General and specific comments

The manuscript “Variation in CO2 and CH4 fluxes among landcover types in heterogeneous Arctic tundra in Northeastern Siberia” by Juutinen et al. presents several years of CO2 and CH4 flux data, measured both with manual chambers as well as the eddy covariance technique. The authors combine their flux measurements with detailed investigations of site vegetation characteristics and site meteorological data, measured at an Arctic tundra site in Siberia.

This is an important study because it highlights the difficulties in determining C emissions from these heterogenous ecosystems. The study is set in an understudied region in terms of C exchange, and considering how challenging measurements in these remote regions are, I highly value the multi-year data series that are presented here. Further, there are only a few studies that report C fluxes measured with different techniques simultaneously, as is done here, and studies such as this are very much needed to improve our ability to constrain the high-latitude C budget. I also appreciate the detailed and thorough vegetation analyses performed in this study to accurately determine LAI and linking vegetation characteristics to fluxes.

I have a couple of comments that I encourage the authors to address before publication.

1) I suggest adding a few sentences discussing the possible reasons for the observed differences between manual chamber and eddy covariance estimates observed here

2) Please add a short explanation of high- vs. low affinity methane oxidation as well as of barrens for the general benefit of the reader (lines 78-80). Barren tundra surfaces can be quite different from each other (rocky surface with thin or absent organic layer/polar deserts, or eroding surfaces in more organic-rich areas, peatlands). Would be good to know which type the authors refer to here, and if CH4 uptake occurs from all barren surfaces or some ecosystem types in particular. Similarly with high-affinity methane oxidation: CH4 oxidation in high vs low CH4 environments (low- vs. high affinity methanotrophy) are important concepts for this study looking at contributions from wet vs dry tundra, so they should be adequately addressed in the introduction if mentioned.

3) The measured CH4 uptake rates seem rather high, especially some of the maximum values presented in Fig. 5 for lichen tundra. I consider the observed large contribution as a CH4 sink of this landcover class to the regional CH4 balance an important finding and agree it is important to highlight this in this study as the authors have done. However, I am skeptical of these very large flux rates that seem to be one order of magnitude larger than what has been reported previously (references below). Since this is a potentially important message of the manuscript, I would suggest the authors double check the slopes used for calculating manual chamber fluxes and start point gas concentrations, and afterwards re-evaluate if the reported 10% offset of CH4 emissions by CH4 consumption is accurate.

Looking at Fig. 5, the maximum CH4 uptake goes as low as -0.1 mmol CH4 m-2 h-1. If my conversion is correct, this corresponds to -39 mg m-2 d-1. This would seem like an unreasonable large flux to me, considering diffusion constraints of atmospheric CH4 into soils. I recommend the authors double-check at least these large uptake rates, as they may substantially distort the mean.

- Are these manual chamber measurements (flux calculation based on only a few data points and lower accuracy when measuring with GC) or were these fluxes measured with the LGR?

- what was the initial concentration at the start of the measurement/starting point of the selected slope? Did the authors check these concentrations were close to ambient? Otherwise, a starting concentration above ambient after chamber placements may not yield realistic flux estimates.

- what was the minimum number of points included, e.g. for manual sampling with 4 time points, were always for points used for determining the flux or even less?

- Reported EC values are in the same range. Is the closed-path eddy covariance instrument that was used reliable for low concentration (below ambient) measurements, or do these concentrations have to be taken with a grain of salt? Any issues with instrument noise for the low end of fluxes?

Compared to CH4 uptake reported from northern soils (Arctic + boreal) these values would appear one order of magnitude larger than could be expected. In lines 499-502 the authors compare their fluxes (mean: 0.02 mmol m-2 h-1, max 0.1 mmol m-2 h-1) to CH4 uptake rates determined at similar sites which were about one order of magnitude smaller (0.005-0.01 mmol from bare ground, 0.003-0.004 mmol m-2 h-1, ref D-Imperio et al. 2017), and are in the range of what has been reported from Arctic-boreal synthesis studies on CH4 fluxes from a large number of sites. I suggest comparing with some of these studies, for example the following references:

Kuhn, M. A., Varner, R. K., Bastviken, D., Crill, P., MacIntyre, S., Turetsky, M., ... & Olefeldt, D. (2021). BAWLD-CH 4: A Comprehensive Dataset of Methane Fluxes from Boreal and Arctic Ecosystems. Earth System Science Data Discussions, 1-56.

Bartlett, K. B., & Harriss, R. C. (1993). Review and assessment of methane emissions from wetlands. Chemosphere, 26(1-4), 261-320.

E.g., Bartlett&Harriss report that CH4 uptake from these ecosystems is generally < -2 mg CH m-2 d-1 on average, and the more recent synthesis by Kuhn et al. report uptake in the range of -1.1 - -0.17 mg CH4 m-2 d-1.

Line edits

Introduction

L62: and warming?

