the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 16 Jan 2025
On the presence of high nitrite (NO2-) in coarse particles at Mt. Qomolangma
Abstract. Atmospheric reactive nitrogen cycling is crucial for maintaining the atmospheric oxidation capacity of background atmosphere on the Tibetan Plateau , with nitrous acid (HONO) and particulate nitrite (NO2-) as important intermediates. During an eleven-day field campaign at the Base Camp of Mt. Qomolangma in spring of 2022, we observed significant enrichment of NO2- in total suspended particulate (TSP) with a mean concentration of 375 ± 386 ng m-3, while NO2- was absent in fine particles (PM2.5). The comparison revealed that NO2- predominately exists in coarse particles. Local surface soil at the sampling site also exhibited high levels of NO2-, with δ15N value similar to NO2- in TSP. This similarity suggests that wind-blown soil is probably the primary source of NO2- in TSP, accounting for the background levels. While concentration changes of water-soluble inorganic ions in TSP and PM2.5 in response to shifts in air mass back-trajectories imply that atmospheric pollutants transported from South Asia may further elevate the NO2-, the specific mechanisms of long-range transport resulting in NO2- accumulation in TSP rather than PM2.5 remain unknown and need to be investigated. Our results reveal an overlooked source of atmospheric NO2-, i.e., soil NO2-, and highlight in remote regions such as Tibet where other sources are limited, wind-blown soil may serve as an important source of atmospheric NO2-. Once lofted into the atmosphere, NO2- may readily participate in atmospheric reactive nitrogen cycling through gas-particle partitioning or photolysis, leading to the production of HONO, OH and NO and thereby influencing oxidation chemistry.
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RC1: 'Comment on egusphere-2024-4165', Anonymous Referee #1, 22 Feb 2025
Understanding the chemistry of reactive nitrogen in pristine environments, such as the Tibetan Plateau, is crucial for advancing our knowledge of atmospheric chemistry. This study undertook a challenging field campaign, collecting PM₂.₅, total particle, and soil samples to investigate the unusual enrichment of nitrite in coarse particles and its potential sources. While the effort in sample collection and extensive analysis is commendable, the presentation of the data in this paper lacks clarity, and the interpretation of the results is, in my opinion, not entirely sound.
After reviewing this manuscript, I remain unconvinced by the authors’ arguments, as significant gaps in explanation persist. Given the high publication standards of Atmospheric Chemistry and Physics (ACP), I believe the current manuscript does not meet the criteria for publication without substantial revisions.
Here are my major concerns:
1. Uncertainties in ion concentrations of PM₂.₅ and total particles.
The comparison of ion concentrations between TSP and PM₂.₅ is particularly interesting. It clearly shows that nitrite ions are present only in TSP, while PM₂.₅ contains none. However, what stands out is that despite PM₂.₅ being a subset of TSP, some PM₂.₅ samples occasionally show higher ion concentrations (in µg/m³) than their corresponding TSP samples. For instance, the April 30 PM₂.₅ sample appears to contain more nitrate than the TSP sample.
I suspect this discrepancy may stem from analytical uncertainties in ion concentration measurements or uncertainties in the blank corrections, but this issue has not been addressed in the manuscript. Understanding these uncertainties is crucial, especially since the ion composition of coarse aerosols is determined by subtracting two similar measurements.
I also suggest that the authors directly present the ion concentrations of coarse aerosols. While this may sometimes result in negative values, it would provide a clearer picture of the uncertainties associated with ion concentration measurements.
2. Missing evidence: mass balance in coarse particles.
I would like to see a little bit more discussion in section 4.3 when the authors attempted to attribute the observed nitrite to lofted dust, maybe as simple as mass balance calculations. For example, if the observed nitrite is indeed coming from soil, to get ~1 ug/m3 of nitrite from soil, how much soil do you need in the air giving average soil nitrite concentration of < 100 ng/g? About 10 g/m3. Then, does the observed TSP concentration support your hypothesis?
