the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 09 Jan 2026
Ice Nucleating Particles Variability Across a Megacity
Abstract. Megacities are a great source of urban aerosol particles, which can impact cloud formation and the local hydrological cycle. However, the aerosol-cloud interaction in megacities, especially in their different microclimates, is poorly understood. In the present study, the physicochemical and biological properties of urban particles, along with their ice-nucleation abilities as a function of size (1.0 μm to 10 μm), were simultaneously characterized at two sites across the Mexico City Metropolitan Area (MCMA). We found apparent differences in the chemical composition, criteria pollutants, and biological content between northern and southern sites in the MCMA. The urban MCMA aerosol particles were found to act as ice-nucleating particles (INPs), with average concentrations ranging between (0.04 ± 0.04) L-1 (at -15 °C) and (23 ± 17) L-1 (at -30 °C). The southern MCMA samples were found to be more efficient INPs, and their ice nucleation abilities correlated positively with PM2.5, potassium, and sulfur. On the other hand, the ice nucleation abilities of the measured urban particles at both sites did not correlate with their size nor the presence of biological particles. Overall, the aerosol physicochemical and biological compositions, their sources, and their role in cloud formation at both sites were found to be different. Therefore, the present results demonstrated the presence of two different microclimates within the MCMA. This highlights the importance to consider that aerosol-cloud interactions within a megacity may vary widely, especially when assessing the role of INPs in the development of extreme precipitation events.
Competing interests: At least one of the (co-)authors is a member of the editorial board of Atmospheric Chemistry and Physics.
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.-
Notice on discussion status
The requested preprint has a corresponding peer-reviewed final revised paper. You are encouraged to refer to the final revised version.
-
Preprint
(1894 KB)
-
Supplement
(1521 KB)
-
The requested preprint has a corresponding peer-reviewed final revised paper. You are encouraged to refer to the final revised version.
- Preprint
(1894 KB) - Metadata XML
-
Supplement
(1521 KB) - BibTeX
- EndNote
- Final revised paper
Journal article(s) based on this preprint
Interactive discussion
Status: closed
-
RC1: 'Comment on egusphere-2025-6106', Anonymous Referee #1, 06 Feb 2026
-
AC1: 'Reply on RC1', Luis A. Ladino, 22 Apr 2026
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2026/egusphere-2025-6106/egusphere-2025-6106-AC1-supplement.pdf
-
AC1: 'Reply on RC1', Luis A. Ladino, 22 Apr 2026
-
RC2: 'Comment on egusphere-2025-6106', Anonymous Referee #2, 24 Feb 2026
Review of „Ice Nucleating Particles Variability Across a Megacity” by Sebastián Mendoza-Téllez et al., submitted to EGUsphere.
The manuscript describes measurements of atmospheric aerosol particles done on a few days (5 to 7, depending on sample) at two different sites (16 km apart) in Mexico city. Measurements include a variety of parameters from three types of samples: a MiniVol Tactical Air Sampler (Airmetrics) with a 2.5 µm cut-size inlet for chemical analysis; an eight stage micro-orifice uniform deposit impactor (MOUDI) for INP (ice-nucleating particle) analysis with an upper sampling size of 10 mm; and a BioStage cascade impactor (cut-off size not given, likely total suspended particles) for the analysis of viable bacteria and fungi. All sample types not only had different cut-off sizes, but also different sampling durations (24h, ~ 4h and 5 min, respectively) but also a different amount of collection days, and it did not become clear which data from which days were used for comparisons.
Conclusions drawn by the authors oftentimes seem to include some wishful thinking, as I will elaborate on in more detail below. Due to this, but also due to the data as such and of what they show, I strongly suggest to the editor to consider if this should rather be published as a measurement report. But in any case, I can recommend publication of this study only after the data interpretation will have been adapted to what the data really show and after the text will have been thoroughly and accordingly revised.
My main points of criticism (all of them equally important) are the following:
1) The above-mentioned different cut-off sizes for the different samples, their different collection durations and the different days of sample collection make a comparison of the (bulk) results for the different particle characteristics difficult or even meaningless.
INP data from the two study sites differ particularly in the larger size bins (> 5.6 mm for 4 of 5 samples, 3.2 – 5.6 mm for two and 1.8 – 3.2 mm for one sample). This is an interesting result, which, however, is not discussed at all. Unfortunately, for these larger sizes, there is no information on the chemical composition.
On the other hand, for the presented correlation between INP data and chemical composition (Fig. 6 and related text) it was not described for which INP data (all MOUDI size bins or only the ones for smaller particles?) this was done. Hence the presented correlation may or may not be meaningless in general. From the text I assume that the fully summed up INP concentrations (over all MOUDI stages) were used for the comparison. It would make sense to sum up the two MOUDI-stages with the smallest INPs on them and compare the resulting INP concentrations with results from the PM2.5 chemical analysis. Then, it can also be described which fraction of all INPs is in these two smallest MOUDI-stages. However, sub-micron particles will still be missed in the INP analysis, making the correlation still less that optimal.
2) As I understand, sampling duration for INP samples cannot be much larger as particles need to be separated enough to allow for droplet formation in your offline measurement technique (the UNAM-MOUDI-DFT) in such a way that droplets do not touch (I deduce this from your remark in lines 274-275). With this, the lowest INP concentration limit that can be measured in this study was roughly 0.2 1/L. And as can be seen from your INP spectra, you mostly only observe INPs that are ice active at temperatures below -15°. INPs of biological origin are typically present at higher temperatures, and typically with lowering concentrations towards increasing temperatures. With the presented measurements you simply cannot detect most of these biological INPs (if they were there). Hence a comparison with results on biological particles cannot really be done.
3) Figure 3 shows (as far as this is visible), that on four of your five sampling days, the overall INP concentrations at your two measurements sites were mostly very similar. You even (correctly) describe this in lines 340-343. “Although the INP concentrations measured at both sites were comparable, the exemption was the May 20th sample, were notable higher and statistically significant INP concentrations were measured in the southern site between -12 °C and -22 °C.” So: Only INP concentrations measured at the southern site on May 20 were elevated, compared to the others. But then you calculate average INP concentrations for the northern site and for the southern site. It is not described how the averaging was done, but it is quite clear that the mean was used (instead of the median). This increases the average for the southern site, due to this one sample on May 20. Then, for the reminder of the text, the southern site is suddenly discussed as being elevated in concentration in general. The latter does not fit to your measurements, and hence also all conclusions drawn from that (biased) observation are invalid.
4) A possible influence of biomass burning (BB) to INPs is discussed. Backward trajectories are shown in Fig. S6 and a fire map with fires from the sampling period in Fig. S7. Overlaying the fire map with the backward trajectories (which I took the liberty to do for this review), it can be seen that the region in the south of the fire map, which showed pronounced fires, is not the region where air masses at the sampling sites came from. The remaining few spots showing active fires on the fire maps in the regions crossed by the backward trajectories are so scarce and small that it is difficult to follow the argument about the importance of BB for INPs.
Also, concerning “regional transport”, the text states: “Figure S6 also suggests that the air masses arriving at the northern site at noon and midnight, at 250 m and 500 m AGL, were not transported over the southern site, and vice versa.” However, when overlaying the backward trajectories for both sides onto the fire map, it becomes obvious that the air masses arriving at both sides often came from the same directions. While the above statement is correct, it does give a wrong impression, as it suggests different air masses were observed at the two sites.
5) A general remark about some of the values that were used in this manuscript to characterize ice activity of INPs, namely the temperature at which the first freezing is observed (T_0) and the temperature at which half of all examined droplets are frozen (T_50):
T_0 and T_50 can only be used to compare data that were collected and evaluated under the same conditions concerning sampling flow, sampling duration and evaluation conditions. This can be seen when looking at equation (2), in which there is “V” in the denominator (“V is the volume of air through the MOUDI (L)”). The sampled air volume determines the INP concentration range one will get. And that determines the temperature range in which data will be obtained. And that determines T_0 and T_50. This makes a comparison of T_0 and T_50 obtained here with data obtained in other studies (as done in e.g. lines 332-334) meaningless, unless these literature data were obtained under the same conditions.
But anyway, the passage in which T_0 and T_50 are described (lines 326 – 334 and Fig. 2) does not add anything above what again is discussed below for concentrations. Therefore, this part could be deleted.
In the following, abovementioned concerns will come up again, together with additional comments. Parts of the text that are concerned by abovementioned concerns that are not explicitly mentioned below nevertheless need to be revised.
Major comments:
Abstract, lines 29: What are “criteria pollutants”? Maybe delete these two words?
