The authors conducted a systematic study of cluster hydration in atmospherically important systems. This purely theoretical study primarily focuses on quantum chemical approaches and evaluates them against one another. Such benchmarking is standard yet crucial for future studies. Additionally, the authors enhance their investigations by exploring cluster properties beyond the standard quantum chemical framework. I commend the authors for their efforts in this regard!

The benchmarking is extensive and done with high rigor. The group’s ability of carrying out such method comparisons is well known and overall top quality, and I have very little to comment or criticize about.

A general remark: While the authors note that no good reference data exist for cluster thermodynamics, I find it useful and interesting that they investigate the potential effects of anharmonicities. These systems likely exhibit significant thermal fluctuations, making the standard harmonic approach inadequate. Therefore, I believe the results and speculation are sufficient as they are and are generally highly welcome.

The nucleation rate section (3.5) is clearly the weakest part of the study, which is unfortunate because it discusses the real-life implications. I will elaborate on my critique below:

In the ACDC simulations, the limiting size is set to 3 acids, 3 bases, and any number of water molecules. Given the studied concentrations, the system size is too small. Except for a few extreme cases, the critical cluster is not included in the set of studied clusters. This is briefly mentioned on Line 465, but not very clearly. Additionally, in the supplementary information, they state:

“Because the maximum simulated cluster size was relatively small, the critical cluster size, where growth starts to vastly outweigh evaporation, might not be included” and “Elm et al.(6) coined the term: potential particle formation rate Jpotential, to indicate that the results cannot directly be related to the actual particle formation rate J, but are rather a measure for the importance of different compounds in cluster formation.”

And the article cited in the SI (Elm et al., 2017) does not include the concept or its coining. It is quite frustrating that authors miscite, but come on, it's one of your own!

If nothing else, I strongly think the authors should at least explicitly state that the nucleation rates studied are not true nucleation rates. Currently, the results may mislead readers into thinking otherwise. As noted in the SI, the measure used here is the potential particle formation rate, which could serve as a good proxy. However, given the magnitude of the effect of hydration (within one order of magnitude), this analysis needs to be more rigorous.

Let me elaborate on my point: The idea that incomplete cluster formation free energies can indicate the magnitude of the nucleation rate applies when comparing nucleation capabilities among different chemistries (e.g., SA-AM to SA-DMA). However, in this case, the comparison is made against hydration or, more precisely, relative humidity. The authors demonstrate, particularly in fig. 7 and 8, that the level of hydration depends on cluster size in a non-monotonic manner. Therefore, extrapolating the level of hydration to larger, unknown clusters lacks proper justification.

To provide a more theoretical perspective: The nucleation rate largely depends exponentially on the free energy of the critical cluster only: J ~ exp(-dG*/RT). Thus, J primarily depends on the height of the nucleation barrier, not its slope. Consequently, if hydration significantly decreases free energy at the critical size but has smaller effect around it, the nucleation rate will increase notably and “unpredictably”. The same reasoning applies in reverse if the critical cluster is hydrophobic among otherwise hydrophilic clusters.

I really don’t understand why the authors chose to study these concentrations. Since they are not directly comparing their results to any experimental or measurement data, they could select conditions where the critical cluster appears within the set of clusters. I believe that limiting the range of critical clusters is a lesser issue than simulating incomplete systems. I kindly suggest that they consider running the simulations at other concentrations.

Some minor comments and questions:

Line 207: Coagulation loss is referred to as CL, but it is also CS (SI, p. S6). Should CL/CS have a unit?

Line 306: The authors state that they have considered multi-conformer Boltzmann averaging, as explained later in Section 3.3.3. However, eq 4 does not resemble Boltzmann averaging. Could the authors elaborate on this approach?

Figure 8 is somewhat difficult to read because of the various colors, markers, line types, and shaded areas. I suggest that the authors consider dividing the data into three separate plots or finding an alternative way to present it for maximum clarity. Otherwise, the visual elements of the manuscript are clear and well presented.

L460: “Since evaporation rates depend exponentially on binding free energies, an error of just 3 kcal mol−1 can likewise produce a factor of 20 difference in J.” Is this correct? I would assume it is 3RT, approximately 1.8 kcal/mol: exp(1.8 kcal/mol / RT) = exp(3) = 20.

Referee’s comments on AR-2025-30

The manuscript by Neefjes et al. evaluates the accuracy of quantum chemical methods in predicting electronic binding energies and equilibrium geometries of clusters containing various atmospheric acids, bases, and up to five water molecules. They identify optimal methods for different purposes, use the most reliable methods to investigate the magnitude of thermochemical corrections (anharmonicity, multi-conformer contributions) and, ultimately, to calculate clusters hydration distributions and particle formation rates (J) for three key systems: SA–AM, SA–DMA, and MSA–MA. A key finding is that while hydration does occur and can stabilize clusters, its effect on enhancing NPF rates is generally modest (typically less than a factor of 2) under typical atmospheric conditions, contradicting some previous studies that reported very large enhancements. The work is methodologically sound, and the conclusions are well-supported by the data. It provides invaluable practical guidance for the aerosol community and further clarifies long-standing questions regarding the role of humidity in new particle formation (NPF). I recommend publication in Aerosol Research after the following few minor comments have been addressed.

