This manuscript describes an interesting and creative approach to measure sediment-height changes using radar-interferometric time series analysis. The author attempt to exploit the high temporal resolution of SAR data to better understand sediment dynamics. The authors rely on topographic residuals (or sometimes called DEM errors) and their changes through time to measure small height changes of sediment deposited in large rivers. This is an interesting approach, because standard radar interferometry will not allow to track height changes due to land-cover changes. This appears to be the first application of topographic residual analysis to sediment-transport studies. While this is creative, it is also tricky and has many caveats (see below). The authors partly field validate their measurements with general budgets, but not with measurements at the timescale of the SAR data and the presented signals have no uncertainties.

The study focuses on the foreland of the Himalaya in the Ganges plains that show a strong sediment-flux dynamics. While there are several creative and interesting thoughts in the manuscript, there exist several points that need structuring and clarification.

In the following, I am listing several points that should be looked at and considered during a revision process:

1) Methodological description. The method section starts out by explaining scattering and polarization and then explains amplitude measurements (the description of amplitude is after the scattering section – this should be reversed). This is followed by some backscattering analysis of rivers using pre-processed GRD data obtained from Google Earth Engine. While this is an interesting exercise (including Figure 3), it is irrelevant to the topographic residual (or DEM error) used for height-change mapping. These topics (several pages of text and figures) is also not picked up on in the Result, Discussion, and only somewhat in the Conclusion section.

The section on SAR coherence is important, but it needs to be clarified what coherence is shown – averaged spatial coherence or temporal coherence (as it mostly used because it accounts for the temporal decay of coherence or decorrelation – see Figure 4).

There are two method section – this is awkward. Here is space to consolidate and significantly shorten the manuscript (to make room for more important analysis – see below).

Coherence Thresholds: I am not certain where the authors picked their coherence thresholds from, but these are not typical (they are too low). The statement that coherence above 0.3 is useful cites a study Cigna and Sowter, 2017) that uses ISBAS (a different method) and this is not relevant for SBAS (or NSBAS).

SAR-Data characteristics.Throughout the manuscript, the authors refer to 20m and 100m data. This is very unusual. You usually give the number of multilooks (range/azimuth), because this better reflects data characteristics. There is certainly an equivalent in square area, but the multilook values are more common and it is also not exactly 20 or 100 m.

I am puzzled by the statements about SBAS. They argue they have used SBAS, but the method implemented by Morishita in LiCSBAS is NSBAS that can also deal with disconnected networks (but require additional terms). The networks shown in Figure 8 and 9 are all disconnected. You can not use SBAS to work with them in a reliable manner. Connected networks are always more reliable than disconnected networks during an inversion. In Figure 9 there is the note that the network has been linked though linear fitting. Is this not NSBAS? The section on the network inversion needs more work (and also more information for the reader to see number of ifgs, images, baselines and coherence history).

2. General information on data, processing, and methodology. The authors never tell us what scenes (track/frame/bursts/swath) and how many connections have been used. What is the number of interferograms? It is also not clear what software has been used and what parameters. I assume LiCSBAS was used, but no information is given on the SAR processing and interferogram generation.

3. Topographic Residuals or DEM errors. This is the core, creative part of the study. The authors should carefully introduce the topographic residuals and their caveats. The authors are also not the first ones using topographic residual for deformation measurements (but likely the first one to apply it to sediment-height dynamics). I remember there was a study to use topographic residual from ALOS data to measure lava thickness: Measuring large topographic change with InSAR: Lava thicknesses, extrusion rate and subsidence rate at Santiaguito volcano, Guatemala, https://www.sciencedirect.com/science/article/pii/S0012821X1200194X They do something similar but using the ALOS-L band and they make sure to use large baselines (see below) and use synthetic models to get a better understanding of uncertainties.

The study by Bombrun et al., 2009 (10.1109/LGRS.2009.2026434) is also something to look at. Importantly, topographic residual is a tricky beast. It is a relative error. It is relative to the network and relative to space. That is, changing the network structure or moving the reference point will result in different topographic residuals.

Reference Point: I am surprised to see the reference point to be far away from the actual stream studied. The coherence is low and it looks like there are disconnected components – which is a problem for unwrapping. How were the disconnected components connected?

