Dear authors,

Thank you for your revised manuscript; I have now received two reviews from referees who had also assessed the initial submission. I am sorry for the longer than normal time for receipt of these reviews, due to challenges faced by all of us during the current pandemic.

One of the reviewer criticisms of the original work was limited scope: a post-retrieval correction to an operational retrieval scheme, rather than an improvement to the algorithm, or something which could be applied more broadly. Although I understand from an operational point of view why this would be done, reviewers questioned whether this is something which warrants a journal publication, or would be better served as a technical report. One reviewer feels the same about the revised version, as the level of technical detail doesn’t provide a direct path to broader applicability or to improving the algorithm in the future. I lean in this direction. The bias correction is in essence a quadratic fit to AOD compared to a reference point taken as unbiased. That is not a particularly detailed approach: it’s great it works, but that doesn’t mean it’s got enough broad interest, applicability, or detailed physics shown for a publication. The reviewer’s comments are reproduced here:

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“For the sake of brevity, I will address the first response of the author as I think the other questions are more technical and not so defining of the nature of this study.

The issue I raise is that I see very little value in a study that limits itself to obtain a correction without addressing the underlaying causes. This study provides a fix to a remotely sensed product using a methodology that seems to work but does not shed any meaningful light on nature of the problem causing the discrepancies first noted. While the methodology seems reasonable, the study does not stand out above a technical report offering a nudge to fix to an operational product.

I acknowledge that in an operational setting and near real time situations, speed is important and as long as the end product is satisfactory, ends justify the means to achieve the desired result. However, for scientific applications the correspondence between end product (in this case AOD) and connection with the physical process in the modeled retrieval is essential. This is the weakness of this study and it fails to make the point why this is of scientific interest if there are not causative demonstrations of the problem such as radiative transfer study, exploration of different surface databases or comparisons with other satellites. As written this study reads as technical report addressing a correction needed because the end product does not match well with independent observations.

In the rebuttal, authors suggest similar approaches have been reported but the examples provided are not convincing. The Lary et al(2009) study is one the first AI papers using MODIS aerosol observations and it is already more than 10 years old. Yet it has not resulted in corrections currently implemented anywhere in the MODIS (and other sensors to my knowledge) algorithms. The Gupta et al (2016) from the MODIS DT group restricts its applicability to very specific scenes where there are very clear and well-defined algorithm deficiencies. The corrections reported in Gupta et al (2016) study are only applicable to those conditions (urban areas). In contrast, the study under consideration here has a much larger scope (whole continental USA) with no much discussions of specifics of the scenes under considerations. In comparison with Gupta et al (2016), this study does not show the same level of detailed and specific analysis. Overall, in one case, the correction provided did not seem to have any meaningful impact or correction in the final product and in the other case, the corrections developed were well defined where they should be applied and it did result in a modified algorithm when those conditions happened.

Overall, if the goal is a proposed methodology that it can be used elsewhere (other sensors, other algorithms) , this study can be of value even there is no addressing of the core surface reflectance problem. However, if this was the case, the authors should expand the methodology and demonstrate that it is usable in other settings/sensors/algorithms. This study as it is now is a well explained report on how an ad-hoc correction was derived and demonstrated to achieve its objective in correcting the differences observed.

Given the nature of this journal with its emphasis on operational and algorithmic atmospheric studies, I think this manuscript is border line with regards to publication. But ultimately, I think this should be an Editorial decision.”
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I also note that the Gupta et al (2016) paper mentioned has resulted in algorithmic updates to the algorithm in question there (MODIS Dark Target aerosols) – an algorithm change to the surface reflectance model, not a post-processing bias correction to the retrieval output (as in this manuscript).

Line 430 says that the data processed using the correction algorithm are available from the author. But my impression from the paper is that this was being done in real-time as a correction to the operational product (i.e. one can get these retrievals now through the standard data server)? Is this not the case? If not, then my suggestion is to withdraw this paper and include some of this material in a follow-up improved algorithm paper; you note in your Response to Reviewers that “Improving the spectral surface reflectance relationships is the subject of an independent, parallel work, and thus it is not discussed in the current paper”. However for me that the most interesting part is identifying the cause of the bias (which is partially discussed here) and fixing it (which is stated to be TBD). Either that or work on making the bias correction even better.

