Developments of Dynamic Shoreline Planform of Crenulate-Shaped Bay by a Novel Evolution Formulation
Round 1
Reviewer 1 Report
The study proposes a simplified method to evaluate the effect of a type of coastal defense in the case of pocket beaches or crenulated shores. The method is similar to the one proposed in ref.20; the Authors use formulas and figures present in ref.20 and in other antecedent papers.
The reviewer is here considering general issues only.
1. Is the transformation by refraction and diffraction of the wave in the bay computed with a commercial calculation code (MIKE 21 FM, GENESIS, …)?. The matter is only hinted at, while it shall be further clarified.
Moreover, the paper should explain the connection between the 2D hydrodynamic model and the 1D beach dynamics model.
2. The paper focuses on the discretization of the mathematical model that uses a mesh in polar coordinates.
The structure of the mathematical model is simple, with only the differential equation of the solid flow balance. The long exposure of the calculation grid drawn in polar coordinates is excessive: see ref. 20. The passage from the mathematical model to the numerical model would clarify the approximations made by the authors.
The origin of the solid transport formulas must be briefly explained by recalling for example [Hanson H. & Kraus N.C., GENESIS, Technical Report CERC-89-19, USACE, 1989].
Equation (5) does not include flows perpendicular to shoreline “q” as shown for example in [Hanson H., Journal of Coastal Research, 5 (1), 1989]. In case 3, the Authors introduce "q" to correct the balance of sediment transport without any physical explanation.
The flow vectors of the longshore current flows parallel to the beach, while the faces of the cells in polar coordinates are not perpendicular to the beach so that “Q” flows through the cell faces that (in polar coordinates) are not perpendicular to the shoreline, see figure 1: is correction is needed to consider and correct this discrepancy? The cells have the form of a ring sector: the DA is not correctly written in (4). Enter the formula (4) of ref. 20.
3. The application of fig. 5 should be better explained: is the bottom of the bay initially horizontal? How are the discontinuities of the geometry in the edges are smoothed to make the computation realistic? The illustration of the shoreline shift over time would be interesting.
The reviewer suggests that the authors improve the presentation of their study before submitting the final version of the paper.
Author Response
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Reviewer 2 Report
Outline
The manuscript deals with the numerical modeling of the long-term morphodynamic evolution of crenulate bays. A curvilinear one-line model is proposed and applied to a series of ideal configurations. The model is demonstrated to be capable to reproduce observed evolution at both experimental and field scales.
The topic is interesting, and the manuscript is well structured. Nevertheless, some aspects of the model and its application should be discussed in more detail. I raise a series of concerns that I ask the authors to address before suggesting my final recommendation.
Major concerns
#1 – My first major concern is related to the novelty of the manuscript. It seems that the novelty of the proposed model is to approximate area \Delta A (Figure 2) as a rectangle. The approximation improves the numerical efficiency of the proposed model. Nevertheless, the authors should discuss the applicability of the approximation. I guess there is a kind of constraint to the maximum allowable spatial discretization (i.e., on \Delta \theta) or to temporal discretization (i.e., on the difference of r between two time steps).
#2 – My second concern is related to the proposed scheme.
The one-line model, in general, allows the displacement of the shoreline along the direction normal to the (local) shoreline. As per the scheme of Figure 2, it seems that the shoreline is allowed to move in the direction r that depends on the selection of the origin of the (polar) reference scheme. Indeed, depending on the extension of the computational domain, the direction r (i.e. constant \theta) may be very different from the normal direction (this is why, in my opinion, previous studies did not use a unique polar reference frame for the whole domain). In my opinion, the selection of the origin of the reference frame should be investigated in the manuscript, also for different extensions of the computational domain (i.e. larger than the extension considered in section 3). This aspect should be clarified.
Figure 2 shows two arrows with the same orientation to indicate the longshore sediment transport. It is not clear, at least to me, if the direction of the longshore sediment transport is the same at the two boundaries of each control volume. I guess that the direction is normal to the central section of the control volume. This aspect should be clarified in the manuscript.
Figure 2 shows the control volume. It seems that the origin of the reference frame is located at the water depth equal to Ds (the depth of closure). Hence it seems that the scheme is not valid if the origin of the (polar) reference frame is located elsewhere. This aspect should be clarified.
#3 – To demonstrate the reliability of the proposed model, the authors performed a series of numerical simulations. Nevertheless, I did not find any details about the method used to estimate the wave parameters needed to estimate the longshore sediment transport. How are the offshore waves propagated up to the breaking point? This aspect should be clarified.
#4 – To perform the parametric analysis, the authors selected a piece-wise linear initial condition (see Figure 5). How the singular points (i.e. corners) were treated for the numerical tests? This aspect should be discussed.
#5 – Table 1, first row. I do not catch the physical meaning of the results. For waves coming from 0°, I expect that a1=a5 and a2=a4. Why are the results asymmetric? I guess this result is related to my concern #2 (the results are influenced by the selection of the origin of the reference frame). This aspect should be clarified.
