the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 13 Mar 2026
Atmospheric new particle formation enhanced by tricarboxylic acids
Abstract. Organic molecules contribute significantly to the formation of aerosols in the atmosphere, forming what is known as secondary organic aerosols (SOA). The organic molecules are emitted as volatile organic compounds (VOCs), and undergo a number of reactions in the atmosphere. Due to the variety in both VOCs and reaction pathways, it has been difficult to elucidate the exact structure of an organic molecule that is able to drive new particle formation (NPF). We have studied the NPF ability of three different oxygenated organic molecules (OOM); 3-methyl-1,2,3-butanecarboxylic acid (MBTCA), carboxyheptanoic acid (CHA) and pinyl diaterpenylic ester (PDPE). These all contain three carboxylic acids, which previous work suggest is a good candidate for driving NPF, and have been observed in the atmosphere, as well as in lab experiments. Using computational methods, we studied the (OOM)1−2(SA)0−2(base)0−2 clusters, where SA = sulfuric acid and base = [ammonia (AM), methylamine (MA), dimethylamine (DMA) and trimethylamine (TMA)]. Geometry optimization and thermochemical parameters are calculated at the ωB97-XD/6-31++G(d,p) level of theory, and single point energies are calculated at the DLPNO-CCSD(T0)/aug-cc-pVTZ level of theory. We found that PDPE was able to produce the most stable clusters, presumably due to its high flexibility. Cluster formation potentials are simulated using the Atmospheric Cluster Dynamics Code. We found that all three OOMs were able to enhance cluster formation for the (OOM)(SA)(base) systems by 2–3 orders of magnitude for the most significant systems. Especially the (OOM)(SA)(DMA) system has a high cluster formation potential, with similar trends across all three OOMs.
Competing interests: At least one of the (co-)authors is a member of the editorial board of Aerosol Research.
Publisher's note: Copernicus Publications remains neutral with regard to jurisdictional claims made in the text, published maps, institutional affiliations, or any other geographical representation in this paper. While Copernicus Publications makes every effort to include appropriate place names, the final responsibility lies with the authors. Views expressed in the text are those of the authors and do not necessarily reflect the views of the publisher.- Preprint
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- RC1: 'Comment on ar-2026-10', Theo Kurtén, 24 Mar 2026
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RC2: 'Comment on ar-2026-10', Anonymous Referee #2, 29 Mar 2026
Decision: Minor revision. The authors have the methodology, the data, and the conceptual framework to produce an outstanding paper, but avoid some essential work in the discussion and presentation, leaving the paper in parts underdeveloped. I suggest to accept the paper after revisions, that do not necessitate further calculations. The authors should consider addressing the following two points: (A) the tables, figures and plots should be revised. I attached some specific suggestions in the PDF. This can be considered as minor revision. (B) The comparison of the tricarboxylic acid results presented in this work with the "cluster-of-functional-groups" approach from their previous work should be addressed in more detail. One worked-out comparison in the discussion section would probably suffice as minor revision.
(1) Scientific significance: Excellent. The chosen systems follow a consequent strategy building on previous work, and the results enable a meaningful discussion of the "cluster-of-functional-groups" approach introduced by the authors earlier. However, this discussion remains very superficial in the present work and is left as an open question in the conclusion. Notably, the authors themselves propose comparing the current results with their previous ones as a future task. It is unclear why this comparison is not carried out in the present work. Should the "cluster-of-functional-groups" concept be properly and thoroughly discussed in light of the new results, this would elevate the manuscript's scientific significance.
(2) Scientific quality: Outstanding The employed methodology is appropriate for the given task, is grounded in extensive prior benchmarking, and the approximations are communicated transparently. The results are discussed with care, and the written text contains correct statements and useful discussion. The scientific approach and methodology represent the state of the art, established by the authors over the last decade, and are of outstanding quality in the field. This aspect does not hold the paper back.
(3) Presentation quality: Good. The presentation of results in the written text is handled with care. However, the presentation in the figures is flawed in several places, bringing the overall assessment down. These issues are straightforward to address, and specific suggestions are provided in the attached PDF. The presentation quality can be easily elevated.
