The manuscript from Bohn et al. deals with a relevant problem of imaging spectroscopy of snow and ice: topography. The authors developed a new methodology to correct imaging spectroscopy data acquired from the EMIT satellite mission for the effect of topography and they conclude that high error in LAPs-induced radiative forcing estimates are possible if the topographic effect is neglected. The study is based on two EMIT scenes in Chile and Argentina without any field validation of the retrieval. This issue partly weakens the outcomes of this study, and I suggest to refine the conclusions in accordance. Several hyperspectral satellite mission will be launched in the future (e.g. SBG, CHIME) and new data will be available for retrieval of surface parameters of snow and ice. The results of this manuscript raise important questions regarding the uncorrected topographic effect in the context of parameter retrieval. I think that the manuscript is interesting both for the cryospheric and remote sensing community, and it can be accepted only after minor comments listed below are taken into account.

lines 69-70: What are the expected signal-to-noise ratio for those two missions? Please provide some numbers.

In the introduction, I suggest to add a brief discussion on the attempts that have been made to model snow albedo in complex topography (e.g. Picard et al. 2020). In fact, those studies already show the "blue hook" that is described later in your manuscript.

Figure 1: I suggest to add the grain size value (100 um and 1000 um) also in the plot. HDRF should be also displayed in the label, in order to be consistent with the main text.

line 154: the spatial, spectral and temporal resolutions of EMIT data should be provided here. Furthermore, I suggest to add a scale bare to Figure 3.

line 256: this info should be provided in the methods. Which bands have been used to calculate ndsi? You used Ndsi<0.0: this is strange, please verify which threshold that you applied to identify snow/ice areas.

line 265: Geophysically? I never read/heard this term..

line 266-268: this is true only during a period of time. When air temperature is low, this may not hold true.

line 282-284: how you can be so sure without any field validation?

line 333: the variance explained by this regression is very low. The reasoning should be more conservative.

Figure 9: this figure is impactful. I would be very curious to see at least reflectance data from one multispectral mission (Landsat 8-9 or Sentinel 2) acquired in the same period over the same spots. This would confirm that the multi-transmittance approach provides a sound correction for HDRF.

Section 4.2.3: in general, I like this narrative but I think that the error in Rf estimates should be put in the right context since no field validation data are provided in this study. I suggest at least to compare your estimates with previous results in the same area (e.g. Rowe et al. 2019 and references therein).

Section 4.2.4. Here your results should be put in context with other modeling results (Picard et al. 2020)

Section 5.1: I encourage the authors to briefly review other studies where the "blue hook" is visible (e.g. Naegeli et al. 2015; Di Mauro et al. 2017; Kokhanovsky et al. 2022). 

Line 412: I agree with this point. In fact, a bending in the blue band is displayed also in the imaginary part of the refractive index of ice. More discussion should be added on this point in the manuscript.

I think it's important to mention that often field spectroscopy data display a "upwarding" hook (e,g. Painter & Dozier 2004), that has been also modeled by Picard et al. 2020. This can be also found in imaging spectroscopy data for snow in particular slope/aspect conditions.

lines 428-429: this would be interesting.

line 430 and on: This is crucial because the OPs of dus are strongly dependent on its mineralogy and source area (Di Biagio et al. 2019). Using optical properties from Colorado is clearly a strong approximation here. I suggest to go in more detail regarding the possible differences in dust mineralogy between those two regions.

line 450: I have the feeling that this threshold is quite low. I suggest to justify in detail this choice also showing frequency histogram of NDSI over the study area. Other possible classification methods can be applied to get snow cover from hyperspectral data (e.g. maximum likelihood, support vector machine etc.). Did the authors tested other methods?

References:

Di Biagio, C., Formenti, P., Balkanski, Y., Caponi, L., Cazaunau, M., Pangui, E., Journet, E., Nowak, S., Andreae, M. O., Kandler, K., Saeed, T., Piketh, S., Seibert, D., Williams, E., and Doussin, J.-F.: Complex refractive indices and single-scattering albedo of global dust aerosols in the shortwave spectrum and relationship to size and iron content, Atmos. Chem. Phys., 19, 15503–15531, https://doi.org/10.5194/acp-19-15503-2019, 2019.

Di Mauro, B., Baccolo, G., Garzonio, R., Giardino, C., Massabò, D., Piazzalunga, A., Rossini, M., and Colombo, R.: Impact of impurities and cryoconite on the optical properties of the Morteratsch Glacier (Swiss Alps), The Cryosphere, 11, 2393–2409, https://doi.org/10.5194/tc-11-2393-2017, 2017.

Dozier J. and T. H. Painter, “Multispectral and hyperspectral remote sensing of Alpine snow properties,” Annu. Rev. Earth Planet. Sci., vol. 32, no. 1, pp. 465–494, May 2004, doi: 10.1146/annurev.earth.32.101802.120404.

