This study develops global estimates of ozone production and its sensitivities using satellite observations from OMI and TROPOMI. The method is complicated, which involves box model, CTMs, observations from several field campaigns, synthetic data, satellite data etc. The authors provide a fairly detailed description of the methods, but it remains unclear how these new ozone production estimates advance our understanding of ozone chemistry. My detailed comments are provided below.

1. Title: The title begins with ‘Beyond HCHO/NO2’, which is confusing. What does the term ‘Beyond’ mean here? How is your study relevant to HCHO/NO2 From the title, one would expect that satellite HCHO/NO2 ratios are central to the analysis, but that does not appear to be the case after reading the manuscript. I’d recommend remove ‘Beyond HCHO/NO2’. A novelty of this study (comparing with Souri 2025) is the use of neural network model, and it should be emphasized in the title.
2. For the abstract, the opening should clearly define the scientific question being addressed, rather than starting with the discussion of the FNR, which is not the main focus of this study. My understanding is that this work aims to derive PO3 from a DNN model, which is different from the indicator ratio or FNR approach. The repeated references to FNR throughout the abstract are confusing and should be reconsidered.
3. This study appears to be a follow-up study of Souri et al. 2025 with some technical improvements, such as use of DNN. While the technical enhancements are clear, the added scientific value is not. It is unclear how the improved PO3 estimates advance our understanding of ozone formation processes. Many figures, including the spatial maps and seasonal variations, are quite similar to those presented in Souri et al. (2025). The main difference seems to be the extension of the study period from one year to multiple years (2005–2023), but only two regional case studies are analyzed for long-term trends. I suggest expanding the long-term trend analysis globally to better demonstrate the added value of this extended dataset.
4. It is unclear to me why a satellite-based PO3 product is needed. PO3 is essentially a “modeled” quantity, which is not directly observable. There is no way to evaluate the robustness of PO3 estimates. The magnitude of PO3 can vary depending on how you define the PO3, whether it’s accumulative production or instantaneous production. It seems that the authors are looking into net production of O3, but it is not clear how the chemical loss of O3 is defined, and how the uncertainties of chemical loss terms would influence the magnitude of PO3.
5. The authors claim that photolysis rates and water vapor have large influence on PO3. However, their calculations of these quantities appear oversimplified. It is unclear how cloud and aerosol effects on photolysis are accounted for. Water vapor and total ozone columns are taken from MINDS simulations, even though satellite-based observations for these variables are available. It is not clear why satellite data are only used for NO2 and HCHO but not for other relevant parameters. This inconsistency needs to be addressed.
6. The authors demonstrate the use of PO3 through some case studies, but these studies are somewhat disconnected. Each focuses on a different region and time period (e.g., northeastern U.S., Middle East, Los Angeles, Tehran), resulting in a fragmented narrative that feels like a collection of isolated examples. I recommend reorganizing these sections to tell a more cohesive scientific story. The analysis of long-term trends is promising. Expanding this analysis to the global scale, and examining how ozone production sensitivities have evolved over time, would substantially strengthen the manuscript.
7. The DNN model is trained using F0AM-simulated data. Although the model shows reasonable performance, the derived relationships remain model-dependent and limited by the diversity of available field campaigns. Rather than randomly withholding data for testing, it would be more informative to exclude one or two entire field campaigns from training and test whether the DNN performs well out-of-sample. This approach would better demonstrate the model’s robustness and generalizability.

Specific comments:

1. Line 155: Unclear what the offset and slope mean.
2. Line 167: Why different cloud fraction thresholds are applied to NO2 vs. HCHO.
3. Line 401: The assumption stated here seems questionable. MINDS-simulated water vapor and photolysis rates carry uncertainties, the influence of clouds and aerosols is not accounted for. These sources of uncertainty should be incorporated into the error analysis.
4. Figure 6: While the absolute PO3 values vary between bright and dim conditions, the spatial patterns (e.g., the ridgeline) appear consistent? It would be helpful to label the ridgeline across all panels.
5. Figure 8: I’m having a hard time interpreting the sensitivity terms. What exactly do these sensitivities represent? Given that the magnitudes of photolysis rate, HCHO, and NO2 differ substantially, and that ozone chemistry is highly nonlinear, are these sensitivities additive?
6. Figure 8: The higher sensitivity of PO3 to HCHO in summer does not necessarily imply stronger sensitivity to VOC emissions. This may simply reflect the shared temperature dependence of PO3 and HCHO. In CTMs, ozone sensitivity is typically analyzed with respect to VOC emissions, whereas HCHO is an intermediate oxidation product rather than a primary species. The production of HCHO varies with VOC speciation, NOx levels and temperature.

