the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 14 Jul 2026
Climatic, tectonic and landslide-dam signals preserved in alluvial terraces of the Naryn Basin, Kyrgyzstan
Abstract. Fluvial terraces can act as geomorphic markers of past environmental change. Although they are commonly interpreted in the context of a single driver, multiple climatic and/or tectonic processes may occur simultaneously in nature. Here, we test our ability to interpret terrace sequences with potentially complex formation histories by studying the Naryn Basin in the central Tien Shan, where glacial–interglacial cycles affected land-surface processes, numerous active faults accommodate crustal shortening, and a large landslide temporarily dammed a lake. We investigate the relative contribution of these terrace-formation drivers by mapping terrace profiles, providing new constraints on the terrace chronology, and numerically simulating terrace formation in response to climate change and lake drainage. Tributary terrace profiles record local deformation in response to faults and a regional concave-up pattern that could be explained by lacustrine sedimentation and subsequent base-level fall induced by lake drainage. Terrace ages cluster between 15 and 20 ka, correlating with both deglaciation following the last glacial maximum and lake drainage. Our modelling, together with the spatial distribution of modelled terraces, indicates that lake drainage had a strong, but spatially restricted impact on river long-profile evolution, whereas Pleistocene climate triggered regional terrace formation. By integrating numerical modelling of alluvial river long-profile evolution with detailed mapping and geochronology, we present a robust approach to establish direct links between environmental change and the resulting terrace record.
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Status: final response (author comments only)
- RC1: 'Comment on egusphere-2026-3489', Anonymous Referee #1, 10 Aug 2026
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RC2: 'Comment on egusphere-2026-3489', Julien Charreau, 17 Aug 2026
The paper presents an innovative approach to modelling and better understanding the formation of alluvial terraces. The Naryn Basin is a relevant and interesting case study where the authors have also tried to better constrain the geochronology of the abandoned alluvial surfaces. Overall, the work is impressive, and I believe that the data and model results will be of interest to a broad community within the Earth sciences.
However, despite my overall positive opinion, I think that the manuscript requires several improvements and modifications before it can be considered for publication.
First, I suggest clarifying the objectives of the paper in order to strengthen its relevance to a broader scientific community, rather than focusing primarily on readers interested in the Tianshan region. Similarly, the discussion is somewhat restricted to the studied case without much opening to broader and more general implications regarding terraces formation.
Second, I encourage the authors to provide a clearer and more detailed presentation of the model parametrization, which is sometimes difficult to understand, at least for a non-specialist such as myself. In particular, the choice of parameters and their respective values could be, sometime, explained more explicitly.
Third, the cosmogenic-nuclide data and their interpretation also require further discussion and clearer presentation. At times, the manuscript is difficult to follow because some figures are missing and the cosmogenic data are not always presented in a sufficiently clear and accessible manner. Improving the presentation of these data would considerably facilitate the reading and interpretation of the manuscript. I also suggest considering a Bayesian approach to interpreting the abandonment ages of the terraces. Such an approach may provide a more robust framework for estimating the ages and would help avoid the rather suggestive and qualitative age assignments currently proposed.
Fourth, the discussion about the geochronoly needs to be revised. The age grouping proposed by the authors is tentative because it relies on an incomplete literature and is based on their age assignment which is, as I said, qualitative and suggestive. The derived conclusions are therefore not robust. In particular, the conclusion that terraces were mainly driven by climate contradicts a recent study carried out in the Eastern Tianshan. Similarly, the interpretation of the terrace shape and comparison to the model results is rapid and may need more explanation and developments.
Overall, I found the discussion to brief with several strong statements and conclusions not sufficiently supported/explained.
Nevertheless, I consider the study promising and potentially valuable, but I believe that the points above should be addressed to improve the clarity, robustness, and broader relevance of the manuscript.
Below I provide more details regarding each of these issues.
The introduction needs polishing
The connection between the paragraphs and the overall flow of the introduction should be revised to (1) strengthen and smooth the logical progression between the paragraphs and (2) clarify the objectives of the paper. Indeed, it is not entirely clear what the primary objective of the study is. Is the goal to address the specific challenge of understanding the complex processes controlling terrace formation in the Narayani Basin? Or is to improve our general understanding of terrace formation, using the Narayani Basin as a particularly suitable (or even ideal) case study? Clarifying this distinction would help readers better understand the motivation and scope of the work.
Age assignment of the terrace
The geochronological constraints on the terraces are fundamental to calibrating and validating the numerical models. It relies mainly on 10Be cosmogenic data that could be better presented and interpreted
First, the cosmogenic raw data are not easy to locate. They are available in the online supplementary information but there is no clear mention of these material in the main text. The reader has to understand that (1) the sup materials were cited as a paper (Ruby et al. (2026), which is, so far, not usual (is it an EGU requests??) and (2) the link to the data is available (only) at the end of the manuscript. The authors should make it easier for readers to quickly locate and access the raw data. For instance, a sentence such as the following should be added somewhere, early in the manuscript to make things clear for the reader and ease the access to the raw data: “Cosmogenic raw data are available in Supplementary information following this link: , Ruby et al., 2026“)
Although the data are indeed available in the online supplementary material, I still think the exposure-age results should be presented more clearly. For example, probability density plots (or similar graphical representations of the age distributions) for each site would greatly improve the presentation and facilitate the interpretation of the data. Parts of the manuscript are currently difficult to follow, and such figures would help clarify the authors' reasoning. In addition, the name of each study site should be included in Table 1 and in the online table, so that the analytical data can be readily linked to the corresponding geomorphic locations. Although figures 5, 6 and 7 identifies the different sites and provide the ages for each terrace level, including this information in the tables would considerably improve readability.