Kokhanovsky A, Di Mauro B and Colombo R (2022) Snow surface properties derived from PRISMA satellite data over the Nansen Ice Shelf (East Antarctica). Front. Environ. Sci. 10:904585. doi: 10.3389/fenvs.2022.904585

Naegeli K., A. Damm, M. Huss, M. Schaepman, and M. Hoelzle, “Imaging spectroscopy to assess the composition of ice surface materials and their impact on glacier mass balance,” Remote Sens. Environ., vol. 168, pp. 388–402, Oct. 2015, doi: 10.1016/j.rse.2015.07.006.

Painter, T. H., and J. Dozier (2004), Measurements of the hemispherical-directional reflectance of snow at fine spectral and angular resolution, J. Geophys. Res., 109, D18115, doi:10.1029/2003JD004458.

Picard, G., Dumont, M., Lamare, M., Tuzet, F., Larue, F., Pirazzini, R., and Arnaud, L.: Spectral albedo measurements over snow-covered slopes: theory and slope effect corrections, The Cryosphere, 14, 1497–1517, https://doi.org/10.5194/tc-14-1497-2020, 2020.

Rowe, P.M., Cordero, R.R., Warren, S.G. et al. Black carbon and other light-absorbing impurities in snow in the Chilean Andes. Sci Rep 9, 4008 (2019). https://doi.org/10.1038/s41598-019-39312-0

In this paper the authors - as of the title - want to investigate the pitfalls of topographic influence when analyzing snow signatures in mountaineous areas. However, the paper does not focus on this topic but rather gives an overview of how to perform a combined retrieval of snow parameters and atmospheric quantities and terrain influences. This work is of considerable importance and the paper's title should be changed accordingly. The pitfall of not considereing topography when analyzing hyperspectral data be it snow or other applications is well known and is of much less interest than the capability of retrieving the broad variety of paparameters from imagery in an optimization procedure simultaneously. However, for the latter the validation presented in the paper is not really sound and would need to be improved to make a convincing case about the accuracy of the such retrieved parameters. It is recommended to focus the paper on the parameter retrieval algorithm and describe the applied processing steps and the validation of the outputs more concisely.

Some detail comments:

- p3: l88: it is stated that the terrain may be rapidly shifting; this is indeed a problem for high spatial resolution imager - but at the resolution of EMIT such shifts are quite seldom and should not be a problem when using standard DSM products.

- p4, l97: it is claimed that a fully physics based model is employed when analyzing the data. On the other hand the optimal estimation is not based on physical parameter retrieval but rather on mathematical optimization what bears the risk of resulting in non-physical outputs at false minima. This limitation should be explained from the beginning.

- p 4, l114: the term HDRF is used ambigously in this paper (and also in Literature). While Nicodemus defines HDRF as a physically well defined surface property with fully diffuse illumination and directional measurement, Schaepman-Strub 'redefined' the term as the real world hemispherical-directional situation with a anisotropic illumination field. That quantity  would better be described as bottom-of-atmosphere directional reflectance rather than talking about 'HDRF". Please clarify in the paper how 'HDRF' is defined and uesd clearly. The same confusion is also geivn in line 120; integrating the 'Schaepman-Strup'-HDRF will not result in spectral albedo as long as the illumination field is not isotropic while integrating the Nicodemus-HDRF leads to a correct result.

- p6, l141: again: the HDRF only depends on atmospheric conditions if the in-field bottom of atmosphere reflectance is confused with the real HDRF. A BRDF correction of the topographic effects would therefore be of high importance to analyze snow parameters in terrain.

- p8  eq (2): this equation does not include adjacency effects and terrain illumination on a pixel. In a snowy environment this assumption is a very rough approximation of the radiative interaction on a ground pixel.

- p9 l204: the transferability of signatures between Greenland and Patagonia is a very rough assumptions. This should be corroborated by appropriate references or reasoning. The same applies to the transferability of dust signatures from Colorado to Patagonia.

- p10, fig5: just wondering: why are algae only influencing the visible part of the spectrum; what was the measurement database or could it be that the SWIR dat was simply not available? 

- p11 l226: it is stated that 'flat priors' are used in OE, however at the same time it is claimed that the method is fully physics based. How are physical boundary conditions enforced in the OE process then to avoid unphysical results?

- p11 eq. 4: how is the anisotropy factor c retrieved, a LUT is mentioned, what's in this LUT?

- p16 l316: it does not seem obvious to me why liquid water and algae outputs should not be depending on terrain- please give some arguments.

- Figure 9: this is very small.. but the differences between L2A and OE is quite large; why?

- P18 l356: 'a good agreement' of incidence angles is reported, how 'good' is it indeed, how large where the samples, and how about the statics on a per-pixel basis?

- Table3: differences in RF are quite large and one does not know the real value. So, how could you absolutely validate the results and why are you sure that the Multi-transmittance output is more reliable?

- p22: Conclusion: it is again stated that a 'full physics' approach was used, maybe I misunderstand the paper but as far as I can see this is not an inversion of full physics model but rather a statistical optimization with flat priors. 

See attached pdf