The paper presents high-resolution WRF-Chem model simulations for the UAE region. The authors carried out evaluation of the model simulations for different meteorological and chemical fields by using ground and satellite-based observations. Given the rapid industrial development and urbanization in the region, it’s important to develop the-state-of-the art air quality models to simulate air pollution in UAE. The authors conducted comprehensive WRF-Chem model simulations with 3 nested grids centered over the UAE. There are a number of shortcomings of this study that need to be addressed before considering this manuscript for publication.

Major comments:

• The manuscript can be shortened quite a bit. There’s plenty of text devoted to the presentation of the evaluation of the meteorological simulations by the WRF-Chem model. Although the main scope of the paper is the evaluation of the gaseous pollutants, there's lengthy discussion about the meteorological simulations in the main text. The discussion about the ERA-5 reanalysis, evaluation of the meteorological simulations using the weather observations and ERA5 reanalysis data should be moved to the supplemental material.
• The EDGAR emission inventory doesn’t provide information on the day-to-day (e.g. weekday vs. weekend) and hourly variability (diurnal cycle) of the anthropogenic emissions. This deficiency of the emission inventory and its impact on the findings of the modeling study aren't discussed.
• How are the emissions from point sources (e.g. power plants) ingested into the model? Is their vertical distribution taken into account?  
• The main weakness of this study is the lack of the model evaluation against ground-based air quality observations. Without such model evaluation it’s hard to determine the applicability of the model to air quality research and prediction applications. I assume there are surface based O3 and PM2.5 monitoring sites available in UAE and neighboring countries, which could be utilized.
• AOD verification by using the available data from the AERONET sites located in the region would be very helpful as well.  
• The model evaluation against the satellite observations of CO, O3 and NO2 is worth of publication. It’d be helpful to add information on uncertainties associated with these observations. But again the satellite observations are sporadic and can't provide information on vertical distribution of the pollutants. 
• Did you include a dust parameterization in the model? Given how significant are the dust emissions in the region, it’s important to discuss the role of the dust aerosols and their impact on photolysis, thus affecting O3 chemistry.
• Was the aerosol feedback turned on in the model?
• The transport of the pollutants from other countries to UAE should be considered here as well. It’d be helpful to conduct sensitivity simulations to estimate the impact of the transboundary pollution in the region.
• Line 614: Are there any NO2 emissions included? Usually 8-10% of NO is emitted as NO2.
• 643-645: How was the nocturnal mixing of the chemical species parameterized in the model? WRF-Chem applies enhanced mixing within the areas with high anthropogenic emissions.
• 687: Are you referring to dry deposition of CO? This part needs more clarification.
• 721: This interpretation is vague.
• Pages 28-29: This chapter needs to be revised quite a bit. First, some of this material is more relevant for the Introduction section. Second, there’s quite a bit textbook material describing different NOx/VOC regimes affecting tropospheric O3 formation. The authors don’t present any sensitivity simulations to show whether O3 is NOx or VOC limited in the region. There aren’t either any surface NOx or VOC measurements used here to evaluate the model. Therefore, I find this discussion as vague and not pointing to any particular mechanism to explain the observed model biases.  
• 798-800: do you see this effect occurring in the model? 

Minor comments:

For WRF-Chem please cite this paper as well:   https://journals.ametsoc.org/view/journals/bams/98/8/bams-d-15-00308.1.xml

204: Fix “meteorology”

The paper “Evaluation of the WRF-Chem Performance for gaseous pollutants over the United Arab Emirates” by Yarragunta et al. present an evaluation of the WRF-Chem chemistry transport model implemented by the United Arab Emirates. This is done against in situ measurements for surface windspeed and temperature, another model for other meteorological variables and TROPOMI-derived satellite measurements for trace gas chemical species. While the application of the WRF-Chem model over this area has certain scientific and applicative interest, the data and methodology of comparison is clearly limited. The only objective of evaluation of a model is better fitted to other more methodological journals such as “Atmospheric Measurements and Techniques” than “Atmospheric Chemistry and Physics” in which actual geophysical results are to be presented (and this is not the case of the current manuscript).

