the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
Using OMPSLP color ratio to extract stratospheric aerosol particle median radius and concentration with application to two volcanic eruptions
Abstract. We derive stratospheric aerosol microphysical parameters from Ozone Mapping Profiler Suite Limb Profiler (OMPSLP) satellite measurements using aerosol extinction coefficient ratios at two wavelengths (the color ratio), which is sensitive to the particle radius, and concentration. We estimate various sources of uncertainty in this technique including extinction coefficient measurement error, sensitivity to the size distribution width assumption, and the OMPSLP algorithm phase function error. We apply our algorithm to extinction coefficient measurements made by the Stratospheric Aerosol and Gas Experiment on the International Space Station (SAGE III/ISS) to verify our approach and find that our results are in good agreement. Our results also compare favorably to balloon borne particle size measurements and concentrations under ambient condition and 2019 Raikoke volcanic eruption assuming a lognormal particle size distribution width of 1.6. We also estimate the changes in aerosol median radius and concentration following the 2019 Raikoke and 2022 Hunga TongaHunga Ha’apai volcanic eruptions and the result is consistent with other retrievals published in the literature.
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CC1: 'Comment on amt2023267', Larry Thomason, 30 Apr 2024
Review of ‘Using OMPSLP color ratio to extract stratospheric aerosol particle median radius and concentration with application to two volcanic eruptions’ by Yi Wang, Mark Schoeberl, Ghassan Taha
This is a resubmission of a paper that was submitted last year and ultimately rejected. I was brought in as an additional reviewer late in the review process by the previous editor due to widely divergent reviews. I spent several days going through the manuscript and provided a detailed accounting of the deficiencies of the manuscript. For whatever reason, my review is not posted on the AMT website, so I have posted as a supplement. In the last few days, a colleague noted that this manuscript had reappeared as a new submission. I must say as a prior reviewer who spent (as I said) several days reviewing the earlier submission, I am disappointed that AMT did not inform me that it had returned as it is incumbent on AMT to be sure that all earlier reviewers were notified of a resubmission.
The new manuscript is better but still exhibits many of the same issues of the prior submission. I will not do a complete review of this document, rather I will concentrate on a couple of issues that, among others, must be corrected prior to publication.
Issue 1
The basic algorithm the authors use is exactly the same as used by Yue and Deepak (1983). Since they have only 2 channels to work with, this is about as good as they can do. Using a fixed width is ok but the authors regularly misrepresent the findings in the reference material particularly those by Rieger, Wrana, and Knepp about how ubiquitous the value of 1.6 is. They could simply note that this value is roughly in the middle of the range normally inferred for SMLN fits and reference the same papers for the range but there are (and must be) negatives associated with this limitation. They could show this with plots that show the impact of using 1.6 when a value of 1.4 or 1.8 is closer to the true value (this sort of hides in Figure 3). I’d recommend that they focus on higher order moments like surface area density or volume density since they are contained much better by the observations, and thus more robustly inferred, than low order moments like number density and number density.
The big problem begins with the basic approach that locks in a onetoone relationship between color ratio and the inferred radius as shown in figure 1. There can be no variation in the inferred radius for the same color ratio wherever it comes from. This is why I am dumbfounded by the authors use of SAGE III as ‘validation’ for their number density/radius retrievals. Since they are employing the exact same algorithm on the SAGE III/ISS data, the only possibility for differences between the inferred SAGE III values and the OMPS values using their algorithm is if their color ratios are different. Since this is an attribute of the extinction coefficient measurements by the two instruments, comparisons of radius and number density are meaningless and have nothing to do with the algorithm and absolutely do not provide validation for their OMPS product. This was specifically called out in my previous review yet remains in this manuscript and, in fact, it is expanded upon. I see no option other than to remove this part of the discussion in its entirety. It could easily be misinterpreted by readers as actual validation. (The authors show a comparison Wyoming OPC during a fairly benign period when comparisons in perturbed periods must be available. These are periods more challenging to their algorithms and the nominal focus of their entire paper.)
Issue 2
In addition to the referencing issues mentioned above, the authors too often misrepresent the content of papers or use irrelevant references when much better ones are available. For instance, the authors state that ‘Our algorithm is similar to the color ratio method developed by Thomason and Vernier’s (2013) for SAGE II that has been also used for cloud identification in SAGE III/ISS data (Schoeberl et al., 2021; Kovilakam et al., 2023).’ None of these papers use the color ratio to infer attributes of the aerosol size distribution but solely use color ratio as an aid to the detection of cloud presence. There are literally dozens of papers which use color ratio to do this (any approach must use color ratios or the aerosol extinction coefficient spectral dependence), these should be used here. I don’t care which ones just use proper ones. When the authors discuss cloud clearing, they reference one of these papers but apparently did not absorb the nuances of cloud detection in limb data nor do they show that their method works well and basically just assert that it works. There are many further such issues like referring to Thomason et al. (2021) as inferring aerosol size distributions (it does not) and so on. I do not normally spend a lot of time on references but it was painfully obvious that they need to scrub their references carefully to ensure relevance and that they are properly represented. Their use of reference material is at best sloppy.
Issue 3
The authors still do not discuss the impact of known deficiencies of the OMPS aerosol products particularly at short wavelengths and after virtually any significant aerosol event in the stratosphere (e.g., volcanoes). The authors must be aware of the ongoing efforts (that they are themselves are doing and/or contributing to) to improve these products but these issues are barely addressed herein. It is well known that there are large differences between SAGE III/ISS and OMPS aerosol products during the HTHH period and other volcanic and smoke events.