Abstract, lines 30-31: Did the INPs you found really originate from the Mexico City region, or was it long-range transport? This cannot be said, based on your data. All you can say for sure was, that aerosol particles collected at the two sites in the MCMA were found to act as INPs.
Abstract, lines 32-33: Samples "are" not INPs, samples "contain" INPs.
Abstract, lines 33-34: There is only a weak positive correlation. Revise.
Abstract, lines 34-35: See my comments on biological particles. Revise accordingly.
Abstract, line 37: The difference was only found for one of five sample collection days.
Abstract, lines 37-39: While there may be different microclimates at the two sites, you do not show this clearly for the INPs, and you do not show the reasons for the higher INP concentrations on May 20. Also, you do not show any connection to conditions higher up in the atmosphere. Any connection to aerosol-cloud interactions cannot be derived from your data. Revise.
Line 99: The sequence in the introduction is strange: You talked about the MCMA before, then added some general text on mixed phase clouds and now come back to the MCMA. There should be a stronger common thread.
Lines 102-105: This sentence is only important for cirrus clouds. However, you are not touching cirrus clouds or cirrus cloud conditions at all in your study. I suggest to delete it.
Line 124-125: You are characterizing the atmospheric aerosol on ground. And although this also includes INPs, which potentially may play a role in clouds in their lifetime, you are not looking into aerosol-cloud interactions in general, let alone for different microclimates in the city. It remains fully open how much mixing would happen from the ground up to a potential cloud level, and how differences in these sites that are 16 km apart would influence this. This is misleading. Revise.
The following remarks down to the one concerning line 243 are about the presentation of your measurements, which was not done in a straight forward way. Generally, information on the three samplers is scattered in Section 2. It would help to have one table including all three methods, their cut-offs, sampling durations and sampling dates.
Line 170: Here you give the impression that culturable microorganisms’ identification is done on samples collected for 24 hours. In 2.2.5, you write that the sampling duration on the BioStage impactor was set to 5 min. What is correct?
Line 172-176: You mention “the 24-hour samples” here, but from the text above it is not clear which samples you are referring to. This is confusing. I assume in the following, that you refer to the MiniVol TAS samples which you describe below. This is part of the flow in this chapter that needs to be improved.
Also, in Table 1 below, the sampling duration is ~ 4 h for the INP samples, which is different from the 24 hours you had for the PM2.5 samples. This is confusing and could be presented more clearly (e.g., in one table for all sampling methods as suggested above). Also: Discuss somewhere in your text: How do you expect different sampling durations to influence correlations between data from different samples?
Then you mention 24 h samples for May 12 and 13 in the text, but on these days, no INP samples were collected. Were these samples from May 12 and 13 used in the analysis, anyway? If yes, how does that influence correlations between data on chemical composition and INPs?
Line 175, Table 1: You show 7 filter samples in this table, but only 5 in the SI, Fig. S4. Where does this discrepancy come from? If you only discuss 5 samples in this manuscript, adjust Table 1 accordingly.
Lines 242-243: The sampling duration of the BioStage impactor was very short compared to the sampling duration for the other samples. That can be problematic. Comment on that. Also, give the cut-off size for the BioStage impactor.
Lines 328-329: Here you give a misleading impression by describing “the highest T_0 difference”. Only in the next paragraph you, quite correctly, state that there was a statistically significant difference between INP concentrations at both measurement sites only on one of the five sampling days. Revise.
Line 354 and Fig. 4: Usually when authors decide to show data at only a few temperatures, this is done to allow for a clearer presentation. Bar charts can be used for that. However, here only INP spectra are shown (again), apart from the fact that now average data are shown and the temperature spacing is larger. This could be presented in a better way. But: as discussed above, using the mean for averaging distorts your results. And even then, the average INP concentrations from the two sites are really only (almost) different at -15°C – generally, as far as I can see, they agree within error bars.
(A further remark: If you show INP spectra in figures, please put your own data on top.)
Line 356: The fact that the southern samples are higher in Fig. 4 only originates in one high sample collected on May 20, and in you using the mean to obtain the average. (Which, by the way, should be mentioned.) This gives the wrong impression.
An example: If data are averaged that span a broad range of values, using the median is better. Imagine you have e.g. values of 1,2,3,4,5,6,7,8,9,10,10000. The median is 6. The mean is 914. What you are doing is similar to interpreting the value of 914 as something representing the whole range of values.
Lines 371-372: Yes, in theory, particle size and INP efficiency ARE related, IF you look at particles of different sizes from the SAME substance. It is not valid in general, when comparing different types of INPs. In your samples, you likely have different particles acting as INPs in the different size classes, and therefore they cannot be compared like that!
You can see this nicely in the possibility to use a parameter as the surface site density. This parameter is valid for INPs from one particle type which shows that indeed particle size and INP efficiency are related. BUT it is different between different particle types. An example can be seen in Fig. 3 in Ullrich et al. (2017).
Lines 375-379: All of this gives a wrong impression – see the comment directly above. Revise text accordingly.
And more general, a difference between the two sites is mainly seen for larger diameters (Fig. S4 and main criticism 1), and from looking at Fig. 4 it may be deduced that this is also what explains the difference in INP concentrations on May 20. Therefore, atmospheric processing is a less likely mechanism to explain the difference you observe. A larger contribution from larger (biogenic?) particles at the southern site may explain your observations.
Line 405-407: In the here cited paper by Wang et al. (2012), amorphous SOA particles are examined. These amorphous particles do not form at the temperatures and atmospheric conditions you are looking at - it takes much lower temperatures (as said in the cited publication). Remove this citation and the reasoning about a possible SOA contribution to INPs for your southern site, as it is highly misleading!
Lines 413 ff and Fig. 6: For which of the INP data is this correlation done? Only for those INP samples on the smaller MOUDI stages, or for all? I assume the latter, which makes the correlations meaningless.
Line 425-426: You again stress “the importance of the different criteria pollutants on the ice nucleating abilities of the urban particles” and how they differ with microclimate. However, from your data, there is no consistent picture, likely because there is no correlation. And, as described above, the two sites do not really differ much, besides for one day on which most notably the largest INPs occurred in higher concentrations at the southern site. These additional INPs were particles > 3.2 mm, which means they were in the size range in which you do not have any chemical information (due to sampling PM2.5).
You yourself mentioned another study (Cabrera-Segoviano et al., 2022) which looked at high pollution. But in that other study, INP concentrations were very similar to yours. To me, this rather indicates that pollution does not add INPs.
Generally, sources for INPs differ from pollution sources. INPs often come from mineral dust or from biogenic sources. So, if you really look at what your data show, your study just repeats what many other studies in other parts of the world also found, and what is easy to explain: No correlation of INP concentrations with pollution! (More citations on that could be added to what you already added in your introduction in lines 96-97.)
In summary: It does not make sense to assume that the two sites at which you measured are different in the sense you suggest with this sentence. Delete!!!
Lines 451-453: The rise in S and K on May 20 is much stronger for the northern site, which, however, did not show elevated INP concentrations. Take that into account in your arguments throughout the text. Also, could K be related to K-feldspar?
There are studies showing that biomass burning (BB) does not increase INP concentrations (e.g. Tarn et al., 2018).
Lines 474-477: I overlayed the fire map with the backward trajectories, and it does NOT seem as if there were many fires along the trajectories. Revise!
Lines 477-479: Similarly, yes, the backward trajectories for one site did not cross the other, but air-masses came from very similar directions (particularly those from the north-east at midnight). Revise!
Lines 481-492: What do you want to show with these dendrograms? They are merely shown but not really discussed. The last sentence just gives a very general statement, reflecting what earlier studies found before.
I expect that these dendrograms were done based on results from the PM2.5 samples? Therefore, while it is fine to corroborate earlier results, it however cannot be connected to the other samples (INP and bio-particles). Make this clear!
Line 494 ff (Chapter 3.3) and related text elsewhere in the manuscript: Particles for biological analysis were only sampled for 5 minutes, compared to ~ 4 h for the INP samples. At what time of the day were the bio-samples taken? Also, likely the inlet cut-off differed between the MOUDI and the bio-sampler (which I assume to have a total air inlet). So while the data on bio-particles stand for themselves, a correlation with INP data and all other data obtained for PM2.5 cannot easily be made. Mention this caveat in the text.
Lines 517-519: Your lower detection limit seems to be too high (i.e., the sampling duration too short) to detect the ice activity of bioparticles. They are rarer than your lowest detection limit, so you cannot say anything about them. Also, the above comment on T_0 applies here. Revise this sentence and also the whole paragraph.
