The paper "Estimation of NO2 emission strengths over Riyadh and Madrid from space from a combination of wind-assigned anomalies and machine learning technique" by Tu et al presents a new simple method to obtain the tropospheric NO2 emission strengths and their spatial patterns derived from the TROPOMI observations. It relies on wind-assigned anomalies and machine learning (ML) technique (the so-called Gradient Descent) and it is applied to 2 cases (Riyadh and Madrid), which have already been used for emission estimates by past literature, to which they compare to in a few words. They also present the week-end effect and the impact of the COVID at the 2 locations.

The paper is well written and easy to follow, the study is interesting and in the scope of the journal, but the method is only briefly described relying a lot on references, and only describing the technical implementation, and no error estimation is mentioned. 

I recommend publication after some revision, including some more discussion and some testing cases (some are suggested below) to provide an estimation of the uncertainty of the method. 

Specific comments:

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The paper to my point of view lacks some discussion about the importance of the choice of different parameters, that here have been fixed "once for all", as coming from a reference (sometimes on a quite different topic), e.g. the choice of the wind (line 85) is the ERA5 at 330m coming from an "empirical choice based on Tu et al (2022b) ...", but where the focus is methane. In the discussion of the Riyadh results (sect 3.1) the output value is compared to Beirle et al. 2019, using a different wind source (ECMWF) and height (450m) and no discussion at all is made to help the reader knowing if these choices have a (large) impact or not. Similarly, when discussing the differences with previous results from Beirle 2011 and 2019 only a sentence "The difference might be due to the different study periods and methods used." (line 162) is mentioned. Also for the Madrid case (line 184: "This discrepancy is partly due to the different 185 periods, methods, and data sets used."). The author could make some tests on either different heights, or different wind source and give an estimation of the final outcome value.

To estimate the impact of the selected choices, I would suggest the following tests:

- use 1 year of S5p data instead of 3. Has this a big impact? Is this helping the coherence with the Madrid results, where yearly inventories are available? 

- test another wind height (why not the surface? as the NO2 is a short-live species, the NO2 will follow the orography)

- what is the impact of S5p in term of pixel resolution (ie wrt to OMI larger pixels used in Beirle 2011 for Madrid)? Could a test be made my resampling S5p to OMI resolution and seeing the impact on the outcome emission estimate?

- be careful that the S5p NO2 dataset is an aggregate of different versions (010202, 0103xx since 20/3/2019 and 0104xx since 29/11/2020, see ROCVR here: https://mpc-vdaf.tropomi.eu/index.php/nitrogen-dioxide). This should be mentioned in Sect 2.1 (v1.4 has an important change in the FRESCO cloud algorithm leading to larger NO2 columns, see e.g. Van Geffen et al., 2022) and a test on the impact of the change of version could also be interesting (as the remote and urban NO2 columns changes differently, is this leasing to a different spatial result of the emissions?). The different versions should be added in figure A9 with the S5p NO2 time-series.

Other minor comments: 

About the COVID impact, the illustrations are interesting, but the context of other studies could be done better. Some studies explicitly mention Madrid, in maps or tables (eg Beuwens et al 2020, table 1 and Levelt et al., 2021, figure 3) and could be discussed.

Some of the figures in the annexe are "quick and dirty" (or give this feeling at least). They seem like simple print-screens, without any latitude & longitude coordiates, etcc (figures A5, A7).

Technical comments and corrections:

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- line 33: "Though our analysis is limited to two cities as testing examples, the method has proved to provide reliable and consistent

results." --> what are the errors and limitations of the method? this is not presented in the manuscript!

- line 34 (and in the conclusions): "Therefore, it is expected to be suitable for other trace gases and other target regions." --> be a bit less optimistic, here only the 2 "easier" cases have been presented, but there can be challenges for other places/gases.

- Sect 2.1: give more details on the TROPOMI NO2 data used. Chich version? OFFL or a reprocessed? which version number? (at least mention that different version exist and give references)

- lines 85-88: see comment above about wind selection. Methane has a much longer life-time than NO2 (about 10 years vs a few hours), so explain why the choices made for methane are still ok for NO2 or five some estimation of the uncertainty related to this choice.

- line 96: how much impact has the choices of tau (4h for Riyadh and 7 for Madrid) on the result? what are the ideas to estimate this value for other trace gases or other target regions? (to follow my comment on the 2nd bullet here above!)

- lines 130-133: I don't understand very well the scope of increasing the area, and then remiving the "outmost ring" (ring is a bit missleading as the ROI is a rectangle)

- lines 141-145: although this paragraph is given to explain things, although for a non-expert on ML as myself, it is just creating confusion, with a lot of different names (without explanations or references), to end up with "This practice is not necessary with our problem." --> why?

- line 157: suggestion to "The estimated emission strengths based on the ML model *(Fig. 1d)* show a very similar spatial pattern to the results in Beirle

et al. (2019) (Fig. 2)."

