This paper describes an interesting analysis of the SO2-to-sulfate oxidation in models relative to those inferred from observations after the Holuhraun eruption. The paper shows that gas-phase oxidation rates in the models are all slower than the observed rates, which is an important result. The main result of the study is presented in Figure 6. However, I have a few concerns about this figure, as detailed below in my major comments below. Most importantly, I am not convinced that a robust separation between gas- and aqueous-phase oxidation is possible based on the available observation data, mostly for two reasons: 1) the mono- and bi-exponential fits are very similar, and it is not so clear that the bi-exponential fit is SIGNIFICANTLY better than the mono-exponential fit; 2) the attribution of the two e-folding times obtained by the fit to gas- and aqueous-phase oxidation seems quite a stretch. I think this interpretation needs independent support before the paper can be published. A few other points also need to be addressed, as outlined below.

Major:

The trajectory analysis is somewhat problematic. First of all, how are the 27 members of the trajectory ensembles (line 174) different from each other? This is not explained in the text. Second, all EMEP stations are located in the atmospheric boundary layer, where air mass trajectories are not well representing the properties of the flow, due to turbulence. This will likely affect the quality of the attribution of events to Holuhraun (or not). Third, the definition of “vicinity” of the Holuhraun eruption is highly subjective. Depending, e.g., on the transport time and distance, trajectory errors will likely be very much case-dependent, and a single “vicinity area” might not be appropriate for all cases (e.g., stations closer to Holuhraun will have a greater chance of hitting the defined vicinity area.

The comparison between models and IASI data is not fully convincing. It seems model output is shown irrespective of whether IASI retrievals are available for a location or not. IASI retrievals can easily miss volcanic SO2, e.g., underneath clouds. Thus, models should only be sampled in pixels where IASI SO2 retrievals are actually made. The authors write that models often have larger plume areas than the IASI retrievals, which can be attributed to clouds affecting IASI. Still, it appears that many models actually have often smaller plume areas than IASI. This would even be worse when cloud screening is applied.

Figure 5: Since the conversion rate of SO2 to sulfate is shown to be uncertain, I am wondering why Figure 5 does not also show a comparison for total sulphur (SO2 + sulfate). This should provide the most robust comparison between the models and the observations.

Figure 6: This is the core result of the paper and quite interesting. However, I am not at all convinced that the bi-exponential fit is any better than the mono-exponential fit. That the bi-exponential fit is better (line 417) is a trivial result. But is it really SIGNIFICANTLY better? The two e-folding times obtained are interpreted as gas-phase and aqueous-phase e-folding times. But I am concerned that the fit is not stable enough to reliably distinguish between the two. Furthermore, how do you know which e-folding time is which? The data per se do not give any information on the two processes, but the authors immediately jump to the conclusion that these are gas- and aqueous phase e-folding times. What is the evidence for this?

Figure 6: The aqueous-phase oxidation occurs only in clouds, so is a single e-folding time even appropriate to characterize this oxidation? This must be highly variable, depending on the time the SO2 spends in a cloud.

Figure 6: All events are exclusively attributed to Holuhraun. However, there are likely always (perhaps minor) contributions from other sources. How might these affect the results, especially far away from the volcano, where SO2/sulfate ratios are low and even relatively small anthropogenic SO2 emissions could affect the ratio substantially.

Line 435: A modelled event is considered successful if both SO2 and sulfate concentrations are within a factor 5 of the observations. Doesn’t this introduce a bias in the analysis? You show that modelled oxidation rates are too slow – in this case one would expect the model to often substantially overestimate observed SO2 concentrations. But large overestimations would be substantially removed from the analysis, which would lead to biased results.

Minor:

Line 161 and Table 2: Why are ERA-Interim reanalyses used? These are superseded since quite a few years already by ERA5 reanalyses with better resolution, and which should have better quality!

Lines 279-280: How do you know that varying IASI SO2 burdens are due to changing IASI retrieval coverage and plumes passing in and out of the region, and not due to variations in emission flux? I don’t think there is good enough data to prove that the emission flux was really constant.

Lines 370-371: Why is a poor performance of concentration ratios expected? The two species are not simulated independently, so a plume in one species should always correlate with a plume in the other species.

Table 3: Why does OsloCTM3 not have the data required for filling Table 3? This should be basic model output (SO2 concentration fields) that is also needed for all other analyses?

Line 55: word aerosol is duplicated in text

For two months of the Holuhraun fissure eruption in 2014 and 2015, this study presents an analysis of the sulphur and sulphate dispersion over Europe as well as an evaluation of the sulphate production. For this, dispersion simulations of multiple models are utilised, compared, and evaluated against IASI SO2 retrievals and surface concentration measurement of European monitoring stations. These comparisons are fairly conducted and discussed. However, to a large extend the authors seem to focus on model comparison and evaluation. Consequently, the manuscript could partly be more adequate to be published in GMD rather than ACP. However, the investigation on SO4 formation fits well with the purpose of ACP and should be emphasised more in the abstract. Furthermore, there are multiple aspects in the model intercomparison, the trajectory-based source assignment, and the SO2-to-SO4 conversion that need further elaboration before the manuscript may be published. 