Line 569: You write “such as particle morphology, coating, and degree of aging”. Already, the two sites show quite similar INP concentrations (besides for larger INPs which were higher in concentration at the southern site on one day). Why go deeper into these effects, as your data suggests that you should look at larger (micron-sized) particles and their origins, first. Remove this statement, as it does not fit your results.
Lines 570-571: To draw the connection to cirrus clouds here is VERY far fetched, given the altitude at which cirrus form. It is a long way (and a lot of mixing) from an emission at a location in a city to the cirrus cloud level. Delete this sentence.
Lines 558-562: The first of the two sentences is correct for your (and earlier) results on chemical composition. However, your study does not show a convincing connection to INPs (for reasons discussed above). Therefore, the second sentence in the paragraph is highly misleading and needs to be removed or strongly revised.
Minor and editorial comments:
Line 53: “along” seems wrong in this context. Replace.
Line 57: You give values in terms of concentrations to describe the difference between the two measurement sites. Additionally giving percentages here would be very helpful to contextualize this information.
Line 75: How is the meteorological situation in the MCMA? Please add at least the main wind direction or describe typical daily wind direction patterns.
Line 85: MPC -> MPCs
Line 126: Which PM? As you use different inlets, please already mention this restriction here by giving the different size ranges (PM2.5, PM10, total suspended particles) you collected.
Line 147: What is the meaning of the different colors of the monitoring stations (green and yellow)? If this does not matter, maybe only use one color.
Lines 154-155: How is the condition of this ecological reserve at the time of your measurements? Dried out? Blooming? Green? Describe briefly.
Line 169: Change “INP abilities” to “INP samples”.
Line 186: “used to collect bacteria and fungi identification”: It certainly collected also other particles. And it certainly does not collect “identification”. Revise.
Line 192: “(Campbell and Davis)”: Is this the company who built the meteorological station? Or a publication describing it? Add this information.
Line 210: “the 47mm Teflon filters” -> You likely mean the MiniVOL samples here. Please add this information.
Lines 216 and 219: Why did you put the anions and cations in brackets?
Line 229: “all the particle samples” -> Please add more precisely which samples were used for this.
Line 231: Change from “(Espinosa et al., 2012)” to “Espinosa et al. (2012)”.
Lines 347-348, Caption of Fig. 3: Replace “northern and southern particles” with "for the measurements done at the northern and southern site".
Line 364-365 (Caption of Fig. 4): Were all three data-sets (given in green, yellow and red) collected during a high pollution episode, or only the latter? Clarify!
Line 370: Delete “the” before “urban”.
Line 459: “notorious” sounds strange in this context -> exchange by a better word.
Line 496: Did you measure “fungi” or “fungal spores”? (If needed, check the whole manuscript.)
Line 533-534: How about vice versa: Were there bacteria and fungi at the southern site that were not present at the northern site? This seems to be expectable, as the southern site seems to be closer to vegetated areas.
SI Line 22: Please format the SI such, that tables are all visible on one page. This may mean to have empty space in between, but it increases readability enormously.
SI Line 44: “the” should not be bold.
SI Fig. S4: Show this plot on an extra page with larger panels (maybe two columns x 3 rows). The way it is now, it is difficult to see details.
SI Fig. S6 and S7: Either show the same section in all three of the panels on display, or overlay the firemap with the trajectories. (This is related to one of the main comments.)
Personally, I would prefer if all trajectories were shown together with the fire map. If you agree to do so, you can color e.g. the north data in aqua (instead of blue) and magenta (instead of red). Then all trajectories are visible.
It will become easier to judge to which extent fires may have influenced the measurement sites, and from which directions air masses came to your two measurement sites.
Literature:
Cabrera-Segoviano, D., Pereira, D. L., Rodriguez, C., Raga, G. B., Miranda, J., Alvarez-Ospina, H., and Ladino, L. A.: Inter-annual variability of ice nucleating particles in Mexico city, Atmos. Environ., 273, 118964, https://doi.org/10.1016/j.atmosenv.2022.118964, 2022.
Tarn, M. D., et al. (2018), The study of atmospheric ice-nucleating particles via microfluidically generated droplets, Microfluidics and Nanofluidics, 22(5), doi:10.1007/s10404-018-2069-x.
Ullrich, R., C. Hoose, O. Möhler, M. Niemand, R. Wagner, K. Höhler, N. Hiranuma, H. Saathoff, and T. Leisner (2017), A New Ice Nucleation Active Site Parameterization for Desert Dust and Soot, J. Atmos. Sci., 74(3), 699–717, doi:10.1175/jas-d-16-0074.1.
Wang, B., Lambe, A. T., Massoli, P., Onasch, T. B., Davidovits, P., Worsnop, D. R., and Knopf, D. A.: The deposition ice nucleation and immersion freezing potential of amorphous secondary organic aerosol: Pathways for ice and mixed‐phase cloud formation, J. Geophys. Res., 117, 2012JD018063, https://doi.org/10.1029/2012JD018063, 2012.
Citation: https://doi.org/10.5194/egusphere-2025-6106-RC2 -
AC2: 'Reply on RC2', Luis A. Ladino, 22 Apr 2026
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2026/egusphere-2025-6106/egusphere-2025-6106-AC2-supplement.pdf
-
AC2: 'Reply on RC2', Luis A. Ladino, 22 Apr 2026
Interactive discussion
Status: closed
-
RC1: 'Comment on egusphere-2025-6106', Anonymous Referee #1, 06 Feb 2026
Review of “Ice Nucleating Particles Variability Across a Megacity” by Mendoza-Téllez et al. (2026)
The paper reports on a one-week measurement campaign collecting samples at two locations in the north and south of Mexico City, 16 km apart. Size-segregated samples were analysed for ice nucleating particle (INP) concentration, and aerosol chemical composition, bioaerosol concentration, concentrations of several gases, and meteorological parameters were monitored. The INP concentration was found to differ between the sites on at least one day of sampling, and a connection to aerosol chemistry is explored. The paper requires major revisions, in particular because of a temporal misalignment problem in the correlation analysis.
Specific comments:
Line 29: Specify which criteria pollutants (PM2.5, SO2, NOx, CO, O3) were measured. Not all readers may be familiar with the term.
Lines 33, 34, 126, 259, 326, 421, 426, 429, 455, 524, 537, 544, 549, 567 and throughout the manuscript: Replace INP “efficiency”, “ability”, “activity”, and “behaviour” with “INP concentration”. This change is necessary because the study measures INP concentration, not the ice nucleation efficiency of a known substance with a defined surface area.
Line 36f: Clarify how the role of aerosol in cloud formation was evaluated.
Lines 38, 353, 396: The concept of microclimates, including their definition and identification criteria, needs to be explained in the introduction. According to Met Office factsheet 14 (Microclimates), microclimate criteria apply on climatic timescales that cannot be determined based on one week of data. Please clarify which factors are assumed to create a microclimate within the MCMA.
Lines 39f, 81: The discussion of how aerosol–cloud interactions impact extreme precipitation events is limited to one sentence in the introduction. If this is a main motivation for the study, it could be summarized in more detail.
Line 69f: Related to the previous comment, elaborate on what is meant by microclimate theory and provide a supporting reference. Molina and Molina (2004) do not discuss microclimate theory.
Line 74: Elaborate on why microclimatic effects are considered highly important for local precipitation events in the MCMA and provide references. It would be expected that synoptic-scale moisture supply and dynamical forcing are at least equally important.
Line 81: Extend the discussion on how INPs affect extreme precipitation, for example through their influence on deep convective clouds associated with extreme rainfall.
Table 1: Provide the sample volume in an additional column.
Line 180: In comparison, the inlet cut-size of 2.5 µm of the MiniVol excludes particle sizes collected on the two upper and partially the third of the four MOUDI stages used to obtain INP concentrations. As the four MOUDI stages contribute equally to the INP concentration (no size dependence observed), this indicates that over 60% of INPs are excluded from the MiniVol samples. This is the first reason why the correlation analysis between INP concentration and MiniVol-derived parameters can be misleading.
Section 2.2: The MOUDI flow rate and sample substrate (line 263) could be included in this section to consolidate information on sampling procedures. It would be helpful to report sampling flow rates, time of day of collection, and time resolution for all samplers.
Line 243: At what time of day were the samples collected, and how many samples were collected per day?
