Spaceborne observations of the lidar ratio of marine aerosols

Dawson, K. W.; Meskhidze, N.; Josset, D.; Gassó, S.

doi:https://doi.org/10.5194/acp-15-3241-2015

Articles | Volume 15, issue 6

https://doi.org/10.5194/acp-15-3241-2015

© Author(s) 2015. This work is distributed under
the Creative Commons Attribution 3.0 License.

https://doi.org/10.5194/acp-15-3241-2015

© Author(s) 2015. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 15, issue 6

Research article

|

23 Mar 2015

Research article |

| 23 Mar 2015

Spaceborne observations of the lidar ratio of marine aerosols

K. W. Dawson, N. Meskhidze, D. Josset, and S. Gassó

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Final revised paper (published on 23 Mar 2015)
Supplement to the final revised paper
Preprint (discussion started on 06 Jan 2014)
Supplement to the preprint

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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- Supplement

RC C10: 'Review of "A new study of sea spray optical properties from multi-sensor spaceborne observations"', Anonymous Referee #2, 21 Jan 2014
- AC C1186: 'Reply to Anonymous Referee #2', Nicholas Meskhidze, 07 Apr 2014
RC C18: 'Interactive comment on “A new study of sea spray optical properties from multi-sensor spaceborne observations” by K. W. Dawson et al. - Anonymous Referee#1', Anonymous Referee #1, 22 Jan 2014
- AC C1185: 'Reply to Anonymous Referee #1', Nicholas Meskhidze, 07 Apr 2014
SC C220: 'a lidarist's perspective', Matthias Tesche, 27 Feb 2014
- AC C1187: 'Response to the comments provided by M. Tesche', Nicholas Meskhidze, 07 Apr 2014

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

AR by Nicholas Meskhidze on behalf of the Authors (07 Apr 2014) Author's response Manuscript

ED: Referee Nomination & Report Request started (22 Apr 2014) by Craig McNeil

RR by Anonymous Referee #2 (01 May 2014)

Suggestions for revision or reasons for rejection

In this paper, "A new method deriving sea spray optical properties from multi-sensor spaceborne observations", the authors determine the lidar ratio of sea salt aerosol using the SODA derived AOD and integrated attenuated backscatter from CALIOP. Spatial variations in lidar ratio are discussed and an inverse relationship with wind speed found. The results suggest that a globally constant lidar ratio is not suitable for sea salt extinction retrieval and this method could be applied to other aerosol types also.

The manuscript is set out well the language adequate. The findings are clear and the previous literature well represented. Below are some minor comments to be addressed, including an important one on the clarification of the SODA AOD retrieval validation.

pg3 ln11 - replace 'although' with 'however'

Please revise:
Other techniques like the inversion of AERONET radiometer data (Holben et al., 1998) along with Mie theory can also provide the lidar ratio (the supplementary Table S1 summarizes available methods to retrieve the lidar ratio). A more complete list can be found elsewhere (Cattrall et al., 2005; Smirnov et al., 2001).
to:
Other techniques like the inversion of AERONET radiometer data (Holben et al., 1998) along with Mie theory can also provide the lidar ratio. The supplementary Table S1 summarizes available methods to retrieve the lidar ratio and a more complete list can be found elsewhere (Cattrall et al., 2005; Smirnov et al., 2001).

pg7 ln22 - symbol error and the sentence is confusing, repeating integrated attenuatted backscatter with different criteria. Please revise.

pg11 ln 31 - replace 'easy' with 'simple'

pg13 ln24 & 29 symbol error

pg14 ln7 - Josset et al. (2008, 2010) show good agreement of the AOD with MODIS at tropical latitudes and for optical depths ranging from clean to polluted. It would be better to characterize the agreement for the conditions and locations that you are considering. It is recommended that the statistics be included for a more relevant subset of the data in Josset et al. (2010) if possible, otherwise the constraints of the evaluation should be stated explicitly.

+/- symbol errors in table S1

Please revise this sentence (in Table S1) to better define 'aerosol return':
Cabannes scattering broadens the molecular scattering channel with the tails removed by a narrow bandwidth iodine filter that only passes the aerosol return.

