you state in the Discussion that fluxes within constantly wet and dry, resp., areas remain stable over the years, claiming this to be ‘indicated by the data from previous site specific campaigns in the valley (l.599)’ (btw., such campaigns should thus be perfect to deal with the issue raised above). Next, you state that the bulk of the temporal variability in landscape scale methane fluxes can be attributed to areas with variable wetness levels, and that ‘fluxes from different surface classes may respond differently to changes in environmental conditions (l.603f)’. How is this taken into account for the upscaled fluxes presented in this paper? Based on this statement, you either have a static land cover type with highly variable fluxes, or you have land cover types with stable mean flux rates, but variable fractional coverage. In either case, the effect introduces considerable uncertainty into the upscaled product, which must be taken into account and quantified. 

3.) Your dataset for the erosion gully only covers one single year, and here only a period of 10 days within the late growing season. Even if you break up the anticipated erosion process of the valley floor until 2100 into yearly fragments, how do you cover the long-term development of the eroded surfaces in this concept? I.e., fluxes will follow a specific trajectory as the eroded landscapes slowly approaches a new equilibrium over the decades to follow. This must be taken into account, and properly described in the methods. If you do not have the option to quantify changes in flux rates over the years since disturbance, this feature at least needs to be properly discussed.

4.) Regarding the prognostic fluxes, it remains undocumented how they were actually derived, with and without erosion:

    > what model was used to produce prognostic flux rates?

    > how exactly did you estimate the area being affected by erosion in each simulation year, besides considering 25 and 100m erosion corridors? 

    > You mention that gully formation coincided with the location of ice wedges - was this taken into account when defining areas for future erosion?

    > how did you take into consideration that you only had data for that erosion gully within 10 days, and a single observation year? 

I find the consideration of the influence of erosion features for the integrated CH4 budget very interesting, but unfortunately one cannot really evaluate the results based on the currently available information.

5.) The summary of datasets from different campaigns over multiple decades is certainty valuable. However, all this material has been published before, and I think that text on this aspect should therefore be reduced within the results part of this manuscript. Besides presenting a summary with a long time series, the main contribution of this paper should rather be to thoroughly discuss the uncertainties that stem from the use of different methodologies over the years, including data processing. The combination of such a heterogeneous dataset may even be subject to systematic biases, so net uncertainties should be a mandatory part of the aggregated time series. 

6.) Regarding the structure, I found several paragraphs and/or display items within the methods section that rather belong into the results, and also a lot of material in the discussion that should actually be part of the methods. Within individual sections, sub-sections jump back and forth between topics. All of this makes it hard to follow the storyline of this manuscript, and should therefore be carefully adjusted. I added several specific recommendations into the detailed comments further below.

In summary, I think there is a lot of interesting material in this study that makes it worth publishing. At the same time, there are still considerable flaws in the presentation, and many adjustments are required (see major comments above). My recommendation is to reduce the part dealing with the aggregated chamber flux time series (since it’s not based on novel data), and instead put the sensitivity study on gully erosion, and its relative role on upscaled emissions compared to climate change effects, in the foreground. Even though your dataset on the gully fluxes is still limited, an attempt to quantify the impact of such a permafrost degradation would be highly interesting. My overall recommendation is therefore to accept this manuscript for publication, but only after taking care of the major revisions summarized above.

MINOR COMMENTS

INTRODUCTION

- some statements in the first paragraph are currently misleading. At present, the CH4 emissions from the Arctic wetlands do not play a major role for the global CH4 budget. The role of global wetlands is correctly described, but the majority of the emissions can be attributed to tropical regions. The authors should rather focus on the potential emissions from Arctic ecosystems, should permafrost degradation continue, or accelerate, under future climate change

- I think this introduction is missing a paragraph between the current 2nd and 3rd ones that highlights the major scientific uncertainties regarding the Arctic CH4 budget, and underlying processes. I believe your storyline will be more convincing if you first summarize these major problems, and then (in the following paragraph) outline how the presented study addresses (part of) them

- I don’t see the need to separate the last 2 sentences as separate paragraphs. 

MATERIAL AND METHODS

Section 2.1, 

- the section overall is very long. I think this would be better structured if broken up into 2-3 sections

    > description of the actual site (location, land cover, etc.)

