Optimal Band Analysis of a Space-Based Multispectral Sensor for Urban Air Pollutant Detection
Round 1
Reviewer 1 Report
Proposed paper describes possibility of atmospheric pollutants analysis using spectral satellite data. The authors brings a short review about the issue of radiative transfer modeling and about optimal spectral bands selection for purpose of pollutant detection using spectral data in the first part of proposed manuscript. The results and discussion of analysis is proposed in the second part. Though I am not very familiar with this issue I have some comments on the paper. Material and methods should be described separately and more in detail in my opinion. Furthermore the results (bands interval and width for particular pollutants) should be verified on basis of real measurement. Presentation of the results is unbalanced - the results for CO are more detailed than for other pollutants.
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Reviewer 2 Report
The paper presents a technique to optimize the selection of spectral channels for the detection of key components of the Earth atmosphere classified as pollutants from VIS, NIR and TIR. The authors illustrate the results for all the gases of interest, concluding that their technique can be useful to select both the central wavelength and the bandwidth of the channels in the context of instrument design to optimize the detection of these gases and aerosols.
Overall, this manuscript presents some elements of interest, which in some cases serve to update the current knowledge and techniques used to analyze the sensitivity of instruments to trace gases and pollutants, as testified by the number of (adequate) references the authors include in the paper. Nevertheless, there are a few problematic elements in the description of the methods, and in the way some results are discussed and presented. The manuscript would in general benefit from the following revisions and recommendations:
1) Line 127: some references for spectral unmixing are given. However, I find them insufficient to provide adequate context to the work developed. The authors should add some words to explain what spectral unmixing is.
2) Line 158 and following: the term "path spectral radiance" is totally unclear. Perhaps the authors mean "radiance computed along the viewing path"? same for many other terminologies in this section. Another problem is related to the total confusion between "radiance" and "irradiance". The terms are not equivalent, and cannot be interchanged. The first term in Eq. 1 is a radiance (because it is scaled on the solid angle), and almost all the times in which "irradiance" is mentioned, should be replaced with "radiance".
3) Line 163: I don't find Figure 1 clear on this point, it does not explicitly show anything about the specifics of the radiative transfer scheme used. In addition, the claim that both scattering and emission should be considered for "medium wave infrared spectrum" has to be better explained (in terms of the possible presence of aerosols, property of surfaces, etc.), since the authors are detailing their radiative transfer scheme.
4) Line 169: besides the continuing confusion between radiance and irradiance, which needs to be corrected, I recommend the authors checking the Eq. 3. It seems that a cos(theta_s) is missing as multiplicating factor of rho_r (which I would recommend to denote as rho_g per similarity with E_g). This factor is necessary to rescale solar contribution in Nadir geometry.
5) Line 175: "spectral emission" is a very confusing term. Did the authors mean "emission contribution to the radiance". Same for "scattering radiance" (there is no such a thing, perhaps "scattering contribution" (to the radiance)).
6) Line 179: omega_i is not the "spectral albedo". Perhaps "single scattering albedo"?
7) Line 178: Similarly to Eq.3, I recommend the authors to check the validity of Eq. 7. If tau were to indicate optical depths, this expression would be valid, but sum of transmittances (rather than multiplication) in this form does not sound correct.
8) Line 186: "observed radiance" rather than "spectral characteristics".
9) It looks like the whole section is missing the contribution of the downwelling radiance emitted by the atmosphere towards the surface, and then reflected back into the space towards the viewer. This contribution is typically 10% or so of the total radiance observed in the thermal infrared (Amato et al., 2002, "The sigma-IASI code for the calculation of infrared atmospheric radiance and its derivatives"). Have the authors verified that the lack of such term does not influence their results?
10) Lines 208-210: this is a very important point that needs to be expanded in its fundamentals (why spectroscopy parameters need to be adjusted), otherwise in this form appears just as "handwaving".
11) Line 217: the fact that the atmospheric density decreases with altitude has nothing to do with the fact that molecular concentration with altitude needs to be known. The authors should recall this fact only when talking about their implementation of radiative transfer, which is not really addressed anyway or recalled in this work. In general, in almost all the cases in which the authors remind to the reader that atmospheric density decreases with altitude, this has nothing to fo with the following sentences/arguments (e.g. line 256). Lines 218-222 are also unclear and should be better rephrased.
12) Line 262: scale height is not "an empirical parameter varying with aerosol concentration", rather it is defined by the P/T profile. If the authors are using z0 with a different meaning, it should not be called a "scale height", rather a " scaling parameter" or so.
13) Line 263: mostly spectral, not spatial.
14) Line 298: it is unclear what the authors mean here, and should be rephrased.
15) Line 322: the two references provided are not essential to understanding what SNR is, and should be eliminated.
16) Fig. 2: the contrast between green and blue is poor and does not help to read the figure. I recommend a pair of more contrasting colors.
17) Line 373: "According to quantum theory" sounds scholastic and inaccurate. I recommend to delete it, and in general to shorten this paragraph, retaining only those elements essential to understand the problem explained thereafter.
