This manuscript investigates an important component of the Earth system for understanding radiative budgets at the land surface, which has significance for land-atmosphere coupling (carbon, water, energy) --- the influence of an interactive atmosphere and land surface radiative transfer scheme. It is limited to vegetated canopies with certain assumed properties but the authors investigate a range of idealized scenarios to quantify the effect of these interactions. Overall, the manuscript is well-written and structured. It was relatively easy to follow what the authors did and what they found, which is challenging given the complexity and technical nature of the topic. I have provided a few general comments that I believe the authors need to consider before it is suitable for publication and a number of minor comments too. It was probably on the border of minor and major revisions - I opted for major as it should give the authors ample time to address the comments.

General Comments

The introduction is written very well and the knowledge gap is identified clearly. The only recommendation I have is to add a little bit more introduction (background/discussion) around how vegetation structure has been studied in the past in the context of surface albedo, and by what mechanism it may impact surface albedo. You present two questions toward the end of the Introduction. Question 1 is given plenty of solid background. However, Question 2 has little.  

Section 3.3.5: “The effect is quantified by the solar radiative forcing ∆F at the canopy level between simulations with a fixed cloud-free albedo and an albedo that accounts for cloud–vegetation-radiation interactions”. I’m not convinced this is the right way to calculate this effect. Essentially, the difference here is (probably) just showing the huge difference in incoming solar radiation properties (mainly the diffuse ratio) between a cloudy and cloud-free atmosphere. This does not strictly isolate the cloud-vegetation-radiation interactions. Instead, it shows the direct effect of clouds. That's why the ∆F values are so large. You may want to do something similar to the simulations shown in Figure 2, where you run coupled and uncoupled simulations with and without clouds (over your range of optical thicknesses in Figure 9). Or reframe the section a little to clarify exactly what’s being quantified and shown.  

- Related to this comment is your conclusion section (L457-463). I don’t agree with the statement on L461, as I don’t believe your comparing coupled and uncoupled simulations, instead your comparing cloudy and clear-sky conditions (both in coupled mode).  

The language used in the manuscript is clear and consistent, yet at times very technical. I suggest making some statements more or adding clarifications to help a more general audience understand what you have done and the significance of it e.g. what does this result mean for understand land-surface radiative budgets or land-atmosphere coupling (e.g. carbon, water, energy), both now and into the future where certain properties of the land surface and atmosphere are expected to change. This is especially important when you're trying to convey a key message of the results – like in the parts of the results/discussion, conclusions and abstract. I think overall the paper would benefit significantly from this, making it much more impactful to a wider audience outside the radiative transfer modeling community.

I think there needs to be more discussion or quantification of the impact of your assumptions on your final results. This is generally lacking. For example, in your simulations “clouds were assumed to be homogeneous”, only a single vertical profile of atmospheric conditions was used, assumptions embedded within the SCOPE2.0 model (e.g. it ignores woody elements, it is horizontally homogenous, has no clumping), assumptions of your canopy composition inputs (chlorophyll content, etc.). This is necessary before someone can decide to use your simpler parameterization in NWP or GCMs.  

Minor Comments

Can you change Equation 4 to integrate between 0.4 to 2.4 um? I can see that you clarify this in the text, but I think the stated equation needs to be the actual one you use throughout the results, and any caveats to the formal definition can be stated in the text.  

I presume you switched off the vegetation chlorophyll fluorescence calculations in SCOPE2.0? There is additional computational requirement when including fluorescence. Can you clarify in the methods whether this was on or off? 

In the text of section 2.2.2, the soil brightness parameter B = 2. However, in Table 2, B=0.5. Can you clarify which was used?  

SCOPE2.0 also requires forcing inputs of meteorology e.g. temperature, humidity, wind speed, etc. What inputs did you use for the SCOPE simulations?  

In Figure 2a and 2b, do the colors represent the same simulations? From what I can understand, they are completely different simulations e.g. the red line in 2a is “uncoupled, including clouds”, but in 2b the red line is “coupled, neglecting clouds”. I think you need to use different colors to avoid confusion here.  

I suggest reducing the y-axis limits in Figure 3g and 3h (perhaps from 0.5 to 1.5), to make the differences more clear.  

Should the black line (tau=0) also be plotted in Figures 3a, 3b, 3g, 3h, Figure 4c, and 4d? I know it will only be a straight line = 1, but I think it is still important to plot it for consistency and clarity.  

Can you clarify in the captions of Figure 3 and Figure 4 the LAD used. That needs to be highlighted more clearly as the difference between these two figures. You could even include text annotation inside the subplot to make it more clear to the reader.  

Please go through and re-check the spelling. There are many instances where words are misspelled or grammar needs revising (e.g. L57, L367, Section 3.3.5 title, L423, L455).  

Section 3.3.6: Can you provide some more detail on why a simple parameterization is useful or necessary? Given the complexities and non-linearity of these relationships in your results, one could argue that use of these coupled, spectrally-resolved RT models is necessary for a more complete and robust representation of the land surface radiative budget and albedo effects.  

Section 3.3.6: Your equation 11 has fdir as being wavelength dependent, yet the calculated broadband albedo is not. Should the fdir input on the right-hand side actually be the average broadband fdir? Or should the broadband albedo actually be spectral albedo?  

Section 3.3.6: The other caveat of this parameterization is that it is limited to the idealized conditions of your simulations. So, it is subject to your other assumptions e.g. homogenous cloud cover, assumed vertical profiles in the atmosphere (aerosols, temp., humidity, gas conc.), assumptions in SCOPE2.0 (no woody elements or canopy clumping considered, fixed soil background and moisture conditions), etc. In addition, it requires LAI to be greater than 2, which is not the case for large portions of the land surface and many times in the seasonal cycle of both deciduous forests and grasslands/croplands.  

- These caveats must also be made clear in the conclusions (L464-471).  

L442-443: “The LAI was found to have the largest impact on the resulting spectral and broadband α”. I disagree with this statement. The sensitivities you have evaluated across different inputs are not necessarily comparable, as the various inputs have different units, meanings, and ranges over which they are evaluated. More importantly, I can see from Fig. 6 a, d, g that for a zenith angle of 25o and optical thickness < 2, the change in LAD has a much larger effect on albedo (a change of up to 0.09) than the change in LAI from 2 to 5 (a change of less than 0.02). I think this statement needs revising and perhaps reconsider how you quantify which inputs have the “largest impact” i.e. show most sensitivity.  

L449-450: “This is caused by the dominating fraction of isotropically reflected radiation from the surface that is less sensitive on the incident angle of the radiation compared to the reflection of direct radiation.” Can you add a clarification for a more general audience? I believe a more simple statement is that “as the incoming radiation becomes more diffuse, the effects canopy structure (LAI, LAD) and solar zenith angle on surface albedo become minimal”. 

L9-11: “The greatest albedo increase is observed during the transition from cloud-free to cloud conditions with a cloud optical thickness (τ) of about 6”. This statement could be misinterpreted as the greatest sensitivity occurs when τ is around 6. I think what you really mean is that the greatest sensitivity occurs in the range from cloud-free (τ =0) to cloud optical thicknesses of about 6.