the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
The linear feedback precipitation model (LFPM 1.0) – a simple and efficient model for orographic precipitation in the context of landform evolution modeling
Stefan Hergarten
Jörg Robl
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- Final revised paper (published on 10 Mar 2022)
- Supplement to the final revised paper
- Preprint (discussion started on 18 Jun 2021)
- Supplement to the preprint
Interactive discussion
Status: closed
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CEC1: 'Comment on gmd-2021-179', Astrid Kerkweg, 09 Jul 2021
Dear authors,
in my role as Executive editor of GMD, I would like to bring to your attention our Editorial version 1.2: https://www.geosci-model-dev.net/12/2215/2019/
This highlights some requirements of papers published in GMD, which is also available on the GMD website in the ‘Manuscript Types’ section: http://www.geoscientific-model-development.net/submission/manuscript_types.html
In particular, please note that for your paper, the following requirements have not been met in the Discussions paper:
- "The main paper must give the model name and version number (or other unique identifier) in the title."
- Code must be published on a persistent public archive with a unique identifier for the exact model version described in the paper or uploaded to the supplement, unless this is impossible for reasons beyond the control of authors. All papers must include a section, at the end of the paper, entitled "Code availability". Here, either instructions for obtaining the code, or the reasons why the code is not available should be clearly stated. It is preferred for the code to be uploaded as a supplement or to be made available at a data repository with an associated DOI (digital object identifier) for the exact model version described in the paper. Alternatively, for established models, there may be an existing means of accessing the code through a particular system. In this case, there must exist a means of permanently accessing the precise model version described in the paper. In some cases, authors may prefer to put models on their own website, or to act as a point of contact for obtaining the code. Given the impermanence of websites and email addresses, this is not encouraged, and authors should consider improving the availability with a more permanent arrangement. Making code available through personal websites or via email contact to the authors is not sufficient. After the paper is accepted the model archive should be updated to include a link to the GMD paper.
Thus provide the models name (or acronym) and version number in the title of your revised manuscript.
As the links you are providing are no persistent archives, please provide a persistent release for the exact source code version used for the publication in this paper (asap and not only at final publication!). As explained in https://www.geoscientific-model-development.net/about/manuscript_types.html the preferred reference to this release is through the use of a DOI which then can be cited in the paper.
Yours,
Astrid Kerkweg
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AC1: 'Reply on CEC1', Stefan Hergarten, 11 Aug 2021
Dear Astrid Kerkweg,
thanks for reminding us! We have now moved the codes and data to a persistent archive at https://freidok.uni-freiburg.de/data/219131, doi 10.6094/UNIFR/219131. Since there are always at least some changes to the figures in the revised version, I usually prefer to have the final version archived instead of the first version, but I do not mind.
We will also think about a name or acronym for the title. Personally, however, I am not convinced that each more or less "new" set of equations deserves an own name or acronym, although I accept that this has become some kind of standard in order to promote work. However, it should not be reduced to the name of the software where it is actually implemented.
Best regards,
Stefan Hergarten
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RC1: 'Comment on gmd-2021-179', Kyungrock Paik, 18 Jul 2021
Co-evolution of topography and local climate is a hot subject, and a numerical modeling approach as attempted in this paper is highly anticipated. I found this paper interesting and well-written. I see a great potential contribution of this paper to the community. Nevertheless, basic questions remain as follows, for the submitted manuscript.
I first am a bit uncertain about the 'main' focus of this study. Is this to propose a new orographic precipitation model? Or do authors put focus on co-evolution? I think this has to be clarified first. I have different comments depending on the choice. If the former is the focus (seemingly from the title of the manuscript), I feel that it requires model comparison and validation with observed data. Earlier orographic rainfall models (e.g., Smith and Barstad, 2004 cited in this work) have done this job thoroughly. By contrast, there is no single comparison with a real precipitation field. This is something missing and requires some work.
If the focus is the latter, I recommend authors to revise the title and importantly compare their results with earlier co-evolution studies. Many co-evolution modeling studies have been published recently, and most of them are not mentioned in this manuscript. I suggest authors first to check the following paper, just published in HESS, and references cited in that paper.
Paik, K. and Kim, W.: Simulating the evolution of the topography–climate coupled system, Hydrol. Earth Syst. Sci., 25, 2459–2474, https://doi.org/10.5194/hess-25-2459-2021, 2021.
