Review of “Dust Transport and Local Anthropogenic Emissions Differently Shape Atmospheric Ice-Nucleating Particles: Insights from an Industrial Urban Atmosphere” by Yang et al.

This study assessed the ice nucleating particle (INP) concentrations and efficiencies in an urban site in China. The authors were able to identify a clear mineral dust event as well as other high pollution events during their sampling period. Additionally, most of the sampling days were assigned as a “non-dust period” considering aerosol composition, particle size distributions, and air masses history. Although INPs are poorly constrained and studied in urban sites, the manuscript requires deep corrections. Also, I think this manuscript better fits into the “Measurement report” category.

Major comments:

1. The authors made a distinction between a “dust event” and a “non-dust period”. Although the INP concentration and ns values are quite different between both periods, I am not fully convinced that the “non-dust period” is really a period without the influence of mineral dust particles. As shown in the back-trajectories, during the “non-dust period” the airmasses crossed northern China and southern Mongolia deserts, including the Gobi Desert. Also, the elemental analysis is not a good way to confirm the absence of mineral dust particles during the “non-dust period” as aluminum (Al) and silicon (Si) were not included. This a key point to be addressed as most of the drawn conclusions took this apparent distinction into account.
2. The size range or cut-off size of the INP samples is not provided. This is very important as it is well-known that particle size is a key variable when assessing their ice-nucleating abilities. I only found the following information: “using a two-channel sampler without a cyclone”. Does it mean that the samples correspond to Total suspended particles (TSP)? Did I miss something?
3. The PMF analysis was performed on PM2.5 particles; however, as mentioned above in point #2, based on the provided information, it seems that the INP samples correspond to TSP. If this is the case, the performed correlations are meaningless.
4. I was surprised that meteorology was not used at all. The authors argue in several parts that the INPs were from local sources during the “non-dust period”. It would have been nice to check the wind speed and wind direction to corroborate this.
5. Figures S4 and S5 are not mentioned/discussed in the main text. These figures contain important information that deserves to be deeply discussed.
6. “All samples in Taiyuan activated before −15 ℃, with the most active samples initiating freezing near –5℃” and “It is also noteworthy that at relatively warm temperatures (approximately T > −12 °C), ns values of the ambient desert dust samples substantially exceed the parameterizations for pure K-feldspar”. If this is true, this corresponds to extremely efficient INPs; however, a deep discussion on the high efficiency of these particles is not provided. Is this because the samples were TSP? Is this coming from an instrumental bias? Were these samples enriched in biological particles?
7. Why the PMF analysis was correlated with the INP concentration at -20 °C only. I suggest testing this comparison at -10 °C and -15 °C as this refers to highly efficient INPs.

Minor comments:

Lines 19-20: “compared with periods without natural dust influence”. I don’t think the authors can completely rule out the presence of mineral dust particles in the “non-dust period”.

Lines 26-27: “Observed NINP variability is likely governed by the interplay of episodic coarse-mode inputs and atmospheric processing rather than a single dominant source.” I am not sure the authors can really say this as a direct correlation between INP concentration and coarse particle concentration was not provided.

Line 178: What was the main motivation to run the back-trajectories at 859 m a.s.l.?

Lines 249-250: “while it is comparable to observations from Sisal, Mexico (Ladino et al., 2016), and New Delhi, India (Wagh et al., 2021) between −15℃ to −20℃”. I disagree with this statement. It would have been better to add to Figure 2 in-situ data for ambient samples under the influence of Asian or Saharan dust.

Lines 252-253: “This implies that the INPs observed in Taiyuan may also be influenced by anthropogenic dust particles.” No information is provided to support this.

Line 256: “they are broadly comparable with those reported in other relevant studies.” I disagree with this statement.

Lines 257-258: I don’t think that it is a good idea to add the data from Petters and Wright (2015). I suggest removing it from Figure 2.