18) Line 384: "vibration phenomenon" to be replaced by "structure of the vibrational band of CO". Figure 4 caption has also to be sloghtly expanded, since it explains only the left panel.
19) Line 443: "at ground".
20) Line 454: "intense" not "intensive". This error is repeated more than once, and should be corrected. Similar confusions occur for other words (e.g. "spectral characteristics" rather than "features").
21) Line 496: this explanation is not accurate. The major reason for this difference is the lack of spectral contrast between surface and aerosol in urban areas. This should be better explicited.
22) What is the vertical profile used for NO2 and SO2? The text is not clear on this point.
Author Response
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Reviewer 3 Report
This study presents a solid methodology to select the appropriate wavelength bands in order to identify 4 pollutants' concentration from space born measurements.
The authors adequately describe the methodology and provide a solid mathematical skeleton on which their research is based.
Some questions/suggestions:
1. Could the authors please elaborate on how they chose the thresholds picked for the SNR (line 326)?
2. I would be better to justify your selections in table 2: could these be based on any of the instruments orbiting around the earth? Do you expect the results to change if any of these set parameters change? (Maybe you could test it to see the differences in your results for different viewing geometries).
3. Although it's not a part of the study, it would be interesting to see how the proposed band selection performs on real life data, as a validation of the findings in here. I believe that there are some hyperspectral images that could offer the information needed for a validation study.
Thank you.
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Round 2
Reviewer 1 Report
I have only two notes/recommendations which can contribute to clarity and readability of the text:
1) The assumptions written at rows 132-136 should be marked by bullets
2) Equations cited directly in the text should be written in form e.g. "eq. 10" instead of "(10)" in my opinion
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Reviewer 2 Report
In the revised version the authors have responded adequately to most of the points raised in the first review round, and the revised manuscript is more robust in many aspects.
Nevertheless, some adjustments are still needed. Here some further recommendations:
1) Regarding to the point 9) of the previous review, I have to disagree with the authors on part of the explanation provided for neglecting some of the terms of the radiative transfer equation. Indeed, for all the molecules analyzed, the paper considers spectral intervals dominated or heavily affected by up- and downwelling thermal radiation emitted by the atmosphere, rather than solar radiance. Therefore, neglecting some thermal contribution will yield a bias which needs to be at least quantified. This is especially true in case, e.g., of clear sky and low emissivity (=high reflectance), where sensitivity can be significantly affected by reflected radiance contribution.
This issue must be addressed, either using actual data from satellite instruments (e.g. IASI, AIRS) to verify the validity of this hypothesis in different conditions, or working with the full radiative transfer equation on the cases already presented.
2) The discussion of O3 absorption (lines 458-465) is confusing. The positive/negative values in the difference (Figure 9b) are not necessarily related to ozone concentration, but they can be definitely related to other influencing factors, such as ground emissivity and temperature, and temperature gradients between the stratospheric ozone layer and the tropopause. These aspects need to be stressed better in the paper, and they still evidence that a comparison with real satellite data would benefit the robustness of the paper.
3) Regarding point 1) of the review, the authors have correctly specified the meaning of "scale height". However, now this is not related to the meaning of z0 in Eq. (14), which has to be specified as a "vertical profile scaling parameter".
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Round 3
Reviewer 2 Report
The authors have answered to my concerns, and I have no further comments.
This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.
Round 1
Reviewer 1 Report
For many decades since the introduction of the Curtis-Godson method, methods for calculating radiation have evolved significantly. There are a number of publications on the methods of calculating scattered and reflected solar radiation, which the authors do not mention. Also algorithms for calculating radiation have been developed. The authors do not say anything about this and do not justify the need to develop their own original algorithm.
All analysis and conclusions are based on the radiation calculation algorithm proposed by the authors. But nowhere in the paper is there any analysis of the reliability of this algorithm, no estimates of its errors. Therefore, to talk about the validity of the results of the work is not possible.
In addition, although the simplest approach to assessing the possibility of detecting and measuring atmospheric constituents proposed by the authors can be used at the initial stage of research, more perfect approaches to evaluating informativity and errors in solving inverse problems that the authors do not even mention have long been known.
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Reviewer 2 Report
The manuscript describes a technique to identify a spectral band and bandwidth of an infrared sensor mounted on a satellite for an atmospheric pollutant based on contrast to background signal and signal to noise ratio. Authors found out the optimal band range for typical criteria pollutants using the technique, which were very similar to the one already being used. While the technique appears to be convincing and useful, there are some major issues in the manuscript to be addressed before it can be published.
Major issues:
1. Introduction needs a comprehensive revision. It includes very basic information on pollutants and aerosols which may or may not be required. However, it missed significantly on describing the current state of the infrared remote sensing, band selection etc. Author’s did not present any previous work on band selection techniques in infrared remote sensing or other sensors. Some references are listed below as an example. Authors also did not describe how their technique is different from anything currently used, possible advantages of their new technique compared to any old one.
