the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 31 Jan 2025
Influence of modes of climate variability on stratospheric gravity waves in the tropics using Radio Occultation and Reanalysis Data
Abstract. The Intertropical Convergence Zone (ITCZ) is a critical driver of tropical climate, characterized by convective activity that transfers energy, influences atmospheric circulation, and modulates precipitation. These processes generate atmospheric disturbances, making the ITCZ a significant source of stratospheric gravity waves (GWs). This study investigates the relationship between the ITCZ and stratospheric GWs, as well as the influence of climate variability modes—Madden-Julian Oscillation (MJO), El Niño–Southern Oscillation (ENSO), and Quasi-Biennial Oscillation (QBO)—on GW activity and ITCZ dynamics. Using GNSS radio occultation (RO) data from COSMIC-1, COSMIC-2, and METOP satellites (2011–2021), we derive the latitudinal positions of the ITCZ and GW potential energy (Ep) maxima via Gaussian fitting. ERA5 and NCEP reanalysis data are used to validate ITCZ positions and estimate refractivity. Results show the ITCZ migrates ~10° latitudinally, with ~5° seasonal shifts between boreal winter and summer, while its strength remains relatively stable. Stratospheric GW Ep maxima exhibit seasonal patterns similar to the ITCZ, with smaller latitudinal gaps in the Northern and Southern Hemispheres. Multilinear regression reveals significant zonal variations in the impacts of QBO, ENSO, and MJO on ITCZ position and Ep, particularly over the American, African, and Asian sectors. ENSO and MJO drive substantial negative trends in ITCZ position, Ep, and refractivity, especially in Asian and African regions. However, zonal trends in Ep maxima and ITCZ positions remain stable, likely due to consistent Gaussian peak locations. Discrepancies in ITCZ trends and refractivity values between RO, ERA5, and NCEP data are attributed to differences in resolution, coverage, and assimilation techniques. This study highlights the complex interplay between the ITCZ, GWs, and climate variability modes.
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RC1: 'Comment on egusphere-2024-4083', Anonymous Referee #1, 17 Mar 2025
In this manuscript, the authors investigate temporal trends in, and the relationship between, atmospheric refractivity, gravity wave potential energy and several climate indices over the tropics over the period 2011-2021. They use multiple datasets to do this, including radio occultation measurements and two reanalysis products.
The topic is interesting, and a very useful paper could be produced on this topic using these datasets.
Unfortunately, the presentation of the paper lets it down somewhat, as does the data treatment (or at least the description of it), and it needs significant corrective work to reach this goal.
I am sorry to be quite negative in my review, but I do genuinely believe there is an interesting story here, and I hope this review helps the authors to produce a new version of the manuscript which presents this story in the most advantageous way.
My main issues with the current manuscript are as follow:1. WRITTEN PRESENTATION
The manuscript has significant and fundamental flaws in its written presentation. It is dense, often very repetitive and as a result difficult to read and to follow. Normally this would be a minor issue easily resolved in revisions and copy-editing (which is definitely necessary, particularly for the introduction), but in this manuscript these issues are sufficiently major that they are by far the biggest weakness it has.
In particular, Section 3.3 suffers majorly in this regard, and I had to start re-reading it many times to make it through to the end, largely due to the variety of topics and extremely dry presentation of the material. This section in particular mentions the same concepts over and over, is very repetitive, and seems to lack any kind of significant narrative flow.
This is also a problem for the other sections of the paper - section 3.3 and the Introduction were the most egregious examples of this, but all sections suffer to at least some degree. I would imagine most readers would disengage well before reaching the the end. In a rewrite, I would very strongly suggest that the authors find a more concise and effective way to present the results to the reader, perhaps by merging and compressing the material down or at the very least by repeating simple concepts as often. It would also be important to present significantly more synthesis of the results - in general the text speculates heavily, but rarely draws firm mechanistic conclusions, and this is arguably a separate major weakness.
For context, the extreme density of the text in section 3.3 is the main reason for the extreme tardiness of my review, as I had to put the paper away and come back to it several times to make it through this text. I expect the same would be true for most readers.
