Di Antonio et al., presents a model evaluation study for the greater Paris area during the 2022 ACROSS campaign. The authors deployed the WRF-CHIMERE model with 3 domains configuration to probe into the model performance of organic and inorganic aerosols on top of several others meteorological parameters and gas-phase species. The model performance is presented and the authors additional described two selected cases of BSOA and wild-fires advection episodes.

The paper is generally well written (there are several typos along the manuscript, and the specificity of few sentences needs to be improved) and it is consistent with previous modelling results focusing on modelling of organic and inorganic aerosols.

Results from such comprehensive evaluation are helpful for the modelling community, and they are clearly presented thought out that paper in a well-structured manner. I have however some major comments that are needed to be addressed by the authors before I can recommend the manuscript for then final publication. I also believe that the manuscript would fit more in the journal GMD – model evaluation paper, since the authors specifically focus on the evaluation of a large array of meteorological and chemical variables.

My major concern is that the description of the physical schemes lacks some keys details in the model description section. Additionally, in order to deeply probe in the overprediction of the organic and inorganic aerosol phase below the 1 micrometer aerodynamic diameter, I think the authors need to provide more details on the modeled size distribution (see my comment below).

Comments:

Abstract:

Line 35: “This overestimation was unexpected”: Why? The authors should elaborate a bit more on that.

Line 37: “The model allows to explain how the interplay of different processes affects the fine aerosol variability and chemical composition over the campaign sites during two heatwave days: biogenic secondary organic aerosol formation in different forests around Paris, advection of wildfire aerosols, and long-range transport of Saharan dust”. I suggest to describe what the main results of the model are, rather than describing what it can be explain, i.e., the main results should be better rephrased in a concise manner in the abstract.

Method:

Substantial more details are needed on how the model approaches the treatment of OA (and eventually also the nitrate fraction giving the results presented here). See my comment below:

The aging reaction constants of OPOA (which I think is homogenous oxidation), ASOA and BSOA, should be all included in the text. Those parameters can highly affect the final modelled OA concentration, especially for what BSOA is concerned. Additionally, the partitioning and redistribution of both organic particle and organic gases mass in the different volatility, and size bin for what particles are concerned, needs to be described in the Method sections. The authors use the VBS approach: How does the module (iteratively?) solve the partitioning equation between the total condensing material in the different volatility classes and the total pre-existing particulate mass? What it is assumed to be pre-existing particulate mass? How does the model redistribute the OA mass with respect to the volatility bins? Are all the compounds in the four volatility bins allowed to partition across all the size bins? Does the model include a kinetic approach for the resulting condensing mass fluxes (how?) as well as a kelvin effects on the vapor pressure of the different classes of organics (per size bin)? How is the growth of particles approached in the model? Those details are fundamental to understand the model results presented here and to put them in a clear prospective.

Line 139: “functionalization (transfer to lower volatility)”. Please correct: functionalization (transfer of organic gases to lower volatility).

Line 143: “The POA can be oxidized by OH to form the Oxidised POA (OPOA)”. I am assuming this is considered as SOA for the comparison of model results, and it does not refer to heterogenous chemistry reactions, right? Please specify.

Line 144: “Four different volatility bins in the 1 to 1000 µg m^–3 saturation concentration C* range and a non–volatile species have been used to represent the ASOA and the BSOA from VOC oxidation by OH, NO3 and O3”. At which reference temperature? Also, the reaction rates and mass/molar yields of each of the ASOA and BSOA precursors with respect to each different oxidant, especially for NO3 and OH, should be reported somewhere in the text along with references, preferably in the form of a table. Again, this will help to put the results in a better perspective, and facilitate the comparison with previous and future modelling studies.

Line 153:” Nucleation, coagulation, condensation and dry and wet deposition processes are also addressed within this aerosol module.” This is too general. Those processes need to be clearly described, at least condensation (see my previous comment).

