the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 08 Dec 2021
Landscape responses to dynamic topography and climate change on the South African source-to-sink system since the Oligocene
Abstract. The South African landscape displays important lithological and topographical heterogeneities between the eastern, western margins and the plateau. Yet the underlying mechanisms and timings responsible for this peculiar layout remain unclear. While studies have proposed a post-Gondwana uplift driver, others have related these heterogeneities to a more recent evolution induced by deep mantle flow dynamics during the last 30 million years. This theory seems supported by the rapid increase of sediment flux in the Orange basin since the Oligocene. However, the triggers and responses of the South African landscape to dynamic topography are still debated. Here we use a series of numerical simulations forced with Earth data to evaluate the contribution of dynamic topography and precipitation on the Orange river source-to-sink system since the Oligocene. We show that, if the tested uplift histories influence deposits distribution and thicknesses in the Orange sedimentary basin, they poorly affect the large-scale drainage system organisation and only strongly impact the erosion across the catchment for two of the four tested dynamic topography cases. Conversely, it appears that paleo-rainfall regimes are the major forcing mechanism that drives the recent increase of sediment flux in the Orange basin. From our simulations, we find that climate strongly smoothed the dynamic topography signal in the South African landscape and that none of the currently proposed dynamic topography scenarios produce an uplift high enough to drive the pulse of erosion and associated sedimentation observed during the Palaeocene. These findings support the hypothesis of a pre-Oligocene uplift. Our results are crucial to improve our understanding of the recent evolution of the South African landscape.
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Interactive discussion
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RC1: 'Comment on esurf-2021-89', Jean Braun, 17 Jan 2022
Review Mallard and Salles, ESURFD 2021
The manuscript by Mallard and Salles describes the results of a study aiming at explaining the observed increase in sedimentary flux from the Southern African craton documented by Baby et al (2018 an 2020) as resulting from dynamic topography (DT) or enhanced precipitation. For this the authors use a surface process model that is subject to a range of model-deduced DT estimates over the past 30 Myr and a rainfall function/distribution that has been reconstructed from various previous studies. The authors find that the sedimentary fluxes predicted by the model offer little resemblance to the observed ones. The observed amplitude of the change in sedimentary flux can be matched by varying rainfall but no its timing. The recent increase (i.e., in the past 10 Myr) is never reproduced by any model scenario. Despite this, the authors attempt to determine which of the imposed drivers is responsible for the increase in erosion rate (and thus in flux) predicted by the model, by computing correlation maps between erosion rate, DT and rainfall for each of the tested model scenarios.
Although I appreciate the efforts that the authors have put in this modeling exercise, I have to recommend that it be rejected as it contains major methodological flaws, and is not clearly presented. I justify my recommendation in the rest of this review and, where possible, I provide hints/suggestions on how this work and how it is presented could be improved.
My major concern include:
- A lack of clear focus/objective for the paper: what are the authors trying to demonstrate/prove? Are they trying to demonstrate that one DT model fits better than others? That DT or climate variations can or cannot be responsible for the observed increased in sedimentary flux in the Orange basin? Reading through the introduction I do not see any clear questions or hypotheses being stated that are later tested against each other. Similarly reading through the conclusions I do not see what the major findings are except that none of the tested DT scenarios or climate scenarios can explain the variations in sedimentary fluxes. The various scenarios are not ranked by their fit to the observations. No alternative scenario is offered apart from stating that some sediment may have been recycled within the marginal basin which implies that the sedimentary flux data cannot be used to say something about what happens on the continent.
- Like others before (Roberts and White, 2010; Paul et al, 2014), the authors have assumed that they know the erodibility coefficient (Kf) in the SPL. This is a major flaw of their approach as WE DO NOT KNOW its value within a few orders of magnitude. Where does the value of 1.6e-7 comes from? Note also that any given value of Kf is only meaning fully if we know what m (the area exponent in the SPL) is. To further assume, like the authors have done, a one-to-one correspondence between rock type and Kf is also rather misleading, especially with a precision that assumes that variations of a few tens of percents are meaningful. The authors should know that there are many factors that influence Kf such as fracturation, degree of weathering, model resolution, etc. To scale Kf, the authors have also used a present-day map of lithologies that, in my opinion, is irrelevant when applied to a model that is run over 30 Myr (the lithology of eroded material is relevant). To present results that depend on the absolute value of the coefficient Kf, one must use time-relevant constrain (thermochron ages, sediment fluxes, etc.) to calibrating Kf. This has been shown over and over (a great demonstration shown in Fox et al, 2014's work on inverting Taiwanese river profiles).
- The authors correlate predicted erosion rate, with the imposed rainfall rate and and DT variations in an attempt to infer which of the main drivers (DT or climate) is responsible for the predicted variations in erosion rate. First I do not understand the purpose of this exercise as, regardless of what is driving the erosion rate, the model cannot represent the observed sedimentary flux. Second, the authors seem to not take into account that, according to the SPL, there always exists a large time lag between variations in uplift rate (or in base level) and the resulting variations in erosion rate, whereas there is no such time lag between imposed variations in rainfall rate and erosion rate (see Whipple and Mead, 2006, Fig 4). Note also that the time lag mentioned above can be of the order of a few to a few tens of million years, depending mostly on the assumed value of the erodibility coefficient Kf, if n=1. The lower Kf, the longer the time lag.
- The way the DT models are incorporated into the LEM is such that very different scenarios (some predict overall subsidence while others predict uplift) all produce a very similar sedimentary flux prediction. This demonstrates that the model is almost insensitive to DT scenarios and that most of the erosion is driven by erosion of the short wavelength topography which is basically identical to the present-day topography.
- The model is poorly presented. There is no brief description of the main relevant equations; the value of key coefficients (such as the slope and discharge exponents, n and m, in the SPL) is not given, which makes the interpretation of the results very difficult to assess. There are major issues with some of the figures too (see below).