The authors cite Du et al. 2016 and this is a detailed study of topographic residual measurements. Du et al. point to several of the above problems, especially the network structure. In order to estimate the impact of the network (and individual connections), one can randomly (?) remove connections to observe how the topographic residual changes. This is also a useful way to estimate uncertainty of the topographic residual.

I am not fully clear how the networks shown in Figure 8 were connected, but the topographic residual is likely to be different between these years just because of a change in network structure (the magnitude of this signal can be identified or modeled).

Most importantly, I am puzzled by the approach to keep the smallest baselines. Topographic residuals are larger for large baselines – in other words, baselines exerts a significant sensitivity on topographic residuals. For interferometric measurements you are aiming at very small baselines to minimize the topographic effect (standard InSAR). I ask the authors to think about the signal they are looking for (if I understand them correctly): Larger baselines would be more appropriate for measuring topographic residual, because the measured signal is larger (see Figure 4 in Du et al.). If you confine the perpendicular-baseline tube to a very narrow range, you are optimizing the network for interferometric purposes, not for topographic residual measurements. This may sound counterintuitive and I may be missing parts of the author’s explanation, but to enhance the topographic residual signal you are aiming at long perpendicular baselines, because these are more sensitive to topographic changes (see equation 15).

One important issue only briefly addressed in the manuscript is atmospheric phase screening or tropospheric delay. The author’s mentioned that they have used GACOS to correct their data, but no magnitude of the correction is shown and no dynamics of the tropospheric signal. This is important, because the tropospheric delay signal may easily exceed the topographic residual signal. Again, I urge the authors to look at Du et al. – they also have looked at different atmospheric delay patterns. The monsoon season in the Himalayan foothills is characterized by heavy, localized rainfall that may generate extreme delay signals. These turbulent components are not corrected for with ERA5 or GACOS data. However, the general water vapour content is captured. A simple question to ask: Is the topographic residual signal the same without any atmospheric correction (or a different correction)? A more careful treatment of the atmospheric correction and their impact is important, because this signal may have the same amplitude. This is also what Fattahi and Amelung (2013) stated in DEM Error Correction in InSAR Time Series; Heresh Fattahi and Falk Amelung, 2013 https://ieeexplore.ieee.org/abstract/document/6423275 (this is also cited).

I mentioned it before, but I am surprised about the treatment of the coherence and connected components. Figure 16 shows the lower multilooking data (what the authors call 20 m resolution) and it looks like as if the individual rivers are not connected and have not been unwrapped together. The reference point appears to be outside the center stream of the plot. Is there a special treatment for connecting the components? The higher multilooking data (called 100 m resolution) appears to be connected but shows different signals. It is difficult to interpret these plots without additional information (also on the network). Maybe a coherence matrix through time would be helpful to better understand the interferometric network. I point out that other researcher have made careful statements before:

“Noisy acquisitions with severe atmospheric delays or decorrelation noise could potentially bias the estimation of topographic residuals, the average velocity or coefficients of any temporal deformation model.” (from “Small baseline InSAR time series analysis: Unwrapping error correction and noise reduction” by Zhang Yunjun, Heresh Fattahi, Falk Amelung , https://www.sciencedirect.com/science/article/pii/S0098300419304194

4. The Discussion starts well after 480 lines into the manuscript. It is very short and touches upon some relevant sediment-dynamics points. But none of the uncertainties of the topographic residuals or the tropospheric delays are discussed here. The section on future prospects is certainly important, but should not take up 1/3 of the Discussion section.

5. It took me a while to understand the vertical rates (I am still not certain that I understood the authors explanation). The Vertical rate are derived from the linear fit of the annual topographic residuals? Is the data in Figure 15 the slope of that linear regression? Are there uncertainties associated with that fit?

6. There are several useful figures in the manuscript. In general, it may be useful to convert the figures showing radians to mm, because the text argues about deposition (or sedimentation) rates in mm.

There is no Figure 18, although it was mentioned several times.

Overall, I see large potential in this study. It will require additional work if this is supposed to become a landmark study to propose topographic residual measurements for estimating sediment dynamics for current and future SAR missions (as suggested by the Discussion section). A thorough investigation of the impact of the interferometric network structure (including perpendicular baselines, temporal baslines, number of connection), tropospheric impact, and inversion approach will help to better understand boundary conditions and measurements uncertainties.

