Review of Manuscript: " Investigating the ability of satellite occultation instruments to monitor possible geoengineering experiments"

The manuscript examines the ability of satellite occultation instruments to monitor potential geoengineering experiments using MAECHAM5-HAM simulations and retrievals with the SCIATRAN radiative transfer model. While the model experiments are straightforward and easy to interpret, I have two major concerns regarding the analyses presented in the paper.

First, the use of data from the initial two years of the simulation raises concerns about whether the model has reached an equilibrium state. It is crucial to ensure that the model's early-phase data are suitable for analysis. Could the authors provide insight into the model's performance during this period and demonstrate that it has stabilized?

Second, in line 214, the manuscript states, “The errors shown and discussed so far are based on one extinction profile per month.” It would be beneficial for the authors to clarify their rationale for this choice and to compare averaged profiles with those currently presented in the manuscript.

Beyond these major concerns, the manuscript is well-written and presents a novel approach by using a relatively small sulfur injection to assess the model's response. The study is valuable to the scientific community, and I have provided specific comments below that should be addressed before publication.

Comments:

1. Lines 71-73: How is the model's dynamics treated? Is it prescribed using a climatology? Please elaborate.
2. Lines 75-76: Could you clarify whether a single realization or an ensemble is used? If only one realization is run for 15 years, what is the spin-up time? If the first two years and the last three years are analyzed, is the model in equilibrium in the first two years (initial phase)? A time series showing equilibrium would be useful.
3. Line 96: Correct the typo “trough” to “through.”
4. Lines 97-98: Are these climatological values equivalent to those used in the model if the dynamics are prescribed?
5. Lines 120-121: Is this statement based on observations or model experiments? Have you conducted a no-sulfur (0 Tg S/year) experiment to establish a background aerosol extinction coefficient? Please see my comment for Figure 7 (lines 187-188).
6. Line 120: Insert "extinction" between "aerosol" and "coefficient" for clarity.
7. Line 124: Could you please define “quasi-steady state” and “initial phase” more explicitly, especially in relation to model equilibrium.
8. Lines 127-130: What is the reasoning behind showing these figures? Are they meant to highlight differences between the initial and quasi-steady-state phases? If so, please clarify.
9. Lines 140-145: The sensitivity analysis is appreciated. Could you elaborate on why differences are larger below 15 km and improve above that altitude? Please do the same for the appendix figures.
10. Lines 149-155: Why return to the initial-phase data here? If the quasi-steady-state phase is used for analysis, maintaining consistency would be preferable. I doubt if the initial phase data and their analyses are relevant as the model may not have attained equilibrium state by then (first two years).
11. First line of section 3.2: Line 149 mentions that retrievals are based on initial-phase data, but this section focuses on quasi-steady-state data. Why mix the two?
12. Third line of section 3.2: Could you explain why total errors for 1 Tg S/y are greater than for 2 Tg S/y in Figure 3? This seems counterintuitive.
13. Line 162: Please clarify the term “true profiles.” Does this refer to model simulation results?
14. Line 175: Please replace ± 55⁰N with 55S-55N or something similar.
15. Line 178: Do you have corresponding model simulation values for Figures 4 and 5? If so, please include them.
16. Lines 180-181: Adding model-simulated SAOD using the 55S-55N latitude band would strengthen comparisons. Can you provide insight into the causes of maxima and minima in these figures?
17. Lines 187-188: Section 3.2 is based on quasi-steady-state data, but here total errors seem to be derived from the initial phase. This is confusing—please clarify. Also, if you are analyzing a background case (0 Tg S/y) from the first month of the initial phase, a table in Section 2.1 listing all model simulations (0 Tg S/y, 1 Tg S/y, and 2 Tg S/y) would improve clarity.
18. Lines 190-192: Could you please elaborate a bit more on as to why the total errors would be larger for Figure 7 compared to Figure 3?
19. Lines 206-207: What is the rationale for using only the first month of the initial phase? How is that related to detectability of satellite occultation instruments? Would the model have reached equilibrium by then? Please see my comments above for line 75.
20. Line 214: How was the selection made to use one extinction profile per month for Figures 2, 4, 5 and 9? It would be beneficial for the authors to clarify their rationale for this choice and to compare averaged profiles with those currently presented in the manuscript. Also, please consider showing model SAOD values in Figures.
21. Lines 219-220: SAGE III/ISS measurements were not available before 2017. Please correct this.
22. Lines 236-237: To highlight differences, please consider overlaying SAOD values from Figure 6 onto Figure 10 (e.g., plotting SAOD for 1 and 2 Tg cases at 50S and 30N from January to December).
23. Lines 258-260: The discrepancy discussed here may result from the model’s non-equilibrium state during the initial phase. To ensure consistency, it would be preferable for the analyses to focus on data from the model’s equilibrium (quasi steady) state.