Other points that need to be addressed:
- Line 51: What do the authors mean by “different flexural uplifts”? Different flexural thicknesses? Flexure is a response to another mechanism such as thinning or thicknenning of the lithosphere/crust or to denudation/deposition. It cannot be an uplift in its own.
- Line 60: How did the authors obtain absolute values for paleo rainfall rates? In the appendix, they provide references where paleo indicators are given. They need to explain to the reader how they have been able to go from indicators to actual rainfall rates.
- Line 69: As explained earlier I have major concerns about the erodibility. The value that is given in the relevant table is very low and should be justified.
- Line 94: The authors should compare the various DT models graphically in an appendix/supplementary section. They should also discuss the origin of their differences. Some predict uplift while others predict subsidence… So what is the point in trying to use constraints that do not agree with each other? Alternatively the authors should have as an objective to differentiate between them. But this is not stated/proposed.
- After the paragraph ending at line 96, the authors should show to the reader what the predicted fluxes from Baby et al (2018, 2020) look like. It would be interesting to see how they correlate with the different dynamic topography history estimates. We also need to know what the flux estimates correspond to: are they just from the mouth of the Orange Basin? Or from what Baby et al call the Cape area too? I also believe that Baby et al produce uncertainty estimates of their fluxes. This is really important as any model that would fit the data within uncertainty should be considered as equally adequate to reproduce the data. This is not provided or discussed here.
- Line 110: I am surprised that the authors included the weight of the sediments removed from the continent but not the sediment accumulated in the margins. In theory (by mass conservation) they should be equal in volume so that the weight of the deposited sediment should be much more localized and may therefore cause a much greater flexural isostatic effect along the margins. Remember that for the LEM, the variations in the height of the base level is the only way it can feel the perturbations caused by DT; it is therefore very important that any other process that can affect the relative position of the base level is taken into account.
- Paragraph ending line 116: What about using an optimization/iterative scheme to determine the optimum initial topography, in which whatever is predicted to have been eroded/deposited is used to readjust the initial topography. This should converge very quickly.
- Line 125: The authors should mention the values they have used for the slope (n) and area (m) exponents of the SPL. These are critical to understand what they have done/interpret their results. The relationship between impose variations in rainfall rate and predicted erosion rate depends strongly on m.
- Line 140: It is not supposing that the predicted topography looks like the present-day topography as you simply add DT to an initial topography that is computed by removing DT from the present-day topography… This is not a result but is part of the model setup.
- Line 150: Why discuss first how the model matches cosmogenic-derived erosion rates (that have not been presented in the data/introduction part of the paper) rather than sediment fluxes that have been mentioned earlier.
- Figure 3: There are major issues with this figure: It says that the dashed lines correspond to values calculated from the landscape evolution model whereas one of them is labeled “Baby et al, 2020” which seems to imply that it corresponds to observed values. I also note a second dashed line with a reference to Kuhlmann et al, 2010, which is not mentioned anywhere else in the paper (not even the reference list). The authors should be more precise.
- Line 161: This implies that the model or the setup the authors have used (substracting first DT then adding it) are insensitive to the assumed DT: whether South Africa has gone up or down over the past 30 Myrs has almost no effect on the predicted sedimentary flux. This implies that the flux and thus the erosion that the model predicts are caused by a slow "downwearing" of the topography that would also likely take place if one had no DT applied to the model.
- Line 165: Here the authors envisage a set of possible reasons for why the model cannot reproduce the sedimentary flux, but they do not envisage the possibility that the DT models are wrong or that DT may not be the driver of the increased flux. It could be the southward propagation of the South African Rift swell, for example.
- Line 175: from the amplitude of the imposed increase in rainfall (4.4) and that of the resulting increase in sedimentary flux (2.2) I can derive that the value of m that the authors have used must be close to 0.5. This relationship between m and the relative changes in driver/response should be discussed (see Braun et al, 2015, EsurfD, Erosional response of an actively uplifting mountain belt to cyclic rainfall variations).
- Line 182: proposed by whom? The authors of the current paper? Baby et al 2018? The authors should be more precise by inserting a reference at the right place.
- Line 230: This is because DT can only be felt in the model as a base level change. And it takes time (according to the SPL) to propagate information from base level to high elevations areas. This should be added to the text to explain this difference between the response they observe.
- Line 237: The first sentence of this paragraph should refer to a figure as it is not clear where the reader should look to see that climate is a major driver of sedimentary fluxes.
- Line 239: It is very difficult to extract this information from Figure 5. What we see is a slightly darker reddish patch near the mouth of the Orange River. But the overall depositional thickness is very similar across the entire margin for the four models. Shown this way, it is impossible for the reader to appreciate that there is a noticeable difference between the models and (most importantly) that one of the model predictions is closer to the "real world" of which we have no display here. The author should provide a more quantitative estimate of these differences and comparison with data (using a cross section or a basin integrated value)
- Line 250: The authors have actually shown that the model's predictions are almost insensitive to the applied DT, despite major differences between the DT scenarios they tested. I do not think that their work can be used to say anything about whether DT is responsible for the recent increase in sedimentary flux as observed. As suggested by Baby et al, it would be more interesting to test the effect of the east African rift opening (as suggested by many, Burke, for example). It would be interesting to see whether any of the DT models shows the well documented southward propagation of the rift system. But we cannot appreciate this as the authors do not propose maps of the various DT models. This could be done by showing (maybe in an appendix) four snapshots at (30, 20, 15 and 0) of DT for the 4 models.
- Line 266: I do not see how an earlier period of uplift could have helped generate faster uplift in the most recent past. The authors should explain this better. Are they suggesting that there might be some recycling of sediment deposited on the shelf? If this is the case, the sediment flux information becomes useless to determine the timing of what happened on the continent (uplift/climate change, ...). This should be discussed in the introduction.
- Line 297: from this description of how the authors estimated their initial topography, it appears that the isostatic effect of deposited sediments was taken into account, whereas the authors state the contrary earlier in the text of the manuscript. This should be made clearer.
- Line 349: this is the only place where the authors specify which sea level curve has been used (of if any has been used); this should be included in the model description/setup.
