Dear Authors,

You can find below the reviewers report on your updated manuscript
Both of them raise important and substantial issues to be addressed, especially for what concerns the IASI data representativity. This is a crucial issue, since this lies at the core of the paper. As mentioned these goes beyond a re-review requiring substantial revisions that I would consider again as major ones. So, I would encourage you to consider these remarks and carefully address them in a detailed answer to both reviewers and a revised manuscript.

Best regards,

Federico Fierli

Rev #1


In general, the authors have done a good job of responding to referee comments. The manuscript has been substantially revised; in fact, in some places it has been almost entirely re-written. The writing and structural flow of the manuscript have been improved. In the process of editing to address reviewer comments, the authors have articulated a new emphasis on “process-based retrieval evaluation”, whereby, unlike in more traditional validation approaches, satellite measurements are assessed qualitatively through their dynamical consistency with meteorological fields (e.g., winds, GPH). The authors stress the value of the nadir sounders’ dense horizontal sampling, but in my view what is probably the most important result from this paper --- the observational evidence supporting the conceptual model of the preferred ASM vertical transport pathway --- was enabled more by the ability of IASI to discriminate variability in the upper troposphere from that in the lower/middle troposphere than by its horizontal resolution.

Because of the extensive nature of the revisions, I have more comments on this draft than is typical for a re-review. However, the vast majority of them should be straightforward to address.

General comment:

I still object to the way the vertical information content of the nadir sounder measurements is characterized. IASI data may be reported on 19 surfaces, but as George et al. [2009] point out, the number of retrieval altitude levels is not representative of the vertical resolution. The statement is made (P5, L16-19): “Averaging kernels for layers centred at 13.5, 14.5, and 15.5 km are highlighted in the figure, because these layers are relevant to the analysis, which is focused on the 150 hPa pressure level. This level is contributed mostly by IASI CO product layer centred at 14.5 km and with a small fraction from the 13.5 km and 15.5 km layers.” I do not see the basis for this statement in Figure 1b. Layers from ~8 to ~18 km seem to contribute almost equally to the value reported at 14.5 km. That IASI cannot discriminate between 150 and 200 hPa is also clearly demonstrated in Figure 4 and accompanying discussion. Although the authors do acknowledge that IASI has maximum sensitivity in the middle troposphere (P5, L23-25), the language they employ could be misleading to many readers, especially those who do not go through the data description subsection carefully. Figure 1b shows that it is simply NOT possible to “focus on the 150 hPa level” with IASI CO data. Thus, the authors may choose to analyze the IASI measurements reported on the 14.5 km level in the data file, but those values represent an average over a broad region of the upper troposphere and cannot be labelled “IASI CO at 150 hPa”, as is done in numerous places throughout the manuscript (e.g., P6, L19; P7, L10, L13, L21, L26, L29, L32, L33; P9, L29; P10, L5, L19; P11, L28; P14, L11, L12, L15; P21, L3; P22, L2; P23, L4; P27, L1; P29, L1). A similar comment applies to IASI data “at 500 hPa” (P9, L29; P10, L7). I think it is fair to say that IASI can distinguish between the lower/middle and the upper troposphere, and that is how the data analyzed here should be referred to, not by association with a specific pressure level.

The same comment can be made for the characterization of OMI data. It is stated (P4, L35) that the “layer 18” OMI product is “comparable to the 100 hPa level”, and that the analysis focuses on “100 hPa OMI O3” data (e.g., P12, L4, L14, L33; P14, L26, L28; P32, L2, etc.). Given that the vertical resolution of OMI profiles near 100 hPa is 11-12 km [Liu et al., 2010b], such a characterization is not justified.

Although this is a significant issue, it is fundamentally a question of semantics that is easily rectified by explicitly noting that the IASI and OMI data represent averages over relatively thick (10-12 km) layers in the upper and lower/middle troposphere and appropriately labelling them as such in a consistent manner throughout the manuscript, rather than referring to them as 500, 150, or 100 hPa values.

Specific substantive comments:

* P3, L23: MLS O3 is not mentioned in this sentence, but the Livesey et al. [2008] validation paper cited for MLS CO also covered UTLS O3.