This is the first time I am reviewing the manuscript entitled: “Sediment aggradation rates for Himalayan Rivers revealed through SAR remote sensing”. The authors describe a method to use differential residuals of SAR data to detect mm-scale elevation changes in the range of 20 mm/yr in four seasonally dry rivers of Nepal. They claim to “demonstrate the feasibility of InSAR techniques in geomorphological monitoring”. The technical and geomorphological aspects of this study are generally interesting and have potential to bring forward this research field.

As I am not a specialist in SAR analysis, I will focus on the structure and storyline of the paper and the geomorphological implications/ interpretations.

Goal of the paper

First, the general goal or main storyline of the paper is not clear to me. I see two possibilities:

1. The goal is to prove that the suggested methodological approach can detect sediment dynamics in the selected rivers, or
2. The measured and processed signals support a geomorphological process that can now be understood or described better.

However, possibility 1) would require some prove that the results of the suggested methodological approach are true or at least reproducible and consistent with other methods.

Possibility 2) would require a clear story/ concept, of which processes should be described and supported. Then, the description of the methods should not be the main focus of the paper but rather be described as a tool to solve the stated geomorphological problem and the observed processes must be discussed in detail.

The conclusions state that this manuscript develops a “novel approach”, provides “detailed, high-resolution geomorphological data”, shows a “significant sediment aggradation” (is it statistically significant?) and that “this approach adds a new tool”. These statements should be supported clearly be the main part of the manuscript.

Structure

In general, the readability of manuscript could benefit from a clearer structure. There are two method sections (methodological background and methods applied in this study). This causes repetitions. The methods should be focused only on things that are needed to solve the focus problem of the study. Starting with the general principal could help non-SAR-specialists to follow. Additionally, some results and interpretations appear in the methods section (which polarization amplitude is higher, the effect of soil moisture, sources of errors and uncertainties…). Vice versa, in the results section, some things are shown that have been presented in the methods before.

The introduction and methods sections take 19 pages, results 3 pages, discussion 4 pages and conclusions 0.5 pages. However, the structure of the manuscript should somehow fit the scope of the paper. It might be possible to increase conciseness by re-evaluating, if all 16 figures are necessary to support the main goal.

The discussion about uncertainties appears as an own section before the section “Discussion”. The section 8.1 “Validation…” consists of one paragraph giving an outlook on further research and only a brief comparison to other sediment aggradation rates. This could be elaborated in more detail.

Geomorphological processes

The positive elevation change is highest close to the mountain range. How can you exclude influences of topographic uplift of the mountains also raising the riverbeds? Fig. 17 touches this aspect by comparing the riverbeds to the surrounding areas. How can you make sure that the differences in elevation change are not influenced by the different datasets and processings (20 m vs. 100 m resolution)?

Following your analysis, the surroundings close to the mountain margin lowered 60-90 mm over the studied time period and the river channels raised 70 mm. This means that the channel raised 130-160 mm relative to its surrounding. Is there a way to verify this?

You interpret a “channel avulsion every few hundreds of years”. If this is true, this should be possible to see in the geological record, detectable by geophysics or in outcrop profiles, and it might even be possible to date avulsion layers. Without further proof or discussion, this hypothesis stands alone.

If the riverbed is incised into the surrounding floodplain, there must be an erosive process. How and when does erosion happen? If I understood right, then during monsoon there is aggradation and during the dry season there is no sediment change. If finally, the channel is filled up and avulsion happens, how does the channel erode into the surroundings again?

I am not an expert in remote sensing or interferometry, so my focus will be on asking questions which I feel the text could benefit from addressing (either to help non-specialists such as myself to understand the paper, or to address the question directly).

The authors use interferometric techniques on repeat SAR observations to estimate sediment aggradation rates of gravel bedded rivers at the base of the Himalaya in the Ganges plains. They compare these rates with subsidence estimates from the local floodplains in order to show a very interesting, and novel methodology. They use these results to explore flooding and avulsion risk in this area, and discuss ways in which the method could be further validated.

Major Comments:

I enjoyed the paper, and the methods developed here are very creative and interesting. I found the quality of the science to be good. The presentation quality is the biggest issue for me, as the paper is confusingly structured, has some grammatical issues which make reading it unclear at times, and has calls to figures and equations in an order which distract from the core message of the paper.

