This is an excellent study estimating NOx emissions in 2022 from TROPOMI data. I appreciate all the assumptions involved and acknowledge that there are several additional sensitivity studies that could be done but also understand most of them are beyond the scope of this manuscript. With that said, I have listed a several minor suggestions that could improve the paper and better clarify some of the unstated nuances of the work.

Major comments:

It’s unclear exactly how OH is being incorporated to estimate the NO2 lifetime. Are you using surface OH concentration at the closest CAMS grid point? Or a model weighted vertical average based on the NO2 distribution? Or something more technical? If it’s the former, I recommend authors perhaps looking into an improved way of inferring the OH concentration and NO2 lifetime… See Figure 1 of Laughner and Cohen https://www.science.org/doi/10.1126/science.aax6832. I would plot NO2 lifetime (calculated from CAMS OH) as a function of CAMS NO2 column data. I am assuming there will be some type of non-linear relationship that can be used to infer the NO2 lifetime when TROPOMI NO2 column data differs substantially from the CAMS column NO2 data. Ideally you’d bin by TROPOMI HCHO which I realize is beyond the scope, but maybe calculating the NO2 lifetime vs. NO2 column relationship by Koppen climate zones could be a quick work-around (which would approximately account for areas with less/more biogenic VOC emissions). This is a long way of saying that if CAMS NO2 has a large mismatch with the TROPOMI NO2 data, your assumed OH may be way off, and there could be an easy way to approximately account for these mismatches. 

There is not enough discussion on why biomass burning emissions are not properly captured. It may be worth framing this paper as quantifying fossil-fuel related NOx emissions and purposely screen out areas of known biomass burning NOx emissions, which appear to be particularly uncertain for a variety of reasons (as the authors correctly note).

In the EDGAR intercomparison, I think small mean bias shown in the “Total” value of Table 3 (i.e..., good agreement) is the product of two offsetting biases: The TROPOMI NO2 operational retrieval is biased low by ~30-50% in polluted areas/cities (Line 468), and NOx emissions are 40% larger at 13:30 local time than the 24-hour average. Therefore I don’t dispute your claims in Section 3.3, but I do think that if the TROPOMI retrieval had no bias, then you would be doing an unfair comparison. More clarification should be added. I have added more references and description below.

In Section 3.3, it would be interesting to dive a bit deeper into where there is poor agreement between EDGAR and TROPOMI. This would really demonstrate the value of TROPOMI and your method.

Detailed comments:

Line 28. A bit more nuance could be useful. You should add something along the lines of “in conjunction with sector- and country- specific NOx/CO2 ratios”. There are many examples of NOx emissions dropping rapidly but CO2 not dropping or dropping modestly. I am sure you (the authors) know this but a future reader may not.

Line 37. The authors are being generous here :-), most bottom-up datasets take 3 years to generate. Unless you know of a emission dataset developed within 1 year, I would default to saying 3 years. This would further demonstrate the utility of your method even if it take several months to process the data.

Line 82. Which levels of the wind data are used? This is important for study replication.

Line 151. Modify “minor” to “less”. I also think you are misrepresenting the Beirle et al. 2019 and de Foy and Schauer 2022 studies a bit as these studies are investigating a relatively small domain over a single season or climatological pattern. A constant NO2 lifetime is not ideal, but a better assumption than if they were global studies. Please correct me if I’m wrong but I don’t know of any global study assuming a constant NO2 lifetime. Beirle et al., 2023 uses a latitudinally dependent NO2 lifetime, and I agree your method of using CAMS data is much better. In short, I agree with all your sentiments here, but be careful with some of the nuance.

Line 202. It’d be best to move discussion in Lines 275 - 278 about wildfires to here. The missing emissions in the Amazonia suggest your method is best for estimating fossil-fuel related sources. Even though Amazonia wildfires take place for only a few months, they should probably show up more distinctly in the annual average than they currently are. Perhaps the days with the largest smoke and NOx emissions are being filtered out as clouds. Another 2-4 sentences are probably needed to discuss these nuances.