Similarly, nitrate/nitrite ratio in soil also do not fully support authors’ hypothesis, the authors argue that it is likely nitrate/nitrite distributed in particles of different sizes but there is no evidence supporting this, nor is there any previous work mentioned such effect. Therefore, I am not fully convinced by the existing evidence that soil is the main source of particle nitrite.
3. Isotopic results do not seem to support authors’ argument.
The isotopic results also do not support the authors’ argument. The O17 signal in soil samples range from 1.4‰ to 7.3‰ but in TSP the O17 is 0-1‰, a clear discrepancy. δ18O also are significant different – 2‰ to 18‰ in the soil but lots of negative values in the TSP. I do not think this can be simply explained by isotope exchange with water because such isotope exchange always occurs: we need more evidence to believe that exchange never happens when the particles are on the surface, then once it was lifted into the air, within hours (typical lifetime of coarse particles) the exchange suddenly occurred.
4. More discussion needed for air mass from different regions.
The back-trajectory analysis clearly shows that the field campaign sampled air from two distinct regions, with corresponding differences in ion concentrations and d15N values. However, the discussion of these differences is too simplistic. It would be beneficial for the authors to separately analyze how the aerosols from each period differ and to explore in greater depth how nitrite concentrations and isotopic compositions varied between them, as the differences are quite significant.
Additionally, while the authors suggest that long-range transport is unimportant for the nitrite budget, their argument in the final section contradicts this claim. To strengthen the manuscript, the discussion should remain consistent and logically cohesive.
5. Implications to AOC is weak.
Since the source of nitrite remains unclear, the discussion on how lofted soil influences atmospheric chemistry is weak. The authors provide no data on atmospheric dust concentrations and do not address the transport potential of soil particles, which is likely limited due to their larger size. As a result, the final section lacks convincing supporting evidence.
Citation: https://doi.org/10.5194/egusphere-2024-4165-RC1 - AC1: 'Reply on RC1', Zhongyi Zhang, 05 Jun 2025
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RC2: 'Comment on egusphere-2024-4165', Anonymous Referee #2, 28 Apr 2025
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2025/egusphere-2024-4165/egusphere-2024-4165-RC2-supplement.pdf
- AC2: 'Reply on RC2', Zhongyi Zhang, 05 Jun 2025
-
RC3: 'Comment on egusphere-2024-4165', Anonymous Referee #3, 05 May 2025
This manuscript, entitled “On the presence of high nitrite (NO2-) in coarse particles at Mt. Qomolangma” investigated the soil-derived particulate composition on TP, specifically focused on nitrite, and concluded that this is a major source of HONO on TP. Although I appreciate their work, the manuscript has strong intrinsic weaknesses in the method used in measurement as well as the data interpretations, leaving many large holes in this work. Therefore, this work cannot be accepted in the current form for ACP publication.
Here are my major remarks.
- First, let’s focus on the methods section. In brief, the sampling method has never been validated in both the lab and field for the TSP nitrite isotopic analysis. The soil extraction method with MQ water is problematic for nitrate and other ions, although it’s been proven to be more effective for nitrite. Below are the specific comments for the methods.
- Line 117, the mountain and valley wind can be from all directions. It is hard to say "upwind" or "downwind" in these areas.
- Line 126, while the authors claim the Whatman quartz filter collects TSP, no test has been done for HONO collection on the quartz filter. There was no method validation.
- Lack of explanation. Line 130, how is “filter face velocity of approximately 0.288 m s-1.” derived? Additionally, details on “surface soil” collection are needed.
- Lines 182-183, based on the statement here, it is confusing why the authors used the suggested Δ17Ο = 0 for N7373 and N23 from Albertin et al., but only use their own measured Δ17Ο value of N10219.
- Lines 189-191, although the ion-exchange method has been verified and used for nitrate ion preconcentration for isotopic analysis, no test has been done for nitrite. Before using the method for field samples, is there supposed to be a lab test for different concentrations and different solution environments?
- Line 199, it is confusing why 6 days was chosen as the HYSPLIY modeling duration. Why and what fire spots need to be identified?
- Lines 164-169, the work used MQ water for soil extraction. While the MQ water may be more effective for nitrite extraction, it has not been proved to be effective for nitrate (and other ions) extraction.