- Figure A1 and many others below: We cannot see the black line so this figure is difficult to appreciate. It is also difficult to see why varying rainfall in this way (with no noticeable large increase in spatially averaged rainfall between 20 and 15 Ma) the model predicts such a large pulse of sediment flux over that period.
- Figure A3a: what is the purpose of using such a high resolution map of flexural thickness. In our case flexural response is only going to be important around the margins where the distribution of the load (eroded and deposited) is small enough for flexure to matter.
- Figure A3b: what is shown here? Estimated sediment thickness from the model, from observations? Over which period of time?
- The model resolution is very coarse. I do not think I have seen SPL models run at this low resolution since the early days of LEMs. Minimum resolution typically used even for continental scale computation should be of the order of 1x1 km. There are good theoretical reasons for this including how slope estimates are affected by spatial resolution and the scale at which the slopes relevant to SPL should be measured.
- Finally, the authors should compare their results to those obtained by Stanley et al (2021): JGR Solid Earth: Constraining plateau uplift in southern Africa by combining thermochronology, sediment flux, topography, and landscape evolution modeling. This study focuses on finding the best uplift history for the South African Plateau that can reproduce observed flux estimates using an LEM. In view of the commonality of objectives and methods, the results of this manuscript and those of Stanley et al (2021) should be compared.
Jean Braun
Citation: https://doi.org/10.5194/esurf-2021-89-RC1 -
RC2: 'Comment on esurf-2021-89', Anonymous Referee #2, 28 Jan 2022
General Comments:
This manuscript aims to test the effects of dynamic topography and climate variation on the sediment flux in southern Africa using a landscape evolution model. The authors aim to test whether any of these factors can produce the increase in sedimentary flux rates observed in some recent reconstructions (as shown in Baby et al., 2018; 2020 – it is not clear to me that previous reconstructions had the resolution to detect an uptick in flux). They first force the landscape evolution model with dynamic topography from four different geodynamic scenarios and find that the model predicted sedimentary flux rates do not match the observed increase in flux rates. They then introduce variability in rainfall based on climate reconstructions and find that rainfall variation can induce a wider range in modelled flux rates but that the patterns still do not match the observations. The correlation between instantaneous dynamic topography, erosion, and precipitation in the simulations is then used to argue that climate is a stronger driver than dynamic topography for erosion since 30 Ma.
I appreciate the modeling effort, but I have some serious issues with the manuscript as presented. Some aspects of the modeling methods and choices are not clear, and many of the methods are incompletely explained. The landscape modeling methods, parameters and choices for the LEM, and what sedimentary data they are trying to match and how various sedimentary datasets combined (or not) all need to be more clearly explained. For example, I think that the observation of increased sediment flux that they are trying to reproduce is that of Baby et al. (2018, 2020) since that is the one displayed on their comparison figure (fig 3) that shows an increase in flux, but this could be much more clearly stated in the beginning. I also think the landscape model should be explained more clearly and some of the many, many choices that go into selecting some of the fixed parameters justified (what are the slope and area coefficients of the stream power model, for example). Additionally, the purpose of the modelling exercise and what, if any, implications exist beyond this study are also not clearly articulated. Was the purpose to demonstrate that dynamic topography sourced from deep in the earth is not a major driver of erosion in the last 30 Ma in southern Africa? If so, I think they have demonstrated that successfully. However, but I find it a bit of a strawman argument and I am not sure what the wider implications are given that the maximum increase in dynamic topography of any of the models over the period of study was ~100 m, and two of the models are subsiding throughout this period. I think they have demonstrated that climate variability could be playing a key role over this period and that the system is complex with interactions between uplift, erodibility, and precipitation. However, have not adequately demonstrated that climate replicates the observations or that it is the only explanation, and the complexity of the system is not a surprise in my opinion. I think it is a neat test to try to drive the landscape model with the dynamic topography predictions, but at this stage I think the manuscript requires extreme revision to be publishable. I outline some more specific points below.
Specific Comments:
Line 12-13: Unless I have misunderstood the methods, this statement seems wrong or misleading. My understanding is that the numerical simulations were driven with the dynamic topography uplift from geodynamic models and inferred precipitation maps that outputs were compared with Earth data not “a series of numerical simulations forced with Earth data”. The distinction is important, and if they are truly forcing their simulations with Earth data that needs to be explained much more clearly.
Line 16-17: I am not sure I agree that the statement “paleo-rainfall regimes are the major forcing mechanism that drives the recent increase of sediment flux in the Orange basin” is fully supported by the manuscript. Paleo-rainfall could be a major forcing mechanism, but it hasn’t been demonstrated that it matches the observations. Also, the logic here seems to be that if dynamic topography is not the forcing mechanism that precipitation must be. It certainly could be, this ignores other possible drivers that haven’t. In this particular setting, many have proposed upper mantle variability may be responsible for recent uplift/erosion (e.g. Burke & Gunnell, 2008; Paul et al., 2014). The authors recognize that the lack of upper mantle input might be affecting their conclusions about dynamic topography in the conclusion (line 251-3) but don’t acknowledge that this could also affect the robustness of the conclusion about the importance of climate.
Line 23: This first sentence and to some extent the first two paragraphs of the introduction are somewhat misleading. Most, if not all, of the previous studies linking source and sink in southern Africa have focused on replicating the major pulse(s) of sedimentation observed in the Cretaceous in the Orange River Basin and off the southern coast (Tinker et al., 2008a, 2008b; Rouby et al., 2009; Guillocheau et al., 2012, Braun et al., 2014; Stanley et al. 2021). As written the first sentence of the paper implies that previous studies have focused on the post 30 Ma increase in sedimentation, which is not the case. This paper focuses on the post-30 Ma history, which is a worthwhile exercise, but it shouldn’t be directly juxtaposed with the previous work without acknowledging that the previous work was focused on a longer observation period. The Cretaceous pulse of sediment in the marine record is much larger than the post 30 Ma increase in sedimentation, especially in the Orange River basin (Baby et al., 2020) and it seems disingenuous not to mention this (it also provides support for one of this manuscript’s conclusions that much of the topographic uplift pre-dated the Oligocene, even though that hypothesis was not directly tested here).