The manuscript presents a new global dataset of net ozone production rates (PO3) derived from a neural network framework constrained by satellite observations. The authors develop a deep neural network (DNN) model trained with simulations from the F0AM box model and aircraft measurements with perturbations. The DNN employs as input a set of geophysical parameters derived from multiple sources, including satellite retrievals of HCHO and NO2 (from OMI for 2005–2019 and TROPOMI for 2018–2023), as well as parameters from the MINDS model. The MINDS framework provides the conversion factors from total column to planetary boundary layer (PBL) mixing ratios for HCHO and NO2, simulated O3, and water vapor (H2O).

The authors validate their DNN-derived PO3 product (termed PO3DNN) against the empirical formulation described in Souri et al. (2025). The manuscript further examines several applications: (i) the intercomparison of OMI- and TROPOMI-based products for 2019, (ii) regional PO3 seasonality (2005–2007) across selected sites worldwide, (iii) a heatwave case study over the northeastern United States (August 2007), (iv) seasonal and spatial patterns over the Middle East (2019), and (v) long-term PO3 trends from 2005–2019 in Los Angeles and Tehran.

Comprehensive uncertainty estimates are presented, including both systematic and random errors, with the dominant source attributed to the column-to-PBL conversion factors from MINDS. The total relative errors are reported to range from about 25% in polluted regions to more than 200% in remote areas.

The manuscript is scientifically interesting and presents a valuable global dataset of ozone production rates derived from satellite observations. However, several key methodological and interpretational issues need to be clarified and better quantified before the study can be fully evaluated. Therefore, I consider the following as major comments.

Major Comments

1. Time period, harmonization, and trend (2005–2023)
   
   The title suggests that the study spans the full period of 2005–2023, implying a continuous long-term trend analysis that combines OMI and TROPOMI data. However, the actual trend analysis uses only OMI data (2005–2019), while TROPOMI is primarily used for 2019 onward and inter-satellite comparison. The manuscript should clarify how the two products were harmonized for consistency and provide quantitative evidence of their agreement or bias (for example, regional mean differences, temporal overlap). It would also strengthen the study to explicitly show the magnitude and spatial or temporal characteristics of any applied corrections and to quantify how harmonization affects the derived PO3 trends (for example, OMI-only vs. TROPOMI-only vs. combined). Finally, please discuss whether a unified 2005–2023 trend is feasible and what systematic offsets might influence its interpretation.

2. Bias correction using MAX-DOAS
   
   The bias correction procedure for OMI and TROPOMI retrievals using MAX-DOAS observations needs more detail. Were corrections applied globally or regionally, and are they time dependent? How large were the typical corrections? The error treatment also appears simplified for bias correction and may underestimate correlated uncertainties.

3. Comparison with FNR
   
   The authors argue that the PO3 framework provides more detailed and continuous information on ozone production and sensitivity than the traditional formaldehyde-nitrogen ratio (FNR). I agree with this conceptual advantage. However, the manuscript does not clearly demonstrate how much additional information PO3 offers beyond FNR in a quantitative or diagnostic sense. It would strengthen the paper if the authors could illustrate specific cases or regions where PO3 reveals gradients or features that are not captured by FNR-based classifications.
   
   The manuscript also describes FNRs as "binary," but it would be more accurate to say that the interpretation of FNRs is often binary, based on thresholding between VOC-limited and NOx-limited regimes, while the FNR values themselves are continuous. Clarifying this distinction would help avoid oversimplifying the FNR framework.
   
   Finally, the description of Figure 14 qualitatively compares the spatial patterns of PO3 sensitivities to HCHO and NO2. This section could be improved by quantifying those relationships, for example by providing correlation or regression metrics between PO3 sensitivities and FNRs, or by showing how the two indicators diverge under different chemical conditions (for example, high-HCHO/low-NO2 versus low-HCHO/high-NO2). Such quantitative comparisons would make the claimed improvement of the PO3 framework more convincing and scientifically interpretable.

4. Conversion factor and averaging kernel
   
   It is unclear whether satellite averaging kernels were applied when deriving the column-to-PBL conversion factors using MINDS. If they were applied, please specify how; if not, discuss the potential influence on near-surface concentrations and the resulting PO3 estimates.

Minor Comments

It would be helpful to clarify whether H2O values are directly inherited from MERRA-2 or modified within the MINDS model.

The description of “Southeast Asia” may be misleading; the text refers to August–September biomass burning, which applies mainly to maritime Southeast Asia, while continental Southeast Asia (Thailand, Myanmar, Laos, Cambodia) experiences its peak burning during February–April. Please clarify the regional definition.

The expression “SZA acquired from the satellite L2 products” could be misleading, since SZA is not directly observed but computed from geometry information. Suggest rephrasing to “SZA derived from the geometry information in the L2 products.”

Check typographical errors (for example, “trend trends” to “trends”; “Tehan” to “Tehran”).

The phrase “textbook example of non-linear chemistry” could be softened to “a clear demonstration of non-linear ozone chemistry.”