This study explores how changing anthropogenic emissions have impacts the O3 sensitivity to temperature from 1990 to 2021 in the United States. The observations demonstrate a diminishing sensitivity, and the authors use GEOS-Chem model simulations to show this is due to decreasing anthropogenic NOx emissions, and that both the direct O3-T mechanisms and indirect (non-T meteorological) factors contribute to this. The study is a very nice example of using a model to interpret an observed result. The study is thorough and well-explained and was a pleasure to read. There are three topics that should be better addressed in the text prior to publication:

1. A central result of this study is that the model can only reproduce less than half (42%) of the observed trend in the O3-T relationship. The paper attributes the source of the trend in the model, but does not sufficiently discuss the possible reasons and implications of the model missing half of the trend. The authors suggest that biases in the MERRA-2 temperature dataset from 1995-1999 contributes to this, but they show that when excluding this part of the record, the model can still only capture 56% of the trend. On lines 304 & 309 they suggest that this is due to biases in the SWUS region, but neither the region nor the degree of bias seen in Figure 5a seem sufficient to explain the majority of the missing trend. If it is indeed due to the SWUS, the paper should (1) discuss why the model cannot capture this region and (2) show that the model can capture the trend without the SWUS and (3) proceed only with non-SWUS results. If the SWUS can only explain a small part of this model bias, then the paper should discuss what other factors could contribute to the model bias, how this could be further explored in future studies and/or how the model could be improved. The paper brings up the temperature impact on anthropogenic emissions on line 146 – how important might this factor be?
2. Line 155 suggests that the simulations have only been spun-up for one month; it’s also unclear what initial condition is used (i.e. consistent with what year of meteorology and emissions). The manuscript needs to justify that the short spin-up time does not impact the results and that the simulation is at steady-state with the emissions. The authors cite the short lifetime for O3 in the boundary layer (and longer aloft) (lines 155-157). However, given that they do not parse how much of the surface O3 in the simulations is locally produced vs transported (regionally, intercontinentally, from the stratosphere), and that one of the important temperature-sensitive drivers is PAN, the 1 month simulation spin-up is not necessarily sufficient. The authors should test this for the year of maximum difference from the initial conditions (i.e. if the initial condition is consistent with 1990 emissions, then perform this sensitivity simulation for 2021): a global simulation that is spun-up for 6 months prior to generating the boundary conditions for the July simulation (to verify that changing transport of ozone and ozone precursors do not impact the results). These results should be included in the SI to justify the approach used here, and, in the unfortunate case that the results are impacted by the spin-up time, the authors would need to perform longer spin-ups for all their simulations.
3. Figure 3a and associated text: Can the authors explain the dip and rebound in the O3-T relationship from 1996-2004? Is this trend present in all regions?

Minor Corrections

1. Line 94: “derive” seems inappropriate since the authors did not produce the MERRA2 product. I suggest “use” would be more accurate
2. Line 129: language “is capable of”
3. Line 151: “gas” should be plural
4. Line 180: language: replace “with both in” to “at both the”
5. Line 312: language: replace “propose by” with “theory using”
6. Line 314: language: “GEOS-Chem model simulates no”
7. Line 318: language: replace “neglectable” with “negligible”

• The CEDS inventory has some known biases in terms of agreement with observations. Of particular relevance for this study, previous work has found regional patterns in NOx biases, pointing overall to overestimates in the US (e.g. Christiansen et al., 2024 https://doi.org/10.5194/acp-24-4569-2024). Considering its importance to this study, it would be worth exploring previous work evaluating the CEDS inventory with respect to ozone precursors and commenting on how any biases or uncertainties may be influencing results shown here.
• The naming scheme for normalized cases confused me somewhat. For most cases it appears to identify the effect being normalized or removed (FTEMP normalizes temperature fields), but for FTRANS this appears to be the opposite, as all meteorology is normalized except for transport. Some clarification and consistency here would help for parsing later results.
• On a related note, it appears that a number of simulations listed in Table 1 are not explicitly mentioned or discussed in the manuscript text. If these simulations turned out to be used in developing manuscript figures and conclusions, it should be clearer how and where they were incorporated, with explicit case names cited for easier reference back to the table.
• While the details of transport effects are not a focal point of this paper, I found the description of transport impacts (lines 365-376) to be a bit thin and muddled relative to other sections, especially considering their apparent importance. Do BASE-TRANS and 1995E-TRANS refer to BASE-FTRANS and 1995E-FTRANS from Table 1? Why would solar radiation and BVOC emissions in the SE be relevant to the patterns shown in 7a, since (if I understand these cases correctly) all meteorology other than transport has been normalized out in the simulations being subtracted here? A bit more attention to these results, identification of possible mechanisms at play, and discussion within the context of the broader literature would be appreciated.