CC2: 'Reply on CC1', Travis N. Knepp, 01 May 2024
I agree with much of Larry's comments, but I disagree with the notion that a static distribution width of 1.6 is acceptable. I understand the limited information content of the OMPS measurement forces assumptions, but the value of 1.6 is only reasonable when we are at background conditions, which are quite boring. When the atmosphere is scientifically interesting (post eruptions or pyroCbs) is when this assumption introduces significant bias in this method as can be seen in the Fig. 10. I'll post a separate review of this paper shortly, but I wanted to comment on this aspect of Larry's review that caught my eye.
Citation: https://doi.org/10.5194/amt2023267CC2 
CC3: 'Reply on CC1', Mark Schoeberl, 04 May 2024
While we appreciate Dr. Thomason reposting his older review for discussion, the resubmitted paper is substantially different from the manuscript he previously reviewed. We tried hard to address his and other reviewer’s comments in this version.
Comment 1. We absolutely agree the algorithm we used has been used before by solar occultation instruments, but we are applying here it to a limb scattering instrument. Yue and Deepak (1983) are referenced as are more recent papers using color ratio, for example Bourassa et al. (2008b) with OSIRIS measurements. We are aware of the threewavelength techniques developed by Wrana et al. (2021) and Knepp et al. (2024) can produce median radius and width of the lognormal size distribution. The three channel techniques make use of the SAGE 1.543 µm channel, not available on OMPS. That said, the twochannel techniques applied to limb scattering appear to be robust to the measurement uncertainty and less likely to filter out many pixels beyond the lookup table ranges. On the downside, two channel methods are sensitive to assumptions about size distribution width as we show.
We agree that the SAGE and OMPSLP color ratio retrievals would show no difference when the color ratios are the same. SAGE occultation measurements are the benchmark. We are careful not to refer to our SAGE comparison as validation, but we note that SAGE does provides a check on our method. We refer to the section as ‘Comparison of OMPSLP with SAGE’ and refer to this as a verification of our technique. Differences occur when the extinction values between the instruments differ. For actual validation, we did comparisons to the Wyoming balloon OPC, before the Raikoke eruption and after.
Comment 2. We will relook at our references again. Note that we have included more relevant recent papers by Wrana et al., (2021) and Knepp et al., (2022), etc.
Comment 3. The width of the distribution is fixed in the OMPS retrievals, and using SAGE, with more wavelengths than is available from OMPS, Wrana et al. (2021) showed that ~1.6 is reasonable for background aerosol concentration. This result is in agreement with studies by Rieger et al. (2018), and in situ balloon measurements. For volcanic distributions, 1.6 is too large for the initial eruption, and we used 1.2 from Duchamp et al. (2023, Fig. 2) for Hunga. The sensitivity of the retrieved median radius to the width is shown in the paper.
Unfortunately, color ratio methods using OMPS, cannot tell us much more than the median radius. SAGE with its 1.543 µm wavelength can produce some estimate of the distribution width (Wrana et al., 2021, 2023 and Knepp et al., 2024). If the distribution is bimodal, as occurs after a volcanic eruption, a ‘wide’ distribution and larger median radius will be inferred rather than a small particle mode and a large particle mode as seen in balloon measurements (Wrana et al., 2023). The Knepp et al. (2024) study suggests that even SAGE probably does not have large enough wavelength range to characterize a bimodal distribution.
Our paper tries to characterize the uncertainty in assuming a fixed width, and our results show that that uncertainty is large if the distribution width is significantly different from ~1.6. It might be useful for future OMPS retrievals to use SAGE estimates of the distribution width when considering volcanic eruptions or pyroCb events.
Yi Wang and Mark Schoeberl
Citation: https://doi.org/10.5194/amt2023267CC3 
CC4: 'Reply on CC3', Larry Thomason, 06 May 2024
I thank Mark Schoeberl for replying to my comments. Reading these, I feel that my comments about the SAGE comparisons and the replies to it need further discussion.
The algorithm used in this paper dates to Yue and Deepak (1983) which is the first paper (that I am aware of) to attempt to infer aerosol size distribution from limb/occultation data. In the following 40 years, there have been literally dozens (hundreds?) of papers to attempt this using a variety of instruments with varying numbers of measurements of extinction coefficient (and similar quantities) and approaches. I've written a couple myself. All of these apply constraints to the solution space (the outcomes_ because none of these measurement sets contain a great deal of information about the underlying aerosol size distribution. The type and strength of the constraint has an important impact on retrieved values depending on characteristics of the data set to which it is applied and the constraints can even dominate the solutions. Low information content on aerosol size distributions is a feature of with SAGE II measurements of aerosol extinction coefficient (at 34 wavelengths) and to SAGE III with nominally 9 measurement wavelengths. It is also true with OMPS as the authors employ only 2 measurement wavelengths. It is exacerbated by measurement uncertainty and correlation among the measurement wavelengths. These retrievals require care and will always be limited in how well they can ever infer the size distribution and describing any of these processes as 'robust' is optimistic particularly without carefully evaluating the impact of the constraints applied.
That said, my concerns about the SAGE/OMPS comparisons isn't actually dependent on the algorithm applied. For the purposes of this comment, the algorithm can be considered a black box into which data from an instrument is injected and size distribution parameters are output. In any algorithm I've seen applied to these sorts of data, injecting similar data yields similar outputs. The outputs are not even required to make sense. Certainly, for the algorithm applied in this paper, the idea that similar data inputs yield similar output data must be true. It doesn't matter where this similar data comes from. Similar OMPS sets of measurements must yield similar output values. A set of measurements from SAGE III must yield an output that is similar to that produced by similar measurements from OMPS. Unless there's something very unusual in how the algorithm is implemented, I don't see how this can be any other way. We also know that at least in benign conditions (as in the example in Figure 7), OMPS aerosol and SAGE III aerosol are in rough agreement at some wavelengths. As a result, as I stated in my original comment, the only thing that the SAGE III comparison shows (e.g., Figure 7) is that the data from the two systems going into the algorithm black box in the spatial/temporal range shown is similar. It says nothing about the robustness of the algorithm being applied and it simply can't. I do not understand what the authors think these comparisons show. And despite carefully not referring to these comparisons as validation, it is very likely that the average reader will interpret comparisons which nominally show decent agreement as just that. Given that it is really relatively the SAGE comparisons are pretty meaningless except as an indirect assessment of how well the extinctions coefficient measurements agree, it really must be removed.
If the authors really want to use SAGE III data in this paper, a suggestion is to use SAGE III to test how sensitive the inferred mode radius and number density (SAD, etc.) from this algorithm are to wavelength pairs. With SAGE III, you could potentially test any number of such wavelength pairs with wavelengths as far apart as 449 and 1540 nm. The results could be interesting. I think Wrana did work similar to this.
For a paper that is focused on the Raikoke and HTHH eruptions, it is kind of surprising that the comparisons between SAGE and OMPS is for a very benign period (Figure 7), a partial comparison for Raikoke (Figure 8 with no number density) and nothing for HTHH. Why is that? There is plenty of overlap between the instruments throughout their lifetimes. It seems necessary that any comparison of SAGE III and OMPS retrievals are shown for nominal time period on which the paper is focused.
The OPC comparisons are Ok as validation. Though only for Raikoke. Certainly OPC data from HTHH exists (see work by Corinna Kloss, Vernier, and the POPS team). Why not extend this?
Citation: https://doi.org/10.5194/amt2023267CC4 
AC4: 'Reply on CC4', Yi Wang, 23 Aug 2024
“I thank Mark Schoeberl for replying to my comments. Reading these, I feel that my comments about the SAGE comparisons and the replies to it need further discussion.”
Response: While we appreciate Dr. Thomason reposting his older review for discussion, the resubmitted paper is substantially different from the manuscript he previously reviewed. We tried hard to address his and other reviewer’s comments in this version. The comments below are specifically addressing his reply to the online discussion.
“The algorithm used in this paper dates to Yue and Deepak (1983) which is the first paper (that I am aware of) to attempt to infer aerosol size distribution from limb/occultation data. In the following 40 years, there have been literally dozens (hundreds?) of papers to attempt this using a variety of instruments with varying numbers of measurements of extinction coefficient (and similar quantities) and approaches. I've written a couple myself. All of these apply constraints to the solution space (the outcomes_ because none of these measurement sets contain a great deal of information about the underlying aerosol size distribution. The type and strength of the constraint has an important impact on retrieved values depending on characteristics of the data set to which it is applied and the constraints can even dominate the solutions. Low information content on aerosol size distributions is a feature of with SAGE II measurements of aerosol extinction coefficient (at 34 wavelengths) and to SAGE III with nominally 9 measurement wavelengths. It is also true with OMPS as the authors employ only 2 measurement wavelengths. It is exacerbated by measurement uncertainty and correlation among the measurement wavelengths. These retrievals require care and will always be limited in how well they can ever infer the size distribution and describing any of these processes as 'robust' is optimistic particularly without carefully evaluating the impact of the constraints applied.”
Response: We acknowledge the limitations of using the two OMPS channels for retrievals compared to SAGE. Our experience is that the number of wavelengths is less important than the spectral range in estimating size. The threechannel technique employed in SAGE III/ISS measurements benefits from the broader wavelength range—specifically, 449 nm, 756 nm, and 1544 nm, as highlighted by Wrana et al. (2021). In contrast, OMPS operates within a narrower range of 510997 nm. Figure A1, which has been added to the manuscript, illustrates how this shorter wavelength range challenges the derivation of distribution width from two OMPS color ratios. We have included relevant discussions in Section 2.2 to address this issue.
To assess the robustness of the algorithm, we have also detailed the sources of error and the associated uncertainties in estimating particle size. The sources of error include assumptions about the particle size distribution width, the phase function and the measured radiances. The OMPSLP aerosol measurement is not as good as SAGE, but comparisons to balloon measurements show that the algorithm does a pretty good job.
“That said, my concerns about the SAGE/OMPS comparisons isn't actually dependent on the algorithm applied. For the purposes of this comment, the algorithm can be considered a black box into which data from an instrument is injected and size distribution parameters are output. In any algorithm I've seen applied to these sorts of data, injecting similar data yields similar outputs. The outputs are not even required to make sense. Certainly, for the algorithm applied in this paper, the idea that similar data inputs yield similar output data must be true. It doesn't matter where this similar data comes from. Similar OMPS sets of measurements must yield similar output values. A set of measurements from SAGE III must yield an output that is similar to that produced by similar measurements from OMPS. Unless there's something very unusual in how the algorithm is implemented, I don't see how this can be any other way. We also know that at least in benign conditions (as in the example in Figure 7), OMPS aerosol and SAGE III aerosol are in rough agreement at some wavelengths. As a result, as I stated in my original comment, the only thing that the SAGE III comparison shows (e.g., Figure 7) is that the data from the two systems going into the algorithm black box in the spatial/temporal range shown is similar. It says nothing about the robustness of the algorithm being applied and it simply can't. I do not understand what the authors think these comparisons show. And despite carefully not referring to these comparisons as validation, it is very likely that the average reader will interpret comparisons which nominally show decent agreement as just that. Given that it is really relatively the SAGE comparisons are pretty meaningless except as an indirect assessment of how well the extinctions coefficient measurements agree, it really must be removed.
If the authors really want to use SAGE III data in this paper, a suggestion is to use SAGE III to test how sensitive the inferred mode radius and number density (SAD, etc.) from this algorithm are to wavelength pairs. With SAGE III, you could potentially test any number of such wavelength pairs with wavelengths as far apart as 449 and 1540 nm. The results could be interesting. I think Wrana did work similar to this.”
Response: Even though we made it quite clear that the SAGE comparisons aren’t ‘validation,’ we understand the concern that it could be interpreted as validation, and have thus removed the section comparing our results to SAGE.
“For a paper that is focused on the Raikoke and HTHH eruptions, it is kind of surprising that the comparisons between SAGE and OMPS is for a very benign period (Figure 7), a partial comparison for Raikoke (Figure 8 with no number density) and nothing for HTHH. Why is that? There is plenty of overlap between the instruments throughout their lifetimes. It seems necessary that any comparison of SAGE III and OMPS retrievals are shown for nominal time period on which the paper is focused.
The OPC comparisons are Ok as validation. Though only for Raikoke. Certainly OPC data from HTHH exists (see work by Corinna Kloss, Vernier, and the POPS team). Why not extend this?”
Response: A detailed validation of OMPS LP retrieved aerosol extinction during the Hunga eruption is beyond the scope of this work. However, we note that an alternate algorithm used by the University of Saskatoon was compared to the NASA algorithm for Hunga conditions (Schoeberl et al., 2024; Bourassa et al., 2023)) where the NASA OMPS retrieved SAOD was higher than SAGE III, and the USask algorithm was lower. Outside of that unique period, the USask, NASA OMPS and SAGE agree pretty well (as noted in the comment). Duchamp et al. (2023) using the methodology developed in Wrana et al. (2021) showed that the width of the size distribution is much smaller for Hunga and in this paper we redid our calculations using the Duchamp’s width estimates.
Citation: https://doi.org/10.5194/amt2023267AC4