1. The goal of the paper appears to be to establish a methodology for using interferometric analysis of repeat SAR data to estimate high resolution aggradation/subsidence rates in an alluvial environment. However, the results presented are not compared with any alternative estimates of topographic change in the study area, and so the validity of the results are unclear. A comparison of the estimated aggradation rates for other dissimilar fluvial environments like the lower Ganga River and the Floodplain of the upper Yamuna Valley are presented as being on the same order of magnitude as their results, but this does little to support the methodology. This technique might provide an amazing new tool for assessing high-resolution topographic changes associated with fluvial processes using publicly available data (awesome!), but a lack of ground truthing or valid comparison with other methods for the results really hurts the papers ultimate impact. If no further validation is possible, I think the paper needs to highlight the preliminary nature of the results so as not to be cited as a source for known aggradation/degradation rates, and soften statements such as “We successfully mapped millimeter-scale elevation changes in (four) river channel(s) over a ~15km stretch…”

2. The paper is challenging to read due to repetitious information and confusing narrative structure, grammatical issues, calls to figures that don’t exist (e.g. figure 18), and calling the figures and equations in a loosely structured order.

Figures: To be clear, I don’t believe all figures and equations must only ever be called in order, but the paper would benefit greatly from trying to streamline the readers experience somewhat. The current structure results in a lot of searching around trying to match up the text with the figures/equations. Additionally, many figures include imbedded text for the axes and legends that are so small they are either challenging to read when printed, or are just unreadable even when zooming in on a computer.

Grammar and consistency: There are many examples of bad grammar and sloppy editing which make the paper challenging to read. For example: using the acronym “LOS” on line 241 and in Figure 9, but defining it on line 328, in Figure 12, then again on line 383, and 467. An example of a grammatical issue is: “Azimuth is along satellite fly track direction, range is across satellite fly track direction”. The paper would greatly benefit from a copy edit. I have included many examples of copy editing issues in my line edits, but they are concentrated at the start of the paper, and are not comprehensive.

Narrative structure: The methodological context followed by the authors specific methods results in some repetition, and there are concepts in the methodological context which do not seem to impact the core thrust of the paper. It seems to me that it could be shortened and focused, although this may just be a product of my lack of experience in the field of satellite based remote sensing.

3. My understanding after reading the paper is that you do interferograms during the dry season, and across the monsoon season, but are unable to resolve interferograms during the monsoon season. However, I’m still not entirely sure how the authors deal with phase ambiguity if changes in elevation that occur across the monsoon season are quite large. Is my understanding correct? Is there data loss in the interannual interferograms associated with phase ambiguity? Can you provide a length scale of observable movement before the phase ambiguity is surpassed? Additionally, the authors see a fair amount of aggradation during the dry seasons in the river channel (fig 16), and explain this as “due to a combination of noise and varying perpendicular baselines caused topographic sensitivity variation.” I don’t understand that explanation, especially when the magnitude of the aggradation is so consistent, doesn’t look like a noise signal, and sometimes looks like it has a similar slope to your inter-annual aggradation rates. Can you clarify my misunderstanding of the work, or address this concern with the data?

Line edits:

L36: “where river channels”

L66: “and are labelled rivers 1-4”

Figure 1: “are approximately 15 km in length, and 300 m in width”

L107: “bars result in stronger”

L117: “Azimuth is along the satellite flight path, and range is perpendicular to the satellite flight path”

L121: “Amplitude is calculated following Eq. (5-8)”

Figure 2: Why are the bar graphs in e-f descending rather than ascending. Not sure if this is some standard I’m unaware of, but it confused me.

Figure 3: I recommend bigger text, hard to read.

Figure 4: bigger text

L241: Define “LOS”

Figure 5,6,7: bigger text

Figure 8,9: way bigger text for the legend!

L330: Figure 18?

Figure 10, 11, 12, 13: Bigger text

Figure 14: it’s interesting that you have larger uncertainty for river 1 and 2 which have more consistent data, and less uncertainty in river 3 and 4 which are much more noisy looking. Can you comment on this? Text size is ok here, but could still be bigger.

L445: Figure 18!

Figure 16, 17: Bigger text. Also where is location E on the map?

L468: Figure 18!

Section 8.3: This is a very interesting hypothesis about the relation between aggradation rates and avulsion timing. Can you find any evidence to support that in the sediment record near these rivers, or just another citation that might support this idea?