In a previous paper, Svenhag et al (GMD 2024) implemented a mechanism for new particle formation (NPF) from H2SO4 and NH3 in EC-Earth and found minor differences in CCN, but despite this they found a change to the radiative effect of clouds of 0.28-1Wm-2. They performed a model evaluation, checking the aerosol size distribution at 12 surface stations worldwide.

In this paper, the authors focus on simulating NPF events  at two surface stations using (I think) the same EC-Earth simulations, and compare them to an ADCHEM model run, presumably one of those published in de Jonge et al (E, S & T 2024). A new EC-Earth simulation without NPF is included, but only features in part of the analysis.

The simulations overestimate primary emissions in winter. ADCHEM has some different NPF mechanisms including iodine and dimethylamine, and no organic NPF, and performs better.

There’s an interesting set of plots comparing simulated and observed size distributions and “bananas” at two sites.  However, given that most of the simulations (as far as I can tell) are already published and a very similar evaluation of ADCHEM at these sites was already published by de Jonge et al (2024) e.g. their Figure 3, it left me wondering whether the paper currently satisfies the “substantial new concepts, ideas, methods, or data” review criterion for ACP. I think it could, if the analysis were broadened and deepened to probe the model more comprehensively and replace some of the speculations in Section 3.2 with additional detailed analysis or sensitivity studies. This is likely to need new simulations.

Major comments

In my assessment, the paper relies for its novelty on two aspects

1. The evaluation of simulated size distributions as a function of time (“banana plots”) in EC-Earth, which is interesting and not often done with aerosol-climate models.
2. The comparison between ADCHEM and EC-Earth.

One could argue that the value of (1) is limited for people outside the EC-Earth community because the size distributions are dominated by the effects of the coupling to the IFS meteorology, and it’s hard to disentangle the odd behaviour resulting from this this from the effects of the NPF. However, it’s still interesting to see.

The value of (2) is currently limited since the authors only show one ADCHEM simulation with very different nucleation mechanisms to the EC-Earth simulations. Perhaps there is an opportunity here to analyse the other ADCHEM simulations published by de Jonge et al, which include simulations that only include H2SO4-NH3 NPF that would (at least to an outsider) seem to be a fairer comparison to the EC-Earth CLUST simulations.

 If the sentence in the abstract “When comparing diurnal EC-Earth model results with ADCHEM and observations, we establish that using solely organic-H2SO4 nucleation parameterization will underestimate the aerosol number concentrations” is not to be misleading, the authors should test what happens when ELVOC nucleation from Riccobono et al (2016) is included in ADCHEM. Currently ADCHEM does not tell us about the organic-H2SO4 nucleation parameterization.

Minor comments

In Figure 2e, NPF is so non-linear that the annual mean NPF rate must be dominated by values close to zero. Would something like the 95^th percentile make more sense instead?

Using the Jokinen et al (2015) yields for ELVOC with the Riccobono et al 2014 nucleation mechanism likely leads to high uncertainty. More discussion of this might be useful in the light of developments to organic aerosol schemes in ADCHEM by the paper’s coauthors (e.g Roldin et al, Nat Comms 2019).

A table of the NPF mechanisms in ADCHEM, and in general a more detailed description of how ADCHEM simulates particle formation and growth and how fair the comparison with a climate model is, would be useful.

The differences between the CLUST schemes are described, but the value of including two EC-Earth simulations with different CLUST NPF mechanisms would be greater if differences  (or similarities) between the behaviour of the simulations (ie the number of particles formed) with these schemes were discussed in the text.

I liked Figure 3 in principle, but it could be tidied up a bit with larger labels, especially the colorbar. Also just reading the caption I was a bit confused why ADCHEM had no aerosols at Hyytiala but did have the data at Hyltemossa (maybe just add to the caption “, while for Hyltemossa the simulation was run from to ”).

Figure 4 also needs larger labels.

The sudden discontinunities in the aerosol size distribution around midday each day are attributed to the coupling of the chemical transport model to IFS. This is interesting. Because NPF is nonlinear, you would expect a systematic bias to result. Can this be studied further? How hard would it be to increase the frequency of the coupling?

