This study investigates the incorporation of coarse and giant desert dust particles (with diameter greater than 20 μm) in the WRF model, together with the GOCART aerosol model and the AFWA dust emission scheme. The authors implemented a number of extensions to the original model. More specifically, they used a prescribed dust particle size distribution for emitted dust particles at the source based on in situ measurements from the FENNEC campaign and employed 5 size bins with diameters up to 100 μm (corresponding to giant particles). Moreover, they implemented an updated drag coefficient that applies to the above bins and is representative of high values of Re number. The simulations were performed from 29 July to 25 August 2015. The model output were validated against various observational datasets.

The article is well written and promotes the research in the modelling of the desert dust. The use of English is excellent and the conclusions are supported by the results. It is suggested to accept this article for publication after some minor corrections are performed.

Suggested corrections:

Section 2.1.3: please include a) whether the vertical levels (line 220) were defined by WRF or by the authors (providing how you chose them in the latter case), b) which UTC time was chosen for the original initialization/each re-initialization (line 221), c) some more detailed information about the model results that you used from each 84 hour run (i.e. whether you removed the first 12 hours of each run due to model spin-up and utilized the rest; line 221), d) the topography and land-use datasets, e) whether the sea-surface temperatures were updated from GFS-FNL analyses every 72 hours at the initial time of each run or every 6 hours together with the lateral boundary conditions.

Line 369-373: Have you validated the simulated upper air wind field, e.g. using ERA5? Western Africa is characterized by a complex wind regime. There is a large area with pink colors (i.e. dust) in area B of Figure 7f. Therefore, the dust errors may be also due to erroneous wind field.

Technical corrections:

Line 23: “… diameters of 5.5-17 μm …”

Line 129: “… are shown in Table 1.”

In equation 5, C_D must be replaced by C_D/C_cun (following the terms of equation 4) or by the equivalent C_D,slip of equation 11.

Line 178: the units of μ should be kg m-1 s-1 so that equation 9 to be unit less.

Line 180: please correct the numerator of μ (i.e. 1.4.58).

Line 182: “Equation 8 has been derived …”.

Line 183: “… Davies (1945) …”.

Line 184: “… drag coefficient becomes:”.

Line 193: “… Substituting Eq. 6-9 in Eq. 5 …”.

Line 197: “… Stoke’s Law (Eq. 11) …”.

Line 200: “… of Eq. 14, proposed …”.

Line 226: please include the full name of DOD (Dust Optical Depth) at its first appearance in the article.

Line 339: Ryder et al. (2013a) or (2013b)?

Line 367: “… and the MIDAS DOD …”.

Line 385: “ … as shown in Fig. 5.”

Line 391: “… for bin 5 (40-100 μm).”

Line 397 and 833-834: What is the domain of interest? Were the results averaged in the whole model domain of figure 3 from 5 to 25 August 2015?

Lines 397 and 830: the Livas pure-dust product is illustrated with the red line.

Line 423: “… 0.066 m/s for particles with D between 5.5 and 17 μm … “ according to line 390.

Line 428: “… compared to this study …”.

Lines 438, 457, 461, 468: “Mallios et al. (2021)” because there is no Mallios et al. 2021a or Mallios et al. 2021b in the References section.

Line 476: “… asphericity …”.

Line 781: “… b932 and b934 are also …”.

Figure 3: are the symbols of each flight below its maximum height necessary? They are hidden by the symbol of the highest flight of each run. The other information (flight number, run, height) must remain. Moreover, some runs of figure 9b (b924_R04, b928_R02, b932_R02, b934_R04) and figure 8 (b928_R02) are not included in figure 3, while b932_R05 appears in figure 3, but not in figure 9b.

Line 817: please clarify how were the uncertainties calculated? At what significance level?

Line 825: please add b928_R02.

Line 834: please add in the caption what are the vertical dashed lines in region II.

Table 2: The MM5 surface layer scheme is 1 or 91 in WRF 4.2.1, but not 2.

This paper addresses the by now seemingly well established underestimation of coarse and giant dust particles by large-scale models. This is an important topic, as these particles are much more abundant than previously thought, such that models could be missing important effects on radiation, clouds, and biogeochemistry. The present paper tries to address this issue by using in situ measurements of dust size distribution over the North African source regions to parameterize the sizes of emitted dust in the WRF-Chem model and then comparing the results against. They find that the deposition velocity of particles must be greatly reduced in order for the model to match measurements further from source regions, which further confirms previous findings in the literature that coarse dust deposits too quickly in models.

Overall, this is a useful contribution to the literature. I did find a series of issues with the description of the methods and results. None of them are serious enough to preclude publication and I’m hopeful that a next version would be suitable for publication. Nonetheless, major revisions are required.

