The revised version of the manuscript entitled "Calculating the vertical column density of O4 from surface values of pressure, temperature and relative humidity" does address most of the reviewers comments or, where the authors disagree, they give arguments for not changing, just as they state in their answer.
In terms of structure, the manuscript improved and is now easier to follow. Adding references to specific equations and subsections in the appendix also makes it easier to follow.
In terms of validation datasets, two of the three datasets increased greatly in number of measurements compared to the original submission. I also acknowledge the extra section on temperature inversions, however, I think it is misleading to exclude temperature inversions from the analysis and urge the authors to re-include them in the analysis to reflect fairly the ability and shortcomings of the proposed method since temperature inversions cannot be detected from just measuring the surface values of temperature, pressure and relative humidity and hence their results could be unfairly biased to better values when intentionally taking out temperature inversions from the comparisons in Sect 5. Likewise, I urge the authors to use a different day for the ECMWF dataset in Sect.5 than the day which was used for the fit.
I mostly checked the new submission with track changes i.e. document amt-2021-213-author_response-version1.pdf. However, I see now that there are actually differences between that version and what was submitted as a new version, likely exclusively attributable to latex issues with the diff package [and hence nothing the authors could influence]. See for example page 11 (page 32) in the former document, last sentence of Sect. 3.2 "For further details see Appendix B0.1 and B0.1" and compare this with the last sentence of the document which was submitted as new version as amt-2021-213-manuscript-version2.pdf (page 9): "For further details see Appendix B1.2 and B1.3". Please ignore comments that refer to non-existing sections or multiple figure numbers if you find them correct in the not-track changed version. Line numbers below refer to the track changed version.
(1) Since the authors only consider in their validation daytime VCDs (see also Sect. 3, especially lines 209- 212), the title should reflect this limitation. Please add this to the title accordingly.
(2) Regarding following the AMT guidelines:
(a) I disagree with the authors that the use of "quantity/ unit" in axes labels and table headings is only a recommendation. I have also never "noted" that it is only a recommendation either. Please read carefully the AMT author guidelines (https://www.atmospheric-measurement-techniques.net/submission.html#math):
"
In addition, the SI and IUPAC recommendations should be followed:
SI brochure
IUPAC Green Book, 3rd edition
IUPAC Gold Book
"
Collins dictionary says about the use of the word "should" (https://www.collinsdictionary.com/dictionary/english/should #2) :
"
You use should to give someone an order to do something, or to report an official order.
All visitors should register with the British Embassy.
The European Commission ruled that the company should pay back tens of millions of pounds.
"
Hence, it is more an obligation than a recommendation to follow the guidelines (or recommendations) of the SI brochure and the green/ gold book. The point is that AMT uses "should be followed" not "it is recommended to follow" or "authors are encouraged to follow".
(b) The argument that the authors give " Thus we prefer to provide units in brackets in figure axis, which is also commonly done in most of recently published AMT papers", is not a valid argument for the validity of their choice; it is merely a statement about the state of quality control at AMT regarding their own guidelines.
(c) Even if following the guidelines of the green book and the SI brochure were just a recommendation:
Who will follow these guidelines, if not even the chief editor of the journal which publishes these guidelines/ recommendations follows them? People in power should set good examples and follow (at least their own) recommendations, otherwise recommendations do not make any sense and could be removed all together.
(d) There are good reasons why AMT refers to the SI brochure and the green book. For a motivation for these guidelines, check out the preface of the green book, where it reads on page IX:
"The purpose of this manual is to improve the exchange of scientific information among the readers in different disciplines and across different nations"
Including the unit in round brackets in an axis label (or table heading) is common in some areas (e.g. physical review letters prefers the notation with round brackets is even recommended: https://journals.aps.org/prl/authors/axis-labels-and-scales-on-graphs-h18; but keep in mind that the article in question was not submitted to APS but to AMT; AMT has different style guidelines, as cited above), square brackets are in fact used to give units of a quantity as follows: [quantity] = unit, e.g.: [T] = K. Using square brackets in axis labels around units is simply not correct and should never be used. Using round brackets is accepted, but has certain disadvantages: It can be easily mistaken as a multiplication factor whereas it really should be the denominator of a quotient. Hence, labeling a distance axis as "distance (m)" could be interpreted as "distance <<times>> meters". This is incorrect. What is labeled on the ticks on the x-axis in the graph is "distance <<over>> meters" (a plain number); the notation "distance/ m" does not leave any room for interpretation and will be understood correctly independent on your field or background. A very instructive explication in German (see the original from the BIPM linked on the AMT homepage) can be found in the German version of the SI brochure: "https://www.ptb.de/cms/fileadmin/internet/publikationen/ptb_mitteilungen/mitt2007/Heft2/PTB-Mitteilungen_2007_Heft_2.pdf", as in the original, in Sect. 5.3.1 (especially page 174 [corresponding to page 33 in the pdf]).