* P4, L1-2: In the MLS Data Quality Document cited here, the accuracies of the v4 CO and O3 data are given as the RSS or the sum of the ppbv/ppmv and percentage uncertainties, respectively. That is, the systematic uncertainty for 147 hPa CO should be quoted as the RSS of 26 ppbv and 30%, and for 100 hPa O3 it should be quoted as the sum of 5 ppbv + 7%. The multiplicative terms are probably not negligible even for O3, and certainly not for CO in the ASM anticyclone. In addition, it would be good to add “single-profile” in front of “precision” in these lines, since the precision is substantially improved when profiles are averaged together.

* P6, L26-31: The issues with IASI data over elevated terrain, discussed later in the manuscript, should probably be mentioned here as well as a possible factor in explaining some of the IASI/MLS differences. In addition, it might be good to clarify that the “missing data in IASI” (L27) arise because of cloud contamination.

* P7, L33-34: “… the IASI 150 hPa product is significantly contributed by the atmosphere at lower UT levels, including the 200 hPa range”. While this is no doubt true, based on Figure 1b it seems possible that some of the features seen in the IASI upper tropospheric seasonal map could have come from even lower in the atmosphere. It would be good to show the IASI JJA map for the lower/middle troposphere in Figure 4 as well. This is done for a daily map in Figure 7, but since the presence of a systematic vertical tilt in the chemical structure of the anticyclone is being argued on the basis of these seasonal maps, a plot representing the lower layer average might be illuminating.

* P8, L30: It is stated (here and in the caption to Figure 6) that daily means are calculated over the longitude range 0-220E. But the study domain was previously characterized as extending over 0-180E (P5, L6), and the Hovmoller plots only cover that hemisphere as well, so it raises the question of why the daily means are calculated over a broader region.

* P9, L12-14: A reference (Pan et al. [2016]?) would be appropriate for this mention of the modeling analysis.

* P9, L32-33: “… effective test whether the retrieval sensitivity is sufficient to resolve independent CO variability”. This statement should be qualified. The comparison represents an effective test of whether IASI’s sensitivity is sufficient to resolve independent upper and lower/middle tropospheric variability.

* P11, L9-11: The weaker CO enhancement over the Tibetan Plateau is attributed to the impact of the elevated terrain on the retrieval. However, the enhancement in Fig. 9a is weak only over part of the Plateau area -- it is relatively strong around 29-30N.

* P11, L13: “the enhanced layers are centered near 150 hPa and vertically extended between 100 and 200 hPa”. Again, IASI cannot really discriminate between these levels. Given the “smoothing error” in the retrieval, it is not possible to quantify the true vertical extent of this feature.

* P11, L12-15: I am a little confused by the discussion of CO enhancement over the Western Pacific High being associated with strong easterlies in the case of Fig. 9b (though not in the case of Fig. 9d). Here and previously (P8), this feature is attributed to eastward eddy shedding, which seems inconsistent with the presence of strong easterlies. Some elaboration of this point would be helpful.

* P12, L8: The previous work of Park et al. [2007, Fig. 9] is described as analyzing MLS 100 hPa CO, but it would be more appropriate here (in a paragraph about O3) to say that Park et al. analyzed the MLS 100 hPa CO-O3 relationship.

* P12, L10: In addition to its relatively coarse vertical resolution, it might be appropriate to mention the potential impacts of clouds and terrain on the OMI data, as discussed on P13.

* P12, L23-24: The weaker signature of in-mixing of stratospheric air in the OMI data is attributed to averaging of variable fine-scale structure in the seasonal map. But it seems to me that it is probably more related to the coarse vertical resolution of the OMI measurements, which effectively smears out the signature of this relatively shallow layer.

* P14, L9-10: The weaker correlation between IASI CO and GPH is largely attributed to the effects of elevated terrain, specifically the Tibetan Plateau, on the retrieval. But I do not believe that the relative contribution of all possible factors was quantified in this work. Couldn’t the coarser vertical resolution and cloud effects (missing data) also have played a role?

* P14, L12-13: “the IASI 150 hPa data include contributions from the level below”. Again, this wording gives the impression that a much narrower layer is influencing the IASI measurements at 150 hPa than is actually the case.

* P14, L32: It is stated that the analysis shows that IASI data have sufficient information content “to resolve upper tropospheric CO variability”. I think it would be clearer and more accurate to employ wording similar to that in the abstract (P1, L24-25). I suggest something along the lines of: “to discriminate upper tropospheric CO variability from that in the lower to middle troposphere”.

