This study presents a sensitivity analysis for a new inversion technique that estimates CO₂ emissions from co-emitted air pollutants (NO₂). The inversion methodology is an interesting way of bypassing challenges in CO₂ remote sensing and takes advantage of the relative ease of NO₂ detection with remote sensing relative to CO₂. While the methodology has been presented elsewhere in the literature with useful applications in real-time greenhouse gas monitoring, a rigorous assessment of its sensitivity to the different input variables is valuable for optimisation moving forwards. The separation of sensitivities into spatial, temporal etc. is particularly nice, especially as we strive for greater and greater resolution in these dimensions. This makes it easy to understand the limitations for specific use cases. In general, the manuscript is of high written and visual quality, and the analysis is sound. I have a few minor comments surrounding the prior NO_x emissions as well as some suggestions below.

Line 89: What are the sector specific scaling factors? Which sectors and by how much they are scaled (inaccurate) is one of the most valuable outputs of this kind of methodology from a NO_x standpoint. It would be nice to see a plot displaying this in the SI.

Line 94: I have concerns about the accuracy of CO₂-NO_x emission ratios. My knowledge of Chinese emissions inventories is poor. However, in European emissions inventories emission factors for NO_x can be very outdated. Perhaps this is taken into account with the scaling factors discussed in Line 89. I think a discussion of the emissions inventory in addition to the sector specific scaling factors, and even a comparison with other international emissions inventories would be useful e.g. EEA/EMEP, US EPA.

Line 104: Where does this 40% reduction come from? This is not discussed in the text.

Line 135: How do the sector scaling factors in Line 89 compare to the -1 to -10 % gradient system? Is -10 % a high enough threshold? Why do you only consider a negative range?

Grammatical:

Line 11: Suggest removal of “to prevent irreversible damage”. Not needed and air pollution is generally not irreversible.

Line 24: add “the” after “example,”.

Line 28: Suggest change to “how much, where, and by what activity pollutants are released…”.

Line 61: Suggest change “Our analytical endeavour” to “This study investigates”.

Line 217: Suggest removal of “(all columns expect the first one)”. No need to clarify.

Line 258: Suggest replacement of “least” with “low”.

Figures/Tables:

Fig S5: misspelling of national in y-axis label

Fig S11: It would be good to see this plot vs temperature. Why is there such a big drop in March? If it is correlated well, this would be a good verification of the system.

Table 1: Please can you clarify what you mean by “reduction ratio of NO_x EFs halves annually”?

This work presents a robust uncertainty analysis for an established mass balance inversion scheme capable of inferring CO2 emissions from TROPOMI’s NO2 measurements. While I do not take issue with the results presented in this manuscript, I found myself carefully re-reading the text multiple times to try and find information I felt to be crucial to the methodology. Some of the information was found after multiple readings while some remained elusive. The omission of certain points in the methodology section and its lack of organization made reading difficult. I have listed my comments, both major and minor, below.

Major Comments

In Lines 38-40, the text mentions the “co-emissions characteristics in time and space” of NO2 and CO2 emissions, leveraging the linear relationship between the two (Yang et al., 2023; Fig. 1). However, in other work by the author (Li and Zheng, 2024; Paper highlight #2), they state that NOx and CO2 are inversely proportional (at least during COVID lockdowns). Upon first reading, this seems like a contradiction. Perhaps the relationship between NOx and NO2 emissions should also be discussed in the introduction, near lines 38-40. At least conceptually highlight the conversion from TROPOMI NO2 to NOx here, particularly how  works (eqn. 2).

Lines 46–50 claim that space-based observers of NO2 have surpassed CO2 observers in revisits, spatial resolution, and coverage. However, I question at least some aspects of this statement. While TROPOMI has a daily revisit time, it is restricted to a ~1:30pm overpass time. The CO2-observing OCO-3 instrument provides coverage at different times throughout daytime hours, providing the potential to elucidate diurnal emissions (albeit with a ~3 day revisit time). Additionally, OCO-3 has a higher spatial resolution than TROPOMI, on the order of 2km x 2km. Thus, it is my opinion that Lines 46-50 make unfair statements by not acknowledging the benefits of the OCO-3 instrument.