- AC1: 'Comment on ar-2026-10', Astrid Nørskov Pedersen, 20 May 2026
Status: closed
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RC1: 'Comment on ar-2026-10', Theo Kurtén, 24 Mar 2026
Astrid Norskov Pedersen, Yosef Knattrup and Jonas Elm have used computational methods to study the effect of three atmospherically relevant tricarboxylic acids on sulfuric acid - base clustering. I collaborate extensively with professor Elm, and in the interest of full transparency I am therefore writing this review openly (i.e. without the typical anonymity of peer review in our field). Readers (and editors) may themselves then judge how they wish to weight my review compared to that of other, presumably less closely affiliated, reviewers. (For example, it is probably not a surprise to anyone that I approve of the general methodology used here, having been involved in numerous similar studies myself…)
With this caveat out of the way, my overall impression of the manuscript is very positive: this is a well-conducted study on a relevant topic, carried out with appropriate methods. Nevertheless, there are a few issues I’d like to discuss with the authors. Please bear with me for a relatively lengthy review, which however contains only relatively few and simple suggested “action items” for the authors. (To aid their work, I’ve spelled out these suggested action items at the end of each longer issue.)
1)Page 3, lines 66-68. This slightly misrepresents the chemistry, and the “ester issue”. First, gas-phase dimers are believed to (predominantly, though not necessarily solely) be formed by cross-reactions of PEROXY radicals. (The reaction does indeed go through a alkoxy-alkoxy intermediate, but that mechanistic detail is less relevant to this big-picture overview, and probably doesn’t even need to be mentioned here). Second, the Peräkylä 2023 paper suggests specifically that part of these gas-phase dimers are actually esters rather than peroxides. Third, the Kenseth paper then shows that esters actually measured (by cromatography-based methods) from the particle phase are almost certainly formed by condensed-phase reactions, i.e. the condensed-phase esters are not the same (= do not have the same structure or formation mechanism) as the (speculated) gas-phase esters. This does not prove that the gas-phase esters don’t exist - it is indeed quite difficult to explain the mass spectra e.g. in Peräkylä (and many other studies) without them. However, it does suggest that if formed, these gas-phase esters very rapidly rearrange (react/isomerize) once in the condensed phase. (Based on discussions with Christopher Kenseth himself, there are plenty of potential mechanisms for this). While the authors are of course correct that molecules formed exclusively in the condensed phase will not participate in NPF, the existence (or more accurately, the likely concentration range) of gas-phase esters should still be considered an open question. (Suggested action item: please reformulate accordingly).
2)On the subject of likely concentration ranges, I’m interested in hearing the rationale for the 1-10 ppt range used for tricarboxylics in the modelling.
I also did some back-of-the-envelope calculations, in the spirit of asking, in a manner hopefully familiar to the authors, “what would it take for tricarboxylics to reach a certain concentration?”. Let’s first assume the precursor is something like alpha-pinene, with typical (non-winter, forest) mixing ratios (based on a quick literature browsing) between 1 ppt and 1 ppb (i.e. about 2.5E7…2.5E10 molecules per cm3). The main (daytime) oxidant for alpha-pinene is usually OH, with a concentration of about 1E6 molecules per cm3, and a reaction rate with a-pinene of around 5-6 x 1E-11 cm3 per molecule and second at the relevant temperatures (using the rate expression from the MCM website). Let’s say the molar (not mass) yield of tricarboxylics is somewhere between 1 and 10% of the oxidation (noting that the latter is certainly an overestimate). So then the production rate of tricarboxylics is between 15 and 150 000 molecules per cm3 and s. Let’s round up to 20…200 000 to account for O3 oxidation also (and get rid of a significant figure). To get a steady-state concentration, we now need a loss term. For a highly soluble and condensable, but chemically relatively stable, molecule like a tricarboxylic, the condensation sink (CS) should be a good estimate of the loss in the absence of substantial nucleation by tricarboxylics (I’ll come back to this soon!). Typical CS values are between 0.01 and 0.0001 per s, with the former corresponding to very polluted and the latter to very clean areas. So we get (setting P = CS x [tricarb], where P is the production rate derived above, and solving for the tricarboxylic acid concentration [tricarb]) a steady-state concentration of 1500 per cm3 (low-end source, high-end CS) to 1.5E9 per cm3 (high-end source, low-end CS). OK, 10 ppt = 2.5E8 is within that range. However to actually get to 10 ppt, we need to simultaneously assume (i.e. the answer to the “what would it take” question is):
-a high-end precursor concentration (close to 1 ppb)
-a very high yield of tricarboxylics from oxidation (closer to 10% than 1 %)
-a very low condensation sink (at least not above 0.001 per second).
