A New Research Scheme for Full-Scale/Model Test Comparison of Wind Effects on Pengcheng Cooling Tower Based on Sinusoidal Flow Field Simulations

Round 1

Reviewer 1 Report

1.       Line Number 36 and 37 – concerns about the reliability of the ABL wind tunnel, following which the subsequent details are presented in 2^nd para, please merge them as it is a continuous information.

2.       Line No:38-50 can be best represented as a table for the convenience of the readers rather than text.

3.       Line No:77, a little more detail about the non-stationary features will be really appreciated.

4.       The idea of an unified scientific scheme is appreciable – Good identification of the research problem. Similarly, it is appreciable to understand and evaluate the details of TJ-6 in later paragraphs.

5.        Line No:168- does not make sense – Please read and modify appropriately.

6.       The equation representing the sinusoidal function can be written as an equation rather than merging with the text.

7.       Sinusoidal and Senior sinusoidal functions can be elaborated in detail for the better understanding of the readers. I appreciate the pictorial representation and analysis of each of them.

8.       Fluent results are not trustable, as it lacks the detailed data of the contours in Fig.7

9.       Fig.7 is not mentioned in the manuscript. Figure number and caption is missing.

10.   Turbulence conditions for the simulations are not mentioned for the fluent simulation.

11.   Fi.8 can be elaborated for more detailed information.

12.   Section 3.3. can be discussed with more facts and details. A mere overview is provided here, which is much like a superficial treatment rather than the extensive analysis.

13.   Justify – Line No:349-350 – “Finally, the turbulent flow characteristics effects are negligible around 349 the half circle”

14.   Please Explain in detail – Line No:370-371 – “The wind field is assumed to be a compressible flow field and the k–ε standard 370 viscous model is utilized.” – Explain about the compressibility

15.   The accuracy and the operation of the novel proposed approach is not suitably proved and it still has a long way.

16.   Its contrary to agree with the following lines : Line No:431-432 –“ However, we found that turbulent flow characteristics effects are negligible and 431 do not significantly impact wind loads on the structure”

  Author Response

Reviewer 1

1. Line Number 36 and 37 – concerns about the reliability of the ABL wind tunnel, following which the subsequent details are presented in 2nd para, please merge them as it is a continuous information.

Response: Thank you for the good comment. As suggested, the two paragraphs have been merged into one for continuity.

2. Line No:38-50 can be best represented as a table for the convenience of the readers rather than text.

Response: Thank you for the suggestion. We have added Table 1 for details of the full-scale/model test comparisons performed in history for readers’ convenient references.

3. Line No:77, a little more detail about the non-stationary features will be really appreciated.

Response: Thank you. A definition of authority for a non-stationary sample refers to a sequence that contains the trend, the seasonality, and/or the periodicity in terms of mathematics [28], which is extremely common in the field of wind engineering. This explanation has been added in the right place (see the part highlighted in blue).

4. The idea of an unified scientific scheme is appreciable – Good identification of the research problem. Similarly, it is appreciable to understand and evaluate the details of TJ-6 in later paragraphs.

Response: Thank you so much. As suggested, we have tried our best to explicate the proposed research scheme and its physical test requirements for TJ-6 to benefit the readers.

5. Line No:168- does not make sense – Please read and modify appropriately.

Response: Thank you for the comment. Yes, the sentence is indeed kind of ambiguous. We have rephrased it as follows: ‘After the numerical simulation, it is found that the simulated velocity samples near the inlet are close to the input velocity time-history (the simulation target); however, when the simulated sample is extracted from a location far away from the inlet, it deviates from the simulation target in both frequency and time domains’. We hope the present expression can help the readers better understand the meaning.

6. The equation representing the sinusoidal function can be written as an equation rather than merging with the text.

Response: Thank you. As suggested, we have written the equation as Eqn. (3), rather than merging it with the text in the revised manuscript.

7. Sinusoidal and Senior sinusoidal functions can be elaborated in detail for the better understanding of the readers. I appreciate the pictorial representation and analysis of each of them.

Response: Basic sinusoidal functions are those that can be mathematically expressed as ; while senior sinusoidal functions are those obtained via the linear superposition of several basic sinusoidal functions, e.g., the function  (see Fig, 11 for a pictorial representation). These are explained in the revised manuscript (see the part highlighted in red).