1. The authors correctly note in the conclusion that humidity may play a more significant role in later growth stages (e.g., for larger clusters or aerosol particles), and this distinction could be emphasized earlier to provide context.
2. In the methodology, considering the "up to five distinct low-energy configurations", what would be the potential for missing significantly populated conformers in this sampling strategy?
3. Page 12, Line 280: "ωB97X-3 could serve as an efficient method..." – There is a typo here, it should be "ωB97X-3c".
4. Page 2, Line 59. The sentence “In recent decades, computational…” deserves few more citations
5. What do the authors mean by “Intrinsic basis set” and “User-supplied basis set” in Table 1, while empirical, semi-empirical and other methods are listed instead? Consider providing clarifications or renaming the headers.
6. The discussion of the "Halonen limit" is excellent for setting an upper bound, but the manuscript could more clearly state what the authors believe is the most likely realistic scenario based on their umbrella sampling and anharmonicity analysis. Is the truth closer to the QHA result or the Halonen limit?

The manuscript presents an extensive benchmark study of quantum chemical methods for the calculation of structures and energies of molecular clusters of atmospheric relevance. Furthermore, it evaluates the impact of various thermochemical corrections on cluster energies and distribution of hydrates. Finally, the results are applied in the calculation of particle formation rates. The overall quality of the manuscript is good, and the data is clearly of relevance. However, as the focus of the study is on benchmarking different methods for energy calculations, whereas calculations of particle formation rates only represent a minor part of the manuscript with less novel insight, the authors might want to adjust the title of the manuscript to reflect this.

In the description of the calculations, it is somewhat unclear at which levels of theory geometry optimization were performed. At the end of page S2 it is stated that the generated cluster geometries are "used as a starting point for geometry optimizations with the quantum chemistry methods included in the benchmark." This would include all methods used in the electronic binding energy benchmark section. If that is the case, why were not all these model chemistries included in the equilibrium geometry benchmark? In case geometries were not optimized at all these levels, this should be clarified. In that case I would also suggest reorganizing the manuscript by swapping places between the two sections, as the method recommended based on the equilibrium geometry benchmark is used to generate the structures used for the electronic binding energy benchmark.

The authors seem to misunderstand or at least misrepresent the way that scaling factors for calculated vibrational frequencies are commonly used. Scaling factors are described to be used to adjust for deviations of harmonic frequencies from their anharmonic counterpart, whereas they are indeed generally used to adjust calculated frequencies (harmonic or anharmonic) to match experimental frequencies. Although the lack of anharmonicity is often a main contribution to the deviation, it is not necessarily dominant.

In this context the authors also somewhat misrepresent the study by Jacobsen et al. (2013) (line 334-336), suggesting the study's conclusion to be that anharmonic calculations can be replaced by scaling factors, whereas the study actually compares scaled harmonic frequencies to scaled(!) anharmonic frequencies.

Given this context, the authors' approach to determine scaling factors using anharmonic frequencies calculated at the same level of theory as reference makes limited sense. Certainly, as we know from Jacobsen et al. (2013) that only calculating anharmonic frequencies using simplified model chemistries might not be sufficient to reproduce experimental spectra. A better approach would be to make use of the experimental data that the authors have gathered and determine scaling factors based on those.

It should also be mentioned that scaling factors for r2SCAN-3c have previously been determined (Tikhonov et al. (2024), https://doi.org/10.1002/cphc.202400547).

Section 3.3.3: It would be interesting to know how the number of conformers that are taken into account changes with cluster size, as this could be a relevant factor for the size of the correction.

Section 3.3.4: It seems that the authors do not fully trust their own methodology - the corrections determined by their umbrella sampling approach clearly exceed the limit determined by Halonen in several cases (Figure 5). Yet the authors decide not to use the umbrella sampling results, but instead use the limit as an upper bound. As it is not used or discussed any further, it is not clear why this section is needed.

Minor comments:

Figures 1, 6, and S10: The structure of TMA is depicted from an unfortunate perspective making it appear planar and hiding several hydrogen atoms.

Line 529: "Henschel et al. (2014)" should likely be "Henschel et al. (2016)"?

Section S1: The authors state that "reacted" structures are filtered out. What exactly does this refer to - do proton transfer reactions fall under the definition of "reacted"?

Page S3, bottom: The authors state the structures were "refined" at DLPNO-level of theory. Please specify what is meant by this - single point energy or geometry optimization.