So while we cannot rule out 10 ppt based on a back-of-the-envelope analysis, it’s worth noting that it is certainly a “maximum possible upper limit” type of estimate. (It’s worth noting that we probably CAN rule out e.g. 100 ppt!)
I would also note that if the tricarboxylics are driving substantial nucleation, then that is an additional loss term that quickly limits the steady-state concentration. (E.g. a J - rate of 1 per cm3 and s, with on average N tricarboxylics in the nucleating cluster, would correspond to a loss rate of N per cm3 and s…) So we can’t really have tricarboxylic-enhanced J - rates above, or even close to, 0.01 per cm3 and s, and tricarboxylic steady-state concentrations above 1 ppt. On the other hand, nucleation is not inherently a steady-state phenomenon, so I guess we could speculate that tricarboxylics first build up to some > ppt threshold, and are then quickly depleted in a short nucleation burst).
Similar reasoning of course applies to all potentially nucleating complex organics (e.g. “HOM dimers”), not just tricarboxylics - it’s hard to build up substantial steady-state reservoirs of compounds that form with relatively low yields from oxidation of precursors that are not super-abundant to begin with.
Note: while I’d like to hear a bit about the reasoning behind the 10 ppt upper limit in the authors’ response, the only actual action item I’m suggesting for the actual manuscript is that the authors acknowledge that 10 ppt is, while not completely impossible, a very high number indeed for something like a tricarboxylic.
3)What is the rationale for using 278.15 K in the ACDC simulations rather than 298.15 K? Is the cluster formation negligible at 298.15 K? Or have some relevant experiments been reported specifically at this temperature? Also, given that monoterpene emissions are strongly temperature-dependent, is it not even less probable to encounter 10 ppt mixing ratios of tricarboxylics at 278 K?
4)The authors rationalise the stability of the PDPE-containing clusters by the flexibility of the molecule. This may well be true in the context studied here (tricarboxylic acids stabilising sulfuric acid -base clusters), but it contrasts in an interesting way with our recent study (https://pubs.rsc.org/en/content/articlelanding/2025/cp/d5cp01931a) where we found that flexibility, in the sense of efficient H-bonding inside a monomer, is a strong predictor for INefficient pure organic cluster formation among a series of “HOM dimer” candidates. The two statements do not necessarily contradict each other. In addition to focusing on pure organics rather than mixed organic-inorganic clusters, our study did not, for example, contain any di- or tricarboxylics. It could be that the stronger H-bonds formed by the carboxylic acids, especially between them and the inorganic cluster constituents, negates the “efficient internal H-bonding leads to reduced cluster formation potential” effect we reported. However, in an older study involving both me and Jonas Elm, we did find some evidence for intramolecular bonding affecting cluster stabilities also for linear dicarboxylic acids (https://pubs.acs.org/doi/10.1021/acs.jpca.9b08020), albeit only for the largest studied case (suberic acid), and with substantial associated entropy-enthalpy compensation. In any case, it would be interesting to see the lowest-energy (and/or lowest free energy) monomers for the three acids studied here - are there any internal H-bonds in any of them (apart from the presumably relatively weak bond between the C=O and O-H in the SAME carboxylic acid group, which tends to be always present)? The suggested action item here is that at minimum, the authors show and briefly discuss the monomers in terms of potential internal H-bonding, and possibly comment on the different role that “flexibility” seems to be playing in their study and ours.