This manuscript re-visits earlier work of Porter and Heald (2019) and extends it to examine specific factors driving observed trends in local relationships between ozone and temperature. While the idea that ozone-temperature relationships are in part fueled by the availability of NOx is not new (Wu et al., 2008; Zanis et al., 2022), the advance here involves quantification of the impact of the known NOx reductions over recent decades in the USA to weakening the ozone-temperature relationship recorded at local monitoring sites. Quantifying the role of the selected individual ‘direct’ and a few ‘indirect’ processes as represented in the GEOS-Chem model to the changes in these relationships as shown in Figures 5, 6, 7 is a useful benchmark against which future work may gauge the importance of changes in these and other processes in the coming years as well as to compare to findings in other models.   

General Comments

GC1. The mean bias of the temperature fields is evaluated (line 100; Figure S1) but aren’t the trends in near-surface temperature over this period more relevant to the present study?  As it is, the mean biases could lead to errors in the ozone simulation as noted by Rasmussen et al. (2012).

GC2. The lateral boundary conditions used to drive the regional nested simulation should be described in a bit more detail.  Was this a continuous run, or was the global model also run for 1-month spinup and June plus July every 2 years?   

GC3.  The authors have missed some prior literature investigating how specific regional conditions shape relationships between ozone and specific meteorological variables such as temperature. Camalier et al. (2007) pointed out the weaker ozone-temperature relationship in the Southeast, which Tawfik and Steiner (2013) linked to differences in the coupling between the atmosphere and land (specifically soil moisture regimes) and suggest that surface drying is a more important predictor.  Furthermore, the strong ozone-temperature relationships in the northern part of the domain has been linked to dynamics associated with the mid-latitude jet (Barnes and Fiore, 2013) and meridional transport (Kerr et al., 2020; Zhang et al., 2022).  Some discussion of how the findings of this study fit in the context of those papers would be useful.

GC4. Uncertainties in the model and their implications for the conclusions could be discussed more clearly.  For example, the underlying assumption is that the model represents all important processes driving ozone-temperature relationships. The BB4CMIP emissions have spurious variations associated with the introduction of GFED emissions (satellite data) after 1997 (Fasullo et al., 2022), which might lead to problems for ozone trends in regions strongly influenced by fire. The dry deposition scheme only includes stomatal deposition variations with with meteorology (line 150) but non-stomatal pathways may also respond to temperature (Clifton et al., 2022). Why does the model miss the observed decline in the slope after 2010 in Figure 5b? Figure S7 suggests this is occurring in the SEUS and Midwest; some of the literature referenced may be helpful for additional context in interpreting the differences across regions from the perspective of the processes that dominate in different regions.

GC5. The focus on NYS in Section 3.4, while interesting, appears arbitrary.  What is the rationale for choosing this state?  Are the correlations between ozone and temperature particularly strong there?  The goal of Figure 9 is very interesting, but additional work would help strengthen the analysis.  What are the trends in the 0-10% temperature bin values as compared to the 90-100% bins? These are likely sampling very different meteorological conditions. How does the metric used in this figure compare to the linear fit between daily ozone and temperature? 

GC6.  The data availability statement regarding the model simulations, which are critical to the conclusions drawn in the paper, does not appear to align with current best practices in sharing data for open science.  Will the authors provide at least the datasets behind their figures, or a limited set of diagnostics from their simulations in a public repository to allow future studies to easily re-visit and extend their findings?

