Comments to Authors:

In their manuscript “Multi-decadal ozone air quality and the role of temperature in Switzerland during summertime”, authors investigated changes in summertime ozone and its relationship with temperature from 12 national stations in Switzerland over the past two decades. Decreases in precursor levels have positively affected ozone in remote locations, while ozone is increasing close to busy roads. The ozone formation regime is becoming more NOx-sensitive, and high ozone is associated with hot days. The study is on a topic of relevance and general interest to the readers of ACP. Yet from an ozone chemistry perspective, the findings are not new. Methodologically, the exclusion of any VOC measurement, the omission of ozone production efficiency (OPE) discussion, the lack of quantitative analysis for NOx-temperature dependence discussion and titration discussion, plus correlating trends in ozone with only one key parameter (temperature) is insufficient to reveal photochemical mechanisms that control ozone levels (Line 100). Therefore, I recommend a major revision and am open to review the manuscript again if needed.

Specific comments:

1. Line 63-75, while I agree the “weekend effect” can be used to qualitatively speculate ozone formation regime, there exists varied quantitative methods to categorize the NOx-sensitive, VOC-sensitive, or transitional regimes based on direct measurement of radicals, or measurement of precursors gases + chemical modeling, or remote sensing of column HCHO/NO2. Given the NABEL network measures ozone, its precursors, and meteorology comprehensively, I am not sure why more quantitative metrics were not adopted in this study. From Line 124-125, it is understandable that VOCs are not always available for all 12 sites. But are they available in a few representative sites (at least one in each of your categories: traffic, (sub)urban, rural, and background) that could be utilized to validate your results/facilitate the discussions in Section 3.2? Diving into the mechanisms of ozone chemistry and its transitioning (Line 224-235) without the inclusion of any VOC measurement or estimation is concerning. 
2. Section 3.3.1 and Figure 5: I am not sure the uniform T>30C is a fair criteria for all sites. As you pointed out, the background sites are at higher elevation and therefore lower temperature and negligible exceedances. I may suggest considering using T>[a nominal percentile of the annual average T] as the more appropriate criteria to filter high temperature days for each site category. This may change your representation of Figure 5b and corresponding discussions. Currently, I am unable to retrieve much useful information from Figure 5b, because 1) the points are looking very scattered- I am not sure how robust is the r-square of that positive slope, 2) it is lumped from all sites, while all other discussions/figures throughout your manuscript are categorized into sites.
3. Section 3.3.2 and Figure 6: per Line 264-265, “Figure 6 presents the relationship between (a) NOx, (b) O3, (c) Ox and (d) the share of O3 in Ox with temperature, which all exhibit strong correlations.” Would you please clarify if the data points here are from all years? If that is the case, NOx went down (due to combustion control) and temperature went up (due to climate change) over years. They will inherently show a negative correlation, right? This correlation could be entirely physical and has nothing to do with chemistry. Therefore, I am not convinced with the interpretation from Figure 6a that higher temperatures drive a lower NOx or the temperature dependence of NOx emissions (Line 268-289). I suggest additional analysis (e.g. multivariate regression) to really distinguish the temperature impact from other confounding factors to validate the corresponding conclusion. Moreover, for the BLH discussions around Line 300, it reads speculative. Even without direct BLH measurement, your dilution theory should be validated using any gas/particle species co-measured at the NABEL that has a lifetime >> NOx.   
4. Throughout the manuscript, ozone "titration" is repeatedly mentioned. However, in both the manuscript and SI, I am unable to identify any quantitative analysis that showed the actual titration effect. Given the main dataset for the analysis focused on summer daytime, I am not convinced of the importance of the titration effect on explaining many observations. From my limited experience, titration usually happens at night-time or early morning, when NO persists (no photolysis) and the boundary layer is shallow. But during daytime, especially between 9:00-18:00 local time in summer as the author stated, NO emitted to the troposphere should theoretically be rapidly converted to NO2 by ROx and HOx within minutes, orders of magnitude faster than NO + O3 titration reaction. But I am no expert on the atmospheric condition in Switzerland. Since you do have simultaneous NO, NO2, and O3 measurements, why not plot the diurnal average of O3 and NO at each site (or categories of lumped sites) to see if NO increases at traffic hours, does ozone drop? If that anti-correlation is obvious and universal across the traffic sites, then you can attribute some of your findings to titration. If O3 remains high even at rush hours, then titration is negligible. You could also try plotting the daytime vs. nighttime O3/NO ratio, as the nighttime titration should be obvious.  