More generally, the cosmogenic exposure ages obtained from cobbles and boulders are often highly dispersed. Moreover, the number of data for each terrace level is rather limited as, so far, it never exceeds 3 per level (see figure 5, 6 and 7). For instance, usually, people collect >6 samples to date boulders on glacial moraines. Yet the authors frequently infer confidently a relatively narrow age range for terrace abandonment rather subjectively without much justification.
At the Tash Bashat site (1), the reported 10Be exposure ages are 10.0, 9.3, 7.4, 54.5, 26.9, 5.7, 67.0, 35.9, 20.3, 15.8, 8.7, 16.7, and 4.6 ka, whereas the pIRIR225 age is 23.0 ka. Despite this substantial scatter, the authors conclude that terrace abandonment of “the most widespread level” occurred between 16 and 23 ka.
The youngest exposure ages (approximately 4–6 ka) are dismissed on the basis of post-depositional human disturbance. However, although the authors reject the possibility of inherited cosmogenic nuclides (which by the way contradict their results in Fig. 7), they neither explain the origin of older exposure ages nor they provided ages for the highest level. Moreover, given the nature of the material dated by pIRIR (line 378), can partial bleaching prior to deposition be confidently excluded?
Similar problems also exist for On-Archa site. Here the ages of the upper terrace are: 5.9, 14.5 and 102ka. Just below the ages are 31.7, 20.2 an 8.3ka. Despite this scattering the authors rapidly conclude : “We interpret the lower surface to have an age between 19 and 25 ka and the large scatter in exposure ages of the high surface to result from a combination of shielding or turnover of the cobbles and boulders. We estimate the high terrace to be > 30 ka, with a small likelihood of being significantly older (~100 ka). “ Why? What are the arguments to assign such ages to the abandonment while the exposure ages are so dispersed?
The manuscript includes a cosmogenic depth profile (lines 184–185), but its presentation is very limited (only shown in Fig. 7 and quickly discussed in section “Kazarman (Site 9) (L450-464). The supplementary material does not provide much more information. How was the depth profile modeled (for the 10.3 ka case)? Which assumptions, misfit approach, associated reference, parameters (e.g. sediment density?) and equations were used? Where exactly was the profile collected? What are the depths of the individual samples (this is neither given in the main text nor in the Sup.)? Any photo showing the profile? Moreover, the absence of a clear exponential is not surprising since sampling started at 1m depth. The authors could have sampled the silt in the upper part. Sample treatment for fine grains sediment is trickier but remain feasible. More importantly, even though this profile cannot really be used to estimate age, it clearly indicates inheritance, which contradicts a key assumption made earlier. A much more detailed description of the depth profile, together with the methodology used for its interpretation, is required. Even if I understand this profile does not provide much constrains.
PIRIR225 ages are systematically taken at face value, without accounting for potential biases, for example partial bleaching that could be possible since most of sampled sediments are not pure loess but includes fluvial/lacustrine deposits. This point deserve discussion.
A Bayesian approach based on the relative chronology between the terraces inferred from their respective elevation might be a more rigorous and less qualitative/suggestive way to assign abandon ages of the studied surfaces. Such approach would also help to identify possible outliers. I encourage the authors to test this methodology on their data.
More generally and to conclude on this part, I think the robustness of the data (i.e number of samples per level, inheritance, partial bleaching) should be better discussed and the age assignment should be stated more cautiously and better justify.
NB: Note that both figures 5h and 5j don’t exist while they are mentioned in the main text. This complicate the reading and understanding of the corresponding studied sites.
Model vs. tested scenario
The description of the model could be improved. In particular, the values assigned to many of the model parameters are often unclear and appear somewhat arbitrary, with sometime little justification provided. For example, at line 311 the authors state, “To simulate terrace formation in the model, we track valley elevation and set a threshold value,” and later (line 500) they mention that they “implemented two terrace formation and preservation thresholds (2 and 5 m).” However, it is not clear how these threshold values were selected or justified.
More generally, I believe the manuscript would benefit from a much clearer explanation of the parameterization of the model. For each parameter, the authors should explain how its value was determined—whether it was derived from observations, calculated within this study, taken from previous work, calibrated, or chosen empirically. I recognize it is if often done but it is not always clear.
To facilitate this, I suggest revising the main text and adding a table that lists all model parameters together with their names; symbols, units, values, and the origin or justification for each value (e.g., literature source, calculation in this study, calibration, or arbitrary assumption).
Moreover, the Methods section does not clearly explain how the model results will be compared with the observations or how the three proposed scenarios will be discriminated. Section 4.3.3 describes how the climate- and lake-driven scenarios are implemented in the model to fit to the Naryan case, but it remains unclear how the resulting simulations will be evaluated against the field data to determine the origin of the terraces in the basin.