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RR by Matthias Tesche (15 Aug 2014)

ED: Reconsider after major revisions (15 Aug 2014) by Craig McNeil

AR by Nicholas Meskhidze on behalf of the Authors (26 Aug 2014) Author's response

ED: Referee Nomination & Report Request started (29 Aug 2014) by Craig McNeil

RR by Matthias Tesche (01 Sep 2014)

Suggestions for revision or reasons for rejection

As I stated from the start, I think that the authors present a very interesting idea. However, the results are not convincing to a reader with a background in lidar and measurements of aerosol optical properties. This is mainly due to a lack of a proper critical discussion of the results (I gave many suggestions on what could be done). I therefore suggest rejection of the manuscript.

The authors did not introduce real changes to the manuscript. The answer to my review mainly deals with few minor comments (use name “marine aerosol” instead of “sea spray aerosol”, change title, omit redundant text) instead of a proper point-by-point answer to all comments (http://www.atmospheric-chemistry-and-physics.net/review/review_process_and_interactive_public_discussion.html). Therefore and because changes to the manuscript have not been marked and are hard to find, I assume that the major issues I raised in my reviews have not been addressed.

The generic statements in the answers to my review suggest that the authors are unwilling to commit any real work to improving the manuscript:

- “SODA output has been successfully compared with MODIS, HSRL and POLDER.” – I addressed this point in my last review. The authors did not answer to my concerns.

- “ Additionally, because of its reliability and ease of use, SODA operational output is now a freely distributed science product used by many investigators.” – This is circular thinking. I would argue that people will use whatever is freely available – regardless of reliability

- “Nevertheless, as wind speed dependence of marine aerosol S_p is of considerable interest for the remote sensing community” – How did the author come up with this conclusion? As I stated before, critical assessment of the presented data does not support the conclusion of a wind-speed dependence.

- “SODA comparison with maritime aerosol network (MAN) data for our time period within 60 km radius results in 13 matched data points, which are too few for a useful comparison.” – Why would the authors restrict the time period for validation of their findings to the time period considered in this paper?

The added evaluation of SODA AOT for marine aerosol is unconvincing. Figure 6 clearly shows three clusters of data: from 0.00 to 0.12, from 0.14 to 0.2, and from 0.24 to 0.30. Without information on

(1) the location of the measurements (most HSRL observations over water took place in the Caribbean, the Gulf of Mexico, or off the coast of the Eastern US; see Figure 1 of Burton et al.; 2012, doi:10.5194/amt-5-73-2012) and

(2) the lidar-based aerosol classification which easily reveals if a scene only consists of marine aerosols

there is no evidence that all the points considered in the new figure actually represent marine aerosol. As I elaborated in my previous comments, observations show that marine AOT hardly exceeds 0.10. As I still don’t see evidence for the reliability of the SODA AOT for marine aerosol, I don’t believe the authors that the subsequently derived parameter lidar ratio can be obtained with an accuracy of less than 50% as stated in the manuscript.

As I stated before, I find it unacceptable that the authors don’t see the need to verify their findings with actual measurement data or put them critically into the context of adequate literature. Direct RL and HSRL measurements of the lidar ratio of marine aerosol are still marginalized and dumped in the attachment. Instead, it is stated: “A suite of directly measured marine lidar ratios reports values on average, 29±5 (Cattrall et al., 2005). Other techniques like the inversion of AERONET sun photometer data (Holben et al., 1998) along with Mie theory can also provide the lidar ratio.” (Page 4, line 21)

This is what is actually written in the first two sentences of the Abstract of the paper of Cattrall et al. (2005): “The lidar (extinction-to-backscatter) ratios at 0.55 and 1.02 μm and the spectral lidar, extinction, and backscatter ratios of climatically relevant aerosol species are computed on the basis of selected retrievals of aerosol properties from 26 Aerosol Robotic Network (AERONET) sites across the globe. The values, obtained indirectly from sky radiance and solar transmittance measurements, agree very well with values from direct observations.

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ED: Reconsider after major revisions (18 Sep 2014) by Craig McNeil

AR by Nicholas Meskhidze on behalf of the Authors (25 Sep 2014) Author's response Manuscript

ED: Referee Nomination & Report Request started (02 Oct 2014) by Craig McNeil

RR by Anonymous Referee #4 (14 Oct 2014)

Suggestions for revision or reasons for rejection

After reading the revised manuscript and stages of peer-review, I agree with many points by reviewer M. Tesche – the work is useful but some more needs to be done, largely along the lines suggested by that reviewer, to demonstrate that the conclusions are robust. I therefore recommend further revisions, after which I think this can be a valuable contribution to ACP.