Technical corrections:

1. Around Line 50, discussion in Pusede et al. (2015) is an estimation of PO3 as a function of NOx and VOCR in a typical U.S. city under 2015 emissions, and the EKMA figure itself is a steady-state simplification. It is classic and important, but since then, more comprehensive field observation-based modeling studies in populated areas around the world have shown that peak ozone formation did not necessarily happen during the transitional regime but rather highly localized. They can occur well within the NOx- or VOC-sensitive regime:

- Peak PO3 in VOC-sensitive regime: Los Angeles, CA, U.S.: Stockwell et al., 2025 (https://doi.org/10.5194/acp-25-1121-2025).  

- Peak PO3 in NOx-sensitive regime: San Antonio, TX, U.S.: Guo et al., 2020 (https://doi.org/10.1016/j.atmosenv.2021.118624).

-  Peak PO3 in VOC- and NOx-sensitive regime in the morning and afternoon respectively, but not the transitional regime in between: Houston, TX, U.S.: Mazzuca et al., 2016 (https://doi.org/10.5194/acp-16-14463-2016). 

- Peak PO3 in NOx-sensitive regime: North China Plain, China: Tan et al., 2024 (https://doi.org/10.1016/j.scib.2018.07.001). 

I recommend incorporating these studies in the introduction and revise the corresponding lines.

2. Section 3.3.2, Line 265, do you mean “data points above 10 and below 35C” instead?

3. I see no where that ozone production efficiency (OPE) was mentioned, which is modulated by both precursor levels and meteorological conditions (jNO2, temperature, cloud coverage, etc.). With NOx and O3 measurement but without NOy, it won’t be easy to use the regression method to calculate OPE. But it should be considered in the discussion, because when the NOx went down and T went up, the OPE could increase and lead to more rapid ozone production (more propagation cycles) as shown in:

- Kleinman et al., 2002 (https://doi.org/10.1029/2002JD002529) 

- Chace et al., 2025 (https://pubs.acs.org/doi/10.1021/acs.est.5c02073)

And also in those referred literature above. It won’t change the main conclusion of your study so I listed it in technical corrections. But it is important to be incorporated and might facilitate some of your discussions (e.g. around Line 365, Line 380, Line 410, and else where).

In this work, approximately two decades of oxidant measurements from a network of ground sites across Switzerland are analyzed to better understand the state of ozone formation chemistry across the region. Although the data streams are relatively simple, the analysis appears thorough and the analytical approach with respect to characterizing mechanistic sensitivities is appropriate for the target journal. This work is of clear importance in advancing the state of knowledge of air quality drivers in Switzerland and has broader implications for advancing the field of ozone and NOx chemistry characterization from ground-based measurements. I particularly commend the authors for a very clearly communicated and easy to follow manuscript which was a real pleasure to read. I believe that this work will be appropriate for publication once the following comments have been addressed:

General Comments:

Some societal and historical phenomena which have great potential significance for analyses here described, specifically those related to traffic patterns, are not sufficiently addressed and should be considered (similarly to relevant phenomena around fuel standards and events such as Dieselgate, which are well discussed). Specifically, I request that the authors discuss changing work patterns (specifically increases in hybrid and remote work), which could be contributing significantly to changes in the weekend vs weekday phenomena here discussed. Is there available traffic data to demonstrate that the relative week day vs weekend number of vehicles on the road has remained constant? I would also request that the authors specifically address the COVID-19 pandemic and related changes in economic activity, which have been extensively studied as significant perturbations of normal traffic and emissions patterns across the world. I do not have sufficient local knowledge to comment on how policies may have impacted the regions in question, but the possibility of a perturbation should be acknowledged and assessed even if there is evidence that it was negligible and therefore ruled out.

I would also request that the authors comment, even if briefly, on continuity and quality assurance related to drift corrections in the main text of the paper, as any potential instrument drifts or instrument changes over such a long stretch of time would have significant potential to bias results.

Line 112: please clarify what differentiates the background sites from the rural sites, as the current background definition states that the sites are rural? Is this low elevation rural sites vs high elevation rural sites? If so why was this differentiation selected?

Line 118: Can you please comment on the potential interferences of VOC cross sensitivity for the UV-absorption method of ozone measurement? How were these either determined to be negligible or corrected for?

Line 303: Please add additional evidence for the assertion that boundary layer height variability is minimized in the selected time area such that dilution is not the most likely explanation for the observed temperature effect on NOx.  I understand the argument around hours after sunrise, but I would appreciate additional analysis to support ~2 hours after sunrise being sufficient to reduce the importance of this effect given the significant lag between light, and temperature and BLH and the importance of surface temperature in driving BLH dynamics.