I suggest adding a dedicated section describing the strategy used to compare the model outputs with the observations and explaining how these comparisons will be used to address the questions and objectives outlined in the Introduction. In addition, the third scenario, involving tectonic forcing, does not appear to be explicitly tested with the model. The authors should explain why this scenario was not modeled or, if possible, include it in the analysis.
Discussion of the geochronology and robustness of the age grouping
In Section 6.1, the authors discuss the distribution/grouping of terrace ages and whether these correspond to specific climatic changes. However, this section raises several concerns.
First, the compilation of published terrace ages across the entire Tianshan is incomplete and far from exhaustive. The Tianshan is a vast mountain range where numerous fluvial terraces have been dated, yet many relevant studies have been omitted. For example, in Charreau et al. (2025), we compiled a dataset of 22 terraces dated using cosmogenic nuclide depth profiles, including six new depth profiles from the Northern Tianshan piedmont. That study specifically investigated the distribution of terrace abandonment ages and their potential relationship with climate. No clear link was found between abandonment ages and climatic proxies, including mean δ¹⁸O values, or any other obvious climatic signal. Furthermore, to avoid methodological bias, the dataset was intentionally restricted to cosmogenic nuclide depth-profile ages and did not include the numerous terraces dated using luminescence or other dating techniques. If the authors intend to compare their results with the entire Tianshan record, they should consider the full body of available data rather than only a limited selection of studies.
Second, it is unclear how the probability density function (PDF) curves for the Naryn Basin were constructed from this study (red curves). It appears that the authors included only the ages they assigned to each terrace. Because these age assignments are, in my view, somewhat subjective, the resulting PDF curves have limited robustness and should therefore be interpreted with caution.
I also found surprising that the authors distinguish the Naryn Basin dataset from the literature (orange curve) and the dataset from this study (red curve). Since the authors are studying the Naryn Basin, and they also use published data in Section 5.2 to constrain the ages of each terrace level, it is unclear why these two datasets are treated separately. On the one hand, the authors use published data to constrain the ages of the studied terraces, but on the other hand, they treat the literature dataset and their own age interpretation as separate. Since the red curve (their age interpretation) is also based on published age constraints, this distinction appears somewhat circular. The authors should clarify how the red curve was constructed and explain why it is presented as independent from the literature dataset. This distinction should be clarified, and the methodology used to construct all the curves should be explained in greater detail.
Interpretation of terrace shape (section 6.2)
Overall, I found this section somewhat unclear, speculative, and insufficiently developed. First, the terminology “concave upward/up” should be clarified. In my understanding, “concave” refers to a surface that curves inward, toward the object. Thus, for a terrace, the outer side would be upward and the inner side downward. A concave terrace would therefore have a bowl-shaped geometry, whereas I believe the authors may be referring to the opposite geometry.
More generally, I think that the interpretations and conclusions presented in this section would benefit from further development and a clearer explanation of the evidence supporting them. For example, the authors emphasize the concave-upward geometry of several terraces located far upstream of the landslide. They argue that this geometry is inconsistent with a tectonic origin and instead supports their third conceptual model, which involves lake damming and delta formation. However, two issues make this interpretation difficult to assess. First, it is not clear from Figure 4 which terraces are referred to as “concave upward.” Second, the proposed model (Fig. 3c) does not appear to illustrate the development of concave-upward terraces. It is therefore difficult to establish a clear link between the observed geomorphology and the proposed model, and consequently to understand how these observations support the authors’ interpretation.
Similarly, the absence of a break in slope, which would be expected based on Model 3c, is not clearly explained. The different possibilities proposed by the authors to account for this absence are mentioned only briefly and would benefit from a more detailed discussion and clearer justification.
Insights from terrace modelling (6.3)
My first remark here echoes what I previously mentioned in the section “Model vs. tested scenario.” I found that the model results were not sufficiently compared with the observations, despite the authors repeatedly stating that the model and data are in good agreement. For instance, the authors state: “The modelled fluvio-lacustrine terraces in the lake-drainage scenario fit the tributary terraces in their concave-up shape as well as, to a first order, in their spatial extent and time lag of formation.” Similarly, in L626, they state: “Furthermore, modelled heights and slopes of climate change induced terraces are consistent with observed terrace profiles throughout the Naryn basin.” However, where can the reader actually see these good fits between the model results and the observed terrace data? As far as I can see, only Figure 8c directly compares observed terrace topography with model results, whereas Figures 9 and 10 show model outputs without direct comparison with the observed data. The discussion in L627–630 therefore remains largely qualitative, requiring the reader to make the connection between what is shown in Figure 9 and what is observed in Figure 4.
I therefore think that a stronger effort is needed to demonstrate, and preferably quantify, the degree to which the model results reproduce the observed data. This would make the comparison between the model predictions and the observations much more convincing and would also allow the reader to assess where the model succeeds or fails.
Moreover, the first paragraph of this section would benefit from further clarification. First, it is unclear what the authors mean by the “channel-incision signal.” Second, how can this signal be identified in Figure 4? Third, given the discrepancy between the modelled propagation distance (90 km) and the observed distance (53 km), why not use the model to explicitly test the mechanism proposed by the authors to explain this discrepancy? Such a test could provide a more quantitative assessment of whether the proposed explanation is consistent with the model results.