Even the focus is on co-evolution itself, some validation of a new orographic model is still desired. However, as long as the authors make good scientific contributions with their modeling, the necessity for thorough validation is less important than the previous story. There have been some earlier studies that I remember which adopted very simple orographic models with little validation but were published due to their independent scientific contributions.
Below, I provide more technical comments.
* L39: This concept, i.e., in reality the flow discharge, instead of the drainage area, controls the erosion is not new. For example, it was stated in Paik (2012 ref below) as "While the above equation expresses the erosion rate as a function of the drainage area, it should be the flow that contributes to the bedrock erosion in reality. In the formulation of empirical equations, the drainage area has often been chosen as a surrogate of the flow discharge due to the difficulty of measuring flow discharge. However, there is no need to use the drainage area instead of flow in the numerical modeling."
Paik, K.: Simulation of landscape evolution using a global flow path search method, Environmental Modelling & Software, 33, 35-47, https://doi.org/10.1016/j.envsoft.2012.01.005, 2012.
* Some notations are not defined in the text, e.g., u_v/c in equation (3).
* L140: I personally had also been tempted to use this approach. But I have had the following peer comment on this idea some time ago: ".. the temperature change with mean elevation change is not likley to represent a reasonable assumption. Yes, the atmosphere is cooler over moutains - but the air souce for the precipitation is over an ocean and topography is not going to force the air to be cooler upwind of it." I still advocate this equation but you would need some supporting argument for its use.
* L364-365: If this is correct, it can be a strong reason to develop an alternative model. But you should demonstrate it in comparison with real observation and Smith and Barstad (2004) model to convince it.
* Section 7.1: The simulation domain here is only about a few hundred km. How can these simulations capture the 'continentality'?
Paik
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AC2: 'Reply on RC1', Stefan Hergarten, 12 Aug 2021
Dear Kyungrock Paik,
thank you very much for your review! Unfortunately, we did not see your very recent paper in HESS and will of course refer to your study in the discussion of our examples in Section 7.
The focus of our paper is indeed on the new model approach for orographic precipitation -- but of course only on a minimum level required for modeling the co-evolution of topography and climate. We started from the model of Smith & Barstad (2004) (SB model in the following) and tried to improve it in detail first, e.g., by lateral dispersion. However, it turned out that the SB model is very limited, although a good approach at the time. As discussed in Section 6 of our manuscript, the SB model cannot capture large-scale patterns. Smith & Barstad already mentioned the respective scales in their paper (Eq. 7), and the modified source term introduced in their Section 3 does not change this behavior fundamentally. So about your comment "L364-365: If this is correct, it can be a strong reason to develop an alternative model.": Of course, it is, and designing a new model from the scratch turned out to be simpler than extending the SB model accordingly.
Since the SB model is apparently often implemented as some kind of black box (which is tempting because the Fourier representation is formally simple), it makes sense to extend the comparison of our model and the SB model a bit. Maybe we can use the scenario with the plateau from Sect. 3(c) considered by Smith & Barstad (2004). There, the limitation of the SB model becomes immediately visible.
But anyway, would you really say that the SB model was validated thoroughly? The original paper ended at a somehow realistic precipitation pattern, but to be honest, it was not much more than a stronger precipitation at the windward side compared to the leeward side. The subsequent study (Barstad & Smith 2005, J. Hydromet.) mainly revealed that a validation is difficult. Even in the later paper by Barstad & Schüller (2011, J. Atm. Sci.), the only real-world example was not very convincing at the leeward side. Right in the beginning, we did some comparison with TRMM data at the Himalayas, where our model was able to nicely reproduce the large-scale precipitation patterns. However, in nature there is more than one moisture source / wind direction, and precipitation is not only controlled by orography -- so the match was not perfect. Hence, we did not find the comparison very useful and then decided to focus on the comparison to the previous models and to show some potential applications where the properties of the model are relevant rather on a qualitative level.
About the technical comments:
(1) L39: This concept, i.e., in reality the flow discharge, instead of the drainage area, controls the erosion is not new. For example, it was stated in Paik (2012 ref below) as "While the above equation expresses the erosion rate as a function of the drainage area, it should be the flow that contributes to the bedrock erosion in reality. In the formulation of empirical equations, the drainage area has often been chosen as a surrogate of the flow discharge due to the difficulty of measuring flow discharge. However, there is no need to use the drainage area instead of flow in the numerical modeling."
