The paper discusses the use of 3 different remote sensing products for the calibration and validation of 3 hydrodynamic models of different scales: AirSWOT to calibrate friction coefficient, UAVSAR to calibrate errors in the intertidal marsh topography and AVIRIS-NG to calibrate sediment properties.

The authors introduce the traditional calibration techniques for such a model, being the use of time series of observations (e.g. water levels, sediment concentration, etc.) and emphasise how remote sensing observations can complement such technique. I believe they innovative character of the research is clearly presented.

Major comments:

Regarding the use of the AirSWOT data: both the calibration and validation are clearly presented. However, whether the use of AirSWOT actually leads to more accurate model results than calibration using time series is less obvious. Can you calibrate the model using the airswot and using time-series to show in a validation period that the airswot actually appears to be better? In the discussion, could you compare your evaluation statistics with other similar hydrodynamic models of intertidal areas? What are typical RMSE values? If needed, the authors could also calculate other evaluation statistics such as the Nash & Sutcliffe model efficiency to allow comparison with more existing studies.

UAVSAR: The method is only very briefly explained how the use of water surface elevation changes can be used to calibrate errors in the marsh topography and the authors refer to another paper where more details can be found. As this is an essential part of the paper, I would like to suggest a slightly more extensive explanation of this method. Furthermore, could you address how the UAVSAR - topography calibration can be validated and why no direct validation of the calibrated parameter (being the marsh topography) is included in the paper? Finally, assuming a uniform friction coefficient  is very likely not to be the case in reality and how do you ensure that the calibration of the marsh topography does not try to resolve these types of errors instead of errors in the marsh topography.

AVIRIS-NG: While the calibration process is clearly explained, I believe more emphasis should be put on validating whether the use of remote sensing indeed improves the model over the use of single point data. The author mentions in-situ observations . I would suggest calibrating the model using the in-situ measurements and independently calibrate the model with a AVIRIS-NG image. Then, independent validation (based on either in-situ measurements and/or AVIRIS-NG imagery of  a different time period) could indicate whether the model calibrated with the AVIRIS-NG image indeed performs better.

Minor comments:

1. Line 134: Could you add the uncertainty on water level measurements.
2. Line 108: Could you explain why small-scale Terrebonne model domain was chosen as a small-scale region of interest? Could you support that this is a representative area?
3. Line 164: could you support the decision for the chosen Chezy coefficients for ocean and marsh platform and on line 186 could you explain why these values differ from the large-scale Terrebone model? Same comment for the values mentioned in line 206.

1. Figure 4 & Figure 7: Spatial patterns are difficult to observe, could you make the map larger (for instance, by rotating the map so that the flight line is either horizontal or vertical)? Could you change the colour scale to stretch the values in the raster map? It seems both negative and positive values on the difference maps never - and + 0.75 m.
2. Figure 5 and 6: Could you make these maps also bigger? I would propose to only show the colorbar for elevation once and the error colorbar once and if needed, drop the grid labels and add a scale (like figure 4). The scale and zoom of figure 2 is a good example. The use of a single colorbar is shown very well in figure 7. In figure 5, subfigures are not labelled.
3. Line 257: unclear which areas are considered critical and why.
4. Line 309: could you refer to the specific figure which supports this statement.
5. Line 267: switch order or ‘always’ and ‘to’.
6. Line 268: switch order of ‘better’ and ‘performs’.
7. Line 269: drop the first ‘best’ and the sentence misses an active verb (online 2017 change ‘as’ to ‘is’).

This study tries to improve numerical model predictions and validation of sediment fluxes between tidal marshes, channels and bays, by data assimilation of high resolution remote sensing imagery.

This topic is worthwhile and important to explore, timely and well suited for the audience of biogeosciences.

The study is of high quality and well written. 