Line 315 and elsewhere: sentences could be improved, a number of typos to fix.

My review here below is formatted as direct answers to the questions posed for consideration in ACPs review criteria.

Does the paper address relevant scientific questions within the scope of ACP?

This paper addresses the questions of how to represent aerosol nucleation and growth in global models, and how to evaluate these representations, both of which are within the scope of ACP.

Does the paper present novel concepts, ideas, tools, or data?

The paper presents novel model outputs to compare with field observations, as well as a novel evaluation of EC-Earth3 using both observations and a more complex chemical model. In particular, this study’s use of both observations and detailed chemistry process model to understand why EC-Earth and observations differ, and to check things are “right for the right reasons” is very valuable.

Are substantial conclusions reached?

Substantial conclusions are reached regarding the need to include ammonia nucleation mechanisms in EC-Earth3 to better represent nucleation and growth in European boreal forest, and the necessity of evaluating seasonal and even hourly outputs to properly assess model representations of aerosol nucleation and growth.

Are the scientific methods and assumptions valid and clearly outlined?

While much of the method used and most of the assumptions made are valid and clearly outlined, some of the assumptions do not seem valid or well justified. I will detail the areas I consider problematic in this respect here below:

The introduction refers to Hyytiälä and Hyltemossa stations as “not heavily impacted by anthropogenic influence” (line 76-81) but then goes on to discuss higher levels of NH3 and H2SO4 at Hyltemossa due to anthropogenic activity. This suggests that at least the Swedish station is influence by anthropogenic activity. We are also aware of anthropogenic activity influencing NPF at the Finnish station, through the presence of NH3 and elevated H2SO4. Since NPF mechanisms and growth of small particles are sensitive to small concentrations of NH3 for example, we cannot justify these as representative natural sites. This does not invalidate the methodology, but greater care should be taken to present the conditions of these measurement sites and not try to present them as representative of the broader northern midlatitude region. Also, this study specifically addresses NH3 NPF, so if the sites were not anthropogenically influence this would be a problem since we would not expect any influence of NH3 in that case.

This problem of representativeness appears again in the conlusions ( line 355). Text states that CLUST mechanism accounts for more NPF between 100m altitude and upper troposphere “especially to northern mid-latitudes”. Firstly, since only data and modelling were presented for northern mid-latitudes, it is not justified to imply these results are applicable elsewhere. Secondly, it is not justified that the 2 presented site are typical for northern mid-latitudes. Indeed, when we consider that the major conclusion is the need to include ammonia nucleation and growth at the 2 sites presented, we see that we are dealing with anthropogenic influence that would likely not apply to the same extent when considering boreal forest sites in north America. The EVOC representation from Riccobono may be more applicable to the emissions from European boreal forest than north American or Siberian boreal forest, and then of course there are marine regions in northern mid latitudes as well.

Are the results sufficient to support the interpretations and conclusions?

While the major conclusion that including ammonia nucleation mechanisms at the sites investigated brings model aerosol size distributions closer to observed values in spring and summer, a number of the finer points appear either not completely supported by the data presented, or the data is presented in such a way that it is not possible to tell if it supports the conclusions reach. I will detail the problems I came across here below. While I refer to parts of the text using quotation marks, I mostly only paraphrase the text for brevity.

Line 226: low availability of condensable vapours postulated to explain low EC-Earth number concentrations but then shown to be not the case because ADCHEM can produce sufficient number with same condensable vapour concentrations. So why leave this in as a possible explanation? Isn’t the benefit of including ADCHEM to be able to show that this is the mechanisms not the vapour concentrations that are the problem?

Line 245: decrease in J for control case explained by decreasing ELVOC concentrations with altitude (fig 2a), which makes sense. But NH3 concentrations also decrease with altitude (fig 2c) and CLUST Js do not show the same decrease with altitude. A more nuanced discussion of the changes in J with altitude for the different mechanisms is needed here.