2. METHODOLOGICAL ISSUES AND AMBIGUITIES
The manuscript also has important methodological ambiguities and issues which need addressing.
The biggest such issue is that I am unclear how the authors have corrected for the effect of equatorial Kelvin waves on their data. As they (correctly) say on line 485, these waves have similar propagation speeds to GWs, but more importantly they have very similar vertical scales, and thus they are extremely hard to filter out of 1D datasets such as GPS-RO temperatures. My biggest concern in this regard is Figure 4 - both panels shows a very strong stripe along the Equator which looks exactly how I would expect the effects of these waves to appear in the data. It's possible that the authors have corrected for this in some way, but if so the manuscript did not make clear how.
Relatedly, I have concerns about their box-based method of removing background temperatures to estimate wave perturbations. Since they use box-means, this will potentially leave large residuals at the box edges which are not due to gravity waves. Again, the data presented in Figure 4 is consistent with this being a problem - I would guess it is the cause of the strong horizontal banding seen in particularly in the northern hemisphere at ~25N and 25S in DJF and in the southern hemisphere at ~25S in JJA, which I do not believe are real features of the global GW distribution.
Setting aside these major concerns, there are also key ambiguities. For example:
- section 2.4 refers to using Gaussians to fit the ITCZ position - but does not specify what dimensions these Gaussians are applied in, or what (e.g.) their standard deviations are - it is completely ambiguous.
- in the linear regression equation (eq 6), it is unclear if the residual is time-varying. I assume it must be as otherwise it would merge with \mu, but this is not stated. Similarly, \mu is stated to represent "a constant Ep value2, but this value is not stated - is it a large fraction of the signal, or a relatively small amount? Finally, what does the dot above t_{i,j} in the first time-varying term of the equation represent? This is not specified.
- around line 184, the authors say that their QBO time series is combined from three separate sources (sondes, reanalyses and satellites). How are these datasets combined to produce a single estimate?3. CONFUSING TERMINOLOGY
The terminology used is often confusing. For example, I do not understand the sentence starting on line 299 - what are the "zonal trends of the 11-year ITCZ ...[in]... refractivity and GWs Ep"? Do the authors mean something like the variation of the trends in each variable as a function of longitude, i.e. meridional differences in the inferred trend? This is very unclear if so - the term "zonal trend" wouldn't describe this, I'm inferring this entirely from context. Same for "zonal correlation coefficients" Unfortunately, it's very hard to understand this section because I'm not clear what is being presented.
Similarly, on line 319, I cannot work out what the "zonal correlation" here is meant to mean - at first I thought it meant the correlation between the two estimates of the ITCZ latitude trend, but then it talks about small regions (e.g. the Asian monsoon area), so I don't think I've understood this.
4. FIGURE ISSUES
Several figures have major design issues. To give some examples:
- on figure 8, the vertical axis labelling is very confusing. In panel a the axis ticks are evenly spaced, but have values of [5,7,8,9,11]e-2 - clearly they are being rounded somewhere below the presented precision. Similarly, panel b has "evenly spaced" values of [-4,1,5,9,14]e-3.
- No units are provided on any vertical axes after figure 7, and all text on these figure is far too small relative to the paper's body text.
- I'm also not sure if the figures are colourblind safe. In particular, for figures 8 onwards the red and green lines look to be a very similar hue, and are often used in the same style on the same panel (e.g. figure 10). Similarly, the rainbow colour table used in Figures 3 and 4 is an issue here.I hope the above pointers give the authors some ideas on how to turn this interesting work into a better manuscript, and wish them the best of luck in doing so. There's definitely an interesting study in here!
I have some additional minor comments, which I include below. Due to the major issues above, and in particular the difficulty I had following the text in places, these should not be considered exhaustive.
L047: "studies have" - what studies?L084 mentions COSMIC-1, COSMIC-2 and MetOp, but then the rest of the paragraph is just about COSMIC-2...
