In this interesting paper the authors use the continuity or mass closure equation to derive emissions from the TROPOMI NO2 column observations. The authors discuss all the relevant ingredients of the calculation and provide estimates of the uncertainty. I am in favour of publishing, but with substantial revisions in response to a large number of questions provided below. 

Why Egypt? I understand there are many cloud-free days over the desert. Does the method require entire regions to be cloud-free? Or could it be applied to France just as well?

Section 2.1: "We use TROPOMI NO2 retrievals from November 2018 to November 2020". Please provide details. Which version (versions) is used?

Section 2.1: "TROPOMI sounding are gridded for this study at a spatial resolution of 0.1 × 0.1". The authors mention that the resolution of TROPOMI is 3.5 x 5.5 km. So the choice of the grid is a bit disappointing (11x11 km). Why choose this resolution and not a higher one? Please provide details of how the gridding is done. Is this conserving NO2?

Section 2.3: "Therefore, the CAMS OH concentrations are used". The resolution of CAMS is not very high, 0.4 degree. Given non-linearities and dependency on NOx, would the use of CAMS OH be a good choice? What are typical uncertainties, in particular those linked to the downscaling from 0.4 degree to 0.1 degree?

Section 2.4: "It is therefore necessary to remove the natural part of the atmospheric signal " We do not expect a lot of lightning and soil emissions over the desert. How large a signal is expected, why is removal needed, and how is this done?

Section 2.4:  "We conduct this removal by subtracting the mean emissions over desert and rural areas from the mean emissions over urban and industrial areas.  " Should "emissions" be "NO2 tropospheric column concentrations" here? Later in the paper there is a background emission term introduced. Why are background corrections not applied to the concentrations?

Section 2.5: The CAMS emissions also seem to rely on EDGAR and will use similar approaches/assumptions and input datasets. Please comment on how independent or dependent these two datasets are.

Section 3.1, line 184: "Slant column densities are used as vertical densities" This does not make any sence to me, and should be a large and unnecessary source of uncertainty. The simplest approach to the air-mass factor would be a geometric path length of the incoming and outgoing light which depends on the viewing angles and is > 2.0. So, neglecting the air-mass factor can easily lead to 50% errors. Why is this better than using the air-mass factors from the retrieval?? Furthermore, the slant column will include (be dominated by) the stratosphere. Why not use the tropospheric column? As mentioned, the sink is modelled as concentration divided by lifetime. But this concentration should be the column in the lower troposphere only, otherwise it does not make sense?! 

Equation 3: What is the omega_NO2 in this formula. Is it the slant column from TROPOMI?

Section 3.2. The discussion focusses entirely on electricity consumption, motivaing that 13:30 is representative for the daily mean. However, I would expect that traffic (industry) is also a major source of NOx, and this has a distinct diurnal (seasonal) pattern. So the discussion seems to be over-simplified. 

Line 258: The city of Riyadh has been extensively discussed by Beirle et al., 2019. A reference to this paper in section 3.3 should be added. 

Line 263: sqrt(w^2) = w. The notation is a bit unclear.

Equation 7: I still have a conceptual difficulty with a "rural emission". Over the desert the estimated emission should be close to =0 and negligible compared to urban emissions, otherwise the methodology is flawed.

line 324: "limit the high inter-day variability due to changing wind patterns or differences between week days and week-ends". What is the real reason averaging over a month is needed? Winds change, but if the method is correct the emissions should be equal (assuming stationary sources). 

l 359: "Level B is therefore the one that leads to the best match between the lifetime calculated with Equation (2) and the lifetime calculated from line densities." What does this really prove?  Does it really mean Level B is better? Due to the coarse resolution we may expect CAMS is biased in OH since it does not resolve the plumes.

Figure 6: Before showing this, I would suggest the authors apply the method to Riyadh and compare with Beirle et al. (2019) to test the consistency of the results. 

