Review of “Restructuring landscapes: an adjoint model of the Stream Power and diffusion erosion equation”

In this manuscript the authors reformulate the much-used stream power model with additional diffusion term as an advection-diffusion equation and then apply the adjoint method for parameter inversion. The approach is quite novel, and I am broadly supportive of it. I think this manuscript would benefit from a bit more pedagogic explanation of the implementation of the approach and how the sensitivity analysis functions or what it means. I found the two applications of the model a bit limited and without a real scientific question behind them. This left me thinking if they are the best examples to demonstrate the potential applications of the new adjoint method.

In detail my main comments are:

1. The explanation of the adjoint method is a bit messy. The derivation of the weak formulation of the advection diffusion equation is more appropriate for a textbook, while other details are missing, such as how the Dinf routing is used to match the upstream area to a vector normal to the gradient, and how accurate is it?
2. The model relative sensitivity is a bit obscure to me. I am used to sensitivity analysis requiring a range of parameters to be chosen, such as running the model for a range of Kf, kappa, m, etc. The sensitivity is therefore a function of both the range of potential values of each parameter and the model response. Here however, the parameters are fixed (line 196). I think some clearer explanation of what the authors mean by sensitivity is required, because I am confused.
3. The misfit in the test with known solutions are never quantified, other than the objective function J. Rather than a visual description of how well the inversion does, it would be good to quantify the misfit. This could lead to the potential to consider other objective functions that might improve the model fit but perhaps with the loss of some other quality of fit.
4. The application to the S.E. boarder of the Massif Central is a bit opaque to me. There are quite a few caveats to the application of the model to this location. Would it not be better to apply the model to a landscape where the influence of erosion is a bit “cleaner”? Perhaps somewhere that has been impacted by dynamic uplift, so the ancient landscape is still partially visible?

Below are point by point questions/comments in the order that they come in the text:

Introduction: I think it would be good to also discuss the many models that invert river long profiles for uplift and past climate. Furthermore, it would be worth discussing the timescale of interest. The study by Barnhart is a sensitivity analysis and inversion for modelling processes on shorter timescales than the intended study in this paper. Have there been any sensitivity analysis of the simpler LEMs as modelled by Equation 1? In the discussion some papers are cited that ran 10’s of thousands of models to fit erosion parameters.

Line 43: I think it is too soon in the introduction to discuss “gradient-free methods” without first explaining the past sensitivity analysis that have been done with qualitative methods such as the Morris Method.

Line 62: I would not cite Simpson & Schlunegger (2003) as they solve a diffusion equation for sediment transport, not the advection-diffusion equation described in equation 2.

Line 66: This explanation is confusing. “u” is a unit vector in the direction of drainage, while its magnitude is K_fA^m, where A is a function of the position. I am not sure if the magnitude of this vector corresponds to the speed of knick-point migration, so the analogy might not be useful.

Equation 3: How is the direction of u calculated from the D_inf routing algorithm?

Line 88: It would be good to explain this a bit further: why would it be “physically meaningless”?

Line 96: What is “g”? There are a few “g”s in this manuscript. I assume it is a fixed topography at all the boundaries, but is this a good boundary condition?

Lines 103 to 110: This paragraph is a bit of a clumsy mix of supplementary information. Perhaps it should be redistributed into the rest of the model description.

Line 115: I understand that “c” is a variable, but it is not like the others, as it is a function of the evolution of the model. Can it be called a parameter? I am guessing this is not a big problem, but perhaps some clarification for non-experts in the adjoint method (people like me) would be useful.

Equation 6: another “g”, but this is not the same as the boundary condition “g”. Right?

Equation 13: The definition if J_reg is maybe a bit out of place, or Equation 15 is out of place, as there is a J and a J_reg and then in equation 16 some more terms to a new J. I think the description of the cost term could be much better organised.

Section 4.1: I think this would be better as an appendix. It ruins the flow of the text.

Line 197: I am a bit lost, again likely due to my lack of knowledge in the adjoint method. The sensitivity to the parameters is discussed without varying the parameters. How can this be done? This is not a quantitative or qualitative sensitivity analysis where hundreds to thousands of models are run with different input values the same as this sensitivity analysis. My hunch is that the sensitivity analysis here is not equivalent to that presented by Barnhart et al. (2020). No range of the parameters are tested, so I don’t see an uncertainty in the diffusivity, the erodibility, the exponent “m” or the uplift and initial condition.

Line 200: I think instead of “somehow” you mean “somewhat”. In any case, better to quantify this difference than to use vague qualitative statements.

Figures 2, 3, and 4: I would prefer it if the authors used perceptually uniform colour maps, and even better linear ones, such as “viridis” etc. I am OK with “terrain”, but even then, this is not really the best as it draws out specific topographic elevation that have no real significance.

Figures 3, 4 and discussion in Section 4.1.1: I think that the spatial distribution in the misfit between the inversion and the known distribution of the diffusivity and erodibility could be quantified rather than just explained in the text. Could this not lead to propositions for a better cost function for the adjoint method?

