This manuscript presents an ambitious and innovative integration of long-term in situ observations, satellite remote sensing, and a modified SWAT framework to quantify multi-decadal hydro-sediment dynamics in the Ucayali River. The development of SWAT-Amazon and the explicit treatment of floodplain hydraulics and sand routing represent a substantial methodological advance for large, low-gradient tropical rivers, and the assembled observational dataset, particularly the long-term “super station” records and dedicated field campaigns, is a clear strength of the study. The results are compelling and potentially impactful for understanding sediment trapping, recycling, and floodplain controls in the Amazon Basin.

My comments below are intended to strengthen the robustness, generalisability, and interpretability of the findings. In particular, they focus on clarifying the separation between calibration and validation, quantifying uncertainty and equifinality in key inferred budgets, and providing additional evidence that internal floodplain processes are realistically represented rather than inferred solely from outlet behavior.  I examined the Supplementary Material, while it provides valuable methodological detail, it does not address the validation, uncertainty, or equifinality issues raised below. Addressing these points would substantially increase confidence in the reported trapping and recycling fractions and enhance the value of the framework for application to other Amazonian basins.

1. The calibration period for discharge and sand overlaps almost entirely with the reported validation; I am wondering whether the authors could provide performance metrics for an independent hold-out period to demonstrate that the high NSE values are not artifacts of overfitting.
2. The daily timestep is justified qualitatively by slow, subcritical flow conditions, but I cannot find any formal numerical analysis; could the authors present Courant number ranges for representative reaches or demonstrate via timestep halving that peak attenuation and timing errors remain acceptably small?
3. The authors state that rectangular main channels and simple-reservoir floodplains were chosen after testing other configurations, but results from these tests are not shown; could the authors include a supplementary comparison of discharge, water level, and sand flux performance under alternative geometries such as trapezoidal channels or compound sections?
4. Validation focuses on outlet hydrographs, rating curves, and sediment fluxes, yet floodplain processes drive the key findings; I am missing independent validation of internal floodplain behavior using, for example, SAR-derived inundation extent time series, floodplain lake stage records, or tracer-based residence time estimates.
5. The Sobol analysis identifies hf, Cnfp, kfp, and db as influential parameters, but does not explore whether multiple distinct parameter combinations yield equivalent outlet performance; could the authors present dotty plots or behavioral parameter ranges to assess equifinality and discuss how it affects the certainty of inferred trapping and recycling fractions?
6. The reflectance–concentration relationship is calibrated on a limited number of samples and applied basin-wide for two decades; given the acknowledged potential for hysteresis and grain-size variability at the surface, I am wondering whether the authors could quantify the bias or uncertainty bounds under contrasting conditions such as rising versus falling limb or low-water resuspension events.
7. The bimodal fine/sand assumption is conceptually justified, but I cannot find any sensitivity test of budget estimates to the threshold grain size separating the two classes; could the authors show how trapping and recycling percentages change if the cutoff is shifted?
8. The paper advocates extending the approach to other Amazonian basins but does not specify minimum data requirements; could the authors indicate the minimum gauging frequency at a super station, the required number of sediment samples for calibrating the reflectance model, and whether performance degrades gracefully as data density decreases?
9. Channel geometry parameters are held constant over the full simulation period in a dynamically meandering system; could the authors test stationarity of the calibrated relationships using moving-window recalibration or change-point analysis to confirm that morphological evolution has not introduced time-varying bias?
10. The MGB model is critiqued for underestimating Ucayali sediment loads, but no controlled comparison using equivalent forcing and calibration effort is provided; I would encourage the authors to clarify whether this difference reflects model structure or calibration intensity, or alternatively defer detailed benchmarking to future work while softening the current language.
11. Key budget figures such as floodplain trapping, recycling contribution, and sand capture at peak discharge are presented without confidence intervals; I strongly encourage the authors to propagate observational uncertainty and parameter uncertainty through to these final percentages using Monte Carlo or ensemble methods.
12. Several figures use cyan for SWAT-Amazon simulations and marine blue for observations, which are difficult to distinguish; some figures also use slightly different shades of cyan for multiple plots. I suggest that the authors consider using higher-contrast colour pairs or different line styles to improve readability.

The manuscript proposes a novel framework integrating remote sensing data with hydrological and hydraulic modelling to monitor hydro-sedimentary fluxes in the Amazon River.

The manuscript provides a clear advancement in hydro-sedimentary modelling of large rivers and it could be considered for publication on HESS after clarifications and revisions. I have listed below some points asking the Authors to address them to improve the current manuscript.

MAJOR COMMENTS

Line 123/132. The Authors have considered two groups of sediments: fine sediments (10-20 μm, fine and medium silt) and sands (80-120 μm, very fine sands). What is the potential effect in model accuracy of having neglected the material with an intermediate diameter?

Line 172. The Authors mentioned "two radiometric calibration-validation campaigns" for fine sediment concentration. My understanding is that the first campaign (November 2011) was for calibration and the second campaign (February 2017) was for validation. I suggest to better clarify this in the text. Furthermore, the Authors should short discuss about the extendibility to the Ucayali Basin of the data collected in few locations.

Section 3.3.3. The Authors should provide more details about this important point. Have any field measurements been made? In which sections of the basin? Have the cross-sectional variations in sediment concentration along the vertical been considered?

Section 4.1. It is unclear if (and how) morphological adjustements of channel cross-section over the simulation period were considered.

Line 343. I would ask the Authors to shortly discuss how largely Eq.(28) is modifying Manning coefficient using the correction factor.

Line 364/365. I would ask the Authors to shortly provide details about the calibration of Eq.(32).

Line 384. Yamazaki et al (2011) suggested to apply the diffusive wave equation to include backwater effect on water surface elevation.

I would ask the Authors present and discuss the difference between the results from the diffusive wave and those from the kinematic wave in a Supplementary Material.

Section 5.3. It seems that the model was applied (Fig.6) for the same period considered for calibration (09/2009–09/2015). The Authors should better clarify this point. 

MINOR COMMENTS

Line 135. The quality of Fig.1 should be improved.

Line 325. On compound channels hydrodynamics see also: Proust, S., & Nikora, V. (2020). Compound open-channel flows: effects of transverse currents on the flow structure. Journal of Fluid Mechanics, 885, A24. https://doi.org/10.1017/jfm.2019.973

Line 342. How was the coefficient Cfnp calibrated ?

Line 667/668. I suggest to further elaborate the discussion on the Kbed coefficient of erosion susceptibility. You might provide details on that at line 289.

Line 785. List of model parameters. Water kinematic viscosity has two different symbols.