Finally, the authors state in L620: “This result is somewhat unexpected, as previous work modelling a single-treaded channel highlighted limited downstream signal propagation in systems with similar or even lower ratios of forcing periodicity to the system’s equilibration time (Ruby et al., 2026).” I find this an interesting result, but the manuscript does not provide an explanation for this difference. Why does the present model produce downstream signal propagation whereas previous modelling studies did not? A more detailed discussion of the mechanisms responsible for this difference would strengthen the manuscript and could help broaden the implications and interest of the study, as also mentioned in my general comments in the letter.
Interpretation of the terrace record (6.4)
This section raises many of the same issues discussed above. The observations are, to my opinion, not sufficiently compared with the model results (L636–637), while the hypotheses proposed to explain the discrepancies between the model and the data are presented only qualitatively, without sufficient investigation or supporting evidence. As a result, some of these interpretations may appear speculative.
Moreover, in my opinion, the final paragraph is also somewhat speculative, as the authors have not considered all the literature on the chronology of terraces across the Tianshan (see my comment above). A more comprehensive consideration of the existing chronological constraints would be necessary to properly assess the proposed interpretation.
Other remarks
Please refer to the annotated pdf file.
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RC3: 'Comment on egusphere-2026-3489', Magali Rizza, 23 Aug 2026
Please find my comments for the paper entitled “Climatic, tectonic and landslide-dam signals preserved in alluvial terraces of the Naryn Basin, Kyrgyzstan” by Andreas Ruby et al.
This study combines terrace mapping, geochronology, and numerical modeling to disentangle the roles of tectonics, climate, and landslide-dammed lakes (Beshkiol, 25-6 ka) in shaping fluvial terraces in the Kyrgyz Tien Shan. The authors show that a major terrace level dated 15–20 ka is widespread across the region, and use modeling to distinguish a spatially restricted signal from lake drainage versus a broader climatic control linked to decreasing sediment-to-water ratio after the local LGM. This approach more generally illustrates how long-profile modeling of alluvial networks can help identify the spatial and temporal signatures of different geomorphic drivers.
This paper presents original data that, despite the seemingly local character of the study, carries broader significance for the questions we ask about the formation of large alluvial terraces in settings where climate and tectonics (two competing controlling processes) interact. Another point explored here is the impact of a major shift in river dynamics caused by the emplacement of a temporary lake, which in turn altered the river's base level and flow regime. This too contributes to the originality of the paper.
Overall, I find this paper very well written and reasonably well illustrated, although some figures are difficult to read without considerable on-screen zooming to properly discern the morphology (Figures 5, 6, and 7). This issue, however, could easily be corrected.
I have several major comments, as follows:
- Regarding the geochronological data:
On the Luminescence data : Being well acquainted with the study area, I recognize that obtaining reliable luminescence ages can sometimes be challenging. However, I believe several points need to be revisited in the paper. The authors used the pIRIR225 protocol, which offers the advantage and the possibility to provide ages from both the 50°C and 225°C readings. However, the authors chose to present only the ages derived from the 225°C measurements, even though this is also the signal known to be the least well-bleached. Based on my own experience in this area, and particularly with samples from Lake Naryn, I have almost systematically obtained a poorly bleached IR225 signal. What is the relationship between your IR225 and IR50 data? I therefore do not understand why the authors never present the ages obtained from the IR50 signal.
I would also recommend the following paper by Roberts et al. (2018) (https://doi.org/10.1016/j.quascirev.2018.10.037), which presents a compelling example of bleaching issues in lacustrine sediments. You could present your data in a similar way to Figure 3 of that paper, which visually illustrates whether the pIRIR225 signal is generally well-bleached or not, and allows the IR50 signal to be examined alongside it.
On the other hand, we know that the IR225 signal fades less than the IR50 signal, and I wonder whether the authors chose to present only this portion of the data specifically to avoid the fading issue. I note that the authors state on lines 244–245: "Fading tests on selected samples yielded generally low fading rates of ~1–1.5% per decade. Therefore, we did not apply any fading correction." While I acknowledge that this fading rate is low, it can still have a meaningful impact on sufficiently old samples. I believe you should, at minimum, present the age both with and without fading correction for one (old) sample, in order to convince the reader. In my own work, I have indeed found values around 1.5% for the basin, but this value can reach up to 2.5% for certain samples, which is not negligible. Do all samples exhibit exactly this 1–1.5% fading rate? Furthermore, I would be curious to know what fading rate you obtained for the IR50 signals? In our samples, we found values ranging between 2.5% and 4%, and accurately estimating this fading rate is therefore important.
For these various reasons, I strongly recommend that both the IR50 and pIRIR225 results be presented in this paper, both without fading correction and with fading correction applied. If the samples are well-bleached, then after fading correction, the IR50 and pIRIR225 ages should be very close to one another.
Finally, one last point that also relates to the issue of fading: you use the MAM (Minimum Age Model) for your equivalent dose calculations, precisely to try to isolate the best-bleached component. However, it is well established that grains with the lowest equivalent doses are also generally those with the highest fading rates. For this reason, I believe fading correction should, at minimum, be applied when calculating the final age. By using only 1–1.5%, a fading rate based on an average across your aliquots, you are likely underestimating the fading associated with these equivalent doses, which could lead to an underestimation of the true age of your samples.
On the Cosmogenic data: 9 sites were surveyed, a large number of samples were prepared and measured for this study, representing a substantial amount of laboratory work as well as a non-negligible financial cost!
