This manuscript describes meta-analysis of a wide range of recently published INP characterizations of mineral dust samples analyzed by several different techniques. Data is reanalyzed to create comparable quantities, and discrepancies between the different datasets are discussed, with a focus on 1) different materials, 2) different measurement techniques, and 3) different sample ageing conditions. Particle coagulation and wet ageing processes are considered for the source of discrepancies between different measurement techniques. Parameterizations are constructed for aggregate data, divided by measurement technique and sample ageing conditions.

There is a lot of interesting data and discussion within this paper, however there are significant weaknesses that prevent any strong conclusions from being made.

Foremost: aggregate equivalent diameters are constructed to examine possible impacts of aggregation on measured freezing temperatures. This is an interesting idea, with some interesting data. In the manuscript it is taken as proof of extensive aggregation, however, which does not logically follow from any of the data or discussion. One of the following needs to happen: 1) Compelling evidence needs to introduced that extensive aggregation is occurring in droplet freezing measurements or 2) much of the manuscript needs to be rewritten to remove the unwarranted conclusion.

Second: Many strong conclusions and atmospheric implications are made without strong, or any, evidence, these need to be walked back or better supported. See comments on lines 500+ below.

Despite these issues, I think there is a lot of interesting analysis and work that has gone into this paper, and I think it will be publishable and of broad interest with the right framing and revised discussion, but extensive revisions are required.

Specific comments:

Section 2.2: In this section it was unclear to me if you are using equations 1-6 and applying them to literature datasets, or simply explaining how these quantities might be calculated and using literature values that have already been calculated. I think it would be much more clear to move this information to the supplemental and expand the discussion to be more explicit about which quantities were used from each dataset to calculate each derived quantity. Right now it feels like there is enough information to make a few guesses but not enough information to be sure what you have actually done. Perhaps a very brief explanation should stay in the main manuscript and point to the supplemental.

Line 232 or thereabout: There is a lot of discussion of feldspar ice nucleation, and the variability in mineral dust ice nucleation properties, and I feel that inclusion of Whale 2017 would greatly benefit this section. In that work, for feldspar samples measured using the same technique, there are >5 orders of magnitude difference in ns, in a similar manner to the combined data within your manuscript. This certainly seems relevant for understanding the origin of the variability and should be discussed.

Line 253: I don’t think it is fair to say “1-8 orders of magnitude higher” when some of the aerosol and suspension points overlap, maybe 0-8?

Line 270: similar to above, maybe “0-6 orders”… or “up to 6 orders” might sound better. Also shows up line 428 and 565.

Line 276: My understanding based on the equations included, is that the way you are estimating Jhet will shift ns values in an identical way based on experimental cooling rate or residence time, is that correct? Such that any relative change between the relative ordering of experiments in ns and jhet is due to cooling rate changes? Some discussion of this would be helpful I think. I also think that more explicit discussion (related to my comments on section 2.2) surrounding what assumptions go into this estimation of jhet and their validity would be helpful.

Line 283: The “two step temperature dependence” is weakest in natural dust samples, and doesn’t appear for the aerosol samples. I’m not convinced that this statement is well-supported by the data presented thus far.

Line 310: referencing eq. 1 and 3 here seems worse than just redefining the terms – Sp is the surface area of a single aerosol and Sd is the total surface area of all suspended aerosol in a droplet.

Line 312: Why are you choosing different definitions for “freezing temperature” for suspension and aerosol measurements? That needs to be justified.

Lines 315-330: So you have constructed an equivalent diameter for all particles in solution drops and compared to actual aerosol diameters, after briefly discussing coagulation. I don’t understand quite how you think these comparisons are meaningful, however. It certainly doesn’t seem to follow that droplet freezing measurements are only relevant to >10 micron single particles within the atmosphere, when you have only constructed a “what if everything coagulates” product with no evidence that coagulation is actually occurring in these measurements…

Related to this, droplet freezing measurements often use serial dilutions to access different INP concentration ranges, with the most dilute samples differing by >1000 fold. In most cases there is overlap in INP concentration between dilutions, which would not be the case if the degree of aggregation were changing with concentrations. Some discussion of this is relevant and warranted in this section.

Lines 367: The transition to parameterizations seems abrupt, especially immediately following a teaser for discussing relevant “|water-ageing” processes. Maybe this belongs elsewhere in the manuscript, or perhaps it just needs to be tied together better.