Figure 5: The axis labels are tiny.

Figure 6: For parts (d), (e) and (f) the y-axis label is not very helpful. Part (f) has no label “f”, or title.

Line 261: “peculiar”, I think this is not the word the authors would use if they could write this article in French. Peculiar is something that is weirdly odd. Perhaps “specific morpho-tectonic”, or “unique”?

Paragraph starting on line 265: How can the authors justify the specific values of erodibility and diffusivity chosen for the inversion? Are these not also free parameters? For the application the Wasarch Fault in Utah the choice of erosion parameters is justified based on previous inversions of river profiles, but here there is none.

Summary:

I think that this is an interesting contribution the research into inverse modelling of landscape erosion. I however feel like in order to get the most out of this research the authors could explain their method more clearly and explain how sensitivity analysis in the adjoint method compares to either Monte-Carlo methods, or statistical approaches such as the Morris method that have been applied to short-timescale landscape evolution models (e.g. Skinner et al., 2018; Barnhart et al., 2020). I am not convinced by the two test cases, but this is not really a problem as I feel that this manuscript is principally about describing the adjoint formulation. However, a more convincing inversion would be a bonus.

I hope these comments are helpful and useful.

John Armitage, IFP energies nouvelles

--

Barnhart, K. R., Tucker, G. E., Doty, S., Shobe, C. M., Glade, R. C., Rossi, M. W., & Hill, M. C. (2020). Inverting topography for landscape evolution model process representation: 1, conceptualization and sensitivity analysis. Journal of Geophysical Research: EarthSurface, 125, e2018JF004961. https://doi.org/10.1029/2018JF004961

Skinner, C. J., Coulthard, T. J., Schwanghart, W., Van De Wiel, M. J., and Hancock, G.: Global sensitivity analysis of parameter uncertainty in landscape evolution models, Geosci. Model Dev., 11, 4873–4888, https://doi.org/10.5194/gmd-11-4873-2018

This paper is about inverting topography in the context of fluvial erosion and hillslope processes. There have been some papers about  this topic in the past years. So I would consider it an important topic in quantitative geomorphology.



I saw that the first reviewer already provided a very detailed review. However, I got stuck much earlier and ended up with three major concerns. Two of these are about the general approach of combining the stream-power incision model with the diffusion equation and the third one about the application of the adjoint method.

(1) At least in the traditional form with discrete flow directions, (D8 algorithm), combining the stream-power incision model with the diffusion equation causes severe scaling problems, which make the results dependent on the spatial resolution of the model (Perron et al. 2008, doi 10.1029/2007JF000977; Pelletier 2010, doi 10.1016/j.geomorph.2010.06.001; Hergarten 2020, doi 10.5194/esurf-8-367-2020; Hergarten & Pietrek 2023, doi 10.5194/esurf-11-741-2023). Obtaining parameter values that depend on the spatial resolution from an inversion would be problematic. At the moment, I do not think that considering the topographic gradient instead of the discrete channel slope, as done  here, fixes these problems.

(2) Combining the stream-power incision model with the diffusion equation has a weird effect on channel steepness. The steepness index of the channels increases with increasing diffusivity and becomes considerably higher than predicted by the stream-power incision model alone. The problem is that this combination of models describes a downslope sediment flux from the hillslopes (with conservation of volume), but then feeds the transported material into a detachment-limited fluvial model without a sediment balance. Practically, this means that the material brought into the rivers get the same properties (erodibility) as the bedrock. The effect was described in a recent paper by Litwin et al. (2025, doi 10.5194/esurf-13-277-2025), and the authors finally admit already in their abstract that this model combination is unrealistic. The problem was also presented on a conference recently (Hergarten 2025, doi 10.5194/egusphere-egu25-5035). This interference of erodibility and diffusivity would also have a strong effect on the inversion.

(3) I do not understand the condition div(c) = 0 (incompressibility, line 73) and the "physical" justification given in line 74 does not convince  me. I would even suspect that this condition is wrong. For instance, if I assume constant erodibility and m = 1 in a traditional model with discrete flow directions, this condition (div(A) = 0 in this case) would imply that the catchment size does not accumulate downstream,  which does not make sense to me. In the general case (div(K_f A^m u) = 0), A and u describe the flow pattern on a given topography, while K_f and m are parameters of the erosion model. The condition would then imply that the catchment sizes A on a given topography depend on the parameters of the erosion model, which is unclear to me. As far as I can see, the entire part of the theory about the adjoint method relies on the assumption div(c) = 0 since the adjoint operator would not be just the original operator with -c instead of c otherwise. Theoretically, even a major part of the theory might collapse if the assumption div(c) = 0 does not hold. However, my concerns may be wrong, but I need a solid argument why div(c) = 0.

Sorry that my comments might be a bit harsh. At present, it is almost impossible for me to give an assessment of the scientific quality of the work as long as I am not sure that everything is correct.



Best regards,

Stefan Hergarten