(3) Regarding the authors answer about the criticism of the limited datasets:
I acknowledge that the authors increased the number of both ECMWF and WRF and I agree that this is a sufficient coverage now. However, two comments here:
(a) regarding the GRUAN dataset, I would still like to mention that more than 70% of their ~6300 datasets come from 3 stations, and hence, I do not agree that that is a good coverage.
(b) from the authors answer on page 5 from document amt-2021-213-author_response-version1.pdf, I understand that the authors submitted the first version of the manuscript in the middle of the process of creating the validation data set, anticipating the full results based on a subset of just ~15%. This is certainly bad practice and should be avoided in the future. It was highly inconsistent (2 months vs a few days) and confusing in the first version.
Minor comments:
line 44: "this study" is ambiguous: does it refer to "the current study" (maybe better refer to the specific Sect. 4.1) or to "Wagner et al." (better use: "that")?
line 51: To which equation does "The final equation" refer to?
Table 1: I think "deviation to" should be "deviation from" (https://www.collinsdictionary.com/dictionary/english/deviation or https://dictionary.cambridge.org/dictionary/english/deviation) (likewise l.195)
line 88: Are the authors sure that they want to refer to Eq. 19 here? This seems to have nothing to do with the derivation here?
line 264: Please check the references here, it currently reads Appendix B0.1 and B0.1 There is not even any B0, Appendix B starts (as it should) with 1. (page 31, page 52 in the document.)
line 284/285: "correlation ... are found". "is"?
Figure 1: The frequency is defined as points in some "square" area made of delta-x time delta-y? Please give more detail here, otherwise the quantitative description in the color bar is not meaningful (of course, the qualitative message still comes across and I think it's a very good idea). Same for Fig. 5. , 10, 11. For most of these figures: The inclusion of the colour bar in either one or all subplots is inconsistent. Consider to include it as a separate axis instead. (Although it is not wrong as it is now since multiple colour bars are included where the colour scale differs between subplots. Still it seems not very pleasing for the eye as it is now. Additionally, e.g. in Fig. 10, the colour bar lacks the top axis while it s present in e.g. Fig. 11).
line 311: "too low" wit respect to what? Why "too low"? They are not "too" low?
Figure 8: Caption refers to "top" and "bottom" in a figure where only left and right are present. Please include horizontal separation lines between the stations. Are the authors serious in including stations with single digit numbers (Beltsville, Darwin, Nauru, LaReunion) here?
line 303: "agreement to"?
Fig. 7: Please choose any of the other 3 days here (or best all) and not the day which was used for fitting the parameters. Using the day used for fitting does not make sense. So replace Fig.7 by Fig. C2. Especially, because your argument of "But there is also a considerable reduction of SD from 1.6% for δΓ to 1.0% for δRH" (line 366) is not that strong any longer if you actually consider days that were not used for the fit, the SD only decreases from 2.0% to 1.8% (Mar), from 1.6% to 1.3% (Sep) and from 1.3% to 1.2% for Dec.
line 495: I acknowledge the footnote here, I was at first a bit puzzled here.
line 513: Maybe better "equation"?
line 614: "Note that the for a"? Remove "the"?
Figure B1: Please increase the space between the map and the x- and y- axis labels. Also: There are four "Fig. B1" (at least in the version with track changes), comment is about the first one. |
1. General comments
The manuscript "Calculating the vertical column density of O4 from surface values of pressure, temperature and relative humidity" presents in varying level of detail the derivation of, and the validation of, a daytime applicable method to calculate the O4 vertical column density from surface values of pressure, temperature and relative humidity. Hence, the title is well chosen. The main application area of this approximation are parametrized profile inversion algorithms for MAX-DOAS measurements. The authors also mention possible benefits for optimal estimation based profile inversion algorithms, stemming from the high correlation of surface relative humidity and temperature effective lapse rate. I recommend this manuscript for publication after intermediate revisions.