Specific comments

SC1. Line 12, line 67: In what applications are ozone-temperature relationships being used to predict the impacts of future climate change?   The overall weak correlations (Figure 2; Table S1; low r values indicate that even at best less than half the variance is captured) suggest this is not a very useful metric for prediction.  It seems relevant to compare the r-values for model versus observations too.

SC2. Lines 114-115: What type of linear regression method is used to quantify the trend? 

SC3. Lines 137-142.  The discussion of BDSNP is very confusing.  The scheme is described but then line 141 suggests it isn’t used, “but here we do not implement this scheme...”.  Please explain more clearly.

SC4. Figure 2. The color bar hides the relatively weak correlations across much of the country.

SC5. Figures 3b & 4. Are the values plotted meaningful in regions where the correlations are weak? It may be worth considering a screening that only plots for p-values above some threshold (0.10?). In Figure 4, the errors on the values of the slopes seem fairly large for the individual months (a lot of scatter).

SC6. Lines 423-236. The increasing role of soil NOx on U.S. air quality has been noted in some other recent work as well; see for example Guo et al. (2018) and Geddes et al. (2022).  Guo et al. (2018) also suggest that soil NOx may be contributing to ozone biases in GEOS-Chem. 

SC7.  In Section 4, it would be useful to summarize how NOx has declined over this period, and whether the largest drops in the slopes/correlations have occurred in locations where anthropogenic NOx has decreased the most.

Technical corrections

Line 132 and elsewhere: biologic à biogenic?

Line 191 caption of Figure 2 black boarder à border

Line 255 least à smallest or weakest

Line 278 transportation à transport

Line 384 caption of Figure 8 temperature-indirect à temperature-direct ?

Line 442 what is “ozone migration”?

Line 468.  Is this a spatial correlation of the slopes from the model vs observations?

References cited above not listed in the manuscript:

Barnes E. A. and A. M. Fiore (2013), Surface ozone variability and the jet position: Implications for projecting future air quality, Geophys. Res. Lett., 40, 2839–2844, doi:10.1002/grl.50411

Camalier, L., W. Cox, P. Dolwick (2007), The effects of meteorology on urban areas and their use in assessing ozone trends, Atmos. Environ., 41, 7127-7137, doi:10.1016/j.atmosenv.2007.04.061

Clifton, O. E., et al. (2020). Dry deposition of ozone over land: processes, measurement, and modeling. Reviews of Geophysics, 58, e2019RG000670, doi: 10.1029/2019RG000670

Fasullo, J. T., et al. (2022). Spurious late historical-era warming in CESM2 driven by prescribed biomass burning emissions. Geophysical Research Letters, 49, e2021GL097420, doi:10.1029/2021GL097420

Geddes, J. A., Pusede, S. E., & Wong, A. Y. H. (2022). Changes in the relative importance of biogenic isoprene and soil NOx emissions on ozone concentrations in nonattainment areas of the United States. Journal of Geophysical Research: Atmospheres, 127, e2021JD036361. doi:10.1029/2021JD036361

Guo, J. J., et al. (2018) Average versus high surface ozone levels over the continental USA: model bias, background influences, and interannual variability, Atmos. Chem. Phys., 18, 12123–12140, doi:10.5194/acp-18-12123-2018

Kerr, G. H., Waugh, D. W., Steenrod, S. D., Strode, S. A., & Strahan, S. E. (2020). Surface ozone-meteorology relationships: Spatial variations and the role of the jet stream. Journal of Geophysical Research: Atmospheres, 125, e2020JD032735, doi:10.1029/2020JD032735

Tawfik and Steiner (2013), A proposed physical mechanism for ozone-meteorology correlations using land-atmosphere coupling regimes, Atmos. Environ., 72, 50-59, doi:10.1016/j.atmosenv.2013.03.002

Zanis, P. et al. (2022), Climate change penalty and benefit on surface ozone: a global perspective based on CMIP6 earth system models, Environ. Res. Lett. 17, 024014, doi:10.1088/1748-9326/ac4a34

Zhang, X., Waugh, D. W., Kerr, G. H., & Miller, S. M. (2022). Surface ozone-temperature relationship: The meridional gradient ratio approximation. Geophysical Research Letters, 49, e2022GL098680. doi:10.1029/2022GL098680