- The authors suggested that the soil-originated TSP nitrite is an important source of atmospheric HONO, but without measuring atmospheric HONO concentration and its isotopic composition. Without seeing the connections between the TSP nitrite and atmospheric HONO in concentration and isotopes, the conclusion hardly makes any sense.
Next, the data interpretation for the major statement and conclusion is problematic.
- Lines 319-328, it is questionable to use the δ15N isotopic fractionation factor of snow nitrate photolysis to explain the aerosol nitrate photolysis. In order to determine the role of a potential source in the observed isotopic signatures, one would need to use a source apportionment model to quantify the contribution of each source. Simply comparing the δ15N values between the nitrite and nitrate doesn’t yield any meaningful interpretation and can lead to the invalid statement.
- There is not sufficient quantitative analysis on why HONO uptake and NO2 uptake, and conversion to nitrite pathways are not important. The conclusion that these two pathways are not important was merely based on the assumption or experience that HONO and NO2 concentrations are very low, while the work did not measure these concentrations. As such, this is a very weak conclusion lacking direct evidence. The work did not show any isotopic evidence, even though there is literature available. What is the lifetime of nitrite on coarse particles, and what is the lifetime on fine particles? Why is nitrite more abundant on coarse particles than fine particles? What is the state of the knowledge? There is no explanation on this at all.
Also, there are several major mistakes in the discussion (Lines 339-347). Specifically, photoenhanced conversion from NO2 to NO2- is not “photocatalysis”; NO2 uptake coefficient varies in a significant range, and 1*10-5 or higher is more typically. For example, see Scharko et al. 2017 ES&T (10.1021/acs.est.7b01363). Also, a typo, “initialed” indicates the recklessness of the manuscript.
- For the investigation of the influence of biomass burning, the authors only did a single back trajectory for each day, which is not sufficient to determine the relative contributions of different air masses transported from different regions. Furthermore, there is no systematic tracer analysis for biomass burning influences. Therefore, the statement in Lines 371-374 is not valid.
Additionally, based on lines 375-381, the authors speculate biomass burning smoke won’t contribute to the coarse mode particulate nitrite, so why would the authors still track the airmass? Additionally, it is inaccurate to state that “particle nitrite has not yet been detected in biomass burning plumes,” according to the cited literature. These works just didn’t measure the nitrite concentrations for some reason, one of which is the detection limit, and nitrite is orders of magnitude smaller than nitrate.
- The interpretation of why nitrite in TSP has a higher δ18Ο is invalid. The author states that aerosol water abundance is at least 3 orders of magnitude larger than NO2- based only on ISOROPIA modeling results without measurement. As we know, the modeled results are highly uncertain and are greatly influenced by the arbitrary input parameters. More important question— What is the hygroscopic property of the soil-derived TSP? What is the relationship between “aerosol liquid water” and TSP? Is the water really in fine particles or coarse particles? Moreover, if the O exchange between water and nitrite is important in aerosol (again, fine particle or coarse particle?), is it supposed to be important in soils? Finally, what is the explanation for the Δ17Ο of soil nitrite compared to the TSP? Unfortunately, there is no clear discussion on this.
- Additionally, what is the Ionic balance for the water-soluble ions in TP and PM2.5?
Additionally, many vague statements prevent me from understanding the key points significantly.
- Line 209, what do you mean by "general decline"? Why use 5/1 as the cut-off date? Is there any statistical analysis?
- Line 212-213, “negligible” is vague.
- Line 214, what is the point of discussing the K+ in PM2.5 that decreases? Why K+ in TSP didn’t show the same trend? Instead, the highest K+ occurs after 5/1?
- Line 215, "comparable" here is not supported by any numerical evidence.
- Lines 220-222, which figure or summarized data shows “average daytime concentrations of the inorganic species were generally higher than those at night”?
- Lines 217-218, what does the Ca2+ and Mg2+ data tell you in addition to “smaller degree”? No point can be achieved.