8. Fluent results are not trustable, as it lacks the detailed data of the contours in Fig.7

Response: Thank you for the comment. Actually, the quantitative data can be extracted from the Fluent CFD platform after the calculation (see, e.g., Fig. 8). Due to the limited article length, we cannot list all data obtained from the numerical analysis in the manuscript. Fig. 7a lacks detailed data because the velocity field is less discernable at the beginning the calculation, and at late stages of the duration, detailed data can be shown in the contour chart (Fig. 7b). As it now stands, we have deleted Fig. 7a. Thank you for your good comment.

9. Fig.7 is not mentioned in the manuscript. Figure number and caption is missing.

Response: Thank you for indicating our error. We have added the number and the caption for Fig. 7.

10. Turbulence conditions for the simulations are not mentioned for the fluent simulation.

Response: It is assumed that the upcoming flow is laminar with negligible turbulence intensity for the numerical simulation. This is explained in the revised manuscript (see the part highlight in green).

11. Fi.8 can be elaborated for more detailed information.

Response: Thank you. As suggested, more detailed information is added for Fig. 8 (see the part highlighted in purple).

12. Section 3.3. can be discussed with more facts and details. A mere overview is provided here, which is much like a superficial treatment rather than the extensive analysis.

Response: As suggested, more details of physical modal tests conducted in TJ-3 wind tunnel have been added for more in-depth analyses (see the parts highlighted in orange).

13. Justify – Line No:349-350 – “Finally, the turbulent flow characteristics effects are negligible around 349 the half circle”

Response: The conclusion is based on the observation that all differences of the mean wind pressure coefficients are less than 0.4 for turbulent flow characteristics effects in Fig. 11, but they are usually greater than 1.0 and 0.6 for Re effects and non-stationarity effects, respectively. These are explained in the revised manuscript (see the part highlighted in bold).

14. Please Explain in detail – Line No:370-371 – “The wind field is assumed to be a compressible flow field and the k–ε standard 370 viscous model is utilized.” – Explain about the compressibility

Response: Compressibility means that the density is noticeably increased and the volume is thereby decreased for the fluid flow under pressure, and this effect should not be neglected for fluids like the wind in CFD simulations or analytical calculations. This is explained in the revised manuscript (see the part highlighted in italic).

15. The accuracy and the operation of the novel proposed approach is not suitably proved and it still has a long way.

Response: Thank you so much for your incisive comment. Indeed, the accuracy and the operability of the proposed approach are not suitably proved and it still has a long way to go. However, due to the limited numerical and physical research conditions, the scientific endeavors presented in the manuscript are all we can do for now. In the future, when the research conditions have been improved, we will undertake more systematic and meaningful works to further prove the effectiveness and efficiency of the proposed research scheme. These are explained in the revised manuscript (see the part highlighted in pink).

16. Its contrary to agree with the following lines : Line No:431-432 –“ However, we found that turbulent flow characteristics effects are negligible and 431 do not significantly impact wind loads on the structure”

Response: This is a tentative conclusion since the present research is based on a single case of Peng-cheng cooling tower merely using the CFD approach. Our future research will validate the correctness of this conclusion using more engineering backgrounds and various technical means. These are explained (see the part highlighted with underline). Thank you for your good comment.

Reviewer 2 Report

In this paper, the authors document their efforts to reconcile the differences observed between atmospheric boundary layer field measurements and wind-tunnel simulations, highlighting the independent effects of Reynolds number differences, unsteadiness and spectral contents.

This is an extremely important problem, and one which has been annoying this reviewer for a very long time. The authors have made some valuable contributions here, which I would very much like to see published in Applied Sciences. However, I think there are some fairly major problems with the manuscript which must be addressed before I can recommend publication.

The first point is that I found this paper a bit difficult to understand. Normally, the use of the English language is a trivial matter, easily addressed at proof stage- but here I am concerned that it interfered with my ability to follow the authors' arguments. It is therefore possible that I misunderstood parts of this work.

The authors have framed their work as a proposal for a new technique. However, the evidence presented here is insufficient to demonstrate the generality of their approach, since they are limited to a single model with a single flow field. Instead, I would suggest that the authors frame this work as a demonstration: that the approach works in at least one case rather than in any generalized case.

There is also no discussion here of uncertainty - at the very least, estimates for uncertainty in simulations and experiments are required.

I remain uneasy about the linear superposition of nonlinear flow fields- but the evidence suggests that, at least in the case tested, the approximation holds in a low-fidelity simulation. However, it is possible that this good agreement is spurious: only the one test case was assessed. A more rigorous examination of this approximation is needed before the authors can make any general claims about this method. On the other hand, they may restrict their claims to flow around cooling towers under their particular conditions.