Line 203. The sentence “Figure 3…”  should be the first sentence of the next paragraph.

Line 267. I am confused by how you are counting the number of pixels in a metropolitan area. Using Baghdad as an example, I am counting maybe 30 pixels within the dotted outline in Figure 6, where does the 198 pixels value come from? And can you highlight that 198-pixel “zone” in Figure 6?

Table 1. Typo of Shanghai

Lines 293 - 325. Thanks for this discussion. There is one policy-relevant question that is still unanswered in this section. From an emissions standpoint, what is the threshold point source emissions rate given a 2 Pmolec-cm-2h-1 threshold? 0.5 tons per hour? Less?

Line 355. I wouldn’t discount there being a real difference in Russia. How do individual cities in Russia (Moscow, St. Petersburg, etc.) compare against EDGAR?

Line 358. This is consistent with Ahn et al., 2023 (https://iopscience.iop.org/article/10.1088/1748-9326/acbb91) which shows something similar for CO2. I think more detail on this would be interesting and helpful. Which countries in particular show worse agreement? Are they all low-income countries and/or countries with a lot clouds? Maybe a few more of the outlier points can be labeled on Figure 8? I understand why a log-scale is used, but it is a bit deceptive as the Russia bias is probably the largest of all countries. Therefore more discussion in the text is needed.

Line 366-369. Urban NOx emissions at 13:30 are still ~1.4 times larger than the 24-hour average since so many nighttime hours have very low emissions: Please cite and see Figure 4a of Goldberg et al., 2019 which shows an example for New York City: https://acp.copernicus.org/articles/19/1801/2019/acp-19-1801-2019.html I have seen other unpublished studies showing the temporal hourly pattern of GEOS-CF NOx emissions in many global cities look like New York City (and not Seoul). I think you have offsetting biases that are conveniently and approximately cancelling out: The TROPOMI NO2 operational retrieval is biased low by ~30-40% in polluted areas/cities (Line 468), and NOx emissions are 40% larger at 13:30 local time than the 24-hour average. Therefore I don’t dispute your claims in Section 3.3, but I do think that if the TROPOMI retrieval had no bias, then you would be doing an unfair comparison. More clarification should be added.

Line 390. Thank you for including Portland in Figure 9. First, I am assuming it is Portland Oregon, USA as there is also a Portland, Maine, USA. It is interesting that 84 days vs. 336 days of averaging shows a factor of 2 difference, whereas other cities show less variance by percent. It may be worth commenting that Portland is a relatively small city and cloudy for much of the year, so it’s probably “worse case scenario” or “limit” to the type of conditions in which your method works.

Line 425. See prior comment. It is also a function of the size of the city/NOx source too. Large sources may only need one month of data, but smaller sources may need a full year of data. 

Rey-Pommier et al. present a global dataset of monthly mean gridded NOx emissions derived from TROPOMI measurements.

The authors apply a flux-divergence method which has been presented in previous studies, but, to my knowledge, has not yet been used to compile such an emission dataset on global scale. Thus, the dataset is generally of interest and matches the scope of ESSD.

However, in the current version, I see two major shortcomings that need to be resolved before publication on ESSD:

1. The dataset contains extreme outliers, which I can only explain with some bug(s) in the processing chain, and

2. The discussion of uncertainties misses some of the most important factors (choice of wind altitude, background correction, air mass factors).

For further details and additional comments see below.

**Methodology**

Horizontal transport

The authors do not directly state which altitude is selected for horizontal wind fields. From the context ("assumption of a stationary state and a pollution concentration close to the ground") I conclude that surface winds have been considered, which is probably not the best choice:

- power plants etc. emit from stacks of altitudes up to some hundred meters.

- even emissions at surface (e.g. from car exhausts) are usually rapidly mixed within the boundary layer.

