Tsunami run-up estimation based on a hybrid numerical flume and a parameterization of real topobathymetric profiles

Aniel-Quiroga, Íñigo; Quetzalcóatl, Omar; González, Mauricio; Guillou, Louise

doi:https://doi.org/10.5194/nhess-18-1469-2018

Articles | Volume 18, issue 5

https://doi.org/10.5194/nhess-18-1469-2018

© Author(s) 2018. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/nhess-18-1469-2018

© Author(s) 2018. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 18, issue 5

Research article

|

29 May 2018

Research article |

| 29 May 2018

Tsunami run-up estimation based on a hybrid numerical flume and a parameterization of real topobathymetric profiles

Íñigo Aniel-Quiroga, Omar Quetzalcóatl, Mauricio González, and Louise Guillou

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Final revised paper (published on 29 May 2018)
Preprint (discussion started on 20 Dec 2017)

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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RC1: 'Review MS No.: nhess-2017-445', Anonymous Referee #1, 01 Jan 2018
- AC1: 'Authors reply to Reviewer 1 comments', Íñigo Aniel-Quiroga, 13 Feb 2018
RC2: 'Comments for: Tsunami run-up estimation based on a hybrid numerical flume and a parameterization of real topobathymetric profiles', Anonymous Referee #2, 29 Jan 2018
- AC2: 'Authors reply to Reviewer 2 comments', Íñigo Aniel-Quiroga, 13 Feb 2018

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

ED: Reconsider after major revisions (further review by editor and referees) (27 Feb 2018) by Ira Didenkulova

AR by Íñigo Aniel-Quiroga on behalf of the Authors (27 Feb 2018) Author's response Manuscript

ED: Referee Nomination & Report Request started (28 Feb 2018) by Ira Didenkulova

RR by Anonymous Referee #1 (05 Mar 2018)

RR by Anonymous Referee #2 (12 Mar 2018)

Suggestions for revision or reasons for rejection

General comments:

In the author reply, many of the details I requested are given, but a lot of them are not included in the revised manuscript, thus leaving a potential reader with the same questions. The coupling between the two models and the setup of the IH2VOF should be dealt with in more detail in the revised manuscript.

I still see some challenges in the coupling the two models. This, however, can be overcome by stating some of the possible limitations. Please see the detailed comments below.

Detailed comments:

1) I asked for typical grid sizes in the RANS model. This is given in the reply and I feel this information should be present in the paper.
a. Further the authors state that the model do not allow more than 5499 cells in X. Why is that? Is that a choice of the authors?
b. It is stated that the aspect ratio between x and z was 5. I completely understand the need for such a large aspect ratio, to limit computational time. However, large aspect ratio has, as shown by Jacobsen et al (2012), an impact on the position of the breaking point. Despite this, I still think that IH2VOF handle more accurately the physics of the tsunamis in this region than COMCOT, and thus it is justified. A comment should however be made that such large aspect ratios, might lead to slightly premature breaking.
c. An equation is given for determining delta z. Where does this come from? The effect of it can clearly be seen, and to me it seem a reasonable way of automizing the process. Again, I feel that this information should be present in the revised manuscript.

2) I asked for boundary conditions for IH2VOF model, and the authors replied that a log wall distribution was used. This seem reasonable, but, if the mesh is not graded near the bed, the y+ values must be extremely large potentially putting the value of the first grid point outside the log layer. Please discuss the possible impact of this. Further, please also provide the wall functions for k and epsilon. Finally, another reference than Lara et al. (2006) should probably be used here, as the turbulence model is not described in this paper.

3) I asked how the x_cut positions was determined. The authors has given a clear and satisfying answer, but not included this explanation in the revised manuscript. Please do so. Further in the response the authors called the model a LSWE model. I thought it was a NLSW model. If it is a NLSW do not alter anything, but if it is a LSWE model, please justify why this sufficient for the simulations since tsunami close to the shore can definitely be nonlinear.

4) I asked about the position of x_cut in relation to capturing the physics of the tsunami. A figure is added in the reply, but this figure the lines cannot clearly be distinguished and thus is hard to read. Further, I do not feel that this figure answers the question posed. One of the physical features a NLSW model cannot handle, but a VOF model can, is the undular bores. These might show further offshore than x_cut. I understand the practical limitation, but feel that a comment stating that there might be situations where the NLSW model is not properly handling the physics, before the VOF models takes over, is warranted.

5) I asked about reflection between the two models. I appreciate what the authors are trying to do, and can see that using the unaltered wave will limit reflection between the models. However, I think that this approach will give difficulties in certain cases. It the beach is steep, the tsunami wave will be reflected entirely, as the steep beach acts more or less likke a vertical wall. In this case a standing wave will be present similar to that shown in Madsen and Fuhrman (2009) figure 9a. By using the unaltered waveform this behavior cannot be captured. This should be reflected upon in the revised manuscript.