Table 1: I would suggest to replace "khab/km^2" by "10^3/km^2"

l 420: "It is also observed that TROPOMI NO2 column densities above this zone are relatively homogeneous" As demonstrated in several papers, there is a clear shipping signal in the TROPOMI data over oceans and seas, and I would expect TROPOMI to be rather inhomogeneous here?! 

Figure 8: The unit is "kt" which I assume is 10^6 kg. But what is the time unit? Per hour, per day, per year? I'm a bit surprised by the big scatter for the weekly (daily) values averaged over the entire country? 

Section 4.5, Covid-19. There is a nice review paper, https://doi.org/10.1525/elementa.2021.00176, which could be added here.

l 488: "no significant changes in OH concentrations ". Does the CAMS system describe the change in emissions and concentrations observed resulting from the lockdown? If not, how would this impact the results (given the non-linearity of the chemistry)?

l521: "TROPOMI-inferred emissions show an annual variability" I was wondering how much we can believe the seasonality in OH as modelled by CAMS? This seems to directly link to the seasonality of the sink term and, as a consequence, the emission estimate. Please discuss.

l551: "S-5P validation activities" Please add a reference

l 558: "For [OH]," The authors showed that OH is strongly height dependent, so it seems that the choice of the vertivcal level is a major uncertainty. Has this been accounted for?

Data availability: TROPOMI data is missing here.

Rey-Pommier and co-workers report on a framework aiming to quantify NO_x emissions in Egypt relying on slant TROPOMI NO₂ columns, wind fields from ECMWF ERA5 reanalyses, and temperature, OH, NO and NO₂ fields from CAMS. This top-down approach is based on the continuity equation in steady state, with the species concentration in an elemental volume being a result of flux transport in and out of the volume, the sources inside the volume from emissions and chemical production (e_NOx), and the sinks inside the volume from chemical loss and deposition (s_NOx). The reaction of NO₂+OH is considered as the only significant sink term in the calculations. The slant columns of NO₂ are used in lieu of the vertical columns in the continuity equation, leading to errors that are not well assessed in the manuscript. The top-down emissions in Egypt are found to be in good agreement with the CAMS-GLOB-ANT_v4.2 bottom-up inventory, except for substantial temporal variations in the TROPOMI-based emissions not found in the inventories. Those variations, in particular a pronounced minimum in the winter 2019/2020, are very implausible. Their proposed explanation in terms of variations in electricity consumption does not stand scrutiny. A more in-depth analysis is required to better understand the possible sources of error.

I cannot recommend publication at this stage due to the following concerns that need to be adequately addressed and the choices made well justified. 

Comments: 

- l. 142 and following: the "urban" pixels (>100 hab. km^-2) are not all truly urban. Croplands in Egypt are located almost exclusively within the "urban" cells of Figure 1, whereas the non-urban pixels are mostly (semi-)desertic. Therefore I doubt that the removal of the non-anthropogenic part of the NOx emissions discussed here makes any sense. Soil NO_x emissions are primarily located within the Nile delta and Nile Valley. Same holds for agricultural residue burning, a substantial source of pollution in Egypt (https://egyptindependent.com/agricultural-burning-clouding-sky-sickness/). 

- l. 174-184 : Equation (1) does not make much sense if slant column densities (SCD) are used as vertical column densities (VCD). The air mass factor (AMF) is generally different from unity, and furthermore, it varies in time and space. Contrary to the assumptions made here (Section 4.7), the albedo over the region is not uniform since we have areas covered by deserts, by crops, by water and by cities. The vertical profiles of NO₂ can also be expected to vary according to the landscape. Those variations will impact the divergence term in Equation (1). The authors state that the AMF is taken "into account in the final uncertainty estimates". However, Section 4.7 only discusses the VCD uncertainty due to the AMF, (~30% following Boersma et al., 2004). This does not say anything about the impact of using SCD instead of VCD in Equation (1). I am worried that the real impact of this substitution is unknown. 

- l. 193 I don't understand "using a temperature-dependent analytical formula for different pressure ranges". Burkholder et al. provides a general expression of the rate as function of both T and [M]. Please clarify.