L78: add reference. Also, useful to add that dry tundra is often reported as CH4 neutral, not necessarily as a small sink even. A recent reference that the authors may find useful: Kuhn, M. A., Varner, R. K., Bastviken, D., Crill, P., MacIntyre, S., Turetsky, M., ... & Olefeldt, D. (2021). BAWLD-CH 4: A Comprehensive Dataset of Methane Fluxes from Boreal and Arctic Ecosystems. Earth System Science Data Discussions, 1-56.

L78-80: a short explanation of tundra barrens and high-affinity methane oxidizers would be useful in this context (see comment above).

L87-88: Please be more specific – biased towards what? Does this mean in heterogeneous environments estimates are biased towards emissions? Or biased in that sense that an integrated flux does not yield sufficient information on sink/source behaviour of individual landcover types?

Methods

L110: delete “normal”

L113: soil organic matter content? Additionally, please provide some information of organic layer thickness at the site in the methods text, and refer to Table 1. Based on the reported low OM content, lichen patches are located exclusively on mineral soil with very thin or no organic layer? Do the authors have any information on the lichen species that could be added?

L170: please add specifics of vials used for storage as well as type of GC (manufacturers, volume, tested for gas tightness during storage, how long were samples stored before analysis?)

L173: Was the 5-minute enclosure time applied to all surfaces, and was this enclosure time sufficient to accurately determine slope for low emitting (or uptake) sites?

L178: What about non-linearity due to PAR for CO2 measured with transparent chambers?

L174-178: Where there some general rules applied as to how many points were usually discarded at the beginning of each measurement, and how many points were included for flux calculation? How was the quality of fluxes assured (R2, RSME, other)? Please add some specifics.

L262: why were different classes for graminoid tundra applied to CO2 and CH4 and not the same for both gases?

Results

L297-298: Check sentence structure.

L330: This is indeed quite large as a mean flux for atmospheric CH4 consumption. Please see specific comments above.

L367-398: It would be interesting to see the time series of CO2 and Ch4 fluxes measured with the eddy covariance technique, instead of just mean numbers based on wind sector contribution. That way the reader would get a better overview of the timing of high/low fluxes or possible peaks that would help interpret the data and help understand discrepancy between chamber and EC data. This time series could be in shown as supplementary in case the authors are tight for space in the main text.

Discussion:

L422: Do the authors mean 9% ? Early they state 10%.

L430-431: their high OM content is already mentioned in line 426.

L441: soil organic matter?

Figures and tables:

Fig. 2: add information on landcover class (wet fen, dry tundra) in figure panels c), d) and e) instead of just in the figure caption. Add info on missing thaw depths measurements (panel f) for some landcover types (e.g., too rocky under lichen cover) in figure caption.

Fig. 3: please add percent explanatory power to each component axis (xx%). The DCA is very much dominated by the high CH4 fluxes from wetlands. The authors may want to consider adding a second panel to this figure, where they provide DCA only for low-emitting and uptake sites, to identify the influence of environmental settings on low fluxes. Also, is there a reason why soil temperature was not included in the figure?

Fig. 5: Please see my comments above regarding large uptake in lichen tundra. Additionally, consider colouring the fluxes by measurement year.

Fig. 6: Symbols for vehicle track and bar

Summary:

For their study, the authors performed closed chamber measurements of CO₂ (in 2014) and CH₄ (between 2012 and 2019) fluxes in different land cover types (LCTs) in Northeastern Siberia during the growing season along with supporting meteorological measurements. Upscaling of the chamber data and comparison with eddy covariance (EC) measurements revealed the importance to distinguish between different land cover types when estimating tundra C exchange on a larger spatial scale: Mainly driven by differences in vegetation coverage and soil wetness, tundra wetlands contributed disproportionately much to the total CO₂ uptake and CH₄ emission regarding their spatial extent. Drier tundra landcover types instead offset the CH₄ emissions through significant consumption of CH₄.

Major comments:

The questions addressed in the study are well within the scope of BG. The study does not really comprise any new ideas or concepts, however publishing greenhouse gas flux data and additional measurements from the still data-scarce Arctic region is valuable in itself. From my point of view (and as the authors state themselves) the small number of replicates per LCT does not allow for a precise quantitative evaluation of greenhouse gas emission depending on the LCT. I expect that assuming that a single plot per LCT (as for example in 2014 for bog and dwarf-shrub tundra, see Table 2) is representative for the whole LCT, might introduce high uncertainty into the upscaled data product. For example different microtopography types within a bog (small hummocks, hollows,…) might already show very different exchange rates of greenhouse gases. The study clearly focusses on the spatial aspect, however, many more temporal replicates were performed. The design of the measurements therefore does not match the aim of the analyses very well. Regarding this issue it is nearly surprising to me, how well the upscaled chamber measurements match the EC measurements (at least from a qualitative point of view) (Figure 7). The main conclusion that different land cover types should be distinguished for upscaling is not new but the proof of its importance, given in the paper, is still useful also regarding possible future changes in the distribution of different LCTs due to climate change.

A new aspect is added to the study by the multivariate analysis that investigates the relationship between gas fluxes and environmental variables. However, this analysis seems a bit redundant to me in this context because it does not add any information to the results or conclusions presented in the paper. Furthermore, the DCA ordination diagram (Figure 3) is only described in a rather technical manner. In my opinion the multivariate analysis should either be removed from the paper or it should be described, analyzed and interpreted in more detail.