- line 163: see comment above about discussing impact of different choices and tests that could be made to estimate uncertainty of the present method.

- line 184: "with a spatial resolution of 0.05º × 0.1º - 0.1º × 0.1º in longitude and latitude" --> I don't understand this resolution notation. 

"on a yearly basis" --> what year is considered in CAMS-REG-AP? or, if different years are available, can a test be made with only one year of TROPOMI to see if the year-to-year variability is similar?

- line 183: comment on the possible OMI vs TROPOMI resolution impact (see proposed test above). An error estimation would really help disentagle choices made with this approach and impact of time-periods (2005-2009 vs 2018-2021). How are the trends in NO2 around Madrid ? (see eg Georgoulias et al 2019 Fig 5)

- line 190: what do you mean by "With an expectation, these actions may help to decrease NO2 concentrations by ~25% in the central area by 2020." ? We are in 2022!

- line 197: mention that the airport is presented on Fig2d with a triangle.

- line 203: what does mean the 1/2 subscript on the different directions? it is also present in Fig A3, but not in its caption.

- line 227: suggestion "The ML-estimated emission strengths *for Madrid* are presented in Figure 4."

- line 228: suggestion "However, for weekends, the northeastern regions *(close to the airport)*, far away from the city center, are the main sources,..."

- line 259: "The NO2 emission estimate in the urban area *of Madrid* is about..."

- lines 260-267: add more discussion of other lockdown studies (see above some suggestions). (Do the same for Riyadh)

- line 282: same as said before "This difference might be due to the different study period and methods"--> this is too general. some investigations should be performed to give at least some error estimate/ quantification of impact of some of the choices made here.

- line 305: "But, it is can be applied to other key gases such as carbon dioxide or methane, and in other regions" --> as mentioned for the introduction, for me this is too general/optimistic. In my view carbon dioxide or methane have very different life-times and the urban emissions should be disentangled from the background. If you feel differently, please provide some supporting comments to your sentence.

 References:

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Levelt, P. F., Stein Zweers, D. C., Aben, I., Bauwens, M., Borsdorff, T., De Smedt, I., Eskes, H. J., Lerot, C., Loyola, D. G., Romahn, F., Stavrakou, T., Theys, N., Van Roozendael, M., Veefkind, J. P., and Verhoelst, T.: Air quality impacts of COVID-19 lockdown measures detected from space using high spatial resolution observations of multiple trace gases from Sentinel-5P/TROPOMI, Atmos. Chem. Phys. Discuss. [preprint], https://doi.org/10.5194/acp-2021-534, in review, 2021.

 

Bauwens, M., Compernolle, S., Stavrakou, T., Müller, J.-F., van Gent, J., Eskes, H., et al. (2020). Impact of coronavirus outbreak on NO2 pollution assessed using TROPOMI and OMI observations. Geophysical Research Letters, 47, e2020GL087978. https://doi.org/10.1029/2020GL087978 

 

Georgoulias, A. K., van der A, R. J., Stammes, P., Boersma, K. F., and Eskes, H. J.: Trends and trend reversal detection in 2 decades of tropospheric NO2 satellite observations, Atmos. Chem. Phys., 19, 6269–6294, https://doi.org/10.5194/acp-19-6269-2019, 2019. 

The manuscript presents an interesting new method for the determination of spatially resolved emission maps around megacities based on TROPOMI NO2 observations, wind fields from meteorological models, and machine learning techniques. The study matches the scope of AMT. Before publication, however, major additions/extensions are needed.

The paper presents results of the new approach exemplarily for Riyadh and Madrid and states that the method "works properly and is reliable" (line 283).

However, the resulting emission maps reveal strong artefacts which are not at all mentioned in the paper.

A critical evaluation/discussion of shortcomings, artefacts, problems, and uncertainties of the proposed approach is missing.

Major concerns:

- The presented results reveal several artefacts:

o several pixels of quite high emissions over regions without obvious NOx sources, e.g. at 25.05°N, 46.45°E and 25.25°N, 46.45°E (Figs. 1d, 3a). 

There is neither a significant NOx emission over this area reported in Beirle et al., 2019, nor is there a local enhancement in the NO2 column (Fig. A4).

o a large extended area of positive emissions north of Madrid (>40.7°N), where CAMS emissions are close to zero. 

While values of individual pixels still look relatively low in the color coded image, the integrated emissions >40.7°N are still considerable, 

and I do not think that these emissions are real. 

o generally "checkerboard-like" structures in the maps for data subsets.

This indicates a problem with the method that involves solving a linear equation iteratively. It seems that initial deviations are overcompensated in the next neighbor, than undercompensated in the 2nd next neighbor, and so on, indicating an instable system with oscillating values in the solution. I think this effect is a known problem for inverse problems, and the authors might check whether they find standard procedures for avoiding or supressing these oscillations.