AC4: 'Reply on CC4', Yi Wang, 23 Aug 2024

CC4: 'Reply on CC3', Larry Thomason, 06 May 2024

CC2: 'Reply on CC1', Travis N. Knepp, 01 May 2024

CC5: 'Comment on amt2023267', Travis N. Knepp, 06 May 2024
The comment was uploaded in the form of a supplement: https://amt.copernicus.org/preprints/amt2023267/amt2023267CC5supplement.pdf

CC6: 'Reply on CC5', Yi Wang, 07 May 2024
We greatly appreciate the thorough and detailed review by Dr. Knepp. Clearly he spent a lot of time on our paper and his remarks and suggestions will be taken very seriously in our revisions. Reviewing is a thankless job, and this review no doubt took some time to develop. It is apparent to us that some of our arguments are not clear, and that is on us. Again, we thank him for this review.
Citation: https://doi.org/10.5194/amt2023267CC6 
CC7: 'Reply on CC6', Travis N. Knepp, 07 May 2024
Hello Dr. Wang! Thank you for the kind words. Indeed, reviewing can be a thankless job.
You commented that "It is apparent to us that some of our arguments are not clear, and that is on us." I am afraid it is worse than that; this is not a simple misunderstanding. I dare say that I understand your method quite well and it is wrong for the reasons I posted in my review. I raised several major concerns with your manuscript (starting with the original submission) and to date they have not been addressed.
Citation: https://doi.org/10.5194/amt2023267CC7

CC7: 'Reply on CC6', Travis N. Knepp, 07 May 2024

CC6: 'Reply on CC5', Yi Wang, 07 May 2024

CC8: 'Comment on amt2023267', Mahesh Kovilakam, 09 May 2024
The comment was uploaded in the form of a supplement: https://amt.copernicus.org/preprints/amt2023267/amt2023267CC8supplement.pdf

AC5: 'Reply on CC8 and CC5', Yi Wang, 23 Aug 2024
The comment was uploaded in the form of a supplement: https://amt.copernicus.org/preprints/amt2023267/amt2023267AC5supplement.pdf

AC5: 'Reply on CC8 and CC5', Yi Wang, 23 Aug 2024

RC1: 'Comment on amt2023267', Anonymous Referee #1, 17 Jun 2024
The comment was uploaded in the form of a supplement: https://amt.copernicus.org/preprints/amt2023267/amt2023267RC1supplement.pdf

AC1: 'Reply on RC1', Yi Wang, 23 Aug 2024
The comment was uploaded in the form of a supplement: https://amt.copernicus.org/preprints/amt2023267/amt2023267AC1supplement.pdf

