The Smoydzin et al. manuscipt presents analysis and modeling of ozone produced as a result of biomass burning and lightning emissions over the Amazon Basin.  The analysis is tied to aircraft observations taken in the UT off the east coast of Brazil.  Backward trajetories are computed from points along the flight track, and chemical calculations are performed in a forward Lagrangian model along these trajectories, which pass over fires and areas affected by lightning.  The resulting model-calculated ozone is compared with that observed on the flight, and NOx-sensitive and VOC-sensitive conditions are estimated.  The analysis is probably the best that can be done, but has a number of uncertaintiies:  e.g., biomass burning emissions, lightning NOx emissions, magnitude and frequency of convective transport. These uncertainties need to be stressed in the conclusions section of the paper.  In general, the text reads well, but more detailed explanations are needed in several locations, as noted in the detailed comments below.  In addition, more comparisons with previous results in the literature are needed.  My recommendation is that minor revisions are needed.

Detailed comments:

line 10:  Why is "eventually" used here?   Lightning often occurred in the same regions as the biomass buning or nearby.

line 52:  Need to add that Fishman et al. (1990) and Watson et al. (1990) used TOMS satellite data to recognize the South Atlantic ozone maximum.

line 56:  There is no Pickering and Simpson reference.  It should be Pickering, K.E., A..M. Thompson, J. R. Scala, and J. Simpson.  Please correct this in the text and reference list.

line 99:   No NOx observations are mentioned in this sentence.  Seems like they are an important piece of the analysis and should be mentioned in the full list of trace gas observations.  They are mentioned at the end of the paragraph (line 112) , but should be given more prominence.  

line 140:  here it is not clear that the MPTRAC trajectory model does not consider subgrid convective vertical transport, and only uses the grid scale vertical velocities.  This needs to be clarified here.

Line 149:  Is the chemistry initiated at the 13-day point of the MPTRAC trajectory?

line 158:  Need to explain what resolution T42L90MA means.

line 173:   Kappa(s) is not defined in Equation 2.   I assume this must be the emission factor.  Is this correct?

lines 175-176:  All biomass burning pollution is bening assumed to reside in the BL.  How accurate is this assumption?  Can you cite references to back up this assumption?   Some other models have assumed it is routinely mixed upward to 3 or 4 km by fair weather cumulus clouds.

lines 178 - 184:  The methodology for computing the LNOx emissions is not at all clear.   Does a single GLM flash in a grid cell trigger LNOx emissions?  Is a count of the GLM flashes in a grid cell used in the LNOx emission calculation?  If so, this needs to be mentioned.   The statement "We chose a LNOx emission factor leading to the addition of approximately 0.02 ppb NO per CAABA timestep." confuses the explanation, where a few lines earlier the 250 moles NO per flash is mentioned.   Is the 0.02 ppb also per flash?   Is this the total amount that is added per flash and then distributed in the vertical according to Pickering et al. (1998)?  This paragraph needs to be totally rewritten.

Equation 3:  Need to better explain what this equation represents.  Maybe quote Nussbaumer et al. (2023):  "Alpha(CH3O2) represents the share of methyl peroxy radicals  forming HCHO with NO and OH versus the reaction with HO2 yielding CH3OOH".     However, of what value is this equation if the OH + CH3O2 reaction is not included in the chemical mechanism?

line 206:  FIgure 3 is being called in the text before Figure 2.

line 219:   The longitude range of SASH is given, but not the latitude range.

lines 235 - 237:  Here finally it is mentioned that only grid scale vertical motion is used in MPTRAC.  The authors are correct that this will underestimate the number of BB trajectories that are lifted by convection.   It will also take longer time for them to be uplifted than in reality.  The potential mismatch between lightning flash location and the uplift by convection is a significant uncertainty in the modeling approach, and needs to be stressed more significantly in the text.

Figure 4 (top):  here we see counts of lightning flashes encountered by the trajectories for the first time.  So, perhaps these counts are included in the emission calculations.   Lines 178-184 need to better explain this.

