A global simulation of ultrafine particle concentrations for the year 2015 is presented and evaluated, with a technique to infer concentrations at high spatial grid resolution from a coarser resolution global model based on a high resolution emission inventory. The primary motivation is health effects.

The chemical transport model is state-of-the-art, as is the emissions data: EDGAR data for 2015 were only recently released at the high resolution used. However, the grid resolution of the model is surprisingly low (see comment below). An impressive number of evaluation datasets are used. The model performs well in the evaluation, though many discrepancies and details are surely lost in the annual averages presented. The paper is well written.

I recommend the paper for minor revisions, though the editor will want to consider that my suggestions are on the boundary between minor and major: calculations will take time and I suggest a new figure be added.

Minor comments

Introduction: a few more state-of-the-art papers on global aerosol number concentration, for example by Liu and Matsui, https://doi.org/10.1029/2022GL100543, and Chen et al, https://acp.copernicus.org/articles/21/9343/2021/, should be cited and discussed.

I think the duration of the simulation or the time period for which the data are applicable should be mentioned in the abstract or early in the introduction, and maybe again when nudging is mentioned. It would also be useful to specify the time resolution of the model output that was used in the evaluation, and the time resolution of the dataset that will be published, in the abstract or introduction, as this will help potential users of the dataset (some might want diurnal or weekly cycles, for example).

The grid resolution is coarser, in both vertical and horizontal, even than that of a good number of CMIP6 climate models (that were run for hundreds of years tens of times). This seems odd since only two years were simulated. Surely, despite the high complexity of the chemistry and aerosol model, simulating two years at this resolution did not take more than a few days using a modest HPC resource at DKRZ? And only one simulation is shown – there are no sensitivity studies (unlike in the study of Gordon et al 2017 the authors cite, which also had low resolution). 1 degree resolution and ~60 levels is typical of CMIP6 Earth System models, which surely are not more than a factor ten cheaper per simulated year unless EMAC is very inefficient or unnecessarily complex (e.g. > 10 volatility bins, or thousands of chemical species). Something to discuss? I should point out that the authors’ work to infer higher resolution output using the emissions datasets is still clearly necessary and valuable despite this comment.

Table 1 and 6: for mountain sites, did the authors compare the lowest model level with observations, or calculate the level that matches the altitude of the site relative to the average surface altitude in the 180x180km grid box?

Table 6: how was the comparison with aircraft measurements done? By interpolating, or matching grid cells, with daily or monthly averaged model output, to the four days (in the case of ATom) in which any given grid cell was sampled? A discussion of representativeness uncertainties would be appropriate here (see papers by Schutgens et al, e.g. https://acp.copernicus.org/articles/17/9761/2017/, which could also nicely set the scene for the downscaling work).

Excluding free-troposphere stations from the evaluation on the grounds that the model wouldn’t perform well there because it is optimized for the boundary layer seems odd. What optimization was done? Do the authors have reason to believe the model will perform badly in the FT, and does this also have implications for the boundary layer?

What diurnal cycles for emissions were assumed? Weekly cycles? The nonlinearities in chemistry and microphysics probably make this quite important even if only monthly averages are considered.

L105 may as well state the actual number of volatility bins.

Figure 2: The nucleation mode geometric mean diameter is between 1 and 1.5nm in this case, so half the particles in the mode are smaller than 1.5nm, and a big fraction are smaller than 1nm. This is really small! The CLOUD NPF parameterizations that are used produce particles at 1.7nm diameter. So does it make sense to produce a dataset with nucleation-mode particles smaller than that? Since the authors use CLOUD NPF parameterizations, I would suggest the authors exclude anything smaller than the CLOUD collaboration’s favourite cut-off diameter of 1.7nm from their model output and their evaluation tables and think about tweaking their model for future studies.

If the authors don’t want to change this, they really need to make the number concentration between 1.7nm and 100nm public so users could exclude particles that are, at face value, molecular clusters, from their analysis. In fact, I strongly encourage the authors to make public at least UFP concentrations in a couple of size ranges, irrespective of the lower cut-off. Say 50-100nm particles and 10-100nm particles. And monthly rather than annual averages. The paper will surely attract more citations that way.

The evaluation section could generally benefit from more time-resolved data. Seasonal cycles are lacking. I suggest adding another figure with seasonal cycles at many sites around the world, to complement Figure 5, which only shows sites in Leipzig.

L354 individuals (typo)

General comments:

This study presents methodology for global modelling of surface level UFP with the ECHAM/MESSy model. Calculations are performed for 2015 and the gridded annual average values are compared to measured annual values obtained from EBAS, GAW-WDCA and ACTRIS covering stations in Europe, North America, India, China and remote regions from 2015 and other years.