- In the paragraph starting with Line 228, the first sentence “The variations of WSIs in TSP generally followed a similar 228 pattern to that in PM2.5 (Figure 1)” is an invalid statement as some species have very different trends between TSP and PM2.5, such as K+.
- Line 239, “similar areas of filters were extracted,” doesn’t necessarily ensure the accuracy of the comparison because the sampling setups are different.
- Vague statement in Lines 282-283, “High soil NO2- and NO3- concentrations were observed on the west and east…”. “high” here is vague.
Citation: https://doi.org/10.5194/egusphere-2024-4165-RC3 - AC3: 'Reply on RC3', Zhongyi Zhang, 05 Jun 2025
Interactive discussion
Status: closed
-
RC1: 'Comment on egusphere-2024-4165', Anonymous Referee #1, 22 Feb 2025
Understanding the chemistry of reactive nitrogen in pristine environments, such as the Tibetan Plateau, is crucial for advancing our knowledge of atmospheric chemistry. This study undertook a challenging field campaign, collecting PM₂.₅, total particle, and soil samples to investigate the unusual enrichment of nitrite in coarse particles and its potential sources. While the effort in sample collection and extensive analysis is commendable, the presentation of the data in this paper lacks clarity, and the interpretation of the results is, in my opinion, not entirely sound.
After reviewing this manuscript, I remain unconvinced by the authors’ arguments, as significant gaps in explanation persist. Given the high publication standards of Atmospheric Chemistry and Physics (ACP), I believe the current manuscript does not meet the criteria for publication without substantial revisions.
Here are my major concerns:
1. Uncertainties in ion concentrations of PM₂.₅ and total particles.
The comparison of ion concentrations between TSP and PM₂.₅ is particularly interesting. It clearly shows that nitrite ions are present only in TSP, while PM₂.₅ contains none. However, what stands out is that despite PM₂.₅ being a subset of TSP, some PM₂.₅ samples occasionally show higher ion concentrations (in µg/m³) than their corresponding TSP samples. For instance, the April 30 PM₂.₅ sample appears to contain more nitrate than the TSP sample.
I suspect this discrepancy may stem from analytical uncertainties in ion concentration measurements or uncertainties in the blank corrections, but this issue has not been addressed in the manuscript. Understanding these uncertainties is crucial, especially since the ion composition of coarse aerosols is determined by subtracting two similar measurements.
I also suggest that the authors directly present the ion concentrations of coarse aerosols. While this may sometimes result in negative values, it would provide a clearer picture of the uncertainties associated with ion concentration measurements.
2. Missing evidence: mass balance in coarse particles.
I would like to see a little bit more discussion in section 4.3 when the authors attempted to attribute the observed nitrite to lofted dust, maybe as simple as mass balance calculations. For example, if the observed nitrite is indeed coming from soil, to get ~1 ug/m3 of nitrite from soil, how much soil do you need in the air giving average soil nitrite concentration of < 100 ng/g? About 10 g/m3. Then, does the observed TSP concentration support your hypothesis?
Similarly, nitrate/nitrite ratio in soil also do not fully support authors’ hypothesis, the authors argue that it is likely nitrate/nitrite distributed in particles of different sizes but there is no evidence supporting this, nor is there any previous work mentioned such effect. Therefore, I am not fully convinced by the existing evidence that soil is the main source of particle nitrite.
3. Isotopic results do not seem to support authors’ argument.
The isotopic results also do not support the authors’ argument. The O17 signal in soil samples range from 1.4‰ to 7.3‰ but in TSP the O17 is 0-1‰, a clear discrepancy. δ18O also are significant different – 2‰ to 18‰ in the soil but lots of negative values in the TSP. I do not think this can be simply explained by isotope exchange with water because such isotope exchange always occurs: we need more evidence to believe that exchange never happens when the particles are on the surface, then once it was lifted into the air, within hours (typical lifetime of coarse particles) the exchange suddenly occurred.
4. More discussion needed for air mass from different regions.
The back-trajectory analysis clearly shows that the field campaign sampled air from two distinct regions, with corresponding differences in ion concentrations and d15N values. However, the discussion of these differences is too simplistic. It would be beneficial for the authors to separately analyze how the aerosols from each period differ and to explore in greater depth how nitrite concentrations and isotopic compositions varied between them, as the differences are quite significant.