However, I note that only 2–3 samples were collected per terrace level. This represents a significant limitation for estimating the true age of the terraces, both from a statistical standpoint and because ages are often widely scattered even within a single terrace. For example, at Site 1 in Tash Bashat, you have 3 samples across different terraces. I note that your 3 samples systematically yield 3 completely different ages. On one terrace, you obtain 54.4/26.9/5.7 ka; on another, 67/35.9/20.2 ka... and finally, when your ages do appear to converge (10/9.3/7.4 ka), these are unfortunately discarded because they occur on a high terrace and are therefore, I acknowledge, inconsistent with what would be expected and of limited significance.
I therefore think the authors should be somewhat more cautious in estimating terrace ages, as they sometimes invoke issues of anthropogenic disturbance or overturned clasts, which can indeed occur extensively given the morphology of the region, where, rather surprisingly, few surfaces are well preserved from human activity and grazing herds. Have you considered examining the effect of surface burial/deflation/weathering on your age models? Indeed, nearly all alluvial terraces in the Tien Shan display a surface unit typically consisting of fine silts/sands with a few scattered pebbles. One might interpret these units as deposits associated with aeolian processes interspersed with remobilization/colluvium by surface runoff during major rainfall events, affecting the uppermost centimeters of the fan surface. I note that you describe this in your paper on line 377: "that we interpret as a mixture of loess, overbank deposition and, probably, colluvium due to the inclusion of rare, small pebbles." If, after several tens of thousands of years, this type of deposit comes to cover your boulders (thereby burying them), partial shielding would occur, reducing cosmogenic isotope production over time and thus leading to an underestimation of the true age, even for burial of just a few tens of centimeters. Competing with this, however, is surface denudation, which could in turn recently re-exhume your boulders... This is admittedly complex to model, but have you tested a partial burial model for calculating your sample ages?
Another point regarding the ages: I also find that the authors sometimes dismiss the issue of inheritance too quickly, and this deserves somewhat more discussion in the paper. For instance, I read on line 383: "We reject the possibility of significant inheritance to the 10Be concentration, as younger ages for these surfaces would imply incision or uplift rates nearly an order of magnitude higher than reported for faults in the region (Thompson et al., 2002; Goode et al., 2014), giving the older sample ages a higher likelihood to represent the actual terrace abandonment age." At first glance, this does seem reasonably coherent; however, in this particular case, and to establish the link between luminescence and cosmogenic ages, this lowest terrace yields cosmogenic ages of 4.6, 8.7, 15.8, and 16.7 ka... alongside a pIRIR225 age of 23 ka. This brings me back to my earlier question: is the pIRIR225 signal well-bleached? If the IR50 signal were to yield an age of 10 ka, how would you then interpret this?
These comments are not intended merely as criticism but also aim to encourage the authors to better justify their reasoning across all their sites, which will help strengthen the robustness of the ages obtained for the different terraces.
- Regarding the numerical model
I do not work with numerical modeling myself, and therefore I do not have the full expertise to properly assess all the parameters underlying the model presented here. I note that your model appears to align well with the field data (e.g., Figure 3c), and I find it reasonably convincing overall. However, I have a few comments that concern form rather than substance.
On my first reading of the paper, I had considerable difficulty with Figure 9. This stemmed from the oscillation plot in Figure 9a, where I initially interpreted the x-axis as representing time before present, with 0 corresponding to the present and 46 corresponding to 46 ka. However, as I could no longer reconcile this with the rest of the figure or with the accompanying text, I eventually understood that the x-axis instead represents simulated time elapsed since the start of the model run. Is this interpretation correct? I would suggest finding a clearer way to distinguish between ages expressed relative to the present and time within the model itself. Perhaps, in this case, labeling the x-axis of Figure 9a as "elapsed time" would help avoid this confusion?
Regarding Figure 9d, again this is primarily a visual/formatting issue: I only see colors in the green/yellow range, yet the terrace ages (y-axis) range between 5 and 15 ka, whereas in Figures 9a and 9b, green represents 23–30 ka. Shouldn't this range instead appear in blue? I therefore find myself somewhat confused between what I see in the figure, what I read in the text, and what I am meant to understand from it. I believe that revising this figure, and in particular its color scheme, would greatly improve the clarity of this section.
Minor comments:
Line 62: You should add reference of paper from Strom
Line 153: The terraces in the Naryn Basin have been used primarily to reconstruct late Quaternary fault slip rates. You should cite Thompson or Goode’s papers there.
Line 141: in sediment supply , you should add here (Qs)
Line 142: sediment supply, you should add here (Qw)
Line 212: See my major comments
Line 235: which is expected particularly in fluvial settings may be replaced by which is expected particularly in fluvial and lacustrine settings. You may also cite Roberts (2018): Roberts, H. M., Bryant, C. L., Huws, D. G., & Lamb, H. F. (2018). Generating long chronologies for lacustrine sediments using luminescence dating: a 250,000 year record from Lake Tana, Ethiopia. Quaternary Science Reviews, 202, 66-77.
Line 245: See my general comments, I am not in agreement with Therefore, we did not apply any fading correction.
Line 285: What is the error/uncertainty of the FABDEM topographic data?
Line 300: we made the simplifying assumptions that rock uplift is spatially and temporally uniform. It is ok for several thousand years… but for longer time ie. 100-500 ka?