The coarse resolution model results are downscaled to high spatial resolution using medium and high spatial resolution emission data together with statistical parameters from the model evaluation with measurements to give estimated annual values on a high resolution grid for the Globe.

The manuscript is a highly relevant contribution to the science revolving around UFP modelling, and it is well-written and clearly structured. I have some comments that may require a bit more work for the authors, but I leave it to the Editor to decide if major revisions are needed (I would be interested in reviewing a revised manuscript, but it is not an ultimate demand).

I encourage the authors to also make the emission data set for UFP in the 7 classes available publicly, as this would surely foster many citations.

Specific comments:

• In my experience, health impact studies of long-term exposure, need two major components from the air quality data: interannual variability and rural-urban contrasts (urban increment). This present study is very thorough and highly interesting for the air pollution modelling community and the research of UFP distribution and dynamics, but promoting it for health effect studies at this stage is a little premature. Often epidemiologists conducting health impact studies have very little possibility to truly realise the issues associated with data sets of this kind. I suggest to rephrase with less emphasis on the possibility for immidiate use of these data for health studies.
• The horisontal resolution of the model is quite coarse in the simulations, and this is discussed and partly addressed in the downscaling. What about the vertical resolution/representation? A surface layer of 45-70 meters is also quite coarse for representing a measurement station at e.g. 4 meters above the surface. How is this handled? Also in connection with the down-scaling? Please share your considerations about this.
• Where does equation (1) originate from? Please either include more information on the derivation or add a reference.
• In the methods description, references for the methodology for median emission diameter for SLV is missing.
• I realise the global model is very complex and time consuming to run, but for the argumentation that it cannot be run for more than 1 year to stand more strongly, please add some numbers on complexity, e.g. number of chemical components included, how long does a simulation take on a state-of-the-art server etc.
• Line 266: there have been made attempts to model street-scale in individual countries/cities using other approaches, see e.g. Ketzel et al., 2021 (this could maybe also be relevant to include in the discussion)
• The authors discuss the issues related to comparing model results for 2015 with measurements from other years. It is an understandable approach, given the small number of measurements available, but it seems problematic when also the measurement-model relations from non-matching years are used to guide the downscaling of results for 2015 using emissions from 2015 (are the emissions from 2015?). Please either repeat the derivation of the linear fit in Figure 7 with only 2015 matches, or discuss the potential issues in depth.
• Using measurements to guide downscaling and then the same measurements to validate the downscaled model results can be considered problematic. Again I understrand the approach, as not many measurements are there to use, but would it be possible to use one set of data to do carry out the downscaling, and then evaluate with another separate set (like it is done in data assimilation)?
• Introduction: One of the issues with UFP measurements is the lack of consolidated guidelines for methodology. Could be good to mention this issue in the introduction, and perhaps also discuss at a later stage.
• Examples of other modelling studies for Europe that could be mentioned (to refer to multi-year modelling studies) are
• Fountoukis, C., Riipinen, I., Denier van der Gon, H.A.C. et al, 2012. Atmos. Chem. Phys. 12, 8663–8677.
• Kukkonen, J., Karl, M., Keuken, M.P., et al 2016. Model Dev. (GMD) 9, 451–478.
• Frohn, L.M., Ketzel, M., Christensen, J.H. et al.,, 2021. Atm. Env. Vol. 264, 118631.
• Line 328: how did you estimate surface level concentrations from a grid cell? Is this methodology also used for the other regions (than remote)?

Technical comments:

• Last sentence of the introduction – how does population density introduce inconsistencies? Surely it is the model representation that introduce inconsistensies?
• What is shown in Figure 3: lowest model layer average, or surface layer (and at what height?)
• Figure 5: the daily fluctuating concentrations are difficult to see in the figure, please consider replotting
• Would be good to make the text consistent across tables, e.g. table 2 should use the formulation from table 4 considering modelling results from 2015 and measurements from other years.
• I am assuming that emission data are from 2015, but please specify the year of the emission data used.
• Table 3: a typo, PNC_M and PNC_M should be PNC_O and PNC_M.
• Line 283: what is meant?
• Line 296: is there really only one grid cell covering Delhi? Or should it be grid cells
• Was the population data regridded to the MESSy grid? Or how did you determine the population density for each of the points in Figure 6
• Line 335: “with a higher than model resolution” – what is meant?
• Line 352: indivuduals should be individuals
• Line 378: “referred to as PAE_GB”
• Figure 9: the symbols for “Before DS” are tricky to see in the plot, please consider using another font or color.