Line 65: could more information been added here. I assume the authors are referring to

    surface concentrations of suspended solids derived from AVIRIS-NG

Line 95: this might be just a detail but I suggest to put species names in italic

Line 125ff: how can the UAVSAR and AirSWOT distinguish between emerged vegetation or the water surface?

    Are there vertical errors ranges that could be reported?

Line 144ff: is TSS surface or depth averaged concentartion derived?

        how applicable is the calibration during different types

        of suspended particles during high and low flow conditions?

Line 159: what was the grain size, what transport equations were used?

      how was the bed initialized, 1- or multiple layers?

      what was the active layer thickness?

    was the option for mixed sediments used?

    how was the non-cohesive/cohseive boundary defined?

Line 165: is it correct to assume that for tidal channels/lakes and bays 

    the same chezy coefficient was used? did the author try a spatial varying chezy?

    which wetting and drying scheme was used?

Line 170: I assume ws is calculated from the median diamter and the sediment density

        i assume the parteniades krone relation is used for sediment pickup please inidicate?

        see comment above what equation was used for sand

Line 175: similar comment as above why was only one muddy sediment class in the bed considered?

        for instance consolidated clay lenses can possess high crit. bss.,, .. did something like that occur?

        how well was the inital stratigraphy incorporated in the model?

Line 185: is the marsh platform chezy also representing vegetation?

Line 199: what kind of data was provided.. suspended sediment concetration,..?

Line 205L was the initial sediment distriubtion unifrom...? was a spinup for the bed tested?

Line 215: see comment above why was no spatial tunning test? 

        this could also improve fig.5?

Line 240: is the RMSE calculated over an entire M2 tide or only during the time-slice the picture was taken?

Fig.7: althouhg the model result are very impressive, the predicted error in SSC is still between 30% - 50% 

    of the mmeasured range, for what conditions in the tide is this representative, is this the best or worst case?

    i think fig.7 could be improved since open water or marsh area are difficult to distinguish?

    if i interpret the results correctly the biggest error seem to appear in shallow areas?

Line 295: was a finer mesh tested,.. was an unstructured grid tested?

Line 305: see comment above,.. very low water levels and gradients,.. will make the mini. water depth and flooding and drying scheme relatively important?

Line 320: how did the marsh microtopography influence the wetting and especially drying of the interior, i.e. Deb 2023,.. used an additional porosity to limit ponding caused by submesh channels?

Line 370: it is unclear how the davg sediment conentration predicted by D3d was correct to compare to the remote sensing product.

I strongly agree with the central argument of this paper, that spatial information from remote sensing provides critical data for calibrating and testing numerical models of coastal wetlands. The paper reports on results of an experiment in which 3 remote sensing products were used in conjunction with modeling of a region of coastal Louisiana to evaluate the value of combining these approaches. Overall I think the analysis is thorough and informative, but the text would benefit from editing for clarity. Most of my comments are editorial.

Comments:

L18: “Peter Sheng et al.” should just be “Sheng et al.”

L19: There is a recent paper by Temmerman et al (2023; Reviews of Marine Science) that would be appropriate to cite here.

L48: Does Gross Primary Productivity need to be capitalized?

L60: change to: “, and coastal wetland above-ground biomass …”

L106-112: The statement is made here that there are 3 models at different scales, but it seems that the scale of the large-scale Terrebonne model and the Atchafalaya model are essentially the same.

L144: “TSS concentration from the …”

L145: Should the phrase “and vegetation structure are produced” be deleted? It seems the same point is made in the next sentence.

L162: What is the resolution of the usSEABED database used to specify the initial sediment distribution in the model? Why use mud and sand (2 classes) in the large-scale Terrebonne model and mud, silt and sand (3 classes) in the large-scale Atchafalaya model?

Figure 2: Perhaps the caption should refer to Figure 3 for the spatial relationship among the 3 imaged regions.

L172-176: What value was used for the erosion parameter? Why wasn’t this parameter varied in the calibration runs? Its effect is different from the critical shear stress.