In any case, the authors have to clearly describe the artefacts and discuss possible reasons.

- The authors should be more careful about the usage of the terms "NO2" and "NOx". Emissions are sometimes referred to as NO2 and sometimes as NOx in the manuscript. 

Clarify the issue of NOx = NO + NO2 in the beginning (emissions should refer to NOx, while TROPOMI only measures NO2).

Specify how you account for the missing NO in the NOx budget.

Note that there are more "oxides of nitrogen" (line 36) such as NO3, N2O5 or N2O, which are not included in NOx.

- In the introduction the authors give a quite high range for the lifetime of NOx of 1-12 hours (should be "tropospheric" rather than "atmospheric" lifetimes in line 43).

However, later they just use one fixed value, ignoring probable seasonal and spatial variability of the lifetime. This simplification has to be stated clearly and the impact on the resulting emission maps should at least be investigated with some simple case studies.

- The study makes several simplifications such as constant lifetime, constant wind field, no consideration of seasonal effects (which might correlate with wind direction and thus would directly affect the wind-assigned anomaly). A discussion of the impact of these simplifications, and in general an error discussion is missing.

- Finally, it is not clear to me what exactly would be the benefit of the proposed method. Quantifying megacity emissions is of course a valid goal, but this could be done with simpler methods as well. So the "extra" of the proposed method would be the generation of spatially resolved emission maps. For this purpose, a discussion of uncertainties and "reliability" of emission values for individual pixels is required. In addition, the authors should indicate concrete applications for the derived emission maps.

Further comments:

- Selection of sample locations: application of the method for Riyadh is quite straightforward due to the good observation conditions, as well as the split of wind directions almost equally in two opposite directions. But I wonder how the method should work for Madrid, as there is basically one dominating wind direction. So the wind-assigned anomaly can definitely tell you where Madrid is located, but with this "unimodal" wind pattern, I really wonder what additional information on spatial distribution of sources should be gained. There might be other megacities where the approach might be more promising.

- Line 70: "used to train": training is a crucial element of any ML, and I wondered here against which "truth" the ML is trained. It needs Eq. 1 to understand how the "modeled truth" is constructed that is used for training. I think that this is also an important component of this approach, that a simple downwind plume model is used to construct the NO2 distribution for the emissions from each grid pixel.

- Section 2.2: The authors describe eq. 1 as the "averaged distribution ... over a long time-period" (Line 90), but later apply this to "daily plumes". Please clarify.

- Eq. 1: what should be the meaning of the division by an angle in degree? I think this cannot be correct - is there a sin or cos missing? Otherwise, please clarify the units of all components of Eq. 1.

- Line 115: I understand the motivation for choosing log(wk) as proxy for wk. However, this drastically modifies the weight of the different pixels with focus on very low emission values.

The satellite measurements, on the other hand, have highest signal to noise for the pixels with very high emission values. 

This has to be discussed. Have you tried to run the algorithm directly with wk instead? This will of course result in some negative emission values, but the results for strong sources like powerplants might be more reliable.

Please also specify the exact procedure: are Eqs. 5-7 applied for wk or actually for log(wk)? If the latter is the case, then there should also be log(wk) written in all equations, plus an additional equation indicating how final emissions are derived (perhaps trivial, but I think very helpful for understanding what was done exactly).

- Line 115: Where is the initial epsilon coming from?

- Line 132: If the outer ring should be skipped in order to skip edge effects, the initial study area must be (n+2)x(m+2), since one pixel on each side has to be skipped.

- Line 152: In addition, for Riyadh the separation into two wind regimes suggests itself.

- Line 279: I would not agree that the spatial patterns aree very well. There are some artefacts present in the presented emission maps, and the conclusions should reflect this.

- I'm no native English speaker myself. However, several sentences and formulations sound strange to me. I would recommend careful language check after dealing with the requested modifications/extensions.

Technical issues:

- Line 49: etal. -> et al.

- Line 50: TROPOMI acronym explained twice.

- Line 80: To which area are the 910,000 measurements refer to? I think it would be more useful to give a typical number how many measurements there are per 0.1° grid pixel.

- all emission maps: The emissions are given in molecules per second, but implicitly refer to the chosen grid. I.e., for 0.05° grid, numbers would be only 1/4 of the presented values.

Emission maps should thus be provided as densities (emissions per time per area).

- all maps: please choose the same lat/lon range for all plots for Riyadh and Madrid, respectively.

- Caption Fig. 1: 0.1° is coarser than most TROPOMI pixels, thus the data is not "oversampled".

- x labels of Fig. 1 (c), 2 (c), 3 (f): "TROPOMI tropospheric NO2" is misleading here, as the shown quantity is a difference (or anomaly).

- Figs. 3 (c) and 4 (c): There are several pixels where weekend emissions are higher than on weekdays. Thus the colorbar in (c) should be symmetric around 0, including negative values as well.