Review of the manuscript “Investigating the ability of satellite occultation instruments to monitor possible geoengineering experiments”, Lange et al.

Dear Editor, dear Authors,

The manuscript “Investigating the ability of satellite occultation instruments to monitor possible geoengineering experiments” by Lange et al. aims at analysing the expected capability of solar occultation instruments like SAGE III to detect and characterise stratospheric aerosol injection (SAI) geoengineering interventions. The topic of the manuscript is potentially important and relevant for a readership of satellite instrument and data scientists. Despite this, I have a few major concerns (especially Major Comment 1 below) about the manuscript and the inherent analyses that must be addressed before the manuscript can be considered for publication, in my opinion. I also have minor and specific comments, listed in the following. Please address the following major and minor comments and I will be willing to further evaluate a new manuscript version.

Regards.

Major Comments:    

1. The overarching motivation of this work is to assess the detectability of SAI interventions with SAGE III-like instruments. To do so, two geoengineering modelling experiments have been used as a pseudo-reality scenario, simulating SAI with injections of 1 or 2 Tg S/year. Now, different moderate stratospheric eruptions occurred in the last few years, e.g. Raikoke 2019, Hunga 2022, and more in the previous after-Pinatubo years, each with SO2 injection of that order of magnitude (1-2 Tg SO2 or less --> 0.5-1.0 Tg S or less). Many scientific works exist that show detection, tracking and quantitative characterisation of these plumes with SAGE III/ISS, e.g. More quantitatively from an aerosol extinction point of view, the perturbation in the aerosol extinction for this geoengineering experiment and study is of the order of 10^-3 km^-1 at 550 nm. This is quite comparable to perturbations of recent moderate eruptions like Raikoke, which sulphate aerosol perturbation was successfully detected studied and quantitatively characterised with SAGE III/ISS (e.g. Kloss et al., 2021, https://acp.copernicus.org/articles/21/535/2021/). So, even without this study, one could affirm that, yes, geoengineering plumes resulting from injection of 1 (or even less) Tg S and producing aerosol extinction perturbation of the order of 10^-3 km^-1 at 550 nm are observable and measurable with SAGE III. Thus, it is mandatory to clarify the scopes of this manuscript, restructure the manuscript accordingly and possibly change the title.
2. The readership of interest for this kind of manuscript is more AMT that ACP, as it is very centred on instrumental aspects. Thus, I propose to transfer the manuscript to that journal.
3. I don't really understand the background idea behind Sect. 3.3. Why is the error analysis performed for background case to study the initial phase of the perturbed case? Why not just making an error analysis of the initial phase itself instead? Why you conclude that "The background profile for 65° N (upper panel) is within the error range for all altitudes considered here, which leads to the conclusion that the emission of 1 Tg S/y cannot be observed at 65° N in January, i.e. the first month of the initial phase."? And why do you conclude that "the stratospheric aerosols formed in the first month of the initial phase can only be detected with satellite occultation instruments in a limited latitude range from – 10° to 14° N." All this is unclear to me and should be clarified.
4. The quality of the text and clarity must be improved throughout the whole manuscript, more in the Specific Comments.

Minor Comments:

1. L14: "and increase" --> "by increasing"
2. L15: "SAI" is rather "stratospheric aerosol injection"
3. L16 and Introduction in general: please consider citing more recent literature, e.g. https://www.frontiersin.org/journals/climate/articles/10.3389/fclim.2025.1507479/full
4. L17: "sulphur" --> "sulphur dioxide"
5. L19: "forcing" --> "radiative forcing"
6. L20-21: "Simulations...W/m2" after how much time of 10 Tg S/y injections?
7. L26-27: I don't get the logic here. Why now it is mentioned that it will be important to observe "small amounts of *sulphate aerosols" while before "large eruptions" where mentioned?
8. L28 "SAGE" acronym not defined here. Please check if all acronyms are defined
9. L29: "active" sounds odd here (SAGE is "passive" so this word can be taken in a different sense), also please mention "*solar occultation" and also why "one of the..."? Are there other solar occultation missions operational at the moment?
10. L32; really there is nothing more recent than McCormick et al., 1979?
11. L35: is 1-2 Tg S/y really a "small" injection? This sound like over a Raikoke-type eruption per year, so much larger than natural occurrence. In my opinion, this cannot be called "small". Please rephrase.
12. -0.3 to -0.6 W/m2 is 10-20% the total greenhouse gases radiative forcing since preindustrial era, and up to twice the 10-years greenhouse gases radiative forcing; so why should this not be considered a significant radiative forcing?
13. L39: again, these are not small amounts of SO2 injections but rather > 1 Raikoke per year...
14. L55: "truncation at wavenumber 63" what does it mean?
15. L66-67: What are the optical properties of sulphate aerosol in input to the radiation scheme? Are they calculated using an online Mie code and using the size distributions obtained with the model?
16. L74: is sulphur injected as SO2? Which is the rate of SO2 injection - one shot per year or different injections finally cumulating to 1 or 2 Tg/y?
17. Section 2.2: I don't think that SCIATRAN is properly introduced (what is it? how it works? relevant publications, etc)
18. Eqs 1 and 2: can you mention here a typical obtained value for the Angström exponent?
19. L104-105: "which is not publicly available": OK but is there at least a previous publication where it is used or this is the first one?
20. L110: "The apriori state vector is kept constant" constant with respect to what? And constant at which value?
21. 1: I'm not sure that the meaning of this figure is clear, especially because of the different color scales. Basically, why this figure is shown? To show how much the extinction coefficient is perturbed by SAI in the simulations? In this latter case, please use the same color scale for both panels
22. L133-138: how are these modified settings chosen? It would be more significant to take variations that are comparable with uncertainties of O3, T, P from other (best available) measurements, and of realistic pointing errors.
23. Eq. 6 is formally wrong because this is not expressed in %, as in the corresponding figure
24. Fig.2: what does it mean, in the caption, the mention to "5°N"?
25. I don't quite get the sense of sentence at L149-150
26. Isn't it rather the square root of Eq. 7 what is actually called, before and after in the text, the "total error"?
27. Section 3.2: can you quantify the typical total error in the stratosphere (the altitude of SAI injection)?
28. L160: Remove "The following"
29. L161: "January and July" of which year?
30. Fig. 4: purple lines are difficult to see: why not another color, e.g. green?
31. L164-166 and L180-185 (also Major Comment 1): the fact that these SAI interventions are visible with SAGE III is not really a surprise because these are not "small" injections but rather the same level of moderate eruptions, like Raikoke 2019, Hunga 2022, etc, which have been already successfully observed with SAGE III/ISS
32. Section 3.3: see Major Comment 3
33. L210: “Although…effect” see my previous comment on this
34. L236-237: why not showing the geoengineering signal here (e.g. in Fig. 10)?

The manuscript addresses one aspect of geoengineering—enhancement of the stratospheric aerosol layer to mitigate climate warming. The authors analyze the detectability of stratospheric aerosols formed as a result of sulphur dioxide (SO₂) injection into the stratosphere. The topic is timely and relevant, and the paper could be suitable for publication after some major issues are addressed.

While the paper is generally well written, further clarification is necessary to ensure the content is accessible to a broader audience beyond specialists in stratospheric aerosols.

The numerical experiment involving SO₂ injection should be clearly described in a dedicated section. Specifically:

    How was the injection distributed over time?  Was it a single injection of 1–2 Tg, or was the amount spread uniformly over the course of a year?   The terms “initial phase” and “quasi steady-state phase” should be explicitly defined in this context.

The key distinctions between the geoengineering experiment and isolated volcanic eruptions should be emphasized more clearly.

The authors argue that the injection of 1–2 Tg/y of SO₂ is relatively small, and therefore, if such an amount is detectable, larger quantities should also be detectable. However, they should clarify what they consider to be the upper limit of SO₂ injection. Additionally, they should discuss how detectability changes with increased injection amounts, particularly in light of the potential zero transmittance in occultation geometry, as observed shortly after the Pinatubo eruption.

It would also be beneficial to model the particle size distribution and its temporal evolution. This would allow for the calculation of transmittance at wavelengths longer than 550 nm and help overcome the issue of transmittance saturation.

Throughout the manuscript, different names are used for the circulation model—ECHAM, EHAM5-HAM, MAECHAM5, and MAECHAM5-HAM. If these refer to the same model, a consistent name should be used. If they are different, the distinctions should be explained.

Table 3: Please justify the use of a 2% value for error estimation.

Equations:

    Is the sigma (σ) in Equation 7 the same as r in Equation 6? If so, use consistent notation.

    Compare your aerosol extinction error estimates with those from SAGE III aerosol extinction retrievals.

Figures:

    A logarithmic scale should be used for figures displaying extinction profiles and optical depths.

    Cases with 1 Tg and 2 Tg/year should be shown on the same figure for easier comparison.

    In Figure 1, part (a) should represent the initial phase, and part (b) the steady-state phase, to reflect chronological order.    Different colors should be used to indicate high and low extinction values for better visual clarity.