Lines 261-262: “suggesting additional contributions from ice-active components or enhanced influence of transported desert dust during certain periods.” This is contradictory as this data corresponds to the “non-dust period”.

Lines 283-284: “particles larger than 0.5 μm in Taiyuan are likely dominated by local surface emissions from the surrounding Loess Plateau and fugitive dust from intensive industrial activities”. No evidence is provided.

Lines 298-300: “This comparison suggests that, under the East Asian desert dust transport regime, typical atmospheric aging does not significantly modify the surface ice-nucleating activity of mineral dust, and that mineralogical composition and particle-size characteristics are likely more important determinants.” I found this highly speculative.

Lines 359-360: “provide a framework for evaluating the contributions of local anthropogenic emissions versus naturally transported particles.” I don’t think this was clearly demonstrated.

Lines 366-367: “suggesting that typical aging processes do not substantially suppress the INP efficiency of East Asian mineral dust.” No evidence was provided for this.

Line 375: “The findings show that long-range desert dust transport is the decisive driver of INP enhancements in Taiyuan” This is a very strong conclusion from a single dust event.

Lines 378-379: “These observations help clarify the relative contributions of natural and anthropogenic sources to INPs”. I am not fully convinced about this.

Section 3.3. I suggest adding a Table similar to Table S1 but for the dust period

Figure 1. Panel a is not easy to follow. Perhaps using more contrasting colors could enhance its readability

Figure 3. add ns values for literature studies on urban particles and dust

Figure 4. This data adds little to the discussion.

Technical comments:

Line 15: Replace “campaign in Taiyuan” by “campaign in Taiyuan (China)”

Line69: Replace “dust in cities” by “dust in urban environments”

Line 71: “urban and peri-urban regions (Chen et al., 2024)”. I suggest adding other references.

Line 35: “thermal activation behavior” What does it mean?

General Comments:

This manuscript reports on the results of a month-long field measurements of immersion-mode ice-nucleating particles (INPs) in Taiyuan, China, in winter (from 3 December 2023 to 14 January 2024). Since INP data obtained in cities of East Asia other than Beijing and Tokyo are limited, I think that the datasets obtained in Taiyuan are valuable for publication. However, the key conclusions of this work are essentially the same as those of previous studies in Beijing and Tokyo. For example, drastic increases in INPs caused by Asian dust events have been reported in Beijing (Zhang et al., 2022) and Tokyo (Isono et al., 1959; Tobo et al., 2020), and a weak correlation between INPs and anthropogenic aerosols (or PM_2.5) have been reported in Beijing (Chen et al., 2018; Bi et al., 2019; Zhang et al., 2022), respectively. For this reason, I don’t think that this work meets the criterion of ACP’s “Research articles”, which should report substantial new results and conclusions from scientific investigations of atmospheric properties, and processes. Instead, I would recommend this manuscript for publication as the category of “Measurement reports” if the authors could improve the quality of the data analysis and figures and provide further discussion.

Specific Comments:

1)    I doubt if the ice-nucleation active site density (n_s) values are calculated appropriately, since the size range used for the calculation of the total surface area (A) is not provided in Line 158. If A was calculated based on SMPS data only (3 to 453 nm) as written in Lines 171-172, both the A and n_s values should be recalculated by combining SMPS data and Optical Particle Counter data (0.5 to 20 μm).

2)    Dust INP parameterization of DeMott et al. (2015) was designed to calculate INP number concentrations related to the number concentrations of dust particles larger than 0.5 μm and not those of total aerosol particles larger than 0.5 μm. If the INP number concentrations for D15 (-20°C) shown in Figure 1a were calculated using the number concentrations of total aerosol particles larger than 0.5 μm, it would not be an appropriate use.