5)Please add units to the x-axes in Figures 7-9 (I assume ppt).
6)I am a bit worried about the boundary conditions used for the ACDC simulations, and their effect on the results. If I interpret the discussion around line 125-128 correctly, the “pure SA-base” clusters are required to have at least 4 sulfuric acids and 3 bases to be counted as “nucleated”, while the organic clusters need less of each (such that one OOM can replace up to one base, and/or up to two sulfuric acids). I understand the reasoning here - if the OOMs are enhancing the nucleation, then it makes sense that they can be counted as “replacing one or two inorganic molecules”. (For simpler notation, I here refer also to the amines as “inorganic”, despite them having C-H bonds, and thus technically also being organic molecules.) And if we knew for sure that the OOMs are enhancing the nucleation, then probably something like these boundary conditions are, in the absence of data on the larger clusters, possibly the best guess we have for the “cluster formation potential”, as the authors define it. However, as I see it, the main research question of the study is IF the tricarboxylic OOMs have a substantial enhancing effect on the cluster formation potential (and thus nucleation), or not. This being the case, the boundary conditions used here risk assuming the answer to this question before it has even been stated. (Or to put it another way, there is a risk of circular reasoning if the boundary conditions are set based on an assumption that the OOMs enhance nucleation, which in turn is based on simulations using these boundary conditions.) To illustrate what I mean, let’s take a hypothetical “inert” organic compound, which behaves in the following way: 1)1 or 2 inert molecules stick to the inorganic clusters, with low enough evaporation rates that they are essentially always present in them, 2)further inert molecules do not stick to the clusters, and 3)the inert molecules do not affect (in either way) the addition of acids and bases. Using the outgrowing cluster definitions of the authors, they would find a huge “enhancement effect” from such inert organics (as you now only need to form clusters with 3 or even just 2 SA rather than the full 4 SA)- despite them (by definition) not actually affecting the SA-base clustering process at all. This is of course quite hypothetical - no real molecule will behave in this fashion - but it illustrates the problem. I strongly urge the authors to redo the simulations reported in Figures 7-9 so that the boundary conditions (outgrowing cluster definitions) in terms of SA and base molecules required for “nucleation” are exactly the same for both the “organic” and “inorganic” case. If the enhancement effect from these simulations is substantially smaller than that observed in the current simulations, then at least part of the effect originates in the assumed boundary conditions rather than the actual clustering chemistry or physics. The “real” cluster formation potential is then likely to lie somewhere between the two alternatives (outgrowing cluster definitions), and there is probably no accurate way of knowing better without actually studying the full set of (as yet too large to be computed) clusters. This is, I think, an inherent limitation of the otherwise elegant “cluster formation potential” approach. It might be that the best way to present results in these types of cases would be as some sort of shaded areas rather than single lines, with the limits of the shading given by different boundary condition definitions. So my suggested action item is to show these types of shaded areas in Figures 7-9.
7)It might be interesting for readers to see estimates of the radii (radiuses) of the clusters in Figures 4 and 6. (This can be done for example by computing the volume in a quantum chemistry programme, using some reasonable default electron density value, assuming a spherical cluster, and solving for r).
Citation: https://doi.org/10.5194/ar-2026-10-RC1 -
RC2: 'Comment on ar-2026-10', Anonymous Referee #2, 29 Mar 2026
Decision: Minor revision. The authors have the methodology, the data, and the conceptual framework to produce an outstanding paper, but avoid some essential work in the discussion and presentation, leaving the paper in parts underdeveloped. I suggest to accept the paper after revisions, that do not necessitate further calculations. The authors should consider addressing the following two points: (A) the tables, figures and plots should be revised. I attached some specific suggestions in the PDF. This can be considered as minor revision. (B) The comparison of the tricarboxylic acid results presented in this work with the "cluster-of-functional-groups" approach from their previous work should be addressed in more detail. One worked-out comparison in the discussion section would probably suffice as minor revision.