#6 – To perform the simulation of case 3 (section 4.3) the authors used a wave height equal to 0.66 m. It is not clear how this value was estimated. A lot of methods are available to estimate the wave parameters for morphodynamic studies. If the average significant wave height has been estimated, it should be discussed if this value has the same effect on the long-term evolution of the shoreline.
Minor concerns
#7 – Thorough the manuscript the authors use the terms “erosion” and “deposition”. As the one-line model relies on the conservation of the sediment mass, “shoreline advance” and “shoreline retreats” should be used instead.
#8 – Line 46. The authors talk about “wave attack” when discussing the role of groins. In my opinion, the influence of groins is related to the trapping of longshore sediment transport instead of a direct influence on wave propagation. This aspect should be clarified.
#9 – Line 77. The authors refer to the “parabolic model”. I suggest using “parabolic macro-model” or “parabolic empirical model” in order to avoid confusion about models based on the resolution of parabolic partial differential equations.
#10 – Line 149. The authors say that “For simplicity, we only adopted the longshore sediment transport and ignore the cross-shore sediment transport in the present study”. Actually, this is the main assumption of one-line model, hence this is not “for simplicity”. I suggest adding a brief discussion of the assumption of one-line models.
#11 – Line 180. “increased” should be “updated”. The shoreline location can either advance or retreat.
#12 – The unit of measure is missing through the manuscript (i.e. lines 269, caption of Figure 5, caption of Figure 7, Line 347, Line 409)
Author Response
The reply content is in the attachment, thank you for your suggestion.
Author Response File: Author Response.docx
Round 2
Reviewer 1 Report
The reviewer suggests the following more refined presentation of equation (7) should consider that:
1) The rectified shape basis of the control volume is trapezoidal not rectangular, so:
DA = ½ Dq (rn+12 - rn2)
2) The shape of the control volume is not prismatic, so:
DV = DA KS DS where the (constant) KS is a shape coefficient with KS>1
Equation (7) becomes:
rn+1 = r n [ 1 + 2 DQ Dt/ (rn2 D q KS DS)]1/2 (.)
The expression given in the paper is the binomial series expansion of the above one truncated at the second term.
Line 256 replace “demonstrated” with “shown” or similar word
Line 321 … 323 erase the sentence
The reviewer suggests the following more refined presentation of equation (7) should consider that:
1) The rectified shape basis of the control volume is trapezoidal not rectangular, so:
DA = ½ Dq (rn+12 - rn2)
2) The shape of the control volume is not prismatic, so:
DV = DA KS DS where the (constant) KS is a shape coefficient with KS>1
Equation (7) becomes:
rn+1 = r n [ 1 + 2 DQ Dt/ (rn2 D q KS DS)]1/2 (.)
The expression given in the paper is the binomial series expansion of the above one truncated at the second term.
Line 256 replace “demonstrated” with “shown” or similar word
Line 321 … 323 erase the sentence
Figures 10, …, 13 show that the sharp corners are slightly smoothed: say something about it.
Author Response
Thanks for the comments and guidance on the content of the article.
Author Response File: Author Response.docx
Reviewer 2 Report
This is the second round of the review process. The manuscript deals with the numerical
modeling of the long-term morphodynamics evolution of crenulate bays.
The authors addressed most of my previous concerns. Nevertheless, I suggest adding some
clarifications in the revised version of the manuscript. I am referring to my previous concerns
#2 and #5 in particular.
I raised a concern related to the role of the selection of the (polar) reference scheme. The
authors basically agree with my comment: “Although the difference between the r direction and
the normal direction of shoreline segments may introduce approximation errors, the numerical
results and comparisons in this submission are acceptable. […] All of the numerical results are
satisfactory and no expected error along down coast is found.”
In my opinion, the doubts raised on the values of Table 2 are related to the selection of the
origin of the reference frame too. Also in this case, the authors seem to agree with me: “We also
noticed that the imbalance, which is point out by the reviewer. There are two possible causes of
these imbalance. One is the reason stated in major concern #2. The other possibility is the
numerical error for calculating the area.”
From a practical point of view, I can agree with the authors. Nevertheless, I guess that the
following points should be added to the manuscript.
1 – A discussion on the approximation of the direction of the shoreline advance and retreat.
2 – A parametric analysis of the role of the selection of the origin of the reference frame location.
Further simulations should be performed (similar to those presented in Figure 6). Simulations
should be performed by moving the reference frame origin at the center of the domain and at
the tip of the structure placed at the right of the domain. Furthermore, a set of simulations
should be performed by increasing the domain (horizontal) length for the three origins of the
reference frame (i.e., located at the tip of the structure placed at the left side of the domain, at
the center of the domain and at the tip of the structure placed at the right side of the domain). I
would expect that the error increases as the domain length increases too.
3 – Update Table 2 with the results of the simulations of the previous point 2.
Author Response
Thank you
Author Response File: Author Response.docx