There is one area where I wonder if Tesche has misunderstood, and the authors could reword to make sure others don’t have the same issue, which is the Cattrall et al. (2005) reference. On first reading, I also thought this was wrong. The authors reference Cattrall et al. (2005) in the context of direct measurements of lidar ratio, while the study is not direct measurements but models based on AERONET inversions. However Cattrall et al. (2005) do also include a table of results from field campaigns which were (I think) direct measurements. I think that table is what the authors mean by ‘direct measurements’, not the Cattrall analysis itself. So the authors should be careful how they reference this study, to make sure people don’t get the wrong impression.

I also feel it’s important to point out the limitations of the AERONET estimates of lidar ratio; it is a calculated value based on an inversion (i.e. a retrieval result). It is sensitive to both coarse mode size but also fine/coarse partition, so there are several effects to disentangle. This links into points Tesche raises about error and the conclusions of the analysis. I have some more suggestions about this below. But, as Tesche notes, I think it’s important to be more explicit about the limitations of these indirect measurements, as others may not be aware of them.

For the SODA data, based on the HSRL comparison, the authors state that for AOD > 0.05 the lidar ratio uncertainty should be <50%. What fraction of the data used for the main study are for AOD < 0.05? From Figure 3 it is hard to tell because these are scatter plots not scatter density plots, but it looks like there are a lot of points there, especially at lower wind speeds. And from Figure 6 I think saying ‘Additionally, Fig. 6b illustrates that the relative uncertainty in the SODA retrieved Sp is less than 50% for AODs > 0.05’ is misleading because it could be understood as an upper bound; it might be better to say a ‘typical uncertainty of order 50%’ because there are a whole bunch of points with errors approaching 100% for AOD in the range 0.05-0.1.

I partially agree with Tesche’s comments on the scatter plot of SODA AOD vs. HSRL. The authors should color-code points in some way to indicate where they were taken, and/or the aerosol type. I would imagine that the type-dependence of SODA AOD validation is weak but we don’t know unless we can see the data. Also, as well as R2, the RMS error and also any bias would more useful (as they will alias into scatter and bias in the lidar ratios too).

In their response the authors point out only 13 coincidences with the Maritime Aerosol Network and say this is not enough to validate the SODA method. I think this data would still be valuable to include, even if only 13 points, as another point of comparison. In fact the small data volume might be an advantage in some ways because if there is some point which matches very well or very poorly it is easy to identify and dig into the data to figure out why. This would be a good backup to the current evaluation against HSRL.

As the reviewers and authors note, there are some spurious regions in Figures 1 and 2 (e.g. Asian coastlines, but also off the west coast of South America, which might be sulfate from mines, and Australia, in some seasons) where the AOD and lidar ratio are elevated, which are probably not marine aerosol cases. I suspect this will affect some things like the PDFs of lidar ratio in Figure 4, and the whole analysis based on wind speed. I therefore suggest that the authors make some further data cut to be more confident that they are looking at marine aerosols, and redo the relevant later analyses based on that. Perhaps take some large boxes over parts of the open oceans, and exclude the data in these coastal regions. That would make the results more convincing, and if these coastal cases were spurious non-marine data, I expect it would bring out any marine signal in the remainder more clearly.

Figure 3: This should be redrawn as a scatter density plot for clarity. Also, the least-squares results should be removed because this technique is not mathematically appropriate for finding regression relationships for this type of data (even though people do it a lot). This is because errors are not Gaussian (in low-AOD conditions the error distribution is truncated because AOD cannot be negative), because both datasets have non-negligible error (least squares regression assumes the x-axis data are ‘correct’), and because the error is AOD-dependent (so treating all points equally is not appropriate). Just plotting a 1:1 line over a scatter density histogram would be clearer to see the main point of the figure, and less statistically problematic.