* P15, L5-6: It is stated that “Although the retrieval has fewer degrees of freedom for each profile …”. I think it would be clearer and more accurate to say “Although the retrieval has limited vertical resolution and is degraded over elevated terrain, …”.

* P26, Figure 7: Are GFS winds at 150 hPa overlaid on both the MLS and IASI upper tropospheric CO maps? I expected the wind vectors to be the same in both panels, but close examination reveals small differences. Are the meteorological fields also gridded differently (as the satellite data are)?

* P29, Figure 10: Similarly, I expected the 150 hPa GPH fields (colored contours) to be identical between Figures 6 and 10, but there are small differences between them.

Minor points of clarification and suggested wording / figure changes (leaving most typos and grammar points to the journal copy-editors):

* P2, L1: I think that “demonstrate the value of” would work better here than “advocate for the use of”

* P2, L10: “composition … displays”

* P3, L18: “variabilities” --> “variability”

* P3, L21: “weak” does not seem like the right word for “resolution”; I suggest “poor” or “coarse” here instead

* P3, L27: “for using … diagnosis” --> “to use … diagnostic”

*P4, L17: delete “works of”

* P5, L9: “no IASI retrieval product once the cloud is greater than 25% in the pixel” is somewhat awkward. I think that something like “no IASI products are available if the cloud fraction in the pixel exceeds 25%” would sound better.

* P6, L20: “rational” --> “rationale”

* P7, L35: delete “are”

* P9, L23: “is almost always referred” --> “almost always refers”

* P10, L14: I think “degraded” would work better here than “weakened”

* P10, L21: “maps” --> “values”

* P10, L34: “over the Iranian mode” --> “over the Iranian Plateau”

* P11, L9-11: “weakening” --> “degrading”

* P12, L15-16: “anticyclonic flow over the ASM” would be better as “anticyclonic flow over the ASM region” or “anticyclonic flow associated with the ASM”

* P12, L17: “interception” should be “intersection”. The same comment applies to P13, L4 and P30, L5

* P13, L5: The text states that Gaussian smoothing is applied to the 1 x 1 degree maps (i.e., OMI), but the figure caption states that smoothing is applied to all maps

* P13, L14: Just to be clear, it would be good to add “in OMI O3” after “structure”

* P13, L16-17: “the weaker vertical resolution for this potentially shallow layer in OMI may contribute” --> “the coarser vertical resolution of OMI for resolving this shallow layer may contribute”

* P13, L32: “surface elevation on retrieval” --> “surface elevation on the OMI retrieval”

* P14, L4: “limb data” --> “higher vertical resolution limb data”

* P14, L9: “the season studied” --> “the 2008 JJA season studied”

* P14, L28-29: “model-based conceptual model” --> “conceptual model”

* P20, Figure 1a: the continent outlines are hard to see. Perhaps it would help to thicken the lines, or use a different color.

* P20, Figure 1b: It would be good to add a vertical line marking the zero line.

* P26, Figure 7: please either re-draw this figure so that panel (a) is at the top, as readers expect and is the case in all other multi-panel figures in this manuscript, or simply label the bottom panel as (c) and alter the references to this figure in the text accordingly.

* P26, L4: “terrains are” --> “terrain is”

* P28, Figure 9 caption: The various overlays, which presumably represent the westerly and easterly jets, tropopause height, theta surfaces, and wind vectors, all need to be defined.

* P32, Figure 13 caption: “tropopause pressure contour” --> “tropopause pressure contour (black)”. Also, although the Tibetan Plateau is clearly marked on other figures, it is pretty hard to see here. Perhaps a different color could be used (or perhaps pink could be used for the tropopause pressure, as in Figure 11, and then black could be used for the TP).

Review #2

I carefully read and revised the new version of the study and I apologize with the authors for the long time I eventually needed. The revised version of the manuscript by Luo et al. was greatly improved in its overall quality and clarity. The questions posed by the authors are very interesting and now more clearly expressed and investigated. However, in my opinion, the authors failed to overcome the main shortages that were pointed out during the ACP discussion phase, i.e. the lack of robustness in the adopted IASI CO profiles and how they are interpreted in the paper. I share with the authors the conviction that many interesting results are shown but these results carry the lack of possibility for the reader to discern robust patterns versus artificious (i.e., induced by the retrieval with poor sensitivity) patterns in the nadir CO (and to a lesser extent in the O3) data. I feel the authors should give more importance to having a consistent and quantified quality of the adopted data in support of their aims. In their current analysis, high and low quality results are presented under uncontrolled circumstances. I cannot therefore recommend the manuscript for publication unless these significant flaws are overcome. I report here below a number of comments that I hope the authors will consider to improve their study.