Fig 3 line 259: “ADCHEM better reproduces observations than EC-Earth3” – Hyytiälä ADCHEM appears to see no aerosols at all. Could this just be a plotting error?

Line 265-268: It is unclear why the lower Aitken mode concentrations in the control case are ascribed to the weakness of the nucleation, but the lower Aitken mode concentrations in the CLUST cases are ascribed to limitations in how aerosols grow between modes in the model.

Line 276: “fig 4k ELVOCs are low on April 6^th Hytlemossa” – figure shows very similar ELVOC concentrations to all other days, what do the authors mean by low here?

Line 277: “April 6^th Hytlemossa NH3 in fig 4 low compared with spring average shown in fig A5” this is very hard to see since the scale on fig A5 makes it hard to pick out where April 6^th is and it requires going between two very separate figures. Suggest either marking April 6^th clearly on fig A5, adding an average line on fig 4, or some other combining of the figures.

Line 283: “H2SO4 generally higher in model level 2 than model level 1 in fig 4” – H2SO4 seems almost identical in both levels. Either a clearer figure is needed to show this is the case, or there is some error in interpretation here,

Line 296: “High ELVOC-H2SO4 nucleation during the 2 week periods for both stations shown in figure 6 yield lower surface aerosol concentrations compared to NH3 nucleation as shown in figure 1” – figure 1 only shows seasonal averages, so I don’t see how conclusions can be drawn by comparing nucleation rates from specific 2 week periods to number concentrations in the seasonal averages. Could the resulting number concentrations from the days shown in fig 6 not be included to make a robust conclusion here?

Line 299: “J is higher in second model layer than surface layer in fig 2” Figure 2 does not indicate where these model layers are and I suspect that both surface and 1^st model layer are so close together at the bottom of this figure as to make it hard to see the changes. A clearer figure would be needed to justify this conclusion.

Line 304: why especially above 100m? Fig A2 shows J>1e-3 below 100 m also.

Line 308 suggests uncertainties on atmospheric concentrations of amines and iodine greater than those of ammonia, ELVOCs and H2SO4, but no sources cited to justify this claim. Considering we lack ammonia observations for most of the atmosphere, and large areas without many observations of H2SO4 and ELVOCs I’m not convinced this is the case.

Conclusion line 356 states that CLUST nucleation mechanism agrees with detailed modelling in ADCHEM; but most of the results presented show that the CLUST nucleation schemes produce less nucleation and growth than ADCHEM and the observations at the 2 sites. The conclusions here also state that CLUST nucleation mechanism agrees with results of Zhao et al (2024), but no comparison with nucleation rates from Zhao et al (2024) was presented in the manuscript, unless I have missed something?

Fig 3: ADCHEM seems to have nucleation when none is observed for Hyltemossa – this is not addressed. EC-Earth3 Hyltemossa seems to see some nucleation for all 3 observed events with all model variants, just less intense and without growth. This is not mentioned in the discussion.

Is the description of experiments and calculations sufficiently complete and precise to allow their reproduction by fellow scientists (traceability of results)?

Yes

Do the authors give proper credit to related work and clearly indicate their own new/original contribution?

Yes.

Does the title clearly reflect the contents of the paper?

The title only partialy reflects the content of the paper. It makes no mention of the use of a complex chemistry model to improve comparison between the global model and the observations, fails to indicate that this paper is specifically addressing the role of ammonia nucleation, and refers to “boreal forests” generally, when the paper only deals with European boreal forest sites.

Does the abstract provide a concise and complete summary?

Yes, the abstract provides a very clear summary of the work. 

Is the overall presentation well structured and clear?

In general, the authors ask the reader to jump between figures a lot to support the scientific conclusions they are drawing, and the figures are not laid out in ways to make it easy to compare between them. This is a problem for readability and makes it hard, as a reviewer, to see if the data presented really support the conclusions drawn.

Is the language fluent and precise?

There are several small instances where use of language, or spelling or grammatical errors hinder readability of the paper. The ones I’ve noted are as follows:

Line 231: is this saying that the CLUST higher Aitken mode concentrations are due to transport either from above or from neighbouring grid boxes? This could be more clearly stated.