Additionally, while the authors suggest that long-range transport is unimportant for the nitrite budget, their argument in the final section contradicts this claim. To strengthen the manuscript, the discussion should remain consistent and logically cohesive.
5. Implications to AOC is weak.
Since the source of nitrite remains unclear, the discussion on how lofted soil influences atmospheric chemistry is weak. The authors provide no data on atmospheric dust concentrations and do not address the transport potential of soil particles, which is likely limited due to their larger size. As a result, the final section lacks convincing supporting evidence.
Citation: https://doi.org/10.5194/egusphere-2024-4165-RC1 - AC1: 'Reply on RC1', Zhongyi Zhang, 05 Jun 2025
-
RC2: 'Comment on egusphere-2024-4165', Anonymous Referee #2, 28 Apr 2025
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2025/egusphere-2024-4165/egusphere-2024-4165-RC2-supplement.pdf
- AC2: 'Reply on RC2', Zhongyi Zhang, 05 Jun 2025
-
RC3: 'Comment on egusphere-2024-4165', Anonymous Referee #3, 05 May 2025
This manuscript, entitled “On the presence of high nitrite (NO2-) in coarse particles at Mt. Qomolangma” investigated the soil-derived particulate composition on TP, specifically focused on nitrite, and concluded that this is a major source of HONO on TP. Although I appreciate their work, the manuscript has strong intrinsic weaknesses in the method used in measurement as well as the data interpretations, leaving many large holes in this work. Therefore, this work cannot be accepted in the current form for ACP publication.
Here are my major remarks.
- First, let’s focus on the methods section. In brief, the sampling method has never been validated in both the lab and field for the TSP nitrite isotopic analysis. The soil extraction method with MQ water is problematic for nitrate and other ions, although it’s been proven to be more effective for nitrite. Below are the specific comments for the methods.
- Line 117, the mountain and valley wind can be from all directions. It is hard to say "upwind" or "downwind" in these areas.
- Line 126, while the authors claim the Whatman quartz filter collects TSP, no test has been done for HONO collection on the quartz filter. There was no method validation.
- Lack of explanation. Line 130, how is “filter face velocity of approximately 0.288 m s-1.” derived? Additionally, details on “surface soil” collection are needed.
- Lines 182-183, based on the statement here, it is confusing why the authors used the suggested Δ17Ο = 0 for N7373 and N23 from Albertin et al., but only use their own measured Δ17Ο value of N10219.
- Lines 189-191, although the ion-exchange method has been verified and used for nitrate ion preconcentration for isotopic analysis, no test has been done for nitrite. Before using the method for field samples, is there supposed to be a lab test for different concentrations and different solution environments?
- Line 199, it is confusing why 6 days was chosen as the HYSPLIY modeling duration. Why and what fire spots need to be identified?
- Lines 164-169, the work used MQ water for soil extraction. While the MQ water may be more effective for nitrite extraction, it has not been proved to be effective for nitrate (and other ions) extraction.
- The authors suggested that the soil-originated TSP nitrite is an important source of atmospheric HONO, but without measuring atmospheric HONO concentration and its isotopic composition. Without seeing the connections between the TSP nitrite and atmospheric HONO in concentration and isotopes, the conclusion hardly makes any sense.
Next, the data interpretation for the major statement and conclusion is problematic.
- Lines 319-328, it is questionable to use the δ15N isotopic fractionation factor of snow nitrate photolysis to explain the aerosol nitrate photolysis. In order to determine the role of a potential source in the observed isotopic signatures, one would need to use a source apportionment model to quantify the contribution of each source. Simply comparing the δ15N values between the nitrite and nitrate doesn’t yield any meaningful interpretation and can lead to the invalid statement.