AC1: 'Reply on RC1', Yi Wang, 23 Aug 2024

RC2: 'Comment on amt2023267', Anonymous Referee #2, 21 Jun 2024
The paper presents an interesting analysis of microphysical properties of stratospheric aerosols from OMPSLP color ratio, using a new algorithm. Then, the analysis concern two main volcano eruptions (Raikoke and HungaTunga). The paper is well written; in particular I really appreciate the parts on the uncertainties.
The analysis makes the assumption that aerosol are liquid, thus their optical properties can be calculated by Mie scattering theory. The authors must say that Mie scattering works well for liquid particles. but not so well for solid and irregular shaped particles. Some of this particles, for example olivine, but also other minerals or carbonaceous ones, has color effect that cannot be related to the mean radius (line 83). The authors must explain how they have considered this problem, probably in sections 2.2 and 23.
I have a problem with the reference list, where European work on similar subject is sometimes ignored. I can encourage the authors to improve their reference list.
Line 17: I think here is one too many “Hunga” in the text.
Line 25 : I am very surprised that authors have not cited our two papers on the nature of stratospheric aerosol from insitu balloon measurements. The first one is the first paper were soot particles in the stratosphere were detected for the first time, superimposed on sulfate aerosols. The second one provides a review of the possible sources of the solid particles in the stratosphere, also superimposed on sulfates. The editor could appreciate if this comment can or cannot be provide to the authors.
J.B. Renard, C. Brogniez, G. Berthet, Q. Bourgeois, B. Gaubicher, M. Chartier, J.Y. Balois, C. Verwaerde, F. Auriol, P. Francois, D. Daugeron, et C. Engrand, Vertical distribution of the different types of aerosols in the stratosphere, Detection of solid particles and analysis of their spatial variability, J. Geophys. Res., 113, D21303, doi:10.1029/2008JD010150, 2008.
J.‐B. Renard, G. Berthet, A.‐C. Levasseur‐Regourd, S. Beresnev, A. Miffre, P. Rairoux, D. Vignelles, F. Jégou, Origins and Spatial Distribution of Non‐Pure Sulfate Particles (NSPs) in the Stratosphere Detected by the Balloon‐Borne Light Optical Aerosols Counter (LOAC), Atmosphere 11, 1031, 2020; doi:10.3390/atmos11101031.
Line 24: The literature shows that particles larger than 1 µm are often detected.
Line 101: Why the authors has not considered the size distribution from the balloonborne LOAC aerosol counter ?
Line 107: True if the particles are liquid, wrong if they are solid. The authors must write that their analysis is for liquid particles.
Line 217: This could be due to the contribution of solid particles above 25 km.
Part 4.2: Again, why the authors has not considered our work on the Raikoke aerosols ?
 Kloss, G. Berthet, P. Sellitto, F. Ploeger, G. Taha, M. Tidiga, M. Eremenko, A. Bossolasco, F. Jégou, J.B. Renard, B. Legras, Stratospheric aerosol layer perturbation caused by the 2019 Raikoke and Ulawun eruptions and their radiative forcing, Atmos. Chem. Phys., 21, 535–560, 2021 https://doi.org/10.5194/acp215352021.
Figure 9: I don’t understand why there are two profiles with black lines.
Citation: https://doi.org/10.5194/amt2023267RC2 
AC2: 'Reply on RC2', Yi Wang, 23 Aug 2024
The paper presents an interesting analysis of microphysical properties of stratospheric aerosols from OMPSLP color ratio, using a new algorithm. Then, the analysis concern two main volcano eruptions (Raikoke and HungaTunga). The paper is well written; in particular I really appreciate the parts on the uncertainties.
The analysis makes the assumption that aerosol are liquid, thus their optical properties can be calculated by Mie scattering theory. The authors must say that Mie scattering works well for liquid particles. but not so well for solid and irregular shaped particles. Some of these particles, for example olivine, but also other minerals or carbonaceous ones, has color effect that cannot be related to the mean radius (line 83). The authors must explain how they have considered this problem, probably in sections 2.2 and 23.
Response: This is a valid point. We added a sentence on line 104 that the particles are assumed spherical, which is true for background and sulphate aerosol.
I have a problem with the reference list, where European work on similar subject is sometimes ignored. I can encourage the authors to improve their reference list.
Response: Thanks for your suggestions; we added several references based on European studies. If you have additional recommendations for key papers that should be included, we would be glad to consider adding them.
Line 17: I think here is one too many “Hunga” in the text.
Response: After careful consideration, we decided to use the official name of the volcano rather than an abbreviation, particularly since the volcano is only a section of the overall study.
Line 25 : I am very surprised that authors have not cited our two papers on the nature of stratospheric aerosol from insitu balloon measurements. The first one is the first paper were soot particles in the stratosphere were detected for the first time, superimposed on sulfate aerosols. The second one provides a review of the possible sources of the solid particles in the stratosphere, also superimposed on sulfates. The editor could appreciate if this comment can or cannot be provide to the authors.
J.B. Renard, C. Brogniez, G. Berthet, Q. Bourgeois, B. Gaubicher, M. Chartier, J.Y. Balois, C. Verwaerde, F. Auriol, P. Francois, D. Daugeron, et C. Engrand, Vertical distribution of the different types of aerosols in the stratosphere, Detection of solid particles and analysis of their spatial variability, J. Geophys. Res., 113, D21303, doi:10.1029/2008JD010150, 2008.
J.‐B. Renard, G. Berthet, A.‐C. Levasseur‐Regourd, S. Beresnev, A. Miffre, P. Rairoux, D. Vignelles, F. Jégou, Origins and Spatial Distribution of Non‐Pure Sulfate Particles (NSPs) in the Stratosphere Detected by the Balloon‐Borne Light Optical Aerosols Counter (LOAC), Atmosphere 11, 1031, 2020; doi:10.3390/atmos11101031.
Response: We added these two valuable references to the manuscript. Thanks.
Line 24: The literature shows that particles larger than 1 µm are often detected.
Response: Our rewrite of this section indicates larger that 1 µm are observed.
Line 101: Why the authors has not considered the size distribution from the balloonborne LOAC aerosol counter ?
Response: We revised to “This size distribution is consistent with in situ stratospheric aerosol measurements (Deshler et al. 2003; Bourassa et al. 2008b), which assumes a bimodal lognormal size distribution. The details will be discussed further below.”
Line 107: True if the particles are liquid, wrong if they are solid. The authors must write that their analysis is for liquid particles.
Response: Revised.
Line 217: This could be due to the contribution of solid particles above 25 km.
Response: In response to the strong opinions expressed in the community comments, we have decided to remove Section 3.1, which compared of OMPSLP PSD retrievals with SAGE III/ISS. Thanks.
Part 4.2: Again, why the authors has not considered our work on the Raikoke aerosols ?
 Kloss, G. Berthet, P. Sellitto, F. Ploeger, G. Taha, M. Tidiga, M. Eremenko, A. Bossolasco, F. Jégou, J.B. Renard, B. Legras, Stratospheric aerosol layer perturbation caused by the 2019 Raikoke and Ulawun eruptions and their radiative forcing, Atmos. Chem. Phys., 21, 535–560, 2021 https://doi.org/10.5194/acp215352021.
Response: We added this reference to Section 4.2. Thanks.
Figure 9: I don’t understand why there are two profiles with black lines.
Response: The ballon data is fit to a bimodal distribution and reported a such. Thus, there are two mode radii as indicated by the two lines. We have added this information to the caption (now it is Fig. 7).
Citation: https://doi.org/10.5194/amt2023267AC2