- l. 196-197 I don't understand "The value of k_mean therefore represents the total loss of NO₂ due to OH and cannot be used to infer HNO₃ and HOONO production". This is not clear. Only the first channel is a true NO_x sink, therefore the other channel should be ignored entirely.

- l. 211-212 "Losses due to deposition and the formation of (...) nitrates are thus considered insignificant in Egypt where the forest cover is totally negligible": this is not correct. Forest cover might indeed by very low, but vegetation (mostly croplands) is present in the so-called "urban cells" of Figure 1 (leaf area index typically between 1 and 2 according to MODIS). Furthermore, TROPOMI HCHO maps show HCHO vertical columns over the Nile Valley and the Delta (>1 Pmolec cm^-2) in summer, which are similar to values found in Southern Europe. This suggests significant NMVOC emissions, of biogenic and/or anthropogenic origin. Organic (peroxy)nitrate formation cannot be assumed to be negligible. There is very likely a significant net export of RONO2 and PAN compounds from the Nile area to the surrounding regions. A comprehensive model might be needed to evaluate its importance. Quite importantly, this export might be seasonally dependent, since organic nitrate formation is strongest in summer. 

- l. 213 Regarding the HNO₃-forming channel of the NO+HO₂ reaction, note that field studies (e.g. Nault et al. 2015, doi:10.1021/acs.jpca.5b07824) indicated that this path is very minor. 

- l. 216-217 Production of PAN might peak in the late afternoon, but it might still be significant earlier in the day.

- l. 221-228 Why is electricity consumption assumed to be the best proxy for NO_x emissions? Traffic and industry follow different patterns. According to current inventories, what are the respective relative contributions of the main sectors (traffic, industry, power generation) in Egypt? Some discussion is needed. 

- l. 258 "We therefore use the nearby city of Riyadh (...) to perform the comparison between the CAMS-induced lifetime and the fit-induced lifetime": despite some similarities, Riyadh and the Nile valley are quite different environments, with much more vegetation and NMVOC emissions in Egypt than around Riyadh, possibly impacting e.g. the wind profile, the OH fields and the NO₂ profile. Therefore, the OH validation for Riyadh might be of limited value for Egypt. I recommend comparing the TROPOMI HCHO columns over Egypt and Riyadh. 

- Equation (7): As explained above, the "urban cells" do contain natural emissions. Moreover, the non-urban cells contain anthropogenic emissions. Those are less intense than in the Nile Valley and delta, but the natural emissions follow the same pattern. I recommend to drop this separation.  

- l. 389-406:  What is the location and capacity of the main power plants in Egypt? Are the industries mentioned in the text (e.g. cement plants) really strong NO_x emitters? 

- Section 4.6 The temporal variation of TROPOMI-based emissions seems very unrealistic. The 2019/2020 winter minimum would be explained by reduced electricity consumption due to reduced usage of air conditioning. But then why not in the previous winter? In any case, it should be possible to check whether the biggest power plants are the places where the seasonal behavior is most pronounced. And regions without any significant power plants should not exhibit this phenomenon at all. I doubt very much that air conditioning would increase so much the traffic-related NOx emissions. I think much more plausible that the temporal variations are due to errors in the methodology, in particular regarding NO_x sinks and the air mass factors. I recommend to check whether the TROPOMI AMF (or an AMF recomputed using CAMS profiles) presents significant temporal variations. This requires a more in-depth analysis than is currently provided. 

- Section 4.7 Regarding uncerainties, as noted above, I doubt that NO₂+OH is really the only relevant NOx sink in the area. Furthermore, the impact of ignoring the AMF in Equation (3) should be assessed. The uncertainty of only 1 m/s for the wind components seems optimistic since the precise altitude at which the wind is interpolated is arbitrary, and the Coburn et al. study concerns the U.S. which is likely better characterized in the CAMS model. 

- l. 239 Burkholer -> Burkholder

- l. 378 "towards in the northeast and southeast quadrants": unclear. Do you mean towards the northeast in summer and southeast in winter? 

- l. 666 : I could not find Huijnen et al. 2016, please provide URL