Figure 5: The aged and fresh data for aerosol/suspension look so similar, can you do significance testing to see if there are population level differences? Maybe a simple thing would be to see how well the best fit lines for fresh populations fit the aged data (calculating R^2 values). There are lots of fancier ways to check for significance between the two populations at a given temperature, or across all temperatures (which should probably be restricted to where you have data for both, i.e. >-27C for suspensions).

Line 575: you aren’t really accounting for the variability in composition and measurement methods, are you? Just fitting the aggregate data separately for the two techniques. You haven’t synthesized them together in any way though…

 Line 616-621: Do you actually know that dry-dispersed measurements are more representative of freshly emitted aerosol? I don’t think there is strong evidence in your analysis that this is the case, and I also don’t think it is well-supported by your citations. I think more realistically, we still have two different techniques with discrepancies in what they  measure but we don’t know which is more representative of ambient concentrations or aerosol-cloud interactions.

Line 626: I don’t think you have shown that De based parameters are atmospherically relevant in any ways, and this discussion seems poorly supported…

References:

Whale, T. F., Holden, M. A., Kulak, A. N., Kim, Y.-Y., Meldrum, F. C., Christenson, H. K., and Murray, B. J.: The role of phase separation and related topography in the exceptional ice-nucleating ability of alkali feldspars, Phys. Chem. Chem. Phys., 19, 31186–31193, https://doi.org/10.1039/C7CP04898J, 2017.

This manuscript compiles laboratory measurements of immersion freezing by mineral dust and seeks to derive revised parameterizations for dust ice nucleation under mixed-phase cloud conditions. The topic is important, and the effort involved in assembling a broad dataset is clear. The plots are interesting, and the compilation itself is potentially useful. The manuscript also raises a genuinely important issue, namely the difficulty of comparing measurements made using different experimental approaches.

However, I am afraid I am not persuaded by the central interpretation of the paper. In my view, the manuscript places far too much weight on the idea that there is a meaningful and general difference between ‘aerosol’ and ‘suspension’ methods, when the analysis presented does not convincingly isolate a method effect from the much more obvious and well-established effects of composition and material-specific behaviour. The paper’s own compilation shows that dust ice nucleation activity varies enormously between mineral classes and within them, including among feldspars, quartz samples, ATD, and natural dusts. Yet these materials are then aggregated in ways that make the subsequent attribution to measurement method, in my view, untenable.

Indeed, I came away with rather a different impression from the one advanced by the authors. Looking at the figures, I am less struck by a clear demonstration of a fundamental dichotomy between aerosol and suspension approaches than by the extent to which the measurements are, in fact, as broadly consistent as they are, given the very large differences in mineralogy, sample origin, preparation, and experimental protocol represented in the compilation. The interesting conclusion here is not, to my mind, that one has established a robust and general method-dependent discrepancy, but rather that a wide and heterogeneous literature still shows a degree of coherence despite the fact that obviously unlike materials have been grouped together.

For that reason, I am not sure that this manuscript is revisable in any straightforward sense. To do this properly, it seems to me that one would need a rather different paper built around careful like-for-like comparison, explicit treatment of compositional heterogeneity, and a much more cautious interpretation of what can and cannot be inferred about method effects from compiled cross-study datasets. As it stands, I do not think the main conclusion is supported.

Major comments

1. The manuscript does not convincingly demonstrate a meaningful general difference between ‘aerosol’ and ‘suspension’ methods. The central claim of the paper is that measurement method introduces one of the largest sources of variability in dust ice nucleation activity, with dry-dispersed aerosol measurements yielding systematically higher ns than wet-suspension measurements, sometimes by several orders of magnitude. This claim appears in the abstract, is developed through Figs. 2–4, and is used to motivate the proposed method-specific parameterizations. I do not think the evidence presented is sufficient to support that conclusion.

The difficulty is that the comparison is heavily confounded by differences in the materials being compared. The manuscript itself repeatedly acknowledges that dust ice nucleation activity depends strongly on mineral composition and can vary substantially even within nominally the same mineral class. For example, the manuscript notes that K-feldspar-rich particles tend to be much more ice active than other feldspars; that non-potassium-rich feldspars can have much lower activity; that quartz samples vary; that ATD may be relatively active where K-feldspar is present; and that natural desert and volcanic dusts are diverse materials with differing nucleation behaviour.