(1) Scientific significance: Excellent. The chosen systems follow a consequent strategy building on previous work, and the results enable a meaningful discussion of the "cluster-of-functional-groups" approach introduced by the authors earlier. However, this discussion remains very superficial in the present work and is left as an open question in the conclusion. Notably, the authors themselves propose comparing the current results with their previous ones as a future task. It is unclear why this comparison is not carried out in the present work. Should the "cluster-of-functional-groups" concept be properly and thoroughly discussed in light of the new results, this would elevate the manuscript's scientific significance.
(2) Scientific quality: Outstanding The employed methodology is appropriate for the given task, is grounded in extensive prior benchmarking, and the approximations are communicated transparently. The results are discussed with care, and the written text contains correct statements and useful discussion. The scientific approach and methodology represent the state of the art, established by the authors over the last decade, and are of outstanding quality in the field. This aspect does not hold the paper back.
(3) Presentation quality: Good. The presentation of results in the written text is handled with care. However, the presentation in the figures is flawed in several places, bringing the overall assessment down. These issues are straightforward to address, and specific suggestions are provided in the attached PDF. The presentation quality can be easily elevated.
- AC1: 'Comment on ar-2026-10', Astrid Nørskov Pedersen, 20 May 2026
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- 1
Astrid Norskov Pedersen, Yosef Knattrup and Jonas Elm have used computational methods to study the effect of three atmospherically relevant tricarboxylic acids on sulfuric acid - base clustering. I collaborate extensively with professor Elm, and in the interest of full transparency I am therefore writing this review openly (i.e. without the typical anonymity of peer review in our field). Readers (and editors) may themselves then judge how they wish to weight my review compared to that of other, presumably less closely affiliated, reviewers. (For example, it is probably not a surprise to anyone that I approve of the general methodology used here, having been involved in numerous similar studies myself…)
With this caveat out of the way, my overall impression of the manuscript is very positive: this is a well-conducted study on a relevant topic, carried out with appropriate methods. Nevertheless, there are a few issues I’d like to discuss with the authors. Please bear with me for a relatively lengthy review, which however contains only relatively few and simple suggested “action items” for the authors. (To aid their work, I’ve spelled out these suggested action items at the end of each longer issue.)
1)Page 3, lines 66-68. This slightly misrepresents the chemistry, and the “ester issue”. First, gas-phase dimers are believed to (predominantly, though not necessarily solely) be formed by cross-reactions of PEROXY radicals. (The reaction does indeed go through a alkoxy-alkoxy intermediate, but that mechanistic detail is less relevant to this big-picture overview, and probably doesn’t even need to be mentioned here). Second, the Peräkylä 2023 paper suggests specifically that part of these gas-phase dimers are actually esters rather than peroxides. Third, the Kenseth paper then shows that esters actually measured (by cromatography-based methods) from the particle phase are almost certainly formed by condensed-phase reactions, i.e. the condensed-phase esters are not the same (= do not have the same structure or formation mechanism) as the (speculated) gas-phase esters. This does not prove that the gas-phase esters don’t exist - it is indeed quite difficult to explain the mass spectra e.g. in Peräkylä (and many other studies) without them. However, it does suggest that if formed, these gas-phase esters very rapidly rearrange (react/isomerize) once in the condensed phase. (Based on discussions with Christopher Kenseth himself, there are plenty of potential mechanisms for this). While the authors are of course correct that molecules formed exclusively in the condensed phase will not participate in NPF, the existence (or more accurately, the likely concentration range) of gas-phase esters should still be considered an open question. (Suggested action item: please reformulate accordingly).
2)On the subject of likely concentration ranges, I’m interested in hearing the rationale for the 1-10 ppt range used for tricarboxylics in the modelling.
