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the Creative Commons Attribution 4.0 License.
| 07 Aug 2026
Comment to "Detecting supramolecular organic nanoparticles during heat wave by Zhang et al."
Abstract. Atmospheric new-particle formation is a major source of aerosol particles that influence air quality, cloud properties, and climate. Understanding the molecular mechanisms governing the initial steps of particle formation is therefore essential for accurately representing aerosol formation and its climatic effects in atmospheric models. Zhang et al. (2026c) recently proposed that hydrogen-bond–driven self-assembly of neutral carboxylic acids is a spontaneous and ubiquitous atmospheric new-particle formation mechanism. If correct, this would represent a fundamental shift in the current understanding of atmospheric nucleation.
In this comment, we show that the proposed nucleation mechanism is not adequately supported by the observations or theoretical analysis presented in Zhang et al. The reported particle-composition measurements lack sufficient validation to establish the proposed molecular composition of the smallest particles and do not directly constrain the molecular processes responsible for the earliest stages of particle formation. Furthermore, using the thermodynamic data reported by Zhang et al., we demonstrate that cluster evaporation overwhelmingly exceeds growth by molecular collisions, resulting in negligible particle-formation rates under the reported atmospheric conditions. These kinetic and thermodynamic analyses demonstrate that hydrogen-bond–driven clustering of neutral carboxylic acids cannot explain the reported observations and is unlikely to represent an atmospherically relevant new-particle formation mechanism.
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Status: open (until 24 Sep 2026)
- RC1: 'Comment on egusphere-2026-3785', Jonas Elm, 07 Aug 2026 reply
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RC2: 'Comment on egusphere-2026-3785', James Brean, 10 Aug 2026
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In February 2026, Zhang et al. published a study in Science reporting frequent NPF during a central Texas heatwave. Using size-resolved measurements of aerosol particles down to 3 nm they measured multifunctional acids dominating the mass, with trace sulfuric acid and no detectable amines except in larger particles. On the basis of quantum chemical calculations, they proposed that hydrogen-bond driven self-assembly of these multifunctional acids drove their observed nucleation. This pathway was argued to have no free-energy barrier, and was not volatility-limited, allowing it to proceed in the hot Texan summer.
They further proposed this as a common mechanism for new particle formation across diverse tropospheric conditions. If correct, this would throw the acid-base and HOM pathways established by a large body of field and laboratory work into question.
This present comment addresses the core limitations of Zhang et al. Zhang et al. base their claim of spontaneous self-assembly on the negative ΔG for successive monomer additions, computed at a reference pressure of 1 atm. However, atmospheric monomer partial pressures are eight to ten orders of magnitude below that, and Myllys et al. show that once the free energies are corrected to ambient concentrations a barrier appears. Zhang et al. also compute forward collision rates without ever computing the reverse rates that their own thermochemistry implies. In this comment, Myllys et al. give this more rigorous treatment, and find that evaporation beats collision by roughly three orders of magnitude for every aggregate from A2 to A6.
The authors also raise some important comments about the experimental evidence, although I feel this section of the comment could be fleshed out slightly. I recommend this comment for publication. I provide a number of comments on the present text and also a couple of extra points for consideration below:
General comments
1) The comment quotes Zhang et al.'s dimerisation free energy as -7.7 (DFT) and -7.6 kcal/mol (DLPNO//DFT). The erratum (Zhang et al., 2026b) revises the value to -6.1 kcal/mol. The comment acknowledges the erratum but does not appear to propagate it, and the -7.6 value is still quoted at line 32 without qualification. I don’t think this would change the major conclusions of this comment if either energy was used, but it is important for consistency.
2) In Zhang et al., only A2 received a DLPNO-CCSD(T) single point correction; A3 to A6 are ωB97X-D only. The larger species were constructed by adding monomers to the previously optimised species. Is it possible to comment on this approach for larger species for us non-specialists in these calculations?