Line 294: Do you mean the area on which aerosol is deposited? Is aerosol deposited exclusively on the coverslip and not over the entire impaction stage? Adeposit is defined as the coverslip area also in Manson et al. (2016); however, their Fig. 7 shows that the coverslip covers only about one third of the impaction stage. For normalization of the sampled volume, the entire area over which aerosol is deposited should be used. Please include a photo of a loaded sample stage in the reply to this comment for clarification.
Section 3.1: Figures S4, 2, and 3 show only one sample per day, while Table 1 indicates that two samples were taken on both 17 and 18 May. Please include these samples to show diurnal variability in INP concentration and add a corresponding discussion.
Line 320: Selecting a restricted size range is not necessary. Using all eight MOUDI stages allows investigation of ~100% rather than 70% of INPs. There are two additional reasons to include the lower stages: (1) these stages are better represented by the MiniVol samples with a 2.5 µm cut-off (see previous comment), and (2) the main finding of no size dependence in INP concentration could be further supported. There is a potential contradiction between “no size dependence” and “70% of INPs are super-micron” that could be resolved. The analysis could clarify whether the lack of size dependence applies only to super-micron particles or across a broader size range.
Line 324: Describe how the homogeneous freezing line was determined and how it compares with published measurements, for example those in Shardt et al. (2022) for 100 µm droplets.
Line 327: Explain how the averages and error bars in Fig. 2 were calculated. In particular, clarify how freezing curves from different MOUDI stages were combined and how differences in droplet numbers between experiments were accounted for.
Line 332f: Please quantify and analyse the causes of the differences in T₅₀ and T₀ compared to literature. For example, the introduction notes that Knopf et al. (2010) reported ice nucleation at cirrus conditions, whereas the present study measures freezing of droplets in the MPC regime.
Line 342, Fig. 3: The error bars of South-20220520 overlap with those of North-20220520. Please clarify what is meant by statistically significant INP concentrations. What do the error bars represent, and how are they calculated? For South-20220520, why are the error bars smaller at −13 and −14 °C than at −12 and −15 °C? Consider using the method of Agresti and Coull (1998) to calculate 95% confidence intervals.
Line 345, Figure 3: Explain why Beijing is an appropriate city for comparison of INP concentrations. Consider adding data from Rodríguez-Gómez (2021) and Pereira (2021) to Fig. 3 (see comment on Fig. 4).
Line 353: Specify how the average accumulated INP concentration is calculated, which data are averaged, and what the error bars in Fig. 4 represent.
Line 357: The difference between the north and south samples at −15 °C is not clearly evident in Fig. 4, given the overlapping concentration ranges.
Figure 4: The figure does not provide substantial information beyond what is already shown in Fig. 3. It could be removed, with the reference data added to Fig. 3 instead. In addition, the yellow data symbol is difficult to see; a darker colour would improve visibility.
Line 371ff: It is correct that particle size and surface area affect the ice nucleation efficiency of particles with the same composition. When multiple particles of different compositions are present in a droplet, the combined abundance of ice-active sites at a given temperature determines ice formation. The amount and composition of particles on different MOUDI stages likely differs but is unknown. It is also unknown how the amount and composition of particles changes from day to day and between the sampling locations. Because only INP concentration per stage is known, interpretations involving coatings or physicochemical heterogeneities require supporting evidence or should be omitted.
Figure 5: Consider avoiding “dynamite stick” plots. Showing individual data points would be more informative. In general, bar plots on a logarithmic scale can be misleading because bar area has no physical meaning.
Line 399ff: It may be useful to note that NOx and measured radiation are higher at the northern site; thus, elevated O3 concentrations at the southern site could reflect higher VOC levels, which were not measured. Any impact on INP concentration remains speculative. Wang et al. (2012) measured naphthalene, an anthropogenic VOC associated with combustion rather than biogenic SOA, and investigated ice nucleation at cirrus conditions, outside the experimental range of the present study. Moreover, typical SOA particle sizes are below 1 µm, whereas super-micron particles were used for the INP analysis.
Line 414: Describe how these measurements were processed and averaged to match the INP sample collection periods.
Line 425: Provide an explanation of how different compounds may influence INP concentration and why these effects could differ between sites. Clarify why INP parameters correlate with chemical parameters at one site but not the other. The small number of data points (n = 5) makes the correlation analysis sensitive to outliers. Inspecting scatterplots could help identify non-linear relationships or outliers. In addition, explain how high correlations with T₅₀ can occur without corresponding correlations in INP concentrations at −20 or −25 °C, the temperature range where T₅₀ is located. Please assess how robust the correlations are at ±1 °C from the chosen temperatures. The possibility of spurious correlations due to limited sample size (second reason why the correlation analysis may be misleading) should be addressed by presenting scatterplots.
Figure 6: Indicate the confidence level associated with values marked by an asterisk.
Line 432ff: INP samples were collected during a 4-hour morning period, whereas filter samples were collected over 24 hours. As shown in Fig. S6, air mass origin changed during the 24-hour period, indicating that different aerosol populations were analysed for composition and INP concentration. For correlation analysis, sampling intervals must be temporally consistent. Correlating temporally misaligned samples constitutes a methodological issue. This is the third reason why the correlation analysis involving MiniVol data can be misleading. I recommend removing this part of the analysis and the associated discussion.
Line 454: In Fig. 6, the correlation with INP concentration at −20 °C is shown as not significant.
Line 466ff: This appears to contradict the discussion of O₃ concentrations in lines 399–407. If VOC concentrations are higher in the north, higher O₃ concentrations would also be expected there.
Lines 470–473: This discussion repeats points made in lines 452–456.
Line 475: Provide the altitude of the trajectories. Overlaying Figs. S7 and S6 could clarify which trajectories are influenced by biomass burning and why this effect is more pronounced at the southern site. Potassium, a tracer for biomass burning, is higher at C5 than at CU on most days (Fig. 7).
Line 481ff: The interpretation of the three clusters requires further explanation. For example, why are Pb, Cl⁻, Mn, and Ca assigned to the soil cluster in the north but to the anthropogenic cluster in the south? Briefly explain the clustering method and how to interpret the dendrogram produced using Ward’s method with Pearson correlation coefficients. Clarify how clustering leads to source identification and whether these sources relate to observed INP concentrations.
Line 510: Explain how the finding that 57% of bacteria are Gram-positive affects the analysis, given that ice-nucleation-active bacteria are predominantly Gram-negative.
Figure 8: INP concentrations were measured between 16–20 May. Why is a longer time series of bacteria and fungi shown? What additional insight is provided by comparison with PM₂.₅?
Line 530: Pseudomonas, Pantoea, Alternaria, and Fusarium from other locations have been reported to nucleate ice above −10 °C. Are local strains not producing ice-nucleation proteins?
Line 533: Clarify why cross-correlation analysis was performed in the context of this study.
Line 550: Explain why correlations with these parameters imply compositional effects rather than simply reflecting aerosol amount (e.g., PM2.5).
Lines 552–556: Clarify the connection between these particle types and INP concentration.
Line 559: Specify which atmospheric processes are referred to and how particle formation is linked to INP concentration.
Lines 560ff, 543: Explain why INP concentrations are compared with those from Beijing. Similar concentrations might suggest that, contrary to the conclusions, urban INP concentrations are not strongly linked to the listed factors.
Line 566: Specify what concrete information was obtained.
Table S6: Consider adding a column indicating Gram-positive or Gram-negative classification and another listing temperature ranges over which species are reported to act as INPs, based on literature data.
Figure S1: Fig. S6 suggests predominantly westerly winds at midday, whereas these wind roses show mainly easterly winds. Restricting the wind analysis to the MOUDI sampling periods could be informative.
Technical corrections:
Line 80: something is missing in this long sentence. Do you mean “… information on the interplay …”?
Line 118: Delete the “B” before proteobacteria.
Figure 6: Br is missing from panel (a) but appears in Fig. S8. CO is missing from panel (b) but is shown in Fig. S2.
Figure 7: Replot the figure including zero on each ordinate rather than overlapping y-axes.
Figure 8: Red stars without connecting lines are filled symbols in the plot but shown as open symbols in the legend.
Figure S3: “Adapted” implies modifications. “Reprint of Fig. 3 from Córdoba et al. (2021)” would be accurate.
Figure S5: The y-axis labels of individual subfigures seem irregular. Replot including zero on each ordinate.
Figures S8 and S9: Blue lines below the green cluster are difficult to see. Consider using different colours for clusters in Fig. S9, as they do not correspond to the same sources as in Fig. S8.