· Lee, Z.; Carder, K.; Arnone, R.; He, M. Determination of Primary Spectral Bands for Remote Sensing of Aquatic Environments. Sensors 2007, 7, 3428-3441
· Jun, Z., Wen-qing, L., Jian-guo, L., Yi-huai, L., Min-guang, G., Liang, X., Tian-shu, Z., Xiu-li, W., 2007. FTIR measurement and analysis based on the selection of optimized spectral band. Spectrosc. Spectr. Anal. 27, 679–682.
· Price, J.C., 1997. Spectral band selection for visible near infrared remote sensing: Spectral-spatial resolution tradeoffs. IEEE Trans. Geosci. Remote Sens. 35, 1277–1285. https://doi.org/10.1109/36.628794
· PRICE, J.C., 1994. BAND SELECTION PROCEDURE FOR MULTISPECTRAL SCANNERS. Appl. Opt. 33, 3281–3828. https://doi.org/10.1364/AO.33.003281
2. In methods and results sections, majority of the cited references are more than 20 years old. Is there not any recent work on band selection techniques in remote sensing? If yes, then authors should emphasize this fact early on in the introduction. If not, then they should at least include the recent literature in the whole manuscript.
3. All the equations presented must be cited, if they are not developed by the authors.
4. In results section, a comparison with current measurements or bands currently used for different pollutants with the results achieved in this work, should be presented.
5. A discussion on the implications of this work on remote sensing as such and applicability in countries/regions with relatively low concentrations of pollutants.
Minor issues:
1. Define all acronyms at least once.
2. j and f are two different symbols. It appears to me they have been used interchangeably, for example, line 140, 141.
3. Are Ee-I and E0-I are different? If yes, define them appropriately.
4. Line 138: What does the symbol P signifies?
5. How is the impact of clouds accounted for in the model work?
6. Line 240: It appears Ib is the background intensity, but is not defined clearly.
7. Figure 3a doesn’t show the polluted and unpolluted response clearly. Must be redrawn.
8. Lines 389 -390: Using just the visual cue to mention no difference in figure 7a and 7b is not appropriate or sufficient. A better and may be a quantifiable way should be presented.
9. Figure 8: Cite reference for the data used in figure 8 or the methodology to calculate/measure that.
10. In section 5.2, Is the absorption by the aerosols (e.g. black carbon) accounted in the model? I understand it is not. If not, why?
11. Figure 11. Why can’t a central wavelength with a better SNR be used? For example, band around 0.7 µm or 1.0 µm has good SNR.
Author Response
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Round 2
Reviewer 1 Report
The paper considers the choice of spectral intervals for satellite measurement of anthropogenic pollution of the surface layer of the atmosphere. On the basis of the radiation model developed earlier by the authors, contrasts of outgoing radiation, caused by the presence of various types of pollution, were calculated. Intervals that maximize these contrasts are selected. The results obtained can be used as an approximation to the optimal spectral measurement scheme. The results of the work can be useful in the development of equipment for satellite monitoring of pollution.
There are typos in the text, for example, in line 218 “moelcules” is printed instead of “molecules”. It is advisable to clarify in lines 256,257 the phrase “λ0 denotes the wavelength at which the spectral absorption coefficient is negligible, such as 0.55μm and 0.61μm”
The work may be published after minor modifications
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Reviewer 2 Report
While many issues have been addressed in the revision, some issues are still pending or not adequately addressed.
Introduction still lacked the motive behind this work. While hyperspectral imaging appears to be much more advanced, detailed and developed, authors focused on multispectral imaging. Why not use hyperspectral imaging for pollutant detection? The advantages I see of multispectral imaging are possibly reduced complexity, lighter satellite and relatively cheaper. Or they are just developing an alternative technique?
Point 5 in the old review is not addressed - A discussion on the implications of this work remote sensing as such and applicability in countries/regions with relatively low concentrations of pollutants. - Authors could possibly add sensitivity analysis with some of the pollutants to infer that.
The title of the manuscript should reflect that it is multispectral technique.
Manuscript requires extensive copy editing.
Minor revisions:
Line 35-37 : Awkward sentence formation. rewrite sentences.
Line 44: "SO2 concentration in ozone". What does that mean?
line 80 : replace "have been" with "is"
line 129: replace "retrieve" with "retrieval"
Line 143: I believe it is figure 1 and not figure 2.
line 179 and 182: two different "phi" symbols are used.
line 283: replace "given" with "written"
line 309: "various". Is it variable?
Table 2: Basis for using the bands for different pollutants.
Line 392-393, 412-413, 464-466, 513-515: The sentences should be rewritten to emphasize the consistency of the results with the previous work. "contrast" is not the correct word.
Line 414 : It should be "more challenging"
Line 420 : Awkward sentence. Rewrite it. If a reference is used as a part of a sentence, then use xxxx et al., (yyyy).
For NO2, the comparison with the previous work is missing.
Line 439-440: it should be "decreases with the height".
Line 480: Replace " a challenge" with "difficult"
Line 489: it should be "intense"
Line 497: replace "locating" with "located"
Line 518: It is figure 11.
Author Response
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