- There is not sufficient quantitative analysis on why HONO uptake and NO2 uptake, and conversion to nitrite pathways are not important. The conclusion that these two pathways are not important was merely based on the assumption or experience that HONO and NO2 concentrations are very low, while the work did not measure these concentrations. As such, this is a very weak conclusion lacking direct evidence. The work did not show any isotopic evidence, even though there is literature available. What is the lifetime of nitrite on coarse particles, and what is the lifetime on fine particles? Why is nitrite more abundant on coarse particles than fine particles? What is the state of the knowledge? There is no explanation on this at all.
Also, there are several major mistakes in the discussion (Lines 339-347). Specifically, photoenhanced conversion from NO2 to NO2- is not “photocatalysis”; NO2 uptake coefficient varies in a significant range, and 1*10-5 or higher is more typically. For example, see Scharko et al. 2017 ES&T (10.1021/acs.est.7b01363). Also, a typo, “initialed” indicates the recklessness of the manuscript.
- For the investigation of the influence of biomass burning, the authors only did a single back trajectory for each day, which is not sufficient to determine the relative contributions of different air masses transported from different regions. Furthermore, there is no systematic tracer analysis for biomass burning influences. Therefore, the statement in Lines 371-374 is not valid.
Additionally, based on lines 375-381, the authors speculate biomass burning smoke won’t contribute to the coarse mode particulate nitrite, so why would the authors still track the airmass? Additionally, it is inaccurate to state that “particle nitrite has not yet been detected in biomass burning plumes,” according to the cited literature. These works just didn’t measure the nitrite concentrations for some reason, one of which is the detection limit, and nitrite is orders of magnitude smaller than nitrate.
- The interpretation of why nitrite in TSP has a higher δ18Ο is invalid. The author states that aerosol water abundance is at least 3 orders of magnitude larger than NO2- based only on ISOROPIA modeling results without measurement. As we know, the modeled results are highly uncertain and are greatly influenced by the arbitrary input parameters. More important question— What is the hygroscopic property of the soil-derived TSP? What is the relationship between “aerosol liquid water” and TSP? Is the water really in fine particles or coarse particles? Moreover, if the O exchange between water and nitrite is important in aerosol (again, fine particle or coarse particle?), is it supposed to be important in soils? Finally, what is the explanation for the Δ17Ο of soil nitrite compared to the TSP? Unfortunately, there is no clear discussion on this.
- Additionally, what is the Ionic balance for the water-soluble ions in TP and PM2.5?
Additionally, many vague statements prevent me from understanding the key points significantly.
- Line 209, what do you mean by "general decline"? Why use 5/1 as the cut-off date? Is there any statistical analysis?
- Line 212-213, “negligible” is vague.
- Line 214, what is the point of discussing the K+ in PM2.5 that decreases? Why K+ in TSP didn’t show the same trend? Instead, the highest K+ occurs after 5/1?
- Line 215, "comparable" here is not supported by any numerical evidence.
- Lines 220-222, which figure or summarized data shows “average daytime concentrations of the inorganic species were generally higher than those at night”?
- Lines 217-218, what does the Ca2+ and Mg2+ data tell you in addition to “smaller degree”? No point can be achieved.
- In the paragraph starting with Line 228, the first sentence “The variations of WSIs in TSP generally followed a similar 228 pattern to that in PM2.5 (Figure 1)” is an invalid statement as some species have very different trends between TSP and PM2.5, such as K+.
- Line 239, “similar areas of filters were extracted,” doesn’t necessarily ensure the accuracy of the comparison because the sampling setups are different.
- Vague statement in Lines 282-283, “High soil NO2- and NO3- concentrations were observed on the west and east…”. “high” here is vague.
Citation: https://doi.org/10.5194/egusphere-2024-4165-RC3 - AC3: 'Reply on RC3', Zhongyi Zhang, 05 Jun 2025
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Zhongyi Zhang
Chunxiang Ye
Yichao Wu
Tao Zhou
Pengfei Chen
Shichang Kang
Chong Zhang
Zhuang Jiang
The requested preprint has a corresponding peer-reviewed final revised paper. You are encouraged to refer to the final revised version.
- Preprint
(1030 KB) - Metadata XML
-
Supplement
(512 KB) - BibTeX
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- Final revised paper