Line 347: “As a matter of fact, sites in the Alpine regions in SE France or over the Massif Central mountains in central France show close to zero or even negative correlations, indicating that the WRF–CHIMERE model does not capture well the NO2 variability for sites affected by orography”. Do the authors mean complex orography? At 6km resolution this is probably not a surprise since much higher horizontal, and vertical, resolutions are needed to reproduce the dynamics of mountain meteorology.

Line 375:

“These overestimations are modulated by meteorological conditions. They are stronger for the organic fraction under heat waves conditions, and especially larger for peak concentrations, probably triggering excessive production of BSOA”. Along with my comments on the Method section, i) how was the aging of BSOA treated and ii) how does the model redistribute the organic mass in the size bins?, i.e. excessive redistribution of the condensing mass in the small diameter sizes, might generate overprediction of OA (since the authors are comparing against ACSM data with aerodynamic diameter lens cut off of 1 micrometer)? Those details are needed to understand the overprediction of OA fraction. This might also apply to the nitrate fraction: excessive partition of HNO3 might be an issue (in that case comparison with total nitrate measurements, if available, might help understanding if the model reproduces at least the sum of the phases, i.e., excluding dilution issues), but the model might be redistributing excessive nitrate mass in the lower tail of the size distribution, which should instead be allocated in the coarse mode. Bulk approach models might lead to this kind of behavior. A quick look at the size distribution of the nitrate, and eventually of the organics, might help bringing some light on that. Also, which version of ISORROPIA is the model currently using?

Line 390:

“Contrary to the French GEOD’AIR sites, organic aerosol is not anymore systematically overestimated by simulations at the three ACROSS sites (Fig. 9). Reasons for this behaviour are not clear and need to be further investigated”. This is an interesting results. At least for the nitrate fraction, an increase in the horizontal resolution of the model have shown to yield results that are in better agreement with measurements (Zakoura and Pandis, 2018). It might be worth to spend some word on that.

Line 421:

“OM–to–OC ratio of 1.8”. Was the ratio applied indistinctly to all the organic species (including all the classes of volatility)?  Please specify.

Section 5.1:

It is difficult to read Fig. 11 in its current form. I would suggest improving the color scale, maybe by using a Viridis palette? Also, it would be nice to overlap the wind vectors field for each of the time-step.

Line 473:

“We interpret this as a BSOA formation rate at first order” I believe that meteorological condition might additionally play an important role in such a step increase.

Line 544:

“In the current version used, the MEGAN model does not explicitly take into account this process, which could result in an overestimation of BVOC emissions during such cases” While this might be true from a theoretical point of view, one has to be careful with such a statements (“overestimation of BVOC emissions”). The EBAS datasets contains BVOC concentrations at several site in Europe, including France. Those measurement could be use to evaluate, or at least to give an idea, about the level of BVOCs, concentrations, currently estimated by the model (and, partially, indirectly on BVOC emissions performance). It is well known that MEGAN historically overestimate isoprene in Europe, and especially over European boreal forests, but monoterpenes concentrations, which also have higher SOA yields compared to isoprene, was not reported to be overestimated (at least as far as I am aware).

References:

Zakoura, M., Pandis, S.N., 2018. Overprediction of aerosol nitrate by chemical transport models: The role of grid resolution. Atmos. Environ. 187, 390–400. https://doi.org/10.1016/j.atmosenv.2018.05.06

The manuscript presents the results of a modelling study based on the ACROSS field campaign observation over Paris and the surrounding region. A thorough evaluation of the model is accompanied by the analysis of a few specific events, focusing mainly on the origins of biogenic secondary organic aerosols (BSOA).

Let me preface the review by saying that I think that the paper is really interesting, presents important data and I’m very happy to see the combination of observations from a campaign being accompanied by modelling to help draw conclusions. However, at the current stage, the manuscript feels very technical, dealing mainly with the evaluation of the model.

