The study by Johnson et al., titled “TOLNet validation of satellite ozone profiles in the troposphere: impact of retrieval wavelengths” used lidar profiles of tropospheric ozone to evaluate the equivalent retrieved from TropOMI, CriS and TropOMI+CriS using the TOPAS algorithm. This represented retrieval schemes exploiting UV, IR and UV+IR wavelengths to retrieve tropospheric ozone. The long-term plan being to use TOLNet to evaluate tropospheric ozone profiles from the new TEMPO geostationary platform. Overall, this is a nice study demonstrating the suitability of this lidar network to evaluate satellite data, with the novel use of a larger network of lidars than previously used over the US. Therefore, this manuscript is suitable for publication in AMT subject to some minor comments below:

• Page 3 Lines 80-88: The paragraph suggested that there are only two retrieval schemes of ozone profiles from OMI. However, the RAL Space retrieval scheme described by Miles et al., (2015) is used for GOME, GOME-2A & B, SCIAMACHY and OMI. Therefore, this should be mentioned in this paragraph and relevant references included (e.g. Keppens et al., (2018); Pope et al., (2020); Russo et al., 2023).
• Page 7 Line 196: Should the Jacobian matrix, K, be in bold?
• Page 7 Line 205: Add “in” after “12 weeks” and before “total”.
• Equation 3: Is the more traditional method to write this equation as Xc = Xa + AK(Xt-Xa)? Also, I don’t think Xc is defined.
• Page 10 Figure 2: It is true that IR tends to have slightly more information on tropospheric ozone. However, I think one sentence discussing the total DOF (as you show it in your plot and provide numbers) would be useful as the UV scheme has much more sensitivity overall (though this is middle-upper atmosphere). E.g. add a sentence on Page 10 Line 279 outlining the general picture and then focus on the tropospheric component.
• General point, the quality of the figures needs improving as many (especially the text) are pixelated.
• In Figures 4,5,6 and 8, can the authors add a sentence making it clear what all the statistical metrics are (e.g. RMSE) and clearly state what the reference is. E.g. what you use as the reference to get the NMB numbers (e.g. apriori or TOLNET/ozonesondes convolved with the TOPAS Aks).
• Where possible, fit all of Table 2 onto a single page.
• I find figure 8 slightly confusing. I can only see one TOLNet profile convolved by the AKs. However, as there are 3 retrievals for UV, IR and UV+IR, there should be 3 sets of AKs to convolve the TOLNet profiles. However, I don’t see this. Do the authors only use e.g. TOLNet + UV/IR AKs? And for the bias plots on the RHS, make it clear what the retrievals are compared to e.g. TOLNet + AKs from one retrieval or each wavelength retrieved compared with TOLNet + their corresponding AKs?
• Page 24 Line 545: Why use TOLNet raw and not TOLnet+AKs?
• Page 24 Lines 549-550: Add some numbers for the RMSE stats discussed.
• Page 24 Lines 555-556: The statement “b) retrievals with minimal dependence on apriori information” is too strong in my opinion. If you were discussing only the tropospheric column, where Fig2 suggests the DOF is approximately 0.7-0.8, then I would be inclined to agree as you have nearly 1 piece of independent information from the troposphere. However, as you are looking at profiles, where the DOF will drop substantially, I would be inclined to replace “minimal dependence on apriori information” with “decent independence from the apriori information”.
• Page 25 Line 585: You discuss the sensitivity of the retrieved ozone to SZA, apriori and surface albedo, but would it be worth looking at cloud fraction? E.g. looking at a cloud fraction of 0.1 vs 0.2 on retrieved ozone? CF is an important factor in retrieving any quantity from space.
• Page 26 Line 609: “and lowermost tropospheric ozone.” I’m not sure you can say that here as the DOF is low at 0.1. Please provide more justification for this statement.

References:

Keppens A, et al. 2018. Quality assessment of the Ozone_cci Climate Research Data Package (release 2017) – Part 2: Ground-based validation of nadir ozone profile data products. Atmospheric Measurement Techniques, 11, 3769-3800, doi: 10.5194/amt-11-3769-2018.

Miles GM, et al. 2015. Tropospheric ozone and ozone profile retrieved from GOME-2 and their validation. Atmospheric Measurement Techniques, 8, 385-398, doi: 10.5194/amt-8-385-2015.