References:
Agresti, A. and Coull, B. A.: Approximate is better than “exact” for interval estimation of binomial proportions, Am. Stat., 52, 119, https://doi.org/10.2307/2685469, 1998.MetOffice factsheet 14, https://www.metoffice.gov.uk/binaries/content/assets/metofficegovuk/pdf/research/library-and-archive/library/publications/factsheets/factsheet_14-microclimates_2023.pdf
Shardt, N. et al.: Homogeneous freezing of water droplets for different volumes and cooling rates, Phys. Chem. Chem. Phys., 24, 28213-28221, https://doi.org/10.1039/D2CP03896J, 2022.
Citation: https://doi.org/10.5194/egusphere-2025-6106-RC1 -
AC1: 'Reply on RC1', Luis A. Ladino, 22 Apr 2026
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2026/egusphere-2025-6106/egusphere-2025-6106-AC1-supplement.pdf
-
AC1: 'Reply on RC1', Luis A. Ladino, 22 Apr 2026
-
RC2: 'Comment on egusphere-2025-6106', Anonymous Referee #2, 24 Feb 2026
Review of „Ice Nucleating Particles Variability Across a Megacity” by Sebastián Mendoza-Téllez et al., submitted to EGUsphere.
The manuscript describes measurements of atmospheric aerosol particles done on a few days (5 to 7, depending on sample) at two different sites (16 km apart) in Mexico city. Measurements include a variety of parameters from three types of samples: a MiniVol Tactical Air Sampler (Airmetrics) with a 2.5 µm cut-size inlet for chemical analysis; an eight stage micro-orifice uniform deposit impactor (MOUDI) for INP (ice-nucleating particle) analysis with an upper sampling size of 10 mm; and a BioStage cascade impactor (cut-off size not given, likely total suspended particles) for the analysis of viable bacteria and fungi. All sample types not only had different cut-off sizes, but also different sampling durations (24h, ~ 4h and 5 min, respectively) but also a different amount of collection days, and it did not become clear which data from which days were used for comparisons.
Conclusions drawn by the authors oftentimes seem to include some wishful thinking, as I will elaborate on in more detail below. Due to this, but also due to the data as such and of what they show, I strongly suggest to the editor to consider if this should rather be published as a measurement report. But in any case, I can recommend publication of this study only after the data interpretation will have been adapted to what the data really show and after the text will have been thoroughly and accordingly revised.
My main points of criticism (all of them equally important) are the following:
1) The above-mentioned different cut-off sizes for the different samples, their different collection durations and the different days of sample collection make a comparison of the (bulk) results for the different particle characteristics difficult or even meaningless.
INP data from the two study sites differ particularly in the larger size bins (> 5.6 mm for 4 of 5 samples, 3.2 – 5.6 mm for two and 1.8 – 3.2 mm for one sample). This is an interesting result, which, however, is not discussed at all. Unfortunately, for these larger sizes, there is no information on the chemical composition.
On the other hand, for the presented correlation between INP data and chemical composition (Fig. 6 and related text) it was not described for which INP data (all MOUDI size bins or only the ones for smaller particles?) this was done. Hence the presented correlation may or may not be meaningless in general. From the text I assume that the fully summed up INP concentrations (over all MOUDI stages) were used for the comparison. It would make sense to sum up the two MOUDI-stages with the smallest INPs on them and compare the resulting INP concentrations with results from the PM2.5 chemical analysis. Then, it can also be described which fraction of all INPs is in these two smallest MOUDI-stages. However, sub-micron particles will still be missed in the INP analysis, making the correlation still less that optimal.
2) As I understand, sampling duration for INP samples cannot be much larger as particles need to be separated enough to allow for droplet formation in your offline measurement technique (the UNAM-MOUDI-DFT) in such a way that droplets do not touch (I deduce this from your remark in lines 274-275). With this, the lowest INP concentration limit that can be measured in this study was roughly 0.2 1/L. And as can be seen from your INP spectra, you mostly only observe INPs that are ice active at temperatures below -15°. INPs of biological origin are typically present at higher temperatures, and typically with lowering concentrations towards increasing temperatures. With the presented measurements you simply cannot detect most of these biological INPs (if they were there). Hence a comparison with results on biological particles cannot really be done.
3) Figure 3 shows (as far as this is visible), that on four of your five sampling days, the overall INP concentrations at your two measurements sites were mostly very similar. You even (correctly) describe this in lines 340-343. “Although the INP concentrations measured at both sites were comparable, the exemption was the May 20th sample, were notable higher and statistically significant INP concentrations were measured in the southern site between -12 °C and -22 °C.” So: Only INP concentrations measured at the southern site on May 20 were elevated, compared to the others. But then you calculate average INP concentrations for the northern site and for the southern site. It is not described how the averaging was done, but it is quite clear that the mean was used (instead of the median). This increases the average for the southern site, due to this one sample on May 20. Then, for the reminder of the text, the southern site is suddenly discussed as being elevated in concentration in general. The latter does not fit to your measurements, and hence also all conclusions drawn from that (biased) observation are invalid.
4) A possible influence of biomass burning (BB) to INPs is discussed. Backward trajectories are shown in Fig. S6 and a fire map with fires from the sampling period in Fig. S7. Overlaying the fire map with the backward trajectories (which I took the liberty to do for this review), it can be seen that the region in the south of the fire map, which showed pronounced fires, is not the region where air masses at the sampling sites came from. The remaining few spots showing active fires on the fire maps in the regions crossed by the backward trajectories are so scarce and small that it is difficult to follow the argument about the importance of BB for INPs.
Also, concerning “regional transport”, the text states: “Figure S6 also suggests that the air masses arriving at the northern site at noon and midnight, at 250 m and 500 m AGL, were not transported over the southern site, and vice versa.” However, when overlaying the backward trajectories for both sides onto the fire map, it becomes obvious that the air masses arriving at both sides often came from the same directions. While the above statement is correct, it does give a wrong impression, as it suggests different air masses were observed at the two sites.
5) A general remark about some of the values that were used in this manuscript to characterize ice activity of INPs, namely the temperature at which the first freezing is observed (T_0) and the temperature at which half of all examined droplets are frozen (T_50):
T_0 and T_50 can only be used to compare data that were collected and evaluated under the same conditions concerning sampling flow, sampling duration and evaluation conditions. This can be seen when looking at equation (2), in which there is “V” in the denominator (“V is the volume of air through the MOUDI (L)”). The sampled air volume determines the INP concentration range one will get. And that determines the temperature range in which data will be obtained. And that determines T_0 and T_50. This makes a comparison of T_0 and T_50 obtained here with data obtained in other studies (as done in e.g. lines 332-334) meaningless, unless these literature data were obtained under the same conditions.
But anyway, the passage in which T_0 and T_50 are described (lines 326 – 334 and Fig. 2) does not add anything above what again is discussed below for concentrations. Therefore, this part could be deleted.
In the following, abovementioned concerns will come up again, together with additional comments. Parts of the text that are concerned by abovementioned concerns that are not explicitly mentioned below nevertheless need to be revised.
Major comments:
Abstract, lines 29: What are “criteria pollutants”? Maybe delete these two words?
Abstract, lines 30-31: Did the INPs you found really originate from the Mexico City region, or was it long-range transport? This cannot be said, based on your data. All you can say for sure was, that aerosol particles collected at the two sites in the MCMA were found to act as INPs.
Abstract, lines 32-33: Samples "are" not INPs, samples "contain" INPs.
Abstract, lines 33-34: There is only a weak positive correlation. Revise.
Abstract, lines 34-35: See my comments on biological particles. Revise accordingly.
Abstract, line 37: The difference was only found for one of five sample collection days.
Abstract, lines 37-39: While there may be different microclimates at the two sites, you do not show this clearly for the INPs, and you do not show the reasons for the higher INP concentrations on May 20. Also, you do not show any connection to conditions higher up in the atmosphere. Any connection to aerosol-cloud interactions cannot be derived from your data. Revise.
Line 99: The sequence in the introduction is strange: You talked about the MCMA before, then added some general text on mixed phase clouds and now come back to the MCMA. There should be a stronger common thread.
Lines 102-105: This sentence is only important for cirrus clouds. However, you are not touching cirrus clouds or cirrus cloud conditions at all in your study. I suggest to delete it.
Line 124-125: You are characterizing the atmospheric aerosol on ground. And although this also includes INPs, which potentially may play a role in clouds in their lifetime, you are not looking into aerosol-cloud interactions in general, let alone for different microclimates in the city. It remains fully open how much mixing would happen from the ground up to a potential cloud level, and how differences in these sites that are 16 km apart would influence this. This is misleading. Revise.