Furthermore, this paper does not take into account the most recent efforts to measure sector-specific CO2 emissions at a sub-annual scale (see Roten et al., 2023 for example). The title of this work “Air Pollution Satellite-based CO2 Emission Inversion: Evaluation, Sensitivity Analysis, and Future Perspective” suggests that the focus will be on the uncertainty/error of the posterior CO2 estimates. There is little discussion of the current uncertainties of these measurements, approximated with “direct” CO2 observations, not NOx. Results should be presented in light of recent OCO-2, OCO-3, etc work. Several publications include city- and sub-city-level emission estimates using CO2 observations, not CO2 approximations. Consider uncertainties determined by Yang et al., 2020 and Ye et al., 2020 presenting constraints on CO2 emissions using CO2 observations directly. (Of course, results presented here are sector-specific. Yang and Ye are not.)

(Roten: https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2023GL104376)

(Yang: https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2019JD031922)

(Ye: https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2019JD030528)

The authors should consider reordering the methodology sections. For example, moving 2.1 (Base Inversion) after 2.2.4 and updating the text would let Sections 2.2.1-2.2.4 provide more context in the presentation of equations 1-4. The way the methodology is currently presented is quite confusing. I found myself rereading these sections multiple times to really understand what was going on. Several of these sections are missing helpful information. For example, the section titled “Prior Emission Inventory” (2.2.1) never actually mentions the name of the inventory being used. This made tracking down information difficult throughout my reading of the manuscript. Furthermore, for readers who are unfamiliar with the MEIC inventory, a figure like Fig. 1 of Roten et al., 2023 would be helpful.

From Line 114, “… while the CO2 EFs are assumed to remain unchanged”. If the emissions of NO2, NOx, and CO2 are linked (Lines 38-40) what is the logic behind the assumption that CO2 EFs remain unchanged? Should a scaling factor  not be applied as well? This is not well explained.

In Lines 88-89: “assuming that each grid’s emission variability was primarily driven by its dominant source sectors (contributing over 50%)…”. What about situations where no sectors make up more than 50% of a grid cell? Hypothetically, what if Power, Industry, Residential, and Transport all made up 25% of a grid cell? Do these situations not exist in the prior emission inventory? If not, why not? How is an observation-driven posterior estimate assigned to a grid cell when it doesn’t meet the criteria?

Minor Comment

For readers who are not familiar with the mass balance inversion method, providing an additional citation, or explicitly pointing the reader to an additional resource, would be more helpful than simply citing Zheng et al., 2020 and Li et al., 2023. Pointing the readers to a paper such as Mun et al., 2023 or something similar will help make the connection between the inversion system being discussed and the corresponding equations 1-4.

(Mun: https://www.sciencedirect.com/science/article/pii/S1352231022004940)

Remove the word “here” in Line 59.

Add “of” in Line 77. “ten-day moving average of anthropogenic NOx and CO2”

I understand the need to be succinct in Lines 78-81 regarding the scaling of emission sectors; however, it is my opinion that a little more information should be included here. The authors should consider including an extra statement explaining where these indicators came from. Were they from external an external inventory? Where they part of MEIC? Does MEIC contain sector-specific information already?

The source of the 40% reduction is confusing (Lines 105-106). Only after reading the rest of the paper did I realize that this was from one of the sensitivity tests. (Again, the authors need to focus on the logical flow of information in the text.)

Section 2.2.1 does not mention the spatial resolution of the inventory.

In Line 172, consider changing “policies” to “protocols”. The use of “policies” has political connotations.

In Line 245, add “the” before “tests’ impact”.

From Line 252, “A reduction in NOx increases rNOx”. Why is this the case? I do not follow.

In Line 273, I think “parameters” should be singular: “parameter”.

In Line 307, “mode” should be “model”.

How are the cities arranged in Figure 5? Are they arranged by longitude?