Line 246 and fig A1: “CLUST schemes produce highest J in spring and autumn at high altitude”  - unclear. do the authors mean that in spring and autumn at high altitude the CLUST Js are higher than control, or that in spring and autumn the high altitude Js from CLUST are higher than low altitude Js from CLUST, or that high altitude Js from CLUST are higher in spring and autumn than summer and winter? Either way it is quite hard to see this from the image plots, and without knowing what the authors classify as high altitude – UTLS? Above the BL?  - perhaps time series of overage J within altitude bins might be clearer? Along with more precise text.

Line 249-251: unclear – I’m not at all sure what is meant here

Line 277: “this variation in event strength is similar to autumn cases”. It is unclear what the authors means by variation in event strength since the text is talking about a single event (April 6^th).

Very minor, but noted here in-case it is helpful to the authors:

Line 16: particular – particulate

Line 162: utilized -> used (clarity of language)

Line 163: spurious comma after “and NPF”

Fig 5 caption: spelling mistake

Are mathematical formulae, symbols, abbreviations, and units correctly defined and used?

Generally yes, but there are some instances where clarity could be improved that I note here below.

Line 140: RICC method and DLPNO method acronyms and methods not fully explained – hard to understand the difference between the 2 datasets here

Line 142: do HIGH and LOW inputs mentioned here refer to CLUST-High and CLUST-low mentioned above? The change in terminology is confusing.

Should any parts of the paper (text, formulae, figures, tables) be clarified, reduced, combined, or eliminated?

There are a number of instances where either the text, figures or tables were unclear. I detail those I found here below:

In general the language used to refer to the different nucleation schemes could be clearer. Once I had read enough of the manuscript I understood that base = binary + Riccobono, CLUST = binary + Nh3 ternary, and then Clust+Riccobono is binary + NH3 ternary + Riccobono, but this could be made clearer in table 1, and earlier in the text.

Table 1: fuller description of the difference between the nucleation schemes would be helpful here. It is hard as a reader who isn’t intimately familiar with Svenhag 2024 to understand from the text and this table the differences between the different model runs

Fig 1: very difficult to see what is going on in nucleation mode because of dominance of accumulation mode. Can’t see ADCHEM line for Hyytiälä except for in summer.

Table A1 and line 233-237: The CRE change from CLUST High in summer for Hyltemossa is also very large and not mentioned, and strange that for the same period and simulation the change for Hyytiälä is 0. The authors are correct to point out the problem of looking only locally at CRE and DRE changes when advection and transport play such a role. The very limited discussion presented here however raises more questions than it answers. Either a more thorough discussion is warranted, or the CRE and DRE discussion should be omitted from this paper altogether (another paper by the same author is referenced – so perhaps it is not necessary to include that analysis here also).

Line 240 and fig 2: ELVOC-H2SO4 and NH3-H2SO4 don’t directly relate to how the mechanisms are named in the legend, so harder for the reader to quickly relate text to plot. It would help to remind that the first is called “control” and the second is both of the “CLUST” cases. It would help to relate the second model layer to a pressure since that is the vertical axis of the graph. Or even to put a line on the graph indicating where the 2^nd model layer starts. Also it is not clear from the figure that the CLUST cases and control case are similar at altitudes below 100m, which is implied in the text.

Fig 3 and 4: would be helpful to have these on same x-axis for direct comparison

Fig 4: what are the dashed lines in e,k,f,l? also e and k show hints of lines in multiple colors but the legend says these are only the no NPF case, so then what are the other colors for?

Are the number and quality of references appropriate?

In general, yes.

There was one instance in the introduction where the availability of vertical profiles of aerosol properties seemed to be understated and the relevant references missed. This is at line 70-75, which mentions a “lack of vertical profiles” and “aerial campaign measurements are not yet sufficient” for sub-100nm aerosol observations. While I believe there may not be vertical profiles made directly over both stations considered here, some airborne observations have been made over Hyytiälä and campaigns over other regions have made a substantial number of vertical profiles from aircraft e.g. such as ATom, Café-Brazil etc. The state of the field would be better represented if reference were made to these, although they are may not help directly with the analysis presented here.

