Cho et al. present a comprehensive aircraft-constrained box modeling framework to examine the sensitivity of POx formation to NOx and VOCs in several urban environments. The study is carefully executed and clearly presented. However, I would like to suggest a few additions and clarifications that could further strengthen the manuscript.

The choice of a 750 m altitude threshold to represent near-surface conditions is reasonable and supported by vertical profiles (Fig. 2). However, the authors should test the sensitivity of this altitude to selecting another altitude and how it would impact the 4 cities considered in this study, particularly given potential vertical gradients in NOx, VOCs, and photolysis rates. A brief sensitivity test or justification based on boundary-layer height variability would improve the methodology.

Averaging observations over 1–2 h flight tracks may obscure rapid chemical transitions and plume heterogeneity, especially in high-NOx urban environments. The authors should discuss the implications of this temporal smoothing for nonlinear ozone chemistry and whether shorter averaging windows were tested.

MCM is a widely accepted chemical mechanism. However, it can be biased due to the neglection of heterogeneous chemistry, for example, HO2 uptake on aerosols, and the impact of halogens on secondary chemistry and radical budget. The authors can include a brief discussion on the direction and impact of these uncertainties.  

"A gridded parameter space was created by scaling the observed 155 mean mixing ratios of NOx and total VOCs from 1 to 300%." Please clarify this scaling approach to improve reproducibility. 

Section 2.3 is conceptually clear but not sufficiently detailed for full reproducibility. For example, grid resolution, ridge identification algorithm, and transition-line fitting are not sufficiently specified to allow full reproducibility of the orthogonal distance metric.

Section 3.2 discusses the individual POx isopleths. However, the authors may consider adding a brief comparative discussion of regime differences across cities and times of day, as this could further strengthen the interpretation

The FSS model and its setup should be included in the methodology section.

The authors state that the box model is constrained using meteorological variables and photolysis rates. Please clarify the source of these parameters (e.g., in situ aircraft measurements, radiative transfer calculations, or model-derived values), and briefly describe how they were implemented in the box model and potentially the bias associated with this.

The manuscript would also benefit from a brief discussion of how uncertainties in observed NOx, VOCs, and photolysis rates propagate into POx estimates and regime classification, particularly near the transition line.

Comments to Authors:

In their manuscript “Insights on Ozone Formation Sensitivity in Southeast and East Asian Megacities during ASIA-AQ”, authors characterized ozone chemistry with a box model constrained by airborne measurements from four Asian megacities during ASIA-AQ. The study is on a topic of relevance and general interest to the readers of ACP. Methodologically, studying ozone chemistry via observation-constrained box models is well-established and not new. Yet the flight campaign data in the region of study is scarce and valuable, and the analyses over the four megacities are carried out comprehensively. After the following comments are addressed, it shall be accepted.

Specific comments:

1. In Introduction, Line 65-75, after discussing NOx- and VOC-sensitive regimes, please consider adding a few sentences about the “transitional regime” because ozone formation is not either or, and more studies in recent years reveal that the formation regime at local scale could shift within a day, modulating peak ozone formation rates (Mazzuca et al., 2016; Guo et al., 2021; Tan et al., 2024; Stockwell et al., 2025). Such context will facilitate your point that “...nonlinearity makes it more difficult to navigate and inform the direction of emission reduction strategies” and better pave the road for the subsequent discussions in Section 4.  

-Mazzuca et al., 2016 (https://doi.org/10.5194/acp-16-14463-2016)

-Guo et al., 2021 (https://doi.org/10.1016/j.atmosenv.2021.118624)

-Tan et al., 2024 (https://doi.org/10.1016/j.scib.2018.07.001)

-Stockwell et al., 2025 (https://doi.org/10.5194/acp-25-1121-2025)

2. In Methods, Line 106-110, please consider adding more contexts about the early ozone season of East/Southeast Asian for the months of February and March. What are the knowns and unknowns from the existing literature? On the other hand, despite earlier understanding that the summer monsoon of Southeast Asia could alleviate local air pollution, recent studies identified summer ozone episodes in the region as well, especially across South China and transported to Southeast Asia (Zhou et al., 2025). Please briefly justify the 1) scientific logic behind the timing of your campaign, 2) key questions it targeted in the scope of ozone chemistry, and 3) its limitations and caveats (e.g. how representative is the winter ozone formation regime from an annual perspective?), so that the broader audience who are not familiar with the region could have a clearer picture. If deemed necessary, please consider moving a portion of this description to the Introduction.

-Zhou et al., 2025 (https://doi.org/10.1021/acs.est.5c10258)

3. In Results, Section 3.2, isopleths of POx across a varying range of NOx and VOC levels are used to show the sensitivity regimes of ozone formations in each area. Yet your criteria of “high production rates” is not consistent across areas (>40 ppbv/hr for MM in Line 249, >20 ppbv/hr for BMR in Line 280, >15 ppbv/hr for TKMA in Line 303, and not explicitly written out for SMA). It is even more confusing when you summarize the fractions into Table 1. The note “a” of the table specifies that “High POx denotes upper 50% in the POx distribution (above the median)” which seems again inconsistent with your text descriptions. From your Figure 4 for example, the color scale is around 0-50 ppbv/hr. Clearly your median POx in MM cannot be 40 ppbv/hr. Please revise and provide a less arbitrary criteria for area-by-area interpretation and intercomparison. 

4. Same issue for NOx and VOCs, for example, your Line 303 describes TKMA at “moderate NOx (4-10 ppbv) and “moderate VOCs (> 40 ppbv)” but Line 280 calls BMR under “relatively low NOx (7-18 ppbv)” and “moderate-to-high VOC (> 40 ppbv)”. Please revise and make them consistent for interpretation. 

Technical corrections:

1. In Abstract, Line 43-47, “In contrast, Seoul, under colder and low solar irradiance conditions, exhibited a primarily VOC-sensitive regime…” is confusing. Even though Seoul is in a higher latitude compared to the other three areas, it is not necessarily the determining factor of its ozone formation regime (or at least not shown in the data analysis). The current description is prone to be mistaken as drawing connections between lower temperature & solar irradiance and the VOC-sensitive regime, which is not the case. SMA’s VOC-sensitive regime could be simply due to its highest ground-level NOx as shown in your Figure 2. Please rephrase.

2. Somewhere in the Methods/Results, please make it clear that your VOCR represents non-methane VOCs (NMVOC) because your Table S2 contains CH4.

3. Somewhere in the manuscript, please make it clear that your 0-D box model and the subsequent result analysis assumed all measured O3 are secondary and formed from your co-measured precursors. In reality, transboundary vertical transport and regional transport could modulate your observed O3 greatly. Detailed wind analysis coupled with night-time surface background O3 analysis shall be preferred, but it might be well out of the scope of this manuscript.