I have a few suggestions that I feel can increase the impact of the study and make it more in line with publications at ACP:

1. As mentioned above, the case studies feel under-represented in the manuscript and at the current stage feel more like an after-thought. I feel that that this is a shame as these broaden the appeal of the study. As the manuscript is not too long I feel that the cases examined can easily be expanded to include more comprehensive analysis.

2. Stemming from point 1, I feel that when it comes to the simulations, the authors stay at a surface-level interpretation and could have easily expanded the experimental design to answer questions set in the manuscript and answered in an interpretative manner. I’ve noted three main points that can be studied by fairly simple repeat simulations

i. Is MEGAN overestimating emissions? > Could be further explored by running a simulation with a biogenic emission dataset (if the possibility exists in CHIMERE) and comparing the results. Or at the very least directly comparing the MEGAN emissions to another dataset.

ii. Are biogenic BSOA emissions from forests in the region the main driver in the observed peaks? > The authors answer this in a qualitative manner, but a simulation could be carried out by modified land use to a non-forest category to quantify the impact. (Since the authors’ mention that the heatwaves conditions can be thought of as a proxy for climate change conditions, at this point even different kinds of forests could be used here to see whether changing vegetation type would mitigate this impact, but I’ll agree that this starts getting out of scope!)

iii. What is the relative importance of fire to forest BSOA emissions? > Again, simulations can be carried out without fire emissions or without forests to further clarify results.

I believe that one of most interesting point of using models is such exploratory, hypothetical simulations that can really quantify the relative importance of different processes. At the very least, as HYSPLIT is used in the simulation, a more comprehensive analysis could be carried out, for example by looking at concentrations over the trajectories to create clearer links. Overall, I feel that there is a number of ways that the study can be expanded, but currently stays at a rudimentary level in the design and analysis.

3. The authors mention specific periods where the observed PBLH is not modelled appropriately and I think that this should be explored in more detail, as misrepresentation in the PBLH can be directly tied to errors in chemical concentrations (e.g. https://doi.org/10.5194/acp-20-2839-2020).

4. I feel that a clearly-separated discussion section is missing from the manuscript as the presentation of results is mixed with interpretation through Sections 3 to 4. I have added a few comments in the attached pdf document at points that I believe could be taken out of the results’ section and organised as discussion points, but I think that some overall restructuring of the manuscript around the basic idea of creating a proper discussion section would help improve the manuscript.

I also have a few more technical questions/comments:

5. The analysis switched between the 6km and the 2km domains and it’s not always clear which model results are being examined. I think that the authors should be very careful with mixing results like this. To be honest, in the current iteration of the manuscript, I don’t really see the point of including the 2km domain as from what I understand results are only examined in Section 4.4. It would actually be interesting to know if the improvement in resolution is actually accompanied by an improvement in either the meteorology or chemistry. I expect that the first will be, but in my experience the latter isn’t, as it’s below the resolution of the anthropogenic emission dataset. However, in this case fire and biogenic emissions are very important so, if results for the 2km are improved, I think this merits some emphasis.

6. Staying at the 2km domain, from what I understand from the description the vertical level structure is different between the two outer domains and the inner domain? If so this can lead to interpolation issues between the two domains and should generally be avoided. Was there a reason to do so? If they are not different then the methodology section needs some modifications to make the simulation design choices clearer.

7. It’s common at least in the meteorological evaluation to provide RMSE values, which can better place the results for the model setup used in the context of the literature. Furthermore, I think that the study merits a comparison of the WRF-CHIMERE chemical evaluation against the literature to add some context for the reader.

8. The HYSPLIT simulation configuration is completely missing from the manuscript.

Finally, there are some minor points, language errors, typos etc. I’ve highlighted some in the pdf, but the manuscript merits another careful read-through by the authors.

My overall recommendation would be publication after major revisions as discussed above. I hope that the authors will find the comments constructive.

Kind regards and best of luck with the revisions.