The following remarks down to the one concerning line 243 are about the presentation of your measurements, which was not done in a straight forward way. Generally, information on the three samplers is scattered in Section 2. It would help to have one table including all three methods, their cut-offs, sampling durations and sampling dates.
Line 170: Here you give the impression that culturable microorganisms’ identification is done on samples collected for 24 hours. In 2.2.5, you write that the sampling duration on the BioStage impactor was set to 5 min. What is correct?
Line 172-176: You mention “the 24-hour samples” here, but from the text above it is not clear which samples you are referring to. This is confusing. I assume in the following, that you refer to the MiniVol TAS samples which you describe below. This is part of the flow in this chapter that needs to be improved.
Also, in Table 1 below, the sampling duration is ~ 4 h for the INP samples, which is different from the 24 hours you had for the PM2.5 samples. This is confusing and could be presented more clearly (e.g., in one table for all sampling methods as suggested above). Also: Discuss somewhere in your text: How do you expect different sampling durations to influence correlations between data from different samples?
Then you mention 24 h samples for May 12 and 13 in the text, but on these days, no INP samples were collected. Were these samples from May 12 and 13 used in the analysis, anyway? If yes, how does that influence correlations between data on chemical composition and INPs?
Line 175, Table 1: You show 7 filter samples in this table, but only 5 in the SI, Fig. S4. Where does this discrepancy come from? If you only discuss 5 samples in this manuscript, adjust Table 1 accordingly.
Lines 242-243: The sampling duration of the BioStage impactor was very short compared to the sampling duration for the other samples. That can be problematic. Comment on that. Also, give the cut-off size for the BioStage impactor.
Lines 328-329: Here you give a misleading impression by describing “the highest T_0 difference”. Only in the next paragraph you, quite correctly, state that there was a statistically significant difference between INP concentrations at both measurement sites only on one of the five sampling days. Revise.
Line 354 and Fig. 4: Usually when authors decide to show data at only a few temperatures, this is done to allow for a clearer presentation. Bar charts can be used for that. However, here only INP spectra are shown (again), apart from the fact that now average data are shown and the temperature spacing is larger. This could be presented in a better way. But: as discussed above, using the mean for averaging distorts your results. And even then, the average INP concentrations from the two sites are really only (almost) different at -15°C – generally, as far as I can see, they agree within error bars.
(A further remark: If you show INP spectra in figures, please put your own data on top.)
Line 356: The fact that the southern samples are higher in Fig. 4 only originates in one high sample collected on May 20, and in you using the mean to obtain the average. (Which, by the way, should be mentioned.) This gives the wrong impression.
An example: If data are averaged that span a broad range of values, using the median is better. Imagine you have e.g. values of 1,2,3,4,5,6,7,8,9,10,10000. The median is 6. The mean is 914. What you are doing is similar to interpreting the value of 914 as something representing the whole range of values.
Lines 371-372: Yes, in theory, particle size and INP efficiency ARE related, IF you look at particles of different sizes from the SAME substance. It is not valid in general, when comparing different types of INPs. In your samples, you likely have different particles acting as INPs in the different size classes, and therefore they cannot be compared like that!
You can see this nicely in the possibility to use a parameter as the surface site density. This parameter is valid for INPs from one particle type which shows that indeed particle size and INP efficiency are related. BUT it is different between different particle types. An example can be seen in Fig. 3 in Ullrich et al. (2017).
Lines 375-379: All of this gives a wrong impression – see the comment directly above. Revise text accordingly.
And more general, a difference between the two sites is mainly seen for larger diameters (Fig. S4 and main criticism 1), and from looking at Fig. 4 it may be deduced that this is also what explains the difference in INP concentrations on May 20. Therefore, atmospheric processing is a less likely mechanism to explain the difference you observe. A larger contribution from larger (biogenic?) particles at the southern site may explain your observations.
Line 405-407: In the here cited paper by Wang et al. (2012), amorphous SOA particles are examined. These amorphous particles do not form at the temperatures and atmospheric conditions you are looking at - it takes much lower temperatures (as said in the cited publication). Remove this citation and the reasoning about a possible SOA contribution to INPs for your southern site, as it is highly misleading!
Lines 413 ff and Fig. 6: For which of the INP data is this correlation done? Only for those INP samples on the smaller MOUDI stages, or for all? I assume the latter, which makes the correlations meaningless.
Line 425-426: You again stress “the importance of the different criteria pollutants on the ice nucleating abilities of the urban particles” and how they differ with microclimate. However, from your data, there is no consistent picture, likely because there is no correlation. And, as described above, the two sites do not really differ much, besides for one day on which most notably the largest INPs occurred in higher concentrations at the southern site. These additional INPs were particles > 3.2 mm, which means they were in the size range in which you do not have any chemical information (due to sampling PM2.5).
You yourself mentioned another study (Cabrera-Segoviano et al., 2022) which looked at high pollution. But in that other study, INP concentrations were very similar to yours. To me, this rather indicates that pollution does not add INPs.
Generally, sources for INPs differ from pollution sources. INPs often come from mineral dust or from biogenic sources. So, if you really look at what your data show, your study just repeats what many other studies in other parts of the world also found, and what is easy to explain: No correlation of INP concentrations with pollution! (More citations on that could be added to what you already added in your introduction in lines 96-97.)
In summary: It does not make sense to assume that the two sites at which you measured are different in the sense you suggest with this sentence. Delete!!!
Lines 451-453: The rise in S and K on May 20 is much stronger for the northern site, which, however, did not show elevated INP concentrations. Take that into account in your arguments throughout the text. Also, could K be related to K-feldspar?
There are studies showing that biomass burning (BB) does not increase INP concentrations (e.g. Tarn et al., 2018).
Lines 474-477: I overlayed the fire map with the backward trajectories, and it does NOT seem as if there were many fires along the trajectories. Revise!
Lines 477-479: Similarly, yes, the backward trajectories for one site did not cross the other, but air-masses came from very similar directions (particularly those from the north-east at midnight). Revise!
Lines 481-492: What do you want to show with these dendrograms? They are merely shown but not really discussed. The last sentence just gives a very general statement, reflecting what earlier studies found before.
I expect that these dendrograms were done based on results from the PM2.5 samples? Therefore, while it is fine to corroborate earlier results, it however cannot be connected to the other samples (INP and bio-particles). Make this clear!
Line 494 ff (Chapter 3.3) and related text elsewhere in the manuscript: Particles for biological analysis were only sampled for 5 minutes, compared to ~ 4 h for the INP samples. At what time of the day were the bio-samples taken? Also, likely the inlet cut-off differed between the MOUDI and the bio-sampler (which I assume to have a total air inlet). So while the data on bio-particles stand for themselves, a correlation with INP data and all other data obtained for PM2.5 cannot easily be made. Mention this caveat in the text.
Lines 517-519: Your lower detection limit seems to be too high (i.e., the sampling duration too short) to detect the ice activity of bioparticles. They are rarer than your lowest detection limit, so you cannot say anything about them. Also, the above comment on T_0 applies here. Revise this sentence and also the whole paragraph.
Line 569: You write “such as particle morphology, coating, and degree of aging”. Already, the two sites show quite similar INP concentrations (besides for larger INPs which were higher in concentration at the southern site on one day). Why go deeper into these effects, as your data suggests that you should look at larger (micron-sized) particles and their origins, first. Remove this statement, as it does not fit your results.
Lines 570-571: To draw the connection to cirrus clouds here is VERY far fetched, given the altitude at which cirrus form. It is a long way (and a lot of mixing) from an emission at a location in a city to the cirrus cloud level. Delete this sentence.
Lines 558-562: The first of the two sentences is correct for your (and earlier) results on chemical composition. However, your study does not show a convincing connection to INPs (for reasons discussed above). Therefore, the second sentence in the paragraph is highly misleading and needs to be removed or strongly revised.
Minor and editorial comments:
Line 53: “along” seems wrong in this context. Replace.
Line 57: You give values in terms of concentrations to describe the difference between the two measurement sites. Additionally giving percentages here would be very helpful to contextualize this information.
Line 75: How is the meteorological situation in the MCMA? Please add at least the main wind direction or describe typical daily wind direction patterns.
Line 85: MPC -> MPCs
Line 126: Which PM? As you use different inlets, please already mention this restriction here by giving the different size ranges (PM2.5, PM10, total suspended particles) you collected.
Line 147: What is the meaning of the different colors of the monitoring stations (green and yellow)? If this does not matter, maybe only use one color.