Line 305 : equilibration time, mean length, sediment-transport diffusivity : please provide units
Line 317: along stream in 23- and 41 ky sinusoidal cycles with amplitudes of 33 and 66%. Please explain to the reader why these particular sinusoidal cycle durations were chosen, as well as the 33% and 66% values. Is there a specific reason behind these choices?
Line 319 : because 𝑄𝑤 affects the efficiency of the valley response as well as its slope. Is it because Qw change after climatic input?
Section 5.1: From line 344 to 350, This section could be reworded as it is not easy to read, between numbers, commas, brackets….
Line 351: For site 7 – Kok-Dschar east and west , lower XX km is missing
Line 366 : Table 1. I strongly recommend adding a new column indicating the site number associated with each catchment. This would greatly help readers understand which samples are associated with which catchment/site.
Table 2:
-See my major commentsIR50 AND pIRIR225, both should be presented.
-Why all samples have 15 +/- 5 % of water content. Alluvial and lacustrine should be quite different.
-Sample 22-KG-17 : I noticed a very high dose rate + only 15 aliquotes. Is it something special with this sample? Dim signal?
Tash Bashat (Site 1):
Figure 5b: in fact the Eki-Naryn trace fault is missing …
Line 374 : took an additional luminescence sample. Please provide here the label
Line 378: 23.0 ± 2.9 ka, sits in fine-grained sediment that we interpret as a mixture of loess, overbank deposition and, probably, colluvium due to the inclusion of rare, small pebbles within this unit.
Indeed, all surfaces in the area are covered by this unit, but even across different terraces elevations, I have consistently noticed ages falling within the 15–25 ka range. This raises a concern: rather than dating the terrace surface itself, this age may instead reflect a much later, more regional depositional event (such as the aeolian/colluvial cover unit discussed earlier) rather than the original abandonment age of the terrace. I am therefore not confident that this age is robust evidence for the terrace's true depositional age.
Also I am concerned by the pIRIR225 age. Is it truly bleached? Please provide the IR50 age too.
On-Archa upstream (upstream of Site 2):
Line 396: We interpret the lower surface to have an age between 19 and 25 ka
First, there is an intermediate level dated at 15.1 ka. What is your interpretation of this age, was it dismissed? If this age is indeed correct, then the lower surface age may in fact be closer to 11.7 ka. Also if the pIRIR225 is not well bleached then it may be much younger.
and the large scatter in exposure ages of the high surface to result from a combination of shielding or turnover of the cobbles and boulders. We estimate the high terrace to be > 30 ka, with a small likelihood of being significantly older (~100 ka).
Ok, but you have to remember that you have huge scatter in ages of two surfaces quite close in elevations: 5.9/8.3/14.5/20.2/31.7/102.6 ka ! So here you force the age model, right? high terrace to be > 30 ka is based on a single boulder, as well as your likelihood of 100 ka… So
Line 400: A terrace patch 9 km downstream of the location, situated at 2100 m elevation, or 80 m above the channel, has a minimum age of 143 ± 15 and 150 ± 23 ka dated by thermoluminescence and IRSL (Thompson et al. 2002).
First you should remember to the reader here your elevation above the riverbed to compare it with the elevation at Thompson site. However, I believe the position stated is uncorrect. The samples were not collected downstream of your site, but rather within the catchment directly east of On Archa, along the Kadjerty river (see Figure 11 in Thompson, 2002). On Archa is the Djergetal river in his figure 11. Also, it is worth noting that these were TL or high-temperature IRSL ages (260-390°C) at the time, and I am not confident they were well-bleached, so they should be taken with caution.
Kek-Scherty (Site 3):
Here, you have no direct dating of your own, only the age reported by Thompson et al., which clusters nicely around 15 ka. It would be useful to state the elevation of this surface above the present river bed. Indeed, when comparing with On Archa, you also have an age of 15.1 ka there (albeit based on a single boulder, which you reject). At a first-order level, some comparison between catchments could be worth exploring.
At-Bashi (Site 18):
Line 411: One luminescence sample from fine-grained sediment (interpreted to be a mixture of aeolian, overbank and loess deposits) topping fluvial gravels within the lowest terrace yields an pIRIR225 age of 15.1 ± 2.3 ka,
See my comment above about the age of 15-25 ka, everywhere capping the different surfaces. So, if you again collected the sample in this capping unit, it may be discussed. 20 m above the river bed is it in the order of elevation on the other catchments?
Terek upstream (upstream of site 14):
As the lower two surfaces yield exposure ages that are well clustered and stratigraphically consistent (ca. 15 to 21 ka), we disregard the younger age of 9.3 ± 0.9 ka on the highest surface, and instead prefer the age of 183.5 ± 10.5 ka.
Ok but you based the age of 183 ka on a single boulder, that may contain inheritance too. Never discussed…
The lower surface yielded two exposure ages that agree within uncertainty (8.7 ± 0.8 and 8.0 ± 0.8 ka).
It is not entirely clear to me what you infer here. Does this mean the age of the lower terrace is now 8.0–8.7 ka? And what about the 14.4–15.7 ka age range, which seems to align well with the ages reported in the other catchments?
Naryn Central (Site 4):
Line 427 : We interpret the terrace abandonment to be younger than the depositional age of 30 ky.