Pope RJ, et al. 2020. Substantial Increases in Eastern Amazon and Cerrado Biomass Burning-Sourced Tropospheric Ozone. Geophysical Research Letters, 47 (3), e2019GL084143, doi: 10.1029/2019GL084143.

Russo, M.R., Kerridge, B.J., Abraham, N.L., et al. 2003. Seasonal, interannual and decadal variability of tropospheric ozone in the North Atlantic: comparison of UM-UKCA and remote sensing observations for 2005-2018. Atmospheric Chemistry and Physics, 23 (11), 6169-6196, doi: 10.5194/acp-23-6169-2023.

General comments:

The paper is intended to describe validation of UV, IR, and UV+IR ozone retrievals based on TROPOMI and CRIS data and the TOPAS retrieval algorithm. The validation data sets are TOLNET (lidar) and ozone-sondes. I have three main concerns with this paper. Firstly, it is not clear how this paper contributes to our understanding of the TOPAS CRIS/TROPOMI ozone retrievals over a previous paper (essentially from the same group) by Mettig et al. (AMT 2022) as well as un-cited work by Malina et al (AMTD). The paper indicates that they use the “full capabilities” of the TOLNET data sets but I could not find what this means or how it advances the validation of these retrievals relative to what is describe in Mettig et al.  The paper suggests that a key result is that using UV+IR radiances improves the ozone retrievals over use of UV or IR radiances alone; however  this result is already well known and well described in other papers (some cited, some not).  My second main concern is that while the paper is well organized, it is poorly written with numerous non-quantitative statements, and with essentially no context, introduction, or comparisons to other work within most of the results component of the paper. Thirdly, much of the paper appears to be repetitive with respect to the Mettig et al. paper. 

To get through review, I would ask that the authors spend more effort in describing what is new and different about this paper relative to the Mettig et al. paper; likely this would also help in shortening the paper as material that appears in Mettig et al. need not be restated in the submitted manuscript. Adding context to each of the results sub sections and how what is presented is similar/different to previous work would also improve the writing.

I next have a few specific comments just for the abstract and more general comments / questions about the paper thereafter.

Abstract:

(first paragraph) It is already well known that use UV+IR radiances to estimate ozone increases sensitivity (vertical resolution), relative to UV and IR alone; it is  therefore not clear why this first paragraph in the abstract is needed.

Line 40: What are the “tropospheric systematic bias requirements”? Is there a source?

Line 41:  If the averaging kernel and prior (observation operator) were applied to the TOLNET profiles before comparison than the a priori is removed from the comparison; therefore this should not be a source of systematic bias unless you can show that non-linearities in the inversion make the choice of prior affect the inversion.

Line 47: “random bias”? Please clarify.

Line 52: If TOLNET was sufficient why also use ozonesonde data. Also what does sufficient mean?

Other comments

There are far more ozone-sondes available than just the ones listed in Table 1. Why do you not use them?

Equations 1 and 2 are inconsistent with Equation 3. Equations 1 and 2 indicate that the retrieval is linear with respect to concentration or VMR. Equation 3 suggests either a log or fractional value is estimated; additional explanation is required.

There is another paper on this subject by Edward Malina that is not cited. The authors should take a look at this paper and describe what is different with their approach and results relative to those in Malina et al.

Joint spectral retrievals of ozone with Suomi NPP CrIS augmented by S5P/TROPOM

Malina, E., Bowman, K. W., Kantchev, V., Kuai, L., Kurosu, T. P., Miyazaki, K., Natraj, V., Osterman, G. B., and Thill, M. D.: Joint spectral retrievals of ozone with Suomi NPP CrIS augmented by S5P/TROPOMI, EGUsphere [preprint], https://doi.org/10.5194/egusphere-2022-774, 2022.

Line 105.. missing Worden et al. GRL 2007 reference where this is first discussed.

Section 3: Combinations of UV and IR have appeared in several papers over the last decade. How do the results appearing in each sub-section compare to this prior research (answer, you are essentially getting what is expected based on this prior research).

Figure 4: Are the UV, IR, and UV+IR, retrievals consistent (especially Figure 4c). Use Rodgers and Connor 2003 (not cited) to determine if purple, red, and blue are consistent or if differences in the troposphere are driven by attributable systematic errors (e.g. albedo, clouds) or because there is a lack of sensitivity in the troposphere.

