This manuscript addresses an important problem that is often ignored when analysing data collected with the eddy covariance (EC) technique, a key method for measuring fluxes between ecosystems and the atmosphere. This problem relates to the representativeness of measurement data, which can be compromised if the measurement site is heterogeneous with respect to vegetation and other land cover properties affecting the fluxes. Heterogeneous small-scale flux distribution makes it difficult to derive an unbiased budget estimate for the study area because the EC measurement unevenly weights different land cover elements. It is also difficult to differentiate between land cover types as the measurement represents a spatially integrated flux, making interpretation and regional upscaling of the data challenging.

Ludwig et al. tackle these challenges by developing a statistical technique that can, in their words, ’un-mix’ the EC flux measurement. They use this Bayesian method to estimate the contribution of different land cover types to the carbon dioxide and methane fluxes measured at their tundra site in Alaska. As part of the analysis, they compare three different flux footprint models and two data gap-filling approaches. Furthermore, in the context of spatial upscaling of fluxes, they assess the effect of land cover map complexity.

The study is interesting, well focused and suitable for the scope of Biogeosciences. The data appear reliable, and the methods are basically sound. Overall, the analysis is convincing and demonstrate the importance of acknowledging the surface heterogeneity when interpreting EC flux data. However, I find the presentation unsatisfactory in various places and thus recommend major revisions before publication. My concerns are detailed below.

Major comments

(1) The authors say that ”numerous footprint models have been developed” (line 35) and ”recommend always using an ensemble of footprint models” (line 458). Their analysis is based on three models, which produce partly diverging results. I have the following questions about this ensemble approach. First, how many models should be optimally used? What were the criteria for choosing these specific models? Did you consider any alternatives? Second, the authors present the results separately for the three models but do not discuss how the results could be combined. How should three different estimates of carbon balance be interpreted, or would it be possible to combine them into a single value and incorporate the variation into an uncertainty estimate?

(2) While Introduction is rich in citations, the same is not true for the Results & Discussion section. Here, the authors should better acknowledge previously published findings. This is especially apparent in Section 3.7 that deals with application of the results. Overall, this is the weakest section of the manuscript and would benefit from a thorough revision; this should be based on tangible results that are related to existing literature (see specific comments).

(3) There are a few places where the text is not supported by data or references.

- lines 163-165: An assumption (about invariability of methane fluxes) central to the statistical approach is presented in the Methods subsection titled ”Gap-filling methods”. No justification or supporting data analysis is provided for stating the constancy. It would of course be possible to formulate such a hypothesis and try and confirm it later with data (both in an appropriate manuscript section), or simply present it as a model assumption and then discuss how the results depend on that assumption.

- lines 203-205: How do you know such details about methane flux variation?

- lines 217-218: Again, the authors have an idea how methane fluxes behave but do not reveal the source of this information. The Bayesian prior selection should be justified more carefully. Disallowing methane uptake clearly affects the posterior methane flux distribution of the degraded permafrost (Fig. 5).

- lines 244-245: Here, the flux independency of biometeorological drivers is presented as if it were shown above in the manuscript (”Since the CH4 fluxes did not have relationships…”).

- lines 290-292: The authors state that ”[a]ll Bayesian gap-filling models were able to accurately reconstruct the tower NEE across the growing season as a function of PAR, air temperature, and source attributions” but show no data, which is a major shortcoming. Only the model performance with respect to filling artificial data gaps is presented (Fig. 3). Also, the ”Tower Total” in Figs. S4-8 are scaled fluxes, not actual EC data. Please include a comparison (plots, statistics) of measured vs modelled NEE and CH4 fluxes.

(4) Why is the temperature scaling needed in the light response of GPP (Eq. 4)? As far as I can see, none of the papers cited here (line 175) include the temperature (or VPD) attenuation incorporated into Eq. 4. It is also unclear how the temperature scale (Tscale_k) is defined.

(5) What is the rationale behind calculating the carbon budget as CO2-equivalents where methane fluxes are multiplied by 28 (lines 265-266), which refers to the global warming potential due to a pulse emission over a time horizon of 100 years. What does this quantity indicate in this context? Why a 100-year period? Why a pulse emission approach for a natural ecosystem with fluxes sustained for thousands of years? Also, it is somewhat misleading to call the resulting sum “carbon budget” (that would logically be CO2-C + CH4-C).  

