Arsenic Sulfide Suspended-core Fiber Simulation with Three Parabolic Air Holes for Supercontinuum Generation
Round 1
Reviewer 1 Report
The manuscript „Arsenic Sulfide Suspendedcore Fiber Simulation with Three Parabolic Air Holes for Supercontinuum Generation“ by Tao Peng et al. deals with fiber design considerations for supercontinuum generation with 1.5µm input wavelength.
This topic is interesting for publication in Photonics.
After the third time reviewing that manuscript, I believe the manuscript is almost in a stage to be published. However, several aspects must be improved.
1. Fitting the dispersion coefficients until the 10th order is still questionable. What happens if less orders are taken into account? The values in Table 3 should be given in meaningful units, e.g. fs/cm or fs/mm.
2. Fitting n_eff with a third order gaussian function is now better explained. However, it is not clear how fitting n_eff by a third order gaussian function, taking equation 4 and fitting to a tenth order polynomial can give a meaningful result. Why n_eff is not fitted by a tenth order polynomial since it is based on the Sellmeier formula (how many orders are used, add a reference). How is the fitting error of the gaussian function related to the accuracy of the coefficients in Table 3.
3. Equation 6 is not correctly formatted in the PDF.
Author Response
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Author Response File: 
Author Response.pdf
Reviewer 2 Report
Please find below my review of manuscript “Photonics-822090” entitled “Arsenic Sulfide Suspended-core Fiber Simulation with Three Parabolic Air Holes for Supercontinuum Generation”.
In the manuscript, T. Peng et al. have designed a nonlinear suspended-core optical fiber and have simulated their optical properties for different values of the core diameter (d) and of the parabolic holes curvature (a).
After having introduced the fiber geometry, in sections 3.1, 3.2 and 3.3 the Authors have numerically retrieved the effective refractive index, the nonlinear coefficient and the chromatic dispersion in order to optimize the balance between high nonlinear features (achievable by reducing d and a) on one side and, on the other hand, a dispersion relation as flat as possible. By so doing, the Authors have chosen the couple of values and in order to get an high nonlinear coefficient and a zero dispersion wavelength in the telecom range: .
With these parameters, in section 3.4, the Authors numerically solved the generalized nonlinear Schrödinger equation for different duration, peak power and wavelength of the pump pulse. The simulated spectral coverage of the supercontinuum source results to span the 0.6 to about 5.0 µm wavelength for 40 kW.
The topic this paper is about is of sure interest, and the several numerical results (that were contained also in the previous version of the manuscript) are now presented in a clear form. In particular, I have appreciated the fact that the figures are readable and properly commented in the main text, all the quantities are expressed in the appropriate units and I found really helpful the introduction of Fig. 6b and 7b, in which the impact of parameter d emerges clearly.
In my opinion, the manuscript in the present form can be recommended for publication, provided a few minor revisions are made.
COMMENT 1:
At line 239, the Authors states that Fig. 9 “the influence of a on the nonlinear coefficient is not significant, whereas its influence on the dispersion is evident”. In my opinion, the link between the electric field distribution plotted in Fig 9, the nonlinear coefficient and the dispersion is anything but evident. Could the Authors supply explain better in the text?
COMMENT 2:
I appreciated the fact that the dispersion coefficients reported in Tab 3 are now expressed in the proper units. Anyway, I still have doubts about the reliability of numbers as small as 10-68 - . I didn’t understand if these numbers come from a fit or have been numerically calculated. In any case, I think they are well below the numerical errors. Could the Authors provide some explanation in this sense? Are they sure the results of simulation based on the GNLSE would be different by considering (for instance) only 5 terms in the Taylor expansion?
Author Response
Please see the attachment.
Author Response File: Author Response.pdf
Reviewer 3 Report
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Comments for author File: Comments.pdf
Author Response
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Author Response File: Author Response.pdf
Round 2
Reviewer 1 Report
The authors modified the manuscript according my suggestions. In my opinion the manuscript is ready to be published.
Reviewer 3 Report
Please see the attached file.
Comments for author File: Comments.pdf
This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.
Round 1
Reviewer 1 Report
The manuscript “ Arsenic Sulfide Suspendedcore Fiber Simulation with Three Parabolic Air Holes for Supercontinuum Generation” by Tao Peng et al. deals with the design and simulation of a fiber for SCG. This topic is interesting for publication in Photonics.
Compared to their previous version the manuscript improved a lot following the reviewers’ suggestions. However, the manuscript still needs improvements before it can be recommended for publication.
1. The main finding of the manuscript is supercontinuum generation with a fiber with has an inner diameter of 1 µm between the air holes. However, a lot of other data are presented for other diameters. Similar data are already shown in Ref. 26 by the authors. The amount of presented data in the manuscript should be drastically reduced. E.g. in Fig. 6 the dependency on parameter a is weak. The authors should show only one plot with different diameters (and information about a). Same for Fig. 7. Fig. 8 and 9 are repetitive. The ZDP are also visible in Fig. 8. Fig. 8 should be reduced to two plots, one for d dependence (and information about the chosen a) and one plot for d=1 µm and different a. Fig. 9 should be removed.