Line 340: where are these requirement thresholds described?

Line 395: This approach makes no sense.. if you do not apply the observation operator, then there will be a bias from the combination of prior and sensitivity.

Line 427: This is an interesting statement about TOLNET “A major advantage of using TOLNet for validation of satellite O3 profile retrievals is the ability to make observations at different vertical levels of the troposphere over an entire day or more. “ However, it is not obvious how this capability is used for the comparisons.

Section 3.3.3. Again, what is different about these comparisons and conclusions versus Mettig et al. and Malina et al.?

The manuscript submitted by Johnson and colleagues is a follow up of the work carried out by Mettig et al., 2022 using tropospheric ozone profiles reconstructed with the TOPAZ tool developed by the University of Bremen to exploit the synergy of UV (TROPOMI) and IR (CrIS) satellite observations. In this work the comparison is made over an 18-month period of TOPAZ retrieval and ground-based observations in North America (TOLNET lidar network and ECC ozonesondes). Mettig has already discussed the extent to which the synergy between UV and IR can improve the restitution of tropospheric ozone profiles but with a different validation data set based on NDACC observations in Europe and the USA. In the present work, the sensitivity study shown in Fig. 4 and the analysis of differences in several tropospheric layers are very useful, and was not present in that of Mettig et al. This work therefore deserves to be published in AMT, especially with the prospect of using TOLNET to validate the future GEO-TEMPO satellite mission.

My only minor concerns, which should be studied even if not taken into account, are the followings:

1) The discussion is sometimes based on the use of ground data convolved with AK of TOPAZ and sometimes based on the raw data interpolated vertically. It is better to use always the same criteria for the comparison of the three configurations. Use of the raw data should be made only for a better understanding of the results.

2) The improvement when using the UV+IR configuration compared with IR-only is real for certain altitude ranges (boundary layer, UTLS) and for certain types of ozone profile (stratospheric intrusion), but does not significantly improve IR-only performance for other cases. This is not sufficiently recognized in the discussions of Fig. 5-6 and tables 2-3.

3) It's a pity that the ozonesonde measurements are not used in conjunction with those from TOLNET for the scatterplots shown in each altitude layers (Fig. 7) and for the analysis of the seasonal variability (Fig.8). This would increase the representativeness of the results, as ozone distributions from TOLNET and ozonesondes are clearly complementary. We are left with the impression that the ozonesonde data have been discarded in the second part of the paper because they do not show a decisive contribution from IR+UV compared with IR-only in Fig. 6 and Table 3.

Detailed questions or suggestions

Abstract line 27: Since contrary to Mettig, 2022 data in Europe are very limited in this work (10 % of the data base in September 2019), it is better to replace « Europe » by « Netherland in September 2019 »

Abstract line 51: TOLNET data are certainly consistent for a seasonal analysis, is it also true for the altitude range analysis?

Line 104: The introduction provides a very nice review of the different satellite missions including their horizontal and vertical resolution. A table to summarize these resolutions would be useful.

Line 112: Mettig et al. study also includes NDACC and SHADOZ observations in Europe and the Tropics (ozonesonde and lidar) in addition to the TOLNET lidar in California and Huntsville. The sentence should be changed to mention it.

Line 125: In order to clarify the contribution of this new study in relation to the work of Mettig et al., might be good to add « with an emphasis on North America and many lidar instruments» after « O3 profile retrieval ».   It might be good to specify here that a detailed statistical analysis at different altitude ranges is conducted in this work while this point was not developed in Mettig et al.

Line 145: The number of lidar observations considered (185) is different from the maximum value in table 2 (176). They should be consistent. The Mettig et al. study is finally not so different (170 lidar data and 200 ozonesondes for the same time period 2018/2019)

Line 165: give here the seasonal distribution of the TOLNET observations given line 473

Line 176: Add the positions of the ozonesonde stations on the TOLNET map (Fig.1). What is the seasonal distribution of the soundings?

Line 236: In equation 3, I guess Xc is the convolved observations using the satellite AK.

Line 245: I guess the “ known TOLNet O3 profile” is the black curve in Fig. 4. Please be more specific here.

Line 285: Once it has been stated that UV-only has limited information below 15 km, I suggest changing the way the end of this sentence is written to focus on the comparison with IR-only:

«are much improved (8-10 km) compared to UV-only profiles below 15 km asl. » by

«are improved (8-10 km) compared to IR-only above 12 km and below 8 km ».