While there is certainly scientific value in the presented method, the quality of the presentation and the structure of the manuscript, have to be improved. The validation of the method is not quite sufficient and has to be extended. The degree of explicit derivation of equations varies from "very detailed" to "almost insufficient" and should be brought to a more "equal" level.
The presented derivation of Eq. 9 seems unnecessarily complicated: Starting at the usual barometric formula for the air density for an atmosphere with constant laps rate
ρ = ρ0 (T0/(T0 + Γ(x-x0)))1+(gM/R/Γ)] = ρ0 (1+ Γx'/T0) -(gM/R/Γ)
(x'=x-x0) and integrating the square of this ρ multiplied by the oxygen volume mixing ratio (i.e. integrate the O4 density) from the surface (0) to infinity, replacing ρ0 by p0/T0/R, directly yields Eq. 9. Maybe the authors can comment on why they chose to over complicate things with introducing the ratio of hO2 and hO4. (Likewise, choose the density formula for 0 lapserate and integrate the square, in order to arrive at the corresponding equation for 0 lapse rate). I highly recommend to streamline this. I cannot see any added benefit of the method used by the authors, but I do see a lot of unnecessary turns given.
At several occasions in the manuscript, the authors refer to later sections or to, at that point, unproven and not referenced statements. This makes it impossible to read the manuscript in a linear fashion.The main line of reasoning should be clearly stated and followed. Several statements are made without proof or proper reference. Regarding style, the guidelines of AMT are, in several aspects, not followed. The quality of the plots is mostly ok but should also be improved before final acceptance (especially the readability of axis labels).
Apart from the unfortunate structuring of the manuscript and the unnecessary turns given in order to arrive at the important equation, the biggest point of criticism is perhaps on the method validation and the lack of showing the improvement when using this new method over other methods to estimate the O4 VCD, as well as the actual effect on the final product, the retrieved AOD.
Three rather limited data sets were used for validation. Each of these datasets needs to be extended. For one of the datasets (global model), half of the dataset was used to fit parameters in the model; still, that same half was also used for validation. This should really be avoided. It is advisable to add a separate day for parameter fitting. For the regional model dataset, the description seems to indicate that it consists of 2 months (May and June 2018, see line 179), although it appears that only a few days (beginning of May) were used to derive the statistics. It would be advisable to use at least 2 months covering different seasons (so instead of May and June, maybe June and December). For the third data set, data from radio sounding, I believe there are plenty of data available since meteorological services such as the MetOffice, launch weather balloons twice a day at several stations (I believe the DWD does the same). In a next step, these results need to be compared to a "current standard method" approximating O4 VCD. This is entirely missing in this manuscript.
I made a quick test using 3 years (2018, 2019 and 2020) of data from 6 stations (some overlap with stations that the authors use) from 12 UTC radiosonde launches (Cambourne [N=1061], Nottingham [N=315], Essen [N=468], Munich [N=1022], Lindenberg [N=1062], Lamont [N=430, 0 UTC for the latter to comply with the SZA requirement]). I find, using Eq.12 and Eq. 13, respectively, a high correlation (0.93, 0.94, 0.92, 0.93, 0.93, 0.93) for estimated and integrated O4 columns (confirming the authors' findings), and, using Eq. 15, low bias and low standard deviation (-1.8±1.0)%, (-1.5±1.1)%, (-1.0±1.3)%, (-1.7±1.1)%, (-1.4±1.2)%, (-0.8±1.7)% (again, confirming the authors' findings). If I do the same but, instead of using the approximation method, use climatology data, I get the following for mean bias and std: (1.6±2.0)%, (0.1±2.1)%, (0.2±2.1)%, (-3.9±1.7)%, (0.8±2.0)%, (-1.2±2.3)% (so 50 -- 100% worse standard deviation, but partly better mean). However, the correlations are certainly much lower (0.45, 0.51, 0.55, 0.65, 0.61, 0.53). I would like to see similar comparisons in the manuscript in order to show that using this method is in fact better than using climatology values [Is it actually worth it? Please show this!]. It would be advisable to include such statistics for at least 20--30 other well distributed weather balloon launching sites for a few years.