GENERAL COMMENTS

As mentioned above, in my opinion, there are major flaws in the CO data quality and the way the data are interpreted that make the whole study unreliable. These are expected because CO data are used in the analysis outside the validated range, at a single layer with no consideration of the vertical resolution and with faulty data not removed from the analysis. This was pointed out in the ACPD phase by the reviewers citing relevant literature and persists. Please see the details in the previous report. I find it interesting and see no restrictions in trying to extract more information by comparing the CO data to known processes with your aim of a processed based evaluation. But then I think the data quality needs to be kept completely under control through error and information content analysis on each individual profile considered, and through sensitivity tests showing under which conditions the profile is correctly reproducing the CO in the sounded airmasses (see e.g. Fig 10 of George et al 2015 where a bump of high CO over a thick middle tropospheric layer is completely missed in the retrieved profile). In their current version, the reader cannot understand what parts of the maps are presenting real CO details and what parts are showing retrieval artefacts. This is clearly evident in the comparison of 3 month averages of Figure 3, which removing variability show clear biases e.g. over Africa, south of the anticyclone, over the Tibetan plateau and possibly elsewhere. This is possibly an effect of vertical displacement of the airmasses which are not correctly picked by the retrieved profiles, leading to 50-100% differences with MLS. There is no possibility to correctly place the CO at a km scale, so at times the CO will be at the right altitude and will be retrieved, other times not. The issue affects also the vertical cross sections shown in Figure 9 where clear agreement of the CO fields with dynamical fields are seen in some parts, unexplained changes are seen in other parts. How much, where and when the reader can trust the data is not evaluated in the study and this severely affects the analysis and conclusions.

I think the general idea of a processed-based evaluation of the nadir data is interesting and important. The results in the study are however presented as they are unexpectedly better than what the averaging kernels are showing. I feel the authors should reconcile the limited information content available with the results that are shown, the latter being in fair agreement with the 2 independent points expected in the troposphere. This information is barely given and then disregarded in the analysis (e.g. in Figure 9 reporting cross sections): the key robust message in my view should be how well the CO vertical profiles are interpolating on 1-km layers the two available independent points, and how well this can describe the real atmosphere. Unless this is made clear and brought forward in the analysis, the reader is wrongly induced to think there is far more information than what is available in the data. If the same figures were to be replicated using raster plots with 2 single cells as deep as the information content is (about 10 km each), then the image would change but the advances of the dense nadir sounding may still be visible and correct. Again, sensitivity tests would clearly show how the profiles respond to the real atmosphere giving the needed support to this study.

I appreciated the effort of the author to adopt the same period of time for CO and O3. However, I missed an even brief comparison of the results of the two targets. There are clear similarities in the deficiency of CO and O3 nadir data as compared to the MLS data in the region south of the anticyclone, and likely above the Tibetan plateau. MLS in these very large regions show even 100% more CO and O3 than the nadir data. These differences are shown both on seasonal averages and on daily data, and are therefore robust and need to be addressed. Also, if the nadir data over the Tibetan plateau is unreliable (as it is for CO and at least partly for O3), then it should be removed from the analysis or a detailed error map shown in couple with the absolute values.


DETAILS (P=page, L=line number)

Abstract: please revise as needed

P3 L 15-17: In order to support their aims, I think the authors should underline that the same (or nearby) airmasses are sounded but with different geometries that involve crossing other portions of the atmosphere. If it were not the case, then the comparison would make no sense.

L18-19: it is not the retrieval which is being evaluated but the retrieved data, which include the whole chain from measurement, through retrieval, to data manipulation. I suggest also to specify the evaluation is left at a qualitative level, i.e. no quantitative information is given on the goodness of this evaluation.