Lines 154-155: How is the condition of this ecological reserve at the time of your measurements? Dried out? Blooming? Green? Describe briefly.
Line 169: Change “INP abilities” to “INP samples”.
Line 186: “used to collect bacteria and fungi identification”: It certainly collected also other particles. And it certainly does not collect “identification”. Revise.
Line 192: “(Campbell and Davis)”: Is this the company who built the meteorological station? Or a publication describing it? Add this information.
Line 210: “the 47mm Teflon filters” -> You likely mean the MiniVOL samples here. Please add this information.
Lines 216 and 219: Why did you put the anions and cations in brackets?
Line 229: “all the particle samples” -> Please add more precisely which samples were used for this.
Line 231: Change from “(Espinosa et al., 2012)” to “Espinosa et al. (2012)”.
Lines 347-348, Caption of Fig. 3: Replace “northern and southern particles” with "for the measurements done at the northern and southern site".
Line 364-365 (Caption of Fig. 4): Were all three data-sets (given in green, yellow and red) collected during a high pollution episode, or only the latter? Clarify!
Line 370: Delete “the” before “urban”.
Line 459: “notorious” sounds strange in this context -> exchange by a better word.
Line 496: Did you measure “fungi” or “fungal spores”? (If needed, check the whole manuscript.)
Line 533-534: How about vice versa: Were there bacteria and fungi at the southern site that were not present at the northern site? This seems to be expectable, as the southern site seems to be closer to vegetated areas.
SI Line 22: Please format the SI such, that tables are all visible on one page. This may mean to have empty space in between, but it increases readability enormously.
SI Line 44: “the” should not be bold.
SI Fig. S4: Show this plot on an extra page with larger panels (maybe two columns x 3 rows). The way it is now, it is difficult to see details.
SI Fig. S6 and S7: Either show the same section in all three of the panels on display, or overlay the firemap with the trajectories. (This is related to one of the main comments.)
Personally, I would prefer if all trajectories were shown together with the fire map. If you agree to do so, you can color e.g. the north data in aqua (instead of blue) and magenta (instead of red). Then all trajectories are visible.
It will become easier to judge to which extent fires may have influenced the measurement sites, and from which directions air masses came to your two measurement sites.
Literature:
Cabrera-Segoviano, D., Pereira, D. L., Rodriguez, C., Raga, G. B., Miranda, J., Alvarez-Ospina, H., and Ladino, L. A.: Inter-annual variability of ice nucleating particles in Mexico city, Atmos. Environ., 273, 118964, https://doi.org/10.1016/j.atmosenv.2022.118964, 2022.
Tarn, M. D., et al. (2018), The study of atmospheric ice-nucleating particles via microfluidically generated droplets, Microfluidics and Nanofluidics, 22(5), doi:10.1007/s10404-018-2069-x.
Ullrich, R., C. Hoose, O. Möhler, M. Niemand, R. Wagner, K. Höhler, N. Hiranuma, H. Saathoff, and T. Leisner (2017), A New Ice Nucleation Active Site Parameterization for Desert Dust and Soot, J. Atmos. Sci., 74(3), 699–717, doi:10.1175/jas-d-16-0074.1.
Wang, B., Lambe, A. T., Massoli, P., Onasch, T. B., Davidovits, P., Worsnop, D. R., and Knopf, D. A.: The deposition ice nucleation and immersion freezing potential of amorphous secondary organic aerosol: Pathways for ice and mixed‐phase cloud formation, J. Geophys. Res., 117, 2012JD018063, https://doi.org/10.1029/2012JD018063, 2012.
Citation: https://doi.org/10.5194/egusphere-2025-6106-RC2 -
AC2: 'Reply on RC2', Luis A. Ladino, 22 Apr 2026
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2026/egusphere-2025-6106/egusphere-2025-6106-AC2-supplement.pdf
-
AC2: 'Reply on RC2', Luis A. Ladino, 22 Apr 2026
Peer review completion
Journal article(s) based on this preprint
Viewed
| HTML | XML | Total | Supplement | BibTeX | EndNote | |
|---|---|---|---|---|---|---|
| 1,407 | 753 | 129 | 2,289 | 321 | 102 | 161 |
- HTML: 1,407
- PDF: 753
- XML: 129
- Total: 2,289
- Supplement: 321
- BibTeX: 102
- EndNote: 161
Viewed (geographical distribution)
| Country | # | Views | % |
|---|
| Total: | 0 |
| HTML: | 0 |
| PDF: | 0 |
| XML: | 0 |
- 1
Sebastían Mendoza-Téllez
Karla Valdés
David Ramírez
Jan Alexis Cedillo
Olivia Rivera-Hernandéz
Fernanda Córdoda
Harry Alvarez
Javier Miranda
Irma Rosas
Graciela B. Raga
Emma Negrete
Leticia Martínez
Eva Salinas
Luis A. Ladino
The requested preprint has a corresponding peer-reviewed final revised paper. You are encouraged to refer to the final revised version.
- Preprint
(1894 KB) - Metadata XML
-
Supplement
(1521 KB) - BibTeX
- EndNote
- Final revised paper
Review of “Ice Nucleating Particles Variability Across a Megacity” by Mendoza-Téllez et al. (2026)
The paper reports on a one-week measurement campaign collecting samples at two locations in the north and south of Mexico City, 16 km apart. Size-segregated samples were analysed for ice nucleating particle (INP) concentration, and aerosol chemical composition, bioaerosol concentration, concentrations of several gases, and meteorological parameters were monitored. The INP concentration was found to differ between the sites on at least one day of sampling, and a connection to aerosol chemistry is explored. The paper requires major revisions, in particular because of a temporal misalignment problem in the correlation analysis.
Specific comments:
Line 29: Specify which criteria pollutants (PM2.5, SO2, NOx, CO, O3) were measured. Not all readers may be familiar with the term.
Lines 33, 34, 126, 259, 326, 421, 426, 429, 455, 524, 537, 544, 549, 567 and throughout the manuscript: Replace INP “efficiency”, “ability”, “activity”, and “behaviour” with “INP concentration”. This change is necessary because the study measures INP concentration, not the ice nucleation efficiency of a known substance with a defined surface area.
Line 36f: Clarify how the role of aerosol in cloud formation was evaluated.
Lines 38, 353, 396: The concept of microclimates, including their definition and identification criteria, needs to be explained in the introduction. According to Met Office factsheet 14 (Microclimates), microclimate criteria apply on climatic timescales that cannot be determined based on one week of data. Please clarify which factors are assumed to create a microclimate within the MCMA.
Lines 39f, 81: The discussion of how aerosol–cloud interactions impact extreme precipitation events is limited to one sentence in the introduction. If this is a main motivation for the study, it could be summarized in more detail.
Line 69f: Related to the previous comment, elaborate on what is meant by microclimate theory and provide a supporting reference. Molina and Molina (2004) do not discuss microclimate theory.
Line 74: Elaborate on why microclimatic effects are considered highly important for local precipitation events in the MCMA and provide references. It would be expected that synoptic-scale moisture supply and dynamical forcing are at least equally important.
Line 81: Extend the discussion on how INPs affect extreme precipitation, for example through their influence on deep convective clouds associated with extreme rainfall.
Table 1: Provide the sample volume in an additional column.
Line 180: In comparison, the inlet cut-size of 2.5 µm of the MiniVol excludes particle sizes collected on the two upper and partially the third of the four MOUDI stages used to obtain INP concentrations. As the four MOUDI stages contribute equally to the INP concentration (no size dependence observed), this indicates that over 60% of INPs are excluded from the MiniVol samples. This is the first reason why the correlation analysis between INP concentration and MiniVol-derived parameters can be misleading.
Section 2.2: The MOUDI flow rate and sample substrate (line 263) could be included in this section to consolidate information on sampling procedures. It would be helpful to report sampling flow rates, time of day of collection, and time resolution for all samplers.
Line 243: At what time of day were the samples collected, and how many samples were collected per day?
Line 294: Do you mean the area on which aerosol is deposited? Is aerosol deposited exclusively on the coverslip and not over the entire impaction stage? Adeposit is defined as the coverslip area also in Manson et al. (2016); however, their Fig. 7 shows that the coverslip covers only about one third of the impaction stage. For normalization of the sampled volume, the entire area over which aerosol is deposited should be used. Please include a photo of a loaded sample stage in the reply to this comment for clarification.
Section 3.1: Figures S4, 2, and 3 show only one sample per day, while Table 1 indicates that two samples were taken on both 17 and 18 May. Please include these samples to show diurnal variability in INP concentration and add a corresponding discussion.