3)    Figure 2: For reference data, the period of the data sampling should be indicated in addition to the location. In this regard, although the period of the INP data in Tokyo (Tobo et al., 2020) shown in Figure 2 is unclear (since the period is not indicated in this figure), it would be appropriate to show the data collected in winter for comparison. In addition, I strongly suggest including the INP data in Beijing reported by Chen et al. (2018), because they reported the INP data in Beijing during winter, which were measured using the same technique as this study.

4)    It seems that the INP number concentrations in Taiyuan are somewhat higher than those in Beijing (Chen et al., 2018) and Tokyo (Tobo et al., 2020) during winter, even though these data have been obtained using essentially the same technique (i.e., cold-stage-based technique). Please discuss possible reasons for higher INP number concentrations in Taiyuan and possible differences (e.g., location and possible major sources of INPs) between Taiyuan and these urban sites in East Asia. In this regard, I would like to suggest comparing available ambient aerosol data (e.g., number concentrations of aerosol particles larger than 0.5 μm, PM_2.5, PM₁₀, chemical composition) between Taiyuan and other sites.

Technical Comments:

5)    Lines 39-41: Given that some recent studies render deposition nucleation unlikely for the formation of ice clouds in the atmosphere and “pore condensation and freezing” is a more likely mechanisms for atmospheric ice nucleation below water saturation (e.g., Marcolli, 2014; David et al., 2019), it might be appropriate to describe “pore condensation and freezing” in addition to the four mechanisms.

6)    Lines 51-52: Please indicate the references regarding this explanation. In addition, the authors would need to explain that some studies have indicated the negligible contribution of soot particles to INPs in the immersion mode (e.g., Kanji et al., 2020).

7)    Line 83: As far as I check the data presented in this manuscript, it seems that the INP data used here are limited to the temperature regime from about -25°C to -5°C.

8)    Lines 160-169: If the confidential intervals for the INP number concentrations were calculated the error bars should be indicated in the INP data in the figures.

9)    Line 227: What do you mean by “secondary pollution”?

10)    All Figures: The size of the figure legends are too small and it is hard to read. Please increase the font size.

11)    All Figures: Since similar colors are used in the figures (especially, Figures 1a, 1b, 1d, and 2), it is hard to see the difference in color. Please use colors and symbols that are easier to distinguish.

12)    Figure 1a: What do the three white horizontal lines indicate?

13)    Figure 1a legend: The symbol “<” should be “>”.

14)    Figure 1b: What is the lower limit for size range of N_<1μm?

15)    Figure 1d: What does a small figure in Figure 1d indicate? (it is too small, anyway.)

16)    Figure 1d: I can’t see the ion data before ~7 December 2023. Is it due to their extremely low values?

17)    Figure 2: The data for “Urban site in New Delhi (Wagh et al., 2021)” would not be appropriate for this figure, because they reported INP data in the deposition mode and not in the immersion mode.

References:

Bi et al. (2019), https://doi.org/10.1029/2019JD030609

Chen et al. (2018), https://doi.org/10.5194/acp-18-3523-2018

David et al. (2019), https://doi.org/10.1073/pnas.1813647116

DeMott et al. (2015), https://doi.org/10.5194/acp-15-393-2015

Isono et al. (1959), https://doi.org/10.2151/jmsj1923.37.6_211

Kanji et al., (2020), https://doi.org/10.1029/2019GL086764

Marcolli (2014), https://doi.org/10.5194/acp-14-2071-2014

Tobo et al. (2020), https://doi.org/10.1029/2020JD033658

Wagh et al. (2021), https://doi.org/10.1016/j.atmosres.2021.105693

Zhang et al. (2022), https://doi.org/10.5194/acp-22-7539-2022

General comments:

Atmospheric ice-nucleating particles (INPs) play a critical role in cloud formation, cloud radiative properties and precipitation through heterogeneous ice nucleation, yet the importance of INPs from anthropogenic sources remains poorly understood. This manuscript investigated INP concentrations (N_INP) and ice nucleation active site density (ns) of immersion mode INPs in Taiyuan, China based on one month-long winter field observations. The results indicated that the temporal variability of INP concentrations is dominated by episodic natural desert dust transport, and the direct impact of anthropogenic emissions on INP loading remains limited. Namely, this study implied that in heavily polluted environments, natural dust rather human activity governs cloud freezing processes. These findings would offer observational constraints for improving INP parameterizations in chemical transport and climate models.