2. Since the fiber with 1µm inner diameter is the most important one. It is not clear, why calculations are shown for different diameters. Fig. 3 and 9 should be presented for 1 µm.
3. Do the authors have permission on showing the pictures in Fig. 1 by the journals?
4. Fig. 11 is too large and gives no further information. It is the power dependence of SPM. In Fig. 12 the label “Intensity (db)” is missing. Numbers and labels in that figure are too tiny.
5. In Fig. 12, 13, 14 and 15 the dB-range is too large. The authors should restrict to a range not smaller than -40 dB or -50 dB in the plots.
6. Since the simulated fiber has only a length of 1 cm, I wonder why the loss is so high and if this is normal for this type of fiber. The authors should comment on the fiber losses (also depending on d and a). E.g. what this means for limitations for the SC average power. What thermal problems of the fiber are caused going to low values of a. Maybe there is a reference for this or peak and average powers of the experiments in Table 1 can be added.
Reviewer 2 Report
The authors did not address my comments satisfactorily, and my recommendation to the editor is to reject its publication. Please see my detailed comments below.
Line 118 – "The shape of parabolic air-hole can be generated by means of extrusion instead of stacking."
Are there any prior work on this? In the response letter, the authors claim that the arsenic sulfide SCF can be completely prepared by extrusion method, but they do not cite any relevant work. As I just did a quick search myself, all prior art on extrusion-based fabrication uses the extrusion for making the “preform”. The preform needs to be further drawn down (often multiple times) to finally arrive at the fiber. In such a case, the parabolic curvature is not likely to be maintained in the final structure.
Moreover, the authors argue in the letter that the deformation of the air holes during the drawing has a negligible effect on the guided mode, as long as the size of the core remain unchanged. If this is the case, then what is special about these parabolic holes, and why are they bothered to investigate the guiding properties as a function of the curvatures at all? They are selling the parabolic holes as the novelty in this work, and included that in the article title. However, the authors, on the other hand, are now admitting that the parabolic holes and the curvature have no effect on the guidance, and only the size of the core matters. The novelty of the work is now obsolete.
Lines 160–176
If I understood this part correctly, the authors are faced with issues when taking numerical differentiation of the effective index with respect to the wavelength to obtain the dispersion parameter. Numerical differentiation is a classical ill-posed problem, and the numerical noise will be largely amplified, especially when taking the higher-order derivatives. By fitting the data into a mathematical function, one can generate a smooth dispersion parameter as a function of the wavelength.
However, I do not understand the logic behind choosing the Gaussian fitting. The authors argue that this is because Gaussian laser beam is widely used as the pump, but here, the pump beam profile has nothing to do with the dispersion of the effective index. I looked up Ref. [30] in an effort to understand this, but I did not see any relevant fitting of the data there. I actually cannot clearly see what the authors have done here, and Eq. (1) appears broken in the PDF, which also did not help. This is a very incorrect approach.
I would also like to point out that for the nonlinear pulse propagation simulation involving the generalized nonlinear Schrödinger equation, it is not necessary to undergo this fitting. I agree that the smoothing will allow the one to obtain β coefficients of up to very high order as the authors have done in Table 3, and then fed into Eq. (5). However, since the authors went through the troubles of calculating the effective index over a wide spectral range using the finite-element method, it would be much better to take the full effective index curve directly in the frequency domain. After all, β coefficients are the Taylor series expansion coefficients of the full beta curve.
Line 192 – "Fig. 7 shows that the nonlinear coefficient of the SCF has a significant inverse proportional relationship with the wavelength."
I would like to point out again, that this really is bad science. Anyone with basic mathematics can expect that the nonlinear coefficient will be inversely proportional to the wavelength, without even plotting Fig. 7, unless the dispersion of the effective mode area is very large. Therefore, the important information that should be presented here is the mode area versus the wavelength.
For the benefit of the authors who did not seem to understand my comment in the last report, let us take a look at Eq. (2). This is the equation for the nonlinear coefficient γ, which depends on nonlinear refractive index n2, effective mode area Aeff and wavelength λ. Here, n2 does not vary with wavelength and is 2.92 × 10−19 m2 W−1. Then, it now becomes obvious that, unless the mode area changes significantly, the nonlinear coefficient will have a simple inverse relationship with the wavelength. The only quantity that can influence this inverse relationship is the effective mode area, and hence my reason for suggesting the authors to present the mode area versus the wavelength plot.
Eq. (5) – The stimulated Raman scattering term
It is now widely accepted that this first-order approximation to the Raman response function does not accurately represent the intra-pulse Raman effect in the supercontinuum generation. It is recommended to use the full Raman response function and take the convolution integral.