RC3: 'Comment on amt2023267', Anonymous Referee #3, 01 Jul 2024
Review of AMT manuscript entitled "Using OMPSLP color ratio to extract stratospheric aerosol particle median radius and concentration with application to two volcanic eruptions" by Wang, Schoeberl and Taha
General comments:
This manuscript presents retrievals of stratospheric aerosol size parameters based on limbscatter measurements with the OMPSLP instrument. The size retrieval is based on a 2step approach. In the first step, aerosol extinction profiles at several wavelengths are retrieved from the OMPSLP measurements (based on the assumption of a gamma PSD (particle size distribution). In a second step, the extinction profiles at different wavelengths are used to form a colour ratio, which is used to retrieve the median radius of a monomodal lognormal PSD with a certain width parameter. Ideally, the size estimates should be used to repeat step one again in an iterative way, but this is beyond the scope of the present paper. I don’t have any major objections against the basic approach used in the current paper, but the paper is not precise in some essential parts and I’m not sure, whether the implementation of the method to estimate the median radius is really robust (see specific comments) below. One central aspect is the exact meaning of equation 1b. It needs to be clearly stated, whether the integration over the PSD is considered in the cross section in equation 1b or not. The cross section includes “s” as an argument, but several other statements in the manuscript imply that the cross section is determined here for a monodisperse PSD with radius r_0. If the latter assumption is correct, then the results are not robust in my opinion.
In addition, the manuscript contains too many statements that are at least misleading, some are wrong. In my opinion, at least a major revision of the manuscript is required before the paper should be accepted for publication in AMT.
I ask the authors to consider the specific comments listed below.
Specific comments:
Line 9: “using aerosol extinction coefficient ratios at two wavelengths”
Are you using more than one ratios? Then it would be more than two wavelengths. The statement is misleading.
Line 9: “(the color ratio), which is sensitive to the particle radius, and concentration.”
The colour ratio is not sensitive to concentration. The concentration cancels out when taking the ratio.
Line 11: “and the OMPSLP algorithm phase function error.“
The reader – who is not familiar – with your approach will probably not understand this part of the sentence. My first though was: if you estimate the size, you can determine the phase function. But this refers to the phase function assumed for the extinction profile retrieval, which is the first step, before you infer the size.
Line 22: “that form in the high relative humidity lower stratosphere”
Doesn’t the stratosphere have a rather low relative humidity?
Line 42: “(Malinina et al., 2018)“
This is an aerosol retrieval paper, Llewellyn et al. (for OSIRIS) is an instrument paper. Perhaps this should be consistent. Flynn et al. and Jaross et al. are also rather instrument papers.
Line 43: “solar osculation“
Line 48: “limb scattering retrievals often requires a forward model calculation“
Why “often”? I think limbscatter retrievals of aerosols always require a forward model. And by the way: also the occultation retrievals require a model, although of a different kind.
“requires” > “require”
Line 73: “The E at wavelength lamda, is proportional to the scattering coefficient (1a)”
This is somewhat unclear. If absorption is neglected then the extinction coefficient is identical to the scattering coefficient. If absorption is not negligible, then the extinction coefficient is not proportional to the scattering coefficient. Please rephrase.
Line 77: “Eq. (1) can be approximated as the equivalent cross section (sigma) times N.“
I don’t understand this statement. Why “approximated”? Does sigma include the integration over the PSD? Then this is not an approximation, but an exact result.
My impression is that the sigma in equation 1b does not consider the integration over the PSD, but is the scattering cross section for median radius r_0? If this is the case, I disagree with the approach taken here. This is a crucial point and needs to be explained well.
Line 80: “the equivalent cross section”
You refer to the product of the scattering cross section and the phase function, right? This product is usually called the “differential scattering cross section” and I suggest sticking to this term.
Line 80: “For occultation measurements p = 1”
This is not correct. For a forward scattering geometry, the phase function can assume many different values, depending on the PSD. Plus: for the occultation measurements the transmitted radiation is relevant, not the (forward) scattered radiation. Different things are mixed up here.
Equation 2: So Equation 1b is used to determine the colour ratios? If the distribution width does not play a role here (which is unclear from the text), then this is the wrong approach.
Line 83: “and the CR is proportional to the Ångstrom exponent”
No, the CR is not proportional to the Angstrom exponent!
Line 84: “The Eq. 1b approximation works for both limb scattering and occultation measurements.”
I do not agree with this statement. Different things may be mixed up here (see comments above).
Line 88: “A radiative transfer model then computes the scattered radiance as a first guess assuming background particle size distribution.”
Which PSD parameters are assumed here?
Line 97: “To demonstrate how using the CR provides information on the aerosol concentration”
The CR itself cannot provide information on the concentration.
Line 109: “By calculating the aerosol extinction coefficient equivalent crosssections“
What do you mean by “extinction coefficient equivalent crosssections”? This quantity does not really exist. I guess you mean the differential scattering crosssection?
Line 110: “Eq. (1b) can then be used to compute the aerosol number density. This method produces both consistent number density and particle size and was used by Bourassa et al. (2008b).”
If you do it this way, the number density and the size may not be consistent, because:
(a) the retrieval of the radius assumed a monomodal lognormal PSD with sigma = 1.6
(b) equation 1b assumes a monodisperse aerosol (if equation 1 b is really meant this way).
Please clarify the exact meaning of equation 1 b.
Line 126: “The second source of uncertainty comes from the assumption that our size computation is independent of the assumed width of the aerosol size distribution”
I’m not sure, how to interpret this? To me, this implies that a monodisperse PSD is assumed for equation 1b? But below you mention again that you assume a monomodal lognormal PSD?
Line 129: “In our algorithm, size can vary, and changes in the particle size may thus be inconsistent with the RTM phase function and this can be a source of error.”
Yes, ideally your retrieval should be iterative and the phase function for the extinction profile retrieval should be updated after the size retrieval.
Line 147: “and found that most of the observations clustered between s = 1.4 and 1.6.”
The Wrana values are for a limited period of time and specific stratospheric conditions. For a volcanically perturbed stratosphere s will typically be smaller.
Line 167: “and averaging color ratios are between 2 and 4,“
“averaged” ? Grammar doesn’t seem to be correct here.
Line 168: “Using (1b) and assuming that effective cross section is proportional to the square of the mode radius leads to a number density uncertainty of 44%.”
How good is the assumption of a quadratic dependence of the cross section on mode radius? I would expect a stronger dependence of the "differential" scattering Xsection on radius.
Equation (5): The units don't match. Is this an exact relationship or an approximation?
Line 190: “lead” > “leads”
Line 193: “increases the peak of the differential size distribution”
What is the "differential" size distribution?
Equation (6): I'm not sure this approach is OK. Equation 6 only works for a monomodal lognormal PSD. In your case the PSD is a gamma function. See also next comment.
Line 204: “The resulting CR and r_m uncertainty increase to ± 1120% and ±1232%”
This means, if you double the median radius (converted from gamma to lognormal), you only get an r_m retrieval error of 12  32 %? This seems inconsistent and if correct, is probably related to the incompatibility of the gamma and lognormal PSDs.
Line 219: “the SAGE III/ISS CR extinction coefficient”
? What exactly does this mean? CR or extinction coefficient?
Line 224: “For the SAGE III/ISS data, we use multiple profiles in the latitude range indicated, while OMPSLP measurements are selected to be near coincident with the location of the SAGE profiles.”
I don't really understand this statement? Why are the two instruments treated differently? The latitude ranges in Fig. 7 are quite narrow and all the SAGE measurements on a given day are essentially for the same latitude anyway? Are the OMPS measurements also within the latitude range given?
Line 229: “are compared for four different scattering angle regimes.”
What latitude bins are used to select the OMPSLP measurements?
Line 248: “is consistent with Bourassa et al. (2012) and Taha et al. (2021) comparison between OMPSLP and SAGE”
Please check grammar.
Line 257: “The total LOPC particle concentration includes particles that are too small to scatter light”