Finally, I get the feeling that there are two independent and only marginally-related projects being presented here, addressing the questions (i) "how do Re effects, unsteadiness and spectral energy distributions each contribute to the discrepancy between field and wind tunnel measurements?" and (ii) can the flow around a bluff body in turbulence be experimentally reproduced by superimposing the responses to each of the isolated waves?" The connection between these two points needs to be much clearer in the logical chain of reasoning, and I would again point out that their answer to the second question is far weaker.

Some additional minor points for the authors to consider:

(a) The introduction and background material was well-written and informative. I would, however, suggest that they include a discussion of their refs. 24 and 25 here to highlight the novelty of this work: if I have understood correctly, the whole point of the spectral decomposition and recombination of flow fields proposed here is to overcome the limitation of fan momentum.

(b) I note that there are undefined acronyms in the body of the text.

(c) Fig 3: the time-domain velocities here are not particularly helpful in providing evidence to support the authors' claim that "only the IMF 1 possesses the commensurate energy in high-frequency domain" - for this, the evidence would be in fig. 4.

(d) Fig 4: these spectra are far too noisy to be discerned: these necessarily need to be smoothed somehow.

(e) P8 L 253, 261-262: providing the explicit sinusoidal equations here is awkward - I would recommend instead a table showing amplitude, frequency and phase for each component. Also, the values given here are are not unitless.

(f) Related to (e), it wasn't clear to me how the authors obtained the individual modes presented. Presumably, their approach would be equivalent to carrying out a standard Fourier-type spectral decomposition, selecting some number of individual waves to reconstruct the original signal with sufficient resolution for the application. I can't see, for example, why the individual amplitudes seem to have been independent variables (0.2 & 0.4 m/s), or why the phase information has been discarded.

(g) Fig 5: from fig 5a, it would seem that the technique doesn't reproduce the characteristics of the signal particularly well at all. Fig 5b is too difficult to interpret- again, the spectra need smoothing.

(h) Something which the authors didn't really address was the difference between their model experiment and CFD- is this what they mean by "turbulent flow characteristics effects"? The disagreement between low-fidelity RANS models and experiment (at matched scales) is usually just down to poor turbulence models or meshing- it's not really fair to include this in their accounting of more fundamental sources of disagreement between scales of (well-designed) experiments.

(i) Since the model was round, I would have expected the authors to have covered it in some sort of roughness: this is best-practice for trying to achieve Re independence. Was this the case? From the image in fig. 13, the model looks smooth.

(j) P16 L 386-389 "...wind effects measured in an intricate ... sinusoidal wave flow fields": the authors do not present sufficient evidence to make this general claim.

(k) P16 L393-396 "Finally, the results ... they are completed": The statement here is speculative - and it may not be appropriate here to describe results not yet reported (that is perhaps an editorial matter).

(l) Fig. 12: Why do these plots appear to have discontinuities? Is this just noise? If so, I'd highlight that the noise is a significant proportion of the differences in the signals themselves, so that my confidence in these would be rather low. Again, a discussion of uncertainty is needed.

(m) Just to be clear - the authors don't seem to be reporting any experimental wind-tunnel) evidence of the superposition independent waves. This renders their claims about approximating results from linear superpositions of modes even more weak.

(m) Fig. 13 does not really provide any additional information. If included, this figure should be in the methodology/setup section.

Needs moderate editing.

Author Response

Reviewer 2

In this paper, the authors document their efforts to reconcile the differences observed between atmospheric boundary layer field measurements and wind-tunnel simulations, highlighting the independent effects of Reynolds number differences, unsteadiness and spectral contents.

This is an extremely important problem, and one which has been annoying this reviewer for a very long time. The authors have made some valuable contributions here, which I would very much like to see published in Applied Sciences. However, I think there are some fairly major problems with the manuscript which must be addressed before I can recommend publication.

The first point is that I found this paper a bit difficult to understand. Normally, the use of the English language is a trivial matter, easily addressed at proof stage- but here I am concerned that it interfered with my ability to follow the authors' arguments. It is therefore possible that I misunderstood parts of this work.

Response: Thank you for the comment. As suggested, we have reread the manuscript several times and found some typos and bad English expressions. We have already corrected the language mistakes, and polished some parts with the help of ChatGPT. We hope the language of the present manuscript can reaches the standard of a publication in Applied Sciences.

The authors have framed their work as a proposal for a new technique. However, the evidence presented here is insufficient to demonstrate the generality of their approach, since they are limited to a single model with a single flow field. Instead, I would suggest that the authors frame this work as a demonstration: that the approach works in at least one case rather than in any generalized case.