I also did some back-of-the-envelope calculations, in the spirit of asking, in a manner hopefully familiar to the authors, “what would it take for tricarboxylics to reach a certain concentration?”. Let’s first assume the precursor is something like alpha-pinene, with typical (non-winter, forest) mixing ratios (based on a quick literature browsing) between 1 ppt and 1 ppb (i.e. about 2.5E7…2.5E10 molecules per cm3). The main (daytime) oxidant for alpha-pinene is usually OH, with a concentration of about 1E6 molecules per cm3, and a reaction rate with a-pinene of around 5-6 x 1E-11 cm3 per molecule and second at the relevant temperatures (using the rate expression from the MCM website). Let’s say the molar (not mass) yield of tricarboxylics is somewhere between 1 and 10% of the oxidation (noting that the latter is certainly an overestimate). So then the production rate of tricarboxylics is between 15 and 150 000 molecules per cm3 and s. Let’s round up to 20…200 000 to account for O3 oxidation also (and get rid of a significant figure). To get a steady-state concentration, we now need a loss term. For a highly soluble and condensable, but chemically relatively stable, molecule like a tricarboxylic, the condensation sink (CS) should be a good estimate of the loss in the absence of substantial nucleation by tricarboxylics (I’ll come back to this soon!). Typical CS values are between 0.01 and 0.0001 per s, with the former corresponding to very polluted and the latter to very clean areas. So we get (setting P = CS x [tricarb], where P is the production rate derived above, and solving for the tricarboxylic acid concentration [tricarb]) a steady-state concentration of 1500 per cm3 (low-end source, high-end CS) to 1.5E9 per cm3 (high-end source, low-end CS). OK, 10 ppt = 2.5E8 is within that range. However to actually get to 10 ppt, we need to simultaneously assume (i.e. the answer to the “what would it take” question is):
-a high-end precursor concentration (close to 1 ppb)
-a very high yield of tricarboxylics from oxidation (closer to 10% than 1 %)
-a very low condensation sink (at least not above 0.001 per second).
So while we cannot rule out 10 ppt based on a back-of-the-envelope analysis, it’s worth noting that it is certainly a “maximum possible upper limit” type of estimate. (It’s worth noting that we probably CAN rule out e.g. 100 ppt!)
I would also note that if the tricarboxylics are driving substantial nucleation, then that is an additional loss term that quickly limits the steady-state concentration. (E.g. a J - rate of 1 per cm3 and s, with on average N tricarboxylics in the nucleating cluster, would correspond to a loss rate of N per cm3 and s…) So we can’t really have tricarboxylic-enhanced J - rates above, or even close to, 0.01 per cm3 and s, and tricarboxylic steady-state concentrations above 1 ppt. On the other hand, nucleation is not inherently a steady-state phenomenon, so I guess we could speculate that tricarboxylics first build up to some > ppt threshold, and are then quickly depleted in a short nucleation burst).
Similar reasoning of course applies to all potentially nucleating complex organics (e.g. “HOM dimers”), not just tricarboxylics - it’s hard to build up substantial steady-state reservoirs of compounds that form with relatively low yields from oxidation of precursors that are not super-abundant to begin with.
Note: while I’d like to hear a bit about the reasoning behind the 10 ppt upper limit in the authors’ response, the only actual action item I’m suggesting for the actual manuscript is that the authors acknowledge that 10 ppt is, while not completely impossible, a very high number indeed for something like a tricarboxylic.
3)What is the rationale for using 278.15 K in the ACDC simulations rather than 298.15 K? Is the cluster formation negligible at 298.15 K? Or have some relevant experiments been reported specifically at this temperature? Also, given that monoterpene emissions are strongly temperature-dependent, is it not even less probable to encounter 10 ppt mixing ratios of tricarboxylics at 278 K?