Line 46-47: It seems odd to cite Partridge & Maud 1987 here but not the new geodynamic models
Line 47-50: It would be helpful to show these scenarios on a figure. I assume they correspond to the four scenarios shown in Figure 1, but it is not immediately clear which is which
Line51-53: I am not clear what is meant by flexural uplifts – be more specific?
Lines 88-95: It is a little confusing to me why one would hypothesize sedimentation rates to increase from the two subsiding scenarios, and even the two uplifting ones have relatively low magnitudes of uplift. Braun et al. (2013, 2013) showed that one of the reasons that dynamic topography can cause so much erosion is because it causes widespread tilting that can cause drainage rearrangement and steepens slopes over large regions, and Stanley et al. (2021) showed that the shape of the uplift (whether tilted or uniform) strongly controlled the erosional response for a given magnitude of dynamic uplift. It is difficult to tell what shape and variabilities these dynamic topography models have based on the information in Figure 1 and whether it is reasonable to hypothesize that they could be causing an increase in sedimentation in a complex system. Clearly stating why these scenarios might cause the increase in sedimentation rate observed (and perhaps which are more likely) might help clarify some of the purpose of the modeling.
Line 115-116: This exercise alone and the assumptions made suggest that the 1st order topography/uplift of the plateau existed at the start of the model. This means that topographic development isn’t something that’s really being tested by the landscape modelling exercise (even though the suggestion of pre-Oligocene uplift is highlighted as an implication in the abstract). It seems that these paleotopography maps (i.e. the initial condition for the models) could be affecting the fluxes as much (more?) than the dynamic uplift driving the models, but this isn’t really tested.
Line 161-164: Two things about these comparisons. First, I guess that some of the reason the modelled flux matches the flux rate is because the choice of some parameters in the model was made to match well, and this should be acknowledged. In particular, the erosivity parameter in the stream power law, is not very well constrained and can be affected by many factors. If a base erosivity had been chosen an order of magnitude larger or smaller, that could have been justified within the range of reasonable values for erosivity and would have affected the flux rates, potentially substantially, I think. This should be acknowledged/discussed. Second, it is a little hard to compare the flux rates because the observational data is averaged over much larger time periods because of limited age resolution in the sedimentary record. The model outputs can resolve 100 000 year variations, but the natural data never could so a more nuanced discussion of the comparison is needed.
Line 185-187 “This can be explained”: what does “This” refer to? Statement needs more explanation
Line 197-8: This statement seems somewhat circular/obvious, what is this statement trying to convey?
Line 228-9: “Smoothed” seems like an odd choice of adjective here. The precipitation changes seem to be overwhelming any dynamic topography signal – the correlation coefficients have changed sign for nearly every comparison with dynamic topography. This also seems true when comparing the dynamic topography only fluxes and the ones with precip (Fig 3). I’m somewhat curious what the fluxes would look like simply starting with the “paleotopogrpahy” inputs that you started with and having no dynamic topography forcing. The flux patterns in 3a are fairly similar between the models, and TX08 has the largest flux despite subsiding throughout the model run. It also has the highest elevations in the input topography so it seems that this starting topography and then the isostatic uplift in response to erosion is swamping any erosion signal driven by dynamic topography. This isostatic, erosion driven uplift is then only enhanced by precipitation increases (and of course modulated by erodibility).
Lines 238-242 and Figure 5: These statements are very hard to evaluate without a comparison to the actual observations. Also, Figures 5a-d look quite similar overall to me, so some way of more direct comparisons to highlight differences (if they exist) is necessary to support the statement that only AY18 and TX08 show preferential Orange River mouth deposition.
Lines 251-254: This mention of the upper mantle here is in important caveat that does not come up at all until the conclusions, and then is supported by a new test and appendix figure that is also not described or discussed until the conclusions section. This merits more discussion in the main text.
Line 271-272: What is meant by a “new framework to fill the data gap”?
Line 273: I realize the model did vary sea level, but there is little to no discussion of the effects on the erosion / sediment flux. This should be explored, especially if it is mentioned here in the conclusions
Lines 292-302: This description of the landscape model is inadequate. A reader should be able to get at least a general sense of what was done without needing to become intimately familiar with the Badlands code. For example, what are the parameters for the stream power law? Only erodibility is shown in the table A1, what about the slope and area exponents? Are the processes of wave induced transport and growth of coral reefs included in this study? If so, what are the parameters involved? More of a description of the marine processes and transitional/coastal areas is needed – what are the units on these parameters given? Is diffusion the only process acting in the marine environment?
Lines 304-309, Table A2 and Figure A2. There seem to be some conflicts between the figure A2 (scale from 0-1 for erodibility) and Table A2 with values of 1-3.2 when figure A2 is stated to be based on table A2. I also find this map a bit confusing because the areas where metamorphic Precambrian basement are exposed look blue implying high (I think?) erodibility similar to the shelves where I would expect (and table A2 would imply) that these areas should have low erodibility (e.g. the Namaqua-Natal belt near the Orange River mouth, Zimbabwe Craton area in the northeast).
Figure A1: Black coastline is not on the map and would be helpful.
Figure A3: Many of the references used to create the sediment thicknesses in part b are not in the reference list (Intawong, Maystrenko, Koopman, Kuhlman). Since this is a major input to creating the paleo topographies and also one of the comparisons for the model outputs, a description of how these were estimated/combined is needed.
Figure A7: Two rows are shown as “Rainfall uniform at 0.6 m/yr, Erodibility uniform” but have different coefficients. One is clearly must be mislabeled.
Table A1: There are a lot more parameters that seem like they should be included here (see comments on landscape modelling methods above). Also, how did you choose 1.6e-7 for the base erodibility? Did you try others and what was the effect?