Line 306: Fig. 4 is a very nice figure and a useful addition to Mettig et al. study. I disagree with the statement « demonstrate the capability of the UV-only, IR-only, and UV+IR retrievals to replicate tropospheric and lowermost tropospheric O3 during a PBL pollution event ». None of the configurations is able to reproduce the ozone enhancement in the lowermost troposphere. It is not so surprising considering the low value of the AK below 2km. It is better to emphasize the very good results obtained for the stratospheric intrusion case for UV+IR, where TOPAZ avoids the downward propagation of the upper tropospheric enhancement compare to IR only.

Fig. 4. Considering the very high value of this figure, I suggest to add the 6-12 km NMB in panel c to discuss the ability of the 3 configurations to reproduce the upper tropospheric enhancement.

Line 314: Yes I agree with this last statement. Why is this result different from the Cuesta et al. comparison between chemical transport model and combined analysis of GOME-2 and IASI showing a reasonable agreement for ozone enhancement below 3 km? This is worth to be discussed in section 4.

Table 2. Why are the numbers of observations different in the different vertical layers? Altitude range of the lidar profiles? Clouds?

Line 370: I would suggest discussing all the results in Table 2, including RMSE and bias, in this paragraph instead of mixing them with other topics of Section 4, which should be limited to a general discussion and comparisons with previous works.

Fig. 5 and Table 2. I do not understand the 89-number of observations in Fig. 5 caption while Table 2 shows up to 172 colocations. Better to have IR-only and UV+IR on the same page in Table 2.

Fig.6 and Table 3. Again I do not understand the 26-number in the Fig. 6 caption while 50 soundings are considered in Table 3.

Line 375-385: It is a pity that the differences with theTOLneT comparison are not highlighted. This paragraph sounds very positive while the differences with the ozonesonde-raw are significant below 4 km. The improvement using IR+UV instead of IR-only is not obvious anymore for this subset (NMB in Table3). Is it because the ozonesonde profiles include several cases with lowermost tropospheric enhancement as shown in the sensitivity study in Fig.4b ?

Line 385. As mentioned for Table 2 it is good also to include the RMSE and bias analysis of Table 3 in this paragraph. By the way why is IR-only RMSE smaller than UV+IR RMSE? This should be discussed.

Line 428: This sentence is relevant for the validation of the future TEMPO-GEO mission. It is not mandatory for the analysis of the satellite data of this paper where lidar and ozonesonde observations are equally relevant. It is a pity that the ozonesonde data are not included in Fig. 7. The latter ozone vertical distributions are indeed different and complementary from those corresponding to the TOLNET observations (see the comparison between Fig. 5 and 6).

Line 441: The results of RMSE and slopes in the 4-6 km are not much better than those in the layers 0-4 km even for the IR-only and UV+IR while the DOF are significantly larger than below 4 km, e.g. the slopes in the layer 4-6 km in Fig. 7 are < 0.5 in the Table 2 and Fig. 7. The reason for this limited improvement of IR or IR+UV could be discussed in this section, instead of focusing again on the limitation of UV-only configuration. The latter is already very well demonstrated by the results presented in p. 13 to p.18.

Line 471-475: The seasonal analysis is indeed a nice contribution of this paper. However the number of limited co-locations being a limitation of the interpretation of the results, once again the use of the ozonesonde data as well as the TOLNET observations would improve the value of such an analysis.

Line 504: I disagree with this statement. The IR-only shows better results below 9 km and the UV+IR SON differences in Fig. 8 are often larger than 10%.

Line 526. The sentence is not complete

Line 527-537. The discussion of RMSE values of Table 2 and 3 would be understood if presented in section 3.3.1 where Fig. 5 and 6 and other statistical parameters of Table 2 and 3 are presented. Mixing this RMSE analysis with a general discussion of the value of the paper results and with a comparison with previous work make reading of this paragraph a little bit difficult.

Line 567-568: Remove or change the part of the sentence saying “more capable of capturing conditions with air quality impacts such as pollution events “ because this paper does not show this paper does not provide strong evidence for this. It is mainly shown that the stratospheric intrusions are better reproduced.

Line 574: Again remove the end of the sentence saying “during times of PBL-level O3 enhancements” as it is not clearly shown in this paper (see Fig. 4 or Fig. 6).