This manuscript investigates the trends of warm-season surface ozone in a polluted region of China: The Middle and Lower Yangtze River Plain (MLYRP), during 2017-2022. The authors highlight a decrease in the monthly 98^th percentile of hourly ozone concentrations, contrasting with a slight increase in the monthly 2^nd percentile. They argue that the changes in anthropogenic emissions, particularly reductions in anthropogenic NO_x emissions, are the main driver of these opposing trends. However, I found their analysis insufficient to support their conclusion. Also, the entire paper reads like a patchwork of different modules (numerous analyses were conducted) but lacks coherence. Many of the analyses are unrelated to the paper’s focus. Additionally, the authors incorrectly use some terms and cite references improperly. Conflicts among their figures raise further concerns about the quality of the work. The manuscript requires substantial revision to ensure a high-quality analysis that meets ACP standards. Furthermore, significant improvements in language and presentation are necessary. Therefore, I cannot support the publication of the manuscript in ACP.

General comments:

1. It’s hard for me to identify the main topic of this paper. While the primary focus appears to be explaining the opposing trends in the 98th and 2nd percentiles of ozone in the MLYRP (part of eastern China), the paper includes many other analyses that are irrelevant to this topic. For instance, Section 3.4 (Interannual differences in surface O₃ formation sensitivity) and Section 3.6 (Key meteorological and anthropogenic factors inducing O₃ pollution) should be removed (they haven’t found anything new in these sections either). The entire paper should be reframed. Additionally, Section 3.5 presents the same analysis and draws the same conclusions as Sections 3.1-3.3 but for a larger area (eastern China). The inclusion of Section 3.5 seems redundant. Why don’t the authors focus on eastern China throughout the manuscript?
2. To understand the drivers of ozone trends, the authors use Multiple Linear Regression (MLR) to separate meteorological influences. There are several issues with their analysis: (a) The predicted variable, O₃ concentration, should also be normalized in the MLR. Normalizing Y first would eliminate the need for natural background O₃ in equation (2). (b) Line 27, Page 6, the statement that O₃ from natural sources is stable is incorrect. Biogenic VOCs and soil NO_x emissions are highly sensitive to temperature. (c) Lines 19-21, 23-24, Page 10, the authors seem to confuse the terms “interannual fluctuation” and “trend.” The trend observed is actually a low-frequency signal after removing the high-frequency signals (interannual fluctuation). In this part, it is only acceptable to conclude that the anthropogenic component drives the trend, but it is apparent that meteorological parameters dominate the interannual fluctuation (as it roughly reproduces the peaks and troughs). All of this needs to be corrected.
3. The authors conclude that the continuous NO_x reduction during 2017-2022 is the reason for the differences in tendencies in the O₃ 98^th and 2^nd percentile trends. However, if you look carefully at Figure 5, which presents the anthropogenic impact for each year on the 98^th and 2^nd percentile trends, respectively, you will find that the anthropogenic impact shows a similar pattern for both trends until mid-2021. It appears that something that occurred after 2021 is the main reason for the divergence. More investigation is clearly needed. Also, how is this opposing trend sensitive to the period studied?
4. The authors have not directly answered why the 2^nd percentile O₃ increased over 2017-2022. The 2^nd percentile should be related to nighttime O₃, while the entire manuscript discusses the O₃ photochemical formation regime, which is a daytime indicator. More investigation is needed on the nighttime process, such as NO titration of O₃, loss of O₃ with VOCs, etc.
5. In Section 3.4, although this section should be removed according to my comment #1, conflicts between Figure 9 and Figure S9 are noted. The area proportions presented in Figure 9 are not consistent with the spatial patterns in Figure S9. For example, Figure 9d suggests a NO_x-limited region up to 75% of the total MLYRP in August of 2022, while Figure S9 shows a NO_x-limited area smaller than the VOC-limited area. Please check your analysis.

Specific comments:

1. Section 2.3, could the authors elaborate more on how trustworthy is the TROPOMI O₃ profile retrieval?
2. Lines 20-22, Page 8, could the authors say more about why 5^th, 50^th, and 95^th could represent background, typical, and polluted conditions.
3. Lines 5-6, Page 12: Why is the primary HCHO contribution much higher than the secondary HCHO at these sites, differing from previous findings cited in the paper? Please provide some explanation.