Specific comments

lines 4-6: Does ’carbon balance’ refer to the Arctic or to ’some locations’?

line 64: This in inexact. The synthesis excluded EC measurements only if they could not be attributed to a specific land cover type.

line 64: I have not previously seen the term ’unmix’ (or ’un-mix’) being used to mean estimation of land cover specific fluxes. Please define the meaning.

lines 66-67: You should refer to regional budgets rather than individual ecosystems, which do not require a network.

lines 67-69: Rantanen et al. only studied warming, not carbon dynamics or related climate feedbacks.

line 83: I do not find any discussion on ”arctic carbon feedbacks”.

lines 98-100: How were the land cover classes defined? Did you have any vegetation or soil survey data available? Did you validate the land cover maps?

Table 1: It would be useful to show similar percentages for the average footprint-weighted land cover proportions during the study period, estimated with different footprint models.

line 127: What criterion was used for nonstationarity?

line 127: What is ’rssi’?

line 128: u* should be defined. You could include the CO2 flux vs u* analysis in the supplement.

lines 128-129: I’m not sure if I’d call an energy balance closure of 70% ’good’. It is a typical value, probably rather low than high. Data or citation needed if this is included.

Figure 1: Please indicate the location of the EC tower.

Section 2.4: Why is this section written from the gap-filling point of view only? The methods presented here are central to flux ’unmixing’, which is the key topic of the manuscript.

lines 171-172: The solution of model equations is presented in Section 2.4.2 and is irrelevant here.

lines 190-198: This sounds like discussion. Especially the last sentences would improve the actual discussion section.

lines 207-208: It sounds a bit strange to present ordinary least squares as the only alternative to MCMC simulations. There exists a plethora of fitting methods suitable for non-linear relationships.

lines 214-216: I do not understand this explanation for using uninformative priors. Please clarify.

lines 245-246: Unclear what is meant by ”calculating the average CH4 flux for each half hour period”. Aren’t you rather calculating the daily (and monthly) averages?

lines 252: What does the percentage range represent?

lines 253-254: Was there any rationale behind this gap scenario; i.e., does it reflect the gaps found in real measurement data?

line 277: Why do you find the agreement between the footprint models ’surprising’?

line 283: Why ’likely’? You can check these ”distinct periods” from the data.

lines 305-306: But, as you say, MDS is biased in high latitudes.

lines 307-308: In many cases, the RMSE differences between models are larger than the differences between land cover maps, so it is not clear what ’overlapped’ implies. The comparisons should be based on a statistical criterion.

lines 308-309: Comparing the RMSE medians, this is true only for the monthly CH4 data, but for the growing season CH4 total the Kormann-Meixner model performs better than the Kljun model. For NEE, the K-M model has the highest RMSE for two out of five months for both land cover maps, so ”more often than not” does not check out. Considering this and observing the large dispersion, I would not imply that the K-M model showed the worst performance.

lines 318-319. While there clearly is the stated difference for degraded permafrost in June, without supporting statistics it is not possible to generalize the model performance for other landcover types and for other months. I also do not understand why the footprint models are not assessed in relation to the measured 30-min EC fluxes.

lines 326-339: Here, the presentation would benefit from more quantitative comparisons (instead of inexact expressions such as ”aligns with”, ”similar to” and ”similar in range”).

lines 342-343: Posterior distributions (Fig. 5), parameter estimates (Supplement) and actual flux data (Fig. S1b) show that you cannot rule out the possibility of occasional CH4 uptake by tundra. Comments on this would be useful.

lines 358-362: This text deals with NEE (Fig. 4), not carbon. Please rephrase.

line 363: ”less prevalent”, please quantify; ”wetland could not to converge”, unclear meaning.

lines 371-372: carbon or CO2-C?

lines 387-388: How do you know you have a representative sample of these fluxes? The footprint coverage of water areas is low and often zero. How does this relate to the sporadic nature of ebullition and the seasonality of plant-mediated gas transport? And earlier in the same paragraph you concluded that the water fluxes are likely overestimated.

lines 390-391: Fig. 7 shows the CO2-eq. budget, not the carbon budget.

lines 391-393: How do you define ”detectable differences” and ”small differences”?

line 395: Why would increasing the number of model parameters increase uncertainty? I would have assumed that this makes the model more flexible and thus decreases uncertainty.

line 398: Not in September.

lines 413-415: It is misleading to use Mg-C as the unit for the CO2-eq budget. Note that Kuhn et al. (2018) you cite here presented carbon balances (CO2-C + CH4-C), not CO2-eq balances. Using the CO2-eq. concept implies that the ecosystem has a warming effect on climate.