Response: Thank you. Indeed, the present work is to deal with a specific case of Peng-cheng cooling tower subject to a specific flow event, and therefore lacks generality. Since we cannot undertake additional works for another case for the time being, we have changed our original claim of a general validation of the proposed framework for the article. The title has been changed to ‘A New Research Scheme for Full-scale/Model Test Comparison of Wind Effects on Peng-cheng Cooling Tower Based on Sinusoidal Flow Field Simulations’, and a lot of phrasing has been changed throughout the manuscript accordingly (see the parts highlighted with shadings). Thank you for your good suggestion.

There is also no discussion here of uncertainty - at the very least, estimates for uncertainty in simulations and experiments are required.

Response: As suggested, the discussions of uncertainties in simulations and experiments have been added in the last paragraph of section ‘5 Conclusions’. According to the discussion, the uncertainty is an important issue perplexing the field measurements, the CFD simulations and the wind tunnel tests in the field of wind engineering. With regard to field measurements, the uncertainties are usually associated with the nature of the realistic wind events (the unsteady and the non-stationary features), the testing errors related to the equipments and the human, and the free choice of the data processing practices. In view of CFD simulations, the uncertainties are fundamentally due to the unrealistic mathematical assumptions and simplifications adopted shown in the forms of free choices of the turbulence model, the wall function, the meshing, etc. The causes of the uncertainties for wind tunnel tests are basically similar to those for field measurements, except that the unsteady and the non-stationary features are less significant for winds generated in the wind tunnel. Therefore, for the proposed research scheme for full-scale/model test comparisons of wind effects on Peng-cheng cooling tower to work well, the uncertainties in simulations and experiments should be further estimated using probability theories or statistical approaches, such as the response surface method. However, due to limited article length, we beg your permission for us to undertake these works in the near future.

I remain uneasy about the linear superposition of nonlinear flow fields- but the evidence suggests that, at least in the case tested, the approximation holds in a low-fidelity simulation. However, it is possible that this good agreement is spurious: only the one test case was assessed. A more rigorous examination of this approximation is needed before the authors can make any general claims about this method. On the other hand, they may restrict their claims to flow around cooling towers under their particular conditions.

Response: Yes, although the evidence approximately holds for the linear superposition practice to simulate the non-stationary flow field, only one specific case is considered, and more rigorous examinations will be performed in the future in order to make the general claims about the proposed simulation method. At present, we restrict the claim to the flow around Peng-cheng cooling tower in the specific wind environment. This is explained in the paragraph before Eqn. (3) in the revised manuscript.

Finally, I get the feeling that there are two independent and only marginally-related projects being presented here, addressing the questions (i) "how do Re effects, unsteadiness and spectral energy distributions each contribute to the discrepancy between field and wind tunnel measurements?" and (ii) can the flow around a bluff body in turbulence be experimentally reproduced by superimposing the responses to each of the isolated waves?" The connection between these two points needs to be much clearer in the logical chain of reasoning, and I would again point out that their answer to the second question is far weaker.

Response: Yes, basically, two scientific issues have been addressed in the present manuscript: (1) how do the three adverse effects (Re effects, turbulent flow characteristics effects and non-stationarity effects) contribute to the total difference between the full-scale measurement and the wind tunnel test; (2) is the approach to create the non-stationary flow field by superimposing the individual basic sinusoidal flow fields reliable. To answer the first question is the main object of the present research, and to make it possible, the second scientific issue should be addressed in the situation that the research scheme proposed cannot be undertaken as planned on a commercial CFD platform or in TJ-6 wind tunnel due to the incapability of both numerical and physical approaches in simulating the non-stationary flow field. This connection between the two points is further emphasized in the revised manuscript (see the second last paragraph of section ‘5 Conclusions’).

Some additional minor points for the authors to consider:

(a) The introduction and background material was well-written and informative. I would, however, suggest that they include a discussion of their refs. 24 and 25 here to highlight the novelty of this work: if I have understood correctly, the whole point of the spectral decomposition and recombination of flow fields proposed here is to overcome the limitation of fan momentum.

Response: As suggested, the power spectrum modification method adopted by Refs. [24,25] in simulating non-stationary velocity fields is introduced in the end of subsection 2.2 to compare with the proposed approach.

(b) I note that there are undefined acronyms in the body of the text.

Response: Thank you for the comment. As suggested, all acronyms have been defined the first time they appear in the manuscript for now.