If this IS being implemented in the operational product (or will be within the coming month or so), a second path forward would be to expand the parts covering the existing surface model and showing why it is the main problem, as well as expanding the validation analysis with more (spatial) results to make this more informative for data users. I note that you added some additional material to the revised manuscript, and appreciate those efforts, but think that more would be needed. Some comments and suggestions from me are below:

The paper notes that the surface reflectance relationship is a function of NDVI and solar zenith angle, yet there is a clear solar angle dependent bias in the AOD retrievals at some of the sites shown in Figure 1. I went to the GOES-R ATBD cited as the source of these relationships and it says that they were empirical based on collocated ABI and AERONET data. However the ATBD does not show these relationships. So one good way to expand the paper would be to show these relationships and then also look at whether the scatter around the relationships in the training data set shows systematic behaviour as a function of e.g. view zenith or scattering angle. Adding this sort of material could better support the conclusion that it is the surface model which is the main problem here. Figure 6 shows that the errors in AOD are a function of scattering angle but the paper is missing the link that it is surface that’s the biggest component. I think we need to see the training data, and ideally retrieval simulations where a known surface error is introduced.

It also raises the question of why this relationship was used in the orginal algorithm? The study cites the MODIS Dark Target over-land AOD algorithm as a source of some assumptions; that algorithm parametrizes surface as a function of scattering angle rather than solar zenith angle. And we know that in the single-scatter limit, both aerosol and surface reflection are more directly linked to scattering angle than solar zenith. So some more background on the reason for choosing solar zenith angle would be useful (e.g. show the simulations indicating why this decision was made). Line 170 indicates that the training was done before the satellite was moved to its current position; however, again, to my knowledge this movement was planned and doing the calculating in terms of scattering angle may have meant that these coefficients would still remain useful for the new position.

The paper mentions MODIS and VIIRS AOD algorithms a lot (as there is some commonality between themand ABI). Yhis is mostly talking about NASA MODIS Dark Target and NOAA VIIRS (as opposed to e.g. NASA VIIRS Dark Target and Deep Blue). This should be made clearer. Maybe we need a statement early on saying that references to VIIRS mean NOAA algorithms.

Line 53: MODIS Atmospheres Collection 6 onwards is both 3 km and 10 km. This is also a place where it should be specified that it is NOAA VIIRS data, as NASA VIIRS is 6 km.

Line 122: this is a bit misleading: AERONET provides a subset of those wavelengths (dependent on instrument), not all of them.

Line 127: I understand there is a delay of up to a year or so between AERONET level 1.5 and level 2 data. However it seems that level 2 should be available by now for the study period, so these ideally should be used . I am also not sure about the statement that level 1.5 has a “bias” of 0.02. It looks like this was taken from the Abstract of the Giles paper cited here. But the relevant passage of that paper is more nuanced: “Therefore, the quality of the Level 1.5 near-real-time AOD changes with time with high-quality data at the start of the deployment but up to a +0.02 bias and 0.02 uncertainty for data collected more than 1.5 years since pre-field calibration.” The conclusions to that paper also note “up to” 0.02. I am not sure why the Abstract to that paper omits “up to”.

Section 4: As I understand it, the bias correction is representing the AOD error as two quadratic functions of time of day (split by whether the Sun is east or west of the sensor), fit based on the difference between retrieved AOD and that from a 30-day minimum retrieved AOD (on a timestep basis), also subtracting a background AOD from AERONET (taken as 0.025). The flow chart here is useful but I think it would be good to have an example showing actual data, perhaps for one of the cases shown in Figure 1.

Since it is known that negative AOD is unphysical (but permitted in the retrieval), wouldn’t it make sense for the bias correction here to also set negative AOD to zero? My understanding is that this is an inherited assumption from MODIS Dark Target retrievals which causes a few issues and misunderstandings for some users.

Line 277: If the retrieval is being done every 5 minutes, I don’t think it makes sense to average the AERONET data in an hour around the time. If there is real AERONET variation, it would be smoothed out by this averaging. Why not compare with the AERONET measurements directly associated with each time step? I understand this choice was the same as the done for earlier VIIRS analyses, but as pointed out in this paper, polar and geostationary are quite different sampling types. Or are the ABI retrievals also being averaged to hour time steps? This was not clear. It would be better to match up without distorting the sampling too much.

Line 356: Wallops may be rural but the 27.5 km circle around it includes a large amount of coastal areas, as well as small towns, so I am not sure I agree fully with the statement about favourability.

Section 5: it would be good to have some maps of site-specific validation metrics for the “before” and “bias-corrected” cases, as well as some maps (maybe a seasonal composite?) of ABI AOD for certain times of the day. Continental all-sites metrics hide this information. This would give the reader a sense of how big the differences are, and how much performance has improved. While the examples shown are useful, it’s hard to know how representative they are, or how much retrievals change in those parts of CONUS away from AERONET sites.

Figures 1, 8: the presentation here needs to be improved – at least site names should be shown on panels, not only in the Figure 1 caption.

Figure 5: the regression fits should be removed from this Figure, as these data violate the assumptions required for ordinary least squares to give unbiased, robust results. I think the 1:1 line and red points get the main message across anyway.