Well, also the small particles scatter radiation (even molecules do; you also measure Rayleigh scattered solar radiation with OMPSLP), but their contribution is buried under the much larger contribution of the larger particles.
Line 297: “The regions of lower extinction and higher CR may indicate the process of aerosol formation or evaporation of larger particles.“
The different regions also correspond to different altitudes, right? By the way, it seems, it is not mentioned what altitude range has been used to produce this Figure.
Line 309: “Figure 11c and 11d show the distribution of aerosols for a 30day period following the eruption.”
The measurements may the also be affected by ash? Why not using a later time interval?
Line 316: “Note that extinction/radius/number density may be contaminated by icelofting”
Also by ash, Raikoke was a relatively ashrich eruption.
Line 326 – 329: you may also include Wrana et al. (2023) (which is listed in the reference list anyway) in the discussion.
Line 335: “which results in ~23% algorithm uncertainty for“
Somewhat unclear, what “algorithm uncertainty” refers to?
Line 336: “showed that V2.1 retrievals have very little sensitivity to the assumed aerosol model errors due to the viewing geometry variations.”
Also not entirely clear, what this means. What exactly does "aerosol model" refer to?
Line 353: “(Wrana et al., 2023)”
This paper does not deal with the HTHH eruption.
Line 358: “Figure 14 shows the time series of zonal median retrieved particle radius and number density between”
Fig. 14 shows extinction coefficient and radius, not number density.
Line 359: “A transition from a width 1.6 before the eruption to 1.2 following the eruption is applied.”
? Why doesn't this show up in the plots? When was this change applied exactly? I don't think this is a good idea. I think this change should show up in some way in the size and number density plots.
Line 364: “The 0.4 micron peak in the median radius”
Above you mentioned that your approach does not allow retrieving radii exceeding 300 nm.
Line 364 following: I suggest discussing the results of Duchamp et al., (2023) in this context. The paper is included in the reference list, but not cited in the text.
Line 370: “and three days (bd) days following the eruption.”
This wording is misleading. You show results for 3 individual days after the eruptions, but the sentence rather suggests that these are the results three days after the eruption. Please adjust the sentence.
Line 375: “The retrieved median radius of ~0.3 micron is consistent with Taha et al., (2022).”
Did Taha et al. (2022) also show size retrievals? Why is Duchamp et al. (2023) not mentioned here? It is listed in the reference list, but not cited.
Line 381: “provide” > “provides”
Line 385: “Using the Mie code inside the SASKATRAN radiative transfer model, we show that the ratio of extinction coefficient at two wavelengths (color ratio) is independent of the number density”
This is correct, but not really shown in this paper (and not really worth mentioning). In contrast, you state several times that number density can be retrieved from the colour ratio!
Line 389: “Our algorithm follows the approach of Bourossa et al. (2008b), Rieger et al, (2018) and Wrana et al. (2021).“
Wrana used a different approach with two colour ratios. I think this is a significant difference and therefore it does not seem to be justified to claim that you use the approach of Wrana.
Line 391: “The OMPSLP algorithm (Taha et al., 2021) assumes the same PSD for each wavelength“
?? well, the PSD is of course independent of wavelength. I don't understand this statement?
Line 403: “There are three major sources of uncertainty in our radius calculation: uncertainty in the measured radiance,“
Above you did not mention the uncertainty in the radiance, but the one in the extinction coefficient, which is something different. Also, in the main text of the papers one of the three major sources of uncertainty is a different one. This should be consistent.
Line 406: “We find that the radius changes for different distribution widths can be substantial leading to nonnegligible uncertainties in median radius and derived number concentration.”
Comparing effective radii would be a good idea here.
Line 410: “The exception appears to be the HungaTonga eruption where SAGE measurements support a smaller distribution width of 1.2 (Wrana et al., 2023)”
Wrana et al. (2023) did not study HTHA.
Figure 2: What do the large colour ratios directly above the cloud height level mean?
Caption Figure 5: “Scattering angles represent the range of are in the northern hemisphere”
Figure 9: What are the "two" lines for the OPC measurements? Different modes of the PSD? This is not mentioned, as far as I can tell.
Figures 9 and 10: a comparison of effective radii would be interesting here.
Figure 11: please explain the difference between “aerosols” and “aerosol plume” in the caption.
Figure 11: what altitude range do the results correspond to?
Citation: https://doi.org/10.5194/amt2023267RC3 
AC3: 'Reply on RC3', Yi Wang, 23 Aug 2024
Review of AMT manuscript entitled "Using OMPSLP color ratio to extract stratospheric aerosol particle median radius and concentration with application to two volcanic eruptions" by Wang, Schoeberl and Taha
General comments:
This manuscript presents retrievals of stratospheric aerosol size parameters based on limbscatter measurements with the OMPSLP instrument. The size retrieval is based on a 2step approach. In the first step, aerosol extinction profiles at several wavelengths are retrieved from the OMPSLP measurements (based on the assumption of a gamma PSD (particle size distribution). In a second step, the extinction profiles at different wavelengths are used to form a colour ratio, which is used to retrieve the median radius of a monomodal lognormal PSD with a certain width parameter. Ideally, the size estimates should be used to repeat step one again in an iterative way, but this is beyond the scope of the present paper. I don’t have any major objections against the basic approach used in the current paper, but the paper is not precise in some essential parts and I’m not sure, whether the implementation of the method to estimate the median radius is really robust (see specific comments) below. One central aspect is the exact meaning of equation 1b. It needs to be clearly stated, whether the integration over the PSD is considered in the cross section in equation 1b or not. The cross section includes “s” as an argument, but several other statements in the manuscript imply that the cross section is determined here for a monodisperse PSD with radius r_0. If the latter assumption is correct, then the results are not robust in my opinion.
In addition, the manuscript contains too many statements that are at least misleading, some are wrong. In my opinion, at least a major revision of the manuscript is required before the paper should be accepted for publication in AMT.
I ask the authors to consider the specific comments listed below.
Response: Thanks for your comments. Note that the gamma size distribution is used only in the first guess in the OMPS RTM expected radiance. Then at each OMPS wavelength, the Chahine algorithm iterates with the observed radiance by varying the extinction. Thus, the extinction is disconnected from the initial size distribution, and the color ratio allows us to reestimate the mode radius. This process is explained in more detail starting in ln 99.
The integration over the PSD is built into the equivalent cross section. Specifically, we assumed a monomodal lognormal PSD with median radius of r_{m} and distribution width of s. There was a notion typo in the equation 1b, which created confusion about this issue. We fixed that.
Specific comments:
Line 9: “using aerosol extinction coefficient ratios at two wavelengths”
Are you using more than one ratios? Then it would be more than two wavelengths. The statement is misleading.
Response: We are using one ratio. Thanks for pointing that, we corrected the sentence.
Line 9: “(the color ratio), which is sensitive to the particle radius, and concentration.”
The colour ratio is not sensitive to concentration. The concentration cancels out when taking the ratio.
Response: Thanks for pointing out. Corrected.
Line 11: “and the OMPSLP algorithm phase function error.“
The reader – who is not familiar – with your approach will probably not understand this part of the sentence. My first thought was: if you estimate the size, you can determine the phase function. But this refers to the phase function assumed for the extinction profile retrieval, which is the first step, before you infer the size.
Response: Your understanding is correct. We added explanation, and the sentence changed to “and the uncertainty in the OMPSLP algorithm assumed phase function.”
Line 22: “that form in the high relative humidity lower stratosphere”
Doesn’t the stratosphere have a rather low relative humidity?
Response: Although the stratosphere is very dry, the lower stratosphere is also quite cold and the relative humidity high enough to prevent the evaporation of sulphate aerosols. They do evaporate at higher altitudes where the stratosphere is warmer.
Line 42: “(Malinina et al., 2018)“ This is an aerosol retrieval paper, Llewellyn et al. (for OSIRIS) is an instrument paper. Perhaps this should be consistent. Flynn et al. and Jaross et al. are also rather instrument papers.
Response: We updated to Bovensmann et al. (1999) for consistency to instrument papers.
Line 43: “solar osculation“