Technical corrections:

1. Replace “unbalanced emission reduction in ozone precursors” with NO_x reduction throughout the text?
2. Replace “unbalanced emission reduction in ozone precursors” with NO_x reduction throughout the text?
3. Line 28, Page 1, remove “experiment”.
4. Line 25, Page 2, Zhai et al. (2019) is a PM₅ study, not ozone study. Please remove. Also in Line 3, Page 4.
5. Line 5, Page 3, it should be Li et al. (2020a).
6. Line 22, Page 3, it should be “diagnose”.
7. Line 24, Page 8, do not use “one-sided understanding”.
8. In Figure 5, the authors seem to fit the observed monthly O₃ and use the fitted lines to connect monthly values. Please replace these with straight lines directly connecting the dots.
9. References, journal names should be included.

The work by Wang et al. investigated the factors driving surface ozone increase over eastern China by combining ground measurements and satellite retrievals. The results show that surface peak ozone concentrations have decreased while the low ozone concentrations showed an increasing trend during ozone season between 2017-2022. Ozone sensitivity regimes are analyzed for the targeted cities based on MAX-DOAS measurements. The work concludes that the opposite trends of peak and low ozone concentrations are mainly attributed to the combined effect of significant emission reductions of NO_x and continuously emission increase of VOCs. The figures are well prepared, and the analyses are relatively sound based on the results. I would also recommend authors polishing English throughout the paper to make it clearer for readers. My major concerns are 1) how to interpret the variations of low ozone concentrations / background ozone for the targeted region as it’s surrounded by polluted areas, and 2) how to identify the ozone formation sensitivity based on FNR (ratio of formaldehyde and NOx).

My detailed comments are listed below.

1. Page 1, Line 27: in the main text, you mainly work on “HRB”, instead of the whole eastern China. Maybe specifying HRB, instead of eastern China makes more sense.
2. Page 1, Line 29: can you elaborate more on the “typical” ozone concentrations?
3. Page 1, Line 31: please rephrase the sentence. “Anthropogenic emissions” is not the “cause” of the ozone trends, maybe “driving force” is better.
4. Page 2, Line 3: change “on spatial scales” to “spatially”.
5. Page 3, Line 5: duplicate reference of Li et al., 2020a
6. Page 5, line 18: have you applied consistent AMF (air mass factor) between MAX-DOAS and TROPOMI for NO2 VCDs?
7. Page 5, Line 21: why the differences of sensitivity peaks between TROPOMI and MAX-DOAS lead to different HCHO VCD retrievals?
8. Page 5, Line 24-26: so, what’s the conclusion? Are MAX-DOAS data not reliable compared to MEE, as the correlation coefficients are not that high (0.66~0.74)? Please specify it.
9. Page 6, line 27: this is not true for summer, as VOCs can be dominated by biogenic sources.
10. Page 6, Line 28: how about transport from surrounding areas? Especially in HRB, the transport cannot be neglected as it’s surrounded by the YRD and Jing-Jin-Ji regions. Please elaborate more.
11. Page 7, Line 7: so, the perturbations of background ozone are neglected when considering the observed O3 anomalies. It’s not true as transport can contribute to this term.
12. Page 8, Line 2: HRB is surrounded by very polluted area, and it can be affected by pollution transport. It's hard to define "background" here, and the background concentrations can change interannually.
13. Page 10, line 5: how about the variations in the background?
14. Page 10, line 28: do you include nighttime O3 data in the MLR model? Why?
15. Page 11, Line 2: “(0.108 ppb/year, +114%)”, what’s this for?
16. Page 11, line 27-28: This is weird. When Sno2 is much larger than Shcho (low FNR), it should be VOC-limited, instead of NOx-limited.
17. Figure 6: How do you calculate the slope of the ratio of O3 to Sno2, and the slope of the ratio of O3 to Shcho? Are you using the ground measurements for all years? Does each point represent the fitted slope each day? I’m curious the temporal intervals between datapoints shown here.
18. Figure 6: I’m curious will the FNR threshold change year by year based on this methodology? How will the interannual variation of the threshold affect your analyses? Please elaborate more.