Figure 12: I don’t think the brief PM bit really fits here. Yes, the correlation is increased but we don’t always expect them to be correlated. The regression comments from earlier also apply here. I suggest removing this. If the authors want to note that better AOD can help downstream derived products like air quality forecasting, I think it’s fine to just say that.

Please let me know if you have any questions or want to further discuss how to proceed here. I am sorry that this is not the decision letter that you hoped for, and for the longer-than-normal review period.

Best wishes,

Andrew

Dear authors,

Thank you for your further revision. I appreciate the effort you have put in adding the new aspects to the analysis in this version. After a careful read through this latest version and your Response to Reviewers, in my view this satisfies the concerns about broader level of interest/novelty raised by one reviewer and myself. I will therefore be pleased to accept your study for publication in AMT, pending the correction of a small number of remaining minor issues I noted in my latest read-through. These are below:

1. Line 79: I suggest moving the formal NDVI definition from the new section 6 to here, since this is the first time NDVI is discussed in the context of the ABI algorithm.

2. Line 131: “Angstrom” should read “Ångström”.

3. Line 171: I think this should be “in the surface reflectance model” rather than “in surface reflectance retrievals”

4. Line 236: I would delete “the” in front of “reflectance space” and “AOD space”.

5. Line 291: this section is quite long and would be more readable if some subsection breaks were added. Perhaps these could be “5.1 Application to NOAA ABI data”, “5.2 Application to Dark Target ABI data”, “5.3 Impact on particulate matter estimation” or similar?

6. Line 370: Figure 10 stands alone and feels a bit odd as a paragraph in between discussions of specific AERONET sites. I suggest moving this text and Figure slightly earlier, to line 350 where Figure 9 is currently introduced. This means that Figures 9 and 10 will switch numbers in the paper. I think that would fit better because you then go from analyzing results in aggregate (e.g. overall stats, error vs. angle and vs. AOD, consistency of times of day) to site-specific discussions.

7. Line 443: I would add a citation to a Dark Target geostationary paper again here, e.g. Gupta (2019) as used before, for the reader’s convenience.

8. Section 6: I appreciate this new material although think it could be organized a bit more clearly. I suggest creating subheadings 6.1 and 6.2, detailing (1) the coefficient fitting and (2) the use of 6SV to generate and analyze the radiative transfer simulated retrievals.

9. Line 499: the notation p0.47[p0.64] is not ideal here: I understand what you mean, but a less familiar reader might not, and the notation used mentioning both wavelengths is nonstandard. I think this would be better writing separate equations for each of p0.47 and p0.64, and likewise defining coefficients c1-c8.

10. Line 504: Should this say the “coefficients” rather than the “equations” are obtained?

11. Line 543: I recommend replacing the word “prove” with “show” because I feel “prove” is too strong (and you do not prove it in a mathematical sense here, you show it empirically).

12. Figure 7: I suggest adding a horizontal line along AOD=0 here (similar to how it is in Figure 8), which will help the reader see the overall sign and magnitude of bias.

13. Figure 9: there is a site in northern Texas (I believe it is NEON_CLBJ) where the bias correction decreases correlation, increases bias, and makes little change to RMSE. This site’s description indicates it is surrounded by mixed forest and grassland (https://aeronet.gsfc.nasa.gov/new_web/photo_db_v3/NEON_CLBJ.html). I recommend looking into what happened here and see if some explanation is forthcoming. I’m not sure, for example, if retrievals did get worse or there is simply a low data volume here and there is therefore a large uncertainty on these summary statistical metrics. If not already done, sites with a low number of matchups might be excluded from the analysis. I noted a similar degradation in the site in Utah as well.

14. Figure 10: I notice the AOD changes between left and right not only over land, but over water as well. Was the same bias correction applied over water? This would seem inappropriate, since the discussion about the approach is restricted to land scenes, and the retrieval approach and surface reflectance uncertainties are different over water. This was not discussed in the text, as far as I can tell. Further, there was no discussion of whether the water retrievals suffered from biases, or analysis of whether the uncertainties were improved using the bias correction. If application over water was an error, then I would suggest updating this figure, or possibly masking out the water locations to avoid confusing the reader. If the application over water was intentional then this really needs to be discussed (and justified and analyzed in the same way) in more detail in the paper.

I expect being able to accept the next iteration of the manuscript for publication. Please let me know if you have any questions.

Best wishes,

Andrew

Dear authors,

Thank you for submitting this further revision of your manuscript. I have read through in detail and accept this version for publication in AMT. I appreciate the additional materials added and reorganisation through the several revisions of the study, which I feel strengthened the paper and expanded its scope and interest for the journal's readers.

Best wishes,

Andrew