Figure S2: This should really be in the paper, not in the supplement. People often don’t read supplements, and it is a plot on which a lot of discussion rests. I expect it may look a bit different if the coastal regions are excluded, but really it highlights some of the issues Tesche and I have. For example, the wind speed distribution has very few low or high values (see also Table 2) and yet these are the wind bins which will have the strongest influence on the linear fit because they are the extrema. And, especially for wind speeds < 5 m/s, many of the bin medians and means lie quite far from the 95% confidence interval of the linear fit. This is clear evidence that the linear model or error estimate on it are not appropriate (perhaps the true model is not linear, the data are not independent of each other, error characteristics of the data are different between low-wind and high-wind conditions, etc). One way to (partially) deal with this would be to chop the data into e.g. 10 equally-populated bins, and do the regression along that wind speed range.

Further, one can draw a roughly flat line through this shaded confidence interval from 0 m/s to about 10 m/s, or about 5 m/s to 15 m/s; either way this is saying that any real change in lidar ratio with wind speed over this data range cannot be distinguished from zero with 95% confidence. So the authors should be careful not to overstate their finding. Perhaps excluding the coastal outliers will help with this.

I am also curious, if the authors attempt a direct correlation between raw (i.e. unbinned) lidar ratio and wind speed, what is the value of R^2? If it is very low then perhaps it would be better to look at one or two parameters which are explaining a higher proportion of the variance in the lidar ratio instead (this kind of echoes Tesche’s statement about the utility of this part of the analysis). Or at least make an estimate of the variance in the lidar ratio caused by their retrieval uncertainty, if possible how much is random vs. systematic, and how this compares to the wind-induced variability. I am not yet convinced that the results are not entirely spurious here. For example higher wind means higher AOD (on average), and so lower uncertainty on lidar ratio. This may in part be the cause of the wide distribution in lidar ratio in Figures 4 and S2 in low-wind conditions. So if a lot of the error in low-wind conditions is systematic and not random, it is possible all we are seeing in this wind analysis is the difference between some positive bias in low-wind conditions, and smaller errors in high-wind conditions. Or it could be that coastal regions with lower wind speed also have contamination from non-marine (continental) aerosol sources which have higher lidar ratios. Or it could be a combination of these factors. It seems like a bit of a waste if the authors do not dig into this more deeply.

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ED: Reconsider after major revisions (06 Nov 2014) by Craig McNeil

AR by Nicholas Meskhidze on behalf of the Authors (27 Jan 2015) Author's response Manuscript

ED: Referee Nomination & Report Request started (30 Jan 2015) by Craig McNeil

RR by Anonymous Referee #4 (02 Feb 2015)

Suggestions for revision or reasons for rejection

I reviewed a previous version of the manuscript. In this revision, the authors have addressed most of my concerns, which were largely about data selection and the robustness of some statistical analyses.

However, I still feel that the aspect about wind speed dependence was not addressed entirely adequately. The authors acknowledge (in their response to reviewers) that their linear fit of lidar ratio to wind speed is suspect, particularly at the extrema, but rationalize it by saying that if they delete the extrema they do not see a statistically significant relationship. Well, this sort of thing is exactly why one must be careful with the conclusions that are being drawn from a statistical analysis. Keeping in questionable data points to force a result to be statistically significant is not scientifically sound, particularly when it’s clear from the data (as in this case) that the technique employed was not appropriate. The authors have de-emphasized this linear wind/lidar ratio relationship in the text of their revised manuscript. I would also suggest going further and deleting Figure S2 (the linear fit) because (as discussed) it is not statistically meaningful or useful. Presenting an unsound analysis does not help and may even help to legitimize bad statistics by other researchers. The PDFs in Figure 4 are sufficient for the purpose of looking at the relationship, as they reflect the shift in peak and width of the lidar ratio distribution without trying to impose a regression, and so are more honest about the underlying data.

My preference remains to move the rest of the supplement into the body text as well, because the paper is not too long, and things in supplements often get overlooked. For example the sampling aspect as shown in Figure S1 is something which deserves more prominence, as discussed in the reviews.

In my view, once those points are addressed, the manuscript is suitable for publication. I would encourage the journal to solicit another review from M. Tesche, if they have not already, who may be better placed to provide a review on some of the more lidar-specific technical points.

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ED: Reconsider after minor revisions (Editor review) (18 Feb 2015) by Craig McNeil

AR by Nicholas Meskhidze on behalf of the Authors (23 Feb 2015) Author's response

ED: Publish subject to technical corrections (26 Feb 2015) by Craig McNeil

AR by Nicholas Meskhidze on behalf of the Authors (27 Feb 2015) Manuscript

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