In any cases, the author should present in the manuscript the Raman parameter tR that they used in their simulations for the arsenic sulfide glass.
Line 304 – "Moreover, Raman solitons and the dispersive waves emitted by them generate new frequency components through the cross-phase modulation (XPM) and FWM effect, which further broadens the SC."
This statement is written without any support. The authors need to show that XPM and FWM are taking place between these entities by showing the phase matching.
Below are minor comments.
Line 41
It should be written, "The nonlinear application of silica-based SCF in the mid-infrared …".
Line 45
The authors say that arsenic sulphide glass is an ideal candidate for the fabrication of SCF as it has a more sophisticated preparation process. Why would that be an advantage? Is it not better to have a simpler preparation process?
Line 46 – "A SC source with a wavelength range from 0.6 µm to 4.1 µm was input into a 2-cm long three-hole As2S3 chalcogenide SCF [15]."
Why would they “input” the supercontinuum into the chalcogenide fiber? The cited work “generates” the supercontinuum in this fiber.
Line 59
What is a “non-independent SCF”?
Line 62
What is an “independent SCF”?
Line 291
P is not defined.
Figure 12
100 dB dynamic range is too large, unless there are important low energy details that need to be shown. Also, I suggest the authors to indicate the zero dispersion wavelengths in these plots.
Line 303 – "abnormal dispersion region"
This should be anomalous dispersion regime.
Line 310 – “dispersion wave"
This should be dispersive wave.
Line 310 – "When the wavelength of the soliton exceeds the second ZDW, the energy gap between each soliton increases, and the dispersive wave cannot make up for the gap between them, which makes the soliton independent."
I did not understand what the authors are trying to explain.
Line 316 – "energy gap"
What is this “energy gap” the authors are talking about? I did not understand.
Line 316 – "dispersion wave"
This should be dispersive wave.
Section 3.4
The authors should present what are the soliton numbers in each simulation.
Reviewer 3 Report
Please find below my review of manuscript “Photonics-798751” entitled “Arsenic Sulfide Suspended-core Fiber Simulation with Three Parabolic Air Holes for Supercontinuum Generation”.
In the manuscript, T. Peng et al. have designed a nonlinear suspended-core optical fiber and have simulated their optical properties for different values of the core diameter (d) and of the parabolic holes curvature (a).
In sections 3.1, 3.2 and 3.3 the Authors have numerically retrieved the effective refractive index, the nonlinear coefficient and the chromatic dispersion in order to optimize the balance between high nonlinear features (achievable by reducing d and a) on one side and, on the other hand, a dispersion relation as flat as possible. By so doing, the Authors have chosen the couple of values and (I suppose a to be expressed in , but it could be declared in the text) in order to get an high nonlinear coefficient and a zero dispersion wavelength in the telecom range: .
With these parameters, in section 3.4, the Authors numerically solved the generalized nonlinear Schrödinger equation for different duration, peak power and wavelength of the pump pulse. The simulated spectral coverage of the supercontinuum source results to span the 1 to about 5.5 µm wavelength for 40 kW.
The topic this paper is about is of sure interest and the Authors provided a remarkable amount of numerical results.
Unfortunately, in my opinion, the way in which these results are presented does not match the quality standard of this journal. For this reason, I’m not comfortable recommending this paper for publication unless it is substantially re-written.
In particular, figures are often unclear and the captions do not help the reader. The physical meaning of red harrows in figs 3, 4, 5 and 9 is not written. Notation in fig 12 are too small to be readable. The same holds for the red harrows in fig 3, while the arrows in fig 9 are too big to fit the figure itself. The Authors should also explain which numerical method they use to obtain the intensity plot of figs 3, 4, 5 and 9 and how they have taken into account of the defects shown in fig 4. As the suspension arms defects of fig 5.
In my opinion the general exposition is really non homogeneous, the several figures are not accompanied by proper comments in the main text, and the available comments are often distributed disorderly. For instance, the sentence at line 145 “There are only two solutions for the FM, as shown in Fig. 3. The electric fields of the two solutions are perpendicular to each other, and the corresponding refractive index…” should have been placed just after fig 3 has been presented (2 pages earlier).
With regard to the methodology, I have no objection about the numerical simulations. On the contrary, I have some doubt about the fitting procedure presented at the end of page 6 of the manuscript. In my opinion the Authors should have declared the physical meaning of the nine fit parameters, reported the retrieved value, and explained with which criteria they varied c3.
Similarly, the Authors should have explained how they retrieved the ten coefficient of table 3 and in which unit they are expressed. Especially, the Authors should explain the reason why a numerical result as small as 10-136 should be considered reliable.
In conclusion, while respecting the big scientific efforts of the Authors and although not doubting about the goodness of the main results, I cannot recommend to accept the manuscript in the present form.
Comments for author File: Comments.pdf