In the discussion of the results of calculated ozone production with regard to the aircraft observations, the authors should include a comparison with the magnitude of ozone production downwind of deep convection shown in Pickering et al. (1996).

Figure 5:  What do the gray shaded areas represent?

Line 275:  "Enhancing LNOx emissions....."   Is this an additional experiment with larger LNOx emssions that is not represented in Figure 5?  The magnitude of enhancement needs to be mentioned, and the results illustrated somewhere (may in Supplement).

With regard to LNOx, some comparison should be included with the NOx observations along the coast of Brazil that were primarily lightning related that were presented by Dickerson et al. (1984, Atmospheric Environment).

Line 276:   ".....mainly in VOC-sensitive regions".   Based on the labeling in FIgure 5b, it looks likely there is mostly NOx-sensitive conditions.  Need to specifiy what values of Alpha(CH3O2) define NOx- vs. VOC- sensitive conditions.

Line 282-284:  Here the potential mismatch of GLM flashes and the times and locations of ERA5 deep convection is mentioned.  This could have a major impact on the P(O3) for the FLASH trajectories.  Need to emphasize this uncertainty more strongly.

lines 358-359:  Comparison with Pickering et al. (1996) needs some revision:   "....who link enhanced UT O3 levels observed in aircraft data and O3 soundings from Natal (northeast Brazil coast site) with biomass burning over central Brazil and deep convective transport of these emissions accompanied by a contribution from lightning."

Conclusions:  Need to add some statement concerning NOx- vs. VOC-sensitive conditions found in the modeling.  Can these results be compared with other UT O3 sensitivity studies? 

Review of “Impact of South American biomass burning emissions on elevated South Atlantic upper tropospheric ozone” by Linda Smoydzin, Vera Bense, Heiko Bozem, Philipp Joppe, Daniel Kunkel, Hans-Christoph Lachnitt, Holger Tost, Andreas Zahn, Helmut Ziereis, Martin Riese, and Peter Hoor

In this manuscript, the authors examine the impact of South American biomass burning emissions on the increase in ozone levels in the upper troposphere over the South Atlantic. For this study, the authors utilize a comprehensive set of observational data and modelling. They combine airborne in situ observations from two flights of the 2019 SOUTHTRAC HALO mission, remote sensing satellite data, back trajectory analysis, chemical Lagrangian box modelling and the EMAC model.

The manuscript is logically organized and the research is in line with the overall subject areas of ACP. However, the authors need to be more precise in some cases (see further minor comments). In the current state of the Discussion and Conclusions section I am not convinced that the results can support statements such as in line 344: “…we can conclude that biomass burning emissions contribute predominantly to the enhanced upper tropospheric O₃ level…”.

I would recommend the manuscript to be published after the following points were addressed in a minor revision.

Comments regarding the conclusions of this study:

The authors show that the BB scenario produces more ozone than the FLASH_BL and FLASH_noBL cases. However, as most trajectories are FLASH cases, the main contribution still comes from the FLASH cases (Fig 4b). The authors rightfully argue that the influence of boundary layer may be underrepresented by the model (for BB and FLASH scenarios) and demonstrate that the ozone production is limited by VOC.

However, in the description of the sensitivity simulations (lines 286ff) the added amount of VOC is not quantified. This leaves the question open if the “predominant” contribution is actually coming from VOC emitted by biomass burning emissions, or if biogenic VOC which is abundant over the South American rainforest (see e.g.: Tripathi at al. 2025) and are uplifted from the BL during convective events associated with lightning could explain a significant amount of the VOCs needed in the model to match the observations.

Without further quantification the presented results together with the also not quantified uncertainties of the simulations can’t support the conclusion stated in lines 12, 308, and 344, that biomass burning emissions are the “predominant” contributor to the observed ozone enhancement. In the current state, the results suggest that the predominant contribution is lightning NO_x associated with VOCs uplifted from the BL, also effected by biomass burning emissions.

Further minor comments:

Line 12: The 50 mWm^-2 does not appear anywhere else in this manuscript. Where does this number come from. Please specify in Section 3.5 and/or 4.