Lastly, since the use of this approximation is clearly, as the authors point out, tailored towards parametrized MAX-DOAS inversion methods, it is highly desirable that the authors show some result of those: compare the retrieval results using the "previously standard method" to results obtained using this new method.
The manuscript frequently refers to Wagner et al. 2019 which makes it appear to be rather suited as an extension of that publication than a stand-alone publication. From my point of view, the innovative part of this manuscript is the empirical relation between the effective lapse rate and the surface relative humidity and the fact that this knowledge can be used in the formalism of Wagner et. al 2019 to replace the fixed lapse rate. This part however, I do find sufficiently important for publishing. However, the current format of the manuscript is not good enough. It over complicates things. It does not include sufficient validation data, nor does it include a test on the final product this method is thought to be used for. Hence, I recommend intermediate revisions of this manuscript.
Restructure the manuscript. Streamline and simplify the method section, especially how to arrive at Eq. 9. For validation, extend regional model data covering a larger time period, use a separate day for the parameter fitting for the global model, use many more datasets from radiosondes. Include comparisons with currently used methods (such as using climatologies). Include tests showing that the final product (AOD retrieved from MAX-DOAS measurements) in fact benefits from this new method to estimate O4 VCDs by comparing results ("old" and "new") to complementary measurements.
2. Specific comments
line 59 - 60: Incomplete list, and a 1 sentence paragraph: skip this.
line 61 -- 64: This should be skipped, does not add any new information (?) n_{O4,0)} == n^2_{O2,0} is stated explicitly in Eq. 5
line 65 -- 68: No new information, all is contained in Table 1. Skip
line 88 -- 89: Neither of equations 7 or 8 is based on Eq. 6. Equation 7 follows, as the authors write themselves, directly from the equation of hydrostatic equilibrium and the assumption of a constant O2 VMR (see comment below), Eq. 8 is simply the ideal gas law for quantities at the surface. Hence, this sentence should be moved to after line 100.
Eq. 7: While the authors spoon feed the derivation of Eq. 6, they skip totally the derivation of Eq. 7 from the equation of hydrostatic equilibrium dp = -rho g dz. (e.g. by Ptop - Pbottom = - rho g h - (Ptop=0)--> -P0 = - rho g h --(rho = n*m/vol)--> P0/g = n m h / vol --(n h / vol == Vair)--> P0/ g/ m = Vair). Apart from assuming that, it is also rightfully assumed that the volume mixing ratio is constant; although implicitly clear by Table 2, it should be added.
line 98 -- 101 (+ Appendix A): All equations should have a number. Please add a number to the equation stated here. Also,reference the derivation of this directly as appendix A2. Regarding equation A3 from the appendix A2: Also here, a derivation of this equation is missing. Maybe start with the equation for polytropic atmosphere p/p0 = ( T/ T0)**(gM/R/Gamma) and T = T0 + Gamma * z' and say that Eq. A3 follows from this together with the ideal gas law. I think there is something not going quite right with the signs: The authors define the laps rate to be negative. As such (since g is defined positive in Table 2), -alpha +1 = -gM/R/ Gamma would be (Gamma < 0) a positive quantity. With this, the term in round brackets in Eq. A6 for z' = ∞ would otherwise not disappear. I also wonder if there might be a minus sign missing in Eq. A6 in the last line (or z should be maybe going from 0 to -∞, this solves the problems, I think, please check) .... In line 429, what does "12" refer to? Eq. 12? It's easy to make mistakes, so it is of course also possible that I made a mistake in my checking. Please carefully check the signs anyway.
It is stated that ECMWF data from June, 18th 2018 was used for the fit. Further, the authors state (line 267) that they investigate June, 18th 2018. This should never be done. You cannot use the same day for fitting and verification. Please choose a third day for the fitting and use the same day (June 18 and December 18) only for verification.
3. Technical comments
3.1 general
Since one of the co-authors is the chief-executive editor of AMT and the first author is an associate editor, I find it slightly worrying that the authors disregard so many of the AMT guidelines:
3.2 specific