2) Lines 158 of the comment onwards make a very important point, which is that a measurement of composition at 3 to 10 nm carries almost no information about nucleation. This could do with a short quantitative treatment. Taking a critical cluster of mobility diameter 1.5 nm and assuming spherical particles of uniform density, the fraction of the mass of a larger particle contributed by the original cluster is extremely small. Approximately 10% for a 3 nm particle, and below 1% for a 10 nm particle. In other words, 90 % of the mass of Zhang et al.'s smallest measured particles, and >99 % of the mass at 10 nm, was acquired after nucleation. Even a perfectly accurate composition measurement at 3 nm is therefore overwhelmingly a measurement of the condensed growth material, not of the nucleating species. More damning is that that the supplement states that the nano-DMA was run at low resolution, with 5 SLPM sample against 15 SLPM sheath, passing a roughly normal distribution of standard deviation equal to 0.3 times the selected size. Because mass scales with the cube of diameter, that means that the mass-weighted effective diameter of the measured 3 nm particles is in fact higher than 3 nm, pushing these fractions down. These would go down even further accounting for the appropriate mobility-to-mass-diameter calculations!
3) Myllys et al. highlight correctly that the authors use CO3-/CO4- to detect acids. This is an ionisation scheme that is highly selective for acids, and Zhang et al. then find that their particles are made of acids, and conclude that nucleation is dominated by acids. This is perhaps slightly circular reasoning. This, as well as the claim that this was unambiguously verified using H3O+ ionisation (which is itself highly selective), could be discussed in more detail.
Additional considerations
The following go beyond the scope of a review of this comment, and stray into reviewing Zhang et al. themselves. I include them because they may be useful during the open discussion, or if the authors choose to expand their treatment of the experimental evidence. None are conditions of publication.
1) A major consideration is that Zhang et al. propose a new mechanism without sufficiently disproving the much more obvious mechanism of sulfuric acid-base nucleation. The authors state that: “For the three strongest NPF events … the average temperature … was] 32°” and then later “An unexpected outcome from our field observations is the high temperatures (approaching 40°C) at which frequent NPF events take place. Such a finding cannot be explained by presently known theories for NPF”. This is simply untrue.
- First, H2SO4-base nucleation can proceed at these temperatures and is routinely observed to do so. The obvious example is Beijing, where summertime NPF frequently occurs at >30 degrees, with formation rates very similar to those observed by Zhang et al. (e.g., Deng et al.: https://doi.org/10.1021/acs.est.0c00808).
- Second, there are already reports of H2SO4-amine-OOM nucleation in Houston. These measurements can be found at Tiszenkel et al. https://doi.org/10.1038/s43247-025-02310-4.
- The authors argue that their observed SO2 was below 0.5 ppb (the detection limit of their instrument), but 0.5 ppb is sufficient to produce 1e6 to 1e7 /cm3 H2SO4 at the low CS and high insolation that they observe, which is once again in-line with Deng et al.'s summertime Beijing observations.
- In their particle phase measurements they measure H2SO4 comprising roughly more than zero, but less than 20% of total particle mass. This is once again completely consistent with the H2SO4:organic ratios observed in the most relevant TDCIMS dataset of Li et al. in Beijing (https://doi.org/10.1021/acs.est.2c01566), where, once again, the nucleation is well known to proceed through an acid-base mechanism, with HOM condensation dominating the growth.
2) Zhang et al. flash-heat their sample to 350 degrees in the span of three seconds. An additional consideration is therefore thermal desorption artefacts. It is well documented in the FIGAERO literature that accretion products and other very low volatility species are detected as higher volatility compounds after heating, because they decompose (e.g. Lopez-Hilfiker et al. 2015; doi:10.5194/acp-15-7765-2015). At 350 °C I am not sure that Zhang’s measured species survive intact. As the collected mass was evaporated into the ID-CIMS within ~3 s, there is no temperature ramp data, so no thermograms exist and the usual diagnostic for separating direct desorption from decomposition is unavailable. Further to this, Myllys et al. highlight that the sensitivity calibration was performed by depositing the small acids onto the collector, which itself provides no information about whether these are instrumental artefacts. I would caveat that we would not necessarily expect larger species to produce multiacids upon heating, but this is still a major uncertainty.