In general more information is included in the manuscript than is needed to answer the research questions (e.g. also the temporal differences between CH₄ fluxes within the growing season). This sometimes makes the manuscript hard to follow. In my opinion it would be better to focus on the data that is relevant for the study aim.

Throughout the manuscript words are sometimes written out although an abbreviation had been introduced earlier. Adding an overview table that contains all the abbreviations would be helpful also because there are quite some abbreviations used in the manuscript.

Minor comments:

l. 78: The word “act” is missing and “-s”

l. 86: I don’t understand the meaning of the word “enhances” in this context

ll. 86, 87: if only the eddy covariance method is meant with “micrometeorological measurements”, I would mention this explicitly.

l. 96: In ll. 87, 88 it is mentioned that flux estimates using the eddy covariance technique might be biased in a highly heterogeneous environment like the study area. Is it then reasonable to compare the chamber measurements to the eddy covariance measurements to assess the spatial representativeness of the chamber method? It is certainly helpful to compare chamber and EC measurements but the way the reasoning is expressed here it seems a bit contradictory. Maybe you could just rephrase your reason for comparing the chamber fluxes with eddy covariance measurements.

l. 106: At several point in the manuscript, when referring to a figure, I would add the relevant part of the figure to the reference. For example in this line I would refer explicitly to Figure 1a instead of just Figure 1.

l. 117: I cannot see this from Figure 1 and would therefore only refer to Table 1.

l. 123: I would also refer to Figure 1 d-h here.

l. 157: “…over 5 °C…” – is that the definition of the growing season?

ll. 176 – 179: Since the analyses are based on little replicates it would be interesting, how many measurements had to be discarded. Maybe this information could be added to Table 2, if the numbers do not already give only the valid flux measurements.

ll. 229 – 238: How exactly was the “light response of Pg and NEE” determined? How exactly did you determine the value of Pg_max and Pg₈₀₀?

l. 238: What do you mean with “collar means”? Are these temporal means over all the measurements performed at one collar?

l. 254: A bracket is missing after “…360°”

l. 275: I would refer only to Figure 2b here.

l. 276: "2011-2019"

l. 282: The reference should be to Figure 2 c-d.

l. 291: a “T” for temperature is missing after “…soil surface…”

l. 297: The sentence structure does not make sense.

ll. 301, 302: Why is the strong correlation of ER with axis 2 not mentioned?

l. 313: What is the meaning of these Eigenvalues?

ll. 313, 314: I would rather add the information that “…axis 1 and 2 explain cumulatively 63% of the variation…” to the main text than keeping it in the figure caption.

l. 335: According to Figure 4 there is no significant linear relationship between CH₄ fluxes and WT...

l. 345: Is the standard error the same as standard deviation? In Figure 6 standard deviation is used and in Table 3, standard error.

l. 364: the “4” in “CH₄” should be made into a subscript

ll. 370, 371: I would say “…comprised…of…” or “…contributed…to…”

l. 377: I would explicitly refer to Figure 7 b-d.

ll. 379, 380: Which wind sector do the percentages refer to?

l. 382: I would refer to Figure 7f.

l. 392: “…exchange of CO₂, photosynthesis, and CH₄ flux,…”

l. 401: “…wind direction sectors (a)),…”. Which years are included for Figure 7 f)? Only 2014 or all years of CH₄ flux measurements?

l. 409: What are the “collar-specific estimates”?

l. 418: Does the “bog” not count as a wetland type?

l. 422: “%” is missing. Is it 9 or 10%? At other points of the manuscript you write that it is 10%.

l. 435: “not” instead of “neither”

l. 473: Better to also refer to Figure 6.

l. 475: I cannot see this from Figure 3.

l. 476: How was the soil organic matter content inferred? The data is not shown anywhere.

l. 497: Why do you expect “an overestimation of the emissions from the wet fens”?

Comments to Figures and Tables:

Figure 1b):

I would be nice to either give a closer view of the map so that it can be seen in which LCTs the chamber measurements were performed or (which would be even nicer) mark the EC footprint (impact area) on the map. Is the “stony” LCT the same that is referred to as “barren” in the text? It would be helpful if the same wording was used for the LCTs throughout the paper.

Figure 2:

Maybe the use of different symbols for the years would be easier to distinguish for color-blinds. In figure 2f the different lines are hard to tell apart, especially where they are overlapping. Which line is for dry fen, which one for meadow?

Figure 5: Differences between the different months are shown in the figure but not discussed in the text and they do not contribute to the study results. The temporal aspect is interesting but maybe beyond the scope of the study. Figure 6 would be sufficient to answer the research question. Furthermore, the data from different months do not really show an annual course of the CH₄ exchange since the data was collected in different years with different meteorological conditions.

Figure 6c): It would be helpful if the markers had different colors for the different LCTs.

Figure 7a): Why is there a vertical line around 50% for the northern wind sector?