Line 320: Selecting a restricted size range is not necessary. Using all eight MOUDI stages allows investigation of ~100% rather than 70% of INPs. There are two additional reasons to include the lower stages: (1) these stages are better represented by the MiniVol samples with a 2.5 µm cut-off (see previous comment), and (2) the main finding of no size dependence in INP concentration could be further supported. There is a potential contradiction between “no size dependence” and “70% of INPs are super-micron” that could be resolved. The analysis could clarify whether the lack of size dependence applies only to super-micron particles or across a broader size range.
Line 324: Describe how the homogeneous freezing line was determined and how it compares with published measurements, for example those in Shardt et al. (2022) for 100 µm droplets.
Line 327: Explain how the averages and error bars in Fig. 2 were calculated. In particular, clarify how freezing curves from different MOUDI stages were combined and how differences in droplet numbers between experiments were accounted for.
Line 332f: Please quantify and analyse the causes of the differences in T₅₀ and T₀ compared to literature. For example, the introduction notes that Knopf et al. (2010) reported ice nucleation at cirrus conditions, whereas the present study measures freezing of droplets in the MPC regime.
Line 342, Fig. 3: The error bars of South-20220520 overlap with those of North-20220520. Please clarify what is meant by statistically significant INP concentrations. What do the error bars represent, and how are they calculated? For South-20220520, why are the error bars smaller at −13 and −14 °C than at −12 and −15 °C? Consider using the method of Agresti and Coull (1998) to calculate 95% confidence intervals.
Line 345, Figure 3: Explain why Beijing is an appropriate city for comparison of INP concentrations. Consider adding data from Rodríguez-Gómez (2021) and Pereira (2021) to Fig. 3 (see comment on Fig. 4).
Line 353: Specify how the average accumulated INP concentration is calculated, which data are averaged, and what the error bars in Fig. 4 represent.
Line 357: The difference between the north and south samples at −15 °C is not clearly evident in Fig. 4, given the overlapping concentration ranges.
Figure 4: The figure does not provide substantial information beyond what is already shown in Fig. 3. It could be removed, with the reference data added to Fig. 3 instead. In addition, the yellow data symbol is difficult to see; a darker colour would improve visibility.
Line 371ff: It is correct that particle size and surface area affect the ice nucleation efficiency of particles with the same composition. When multiple particles of different compositions are present in a droplet, the combined abundance of ice-active sites at a given temperature determines ice formation. The amount and composition of particles on different MOUDI stages likely differs but is unknown. It is also unknown how the amount and composition of particles changes from day to day and between the sampling locations. Because only INP concentration per stage is known, interpretations involving coatings or physicochemical heterogeneities require supporting evidence or should be omitted.
Figure 5: Consider avoiding “dynamite stick” plots. Showing individual data points would be more informative. In general, bar plots on a logarithmic scale can be misleading because bar area has no physical meaning.
Line 399ff: It may be useful to note that NOx and measured radiation are higher at the northern site; thus, elevated O3 concentrations at the southern site could reflect higher VOC levels, which were not measured. Any impact on INP concentration remains speculative. Wang et al. (2012) measured naphthalene, an anthropogenic VOC associated with combustion rather than biogenic SOA, and investigated ice nucleation at cirrus conditions, outside the experimental range of the present study. Moreover, typical SOA particle sizes are below 1 µm, whereas super-micron particles were used for the INP analysis.
Line 414: Describe how these measurements were processed and averaged to match the INP sample collection periods.
Line 425: Provide an explanation of how different compounds may influence INP concentration and why these effects could differ between sites. Clarify why INP parameters correlate with chemical parameters at one site but not the other. The small number of data points (n = 5) makes the correlation analysis sensitive to outliers. Inspecting scatterplots could help identify non-linear relationships or outliers. In addition, explain how high correlations with T₅₀ can occur without corresponding correlations in INP concentrations at −20 or −25 °C, the temperature range where T₅₀ is located. Please assess how robust the correlations are at ±1 °C from the chosen temperatures. The possibility of spurious correlations due to limited sample size (second reason why the correlation analysis may be misleading) should be addressed by presenting scatterplots.
Figure 6: Indicate the confidence level associated with values marked by an asterisk.
Line 432ff: INP samples were collected during a 4-hour morning period, whereas filter samples were collected over 24 hours. As shown in Fig. S6, air mass origin changed during the 24-hour period, indicating that different aerosol populations were analysed for composition and INP concentration. For correlation analysis, sampling intervals must be temporally consistent. Correlating temporally misaligned samples constitutes a methodological issue. This is the third reason why the correlation analysis involving MiniVol data can be misleading. I recommend removing this part of the analysis and the associated discussion.
Line 454: In Fig. 6, the correlation with INP concentration at −20 °C is shown as not significant.
Line 466ff: This appears to contradict the discussion of O₃ concentrations in lines 399–407. If VOC concentrations are higher in the north, higher O₃ concentrations would also be expected there.
Lines 470–473: This discussion repeats points made in lines 452–456.
Line 475: Provide the altitude of the trajectories. Overlaying Figs. S7 and S6 could clarify which trajectories are influenced by biomass burning and why this effect is more pronounced at the southern site. Potassium, a tracer for biomass burning, is higher at C5 than at CU on most days (Fig. 7).
Line 481ff: The interpretation of the three clusters requires further explanation. For example, why are Pb, Cl⁻, Mn, and Ca assigned to the soil cluster in the north but to the anthropogenic cluster in the south? Briefly explain the clustering method and how to interpret the dendrogram produced using Ward’s method with Pearson correlation coefficients. Clarify how clustering leads to source identification and whether these sources relate to observed INP concentrations.
Line 510: Explain how the finding that 57% of bacteria are Gram-positive affects the analysis, given that ice-nucleation-active bacteria are predominantly Gram-negative.
Figure 8: INP concentrations were measured between 16–20 May. Why is a longer time series of bacteria and fungi shown? What additional insight is provided by comparison with PM₂.₅?
Line 530: Pseudomonas, Pantoea, Alternaria, and Fusarium from other locations have been reported to nucleate ice above −10 °C. Are local strains not producing ice-nucleation proteins?
Line 533: Clarify why cross-correlation analysis was performed in the context of this study.
Line 550: Explain why correlations with these parameters imply compositional effects rather than simply reflecting aerosol amount (e.g., PM2.5).
Lines 552–556: Clarify the connection between these particle types and INP concentration.
Line 559: Specify which atmospheric processes are referred to and how particle formation is linked to INP concentration.
Lines 560ff, 543: Explain why INP concentrations are compared with those from Beijing. Similar concentrations might suggest that, contrary to the conclusions, urban INP concentrations are not strongly linked to the listed factors.
Line 566: Specify what concrete information was obtained.
Table S6: Consider adding a column indicating Gram-positive or Gram-negative classification and another listing temperature ranges over which species are reported to act as INPs, based on literature data.
Figure S1: Fig. S6 suggests predominantly westerly winds at midday, whereas these wind roses show mainly easterly winds. Restricting the wind analysis to the MOUDI sampling periods could be informative.
Technical corrections:
Line 80: something is missing in this long sentence. Do you mean “… information on the interplay …”?
Line 118: Delete the “B” before proteobacteria.
Figure 6: Br is missing from panel (a) but appears in Fig. S8. CO is missing from panel (b) but is shown in Fig. S2.
Figure 7: Replot the figure including zero on each ordinate rather than overlapping y-axes.
Figure 8: Red stars without connecting lines are filled symbols in the plot but shown as open symbols in the legend.
Figure S3: “Adapted” implies modifications. “Reprint of Fig. 3 from Córdoba et al. (2021)” would be accurate.
Figure S5: The y-axis labels of individual subfigures seem irregular. Replot including zero on each ordinate.
Figures S8 and S9: Blue lines below the green cluster are difficult to see. Consider using different colours for clusters in Fig. S9, as they do not correspond to the same sources as in Fig. S8.
References:
Agresti, A. and Coull, B. A.: Approximate is better than “exact” for interval estimation of binomial proportions, Am. Stat., 52, 119, https://doi.org/10.2307/2685469, 1998.
MetOffice factsheet 14, https://www.metoffice.gov.uk/binaries/content/assets/metofficegovuk/pdf/research/library-and-archive/library/publications/factsheets/factsheet_14-microclimates_2023.pdf
Shardt, N. et al.: Homogeneous freezing of water droplets for different volumes and cooling rates, Phys. Chem. Chem. Phys., 24, 28213-28221, https://doi.org/10.1039/D2CP03896J, 2022.