Line 48: “limb scattering retrievals often requires a forward model calculation“
Why “often”? I think limbscatter retrievals of aerosols always require a forward model. And by the way: also the occultation retrievals require a model, although of a different kind.
“requires” > “require”
Response: We corrected these errors. We revised to “However, unlike the solar occultation, limb scattering retrievals require a forward model calculation and aerosol particle assumptions for the aerosol retrieval.”
Line 73: “The E at wavelength lamda, is proportional to the scattering coefficient (1a)”
This is somewhat unclear. If absorption is neglected then the extinction coefficient is identical to the scattering coefficient. If absorption is not negligible, then the extinction coefficient is not proportional to the scattering coefficient. Please rephrase.
Response: We changed it to “is identical to the scattering coefficient when gas or particle absorption is neglected (1a)”
Line 77: “Eq. (1) can be approximated as the equivalent cross section (sigma) times N.“
I don’t understand this statement. Why “approximated”? Does sigma include the integration over the PSD? Then this is not an approximation, but an exact result.
My impression is that the sigma in equation 1b does not consider the integration over the PSD, but is the scattering cross section for median radius r_0? If this is the case, I disagree with the approach taken here. This is a crucial point and needs to be explained well.
Response: We use the integration over the PSD in this study. In equation 1b, it should be r_m, which is median radius of a monomodal lognormal PSD. We corrected it and rephrased the sentences.
Line 80: “the equivalent cross section”
You refer to the product of the scattering cross section and the phase function, right? This product is usually called the “differential scattering cross section” and I suggest sticking to this term.
Response: We changed to “differential scattering cross section”.
Line 80: “For occultation measurements p = 1”
This is not correct. For a forward scattering geometry, the phase function can assume many different values, depending on the PSD. Plus: for the occultation measurements the transmitted radiation is relevant, not the (forward) scattered radiation. Different things are mixed up here.
Response: Thanks. We removed that sentence to provide more clarity.
Equation 2: So Equation 1b is used to determine the colour ratios? If the distribution width does not play a role here (which is unclear from the text), then this is the wrong approach.
Response: The distribution width does play a role in Equation 1b. We added more explanations to the relevant places.
Line 83: “and the CR is proportional to the Ångstrom exponent”
No, the CR is not proportional to the Angstrom exponent!
Response: The optical depth (t) ratio is related to the Ångström as noted by Rieger et al. (2014). The optical depth is the integral of the extinction over the path, hence the color ratio is related to the Ångström exponent. This is made clearer in the text.
Line 84: “The Eq. 1b approximation works for both limb scattering and occultation measurements.”
I do not agree with this statement. Different things may be mixed up here (see comments above).
Response: We deleted that sentence for avoiding misunderstanding.
Line 88: “A radiative transfer model then computes the scattered radiance as a first guess assuming background particle size distribution.”
Which PSD parameters are assumed here?
Response: The OMPSLP aerosol retrieval algorithm assumes a gamma aerosol size distribution. More information can be found at Section 2.3.
Line 97: “To demonstrate how using the CR provides information on the aerosol concentration”
The CR itself cannot provide information on the concentration.
Response: You are right. We correct it to “To demonstrate how using the CR provides information on the aerosol radius”.
Line 109: “By calculating the aerosol extinction coefficient equivalent crosssections“
What do you mean by “extinction coefficient equivalent crosssections”? This quantity does not really exist. I guess you mean the differential scattering crosssection?
Response: Changed to “differential scattering crosssection”. Thanks.
Line 110: “Eq. (1b) can then be used to compute the aerosol number density. This method produces both consistent number density and particle size and was used by Bourassa et al. (2008b).”
If you do it this way, the number density and the size may not be consistent, because:
(a) the retrieval of the radius assumed a monomodal lognormal PSD with sigma = 1.6
(b) equation 1b assumes a monodisperse aerosol (if equation 1 b is really meant this way).
Please clarify the exact meaning of equation 1 b.
Response: We used (a) in this study. We modified the text to clarify it.
Line 126: “The second source of uncertainty comes from the assumption that our size computation is independent of the assumed width of the aerosol size distribution”
I’m not sure, how to interpret this? To me, this implies that a monodisperse PSD is assumed for equation 1b? But below you mention again that you assume a monomodal lognormal PSD?
Response: We are not using a monodisperse PSD. The σ_λ are calculated assuming a monomodal lognormal PSD with median radius of r_{m} and a fixed distribution width of s as shown in Eq (3). Since s remains constant during the calculations, we aim to evaluate the impact of varying s on retrievals, which is defined as the second source of uncertainty here.
Line 129: “In our algorithm, size can vary, and changes in the particle size may thus be inconsistent with the RTM phase function and this can be a source of error.”
Yes, ideally your retrieval should be iterative and the phase function for the extinction profile retrieval should be updated after the size retrieval.
Response: Your understanding is right. However, as you noted earlier, this is beyond the scope of this paper.
Line 147: “and found that most of the observations clustered between s = 1.4 and 1.6.”
The Wrana values are for a limited period of time and specific stratospheric conditions. For a volcanically perturbed stratosphere s will typically be smaller.
Response: You are right. We used s of 1.2 after Hunga TongaHunga Ha’apai volcano eruption. Please see Section 4.3.
Line 167: “and averaging color ratios are between 2 and 4,“
“averaged” ? Grammar doesn’t seem to be correct here.
Response: corrected.
Line 168: “Using (1b) and assuming that effective cross section is proportional to the square of the mode radius leads to a number density uncertainty of 44%.”
How good is the assumption of a quadratic dependence of the cross section on mode radius? I would expect a stronger dependence of the "differential" scattering Xsection on radius.
Response: deleted.
Equation (5): The units don't match. Is this an exact relationship or an approximation?
Response: We slightly modified the equation based on couple of references, which were added to the text. We also modified the text to use the correct formula. We believe that the modified formula is exact relationship according to the added references.
Line 190: “lead” > “leads”
Response: Fixed.
Line 193: “increases the peak of the differential size distribution”
What is the "differential" size distribution?
Response: The differential size distribution is dN/dlogr, we added this to the text.
Equation (6): I'm not sure this approach is OK. Equation 6 only works for a monomodal lognormal PSD. In your case the PSD is a gamma function. See also next comment.
Response: That is correct. We are deriving to convert the gamma distribution parameters used in the OMPS LP algorithm to monomodal /log normal parameters to apply the algorithm error estimate to our PSD retrieval. We added the word approximately to the text.
Line 204: “The resulting CR and r_m uncertainty increase to ± 1120% and ±1232%”
This means, if you double the median radius (converted from gamma to lognormal), you only get an r_m retrieval error of 12  32 %? This seems inconsistent and if correct, is probably related to the incompatibility of the gamma and lognormal PSDs.
Response: The CR uncertainty is derived using OMPS LP retrieval (Figure 5c), while the rm uncertainty is based on a lognormal distribution, which is used to derive the PSD.
Line 219: “the SAGE III/ISS CR extinction coefficient”
? What exactly does this mean? CR or extinction coefficient?
Response: It is CR. Corrected. In response to the strong opinions expressed in the community comments, we have decided to remove Section 3.1, which compared of OMPSLP PSD retrievals with SAGE III/ISS. However, we will restore this section if the reviewers disagree. Although we are responding to the comments below, they are irrelevant for the new manuscript.
Line 224: “For the SAGE III/ISS data, we use multiple profiles in the latitude range indicated, while OMPSLP measurements are selected to be near coincident with the location of the SAGE profiles.”
I don't really understand this statement? Why are the two instruments treated differently? The latitude ranges in Fig. 7 are quite narrow and all the SAGE measurements on a given day are essentially for the same latitude anyway? Are the OMPS measurements also within the latitude range given?
Response: Due to the solar occultation measurement, SAGE data is collected over a much narrower latitude range compared to OMPS. This difference leads to distinct treatment for each dataset. For Fig. 7, the OMPS measurements are within the same latitude range as SAGE.
Line 229: “are compared for four different scattering angle regimes.”