4)The authors rationalise the stability of the PDPE-containing clusters by the flexibility of the molecule. This may well be true in the context studied here (tricarboxylic acids stabilising sulfuric acid -base clusters), but it contrasts in an interesting way with our recent study (https://pubs.rsc.org/en/content/articlelanding/2025/cp/d5cp01931a) where we found that flexibility, in the sense of efficient H-bonding inside a monomer, is a strong predictor for INefficient pure organic cluster formation among a series of “HOM dimer” candidates. The two statements do not necessarily contradict each other. In addition to focusing on pure organics rather than mixed organic-inorganic clusters, our study did not, for example, contain any di- or tricarboxylics. It could be that the stronger H-bonds formed by the carboxylic acids, especially between them and the inorganic cluster constituents, negates the “efficient internal H-bonding leads to reduced cluster formation potential” effect we reported. However, in an older study involving both me and Jonas Elm, we did find some evidence for intramolecular bonding affecting cluster stabilities also for linear dicarboxylic acids (https://pubs.acs.org/doi/10.1021/acs.jpca.9b08020), albeit only for the largest studied case (suberic acid), and with substantial associated entropy-enthalpy compensation. In any case, it would be interesting to see the lowest-energy (and/or lowest free energy) monomers for the three acids studied here - are there any internal H-bonds in any of them (apart from the presumably relatively weak bond between the C=O and O-H in the SAME carboxylic acid group, which tends to be always present)? The suggested action item here is that at minimum, the authors show and briefly discuss the monomers in terms of potential internal H-bonding, and possibly comment on the different role that “flexibility” seems to be playing in their study and ours.
5)Please add units to the x-axes in Figures 7-9 (I assume ppt).
6)I am a bit worried about the boundary conditions used for the ACDC simulations, and their effect on the results. If I interpret the discussion around line 125-128 correctly, the “pure SA-base” clusters are required to have at least 4 sulfuric acids and 3 bases to be counted as “nucleated”, while the organic clusters need less of each (such that one OOM can replace up to one base, and/or up to two sulfuric acids). I understand the reasoning here - if the OOMs are enhancing the nucleation, then it makes sense that they can be counted as “replacing one or two inorganic molecules”. (For simpler notation, I here refer also to the amines as “inorganic”, despite them having C-H bonds, and thus technically also being organic molecules.) And if we knew for sure that the OOMs are enhancing the nucleation, then probably something like these boundary conditions are, in the absence of data on the larger clusters, possibly the best guess we have for the “cluster formation potential”, as the authors define it. However, as I see it, the main research question of the study is IF the tricarboxylic OOMs have a substantial enhancing effect on the cluster formation potential (and thus nucleation), or not. This being the case, the boundary conditions used here risk assuming the answer to this question before it has even been stated. (Or to put it another way, there is a risk of circular reasoning if the boundary conditions are set based on an assumption that the OOMs enhance nucleation, which in turn is based on simulations using these boundary conditions.) To illustrate what I mean, let’s take a hypothetical “inert” organic compound, which behaves in the following way: 1)1 or 2 inert molecules stick to the inorganic clusters, with low enough evaporation rates that they are essentially always present in them, 2)further inert molecules do not stick to the clusters, and 3)the inert molecules do not affect (in either way) the addition of acids and bases. Using the outgrowing cluster definitions of the authors, they would find a huge “enhancement effect” from such inert organics (as you now only need to form clusters with 3 or even just 2 SA rather than the full 4 SA)- despite them (by definition) not actually affecting the SA-base clustering process at all. This is of course quite hypothetical - no real molecule will behave in this fashion - but it illustrates the problem. I strongly urge the authors to redo the simulations reported in Figures 7-9 so that the boundary conditions (outgrowing cluster definitions) in terms of SA and base molecules required for “nucleation” are exactly the same for both the “organic” and “inorganic” case. If the enhancement effect from these simulations is substantially smaller than that observed in the current simulations, then at least part of the effect originates in the assumed boundary conditions rather than the actual clustering chemistry or physics. The “real” cluster formation potential is then likely to lie somewhere between the two alternatives (outgrowing cluster definitions), and there is probably no accurate way of knowing better without actually studying the full set of (as yet too large to be computed) clusters. This is, I think, an inherent limitation of the otherwise elegant “cluster formation potential” approach. It might be that the best way to present results in these types of cases would be as some sort of shaded areas rather than single lines, with the limits of the shading given by different boundary condition definitions. So my suggested action item is to show these types of shaded areas in Figures 7-9.
7)It might be interesting for readers to see estimates of the radii (radiuses) of the clusters in Figures 4 and 6. (This can be done for example by computing the volume in a quantum chemistry programme, using some reasonable default electron density value, assuming a spherical cluster, and solving for r).