Major comments:

A multi-model intercomparison necessarily needs to consider differences in the models’ characteristics as model physics/dynamics/chemistry and the model setup as parameterisations and model resolution to allow for a fair comparison and meaningful discussion. Therefore, I suggest adding the advection schemes used in Table 2. How can the OsloCTM3 not have a chemistry/aerosol module as a CTM? Furthermore, the vertical model level distribution is essential with respect to the volcanic emission plume. Please include the model layer thickness of the lowest model level and the number of model layers between 0 km and 3 km height in section 2.3 and consider this in the discussions! How do the different models differentiate with respect to vertical layering, vertical distribution of emissions etc.? Further, it is very hard to assess the performance of the different models individually, as the evaluation and the figures/tables often include just a selection of the models. It seems to be not a full and fair comparison between all models. Figure 2 does not include the CTM due to missing required diagnostics (lines 290-291). What does this mean? Why is it then being listed in table 3? Figure 3 just evaluates the performance of 3 models. Why are the model outputs not designed in the way that they are comparable? Please consider producing comparable model output to fully discuss all model performances.

The setup of the backward trajectories simulated with HYSPLIT needs clarification (lines 174-178). It remains unclear how the ensemble trajectories are designed. Are there 27 ensemble members defined for each station and each hour? If so, how are the ensemble members at the individual stations perturbed? Or do you have one ensemble member per hour for each station? However, 27 stations do not agree with table 1. Table 1 lists the starting heights for the trajectories at each station. How are these heights defined? Is there a basis for these heights as the station height above the surface height of the corresponding GCM’s grid cell? How do you ensure that the trajectories allow for a fair comparison with ground-based observations? Further, are 2 % of the trajectories passing through the 3D bounding box (line 184) significant enough to connect these to the Holuhraun event? 

The assessment of the transport time (lines 185-192) is not fully clear and needs some rephrasing. I would have expected a circular influence region around the eruption site instead of a squared bounded domain. Please also elaborate on the definition of the idealised trajectory points in Fig. 1. Do these relate to full hours? And how many black circles are attributed to which trajectory?

Regarding the IASI SO2 retrieval, it remains unclear what “the SO2 detection is positive” means (lines 112-114). Is 0.49 DU a detection limit? Or is it an individually defined value to discriminate volcanic SO2 from other SO2 (which is the climatology)? Please clarify this. Furthermore, in line 118, you are referring to meteorological temperature profiles for the height conversion. Where do these profiles come from? Are they standard profiles or from meteorological model analyses? To better understand the uncertainty of the IASI retrievals, it would be desirable to have a short summary of the different components contributing to the retrieval error. For example, do the uncertainties of assuming Gaussian profiles and the uncertainties of the temperature profiles contribute to the retrieval error? With respect to the discussion in line 249, please justify why the central height of a Gaussian SO2 vertical profile can be an estimate for the injection height. There are enormous amounts of mass being distributed above the central height of a Gaussian profile.

The core element of the manuscript is the investigation of the SO2-to-SO4 reactions. The use of the biexponential fit and the division into gas-phase and aqueous-phase pathways seems promising on a first sight. Are there any references, where you base this method on? When exploring Figure 6a, the monoexponential and biexponential fits appear very similar and it is hard to justify why the biexponential fit performs better. How can you make sure that the two reaction pathways can directly be mapped within a biexponential fit? The scattering of the data point remains widely spread while the exponents derived from the biexponential fit are fairly close. Please re-evaluate this analysis and provide more evidence for the pathway assumption.

Minor comments:

Please review all citations (e.g., in line 50 Aas et al., 2015 is cited, but does not exist in the reference list).

Please check punctuation. Extra commas would increase readability. And e.g., line 209 misses a “.” after “respectively”.

Regarding the tables’ captions, these are typically written above the tables. Please revise.

Line 36: “ugm^-3” must probably be µgm^-3

Line 55: delete doubled “aerosol”

Line 111: SO2 column load and plume height “are” derived…

In line 138, the calculation of monthly surface mass concentration climatology is not fully clear. What time span is used here? Is the full temporal coverage mentioned in the text corresponding variable for the different stations and corresponds to the column “Temporal coverage” in table 1? 

Table 1: I just count 22 EMEP stations being listed in the table. 

Figure 2: Why mentioning the 21 UTC sampling in the caption, if the figure shows simulation results in the morning?

Lines 264-265: Here, sharp peaks and troughs are mentioned but probably only the troughs are discussed. This is confusing. Please also check the dates listed here. These are not well recognisable in Fig. 3c.

Figure 4: Please define “pollution event”. What is the timeframe of high sulphur concentrations for such an event? And can events occur multiple times a day?

In lines 337, 387, and 401, there are 22 EMEP stations mentioned. However, the explanation before states 20 stations. Please check!

Line 371: Meaning of “… as the models are essentially trying to correctly capture the behaviour of two pollutants as opposed to one” is unclear. Please rephrase. 

Line 425: Please add SO2-to-SO4 again before “ratio of 31+-4”.

Table 5: Should ECHAM6.w-HAM2.3 have a footnote indicated by the “*”? If yes, where is the explanation?

Line 462: A comparison against IASI SO2 retrievals “shows” that…

Lines 464-465: Please be more precise here. What is an underestimation of a distribution?

Line 473: “whilst considering everything else equal” Is this really the case? What is about the different resolutions, different chemical mechanisms, different transport schemes? Please extend this discussion.