This issue is especially clear in the treatment of the different dust classes shown in Fig. 2. The manuscript aggregates feldspars, clays, ATDs, and natural dusts in ways that I do not think are well justified physically. For feldspars, the manuscript explicitly states that not all feldspars are equal, and that K-feldspar and non-potassium-rich feldspars can differ by orders of magnitude in n_s. It therefore seems unreasonable to collect all feldspar data in the manner done in Fig. 2 and then interpret the resulting contrast as evidence for a difference between techniques. The feldspars used in the various studies may simply not be comparable substances. Even amongst relatively active k-feldspars there is plenty of evidence for a wide spread in activity (Whale et al., 2017; Canet et al., 2025). If the authors think there is good reason to treat them as a common category for this purpose, that case needs to be made explicitly and convincingly. At present it is not.

For clays, I do not find it obvious why illite, kaolinite, and montmorillonite should be aggregated in the way shown in Fig. 2. These are distinct minerals, and the manuscript provides no clear physical basis for expecting them to share a common n_s behaviour such that method-dependent offsets can be meaningfully interpreted once pooled

For ATD, the paper treats Arizona Test Dust as though it were effectively one material class. However, different ATD samples are well known to have different compositions e.g (Ehlers et al., 2026) and therefore could quite plausibly differ meaningfully in their ability to nucleate ice. I therefore do not think it makes sense to compare the ATD datasets in Fig. 2 as though they were directly interchangeable across techniques. Again, this is not like-with-like.

For natural dust, the problem is even more obvious. The natural dusts included here are clearly different substances from different desert and volcanic sources. It is not clear why one would expect them to nucleate ice similarly in the first place, let alone why they should be pooled in a way that supports a general conclusion about measurement method.

2. The paper appears to assume that ‘aerosol’ approaches are, in some sense, the correct ones. The manuscript seems to carry an implicit assumption that dry-dispersed ‘aerosol’ methods give the more correct or atmospherically representative measure of dust ice nucleation activity, whereas suspension methods are treated as being depressed by water exposure and aggregation. This perspective/bias runs through the discussion and is especially clear in the atmospheric implications section, where aerosol-derived n_s  is presented as representative of fresh near-source dust, while suspension-derived n_s is treated more as something affected by artefacts or processing. I do not think this is adequately thought through or justified. It may indeed be the case that some droplet-freezing experiments are influenced by aggregation or prolonged water contact. But the converse is also true: many aerosol instruments have short residence times compared with the timescales over which particles may be immersed in cloud droplets in the atmosphere. If there are rapid aging effects, or if immersion time itself matters, then short-residence-time aerosol measurements are also only probing a particular experimental regime, not some obviously privileged ‘truth.’ The manuscript acknowledges different water-contact times and briefly notes time dependence via J_het but the discussion still treats aerosol methods as more representative in a way that seems asserted rather than demonstrated.

If the authors wish to argue that one class of method is more atmospherically relevant than the other, then they need to define the atmospheric scenario and provide evidence for that claim. As things stand, I do not think the asymmetry in how the two method classes are treated is warranted.

3. The ‘aerosol’ / ‘suspension’ binary is itself too coarse. The manuscript tends to treat ‘aerosol’ methods and ‘suspension’ methods as though they were two coherent and internally homogeneous methodological classes. I do not think that is really tenable. Each category contains a range of techniques with different sample preparation routes, concentrations, residence times, droplet sizes, cooling rates, activation conditions, and thermal histories. The manuscript itself notes variation in chamber residence times and in droplet-freezing conditions across studies.

4. The manuscript puts too much weight on the aggregation/coagulation hypothesis. The paper repeatedly advances the idea that the lower n_s values obtained in suspension measurements, particularly at warmer temperatures, may be explained by particle coagulation in highly concentrated suspensions, which reduces effective surface area available for nucleation. This is discussed in Section 3.2 and is then used to motivate the D_e based treatment.

This may be a plausible hypothesis, but I do not think the paper provides actual evidence sufficient to carry the weight placed upon it. Nor, in truth, did I think the prior literature cited established this in a definitive physical sense either. The reasoning here seems entirely inferential: there is an apparent discrepancy between compiled aerosol and suspension datasets, one can imagine aggregation occurring in concentrated suspensions, and therefore aggregation is proposed as an important explanation for the discrepancy. One can easily perform calculation showing such a mechanism to be plausible, given a set of assumptions. But that is not the same thing as demonstrating the mechanism.

Moreover, impairment of ice nucleation activity by aggregation would presumably require that the aggregation in some way reduces access of water to the active nucleating surfaces or otherwise alters the availability of those sites. I do not see physical evidence for that process being provided here. The manuscript’s D_e analysis shows that suspension-derived equivalent particle sizes are often large and interprets this as evidence of unrealistic multi-particle loading and coagulation, but this does not in itself establish the causal mechanism by which freezing efficiency is impaired.