It was not our intention to claim that the idea was new. At least the studies cited in line 38 of our manuscript used this concept. The models can, of course, easily be written in terms of discharge. However, many concepts in the field of landscape evolution and tectonic geomorphology (e.g., erodibility, steepness index) refer to catchment size. Therefore, the models usually involve an actual precipitation and a reference precipitation, while we prefer the concept of the catchment-size equivalent described at the end of the paragraph (Eq. 2). To be frank, we have no idea what to do with the comment.
(2) Some notations are not defined in the text, e.g., u_v/c in equation (3).
We thought that defining u_v and u_c and speaking of the "respective" property, it should be clear that u_v/c can be either u_v or u_c. Anyway, we can mention this explicitly if you find it helpful. And please let us know whether there are any other undefined notation.
(3) L140: I personally had also been tempted to use this approach. But I have had the following peer comment on this idea some time ago: ".. the temperature change with mean elevation change is not likely to represent a reasonable assumption. Yes, the atmosphere is cooler over mountains - but the air source for the precipitation is over an ocean and topography is not going to force the air to be cooler upwind of it." I still advocate this equation but you would need some supporting argument for its use.
What did your colleague tell you? The decrease of temperature with increasing altitude is the basis of all models in this context. Also of the SB model that you used in your study. If the air is blown uphill, it is of course cooled down already by adiabatic expansion. So we either missed the point or your colleague told strange things.
(4) L364-365: If this is correct, it can be a strong reason to develop an alternative model. But you should demonstrate it in comparison with real observation and Smith and Barstad (2004) model to convince it.
Of course, it is and this was exactly the reason developing this novel approach. Please see comment above.
(5) Section 7.1: The simulation domain here is only about a few hundred km. How can these simulations capture the 'continentality'?
We see continentality just in the sense that the moisture input from the ocean decreases with increasing distance from the ocean. This decrease is controlled by the parameter L_l in our model. Since we wanted to use basically the same mountain range geometry in Sections 7.1 and 7.2, we tested a "realistic" value of L_l where the effect is rather weak over the scale of the mountain range and an artificially low value of L_l where "continentality" is even visible at this scale.
Best regards,
Stefan and Jörg
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AC2: 'Reply on RC1', Stefan Hergarten, 12 Aug 2021
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RC2: 'Comment on gmd-2021-179', Sebastian G. Mutz, 13 Aug 2021
Assessment of the study’s contribution
The manuscript represents a potentially very important contribution to model-based approaches in the field of tectonics-landscape-climate interactions. A common problem in landscape evolution modelling is the efficient inclusion of realistic orographic precipitation, since General Circulation Models (GCMs) have weaknesses in representing such precipitation, and non-hydrostatic regional climate models (RCMs), which are able to represent orographic precipitation much better, are equally complex and also have high computational requirements. An efficient orographic precipitation model, that is able to respond quickly to orographic changes produced by landscape evolution models (LEMs) or prescribed topography therefore bridges this gap in modelling. The authors address an important and widely recognised gap by presenting an alternative to the previous, simple orographic precipitation models, such as Smith and Barstad’s model based on linear theory for orographic precipitation (LTOP). While the LTOP model has increased in complexity over time and represents a viable option for LEMs, the model presented here has some advantages over it, and model diversity in general increases the overall reliability and knowledge gain of the community’s modelling efforts. The presented study therefore is, in my eyes, a very valuable contribution to the LEM and Earth system science community in particular.
General Comments
The manuscript is well written and generally easy to follow, as is appropriate for a manuscript that is of potential interest to different geoscientific communities. The authors present the readers with backgrounds on SPIMs, the need for simple orographic precipitation models, and how the model presented here complements previous approaches. I believe this is appropriate given the contribution assessment above. The readers are talked through the governing equations and model in sufficient detail to develop a feeling for the model’s potential applications and limitations. The demonstrations (section 7) are particularly useful for the LEM community. The conclusions are helpful for readers to determine the suitability of the model for their purposes. I do, however, have a few (mostly minor) concerns about this study. I believe these can be addressed fairly easily:
1. Title: Since the focus of this study - judging by introduction, examples and references - currently lies on presenting an orographic precipitation model specifically for LEM/geomorphology community, I think it is better for the title to reflect that when it is published in a journal that also sees publications of climate models “for climatologists”. If the manuscript is intended to simply present an orographic precipitation model, the text would have to be adjusted to highlight how it fits into the realm of climatology/meteorology and its vast model landscape. Given that this type of model is likely most needed in the geomorphology/LEM community, I would simply adjust the title here rather than change focus of the manuscript.