Please state well the elevation of the surface in which the samples were collected. Also just ages from pIRIR225, what about IR50?
Kok-Dschar east (Site 6):
You are reporting an age from Goode but this age is not from “a low and continuous terrace” (Line 430). The GPS coordinates provided by Goode (see table 1, Goode 2014) place the sample on a perched and high alluvial fan. You have a lower and well developed alluvial surface below this one.
Kok-Dschar west (Site 7):
You report here ages from Goode (2014). First the locations are not super clear in his paper and the description of the units sampled too. Really close to the place of Goode (along the same river), in Losen et al. (2024) you have “ Collected within alluvial fan sediments interbedded with the upper part of Sultan Formation, samples NAR21- PIT3 (OSL) and NAR21-PIT3-GN (14C) yielded ages of 7590 ± 730 yrs. and 7910–7590 yrs cal BP, respectively. These samples mark the end of the Sultan Formation at Kok-Dhzar”
Ugut (Site 8):
You mention this here, and indeed there are strath-like levels in the area, but in fact the deposits are lacustrine sediments (Erkin Fm). Just for your information, your ages are consistent with new OSL samples collected very close to your site (Losen, paper in preparation), for which the IR50 signal yielded ages of 24.2 and 18.4 ka, while the pIRIR225 signal yielded 33.5 and 31.5 ka for the same samples.
You state “their similar age despite their elevation difference of 45 m could indicate that lacustrine sediments here cover a preexisting terrace sequence”. Yes indeed. Another possible explanation is that your samples are also not well-bleached, which would mean they could be younger and thus fall into a stratigraphically consistent position within the lacustrine deposits.
Kazarman (Site 9):
Line 455 : The terrace level below yielded an pIRIR225 age of 19.0 ± 2.6 ka from fine-grained material incorporating rare pebbles and cobbles sampled 0.7 m below the surface.
Once again, this capping unit would fit for an age between 15 and 25 ka on a regional scale...
Line 457: Scatter in the depth profile of 10Be concentrations results in a poor fit to the expected exponential function and does not allow a straightforward exposure age calculation
Also found in the Supplementary :
Assumption of zero erosion since deposition of the full profile. Less 10Be concentration is achieved by shorter cosmic ray exposure, lowest misfit is 10.3 ky.
Both scenarios might represent endmembers and the actual processes might lie in between. However, we hypothesize the 2nd scenario (deposition at 19.0 ka) to be more relevant as a thicker silt cover is likely and would not cause the stratigraphic mismatch of an pIRIR225 sample age nearly twice as old above the 10.3 ky 10Be depth samples.
Despite the limited number of samples available for the depth profile (4 on which the model is using 2), you should perhaps also acknowledge that 10.3 ka remains a viable solution. It seems you are favoring the 10Be depth-profile model primarily because of your pIRIR225 age, which may itself not be well-bleached; I would be more convinced if this were supported by the IR50 data as well.
Also, have you tried modeling your profile in two steps: a first stage involving steady exposure of the gravels, followed by a second stage in which the "loess-like unit" progressively caps the surface? (See also Rizza et al., 2019, for examples of multi-stage modeling approaches.)
Another point in your profile, you have inheritance (more than 1.5 * 10^5 at/g!) if I am correct, but never used it in your model. Why?
Line 497: Section 5.3.2:
See my major comments, especially for Figure 9
From Line 515 to line 520: This paragraph is difficult to follow, I recommend some rewording.
Line 542: Section 5.3.3.
I really enjoyed seeing the modeled effect of the lake on the Naryn basin. I am wondering whether you tried simulating a gradual emptying of the lake, as appears to have been the case for the second (and more recent) lake. In Losen et al. (2024) and subsequent work, we found no evidence of catastrophic dam failure for this second lake, suggesting that drainage should instead have been gradual after 8 ka.
Discussion
Line 563: These occur at around 180 ka, between 120 and 150 ka, around 80 ka, and most clearly throughout the region, between 15 and 20 ka (Figure 11b).
Based on which data are these ages ? Are they based on your work (but with very poor constrain for the upper levels and the oldest ages)? Here, in my opinion, a paragraph, or at least a few sentences, is missing that would recall/summarize your work and previous geochronological studies in the region.
Discussion :
I generally agree with the authors that the tectonic signal is only weakly visible in the examples presented. However, in the basin, some rivers show a greater number of low-elevation terraces just upstream of thrust faults. These terraces, which are not shown here, would be worth modeling to see whether a tectonic signal could emerge. This is simply meant as a point for discussion, and I fully understand that the authors will not be able to address it within the scope of this work.
Another important point, which should perhaps be given more emphasis in the paper—possibly by citing previous work published in the region more thoroughly—is that the 15–20 ka terrace is consistently found across numerous sites. This timing also coincides with the moment when the Beshkiol landslide abruptly failed, triggering a catastrophic outburst flood, before being reactivated to form a second lake. This suggests that something is happening climatically during this period that is influencing the entire landscape dynamics of the Tien Shan range. The paragraph between lines 600–605 could therefore be expanded along these lines, for example.
Another point that could be brought out more in your discussion is the possible ages for at least the second major morphological surface observed across the different catchments. While the 15-20 ka terrace is now well established, if these terraces do indeed -reflect a genuine climatic control, then what would their age be?