Moreover, the paper needs substantial major revisions to be publishable. I strongly recommend the full revision of the three major aspects:

• Ozone total column: The paper only evaluates ozone simulations by comparing with total column ozone retrievals from TROPOMI. The ozone total column is largely dominated by stratospheric ozone, that accounts for 90% of the total column ozone or more. The influence of tropospheric ozone in these measurements is negligible. This is not a validation of tropospheric ozone which is the only part of ozone that affects air quality, which is the aim of the paper. Stratospheric ozone is only linked with stratospheric chemistry and transport (not mentioned in the paper). Moreover, it is unclear why there is a long paragraph (lines 721-746) describing the phenomena exclusivity driving the variability of tropospheric ozone (anthropogenic precursors, NOx or COV limited photochemical regimes).
  
  This part of the paper should be fully revised. It is mandatory to include a validation of tropospheric ozone (from the surface up to the tropopause) from WRF-Chem, which is an available ozone product from TROPOMI. Also, variability of total ozone columns should be linked with stratospheric ozone and pollution-related phenomena with only tropospheric ozone.          
• The comparison method : authors evaluate WRF-Chem by only comparing a single monthly average maps (for 2 months) for different variables, which does not consider any information on diurnal variation. This is not sufficient for a model that is expected to provide diagnostics of air quality, since air pollution outbreaks strongly vary at daily scale and they only last for a few days (1 to 10 days). This method of validation gaseous pollution should be completed with comparisons including the daily evolution (temporal evolution within the month) and it also illustrate with a comparison of the description of at least one air pollution outbreak. More in details, strong biases should be very justified (only general arguments are provided) and statistic estimators such as RMSE should be calculated again since their values are not consistent with their definition.
• Validation of the planetary boundary height: Given that this variable is only forecasted in models or reanalysis such as ERA5, a comparison between models is not a sufficient validation. I strongly suggest adding a comparison against measurements (typically from radiosondes or lidar). ERA5 PBL height are useful to compare its relative spatial distribution, but a validation should include absolute comparisons against measurements. It would also be important to analyze the influence of the PBL in surface air pollutant concentrations.

These additional minor aspects are to be revised:

• Line 318 : the definition of the AK vector should be revised, they describe the vertical sensitivity with respect to the true vertical profile of the target variable in the atmosphere
• Equation 3 : Xret seems to be related to the “retrieved variable”, which is not the “model profile”. Subindexes should be renamed for consistency. The same for Xtrue.
• Figures : each panel of all figures should have a label (a), (b), etc.. otherwise it is unclear
• A figure of Group for High Resolution Sea Surface Temperature can be provided. It is actually a valuable comparison against measurements. We strongly need a graphic support for the long description of this comparison in a paragraph (near line 523).
• Cities, locations in the figures: We need to point out at least in one map the geographical location of the cities or places described in the paragraphs.
• Lines 534-536 : we need wind vectors overlaid in the figure to understand these circulation aspects.
• Line 566: there is not “trend” between two months, but a variation. We use the term “trend” for clear multiyear evolution with many time steps.
• Line 572 : too many digits are used to described the PBL height comparisons (e.g. 646.7 m ?) as compared to its precision.
• Line 655 : It should be clearly stated that the WRF-Chem model overestimates (positive bias) by a factor of 2 both background and peaks of NO2
• Line 690 : these RMSE values are not compatible with the actual differences seen visually in the maps. If it is an unbiased RMSE that is calculated, the definition and name of the quantity should be revised.
• How are the biases, RMSE, R of WRF-Cem in other regions in literature (East Asia and India) compare to those found in this study? Provide this comparison in percentage and the comparison with the results of the paper should be explicitly stated.
• Ozone columns are often express in Dobson Units. For comparison, this unit should be used.
• What is the influence of the altitude in the comparison between gaseous pollutants ? Where do averaging kernels peak? Model values without AVK should be shown as well to understand its influence.