Technical Comments:
Line 41-44: This sentence was somewhat confusingly worded – I think it would make more sense if it started with “While” rather than “If”
Line 251: I think this should be “allow us to generate”
Note: I completed the above review without reading the previously posted reviewer comment as I think it is valuable to have two independent reviews/read throughs that are not biased by one another. However I have now read the other reviewer’s comments and I agree with much of what he says. His point 3 about the differences in landscape response time to a change in uplift vs a change in precipitation is not one I had appreciated while reading the paper, but it seems like would make it rather difficult to compare the uplift and precipitation correlations with instantaneous erosion directly. I also agree with many of his points about he erosivity parameter - something that was also an area of concern in my reading of the manuscript.
Citation: https://doi.org/10.5194/esurf-2021-89-RC2
Interactive discussion
Status: closed
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RC1: 'Comment on esurf-2021-89', Jean Braun, 17 Jan 2022
Review Mallard and Salles, ESURFD 2021
The manuscript by Mallard and Salles describes the results of a study aiming at explaining the observed increase in sedimentary flux from the Southern African craton documented by Baby et al (2018 an 2020) as resulting from dynamic topography (DT) or enhanced precipitation. For this the authors use a surface process model that is subject to a range of model-deduced DT estimates over the past 30 Myr and a rainfall function/distribution that has been reconstructed from various previous studies. The authors find that the sedimentary fluxes predicted by the model offer little resemblance to the observed ones. The observed amplitude of the change in sedimentary flux can be matched by varying rainfall but no its timing. The recent increase (i.e., in the past 10 Myr) is never reproduced by any model scenario. Despite this, the authors attempt to determine which of the imposed drivers is responsible for the increase in erosion rate (and thus in flux) predicted by the model, by computing correlation maps between erosion rate, DT and rainfall for each of the tested model scenarios.
Although I appreciate the efforts that the authors have put in this modeling exercise, I have to recommend that it be rejected as it contains major methodological flaws, and is not clearly presented. I justify my recommendation in the rest of this review and, where possible, I provide hints/suggestions on how this work and how it is presented could be improved.
My major concern include:
- A lack of clear focus/objective for the paper: what are the authors trying to demonstrate/prove? Are they trying to demonstrate that one DT model fits better than others? That DT or climate variations can or cannot be responsible for the observed increased in sedimentary flux in the Orange basin? Reading through the introduction I do not see any clear questions or hypotheses being stated that are later tested against each other. Similarly reading through the conclusions I do not see what the major findings are except that none of the tested DT scenarios or climate scenarios can explain the variations in sedimentary fluxes. The various scenarios are not ranked by their fit to the observations. No alternative scenario is offered apart from stating that some sediment may have been recycled within the marginal basin which implies that the sedimentary flux data cannot be used to say something about what happens on the continent.
- Like others before (Roberts and White, 2010; Paul et al, 2014), the authors have assumed that they know the erodibility coefficient (Kf) in the SPL. This is a major flaw of their approach as WE DO NOT KNOW its value within a few orders of magnitude. Where does the value of 1.6e-7 comes from? Note also that any given value of Kf is only meaning fully if we know what m (the area exponent in the SPL) is. To further assume, like the authors have done, a one-to-one correspondence between rock type and Kf is also rather misleading, especially with a precision that assumes that variations of a few tens of percents are meaningful. The authors should know that there are many factors that influence Kf such as fracturation, degree of weathering, model resolution, etc. To scale Kf, the authors have also used a present-day map of lithologies that, in my opinion, is irrelevant when applied to a model that is run over 30 Myr (the lithology of eroded material is relevant). To present results that depend on the absolute value of the coefficient Kf, one must use time-relevant constrain (thermochron ages, sediment fluxes, etc.) to calibrating Kf. This has been shown over and over (a great demonstration shown in Fox et al, 2014's work on inverting Taiwanese river profiles).
- The authors correlate predicted erosion rate, with the imposed rainfall rate and and DT variations in an attempt to infer which of the main drivers (DT or climate) is responsible for the predicted variations in erosion rate. First I do not understand the purpose of this exercise as, regardless of what is driving the erosion rate, the model cannot represent the observed sedimentary flux. Second, the authors seem to not take into account that, according to the SPL, there always exists a large time lag between variations in uplift rate (or in base level) and the resulting variations in erosion rate, whereas there is no such time lag between imposed variations in rainfall rate and erosion rate (see Whipple and Mead, 2006, Fig 4). Note also that the time lag mentioned above can be of the order of a few to a few tens of million years, depending mostly on the assumed value of the erodibility coefficient Kf, if n=1. The lower Kf, the longer the time lag.
- The way the DT models are incorporated into the LEM is such that very different scenarios (some predict overall subsidence while others predict uplift) all produce a very similar sedimentary flux prediction. This demonstrates that the model is almost insensitive to DT scenarios and that most of the erosion is driven by erosion of the short wavelength topography which is basically identical to the present-day topography.
- The model is poorly presented. There is no brief description of the main relevant equations; the value of key coefficients (such as the slope and discharge exponents, n and m, in the SPL) is not given, which makes the interpretation of the results very difficult to assess. There are major issues with some of the figures too (see below).
Other points that need to be addressed:
- Line 51: What do the authors mean by “different flexural uplifts”? Different flexural thicknesses? Flexure is a response to another mechanism such as thinning or thicknenning of the lithosphere/crust or to denudation/deposition. It cannot be an uplift in its own.
- Line 60: How did the authors obtain absolute values for paleo rainfall rates? In the appendix, they provide references where paleo indicators are given. They need to explain to the reader how they have been able to go from indicators to actual rainfall rates.
- Line 69: As explained earlier I have major concerns about the erodibility. The value that is given in the relevant table is very low and should be justified.
- Line 94: The authors should compare the various DT models graphically in an appendix/supplementary section. They should also discuss the origin of their differences. Some predict uplift while others predict subsidence… So what is the point in trying to use constraints that do not agree with each other? Alternatively the authors should have as an objective to differentiate between them. But this is not stated/proposed.