Code and data availability
I really appreciate that all the supplementary data are made available, but I had to download the entire 1 GB folder just to access the supplementary docx on the ¹⁰Be profile modeling. This could be a small point to improve, for instance, by allowing individual files to be downloaded separately.
I have no doubt that the authors will benefit from the various reviewers' comments and that this paper will be read with great interest by the community. I congratulate the authors on this substantial piece of work.
Sincerely,
Magali Rizza
Citation: https://doi.org/10.5194/egusphere-2026-3489-RC3
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General comments
This manuscript addresses an important question: how to distinguish climatic, tectonic, and landslide-dam controls on alluvial terrace formation in a complex river network. The integration of terrace mapping, cosmogenic and luminescence geochronology, and network-scale numerical modelling is innovative and has the potential to make a valuable contribution to fluvial geomorphology.
I recommend moderate revision. The manuscript is promising, but several methodological and interpretative issues require further clarification. I have four major comments, followed by several specific minor comments, as detailed below.
Major comments:
Lines 225–245: While there is no universally prescribed integration interval for feldspar IRSL/pIRIR signals, the selected 100-s background interval is relatively long compared with commonly used approaches, such as ~2 s signal integration combined with a ~20 s terminal background. A long background interval may incorporate low-level signal decay, instrumental drift, or other variations (Galbraith, 2002; 2012). Please justify this choice and, if necessary, recalculate the De values using an alternative integration interval, preferably with reference to comparable studies from the region.
Lines 230–235: The MAM is applied to all samples because incomplete bleaching is expected in fluvial settings. However, incomplete bleaching may vary substantially among samples, and inappropriate application of the MAM could lead to age underestimation. Please provide the De distributions and overdispersion values, preferably in the Supplementary Information, and select CAM or MAM according to the characteristics of individual De distributions.
Please also report the aliquot size or mask diameter, because this information is relevant when evaluating De distributions, and the choice of age model.
Table 2: Please add overdispersion values. Sample 22-KG-17 has an unusually high De (~650 Gy) and dose rate (~6 Gy ka−1). Please verify these values and, if correct, briefly explain whether the high dose rate is related to a particular lithology, sedimentary facies, or geochemical setting and so on.
My second major concern is the presentation of time in the modelling results, particularly in Figures 9 and 10.
In Figure 9a, “Time [ky]” represents elapsed model time, whereas Figure 9d shows terrace age relative to the end of the simulation. Similarly, the labels 0, 2, 10, and 20 kyr in Figure 10 represent elapsed model time, whereas the text refers to terrace ages of 20–8.9 ka relative to the end of the model run.
This distinction is not sufficiently clear and may easily confuse readers. I suggest using consistent notation throughout the manuscript. For example:
t = elapsed time since forcing onset;
A (terrace age) = age relative to model termination.
Alternatively, the authors may adopt another notation, but model time and terrace age should be clearly distinguished and consistently presented in Figures 9 and 10.
The Introduction frames the study around three end-member mechanisms: tectonic forcing, climate-driven Qs/Qw changes, and lake drainage. However, the numerical modelling mainly evaluates the latter two, whereas tectonic forcing is treated more qualitatively. The authors should either provide additional quantitative evaluation of the tectonic end-member or reduce the emphasis placed on tectonic forcing in the discussion, as the supporting evidence is less comprehensive than other two.
I also encourage the authors to strengthen the discussion of transient responses and lag times. Figure 9 and 10 show that terrace abandonment may occur several thousand years after the forcing maximum and that the timing varies spatially across the river network. This is an important result because it demonstrates that terrace age does not necessarily correspond directly to forcing age. The broader implications of this diachronous response deserve greater emphasis.
Section 2.2: “Geomorphic features” focuses mainly on the Beshkiol landslide and paleolakes, but provides little regional overview of the terrace system itself. Please add a concise description of the number of terrace levels, typical heights above the modern channel, and their spatial distribution along the trunk river and tributaries.
Sections 5.1–5.2 contain detailed site-by-site descriptions, but some interpretation, particularly the acceptance or rejection of individual 10Be ages, is already mixed into the Results. I suggest moving the regional terrace framework to Section 2 and reserving detailed chronological interpretation for the Discussion.
Minor comments
Lines 315–318: Please explain why 23- and 41-kyr periodicities were selected for the Qs/QW forcing experiments.
Figure 1: Consider adding glacial extent, distinguishing fault types where possible, and showing the spatial extent of Figure 2.
Figure 4: Please clarify the x-axis and improve the legend/caption. In particular, explain the white lines and why some segments differ in thickness or connectivity.
Tables 1 and 2: Consider adding tributary name, terrace level, and height above the modern channel for each sample. Please also add overdispersion values to Table 2.
Figure 5: The symbols for 10Be and luminescence samples are difficult to distinguish. Please use more contrasting colours and/or different symbols. The caption should also indicate the 14C ages and their source.
Line 530: “signals can propagated” should be changed to “signals can propagate.”
Lines 560–565: “Surfaces of the latter range of ages cluster often form…” is grammatically unclear and should be revised.
Lines 605–610 / Figure 10: Consider expressing the x-axis as upstream distance from the landslide dam, with the dam as zero, to make upstream signal propagation more intuitive.
Please standardize terms such as “rock uplift/rock-uplift” and “lake drainage/lake-drainage.”