L100: ERA5 is a spectral model, not a grid-based formulation - they may have processed it on a lat/lon grid, but it wasn't generated that way. Also, 37 levels is one version - the model itself runs on 137 levels.
L103: "accessible since 1940"?!? Erm...
L115: the use of 'N' for both refractivity (eq 1) and the buoyancy frequency (eq 2) is very confusing - throughout the paper I'm never entirely sure which is meant. This needs fixing.
L140: decomposed in what way?
L157: "the data series includes" - is this the satellite data, and if so by this do they mean that they have gridded it onto this scale? Furthermore, if so, what is the time dimension of this grid - is it the monthly average described a few lines after? (if so, the order of the text is confusing)
L173: I don't understand what they mean by saying that \alpha_0 "depicts the change in GW parameters over time" - if this is a standard linear regression equation, then isn't this a constant derived from your analysis? Also, line 175: what do they mean by \alpha_n "shows the relationship between the time series"?
L200: by "two tens of N units", do they mean "20 N units"? This is a really odd way of saying this!
Fig 4: it would be very useful to contextualise this figure in the broader literature of GW Ep and amplitude studies, as there are a lot of papers on this. Do the maps look normal? Are they consistent with the previous literature? If not, why not?
L202: what contour intervals? Do they mean the range of the colour scale?
L225 and 226 seem to contradict each other - they say that it "shifts 5-15 degrees north and south", but then that it's "practically similar" over an 11-year period. Presumably one of these sentences is referring to seasonal variability and the other to interannual variability, but they say explicitly that they're talking about interannual variability when talking about the 5-15 degree shift, so I am confused. Maybe they're talking about the differences between datasets? This whole paragraph needs a full rewrite for clarity.
L230: they talk about the "global oceanic areas", but as far as I can tell they're only talking about a small part of the tropics, not the whole globe? Do they mean e.g. "across the tropical Pacific"?
s3.2 - it needs making much clearer here that they've switched from talking about observations to reanalysis, currently the two are elided together quite seamlessly, but the degree to which these two types of data reflect the real Earth system is quite different, and it's important that the reader is able to keep clear track of which part is which. As a result I am completely confused in this section which data comes from where - for example, is that the RO-derived Ep, or is it a similar metric derived from the reanalyses? As a result, it is very hard for me to understand the science presented in this section.
s 3.2 I am unclear on exactly what the thematic distinction is between 3.1 and 3.2 and, in particular, why they're in this order? It seems like s3.2 is validating your ITCZ location against other datasets, but surely this belongs before they use your ITCZ for comparison to GW maps, which they did in 3.1?
Figure 7b - missing data along the prime meridian.
L280: I don't quite understand why they're defining the ITCZ after 14 pages of talking about it?
L326: there's a sudden switch here of the hPa to the mbar, which seems to be used everywhere after this. Why?
Citation: https://doi.org/10.5194/egusphere-2024-4083-RC1 -
RC2: 'Comment on egusphere-2024-4083', Anonymous Referee #2, 27 Mar 2025
In the study titled "Influence of modes of climate variability on stratospheric gravity waves in the tropics using Radio Occultation and Reanalysis Data" the authors provide a mixture of analyses of the ITCZ position (from GPS RO and reanalyses) and of the position of local maximum of the potential energy of disturbances (from GPS RO data only). For both, long-term variability and trend is assessed.
After reviewing the paper I unambiguously recommend rejection from publication in ACP for the reasons listed below (only major comments are listed, because the list of minor and technical comments would be overly extensive).
The title does not accurately reflect the content of the article.
Abstract, Introduction - Besides being poor quality and badly structured with multiple repetitions, scientific questions or hypotheses are completely missing.
In my eyes, this is the most crucial aspect of scientific articles and the fact that it is completely missing here warrants rejection.Methodology - many unclear aspects throughout the whole approach - Why refractivity is studied in the troposphere and temperature in the stratosphere, when the refractivity can be used also in the stratosphere, or one can use density which is directly related to it? - Insufficient justification of the methodology for GW induced temperature perturbations. It is not clear at all, how the background profile construction method works (the authors only state - mean temperature profile is decomposed using a continuous wavelet transform) and it is not clear whether other processes cannot contribute to the perturbations (other wave modes, overshooting convection..)
