General comments

The paper analyses the effect of NOx and VOC emission reductions on surface ozone using observations and a model in Saxonia. The paper fits to the scope of ACP. There are mostly technical issues that have to be fixed before publication like missing definitions or information on input data and model version, and the need to improve figures and tables.

Specific comments

Line 12: Is NOx=NO+NO₂ or are also NO₃ and N₂O₅ included? Please define for clarity.

Line 16: Spell out "VOC" already here, line 29 (or line 19, hidden) is too late.

Line 125: I suppose "p" is probability. Please spell out since "p" can be used also for pressure.

Line 131: Is this a boxmodel on trajectories? Please more details, from the given reference that is possible. The information on meteorology provided in the following lines is too general. 

Line 133: Which version of CAPRAM? You need it on the website cited in the supplement.

Line 141: After "S1" "showing NOx emissions of the main roads and urban centers".

Line 147: The fixed value for HONO is not far off from typical values but it might be better to keep HONO/NOx constant which might help to get a faster increase of NO due to HONO photolysis after sunrise in Fig. 8, especially in winter (Elshorbany et al. 2012). Maybe for a sensitivity study or outlook.

Line 166: Does table S4 refer to the pre-runs?

Line 255: Isn't Fichtelberg due to the prevailing wind direction less affected by air masses from polluted regions than the other mountain stations?

Figure 4, caption: Better write "differences" as in the text.

Line 266: From Fig. 4 it can be also said that the difference between rural and urban stays about constant if the first 2 points are included. Please improve text in this paragraph.

Lines 340f: These numbers do not agree with Fig. 5, 100, 50 and 0 percentiles. Typos or misunderstanding? Please correct or clarify.

Line 362: Insert "of the latest period"

Line 431: A table with emissions for this base case for Saxony would be useful here or earlier (line 141). Or refer at least to Figs. 11 and S9.

Line 478: "of the base cases for Saxony (Sect 3.3.1)", right? If yes please insert.

Line 498: "for the station types"? Insert if yes, if no please explain already earlier in this subsection.

Line 503: Mention the mean values also here, then table S11 is not needed. 

Technical corrections

Line 148: Better new paragraph.

Fig. 1: Include the frame of Fig. S1 for convenience.

Fig. 2: Include in caption after "1997" "or later".

Fig. 5: Here colors superfluous.

Lines 665, 673, 700: Please provide DOI or URL for technical reports.

Lines 712, 717, 747, 789, 794: Same journal? If yes use the same abbreviation.

Line 772: Final revised version available?

Supplement: Fig. S1: Please define grid and its relation to the one in Fig. 1. It appears to be a subset of Fig. 1. Meaning or purpose of red rectangles not clear (is the sum of all 3 used in Fig. S9 which should be referred to?)? Mark the location of the extreme maximum which is almost one order of magnitude out of scale. Mark also the reference point mentioned in main text. Maybe  a logarithmic color bar for the emissions would be useful. 

Table S3: "Dry deposition", right? It might be useful to include conversion factors to ppbv for the species not listed with this unit.

Table S4: Your compound strings are often inconsistent with the MCM-notation and could not be found in the CAPRAM-link. Instead of listing them twice it would be useful to replace one column by a column with the full chemical notation or the compound names as in Table S10. Also some compound strings change from summer to winter, typos?  

Table S5: Add in caption or text, line 176, "i.e. each combination is considered." 

Fig. S2: There is enough space to keep the time axis in the last frame on scale.

Fig. S9 to S13 and 11: It is often difficult to attribute the legends with source categories to the color bars in the figures since the order differs from figure to figure. Please stay to the order in the legends in every figure. Captions too short or misleading (e.g. traffic dominated by solvents in Fig. S10).

Fig. S13 and S14: Better convert to a table.

Please no page break directly after the table head, and no line break in a number.

References

Y. F. Elshorbany, B. Steil, C. Brühl, and J. Lelieveld: Impact of HONO on global atmospheric chemistry calculated with an empirical parameterization in the EMAC model, Atmos. Chem. Phys., 12, 9977–10000, 2012.

This paper summarizes the trends of O3 and its precursors over a 20 year period in Saxony and concludes that NOx reductions outpacing VOC reductions has led to increasing mean concentrations of ozone in urban regions.  The paper fits the scope of ACP and is an important analysis with direct implications for designing effective future mitigation strategies in the region. Overall, the analysis is detailed despite the fact that there were a lot of assumptions that had to be made given data availability over this time period. 

General Comments:

(1) Overall, I found it difficult to read the paper given mis-matches between the text and figures/captions and I think particular attention needs to be paid to better align this information.  In particular, the figure captions do not adequately describe was being shown in each figure and I was not able to determine what information was different in the subpanels without referencing the text. All figure captions should “stand alone” and be able to fully describe what is being shown and should be edited accordingly. Additionally, I found that there just seemed to be “missing” information where a figure was first referenced that was only mentioned much further down in the text. This made it difficult to understand what was in the figure the first time I encountered it, especially if that information was also not defined in the caption

(2) In general, I found it odd that gas phase concentrations are being reported in ug/m3 rather than ppb. Moreover, the units used throughout the paper are broadly inconsistent with production rates being reported in ppb/h, but concentrations reported in ug/m3. I am more familiar with O3/ NOx/ VOC concentrations being reported in ppbv than ug/m3 given that U.S. standards are in those units. But, regardless of the authors preference for units, at minimum the units of the concentrations and production rates should be consistent throughout the paper. For example, in Figure 10, NOx concentrations are in ppb and O3 production is in ppb/h, but in Figure 8 & 9 NOx and O3 concentrations are ug/m3).