lines 417-420: This text basically repeats what is written in the previous paragraph.

line 434: In the previous paragraph, you said that the edge of the degraded areas was the most uncertain land cover type.

line 440: This obviously depends on the accuracy of the deterministic approach. Do models and data exist for this?

lines 447-455: This paragraph is basically a list of potential improvements to the method presented in the manuscript rather than a discussion of actual applications of the method as it is. Citations are needed to indicate previous occurrence of these ideas.

lines 456-467: This paragraph is more relevant to the applicability of the method than the previous one. However, the discussion is rather superficial and requires more quantitative results. Would it be possible to specify the required ”variability in footprints” (line 462) and what kind of ”differences between observations” are ’enough’ (line 463)? In addition, the conclusion that violation of model assumptions increases uncertainty is rather trivial (line 459); isn’t heterogeneous turbulence a problem that concerns the EC measurements in the first place (if the measurements do not fulfil assumptions, then any related modelling is obviously redundant) (lines 461-462); suggesting that ”consistent wind directions and atmospheric stability” could be a problem requires a real-world example (lines 464-465).  

Table S10: A similar table showing monthly mean (SD) fluxes for all land cover types would be useful.

Technical comments

line 73: Word(s) missing.

line 79: ”compared net ecosystem exchange (NEE) results from CO2 fluxes”; please rephrase.

line 128: Unit missing.

Section 2.3: Incorrect title.

line 169: Remove ”equation 1”.

line 202: Remove ”equation 5”.

line 227: A wrong unit.

Figure 4. Why is the corresponding CH4 plot placed in the supplement? The time unit (month) of the flux is rather uncommon.

lines 430-431: The word ’tundra’ missing.

Whole text: There are inaccuracies in writing, some examples:

- Expressions such as ”chamber fluxes”, ”tower fluxes”, ”tower NEE and CH4” and ”eddy tower” sound colloquial.

- Incorrect prepositions: ”from May-October”, ”Between 15-20%”, etc.

Tables S1-S3: Please explain the distribution notation.

Tables S1-S10: Please unify the number of decimals.

Table S3: A value missing.

This paper explores the spatial heterogeneity in fluxes of CO₂ and CH₄ in a Tundra ecosystem in Alaska. The authors present a novel approach to decompose (“un-mix”) the EC signal from the different land covers. The authors find that using gap-filling methods that take into account the decomposed signal from this approach results in better performances than other gap-filling methods, and that scaling up using this decomposition approach can result in up to 2-fold differences in the total fluxes.              

I think the use of Markov Chain Monte Carlo (MCMC) simulations to predict the fluxes using footprint decomposition is novel and worth of publication. The manuscript is well-written, well organized and the message is clear. However, some methodological questions need to be addressed first:

Perhaps the most important one is the assumption of constant fluxes of methane (L. 198) from different land covers. This is a big assumption since one would expect seasonal changes in methane driven by temperature and variability among land cover contributions driven by fluctuations in water level. For example, one land cover may have a larger flux than other under low water table conditions, but the relationship may switch under highwater tables. How can this be addressed? Some of these limitations are addressed in the discussion, but perhaps a bit more discussion on the specific limitations for methane flux calculation is needed. More comparison against chamber derived CH₄ fluxes from different land covers can enhance this discussion.

More details about the footprint calculations are needed. It is not mentioned if footprint contours were applied or if all the footprint weights were calculated for the domain of the area shown in Fig 1? This needs more detail. Perhaps a table with summaries of average percent footprint coverage before normalization, fetch at 80% footprint contour, average footprint width, and average distance from the tower to the point of maximum footprint weight, will inform the reader about the footprint differences for each model.

The MCMC simulations is a useful approach but how good is it for methane emissions given the assumptions. One key question is how does this method compare to machine-learning gap-filling approaches (e.g. Artificial Neural Networks) that take into account the wind direction but also all the other important environmental drivers?

Specific Comments

What are the references for the equations for Respiration and GPP? (Eqs 3 and 4)

Fig 1. Is the location of the tower in the center of the map?

1. 125 Is the time lag removal by covariance maximization necessary for open path instruments?

L.127 an RSSI lower than 15% is an extremely low threshold. Can you provide justification for the use of this threshold?

L.146 Can you provide more details about the roughness length calculation? It seems rather low. It is also not clear how canopy height was estimated. Was it assumed to be zero?