- After the paragraph ending at line 96, the authors should show to the reader what the predicted fluxes from Baby et al (2018, 2020) look like. It would be interesting to see how they correlate with the different dynamic topography history estimates. We also need to know what the flux estimates correspond to: are they just from the mouth of the Orange Basin? Or from what Baby et al call the Cape area too? I also believe that Baby et al produce uncertainty estimates of their fluxes. This is really important as any model that would fit the data within uncertainty should be considered as equally adequate to reproduce the data. This is not provided or discussed here.
- Line 110: I am surprised that the authors included the weight of the sediments removed from the continent but not the sediment accumulated in the margins. In theory (by mass conservation) they should be equal in volume so that the weight of the deposited sediment should be much more localized and may therefore cause a much greater flexural isostatic effect along the margins. Remember that for the LEM, the variations in the height of the base level is the only way it can feel the perturbations caused by DT; it is therefore very important that any other process that can affect the relative position of the base level is taken into account.
- Paragraph ending line 116: What about using an optimization/iterative scheme to determine the optimum initial topography, in which whatever is predicted to have been eroded/deposited is used to readjust the initial topography. This should converge very quickly.
- Line 125: The authors should mention the values they have used for the slope (n) and area (m) exponents of the SPL. These are critical to understand what they have done/interpret their results. The relationship between impose variations in rainfall rate and predicted erosion rate depends strongly on m.
- Line 140: It is not supposing that the predicted topography looks like the present-day topography as you simply add DT to an initial topography that is computed by removing DT from the present-day topography… This is not a result but is part of the model setup.
- Line 150: Why discuss first how the model matches cosmogenic-derived erosion rates (that have not been presented in the data/introduction part of the paper) rather than sediment fluxes that have been mentioned earlier.
- Figure 3: There are major issues with this figure: It says that the dashed lines correspond to values calculated from the landscape evolution model whereas one of them is labeled “Baby et al, 2020” which seems to imply that it corresponds to observed values. I also note a second dashed line with a reference to Kuhlmann et al, 2010, which is not mentioned anywhere else in the paper (not even the reference list). The authors should be more precise.
- Line 161: This implies that the model or the setup the authors have used (substracting first DT then adding it) are insensitive to the assumed DT: whether South Africa has gone up or down over the past 30 Myrs has almost no effect on the predicted sedimentary flux. This implies that the flux and thus the erosion that the model predicts are caused by a slow "downwearing" of the topography that would also likely take place if one had no DT applied to the model.
- Line 165: Here the authors envisage a set of possible reasons for why the model cannot reproduce the sedimentary flux, but they do not envisage the possibility that the DT models are wrong or that DT may not be the driver of the increased flux. It could be the southward propagation of the South African Rift swell, for example.
- Line 175: from the amplitude of the imposed increase in rainfall (4.4) and that of the resulting increase in sedimentary flux (2.2) I can derive that the value of m that the authors have used must be close to 0.5. This relationship between m and the relative changes in driver/response should be discussed (see Braun et al, 2015, EsurfD, Erosional response of an actively uplifting mountain belt to cyclic rainfall variations).
- Line 182: proposed by whom? The authors of the current paper? Baby et al 2018? The authors should be more precise by inserting a reference at the right place.
- Line 230: This is because DT can only be felt in the model as a base level change. And it takes time (according to the SPL) to propagate information from base level to high elevations areas. This should be added to the text to explain this difference between the response they observe.
- Line 237: The first sentence of this paragraph should refer to a figure as it is not clear where the reader should look to see that climate is a major driver of sedimentary fluxes.
- Line 239: It is very difficult to extract this information from Figure 5. What we see is a slightly darker reddish patch near the mouth of the Orange River. But the overall depositional thickness is very similar across the entire margin for the four models. Shown this way, it is impossible for the reader to appreciate that there is a noticeable difference between the models and (most importantly) that one of the model predictions is closer to the "real world" of which we have no display here. The author should provide a more quantitative estimate of these differences and comparison with data (using a cross section or a basin integrated value)
- Line 250: The authors have actually shown that the model's predictions are almost insensitive to the applied DT, despite major differences between the DT scenarios they tested. I do not think that their work can be used to say anything about whether DT is responsible for the recent increase in sedimentary flux as observed. As suggested by Baby et al, it would be more interesting to test the effect of the east African rift opening (as suggested by many, Burke, for example). It would be interesting to see whether any of the DT models shows the well documented southward propagation of the rift system. But we cannot appreciate this as the authors do not propose maps of the various DT models. This could be done by showing (maybe in an appendix) four snapshots at (30, 20, 15 and 0) of DT for the 4 models.
- Line 266: I do not see how an earlier period of uplift could have helped generate faster uplift in the most recent past. The authors should explain this better. Are they suggesting that there might be some recycling of sediment deposited on the shelf? If this is the case, the sediment flux information becomes useless to determine the timing of what happened on the continent (uplift/climate change, ...). This should be discussed in the introduction.
- Line 297: from this description of how the authors estimated their initial topography, it appears that the isostatic effect of deposited sediments was taken into account, whereas the authors state the contrary earlier in the text of the manuscript. This should be made clearer.
- Line 349: this is the only place where the authors specify which sea level curve has been used (of if any has been used); this should be included in the model description/setup.
- Figure A1 and many others below: We cannot see the black line so this figure is difficult to appreciate. It is also difficult to see why varying rainfall in this way (with no noticeable large increase in spatially averaged rainfall between 20 and 15 Ma) the model predicts such a large pulse of sediment flux over that period.
- Figure A3a: what is the purpose of using such a high resolution map of flexural thickness. In our case flexural response is only going to be important around the margins where the distribution of the load (eroded and deposited) is small enough for flexure to matter.
- Figure A3b: what is shown here? Estimated sediment thickness from the model, from observations? Over which period of time?