3) The measurements of Zhang et al. used a triple quadrupole CIMS instrument. They do not state the mass resolution of the instrument, but a unit-mass resolution instrument is implied by their survey scans followed by single ion monitoring. If so, then how can the Zhang et al. be so sure of their molecular assignments? CIMS measurements will often show many overlapping peaks, even in this <300 m/Q region. If there is indeed major thermal fragmentation of the measured molecules, then many of these fragmentation products will overlap with the masses of the multiacids.
Technical comments:
In this comment there are three Zhang references which are often incorrect, and out of order. E.g., the statement “Zhang et al. (2026a) concludes that”… points towards the Zenodo dataset.
Line 48: “For GlA–ToA complex,…” is a broken sentence.
Line 60: “In the DLPNO calculations”?
Line 61: “even Zhang et al. performed some…” should this say “even though Zhang.”…? Similarly it then goes on to say “we found 0.6 kcal/mol lower DFT free energy”. Should this say “We found a structure 0.6 kcal/mol lower in energy” or similar?
Line 66: Zhang et al conclude rather than concludes?
Line 100: I think the kD units are wrong.
Line 108: “The original article” rather than “an original article”?
Line 127: “which leads to overestimated collision and NPF rates”. This could be clearer as it’s not clear whether the overestimation is relative to measurement or a physically more justifiable calculation. Perhaps “which yields an upper bound…”?
Line 141: Maybe it would be better to state that it was done at lower detection limits, rather than higher sensitivities than previous achieved.
Line 147: A small comment that does not majorly change any conclusions: here the authors presume a density of 1 g/cm3, whereas Zhang presume 1.23 g/cm3. This is a generous choice, so I’d state that explicitly as you do for the evaporation calculations.
Line 148: where does the 10% charging and 10% penetration come from? Zhang et al. state that their polonium charger produces efficiencies of 10 to 70%. Presumably 10% is for the smallest diameters as charging efficiency decreases with decreasing size. What about the penetration?
Citation: https://doi.org/10.5194/egusphere-2026-3785-RC2
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- 1
Review of “Comment to Detecting supramolecular organic nanoparticles during heat wave by Zhang et al."
Myllys et al comments on the recent 2026 paper entitled “Detecting supramolecular organic nanoparticles during heat wave” by Zhang et al, published in Science. Zhang et al proposed that self-assembly (hydrogen bonding) of carboxylic acids is a spontaneous process leading to new-particle formation, even during extreme heat events. The submitted comment present evidence of misinterpretation of the experimental and theoretical results, essentially falsifying the conclusions of Zhang et al.
When I first read the study by Zhang et al, my immediate thought was that this paper completely ignores the immense knowledge obtained on organic enhanced cluster formation during the past two decades.It is by now well-established that it is most likely covalently bound dimers (accretion products) that drive organic nucleation at ombient conditions. In particular, Figure 5 in the paper by Zhang et al is highly misleading, as it only presents the standard free energies giving the impression that the clusters are stable. Considering the evaporation rates, or calculating the equilibrium cluster concentrations, would immediately demonstrate that the reported clusters are not sufficiently stable to explain the proposed mechanism. Hence, I am pleased to see the authors submit this critical comment, as I believe it exposes an important issue with the published paper. The comment is written by a strong team of highly qualified professionals. The critical analysis is technically sound, and the comment can essentially be published as is. I only have a few minor optional comments for the authors below.
Comments
Line 12: “These kinetic and thermodynamic analyses demonstrate that hydrogen-bond–driven clustering of neutral carboxylic acids cannot explain the reported observations and is unlikely to represent an atmospherically relevant new-particle formation mechanism.”
To be on the safe side, perhaps state that this refers to the “studied neutral carboxylic acids” in Zhang et al. We have recently shown that tricarboxylic acids might contribute to NPF, so there might be very special cases where neutral tricarboxylic acids can actually nucleate (if they exist).
Line 33: “These ∆G values appear unrealistically favorable, …”
I had the exact same thought when I first read the study. This is substantially more favourable than what have previously been found for carboxylic acid-carboxylic acid interactions. In addition, while addressed on page 7, it might also be worth pointing out already here that the free energy analysis is carried out at 298.15 K, while the paper states the mechanism to be relevant for up to 311.15 K (up to 38°C). This would further destabilize the studied carboxylic acid-carboxylic acid clusters.