Specific comments:

• I think the paper should be clearer about the actual objective of the paper is or the scientific question it addresses. If this is just to “extend the parameterization the mineral dust cycle in the GOCART-AFWA dust scheme of WRF4.2.1 to include also coarse and giant particles” then this is pretty narrow and perhaps better suited for GMD or a similar journal. But it seems that the authors also investigate the reasons for why coarse and giant dust is underestimated by models, finding that particles settle much too fast in the model. I would suggest making this objective of the paper clearer, especially in the abstract and the end of the introduction.
• I’m puzzled by the lengthy discussion of the inclusion of a new drag coefficient in section 2.1.2. I understand that a drag coefficient parameterization that is valid for larger Re number must be implemented since you’re treating coarse and giant dust (with Re up to 10 or so), but I think the drag law you use (Eq. 14) is fairly standard. So rather than taking up the reader’s finite attention with this lengthy description, I recommend you just state you implemented the drag coefficient law from Clift et al. (2005). Additionally, you should show that implementing this new drag coefficient law is actually important by including a plot of the new and old drag coefficients versus particle size.
• This paper was posted online a few days before the publication of a rather similar paper by Meng et al. in GRL that also found that the settling speed needs to be greatly reduced for a large-scale model to match measurements of coarse and giant dust particles. A brief comparison between the results in the two papers should be included.
• Lines 135-140 and Fig. 2: Here and elsewhere in the paper (section 2.2.2, Figure 5), not enough detail is provided on the used in situ measurements. Please describe exactly which runs were used for this data, how measurements were averaged over different runs and any other processing. Which instruments of the FENNEC and AER-D data did you use and how did you treat data that overlapped in the particle size range? And please include the measurement uncertainties and describe what’s included in them.
• 240-241: “The fine resolution increases the accuracy of the dust simulations and provides a good estimate of the missing mechanism.” Please include either citations or original results that support this statement. Also, how does the fine resolution affect the numerical diffusion in the model? And please include a discussion in this section of the numerical diffusion in WRF-Chem as Ginoux (2003) hypothesized this to be a main factor in why coarse dust particles deposit too quickly in models. Currently, there’s only a brief mention of this in the last paragraph of the paper but not really any discussion of how big a problem numerical diffusion is in WRF-Chem and thus of whether it can explain your results.
• Section 2.1.4: here the effect of asphericity on dust extinction is neglected, which could be substantial. I think that’s fine as the focus is on the size distribution, but please note that simplification.
• (16): here the units for dust mass concentration, particle density, and diameter don’t match (they all use different length scales). Please correct.
• Line 273: please elaborate on how you are “taking into account the absolute difference between WRF forecast time and Aqua overpass time”
• I find Figure 5 hard to interpret and I think a lot more information is needed here. The text notes (L. 347) that this result is for “an emission point in Mali” - could you indicate exactly what location? And are the model results here for the closest grid box? Did the model include emissions only from that grid box or from the entire domain? And see comments above on more details needed for the experimental data. Is this the same data as shown in Fig. 2a, except sorted into the five bins? And could you also include uncertainties on the measurements? I also recommend including your parameterized size distribution at emission to help interpret the model results.
• L377-380: Why do you average over the eight neighboring grid points when you’re already interpolating the measurements? Some more explanation is needed here.
• Figure 8: Please describe what exactly the error bars represent. Is this derived from the counting uncertainty in a given run? Or the standard deviation (or standard error?) over several measurements?
• Also for Figure 8: I find the results in Fig. 8a puzzling. The measurements shown here are at the very lowest level, only 38m above the ground. So presumably, these measurements were part of the data used in Fig. 2 to parameterize the emitted size distribution, is that correct? Then why does the model do so poorly in reproducing these measurements so close to the surface? Please show the emitted size distribution in this plot to help the reader interpret your model results. Please also discuss why the model does not capture the measurements so close to the ground, where errors in deposition would presumably have not as much impact on the results.
• Figure 10: What are the grey, yellow, and blue shading here?
• Discussion and conclusion section: As written, this is really only a discussion section. I recommend the authors add a summary of the results of their study for the reader.
• 441: The gravitational force acts on the center of mass and thus does not create a torque. Perhaps you mean that the aerodynamic force creates a torque? Please correct.
• 438-455: This is an interesting discussion of the effects of shape and particle orientation on settling speed. It left me confused on a few points though. The text states that “prolate spheroids fall faster than their spherical counterparts” even though their surface area is larger. How is that possible as more surface area would create more drag? This conclusion is also opposite of results in, for instance, Ginoux (2003). Do you perhaps mean that for this statement to apply to the special case when the prolate spheroid is aligned with its longest axis in the vertical direction, such that its cross-sectional area is smallest? If not, wouldn’t the drag of the spheroid relative to an equal-volume sphere depend on the orientation, which itself is unknown as it depends on a variety of factors including the electric field (per Mallios et al. 2021)?
• Later in this same section you seem to state the opposite conclusion (L. 452-5), that prolate spheroids do fall slower than spheres. But I think here the difference is that you’re comparing it to spheres of the same max dimension (rather than volume)? I think this is quite confusing to the reader and I recommend you focus on the comparison that could actually explain that particles settle slower than your model simulations predict. And these measurements are presumably for volume-equivalent spheres? Or are these optical diameters, so it depends on particle index of refraction and the shape of real dust particles? That should also be discussed in section 2.2.1 for the discussion here to add value. In general, I think the discussion on the effects of asphericity on settling should be presented more clearly for the statement on L. 476 (“the particle asphericity seems to be a strong candidate for the suggested corrections”) to make sense to the reader.
• I think the author contribution sections requires more detail. There are a large number of authors with only a generic description of their contributions, with only the descriptions for ED, VA, AT, EP, and AG more specific. I think the contributions of each individual author should probably be spelled out more.