I therefore think the language throughout the paper should be much more cautious. Aggregation/coagulation may be one possible contributor to the posited discrepancies (if these do indeed exist), but it is certainly not shown here to be the dominant explanation.

5. I am not at all convinced by the manuscript’s implicit assumption that the fitted relationships should be linear in the chosen coordinates. I know it is pretty commonly observed/assumed, but what physical reason is there for this? The paper repeatedly adopts forms such as log(n_s)=AT+B, but no real justification is given for why such a relationship should be expected for a compilation that mixes different minerals, different samples, different methods, and different aging pathways. In that setting, a straight line in log-space may simply be a convenient summary of a broad and heterogeneous cloud of data, rather than evidence of a common physical law. This concern is reinforced by the fact that the authors themselves introduce two separate temperature regimes for the suspension data, which rather undermines the idea that a simple linear form is appropriate in the first place. At minimum, I think the manuscript should acknowledge that the chosen fits are empirical conveniences and should avoid implying that the linearity itself has some deeper ‘physically grounded’ significance.

6. I also take issue with much of what is said here about aging and water exposure. The discussion is presented rather too neatly, whereas the literature on these processes is more extensive and more nuanced than is reflected in the manuscript, see e.g (Reischel and Vali, 1975; Klumpp et al., 2022; Whale, 2022; Ren et al., 2022) amongst many others. Different dusts behave differently, the timescales matter, and I do not think the present paper supports the level of confidence with which some of these statements are made. I would suggest either engaging more carefully with the wider literature or substantially toning down the claims.

7. I want to stress that I do think the plots are interesting. There is value in assembling this literature, and there is value in showing the broad spread of measurements and the practical challenges this presents for parameterization. But, to my mind, a quite different conclusion should be drawn. The most striking thing about the compilation is not that it proves a fundamental and general discrepancy between aerosol and suspension methods. Rather, it is that a body of literature spanning many minerals, sample origins, and experimental methods still shows some consistency as it does. That suggests to me that the interesting scientific question is not ‘which method is right, and how do we correct the other one?’ but ‘under what specific circumstances, and for which materials, do different experimental approaches diverge meaningfully?’ The present manuscript is not really set up to answer that question, because it aggregates unlike things too readily and then draws a conclusion that rests on that aggregation. For that reason, I think that if this work were to be developed properly, it would need to become a rather different paper.

References

Canet, J., Rodriguez, L., Renzer, G., Alfonso, P., Bonn, M., Meister, K., Garcia-Valles, M., and Verdaguer, A.: Measurement report: Ice nucleation ability of perthite feldspar powder, EGUsphere, 2025, 1-24, 10.5194/egusphere-2025-5014, 2025.

Ehlers, A. M., Bunin, D. J., Caddick, M. J., Loebig, J., and Clarkson, R.: On the composition of the Arizona test dust: A comprehensive characterization of an analog for atmospheric mineral dust, Powder Technology, 471, 122076, https://doi.org/10.1016/j.powtec.2025.122076, 2026.

Klumpp, K., Marcolli, C., and Peter, T.: The impact of (bio-)organic substances on the ice nucleation activity of the K-feldspar microcline in aqueous solutions, Atmos. Chem. Phys., 22, 3655-3673, 10.5194/acp-22-3655-2022, 2022.

Reischel, M. T. and Vali, G.: Freezing nucleation in aqueous electrolytes, Tellus, 27, 414-427, 10.1111/j.2153-3490.1975.tb01692.x, 1975.

Ren, Y., Soni, A., Kumar, A., Bertram, A. K., and Patey, G. N.: Effects of pH on Ice Nucleation by the α-Alumina (0001) Surface, The Journal of Physical Chemistry C, 126, 19934-19946, 10.1021/acs.jpcc.2c06417, 2022.

Whale, T. F.: Disordering effect of the ammonium cation accounts for anomalous enhancement of heterogeneous ice nucleation, The Journal of Chemical Physics, 156, 144503, 10.1063/5.0084635, 2022.

Whale, T. F., Holden, M. A., Kulak, A. N., Kim, Y.-Y., Meldrum, F. C., Christenson, H. K., and Murray, B. J.: The role of phase separation and related topography in the exceptional ice-nucleating ability of alkali feldspars, Physical Chemistry Chemical Physics, 10.1039/C7CP04898J, 2017.