R/e other reviewer’s comments: Overall, I concur with most of their comments and technical notes, particularly in regards to their suggestions to improve the match between figure captions/the text and their detailed notes about things that are missing distinctions within the text. I only note I have one distinct difference in opinion from their comments. References to “p” in the figures is clearly meant to be a p-value indicating statistical significance and to me including it next to the r2 value makes this abundantly clear, as well as the fact that there would be no reason this should be “pressure”. However, defining this the first time they reference the p-values in the text would be useful.

Specific Comments:

Lines 130-140: This section is missing some details that would be required to reproduce the simulations (e.g. Which version of CAPRAM is used in the work? What meteorology fields/versions are used? What other model options (e.g. specific deposition schemes, emissions inventories etc.) were assumed?) I’m not a CAPRAM user, so I don’t know what details are typically provided, but it seems to me that versions/meteorological field names are certainly relevant/ required to reproduce the work.

Lines 156-157: The choices for the boundary layer heights ascribed need to be justified. These seem reasonable to me, but given the model-measurement discrepancies for NOx/O3 ascribed to this choice, I think its important they state why they were chosen (e.g. match available measurements decently well?). I have more typically seen BLH set in box modeling by toggling them until a secondary species with a long lifetime expected to be lost primarily to dilution is matched.

Section 3.3.1 - Were all modeled [NO] concentrations adjusted up by 1 ug/m3 or only nighttime values??  Seems like it’s a bit misleading if all modeled [NO] is arbitrarily adjusted up when only the values < DL are adjusted in that manner for the observations.

Figures 8/9: It would be nice to add an “average of all sites” line that’s directly comparable to the single model line in Figures 8 and 9. And would also enable you to calculate the normalized mean bias factor (NMBF) summarizing the model-measurement average disagreement (in addition to r2) between average of all sites and modeled results to more robustly support the conclusions of this section.

Figure 10- The markers depicting the years are hard to see on the figure because the lines marking the trends and future emission scenarios are on top of them. I’d suggest flipping the order these are plotted in so that the markers appear on top of the lines so that where each year appears on the figure is easier to see.  Additionally. I can’t tell the difference between the dark blue that 2010 is plotted in vs the black that 2019 is plotted in, particularly for the summer urban cases that are the focus of the paper. Additionally, I think it would be useful to lower the y-limit a bit on these figures so that it is easier to see what’s happening on the lower end of the figures (e.g. whether the reductions in NOx vs. VOCs lead to more /less P(O3) in the future emission scenarios shown as dotted lines on the figure).  Some simple edits to this figure would make it much more readable. The caption needs to better describe what the future scenario lines are. These are only mentioned *much* further down in the text far after this figure is first referenced. Additionally, the lines don’t all appear to be aligned properly to the last 2019 value… Finally, I wonder if its even necessary to “label” these future scenario lines on the figure itself, as these are pretty typical in the literature. Rather, a key describing if it’s a NOx/VOC reduction or a reduction of both after 2019 would suffice and clean up the figure a bit.   

Lines 490-499: I can certainly appreciate the challenge of not having enough VOC data to create Figure 10. But, I’m generally confused about how TNMVOC is estimated here and further clarification is needed in this section especially. The main text states that “The grid of modelled NetPO3 as a function of modelled, inventory-derived NOx and TNMVOC concentrations (see Sect. 2.3), was therefore interpolated to derive TNMVOC concentrations for given measured NOx and dO3/dt. I read this to mean that they used the model with inventory estimates for NOx and TNMVOC which is what is shown in the column for Table S8? And because they see decent agreement between the model & measurements of NetPO3 and NOx that they are assuming TNMVOCs predicted by the model are “right” at each station. What is extremely unclear to me is this “interpolated to derive TNMVOC concentrations for given measured NOx and dO3/dt” statement. That implies that they preformed some sort of correlation/interpolation that is not shown anywhere in the manuscript or supplement to estimate “where to place the markers on Figure 10 on the TNMVOC axis” / get the values shown in Table S9. If that’s what was done, I would like to see this figure and have it described with quantitative supporting statistics to convince us that where their TNMVOC estimates are accurate (e.g. show Table S8 as a figure and the equation used to generate the values in Table S9). Additionally, if this methodology has been used in the past for such analysis, it would benefit the paper to reference that such a methodology has been used before in this section to justify this methodology choice. I have seen prior papers use the correlation between CO or HCHO with TNMVOCs to estimate TNMVOC when only CO or HCHO is available in the past, but all of those showed this in the supplement with supporting statistics to show it was a reasonable way to estimate TNMVOCs.  Regardless, I’m confused enough about this section that I really don’t understand how the values in Table S8 correspond to that shown in Figure S6 or how what’s shown in Table S8 is used to get the data in Table S9/ the values used on the TNMVOC axis in Figure 10 and the authors certainly need to clarify this.  

Line 499-501: “… because of lowered emissions through environmental mitigations.” Are you talking about reductions in anthropogenic VOCs through emission controls/regulations or reductions in biogenic VOCs? Would be useful to clarify what is meant by “environmental mitigations” here / which VOC category is assumed to be affected.

Table S4. I appreciate the authors giving the smiles strings of the VOC compounds, but it would be useful for reproducibility if they also supplied the MCM species names of each in another column. As an MCM box modeler, if I wanted to recreate this study, I would have to go through the MCM mechanism and identify each one of these compounds by hand in order to recreate their simulation. Thus, while giving the strings does mean that these concentrations could be used in other mechanisms (and why it is important to retain that information), for reproducibility, it would also be useful to have the MCM compound name (since there are indeed existing “mapping” tools to map those tracer names to the tracers of other mechanisms).