Thus, wind fields for a typical altitude within the boundary layer would be more appropriate, as shown in several previous studies.

In any case, the authors should 

- explicitly state which altitude was chosen for wind fields, 

- justify that choice and

- quantify the uncertainty associated to that choice (by comparison to alternative processing with different altitude).

Noise 

The presented emission data is very noisy at high latitudes, in particular over ocean.

This is shortly mentioned in the manuscript, and the authors explain it with the low amount of available data.

However, there seem to be some issues in the processing that cause quite extreme outliers:

For instance, in the January data at (2348, 582), corresponding to 143.6°W, 56.8°N (northern Pacific), emissions are 20 Pmolec/cm2/h, which is a factor 10 higher than the threshold for the "high emission densities" classification in the paper. There are many more such pixel, and also many examples for negative values of the same order of magnitude.

Monthly mean maps of NO2 column densities from TROPOMI are usually quite smooth, and noise of individual pixels is about 1Pmolec/cm2. 

If divided by lifetime, the sink term over ocean should thus be well below 1Pmolec/cm2/h. Topography is not existing over the ocean. Thus only the derivative terms could cause these high numbers. But with low column, and thus low fluxes, how can the derivative be that large?

One even more extreme case occurs at (225, 419) with emissions of -173 Pmolec/cm2/h. This corresponds to 153.8°W, 75.9°S, and might be over Antarctica, i.e. the topographic term might have issues as well.

I suspect that the derivatives and/or gridding algorithms, in combination with gaps, causes these extreme outliers. 

The authors should check these examples and investigate the values in the "orbit" reference frame: 

- if the values for individual TROPOMI pixels show such high values, check from which term they come from

- if the orbit data looks reasonable, check the gridding routine.

These extreme and unexplainable outliers devalue the whole dataset. They should be identified and fixed before publication of this product on ESSD. 

Background correction

The choice for background correction is quite extreme: a full swath width of TROPOMI can cover a wide range range of conditions and rather presents a "mesoscale" than a "local" background.

I would expect that changing the settings for the background correction can have strong impact on the presented results. This effect has to be investigated and quantified.

What is the reason for including a far larger distance across-track than along track?

The choice of the 1st tercile for defining the background implies that 1/3 of all considered TROPOMI pixels have corrected columns < 0. This should be mentioned, and this is also one of the reasons for negative emissions.

Negative emissions

The dataset includes negative values for numerous pixels. This is shortly discussed in the manuscript, but this discussion should be extended.

In particular, the authors should provide a recommendation to the user how to treat negative emissions in potential applications.

In my point of view, it makes sense to keep the negative results in the data product, even if unphysical, as the alternative

(skipping or setting them to 0) would bias high the overall mean.

But this is exactly what happened in the spatial integration of country/regional emissions, which only considers pixels above a (positive) threshold.

This might be one reason for the results being systematically higher than those from previous studies (even though no air mass factor correction was applied).

The authors should discuss this aspect, and should provide information about how the derived emissions depend on the selection of pixels, and how they would look like if also the negative emissions would be considered in the spatial integral.

Air mass factors

The authors just took the operational product without any correction of the air mass factor (AMF).

This is problematic, as the AMF, and also its stated uncertainty, refer to the full tropospheric column, while the authors performed a background correction with the aim to only consider near-surface pollution. For this, the operational AMFs are not appropriate, and are systematically too high (and thus Omega' is biased low). 

This systematic effect cannot be described by a 30% uncertainty (in both directions).

Uncertainties

The section on uncertainties needs to be extended with discussions of the aspects listed above.

The presented agreement to EDGAR is quite good, but due to the issues discussed above, there might be some of the systematic effects compensate each other.

Purpose

In the abstract, the authors claim that "this dataset is designed to be updated with a low latency to help policymakers monitor emissions".