    > (recent) climatology: You may consider moving a large fraction of what is currently written about climate/weather to the results section. While I find it appropriate to show mean climate in the methods, here you go into much further detail, showing trends over time, rates of change, etc. If you decide to keep it in here, this may be a part of the site description sub-section, but should follow the landscape description

    > history of observation programs. Very informative, but would be easier to find if listed as a separate section included into sub-section 2.2 (measurements)

- The references to sites shown in Fig.2 are given in a misleading format (e.g. Fig.2a), rather suggesting separate panels. Please use a different format, e.g. (site (a) in Fig.2)

- since one of the study foci is on upscaling, you should add a table in this section that provides the coverage fractions of the main landscape elements within the larger valley floor area, but also within the wetland (moved here from Section 3.2)

- Section 2.2: Merge with later part of Section 2.1, but also with the material in the first few sections of 4.1, to summarize the previous monitoring programs in one place. At the same time, split off the last 3 paragraphs that describe the chamber approach for the gully area into a separate sub-section

- Section 2.2.2: So is what you describe here the map shown as Fig.2 in this work? If so, please reference it properly. If not, please make clear why the remote sensing data needs to be described in detail herein

Section 2.3.4: 

- l.233: Please provide some more details on the ‘linear flux model’

Section 2.3.5: 

- l.247: You claim an increase of CH4 emissions by the end of the century by a factor of 2.43. There is neither a reference nor a method given, so please document where this number came from

RESULTS

Section 3.2

- this information belongs into the methods section. Please move Table 2 into Section 2.1. It’s not necessary to repeat these numbers in the text, so the rest of the section can be deleted.

Section 3.3

- the results presentation is a bit weak here. Just plotting the mean fluxes into a photo isn’t sufficient to understand the data. It would be helpful to learn more about spatial and temporal variability of this dataset. Did you find consistent flux signals over time at individual plots? Was there a meaningful spatial pattern of flux rates within the gully area? 

Section 3.4

- in the way that this is currently presented, I do not see the benefit of showing the temporal variability of upscaled fluxes for these 2 domains. If I got the methodology right, the temporal variation is exactly following those of the AC program, which is shown already in Fig. 3. So why repeat this? Either remove Fig. 3, or find a new format for Figure 5. 

Section 3.5

- Figure 6 needs to be revised. It took me a long time, and a lot of scrolling back and forth, to come up with an explanation what might be shown in there. My current interpretation is that the height of all bars indicates the mean valley floor flux WITHOUT erosion. Considering the colors, the red bars show the total mean flux for the valley WITH erosion, and all other colors indicate how this change between both cases can be attributed to erosion within one of the four land cover types. Not sure if this is correct. In any case, please find a new format that emphasizes your intended message. I think it would be easier if you first indicated in the legend that the colors for those 4 LC types indicate changes, not absolute fluxes. Also, it would help if you added a third column within the prognostic scenarios for ‘no erosion’, and then find a different format to clearly show net fluxes for each erosion scenario.

DISCUSSION

Section 4.1

- Starting l.405, you discuss very broad aspects of spatial and temporal variability in flux rates, and what control factors were identified in previous studies. While this is of course of relevance, obviously these are all previously published results. The main value I see in the current compilation of summertime flux rates across all these studies is that a long time series is being constructed; however, this comes with additional uncertainties: what is the implication in changes in methodology between studies? Chamber sizes, sampling rates, etc., changed considerably over the years. This should primarily be discussed here. 

- Figure 7: I do not see the extra value of the small inset plot in the upper right corner. It is also not documented in the caption. Please remove.

- Figure 7, and the first paragraph of Section 4.1, should be a part of the methods section outlining the previous observation studies summarized in this paper

- l.362-394: This section, including Figure 8, is a result, and nothing is being discussed. So it should be integrated into Section 3. Since basically the same numbers are listed that are given in Figure 8, it’s a rather dull read. I recommend transferring the text into a table.

Section 4.2

- l.432f: The explanation that different temporal variability in fCH4 in different sub-section of the fen can be linked to water level fluctuations is plausible. However, it should be straightforward to analyze this quantitatively, since I’m sure that soil moisture and/or water level conditions were closely monitored at each of these automated chamber sites. So why not exploit this dataset?

- starting with line 491, the authors compare their upscaled mean flux rates to other studies across the Arctic. This is certainly interesting, but I think it would make more sense to split this into a separate sub-section of the discussion, and relabel the preceding sections as ‘methane flux upscaling’, or something along those lines

Section 4.3

- l. 542f: I think this statement should be put into the center of this manuscript!

- l. 546: why do you assume that riverbank erosion will lead to similar effects on fCH4? I would assume that this leads to rather steep cliffs at the river bank, i.e. a very different geomorphology than those shallow gullies depicted in e.g. Figure 4.

- l.558: but there are no uncertainties given for the projected fCH4 values (Figure 6) ..??

- l.562: repeat from statement in l.546, but still no reference …