In general, I think the research goal of this manuscript is clear, and the structure and results are reasonable. Therefore, I recommend this manuscript is accepted and published in the journal of EGUsphere after some revisions. The authors are advised to consider the following comments.

Specific comments:

(1) Page 1, Abstract, Lines 18-19: ‘CI: 6.64-8.41, CI: 1.58-1.99’.

   Comment: When an English abbreviation first appears in the manuscript, please provide its full form.

(2) Page 1, Abstract, Lines 22-23; Page 6, 2.2.5 Positive matrix factorization (PMF), Lines 179-186: ‘Positive matrix factorization (PMF) identified five PM₅ sources: coal combustion and traffic emissions, industry, (anthropogenic) dust, secondary aerosols and fireworks.’

Comment: How did the PMF method distinguish between natural dust and anthropogenic dust? Please provide a detailed description in the context. This is of great significance for the analysis of how the two different types of dust affect the INPs in the manuscript.

(3) Page 1, Abstract, Lines 26-27 and in the context: ‘Observed N_INP variability is likely governed by the interplay of episodic coarse-mode inputs and atmospheric processing rather than a single dominant source’.

Comment: In the manuscript, the authors only provided one month-long winter field observations in Taiyuan, which is insufficient to confirm this conclusion. That is, this conclusion is difficult to convince the readers.

(4) Page 3, Lines 69-71: ‘Furthermore, the influence of dust in cities is not limited to long-range natural transport; anthropogenic dust-such as agricultural operations, construction, and other urban processes-can also contribute substantially to atmospheric INPs in urban and peri-urban regions (Chen et al., 2024)’.

Comment: The main conclusion of this manuscript seems to be in contradiction to the results obtained by Chen et al. (2024). In order to facilitate readers' understanding, please provide a reasonable explanation in the context.

(5) Page 4, Lines 100-102: ‘In addition, a two-channel sampler was used to collect particles on filters for INP measurement. INP filter samples ……using a two-channel sampler without a cyclone, from 4 December 2023 to 5 January 2024’.

Comment: What is the meaning of ‘using a two-channel sampler without a cyclone’? Please provide the measurement particle size ranges of INP in the context, which is vital to the analysis of the results in this manuscript.

(6) Page 9, Lines 251-253: ‘Chen et al. (2024) found that anthropogenic dust particles, such as road dust influenced by traffic emissions, are important INP sources in the urban atmosphere. This implies that the INPs observed in Taiyuan may also influenced by anthropogenic dust particles’.

Comment: The conclusion of ‘This implies that the INPs observed in Taiyuan may also influenced by anthropogenic dust particles’ seems to be in contradiction to the main conclusion of the manuscript ‘In summary, long-range mineral dust transport is the decisive driver of INP enhancements, while traditional anthropogenic fine aerosols contribute minimally’ (Abstract, Lines 25-26). Please provide a reasonable explanation in the context.

(7) Page 11, Lines 298-300: ‘This comparison suggests that, under East Asian desert dust transport regime, typical atmospheric aging does not significantly modify the surface ice-nucleating activity of mineral dust, and that mineralogical composition and particle-size characteristics are likely more important determinants’.

Comment: The author didn’t provide direct and sufficient evidences in the manuscript to prove this conclusion. Please revise this conclusion or provide sufficient evidence in the manuscript. For instance, ‘typical atmospheric aging does not significantly modify the surface ice-nucleating activity’, the authors didn’t provide the ‘typical atmospheric aging processes’ or ‘aging mineral dust aerosol’ in the context.