2. The study’s focus (only a potential concern): If the study’s focus is the perceived one (described above), my only concern is the title. The model of course has potential applications beyond the geomorphological community. However, if the idea is to address a wider audience in this particular manuscript, I would expect much more discussion of its fit into the climate model landscape, as well as (performance and skill) comparisons to models that are well established in climatology for precipitation simulations in orogens (e.g. WRF), for example by application of the model presented here to a region already investigated with WRF and/or other models (ideally of varying complexity).
3. Model validation: The manuscript describes well the conceptual differences between this and comparable models (e.g. LTOP), and the model construction seems very reasonable. However, it is not clear what its prediction skill is compared to other models. There is no application of the presented model to a real setting, followed by a comparison to observational data or other comparable models. Esp. for scientists interested in applying the model outside a purely theoretical framework, this lack of validation is problematic and should be addressed.
4. The manuscript lacks discussion of the potential applications (and caveats) of the model outside the more theoretical realm/sensitivity experiments. The point above is one way to address this. Furthermore, I imagine that this model is of great interest to those investigating the co-evolution of orogens, climate and landscapes for real settings and times in the past. To do that, however, a number of additional steps need to be taken (see specific comment for L48-51). I think a discussion of this would increase this study’s usefulness and also avoid ill-informed use of the presented model.
5. Equations (minor point): Each term in the equations, starting in the introduction or at least from the very beginning of section 2.1, should be given units explicitly. Partially, this suggestion may stem from the way I think of and follow/read equations (I find it more difficult to think them through without units in front of me), but it would enhance reproducibility and help avoid confusion regardless. I strongly suggest clearly stating the units for each of the terms in the equations throughout the entire manuscript, even if they are just the SI units the terms are usually expressed in. I also recommend going through all again carefully to catch possible oversights during write-up (see specific comments).
6. Code documentation: This point is not directly related to the manuscript, but important for potential users nevertheless. As someone who is actually interested in applying this model, I downloaded the code for openLEM from the link provided here. My go-to language for modelling (and most other things) is Fortran, but I usually don’t have issues following C++ code if it is well commented and/or documented. However, it is difficult to locate the relevant code if I am interested in only the orographic precipitation model (decoupled from openLEM). Much of it seems to be in orogen.cpp, but much of the code lacks sufficient comments to navigate easily. I think a clean documentation, more comments and orographic precpitation model packaged as a separate model (decoupled from openLEM) will remove barriers for other scientists to use it. I appreciate the explicit offer of assistance in the “code and data availability” statement, but think a an independence of the authors' assistance through documentation benefits everyone, including the authors.
Technical/Specific Comments
Below, I suggest a few small corrections that came to mind during reading.
L4: GCM coupling not only increases the complexity, but GCMs also have notable weaknesses in representing precipitation, esp. in mountanous regions. That is arguably the bigger problem of using GCMs. In case of RCMs like WRF, “only” the increased complexity and high computational demands remain a problem. I suggest a small adjustment to this statement in the abstract.
L18: “[...] the the geometry […]”, omit one “the”
L29: Maybe change to “[...]all particles are immediately excavated once detached from bedrock.” for better readability.
L48-51: In addition, GCMs would not be suitable tools for predicting orographic precipitation [e.g. Meehl et al. 2007], esp. not at the catchment scale (see above comment). However, RCMs come with the same computational drawbacks the authors mention here. I suggest highlighting this point here. That said, once a study is upscaled for larger orogens in studies of how their evolution is linked to climate, landscape evolution and erosion, the changes in large scale surface uplift has significant impacts on regional and global climate [e.g. Takahashi and Battisti, 2007; Paeth et al., 2019], and thus on the boundary conditions (moisture availability, wind and therefore advection velocity , etc.) for RCMs or less complex orographic precipitation models like LTOP or the model presented here. This means that once larger changes are introduced to an orogen, there is no way around running GCMs, even if they then simply drive simpler orographic precipitation models rather than RCMs. The same is true once we leave the realm of sensitivity experiments and look at an orogen in the geologic past, when palaeoenvironmental boundary conditions create a very different global climate and thus change the input fields for any RCM or simple orographic precipitation models [e.g. Mutz and Ehlers, 2019]. The need for GCMs for such upscaled experiments ought to be highlighted somewhere – here or (probably more fittingly) in a “caveats/warning” paragraph in conclusions, or both.
L79: I would describe it more accurately as “the goal of this study”; the goal of the paper is to present the study/model.