L178: CRMS station 421 is referred to in this paragraph, but the CRMS acronym is not introduced until the end of section 2 (L226).

L182: Here and elsewhere, rather than refer to the bottom and upper boundaries of the model grid it would be better to use terms south and north boundaries.

L183: Where is Trouble Bayou and how far is that from CRMS station 421?

L186: Why is the Chezy coefficient for the channels set here (55) while the Chezy coefficient for the channels in the large-scale Terrebonne model setup allowed to vary (between 40-45) and over a smaller range of values?

L189-190: Couldn’t a change in vegetation roughness affect the water-level changes in addition to marsh topography?

Table 1: It could be helpful to provide values of the calibrated parameters (where appropriate) in this table.

Figure 3: It would be helpful if boxes were used to show the domains of the 3 models in relation to the remote sensing.

L214: “and the corresponding remote sensing …”

L216: “allow us to tune model parameters …”

L241: Delete “For the” before “Atchafalaya model results …”

L246: Why was a Chezy coefficient of 65 not considered in the Terrebonne model? Are any time series available for comparison with the model?

L252-3: “water level change in the southern area”?

Fig. 7: It would be helpful to add the date of the image in the figure (as in, e.g., Fig, 8) or in the caption. For the model calibration runs shown in this figure, what settling velocity was used for the results shown in Fig. 7A and what critical shear stress was used for the results shown in Fig. 7B?

L271: Add a reference to Fig. 8 after noting the date/time of the imagery.

L274: Add reference to Fig. 8B after providing the RMSE of 35.88. Are there any in situ measurements of SSC available for checking model values?

Section 4.1-4.3: Are there any reasons to think that the Chezy coefficient might not be uniform?

L285: Does “lower half of the flight line” = “southern half of the flight line”? If so, it would be clearer to refer to southern half.

L285-290: Could the comparison with Manning values be included in results instead of discussion, or is the Manning value so well known that the agreement is a useful point of discussion?

L306: “The validation of the water levels across the domain …further confirms the goodness of the calibrated friction coefficient” seems like an overstatement given that the previous paragraphs described portion of the model domain where the modeled and remotely sensed water levels do not agree – for reasons that may be unrelated to friction coefficient, but the disagreement makes it impossible to evaluate how well the friction coefficient works in those regions.

L316-327: The argument that friction plays w marginal role in affecting water levels on marsh platforms merits more discussion, since otherwise that seems like a reasonable alternative to arguing that marsh platform topography is poorly quantified. Is there a correlation between where the topography must be adjusted and vegetation characteristics on the marsh? Is it also possible that the model isn’t resolving microtopography that affects water fluxes? How much was the topography altered to improve fluxes. Were the values realistic?

L333: change “worst” to “worse”

L337: Are any data available to evaluate this possibility?

L349: Was TSS sampled just one time and at one location? If so, this doesn’t seem like a robust enough test to declare the in situ sample to be more in error than the modeled value. What is the TSS value at that time and place in the AVIRIS-NG data? How much spatial and temporal variability do the model and remote sensing suggest?

L356: Consider revising to “due to flocculation which increases settling velocities compare to …” In any case, the settling velocities used in the model for mud are effectively floc settling velocities.

L360: Not clear what is meant by:  “errors might be related to some the bathymetric modification”

L361: The channels were enlarged in the model?  “might have generated”

L363: “inherent to the model. Although Delft-3D has 3-dimensional …”

L365-366: replace “tri-dimensional” with 3D and “bi-dimensional” with 2D

L371: This paragraph might be better combined with the one before.

Fig. 9: It would be much better to use the same vertical scale for both profiles. Were the wave conditions much higher on Aug 19 (red curve) than on Aug 17? It seems important to recognize here that optical properties of sediment in suspension is strongly controlled by sediment size, and that the vertical profile of the finest, most optically active fractions might be more uniform that that of coarser bed fractions.