Technical corrections:

• Can you provide a reference for Eq. 10?
• 138: “upwelling” is probably not the right word here
• 184: “become is” à “becomes”
• Line 448: I think ellipsoids here should be spheroids

The authors apply the WRF-Chem model to simulate coarse and giant dust (besides the fine dust). For this purpose, they modified the dust transport bins in WRF-Chem, applied a modified (observations-derived) pre-defined particle-size distribution (PSD) to dust at emission and also modify the settling velocity to be applicable beyond the Stokes regime. With their modified model version, they conduct sensitivity runs with reduced settling velocities to test the impact of settling velocity compared to aircraft dust observations.

The study is timely and interesting, but I see two major weaknesses, one related to the comparison with observations and the other related with the transfer of the simulation results to processes other than settling velocity. I detail those aspects below besides other specific comments.

While the manuscript is overall well organized (although I suggest some changes, see below), grammar and orthography need to be improved throughout the manuscript.

Main comments:

The authors distribute the total emitted dust mass (all sizes) across their new bins using a prescribed PSD obtained from aircraft observations (FENNEC-PSD) at 1 km altitude. Given that particles settle when they are airborne (even if less than expected), the actual PSD at emission has to have been coarser than that observed at 1 km. It is still possible technically and no issue to apply this observed PSD at 1km to the emissions. However, in Fig. 5 / Section 3.2 / Section 3.4 / Discussion, the authors compare the modeled PSD at 1, 2, and 3 km height with the mean FENNEC PSD at 1km height and conclude that the model underestimates coarse dust, even when the settling velocity is reduced by 80 %. This is only natural as the FENNEC-PSD has been used at the PSD at emission, hence the model could only ever reproduce the observed PSD at 1km if all the emitted dust would be transported to 1 km in the model without any sedimentation. Otherwise the model has no chance to do so. If this is the goal, then the PSD at emission would need to be described as coarser than the FENNEC-PSD, possibly by assuming a certain settling rate. In the context of the comparison between modeled PSDs and those observed in AER-D, I would like to see a specific comparison between the AER-D PSDs, the FENNEC-PSDs (this could in principle be seen from Figures in the paper, but a direct comparison would make this much easier): Are those PSDs, which have been measured above (FENNEC) and distant (AER-D) to dust source regions “sufficiently” distinct (i.e. is the FENNEC-PSD, which has been used for the emission, “sufficiently” [whatever this means] coarser than the AER-D PSD), such that the model has a chance to reproduce the after-transport AER-D PSD? I believe this aspect is critical, because it might well be that settling is one, but not the only key problem, but that particle sizes at emission are considerably underestimated, even if using the FENNEC-PSD. Besides this general discussion, I would like to ask how the part of the FENNED-PSD, that extends beyond 100 microns has been dealt with when distributing the emissions. Was this fraction ignored and the remaining PSD re-normalized?

I understand that the sensitivity experiments on settling have been performed to mimic the effects of other processes. This is particularly applicable to effects of particle asphericity. However, the effects of other processes mentioned in the introduction, e.g. turbulence or vertical mixing in the Saharan Air Layer, are most likely much less homogeneous than settling and much more closely related to the meteorological conditions. I am not convinced that sensitivity experiments on the settling velocity are suitable to represent the effects of these processes. My recommendation is therefore to focus the manuscript on settling (which contains uncertainties as well, e.g. due to asphericity) and only discuss the other processes as possible additional contributors.

At several locations in the manuscript average PSDs or other quantities are discussed, but (some examples are mentioned below), but it was often not clear to me what averages those are (temporal, spatial, weighted?). I might have missed it, but I suggest to check this and clearly state how the shown and discussed quantities have been calculated.

L 14 Why is there a limit of dust particle sizes (0.2 < D < 100 um), in particular in the context of observations?