Is the amount and quality of supplementary material appropriate?

The reader is asked frequently to refer to supplementary figures to justify major conclusions in the main text. It might improve readability if more of the relevant parts from supplementary figures were combined with the relevant figures in the main text.

I have mentioned above a number of areas where conclusions drawn do not seem to be fully supported by the data presented. It may therefore be necessary to include further supplementary material, but in my opinion, the paper might instead benefit from changes to the main figures presented and a re-evaluation of some of the conclusions drawn.

1. Does the paper address relevant scientific questions within the scope of ACP?

Yes. The authors examine the representation of particle formation and growth in the Earth System Model EC-Earth3. They run EC-Earth3 with different new-particle-formation schemes. They focus on two boreal forest stations in Finland and Sweden. They compare EC-Earth3 with observations and the Lagrangian model ADCHEM.

2. Does the paper present novel concepts, ideas, tools, or data?

Yes. A novel aspect is the comparison of EC-Earth3 and ADCHEM including aerosol size distributions resolved over time.

3. Are substantial conclusions reached?

Yes. But the authors examine only two locations in Finland and Sweden. It would be helpful to discuss how representative their results are for other locations.

4. Are the scientific methods and assumptions valid and clearly outlined?

To some extent. Some parts of the methods section are not clear to me:

- line 112: what are ”specific dimensions”?

- line 127: what does ”explicitly modelled” mean?

- line 138: how are the five dimensions of the lookup table discretized?

- line 139: how is the ”cluster scavenging sink” computed?

- line 142: what are the dimensions of the IPR lookup table?

- line 169: there seem to be different emissions for EC-Earth3 and ADCHEM. how does that influence the results?

- line 167: how is the trajectory discretized in time? how is the column discretized in space?

- line 181: ”Particles and gasses were mixed by use of the GDAS” how does that work in ADCHEM?

- line 183: ”The ADCHEM model thereby attempts to reproduce the concentration of gasses and particles” how does that work in ADCHEM?

- line 231: what grids are used in EC-Earth3?

5. Are the results sufficient to support the interpretations and conclusions?

Yes.

6. Is the description of experiments and calculations sufficiently complete and precise to allow their reproduction by fellow scientists (traceability of results)?

Mostly yes. Some parts of the methods section rely on previous publications and could be revised to be more self-sufficient.

Do the authors give proper credit to related work and clearly indicate their own new/original contribution?

Yes.

8. Does the title clearly reflect the contents of the paper?

The title of the paper seems to be too generic. The authors do not examine boreal regions in general but two forest stations in Finland and Sweden.

9. Does the abstract provide a concise and complete summary?

Yes.

10. Is the overall presentation well structured and clear?

Yes.

11. Is the language fluent and precise?

Mostly yes. Some sentences are rather long and complex and should be rephrased for a better readability.

12. Are mathematical formulae, symbols, abbreviations, and units correctly defined and used?

Mostly yes. Mathematical symbols sometimes appear in text font instead of math font. For example, particle diameter d on lines 111 and 112 or nucleation rate J on line 124. The long terms on lines 176-178 should be simplified.

13. Should any parts of the paper (text, formulae, figures, tables) be clarified, reduced, combined, or eliminated?

Some figures should be revised. There are no subplot labels in figures 3, 5, A1, and A6. The font sizes in figures 3, 4, 5, 6, A4, A5, A6, and A7 are too small. The captions of some figures are not self-explanatory. In figures 3 and A6, it is unclear why the ADCHEM base case has a non-zero value of 10 cm-3. In figures 4, 6, and A7, its is unclear what ”modelled layer 1 and 2” or ”level 1” and ”level 2” mean.

14. Are the number and quality of references appropriate?

Yes.

15. Is the amount and quality of supplementary material appropriate?

N/A.