This work addresses the uncertainties in the simulation of surface ozone in chemistry-climate models by offering a novel approach, using machine learning, in identifying the causes of biases originating from the representation of related key processes. As such, it is an excellent feasibility contribution in correcting modelled O3 biases. The results demonstrate that these biases are mainly due to the UKESM1 model effect of temperature and photolysis rates, and thus provides valuable insight for further model improvement which ultimately should allow improving the assessment of the impacts of changing emissions and climate on future air quality. The paper is very well written and supported with solid analysis, clear presentation and meaningful interpretation and I have no comments of technical nature. I would only like to point out the need for follow-up studies to tackle the questions of the sensitivity of the obtained results on the particular machine learning technique employed here and the enrivhment of the technique validation with the consideration of additional, indepedent derivations of the O3 biases with alternative observational data. These are included in the following specific commnets indicated by the corresponding line numbers.

SPECIFIC COMMENTS

49-51: This sentence does not clearly introduce the motivation/justification of this study. How is the "gain of greater physical insight" consistent to "loss of interpretability of the results"? Please rephrase. 

52-53: Is the current study the first one to apply machine learning for estimatins and correcting global model ozone biases? If yes it should be mentioned explicitly.

102-103: Can this starement be elaborated? Is there no value in repeating the process (in a separate study perhaps) including observed station data from locations around the globe as to verify the results from the current gridded data analysis? 

151-154: In relation to the previous comment and in conjuction to the method description in the first paragraph of sub-section 2.5, the results of this test are impressive but of course must be viewed in the framework of comparing a test run against a validation run of the same (machine leaning) model. Is it possible to compare the resulting O3 biases from this test run (for selected locations) with respective biases obtained from a conventional method and an alternative observational data source?

186-188: Can the results and the conclusions of Fig.5 be compared to those of other studies (based on any other methodology)?

296-298: Also the choice of the particular machine learning model influences the derived O3 biases and conclusions.

Overview:

The paper presents a multilayer perceptron ML approach to predict the differences between monthly-mean simulations of ozone surface concentrations simulated by the UKESM1 and the EAC4 CAMS Reanalysis. The ML approach manages to predict the differences to a good degree, which is exploited by the authors to ML predict the differences for UKESMI1 scenarios simulation of future ozone surface concentrations. The ML approach is trained by set of 20-30 input variables, such as temperature, photolysis rates and boundary layer height. While not a direct outcome of the ML approach, the importance of the different input variables is quantified using the SHAP framework.  The paper is well written.

General review:

The fundamental problem of the paper is the use of the ozone surface concentration fields of the CAMSRA data as the “truth”. The ozone surface analysis is corrected too little by the assimilated ozone satellite retrievals, which are dominated by the stratospheric signal, to be considered a representation of the “truth” or the observations; they are just another model run.   https://atmosphere.copernicus.eu/sites/default/files/2021-06/CAMS84_2018SC3_D5.1.1-2020_reanalysis_validation.pdf. CAMS84_2018SC3_D5.1.1-2020_reanalysis_validation (copernicus.eu)  There is no continuous gridded data set, which would make the identification of biases of simulated ozone surface values for all regions of the earth surface a straightforward task. This is in contrast to meteorological simulations for which meteorological re-analysis (i.e. ERA5) are considered a continuous global reference data set.

For this reason, I suggest rejecting the paper because I can not think of an easy fix of that dilemma. It seems necessary to introduce independent surface in-situ observations such as the TOAR data sets. Using the TOAR data set as reference make sense but limits strongly the area for which biases can be determined.  The TOAR data set could also be used to demonstrate that the biases of UKSEM1 are indeed much larger than the biases of CAMS RA.  An alternative approach could be to use the applied method to transition results between different model types, but I am not sure if there are useful applications for that.

The conclusion from the SHAP based ranking of feature importance remains too general and I am not sure what can be learned from that. All the mentioned factors contribute to ozone variability, and it is likely that that is also reflected in their correlation with the inter-model differences.  The often-mentioned biases of the emissions were seemingly not identified as a large contributor to ozone biases, which is surprising as the relatively small impact of the NO concentrations. I also wonder why ozone concentrations itself were not used as an input variable for the training. I am not saying the results are wrong, I would only suggest avoiding the over-interpretation of these correlations into actual causes of the biases. But, if the authors can demonstrate that so far unknown deficiencies of UKSEM1 were identified and potentially even fixed based on the finding of the feature importance, this should be mentioned more convincingly.