L 15 The formulation “extend the parameterization of mineral dust cycle” is not suitable. The parameterization of the mineral dust cycle (emission, transport [which includes itself several parameterizations], and deposition [again more than one parameterization]) was not extended, but some aspects of it were modified. The same applies for “our parameterization” (L 17).

L 21 - 22 Those additional processes have been proposed in the past, hence this statement is inaccurate. I suggest revising it and stating (after mentioning the sensitivity experiments) that those processes are discussed as candidates to cause such a reduced settling.

L 24 in the range

L 25 UR60 has not yet been introduced

L 30 Important to mention that dust only ranks first/second by mass.

L 32 Dust can be windblown, but I believe the emissions cannot.

L 34 Aren’t all regions “spatially limited”? Perhaps use “Spatially more limited”.

L 41 after their wet and dry deposition

L 46 I propose “cloud microphysical processes and their evolution” [omit the dissolution part] as I believe the processes do not stop.

L 51 Please give a reference for this diameter range. The lower limit seems relatively large to me.

L 65-66 gravitational settling

L 69 of all cases

L 70 Please give a (spatial) reference for “larger distances”

L 71 Stokes’ theory is on settling, not on gravity.

L 112 The modified model version considers dust up to 100 microns, but airborne dust particles can also be larger, hence “the entire size range” is exaggerated.

L 131 Please add [in the default GOCART-AFWA] dust emission scheme [of (in) WRF]

L 152 Please introduce variables directly to Eqs. 3 and 4.

L 160 The Cunningham correction is missing in Eq. 5

L 172/176 I know the drag coefficient equation for the Stokes regime as C_D = 24 / Re with Re = U D / nu with nu = mu / rho. Is there any reason I am missing why the formulation shown here is different and contains the factor 2 in Re rather than C_D? (The result is the same.)

L 178/192 The Kelvin scale has no degree symbol.

L 182 I don’t think Equation 7 is meant here. Equation 4 maybe?

L 184 delete become

L 193 Eq. 13?

L 200 remove parenthesis around first reference

L 208 Re < 1?

L 218 Why did the authors choose to include so much ocean in their domain while omitting east N African dust sources? This seems not an ideal choice to me.

L 225-226 The authors state that “scaling of the dust source strength is chosen to best match the modeled DOD with the AERONET measurements”. I would like to know more about this. What scaling do you refer to? Is this a universal scaling/tuning factor or a map scaling? Did you modify the Ginoux/GOCART erodibility function typically used in WRF or is a different scaling used? How has the modeled dust been compared with the observations to infer any kind of scaling? Please give more detail as this is an important aspect of the modeled dust fields.

L 228 A minimum DOD of 0.75 seems very high to me, even close to dust sources.

L 233 by up to 80 % with a step size…

L 234 “sensitivity experiment” instead of “artificial tuning”

L 235 Please revise “falling into the atmosphere”

L 236 “all real forces” is exaggeration. Gravitation and drag forces are real and considered.

L 240 What “fine resolution” are your referring to here? I would not consider 15 km a particularly fine resolution. Also, Table 3 does not contain any experiments on resolution (L 248).

L 243 Dunes are no meteorological condition.

L 270 The explanation is hard to understand, please revise it if possible. How did you handle missing values in the observations for the model comparison?

L 288 I suggest mentioning here again how the FENNEC PSD has been used. This will be as brief as mentioning that it is explained elsewhere (you can keep the reference toy Sec. 2.1.1).

L 338/Fig. 5 Are the modeled PSDs for a particular time step or averaged?

L 360 I suggest showing deposition rates for bin 5 to see whether all particles have settled already over land.

L 363 – 375 The discussion about Flight b920 in the context of Fig. 7 is a bit confusing as Fig. 7 does not contain the PSD measured during the flight (but only the displaced dust plume). Why don’t you show the PSD from b920 to provide a basis for the discussion?

L 393 The relative difference shown in Fig. 9b does not seem to vary systematically with height for bin 5.  Shouldn't this be expected?

L 397 What kind of average is the “mean extinction coefficient”?

L 399-400 It has been discussed before how a few dust plumes were displaced, hence I do not agree with this general affirmation of simulation quality.

L 402 How can these mean (?) profiles be related to the night-time boundary layer? Was any more detailed analysis performed?

L 403-407 This discussion sounds like the observations are the main cause for model-observations discrepancies. I understand that this discussion is done to provide a justification why only Region II has been assessed. I suggest to revise the wording to avoid misinterpretation.

L 418 “acknowledged” is not the right word here, neither “transport code”.

L 440 “(two times the particle major semi-axis)” seems out of place.

Discussion: I believe that much of the discussion around the different processes that might affect particle transport should go into the introduction. Only the discussion around the percentages in reduced settling these processes might account for should remain in the discussion.

L 482 losses instead of loses