Line 31: Abbreviation BB emissions is not introduced yet.

Line 89: “NO, NOy” comma missing.

Line 91: Please specify which parts of these observations were under day- and which under night-time conditions.

Line 112: Please add the uncertainty for the NOy and NO measurements and remove double brackets around the citation.

Line 118: “...,it can retrieve vertical profiles for almost two independent layers of CO.” This statement on it’s one is not very helpful and unprecise. As it is not necessarily needed for the utilization of the MOPITT data in this study, I would suggest removing this part.

Line 182: Is the flash count of the GLM observations used for the estimation of the lighting NO_x individually for each timestep or is 0.02 ppb NO per timestep added for all lightning cases? Please specify.

Line 198: Abbreviation BL is not introduced yet.

Line 253: As the N₂O measurements are not shown anywhere, please quantify the observed range and compare it with literature values for the not specified “tropospheric range”.

Figure 6 caption: 300 hPa values are shown in blue not in yellow.

References:

Tripathi, N., Krumm, B.E., Edtbauer, A. et al. Impacts of convection, chemistry, and forest clearing on biogenic volatile organic compounds over the Amazon. Nat Commun 16, 4692 (2025). https://doi.org/10.1038/s41467-025-59953-2

The manuscript “Impact of South American biomass burning emissions on elevated South Atlantic upper‑tropospheric ozone” by Smoydzin et al. presents an analysis of measurements taken during two HALO flights in 2019. One of the flights showed large O₃ and CO values, likely influenced by biomass burning. Using trajectory analyses and satellite data, the authors further interpret the measurements.

I think the manuscript generally fits within the scope of ACP. In its current state, however, major revisions are necessary before it can be accepted for publication. Alternatively, I suggest converting the manuscript into a measurement report.

Main comments

The data analysis is well done and the two flights constitute an interesting case study. My main concern, however, is that the manuscript does not yet meet the definition of a research article in the journal. According to the ACP guidelines, research articles must include substantial advances and general implications for the scientific understanding of atmospheric chemistry and physics. In my opinion, the manuscript currently does not fulfil these criteria, especially because the authors provide a lot of references to previous analyses with similar findings (l52ff).

The authors attempt to contextualise the measurements with CO satellite data, but CO alone does not fully describe the situation. I wonder: Does ozone show similar enhancements in this region each year and is it caused by biomass burning? Insights from either satellite data (which may be complex) or model results would help.

To satisfy the journal’s criteria the authors would need to place their results into a broader context, e.g. by addressing questions such as:

• How typical/atypical were the emissions during that period?
• How common are such high ozone values caused by biomass burning in this region?
• (Based on the above) What is the radiative‑budget impact of these events?
  
  The answers to these questions are particularly important because the authors calculate an effect of ozone on the radiation budget. The 50 mW m⁻² figure they report is not very useful without a larger picture.

I understand that these analyses will require substantial additional work. Therefore, publishing the manuscript as a measurement report might also be an option. In that case, only the minor comments below need to be addressed.

The second main comment concerns the radiation calculations. Many details of the model and the exact methodology are unclear. Please specify them. The text and figures are also difficult to follow. As already mentioned by the reviewer, it is also not clear where the numbers in the abstract come from.

Minor comments

• Please check the usage of the word “scenario” with respect to the model runs. In my understanding you do not consider emission scenarios (which would refer to future developments) but rather different sensitivity/emission cases.
• L279: The authors write that EMAC model data are on a 1 × 1 ° grid, but on L158 they mention T42L90MA, which would be 2.8 × 2.8°. Please clarify.
• L164: If you use RCP6.0 emissions, they are outdated and may not reflect the “real” emissions in 2019. How does this affect your results? Could anthropogenic CO/NOₓ emissions in the region of interest have increased strongly compared to RCP6.0? This is important because it would strongly influence your BB trajectories.
• Figure 4: Please explain the colours in the bar fractions. Is the yellow the same as FLASH_noBL? If so, please use the same colour.