This manuscript focuses on identifying global surface ozone formation regimes and their long-term trends. The authors use satellite observations of HCHO/NO₂ ratio, together with ground-based ozone observations, to determine whether a region is NOx-limited, VOC-limited, or in a transitional regime. The main findings are (1) The HCHO/NO₂ ratio can be linked to the ozone weekend-weekday effect (WE-WD). (2) Satellite and surface observations indicate similar long-term changes in regimes across different continents. (3) There has been a global transition from a VOC-limited regime toward a NOₓ-limited regime, and most urban areas remain VOC-limited.

This study is valuable in demonstrating the effectiveness of this satellite indicator by linking it to the surface WE-WD ozone effect and identifying long-term trends in global ozone chemical regimes. However, I find the paper not well organized, with some sections being repetitive and the analysis lacking depth. Therefore, this manuscript requires thorough editing before being considered for acceptance in ACP.

Major issues:

1. In Section 3.1, the authors define HCHO/NO2 thresholds at each site and find large spatial variability across regions. However, in their later analysis, they use a uniform threshold everywhere, which could lead to misidentification of regimes. An example of potential misidentification: in the last section (Line 450), where they conclude that, unlike other places, the southeastern US has entered an NOₓ-limited regime. However, this could simply be because this region requires a higher threshold than 3.5 (as shown in Figure 3a). I would recommend using at least region-specific thresholds, as derived in Figure 3c.
2. The analysis should be more in depth. The authors provide little interpretation of (1) the large regional variability in the HCHO/NO₂ threshold (e.g., what are the key driving factors, and why is the threshold in East China much lower than in other countries), and (2) the drivers of changes in HCHO, NO₂, and the HCHO/NO₂ ratio outside of East Asia and the US, including Europe, India, Australia, Africa, and South America (e.g., why is the HCHO/NO₂ trend in Africa significantly positive). This lack of discussion makes it seem as though the authors are only familiar with the background and policies of East Asia and the US, despite the study's intended focus on global changes.
3. The paper could be more concise and better organized. (1) Similar interpretations of trends in HCHO/NO₂ and the WE/WD effect for East Asia and US appear repeatedly without deeper insight. These discussions could be condensed and analyzed within a single section. (2) The purpose of Table 1 and Figure 7 is unclear and somehow very confusing. Figure 8, which presents regional time series of HCHO/NO₂, already conveys the information clearly.
4. The free-tropospheric (background) contribution to the satellite-observed NO₂ columns is increasingly important, especially in the US and Europe, where surface emissions have declined continuously. Could this alter the threshold (should the threshold remain fixed over time?), given the reduced representativeness of the column for surface conditions due to NO_x reduction? Additionally, please consider discussing how background interference might affect the results.

Minor comments:

1. Section 2.1, this harmonized GOME, SCIAMACHY, OMI, and TROPOMI product should be better described, including how biases across different platforms are addressed.
2. Line 97-99, what do you mean by “using the same a priori profile”? Does the TM5-MP provide a priori shape factors for all instruments, and does its emission input change annually/monthly?
3. Figure 4, the presence of many discrete low values over Inner Mongolia in East Asia seems unreasonable. Could this be an issue with satellite observations, or is there another possible explanation?
4. Line 23, “WHO” should be capitalized.
5. Line 275, there is no label of “a” in Figure S3.
6. Line 285-286, please provide references to support this statement.

General Comments

The article presents a novel approach to inferring ozone formation sensitivity on a global scale. The authors combine two widely used indicators—the ozone weekend effect (WE-WD O₃) and the formaldehyde-to-nitrogen dioxide ratio (HCHO/NO₂)—to determine regime thresholds. By correlating these variables and applying linear regression, the HCHO/NO₂ threshold for regime transition is identified as the point where WE-WD O₃ shifts from positive to negative values. The study includes an extensive trend analysis and trend reversal evaluation, ultimately establishing a global threshold of 3.5, with regional variations. This approach makes a valuable contribution to ozone mitigation strategies by providing a framework for more precise regime classification on a global scale. I suggest several revisions and clarifications before the paper can be considered for publication in Atmospheric Chemistry and Physics.

Specific Comments

1.  Given the nonlinear nature of O₃ formation due to complex VOC-NOₓ interactions, comparing linear and nonlinear models would help justify the choice of linear regression for deriving regime threshold values.
2.  A gradual transition between VOC-limited and NOₓ-limited regimes is expected rather than an abrupt shift at a single point. Could nonlinear regression methods better capture this transition?
3.  The long-term trend and trend reversal analyses rely on datasets with different spatial and temporal resolutions and measurement times. Although the datasets were harmonized, these differences may introduce biases in the observed trends and reversals. Were any considerations made to assess these biases?
4.  The method used for trend and trend reversal evaluations assumes that trends are linear within 5-year windows and does not account for seasonality. Complementary statistical methods, such as seasonal-trend decomposition, could help verify the detected trends and reversals.
5. Providing more details on the methodology for linking satellite and ground-based observations would improve clarity. Specifically, was the monthly WE-WD O₃ value calculated using all available hourly O₃ observations? Additionally, were all ground monitoring stations within a 0.25° grid included in computing the WE-WD O₃ averages before pairing with HCHO/NO₂ data?
6.  Although Figure 2 covers 2004–2022, some sites (e.g., Las Vegas, Los Angeles) have a higher number of data points. What explains these differences? Additionally, including the R² value would help assess the regression fit. Clarifying the criteria for selecting the nine representative urban areas would also be recommended.
7.  Line 205. A discussion on the reasons behind the large spatial variability of threshold values would strengthen the analysis.
8.  Line 247. The methods indicate that trends were calculated using the Mann-Kendall test and Theil-Sen estimator, not linear regression.
9.  Line 277. The decline in HCHO/NO₂ is attributed to NOₓ reductions, but this interpretation appears counterintuitive.
10. Line 383. The identification of a single transition year for ozone sensitivity regimes seems somewhat ambiguous, given the temporal and spatial variability of regime classification thresholds, which may have also evolved over time. Focusing on trend changes rather than a specific transition year would provide a more robust interpretation.