I think that this is an important aspect, as monitoring of changing emissions in timeseries might even work with the remaining high uncertainties. However, this aspect is not discussed any further in the manuscript. It would help a lot to support this argument if the authors could find e.g. a power plant that has been switched off in 2022 and show the corresponding time series of monthly mean emissions.

**Dataset**

- Unit

I understand the origin of the unit used (Pmolecules.cm−2.h−1) as this is just the commonly used unit for NO2 column densities (Pmolecules.cm−2) divided by a lifetime.

However, the presented dataset provides global emissions, which is of high interest for communities beyond those familiar with satellite NO2 products.

Thus, the unit should be modified to an (SI) unit commonly used, like kg/m2/s. At least, a conversion factor needs to be provided in manuscript and data product metadata.

- NC files

  - The coordinates should directly be lat and lon. There is no need for a "lat_grid" index. The unit "degrees_north" for the grid *index* makes no sense.

    When having lat and lon as coordinates, there is no need for additional "latitude_data". 

  - I propose to add the grid pixel area (1d, latitude dimension only) such that the user can simply convert the emission densities to total emissions for each grid pixel, which simplifies spatial integration.

- Annual mean

As the figures in the paper often display annual means, also an annual mean data file should be provided next to the monthly means.

- Negative values

The negative values should not be skipped in the dataset. But I would propose to add a disclaimer to the metadata of each file explaining the reason for the occurence of negative data.

**Minor comments**

Line 64: A reference to TROPOMI (e.g. Veefkind) should be added.

Line 68: This high spatial resolution only holds for nadir pixels.

Line 92: Provide information about the spatial resolution of GMTED2010. How exactly is this data "regridded on the TROPOMI grid"?

I assume that one TROPOMI pixel covers many GMTED2010 pixels, and simple interpolation of GMTED2010 data to the TROPOMI center pixel coordinates would not be appropriate. Instead, all covered GMTED2010 pixels should be averaged.

Line 110: "resulting in a purely horizontal calculation of emissions": 

The considered transport is "purely horizontal". Emissions are calculated as sum of divergence and sink term (proportional to the column). 

Line 113: Of course the approach requires input data like wind fields which have uncertainties. 

But on top, the assumptions (stationary state and a pollution concentration close to the ground) are probably just wrong afar from strong local emission sources. 

Line 130: Note that even without NOx from lightning and soil emissions, there would be a free tropospheric background from long range transport of NOy & PAN.

Line 139: This reads as if the enhanced NO2 over ship tracks is caused by lightning NOx, but it is primarily caused by direct ship emissions.

Line 141: Sink term: k[OH] needs to be multiplied with Omega.

Line 143: Please provide more specific information, e.g. global maps of NOx lifetimes from CAMS for Jan and Jul, which might be added to the Supplement.

Line 150: In particular, CAMS cannot resolve the extreme conditions within power plant plumes. This should at least be mentioned.

Equation 4: I think that the topographic correction must be determined from Omega, not Omega', as it describes the change of the *background* column when blown over a inhomogenous terrain. With Omega', the effect will be underestimated.

Equation 5:

- is the divergence calculated for Omega or for Omega'?

- k[OH] needs to be multiplied with Omega.

Line 239: Tehran was discussed in Beirle et al., 2023 (Fig. A1 therein) as example for the benefit of the topographic correction: without correction, emissions were negative, but with topographic correction, maps were far more plausible.

I suspect that the topographic correction does not work properly here, which might be due to the way of interpolation of the GMTED2010 data to TROPOMI grid and/or the choice of Omega' instead of Omega in Eq. 4. Please check.

Fig. 4: The extreme outlier of -173 Pmolec/cm2/h occurs in January, while Fig. 4 refers to annual means. But even if values would be close to 0 for the other months, the annual mean at that pixel would be about -14 Pmolec/cm2/h, i.e. there should be at least one "negative" pixel with absolute value > 10. Why does this not show up in Fig. 4?