L19-20: I do not see any effort in the manuscript to relate the information content of the data to the dynamical/chemical patterns that are described. Therefore, I feel the sentence “From the remote sensing information content point of view” should be rephrased. Unless of course an analysis of the information content of the data was introduced in parallel as suggested in the first revision and still strongly recommended.

L21: to me the 10-14 km vertical resolution is poor for the aims of describing vertical resolved CO tropospheric structures, rather than “relatively weak”.

L26: why is there no attempt to improve the analysis by comparing results for CO and O3? It seems straightforward to see that shortages south of the anticyclone in the nadir-limb comparison in CO are also present in O3.

P4 L8-20: the reader should be informed that the IASI CO data is used outside the validated range (which extends up to 225 hPa in Wachter 2012 and was performed on 2 partial columns) and that the use of one point of the profile at 150 hPa is equivalent to take into account a partial column about 10 km high given the available vertical resolution. I think the study would be greatly improved if these essential details were more carefully explained and dealt with throughout the paper.

L14: I think it is necessary to add that given the 0.8-2.4 DOFS, only 1 or 2 independent partial columns can be generally extracted and the vertical profiles will be based on 1 or 2 points. The 1-km vertical grid is oversampling the available information, acting as interpolation based on the 2 independent points. This is a fundamental information for the reader and I think it needs to be correctly emphasized here and in the analyses. Again, I think the manuscript would be greatly improved by showing detailed calculation of the DOFS for the horizontal maps and vertical cross sections shown in the manuscript, possibly showing better consistency with MLS when the DOFS is higher. Having this information under control would support the strategy adopted by the authors.

P5 L15-20/Figure 1b: the averaging kernel at 14.5 km is completely overlapped with those from nearby altitudes. What do the authors mean when writing “This level is contributed mostly by IASI CO product layer centred at 14.5 km and with a small fraction from the 13.5 km and 15.5 km layers.”? Where is this information taken from? The averaging kernels are so spread that the vertical resolution (e.g. half width half maximum of the averaging kernel) is of the order 10-14 km. In fact, the plot shows that the signal at 14.5 km is almost evenly contributed by averaging kernels from 10 to 16 km and with still relevant contributions from layers below down to at least 7 km altitude. I think the sentence needs to be rephrased and the correct emphasis to what the plot is showing given here and throughout the analysis (as it is mentioned a few lines below).

L28-31: I appreciated the clarity for the usability of O3 in this study.

P6 L6-16: Wachter et al. 2012 finds very large sensitivity variations in CO between day and night and over land/ocean, with a shift of the maximum sensitivity from the low to the middle troposphere. Maybe this is affecting part of the nadir data and could help reconciling them with MLS?

L33-34: I would clearly state that this comparison is needed because the data is used beyond their validated range and with an approach that is not supported by the current literature.

P7 L5: typo: “is the strongest”  rephrase?

L9: it would be useful to specify how the “the vertical information content of IASI CO retrieval” led to use the 150 hPa level.

L11: typo: “of THE single year 2008”

L16-19/Figure 3: Considering this is a three-month average over fairly large boxes, the agreement seems to me not so good, with a broad spread showing very large differences in the dataset at uncontrolled times and locations: 50 ppbv of IASI CO can be associated to 30-100 ppbv of MLS CO, 50 ppbv in MLS CO can be seen as 50-100 ppbv in IASI. Indeed, the measurement and retrieval shortages in IASI have an impact on the spread and I think this should be quantified and its goodness tested. Would removing regions producing the significant difference seen in Figure 4 greatly improve the correlation shown in Figure 3 and its significance? If so, then it should be possible to isolate those regions, investigate the source of error and seek a method for keeping or rejecting nadir data.

L25-27/Figure 4: the comparison of seasonal averages should give the best results given that temporal and spatial sampling shortages are removed. The figure clearly shows that there are serious deficiencies that need to be investigated and isolated in order to support the analysis at shorter time scale. There are large differences which do not appear to have a simple and consistent interpretation, e.g. over Africa, south of the anticyclone, over the Tibetan plateau. Looking at a IASI CO map it is not possible to understand whether the data in one region is trustable or not. Since IASI CO at 150 hPa is picking signal from different layers, it is very likely that if high CO values are encountered at the wrong altitude the retrieved data may not show it. Showing maps of error and information content may help understanding why there is agreement in some regions and not in others.

