General Comment:

I enjoyed reading this paper. The results are relevant and interesting, and most of the figures are clearly labelled and easily interpretable. However, the authors should address a few points to improve the manuscript.

Comments:

• Figure S1 and Table S1 should be moved to the main text. The reader needs to have an overview of the satellite instruments used in the study.
• The results and discussion section should be reformulated to avoid starting the paragraphs/sentences with Figure X (for example, on lines 205, 212, …). The explanation of the figures should be integrated into the text.
• Figure 11 should be changed to make the text in the figure more readable.

In this study, the authors integrated the high-resolution GEOS-Chem model and newly-available measurements to estimate the impact of biomass burning (BB) and anthropogenic emissions on tropospheric ozone over Southern Africa. They identify the best estimate of BB emissions inventory and quantify the effect on regional tropospheric ozone over Southern Africa. The authors compare simulation outputs using different emission inventories. However, the discussion would be strengthened by providing a more in-depth coverage of the physical and chemical processes driving ozone and PM formation.

Comments:

1. The authors should provide a summary of available surface observations and satellite data for chemical species and compare the model results with observations, including statistics on the spatial distribution.
2. In addition to the overall emission rate difference, how do spatial variations compare across the different emission inventories? A summary of statistics analysis would be helpful.
3. BB not only emits NOx, but also VOCs and PM. The authors should summarize the related information such as CO, VOC, NOx, BC and OC, which were stated to play a role in ozone concentration. Are there any specific ratios among emitted chemical species?
4. Line 174: should “Run_QFED_34%” be corrected to “Run_QFED_66%NOx”?
5. Lines 227-228: When comparing ozone concentrations with Dewitt et al. (2019), the authors should present results for both GFED and QFED emissions at the grid point associated with the station location. Currently, only Run_GFED is presented.
6. Lines 235-240 and Figures 5(a)-(c): OMI O3 shows significantly higher ozone concentrations over the Atlantic Ocean compared to the simulation. Could this discrepancy be related to the meteorological conditions in the model? This issue might also influence the comparison of NOx concentrations between the model and observations in the studied cases.
7. Line 303: if the case with QFED2 NOx emissions reduced by 34% (Figure S3) better aligns with satellite TCO data, would the FINNv1.5 emission inventory, which has ~ 0.67 of QFFD2 NOx emission (Figure 4c), be a more appropriate NOx inventory for this study?
8. Figures (g)-(l): the authors should address why the model predicts relatively low HCHO and CO concentrations.
9. Since pollutant concentrations can exhibit strong diurnal variation, was the simulation data aligned with the satellite overpass times in the region for the model-observation comparison?
10. Lines 318-319: how do BB VOC emissions in both emission inventories compare with anthropogenic (AVOC) and biogenic (BVOC) VOCs in Figure 3?
11. Lines 327: What are the major chemical species in BB VOCs, and how do they influence ozone formation beyond HCHO formation?
12. Lines 340-341: The authors briefly mention the model results without adequate discussion. A more detailed explanation of how aerosol chemical processes influence surface ozone concentrations would be helpful to illustrate the causality.
13. Figure 9 and the associated discussion: The authors should evaluate the comparison between observations and simulations. Could the higher observed NOx concentrations at the observation site compared to the simulation be due to the emissions being concentrated in a small area, whereas the model averages emissions over a larger grid? This could explain the lower simulated concentrations.

The study evaluates several available NOx emission inventories from biomass burning and anthropogenic activities using GEOS-Chem sensitivity simulations against a few ground-based measurements and multiple satellite observations in Southern Africa. While the manuscript is readable, it lacks depth in scientific analysis. The conclusions are based solely on sensitivity simulations with altered emissions, ignoring other factors that might affect surface ozone, NOx concentrations, and vertical column densities. The authors seem to imply that GEOS-Chem is flawless except for the input emission inventories, which is obviously untrue. Additionally, when evaluating anthropogenic NOx emissions, the uncertainties of QFED2 are not mentioned, which could undermine the entire analysis. Thus, the current analysis is unconvincing, even if some conclusions might be correct. A more comprehensive analysis is needed to draw more robust conclusions.

Minor comments:

Line 23: Please provide the full words of GFED4.1 at its first appearance, similar to other acronyms throughout the manuscript.

Line 34: “high-quality” to “high-resolution”

Line 42-43: What do you mean by the photochemical oxidation of nitrogen oxides? Which species is NO2 oxidized to? Please change “oxidation” to “reactions.”

Line 55: Delete “emissions” and change “emit” to “emits.”

Line 107: Delete the last “The.”

Line 130: “there” to “these”?

Lines 141-144: It would be better to clarify the uncertainties of these satellite datasets.

Lines 167-189: Why are these sensitivity simulations conducted in different years? Are you sure these simulations are consistent, considering the natural variability of climate? In Line 169, you mentioned simulations from 2019-2023, but I didn’t find any corresponding simulations in Table 1.

Figure 2. Why didn’t you use soil NOx and BVOC emissions from your simulations but those from Offline documents? Soil NOx and BVOC are sensitive to meteorological conditions and are calculated online in GEOS-Chem.

Lines 234-235: Compared to what? The observed 70 ppb? Do the simulation results and observations match in timing?

Lines 238-239: I don’t understand the logic. How can the simple comparisons above support such a conclusion? How about the surface ozone seasonal variations? Are surface ozone concentrations lower in the non-fire season?

Lines 244-245: I wonder how you processed the observed and modeling data. Aren’t coincident observations and model results used in the comparison? Did you just calculate the seasonal or monthly mean model values regardless of the availability of observations?

Line 263: It can only explain the lower NOx emissions of FINNv1.5. How about GFAS?

Line 271: “he” to “the”.

Line 271-272: You can’t make such a conclusion based on a single set of sensitivity tests with perturbed BB NOx emissions, although the conclusion may be correct.

Line 276: Delete “whether” and add “simulating” before “in.”

Line 282-283: The differences are also significant in the mid-troposphere. Did you calculate which part in altitude contributes most to the TCO difference between GFED4.1 and QFED2? It can’t be directly derived from the vertical profiles in Figure 6.

Line 296-305: NO2 vertical column retrieval is sensitive to the NO2 vertical profile. Did you redo the retrieval using your simulated NO2 vertical profiles?

Line 410-411: I’m afraid I must disagree with such a derivation.

Line 454: “high” to “large low”

Line 467-468: I don’t understand the logic here. The sea downwind is also susceptible to BB’s long-range transport.

Line 472: “like Southern Africa” to “with significant NOx spatial heterogeneity.”

Lines 493-494: Did you check NO2 in the free troposphere? A large portion of NO2 lies in the free troposphere, significantly contributing to NO2 VCD.