Review of “Investigating fire induced ozone production…” by Palmo et al.

In this manuscript the authors have assembled a high quality dataset of smoke observations and evaluated the ozone production from these with both a global and box model.    The authors work has led to several insights into smoke chemistry, and as such, will be a useful addition to the literature on this topic.     However I have a number of comments on the methodology and suggestions on the overall presentation.

Major points:

1. In section 2.4 they describe scaling of photolysis rates to examine the impact of aerosols on photochemistry. It seems they use an equal scaling for all photolysis rates.    This is probably not right as some are more sensitive to aerosol scattering and absorption then others, depending on the wavelength.   Can the authors comment on this or describe how this would impact their analysis.  
2. Similarly, for the idealized box model, it seems the SZA is fixed at zero. Can the authors discuss the impacts of this assumption.
3. In Figure 3, the authors an enhancement in NOx/CO at high photochemical age. This is a bit surprising.  Is this due to PAN decomposition?   How would this plot look if NOy were used instead of NOx.   What is the role of PAN decomposition on ozone production?
4. The discussion on photolysis is mostly good. But I am left with a question of whether this photolysis suppression impacts the overall ozone production?   Perhaps this photolysis suppression of ozone is a short term effect, which simply prolongs the NOx lifetime and therefore has little (or less) impact on the overall ozone production.   Comments?
5. In the abstract and elsewhere, the authors describe several key limitations of Geos Chem; too high ozone production and too little biomass burning emissions. It is not clear if these “two wrongs make a right”.  In other words, can we assume that GC is getting the right answer due to offsetting errors?   Can the authors describe more quantitatively how well these errors offset?

Other points:

Line 35 (abstract):   Is this reduction in ozone production temporary or permanent?

L37:   Sentence beginning with “Using a box model…”    This needs rewriting.  Hard tofollow this very long sentence.

L42:   Sentence starting with “these discrepancies” describes the problems, but then next sentence ignores the problems.   We need to better understand if we can believe the GC results here.

L110:  Note that Lee and Jaffe extended this analysis to include more than 600 sites in the continental US.

https://doi.org/10.1021/acs.est.4c05870

L154:  If I am understanding the units here, I am not sure this excludes all stratospheric airmasses.  For example, an airmass with O₃ = 500 ppb and water vapor of 2 g/kg would have a delO3/H2O ratio of  around 0.4 ppb/ppm and so would be included.   Comments?

L195:  Using the emission factors to get the t=0 ratios seems like a big assumption, given large plume to plume variability.   What is the uncertainty in this?   Why can’t you use the observations directly to get the t=0 values?

L210:   There are a number of simplifying assumptions here that need to be discussed as to implications.   Mainly fixed SZA at 0 degrees and scaling all photolysis frequencies the same, despite some mainly in the visible part of the spectrum, while others are more related to UV.

Figure 3:   It took a few minutes to figure this figure out.    It would help to discuss phi in the context of high and low NOx regimes.  There are some points at very high O₃/CO ratios (light blue).   I wonder if these might be better removed with a lower delO3/H2O screening ratio?   As noted above, it is surprising to see high NOx values at large photochemical ages (eg 50-200 hours).    Is this related to PAN decomposition?   Can you show this plot with NOy instead of NOx?

L295:  These equations are out of place.  They should be moved to before Figure 3.   Also, as noted above, the phi values are approximately equal to k*Conc(NOx)/Conc(CO).    Thinking about these as concentration ratios makes it a bit easier to conceptualize what is happening here…

L318:   Suggest to “observed J-NO2”.     As noted above, need some discussion on whether this is a temporary or permanent reduction in O₃ production.

Figure 5:   It is interesting that you see enhanced NOx in the fire regimes.   This contrasts with the work of Buysse 2019 (DOI: 10.1021/acs.est.9b05241).   Can you discuss in more detail?

Figure 6:   Suggest a statistical comparison of O₃ concentrations for the points with higher TCE values…

L370:   This whole paragraph is confusing and needs rewriting.

L390:  Didn’t you also test something having to do with NOx?

Figure 7 is hard to decipher.   A lot going on here.    Suggest to simplify to emphasize the main points. 

L423/section 3.3:

So this is where we need some discussion on the GC discrepancies and how the two major issues (ozone production and too little bb emissions) balance.

L465:   I am not seeing this in the Bourgeois analysis.  Can you clarify?

Figure 9:  This is good representation of the results, but we need more details.   What years does this represent, what months/ozone season and what are the area boundaries?

L530:  Please add “and under-estimates biomass burning emissions “ or something along this line.

Palmo et al. “Investigating fire-induced ozone production from local to global scales”

GENERAL

This study provides valuable insights into wildfire-driven tropospheric ozone production by integrating airborne observations, box modeling, and global-scale simulations with GEOS-Chem. While the work makes a meaningful contribution to understanding of fire plume chemistry and its impacts on atmospheric ozone, several limitations and uncertainties remain that warrant further consideration.

First, the reliance on airborne measurements, though offering unique perspectives, is inherently constrained by the limited temporal and spatial coverage of individual campaigns. Wildfires are highly heterogeneous in terms of fuel type, combustion phase, meteorological conditions, and plume dynamics, all of which can strongly influence ozone chemistry. The study synthesizes results from several campaigns, but it is unclear whether the dataset fully represents the diversity of global fire regimes, especially those occurring in tropical regions and the Southern Hemisphere, which are under-sampled compared to North American events (see Fig. 2). In addition, the airborne sampling indicates ozone formation process at the height of several kilometers, missing the information near the surface. This raises questions about the broader generalizability of the conclusions.

Second, the evaluation of GEOS-Chem highlights important discrepancies, such as the model’s overestimation of near-field ozone enhancements and inability to capture the chemical regime transition. However, the analysis seems largely diagnostic rather than mechanistic, as it does not indicate whether targeted sensitivity tests within GEOS-Chem were performed to isolate specific causes (e.g., emission inventories, plume injection heights, or chemical mechanisms). In addition, the coarse spatial resolution (2x2.5 or 0.5x0.625) can not resolve the ozone changes in the near-field plumes. Even though the model captures the ozone enhancement in the aged or far-field plumes, the derived sensitivity may not warrant the reasonableness of predicted ozone enhancement (e.g., in Fig. 9) on the global scale due to the lack of wide-range calibrations.

Third, the global attribution of 2.4% of the tropospheric ozone burden and 3.1% of surface ozone concentrations to fire emissions in 2020 may mask large regional and interannual variability. Fire activity is strongly influenced by El Niño–Southern Oscillation, land-use change, and climate variability. Using a single year could underestimate the range of fire impacts on global ozone. Moreover, uncertainties in fire emissions inventories, especially in Africa and South America, propagate directly into modeled ozone impacts but are not explicitly discussed.

SPECIFIC

Line 94: Previous studies have shown that “a smoke plume begins in a NOx-saturated regime before transitioning to a NOx-limited regime within a few hours.” Since this is also a key conclusion of the present study, the authors should explicitly clarify what advances their work provides beyond prior findings.

Section 2.4: What are the input factors used in the box model? How does the model account for potential impacts of meteorological variability or plume height on ozone formation?

Line 263: Why was a 10% variation chosen? For example, why not 50%?

Lines 292-299: These equations and related descriptions should be moved to Method.

Line 335: What is the sample size for each group?

Lines 347-348: “In general, NOy concentrations are largest in mixed air masses, followed by fire, then anthropogenic” It seems that the NOy concentrations are lower in mixed than fire as shown in Fig. 5b?

Lines 476-477: To what extent can increasing resolution and/or emissions be expected to improve the model’s predictability for near-field plumes?