L97: I suggest giving discharge a different symbol in the introduction to avoid potential confusion altogether. If the authors think it is merited to referenece q in context of discharge anyway, this may be done by adding a side note a la “[new symbol] is discharge, often denoted as q in other manuscripts, […]” in the introduction.
L135-144: Equation 15 does not follow 14 as it currently stands. However, the flaw seems to be in 14. If β/β0=e^-[a/(T0-ΓH)] / e^-[a/T0], then 14 should read as e^-[a/(T0-ΓH)-a/T0], i.e. the last term in the exponential should be subtracted if I’m not mistaken. 15 would then follow 14 again, so I think it’s simply a matter of getting a sign wrong during the write-up of the manuscript. For 16, it’s not clear from the text why the -T0ΓH term in the denominator is considered negligible.
L534 (Fig.9): The coloured dots next to uplift rates are somewhat difficult to make out. Furthermore, I suggest adjusting colours to take into consideration common forms of colour blindness. This is a general recommendation, but something I notice every time I see red next to green as here. If that has been considered when these particular shades were picked, please ignore my second comment.
L181 (Fig. 10): I suggest changing the colour scale to something other than the rainbow colours (e.g. a simple grey scale) (1) to make visualisation more accessible (consider colour blindness), and (2) because the rainbow scale has been demonstrated to be misleading due to the lack of clear perceptual ordering.
I hope my input here helps polish the manuscript somewhat and look forward to seeing a revised version.
Best wishes
Sebastian MutzReferences
Meehl, G. A., Covey, C., Delworth, T., Latif, M., McAvaney, B.,Mitchell, J. F. B., Stouffer, R. J., and Taylor, K. E. (2007). The WCRP CMIP3 multi-model dataset: A new era in climate change research, B. Am. Meterol. Soc., 88, 1383–1394
Mutz S.G. and Ehlers T.A., (2019). Detection and Explanation of Spatiotemporal Patterns in Late Cenozoic Palaeoclimate Change Relevant to Earth Surface Processes. Earth Surface Dynamics. doi.org/10.5194/esurf-7-663-2019
Paeth H., Steger C., Li J., Pollinger F., Mutz S.G., Ehlers, T.A., (2019). Comparison of Climate Change from Cenozoic surface uplift and glacial-interglacial episodes in the Himalaya-Tibet region: Insights from a regional climate model and proxy data. Global and Planetary
Change. doi.org/10.1016/j.gloplacha.2019.03.005
Smith, R.B. and Barstad, I. (2004) A linear theory of orographic precipitation. J. of the Atmospheric Sciences, 61:12, 1377-1391, doi.org/10.1175/1520-0469(2004)061<1377:ALTOOP>2.0.CO;2.
Takahashi, K. and Battisti, D.(2007). Processes controlling the mean tropical pacific precipitation pattern. Part I: The Andes and the eastern Pacific ITCZ, J. Climate, 20, 3434–3451
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AC3: 'Reply on RC2', Stefan Hergarten, 19 Aug 2021
Dear Sebastian Mutz,
thanks a lot for your encouraging comments!You are definitely right that we should clarify the focus of the model development already in the title. There is a huge gap between regional climate models and these oversimplified models such as the linear model originally proposed by Smith and Barstad. So our goal was indeed to develop a model that is a bit better than the simple linear model.
One thing that we will definitely include in a revised version is a more detailed comparison to the linear model. Such a comparison can even be done on a semi-quantitative level, so by analyzing which phenomena are captured "realistically" by which model. The discussion paper mentioned some aspects only theoretically, and it would be helpful for the readers to see some examples.
While we wrote the manuscript, we also did some comparison with TRMM data at the Himalayas, where our model was able to reproduce the large-scale precipitation patterns reasonably well. The match was, however, by far not perfect, and we arrived at a point where we could not tell whether the simple precipitation model or the assumption of a uniform flow field with a single source of moisture are more severe. We will point out more clearly that the is still a huge gap to regional climate models and will also look at our previous attempts to "validate" the model again.
Discussing the potential caveats, e.g., that large changes in topography may not only change the precipitation pattern, but also the circulation pattern, is also a good point. For the moment, there are still "enough" open questions that can be addressed on a rather generic level (with artificial topographies), but this will require further developments as soon as we proceed towards the evolution of real orogens.
Concerning the code, I already developed a commented standalone version (approx. 200 lines C++ code), which will be made available in a few days at the OpenLEM page and also in the code and data repository of the revised version.
Best wishes,
Stefan
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AC3: 'Reply on RC2', Stefan Hergarten, 19 Aug 2021
Peer review completion





