General remarks

The paper compares 5 data-driven methods to estimate local CO₂ emissions from satellite images as an extension of earlier studies (e.g. Kuhlmann et al. 2021). The images including clouds were generated using a regional atmospheric transport model and known emissions from power plants and a city with output sampled as for the satellite in construction. 

In general the paper is well written and contains a lot of details. Concerning the cloud effects the language is sometimes not clear or too lengthy. It should be clearly said that in the 'cloud-free' scenario (section 2.3) modeled clouds are ignored and all pixels used for analysis, right? 

It might be interesting to include a remark what will happen for the accuracy of the methods if a cloudiness threshold of 2 or 5% is selected which might be more typical for real images.

A companion paper in preparation (Kuhlmann et al., 2023) is not a proper reference. Include only a short remark in parentheses on that in the text or refer to the code repository.

Some acronyms are defined several times in abstract and text, including section headers. Usually it should be defined only at the first occurrence.

Specific remarks

Line 13 and 47: Conflicting definitions of an acronym.

Line 16: Insert 'mole fractions' or 'volume mixing ratio'.

Line 17: Is that 'tropospheric column NO₂' like later in the text? Please be consistent.

Line 29ff: This long sentence is difficult to understand and should be split and improved for clarity.

Line 55 and 108: Define acronyms.

Line 199: This is in strong contrast to the swath of CO2M (line 14). Add a remark please.

Line 220: Because of typical stack heights?

Line 255ff, 275 and 280: Better use equation style with separate lines, don't repeat parts of an equation.

Line 257: This differs from the recommendation for LCSF.

Line 397: Also more combustion of fossil fuels for heating (cities).

Line 608: Refer to Fig.4.

Line 804: Filtered for clouds or what?

Table 2: 'Cloud fraction' is confusing here. In meteorology a cloud fraction of 100% means overcast sky and not clear sky or cloud free (scenario 1, 5, 0%?). If you like to say with a 'threshold of 100%' that model simulated clouds are ignored as in Kuhlmann et al. (2021) or line 324 please say that in caption or footnote.

Technical corrections

Line 342: typo.

Line 360ff, Fig. A3: The unit is 'ms^-1' (or 'm/s'), remove '.'.

Line 371: 'considering or ignoring the cloud cover'

References: Use consistent style for the year of publication.

Line 974ff: Is there a preprint (URL) available? Status?

Skip lines 991 to 994 (twice!).

Line 1018f: In the doi of this important paper '689838' is missing at the end.

Line 1020ff: This is not a reference. Status?

Figure 3: Shouldn't it be [  ] in the legends?

Figure 4, 9: Mention the meaning of the numbers in the inter-quartile boxes in caption (number of estimates?).

Figure 5, 6, 7, A4, A7: Remove '.' in units at label, better write 'CO₂ emissions (Mt yr^-1)'.

Figure 6, 7, A3, A4, A7, A8: Jänschwalde! Correct spelling!

Figure 8, A5, A6: Legend and caption inconsistent concerning percentiles.

Table 1: What is 'mn'? Should it be 'min' for minute?

The study "Benchmarking data-driven inversion methods for the estimation of local CO2 emissions from XCO2 and NO2 satellite images"

investigates the performance of various approaches for the quantification of CO2 emissions from synthetic satellite images.

As the quantification of CO2 emissions from upcoming satellites is a very important task with strong political and economical impact, 

this study provides an important scientific contribution.

The study is generally well written, and matches the cope of AMT.

However, I see one of the main results of this study, i.e. the rather poor performance of the divergence method, related to the way this method was implemented (temporal mean only), which is quite different from for treatment of the other methods (single images). 

I thus recommend publication after dealing with the comments below.

Implementation of the divergence method

The authors find the divergence method to show poorest performance for the quantification of CO2 emissions.

However, I suspect that this result is partly due to the way the retrieval was done. In particular, the divergence method was treated quite differently,

and - if I understood correctly - uses a different data selection then the other methods:

The quantification of emissions from methods (1) to (4) require the identification of a plume. I.e. these methods are only applied to favourable conditions which are close to steady state - which is more or less assumed in all approaches.

In contrast, the divergence method was applied to a temporal mean flux which probably contains unfavourable conditions as well - please clarify.

In any case, I don't see why the divergence method is not applied to single images as well, as all other methods. For a plume as the one shown in Fig. 1, the divergence of the flux should directly yield the corresponding emissions.

The motivation to use a long-term mean in Beirle et al. (2019, 2021, 2023) was that we wanted to *identify* and *localize* point sources first.

These tasks are considered as solved in this study - the locations of the considered point sources are given a-priori. 

Thus the divergence might easily be calculated for the single image data as well, and emissions can be derived by simply integrating the divergence signal within e.g. 15 or 30 km radius around the point source.

I don't see the need for an a-priori background correction, as the derivative does this automatically.

Furthermore, the noise of CO2 is probably not critical neither - an outlier pixel causes a high positive and a corresponding negative derivative next to each other, which just cancel out in the spatial integral.

Only outliers at the edge of the integration radius might be problematic; this effect can easily be quantified by varying the integration radius.

Thus I would like to ask the authors to add a further simple divergence-based emission estimate by just calculating and integrating the divergence on the original (unsmoothed) CO2 data for those days where a plume could be detected, and update all figures accordingly. 

I consider this to be a fairer comparison to the other methods, and actually expect the divergence method to be competitive to the other methods.

Additional comments

Title: The authors should add "synthetic" before "satellite" in order to avoid misunderstandings.

Line 91: I would propose to have a real enumeration here with new lines for each item.

Line 143: "however the ability of the different approaches to detect unknown point sources has not been studied here"

It might be mentioned that the divergence method is particulary suited for this task.

Line 284: Yes - if the focus is the detection/localization of point sources, temporal averaging is needed. But in this study, the locations are known and assumed as given for all other methods, so they should be considered as given for the divergence approach as well.

Table 1: I find the statement that the "Potential for joint use of NO2 to detect plumes" is not given for the divergence method highly misleading. 

The divergence does not need to detect a plume - it is based on changes of the flux. But for this, it is of course very helpful to have information on the respective divergence for NO2! 

Generally, the divergence method is the only method capable of localizing a point source without a-priori knowledge, i.e. the NO2 measurements analyzed with the divergence method could build the base for all different methods for CO2 emission estimates by providing the location of point sources. 

For the concrete focus of this study, the NO2 divergence might be used as indicator (filter) for favorable (steady state) conditions - if the divergence does not yield reasonable results for NO2, also the CO2 results are probably questionable and should be skipped.