L29-30: the blob of high CO at 120-150E in MLS at 215 hPa is very similar to that in IASI at 150 hPa. This strongly suggests IASI is picking signal from the wrong layer and there is no control on the vertical distribution as correctly shown by the averaging kernels.

L35: typo: “likely involve”

P8 L1-3: I agree. So, if there are regions where the data is so poor, then I suggest these data to be removed or marked somehow. But if this is the case for a certain region, how can one further trust the data at a more detailed level? I think these sentences in the text should be translated in careful selection of what is trustable and what is not.

L5-7: following the above comments, the comparison shows significant shortages in CO data that are not characterized nor explained. Further examples: the patch of high CO is at 60E in IASI while it is over India in MLS. How to explain the weak IASI CO at 30N/30E? MLS nicely fills the white contour. What about the high CO patch below 0N/30E in MLS? There is no sign of it in IASI CO.

P8L11-12/Figure 5: Why are the peaks in MLS CO always south of the peaks in GPH? Is it related to the tropopause interception of 100 and 105 hPa as shown for O3? A comparison of the results of the two targets may help.

L29-30: possibly rephrase? E.g., a latitude band restricted to a longitude interval. The plots are for 0-180E and not for 0-220 as written.

Figure 6: the figure is difficult to read a part from the zero lines. Fewer color levels may help promptly identifying highs and lows. Or possibly the addition of a few contour lines? Would it be possible to extend the longitude range to 20W or so in order to capture the zero-anomaly contour line in both GPH and MLS CO?

P9 L12: what model analysis are the authors referring to? Is this literature or performed within this study? Please clarify.

Figure 7: Indeed, IASI CO shows very interesting information but it is again difficult to understand what parts are robust and what not. For example, why would MLS pick signal along the 135E cross section at 150hPa that is not seen in IASI? The maximum contribution of an individual measurement in MLS comes from the tangent point (say 14 km altitude in this case) along the line of sight with a spread of a few hundred km, i.e. maximum +_2/3 degrees latitude. Moving 10 degrees latitude away from the tangent point, the line of sight crosses the atmosphere already 100 km higher. So, there is no possible contamination of nearby portion of the atmosphere at a distance of 10 degrees latitude and the MLS data must be trustable within their validated errors. Why is then IASI CO about 45 ppbv at 0-20 N along the 135E cross section where MLS is seeing 80 ppbv? This and other examples show IASI CO is picking signal but with no control on when it is placing it at the right location (see comments below for Figure 9). Even more, it seems various regions lead to persistent lower values as compared to MLS, pointing to physical conditions that affect the retrieval in the same way. Again, IASI CO above the Tibetan plateau seems completely wrong. I would recommend to remove known faulty data.

Figure 9: please add to the caption that black contour lines represent zonal winds.

Figure 9b: I see oscillations along the longitudes with vertical plumes of low and high CO (60/100 ppbv) at 750/250 hPa between 10N to 35N. The wind field does not seem to predict those. The same in other regions and figures. On the contrary other portions seem to be in very good agreement. However, in my view, the wind field may be consistent with CO fields that are different from those shown and 50-100% changes could be easily accommodated. Therefore, it is very difficult to validate the use of nadir CO through this possible agreement with dynamical fields with no further quality control. Which parts can one trust and which not? I find it essential to support these interesting findings with a thorough analysis of the information content, error budgets and sensitivity tests on the ability of the profiles to reproduce the real data and not produce artefact. It is very well known that artefacts/oscillations can be produced by retrievals under low information content conditions, which in fact usually lead to data rejection.

P10 L5-8: to me the example show two independent fields can be obtained, not whether the retrieval is reproducing the two layers correctly. Nor whether the 150 hPa is unrelated to the 250 or 300 hPa level. What is the correct altitude of those high CO values?

L13-17: because of the many flaws reported above, I think the comparison does not look convincing.

P11 L9-11: if the data is known to be of bad quality, why not removing it from the analysis?

P11 L16-19: this is likely to be the case but the study fails to have support from the missing data quality analysis: with what error? How much is real? It seems IASI CO can very likely pick strong localized CO enhancements but how it depicts them along the vertical profile is unknown. I recall George et al. 2015 Fig 10 example.

L21-22: again the results showed IASI CO is able to pick variability, not that it is able to correctly reproduce it.