Results - the results are an incoherent flow of poorly described figures and overly descriptive text. Clearly, the absence of a scientific question makes it impossible for the authors to make this section more focused. After I finished a second reading of the text, I am still scratching my head about the motivation for the study. Namely, what is the added value of diagnosing ITCZ from GPS RO wet profiles over the reanalyses, when the wet profiles are not pure observations but also rely on assimilation of model information? Is the motivation the intention to show that dry GPS RO profile in the stratosphere can be used for ITCZ detection, because the location of maxima of GW activity in the stratosphere is perfectly collocated? But, this can never be possible with reasonable accuracy due to GWs propagating also significantly horizontally!
Discussion and Conclusions sections do not follow the required structure for ACP papers and are nothing more than a very extensive and chaotic summary of results. No new discovery or finding can be identified. As there is no hypothesis or scientific question, the conclusion cannot return to its validity. Synthesis, context and implications are missing completely as well.
I am sorry to the authors that this review is not constructive. Maybe that parts of the results can be used in a new manuscript, but first, the authors need to formulate a scientific question that would be central to the study and pertinent for the readers of ACP.
Citation: https://doi.org/10.5194/egusphere-2024-4083-RC2 -
EC1: 'Comment on egusphere-2024-4083', Farahnaz Khosrawi, 31 Mar 2025
I would like to thank both referees for reviewing the manuscript by Ayorinde et al. Having read the manuscript version published in the open discussion myself, I must say that I fully agree with the comments made by the referees.
Definitely, the major drawback of the manuscript is the poor writing and the many repetitions and missing clear structure in the manuscript. There may be an interesting story behind, but as long as this is not clearly written, I agree that the manuscript cannot be accepted for publication.
My suggestion is that the authors take the time to thoroughly rewrite their manuscript and then we have a further round of reviews. Additional time for preparing the answers to the referee comments and submitting the revised version of the manuscript is usually granted by the editorial support team without any problems, thus you can take as much time as you need for thoroughly rewriting your manuscript.
In the following I list a selection of my specific and technical comments.
Specific comments:
Title: Here the GWs are the major object of study, but in the main text it seems to be rather the ITCZ.
Introduction: Many statements are made without providing according references. As stated by the referees there is no clear structure in the introduction and many times the same is said over and over again.
L82: Section 2 header should read “Data and Methodology”.
Methods: Statements on the accuracy of the observational data is missing. For differences always the reanalysis data is blamed, but how can you be sure about this? What is the uncertainty from your analysis?
L93: This sounds like you are using only 2 months of data, but actually you are using 11 years of data.
Section 3: Should be restructured to be more concise. Consider splitting up the result section into two sections. Sections header should have clear titles. As stated by the referees it should be clearly stated what is the research question, what is the approach etc.
Figure 6 caption: Why not using for labels for the four panels. This would make the description of the figure much more concise, especially if then also is mentioned what is seen in each panel.
L272: Shouldn’t this rather be the horizontal wind which has 0 ms-1 where the convergence of the wind is found. Having a vertical velocity of 0 ms-1 would mean the air is neither moving up or down which would be contradictory to the location of the ITCZ.
Figure 7 caption: Is there a difference between vertical velocity and vertical wind velocity? Why are here different units used (Pa s-1 and m s-1)?
Figures 8 to 11 are quite similar. What is the difference between these figures?
Discussion and Conclusion: Needs to be significantly improved. What is the take home message? What impact do your results have for the scientific community.
Technical corrections:
L85: What do you mean with “(a,b,c)”? Is there a figure reference missing?
L102: and 37 pressure levels -> on 37 pressure levels
L295: reduction -> decrease
L382: vulnerable -> sensitive
L383: mildly -> weak
Citation: https://doi.org/10.5194/egusphere-2024-4083-EC1
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