- The model resolution is very coarse. I do not think I have seen SPL models run at this low resolution since the early days of LEMs. Minimum resolution typically used even for continental scale computation should be of the order of 1x1 km. There are good theoretical reasons for this including how slope estimates are affected by spatial resolution and the scale at which the slopes relevant to SPL should be measured.
- Finally, the authors should compare their results to those obtained by Stanley et al (2021): JGR Solid Earth: Constraining plateau uplift in southern Africa by combining thermochronology, sediment flux, topography, and landscape evolution modeling. This study focuses on finding the best uplift history for the South African Plateau that can reproduce observed flux estimates using an LEM. In view of the commonality of objectives and methods, the results of this manuscript and those of Stanley et al (2021) should be compared.
Jean Braun
Citation: https://doi.org/10.5194/esurf-2021-89-RC1 -
RC2: 'Comment on esurf-2021-89', Anonymous Referee #2, 28 Jan 2022
General Comments:
This manuscript aims to test the effects of dynamic topography and climate variation on the sediment flux in southern Africa using a landscape evolution model. The authors aim to test whether any of these factors can produce the increase in sedimentary flux rates observed in some recent reconstructions (as shown in Baby et al., 2018; 2020 – it is not clear to me that previous reconstructions had the resolution to detect an uptick in flux). They first force the landscape evolution model with dynamic topography from four different geodynamic scenarios and find that the model predicted sedimentary flux rates do not match the observed increase in flux rates. They then introduce variability in rainfall based on climate reconstructions and find that rainfall variation can induce a wider range in modelled flux rates but that the patterns still do not match the observations. The correlation between instantaneous dynamic topography, erosion, and precipitation in the simulations is then used to argue that climate is a stronger driver than dynamic topography for erosion since 30 Ma.
I appreciate the modeling effort, but I have some serious issues with the manuscript as presented. Some aspects of the modeling methods and choices are not clear, and many of the methods are incompletely explained. The landscape modeling methods, parameters and choices for the LEM, and what sedimentary data they are trying to match and how various sedimentary datasets combined (or not) all need to be more clearly explained. For example, I think that the observation of increased sediment flux that they are trying to reproduce is that of Baby et al. (2018, 2020) since that is the one displayed on their comparison figure (fig 3) that shows an increase in flux, but this could be much more clearly stated in the beginning. I also think the landscape model should be explained more clearly and some of the many, many choices that go into selecting some of the fixed parameters justified (what are the slope and area coefficients of the stream power model, for example). Additionally, the purpose of the modelling exercise and what, if any, implications exist beyond this study are also not clearly articulated. Was the purpose to demonstrate that dynamic topography sourced from deep in the earth is not a major driver of erosion in the last 30 Ma in southern Africa? If so, I think they have demonstrated that successfully. However, but I find it a bit of a strawman argument and I am not sure what the wider implications are given that the maximum increase in dynamic topography of any of the models over the period of study was ~100 m, and two of the models are subsiding throughout this period. I think they have demonstrated that climate variability could be playing a key role over this period and that the system is complex with interactions between uplift, erodibility, and precipitation. However, have not adequately demonstrated that climate replicates the observations or that it is the only explanation, and the complexity of the system is not a surprise in my opinion. I think it is a neat test to try to drive the landscape model with the dynamic topography predictions, but at this stage I think the manuscript requires extreme revision to be publishable. I outline some more specific points below.
Specific Comments:
Line 12-13: Unless I have misunderstood the methods, this statement seems wrong or misleading. My understanding is that the numerical simulations were driven with the dynamic topography uplift from geodynamic models and inferred precipitation maps that outputs were compared with Earth data not “a series of numerical simulations forced with Earth data”. The distinction is important, and if they are truly forcing their simulations with Earth data that needs to be explained much more clearly.
Line 16-17: I am not sure I agree that the statement “paleo-rainfall regimes are the major forcing mechanism that drives the recent increase of sediment flux in the Orange basin” is fully supported by the manuscript. Paleo-rainfall could be a major forcing mechanism, but it hasn’t been demonstrated that it matches the observations. Also, the logic here seems to be that if dynamic topography is not the forcing mechanism that precipitation must be. It certainly could be, this ignores other possible drivers that haven’t. In this particular setting, many have proposed upper mantle variability may be responsible for recent uplift/erosion (e.g. Burke & Gunnell, 2008; Paul et al., 2014). The authors recognize that the lack of upper mantle input might be affecting their conclusions about dynamic topography in the conclusion (line 251-3) but don’t acknowledge that this could also affect the robustness of the conclusion about the importance of climate.
Line 23: This first sentence and to some extent the first two paragraphs of the introduction are somewhat misleading. Most, if not all, of the previous studies linking source and sink in southern Africa have focused on replicating the major pulse(s) of sedimentation observed in the Cretaceous in the Orange River Basin and off the southern coast (Tinker et al., 2008a, 2008b; Rouby et al., 2009; Guillocheau et al., 2012, Braun et al., 2014; Stanley et al. 2021). As written the first sentence of the paper implies that previous studies have focused on the post 30 Ma increase in sedimentation, which is not the case. This paper focuses on the post-30 Ma history, which is a worthwhile exercise, but it shouldn’t be directly juxtaposed with the previous work without acknowledging that the previous work was focused on a longer observation period. The Cretaceous pulse of sediment in the marine record is much larger than the post 30 Ma increase in sedimentation, especially in the Orange River basin (Baby et al., 2020) and it seems disingenuous not to mention this (it also provides support for one of this manuscript’s conclusions that much of the topographic uplift pre-dated the Oligocene, even though that hypothesis was not directly tested here).
Line 46-47: It seems odd to cite Partridge & Maud 1987 here but not the new geodynamic models
Line 47-50: It would be helpful to show these scenarios on a figure. I assume they correspond to the four scenarios shown in Figure 1, but it is not immediately clear which is which
Line51-53: I am not clear what is meant by flexural uplifts – be more specific?