L26-27: I do not agree. The results presented in this manuscript are fairly in agreement with the limited information content calculated by the retrieval and are coupled with the several shortages that were discussed. I think this work deserves to be fully supported by a detailed quantification of the goodness of the data and retrieval sensitivity tests that show how much, when and where the profiles are correctly reproducing the sensed CO.

L28-32/Figure 10: this figure shows the limited agreement of the data with a not refined spatial and temporal reproduction by IASI CO of the real atmosphere. This does not seem to be dependent only on the Tibetan plateau faulty data. I would recommend to repeat the correlation removing the Tibetan plateau to test it.

Figure 11: considering these are 3-month averages over such a broad region and that the target is the well defined O3, I think the comparison shows significant differences that need to be addressed. This is the case of Africa and the whole regions south of the anticyclone. And the Tibetan plateau as already discussed for CO. The strong disagreement south of the anticyclone was already found in CO and inter-comparison of the two targets would likely bring new insight in these shortages. Could MLS be picking stratospheric air (as seen by O3) which OMI is missing, and IASI retrieved CO be affected by this vertical displacement of stratospheric air along its line of sight? But why would MLS see more CO than IASI does?

P12 L10 please revise the conclusions accordingly with the rest. This (10-14 km) is a very poor vertical resolution for resolving the troposphere in detail, I do not see how a different claim can be made.

L17: does this also explain why peak CO is displaced south of the highest GPH in Figure 7 and following?

Dear Authors,

Reviewer 2 raises some important issues that I would encourage you to tackle in a final revised version. Below his/her statements. Kind regards

Federico Fierli

I have appreciated the efforts of the authors in responding to the reviewers, which I think helped in better defining the aims of the authors and give a more balanced presentation. As previously stated, I share with them that they present interesting ideas and results. However, I was not fully convinced by their revision and think that 1) the way their results are presented can still be misleading, and 2) they did not perform enough (and easily achievable) analysis to support their claims. I am afraid in my opinion these two issues should still be taken in consideration to fully support publication of the manuscript. The authors stressed that they show IASI retrieved data carry sufficient information to have independent variability in the lower and upper troposphere. This is evident from both maps and averaging kernels, and the new panel in Figure 1 greatly improved this by constraining most of the profiles to 1.7-2 degrees of freedom. Since better constrains were given to the available information content, I think better care should still be given to the presentation. As previously stated, the performed analysis does not leave room for understating whether this variability is correct and from what altitude it is coming from, and the qualitative comparisons performed in e.g. Fig. 3 and 4 is in my view not satisfying enough to exploit the data in detail, nor it is the comparison of Fig. 6 and 10 (Hovemoeller diagrams for MLS and IASI) where MLS show a much better agreement with GPH. I would therefore expect to stress pros and cons in a more balanced way throughout the manuscript (see e.g. abstract, and the discussion in page 7 and related text – whereas I appreciated the much more balanced text in the conclusions). This includes discussion of the 10-14 km vertical resolution (still missing in the text and misleading in Fig 9) and removal of labelling 150 hPa (or 500 hPa) layers in favor of “upper troposphere” and “lower-middle troposphere” layers. The wrong statement that the 150 hPa layer “is contributed mostly by IASI CO product layer centred at 14.5 km and with a small fraction from the 13.5 km and 15.5 km layers” (P5 L19-20) was not removed and is not supported by the averaging kernels shown in Fig. 1. Of course, also MLS have shortages, but these are known, kept under control by using validated data and, moreover, a 5 km (3 km for O3) vertical resolution and related smoothing errors are very different from IASI CO 10-14 km (10-12 km OMI O3) vertical resolution. I feel the authors’ results and ideas would be much better supported by a more balanced presentation. In my views, given the aims of the authors to show an open-minded and novel approach to explore the information content of nadir data, it remains a clear shortage not supporting their claims with available knowledge: It would be very straightforward to perform a few simulations of the retrieval under the various CO and O3 scenarios encountered in the ASM area, or to use a chemical transport model to show how CO is vertically distributed and how different layers may impact IASI “lower-middle troposphere” and “upper troposphere” layers. Because of the ambiguity in assigning the retrieved CO to the correct altitude, I think this further analysis is essential and not simply further work for the future. I therefore remain convinced that the promising ideas and results presented require further refinement to be fully supported and recommendable for publication.