What latitude bins are used to select the OMPSLP measurements?
Response: The latitude bins are consistent with the OMPSLP measurements, as indicated in the figure subtitles. For example, in Fig. 7a, the latitude range for OMPSLP measurements is 43°N to 44°N.
Line 248: “is consistent with Bourassa et al. (2012) and Taha et al. (2021) comparison between OMPSLP and SAGE”
Please check grammar.
Response: This sentence has been deleted along with the removal of Section 3.1.
Line 257: “The total LOPC particle concentration includes particles that are too small to scatter light”
Well, also the small particles scatter radiation (even molecules do; you also measure Rayleigh scattered solar radiation with OMPSLP), but their contribution is buried under the much larger contribution of the larger particles.
Response: Thanks. We revised to “Although the total LOPC particle concentration includes particles that are too small to scatter light, it should be noted that these small particles still contribute to scattering. However, their contribution is often overshadowed by the larger particles. Thus LOPC concentrations may be higher than satellite derived concentrations where there is an abundance of CN.”
Line 297: “The regions of lower extinction and higher CR may indicate the process of aerosol formation or evaporation of larger particles.“
The different regions also correspond to different altitudes, right? By the way, it seems, it is not mentioned what altitude range has been used to produce this Figure.
Response: Tropopause to 35 km, added to caption. Yes, the distributions vary somewhat with altitude with the smaller particles at higher altitudes.
Line 309: “Figure 11c and 11d show the distribution of aerosols for a 30day period following the eruption.”
The measurements may the also be affected by ash? Why not using a later time interval?
Response: The way we plotted it clearly shows the initiation of the eruption. Large ash may be important in the first couple days, but usually falls out quickly. As noted in the text, the Raikoke aerosol particles were composed of sulfate mixed with ash, resulting in larger particles.
Line 316: “Note that extinction/radius/number density may be contaminated by icelofting”
Also by ash, Raikoke was a relatively ashrich eruption.
Response: We added ash to that sentence.
Line 326 – 329: you may also include Wrana et al. (2023) (which is listed in the reference list anyway) in the discussion.
Response: Added.
Line 335: “which results in ~23% algorithm uncertainty for“
Somewhat unclear, what “algorithm uncertainty” refers to?
Response: Revised. It means the uncertainty in retrieved radius.
Line 336: “showed that V2.1 retrievals have very little sensitivity to the assumed aerosol model errors due to the viewing geometry variations.”
Also not entirely clear, what this means. What exactly does "aerosol model" refer to?
Response: The PSD – added to text.
Line 353: “(Wrana et al., 2023)”
This paper does not deal with the HTHH eruption.
Response: The reference should be Duchamp et al. (2023). Thanks for pointing out.
Line 358: “Figure 14 shows the time series of zonal median retrieved particle radius and number density between”
Fig. 14 shows extinction coefficient and radius, not number density.
Response: Thanks. Corrected.
Line 359: “A transition from a width 1.6 before the eruption to 1.2 following the eruption is applied.”
? Why doesn't this show up in the plots? When was this change applied exactly? I don't think this is a good idea. I think this change should show up in some way in the size and number density plots.
Response: We reduced the distribution width from 1.6 to 1.2 over days 2129 in the region below 27 km – the volcanic zone. The distribution width was kept at 1.6 above 30 km and we smoothly transition the distribution width between the two altitude regions. This explanation is added to the manuscript. Because of the smooth transition, the change is not apparent in the figures.
Line 364: “The 0.4 micron peak in the median radius”
Above you mentioned that your approach does not allow retrieving radii exceeding 300 nm.
Response: The threshold should be 0.4 μm in this study. We corrected the value in the Section 2.1.
ine 364 following: I suggest discussing the results of Duchamp et al., (2023) in this context. The paper is included in the reference list, but not cited in the text.
Response: We added the following sentence to the place. “This size estimate is compatible with the retrievals by Duchamp et al. (2023) based on SAGE III/ISS measurements, which estimate the size to be near 0.4 μm in the plume, starting from 0.2 μm or less in the background.”
Line 370: “and three days (bd) days following the eruption.”
This wording is misleading. You show results for 3 individual days after the eruptions, but the sentence rather suggests that these are the results three days after the eruption. Please adjust the sentence.
Response: Revised.
Line 375: “The retrieved median radius of ~0.3 micron is consistent with Taha et al., (2022).”
Did Taha et al. (2022) also show size retrievals? Why is Duchamp et al. (2023) not mentioned here? It is listed in the reference list, but not cited.
Response: We removed that sentence and added the comparison with Duchamp et al. (2023).
Line 381: “provide” > “provides”
Response: Fixed.
Line 385: “Using the Mie code inside the SASKATRAN radiative transfer model, we show that the ratio of extinction coefficient at two wavelengths (color ratio) is independent of the number density”
This is correct, but not really shown in this paper (and not really worth mentioning). In contrast, you state several times that number density can be retrieved from the colour ratio!
Response: Revised.
Line 389: “Our algorithm follows the approach of Bourossa et al. (2008b), Rieger et al, (2018) and Wrana et al. (2021).“
Wrana used a different approach with two colour ratios. I think this is a significant difference and therefore it does not seem to be justified to claim that you use the approach of Wrana.
Response: Corrected.
Line 391: “The OMPSLP algorithm (Taha et al., 2021) assumes the same PSD for each wavelength“
?? well, the PSD is of course independent of wavelength. I don't understand this statement?
Response: We would like to explain that the median radius is fixed at each wavelength. The algorithm then iterates the aerosol concentration until the modelcomputed radiance matches the observed radiance. Consequently, the aerosol number concentration may differ at each wavelength in the OMPS aerosol product. We have rewritten this section.
Line 403: “There are three major sources of uncertainty in our radius calculation: uncertainty in the measured radiance,“
Above you did not mention the uncertainty in the radiance, but the one in the extinction coefficient, which is something different. Also, in the main text of the papers one of the three major sources of uncertainty is a different one. This should be consistent.
Response: We updated the term to 'uncertainty in measured extinction coefficient' to maintain consistency with the main text.
Line 406: “We find that the radius changes for different distribution widths can be substantial leading to nonnegligible uncertainties in median radius and derived number concentration.”
Comparing effective radii would be a good idea here.
Response: Thanks. We added a plot to Figure A4.
Line 410: “The exception appears to be the HungaTonga eruption where SAGE measurements support a smaller distribution width of 1.2 (Wrana et al., 2023)”
Wrana et al. (2023) did not study HTHA.
Response: It should be Duchamp et al. (2023). Corrected.
Figure 2: What do the large colour ratios directly above the cloud height level mean?
Response: The instrument is running out of aerosol signal at 869 nm. This is near the top of the aerosol layer so particles are small and provide little scattered radiation at the longer wavelength.
Caption Figure 5: “Scattering angles represent the range of are in the northern hemisphere”
Response: Fixed: “Scattering angles at the upper end of the range are in the Northen Hemisphere.”
Figure 9: What are the "two" lines for the OPC measurements? Different modes of the PSD? This is not mentioned, as far as I can tell.
Response: Yes. It is two modes of PSD in the CPCLOPC balloonderived measurements. We added the information to the caption.
Figures 9 and 10: a comparison of effective radii would be interesting here.
Response: We added a plot to Figure A4, which compared the radius with different distribution widths.
Figure 11: please explain the difference between “aerosols” and “aerosol plume” in the caption.
Response: Plumes are regions with high aerosol concentration as opposed to background. We added ‘e.g. volcanic events’ in the caption.
Figure 11: what altitude range do the results correspond to?
Response: ‘tropopause to 35 km’ added into caption.
References:
Bovensmann, H., Burrows, J. P., Buchwitz, M., Frerick, J., Noël, S., Rozanov, V. V., Chance, K. V., and Goede, A. P. H.: SCIAMACHY: Mission Objectives and Measurement Modes, J. Atmos. Sci., 56, 127–150, https://doi.org/10.1175/15200469(1999)056<0127:SMOAMM>2.0.CO;2, 1999.
Duchamp, C., Wrana, F., Legras, B., Sellitto, P., Belhadji, R., and von Savigny, C: Observation of the aerosol plume from the 2022 Hunga Tonga—Hunga Ha'apai eruption with SAGE III/ISS. Geophys. Res. Lett., 50, e2023GL105076. https://doi.org/10.1029/2023GL105076, 2023.
Citation: https://doi.org/10.5194/amt2023267AC3

AC3: 'Reply on RC3', Yi Wang, 23 Aug 2024
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