Lines 88-95: It is a little confusing to me why one would hypothesize sedimentation rates to increase from the two subsiding scenarios, and even the two uplifting ones have relatively low magnitudes of uplift. Braun et al. (2013, 2013) showed that one of the reasons that dynamic topography can cause so much erosion is because it causes widespread tilting that can cause drainage rearrangement and steepens slopes over large regions, and Stanley et al. (2021) showed that the shape of the uplift (whether tilted or uniform) strongly controlled the erosional response for a given magnitude of dynamic uplift. It is difficult to tell what shape and variabilities these dynamic topography models have based on the information in Figure 1 and whether it is reasonable to hypothesize that they could be causing an increase in sedimentation in a complex system. Clearly stating why these scenarios might cause the increase in sedimentation rate observed (and perhaps which are more likely) might help clarify some of the purpose of the modeling.
Line 115-116: This exercise alone and the assumptions made suggest that the 1st order topography/uplift of the plateau existed at the start of the model. This means that topographic development isn’t something that’s really being tested by the landscape modelling exercise (even though the suggestion of pre-Oligocene uplift is highlighted as an implication in the abstract). It seems that these paleotopography maps (i.e. the initial condition for the models) could be affecting the fluxes as much (more?) than the dynamic uplift driving the models, but this isn’t really tested.
Line 161-164: Two things about these comparisons. First, I guess that some of the reason the modelled flux matches the flux rate is because the choice of some parameters in the model was made to match well, and this should be acknowledged. In particular, the erosivity parameter in the stream power law, is not very well constrained and can be affected by many factors. If a base erosivity had been chosen an order of magnitude larger or smaller, that could have been justified within the range of reasonable values for erosivity and would have affected the flux rates, potentially substantially, I think. This should be acknowledged/discussed. Second, it is a little hard to compare the flux rates because the observational data is averaged over much larger time periods because of limited age resolution in the sedimentary record. The model outputs can resolve 100 000 year variations, but the natural data never could so a more nuanced discussion of the comparison is needed.
Line 185-187 “This can be explained”: what does “This” refer to? Statement needs more explanation
Line 197-8: This statement seems somewhat circular/obvious, what is this statement trying to convey?
Line 228-9: “Smoothed” seems like an odd choice of adjective here. The precipitation changes seem to be overwhelming any dynamic topography signal – the correlation coefficients have changed sign for nearly every comparison with dynamic topography. This also seems true when comparing the dynamic topography only fluxes and the ones with precip (Fig 3). I’m somewhat curious what the fluxes would look like simply starting with the “paleotopogrpahy” inputs that you started with and having no dynamic topography forcing. The flux patterns in 3a are fairly similar between the models, and TX08 has the largest flux despite subsiding throughout the model run. It also has the highest elevations in the input topography so it seems that this starting topography and then the isostatic uplift in response to erosion is swamping any erosion signal driven by dynamic topography. This isostatic, erosion driven uplift is then only enhanced by precipitation increases (and of course modulated by erodibility).
Lines 238-242 and Figure 5: These statements are very hard to evaluate without a comparison to the actual observations. Also, Figures 5a-d look quite similar overall to me, so some way of more direct comparisons to highlight differences (if they exist) is necessary to support the statement that only AY18 and TX08 show preferential Orange River mouth deposition.
Lines 251-254: This mention of the upper mantle here is in important caveat that does not come up at all until the conclusions, and then is supported by a new test and appendix figure that is also not described or discussed until the conclusions section. This merits more discussion in the main text.
Line 271-272: What is meant by a “new framework to fill the data gap”?
Line 273: I realize the model did vary sea level, but there is little to no discussion of the effects on the erosion / sediment flux. This should be explored, especially if it is mentioned here in the conclusions
Lines 292-302: This description of the landscape model is inadequate. A reader should be able to get at least a general sense of what was done without needing to become intimately familiar with the Badlands code. For example, what are the parameters for the stream power law? Only erodibility is shown in the table A1, what about the slope and area exponents? Are the processes of wave induced transport and growth of coral reefs included in this study? If so, what are the parameters involved? More of a description of the marine processes and transitional/coastal areas is needed – what are the units on these parameters given? Is diffusion the only process acting in the marine environment?
Lines 304-309, Table A2 and Figure A2. There seem to be some conflicts between the figure A2 (scale from 0-1 for erodibility) and Table A2 with values of 1-3.2 when figure A2 is stated to be based on table A2. I also find this map a bit confusing because the areas where metamorphic Precambrian basement are exposed look blue implying high (I think?) erodibility similar to the shelves where I would expect (and table A2 would imply) that these areas should have low erodibility (e.g. the Namaqua-Natal belt near the Orange River mouth, Zimbabwe Craton area in the northeast).
Figure A1: Black coastline is not on the map and would be helpful.
Figure A3: Many of the references used to create the sediment thicknesses in part b are not in the reference list (Intawong, Maystrenko, Koopman, Kuhlman). Since this is a major input to creating the paleo topographies and also one of the comparisons for the model outputs, a description of how these were estimated/combined is needed.
Figure A7: Two rows are shown as “Rainfall uniform at 0.6 m/yr, Erodibility uniform” but have different coefficients. One is clearly must be mislabeled.
Table A1: There are a lot more parameters that seem like they should be included here (see comments on landscape modelling methods above). Also, how did you choose 1.6e-7 for the base erodibility? Did you try others and what was the effect?
Technical Comments:
Line 41-44: This sentence was somewhat confusingly worded – I think it would make more sense if it started with “While” rather than “If”
Line 251: I think this should be “allow us to generate”
Note: I completed the above review without reading the previously posted reviewer comment as I think it is valuable to have two independent reviews/read throughs that are not biased by one another. However I have now read the other reviewer’s comments and I agree with much of what he says. His point 3 about the differences in landscape response time to a change in uplift vs a change in precipitation is not one I had appreciated while reading the paper, but it seems like would make it rather difficult to compare the uplift and precipitation correlations with instantaneous erosion directly. I also agree with many of his points about he erosivity parameter - something that was also an area of concern in my reading of the manuscript.
Citation: https://doi.org/10.5194/esurf-2021-89-RC2
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