6) I asked for more details regarding the calculations for figure 4. These have been provided, but some things are still unclear. Now it is stated that L_i=50/tan(beta_0). How can this be true? In page 10 lines 17-19 it is stated that horizontal length of the domain comes from a separate simulation using COMCOT only.

7) I asked for a validation of the Hybrid model. I fully appreciate that both models have been used with great success in the past, and I did not question the validity of the models. In Lara et al. (2006) however smaller aspect ratios were used compared to here. The additional figure indeed provides validation for that IH2VOF can handle run-up. It is however important that the mesh for these simulations were performed using the same rules as in the present paper. I.e. delta z= (K H)/10 *0.05) *0.05, and r=5/1. Is this the case? If not, I would argue that the validation is made on a much finer mesh than the simulations in present paper. In this case, I do not feel that the model is validated satisfactory, and new validation simulations should be made.
The accompanying text to the figure is also unclear. In page 13 line 4 it is stated that the validation and coupling of the numerical models was made by comparing to experimental results. In the legend in the figure however, it is only the IH2VOF model, and thus no coupling between the models are present. Which of these are correct?

8) The authors have compared now both to Synolakis as well as Madsen and Schaëffer. I am however curious how the results from Synolakis as well as Madsen and Schäeffer were obtained, as these were created for only a single sloped region. Was an average slope calculated? Or only beta_1 or beta_0 used? Please describe how it was done, and why this is the best approach.

9) I asked about the determining of period and wave height. In the reply the authors state that no serious differences between trough led or crest led were experienced. What about difference between a single wave, and a leading depression n-wave for instance. With the N-wave height is the summation of the positive negative amplitude, whereas the wave height of the single wave is just the positive amplitude. I can see how a single wave with a similar positive amplitude as a leading depression N-wave, will run-up similar but I would imagine a single and an N-wave with the same wave height will run-up differently. Perhaps it would be better to called maximum positive amplitude in the revised manuscript rather than wave height.

References:
Jacobsen, N. G., Fuhrman, D. R. & Fredsøe, J. 2012 A wave generation toolbox for the open-source CFD library: OpenFoam (R). Int. J. Numer. Meth. Fluids 70, 1073–1088.

Madsen, P. A., Fuhrman, D. R., 2008. Run-up of tsunamis and long waves in terms of surf-similarity. Coast. Eng. 55, 209-223.

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ED: Reconsider after major revisions (further review by editor and referees) (12 Mar 2018) by Ira Didenkulova

AR by Íñigo Aniel-Quiroga on behalf of the Authors (21 Mar 2018) Author's response Manuscript

ED: Referee Nomination & Report Request started (22 Mar 2018) by Ira Didenkulova

RR by Anonymous Referee #2 (30 Apr 2018)

Suggestions for revision or reasons for rejection

General comments:

I am happy to see that many of the previous replies have now been included in the manuscript. It has improved the manuscript as a whole. The implemented changes are not as well written as the remainder of the manuscript. Please re-write these. Furthermore, only some of you equations are numbered. Please make sure to correctly number all the equations. Beside this, I only have a few minor comments.

1) Page 11 line 10 please rephrase the sentence. E.g. “… Jacobsen et al., 2012) it limits the computational times relative to those achieved with smaller aspect ratios”
2) Page 11 line 11: please add “the” in front of RANS
3) Page 11 line 11: please replace what with which
4) Page 11 line 15: Please provide units for ∆z.
5) Page 11 line 28-30: My earlier comment in relation to the NLSW models are not that they are bad at handing non-linearities, but rather that they cannot describe physical dispersion, which become important in the formation of undular bores. I would not necessarily say that the IH2VOF domain is optimized in order to minimize this limitation. How well the setup handles this situation will probably depend on the local steepness of the tsunami when the IH2VOF domain take over. Please slightly rephrase the sentence to take the above into account.
6) Regarding the wall functions for the turbulence model, I am happy to see it now in the manuscript. As you write in the reply, these kind of wall functions should be used for cells inside the logarithmic layer. Since you have not described any vertical near wall grading, I must assume that the first cell has the same height as the remainder of the domain. That can lead to very high y+ values potentially far outside the logarithmic layer. Please reflect upon this.
7) Page 4, line 27. Please define E
8) Why was a smooth wall function used? I would imagine that the most situations would be hydraulically rough.

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ED: Publish subject to minor revisions (review by editor) (30 Apr 2018) by Ira Didenkulova

AR by Íñigo Aniel-Quiroga on behalf of the Authors (02 May 2018) Author's response Manuscript

ED: Publish as is (03 May 2018) by Ira Didenkulova

Short summary

Recent tsunami events have exposed the need for further work to develop and apply tsunami risk reduction measures. A key parameter that must be adequately determined is the run-up, the maximum elevation to which water from a tsunami wave will rise during its flooding process. In this work, a new methodology to simply calculate the run-up is presented. The methodology has been applied to calculate a tsunami run-up database, where the run-up of new events can be calculated by interpolation.