(c) Fig 3: the time-domain velocities here are not particularly helpful in providing evidence to support the authors' claim that "only the IMF 1 possesses the commensurate energy in high-frequency domain" - for this, the evidence would be in fig. 4.

Response: Thank you for pointing out our error. Yes, the evidence should be in Fig. 4, and we have revised it.

(d) Fig 4: these spectra are far too noisy to be discerned: these necessarily need to be smoothed somehow.

Response: As suggested, all spectra presented Fig. 4 have been smoothed using the 5 point FFT technique.

(e) P8 L 253, 261-262: providing the explicit sinusoidal equations here is awkward - I would recommend instead a table showing amplitude, frequency and phase for each component. Also, the values given here are are not unitless.

Response: As suggested, a table (Table 2) has been added listing the amplitude, the frequency and the phase of all components.

(f) Related to (e), it wasn't clear to me how the authors obtained the individual modes presented. Presumably, their approach would be equivalent to carrying out a standard Fourier-type spectral decomposition, selecting some number of individual waves to reconstruct the original signal with sufficient resolution for the application. I can't see, for example, why the individual amplitudes seem to have been independent variables (0.2 & 0.4 m/s), or why the phase information has been discarded.

Response: Thank you for the comment. According to the present method, empirical mode decomposition is conducted for the original sample first, and IMFs of different dominant frequencies are obtained. As can be seen in Fig. 3, IMF 1 possesses the highest dominant frequency, while IMF 12 possesses the lowest dominant frequency. According to the principle of empirical mode decomposition, the original sample can be reconstructed by linearly superimposing all IMFs. Second, the resulting IMFs are manually approximated using basic sinusoidal waves. According to Table 2, amplitude, frequency and phase of basic sinusoidal functions selected for different IMFs involved are different due to the IMFs are different. For example, the amplitude for IMF 11 is roughly twice as many as that for IMF 10; therefore, A is chosen to be 0.2 and 0.4 for IMF 10 and IMF 11, respectively.

(g) Fig 5: from fig 5a, it would seem that the technique doesn't reproduce the characteristics of the signal particularly well at all. Fig 5b is too difficult to interpret- again, the spectra need smoothing.

Response: Thank you for the good comment. Fig. 5 gives time-histories of all IMFs and the approximating basic sinusoidal functions. Yes, as it seems, the manual approximation method doesn't help to reproduce the characteristics of the signal particularly very well. However, it is all we can do now. However, according to Fig. 6, the original non-stationary velocity sample and the simulated senior sinusoidal function are basically close together in both time and frequency domains. All spectra are smoothed as suggested now (Figs. 4 and 6b).

(h) Something which the authors didn't really address was the difference between their model experiment and CFD- is this what they mean by "turbulent flow characteristics effects"? The disagreement between low-fidelity RANS models and experiment (at matched scales) is usually just down to poor turbulence models or meshing- it's not really fair to include this in their accounting of more fundamental sources of disagreement between scales of (well-designed) experiments.

Response: Thank you for the comment. Yes, as suggested, the disagreement between low-fidelity RANS models and experiment (at matched scales) is usually just down to poor turbulence models or meshing- it's not really fair to include this in their accounting of more fundamental sources of disagreement between scales of (well-designed) experiments. Therefore, a new ABL flow field is modeled in TJ-3 wind tunnel in accordance with the wind velocity field measured on location, which is now regarded as flow field A, and model test is then conducted in that flow field to obtain results for the required comparison to take place. This simulation approach for flow field A employing a passive wind tunnel is different from the planned simulation method of utilizing a CFD platform or an actively controlled wind tunnel for the proposed research scheme (see section 2), as the former is more economical and comparatively more effective.

(i) Since the model was round, I would have expected the authors to have covered it in some sort of roughness: this is best-practice for trying to achieve Re independence. Was this the case? From the image in fig. 13, the model looks smooth.

Response: According to Fig. 1, to quantify the Re effects, the model test in flow field B should be conducted at a low Re (around 1e5 order of magnitude), without the high Re effects simulation (increasing the surface roughness of the test model). To fairly compare with the result obtained flow field B to quantify the other two adverse effects, the model tests conducted in flow field A and the traditional ABL wind tunnel should use the model without high Re effects simulation too. Anyway, thank you for your good suggestion.

(j) P16 L 386-389 "...wind effects measured in an intricate ... sinusoidal wave flow fields": the authors do not present sufficient evidence to make this general claim.

Response: Thank you. As suggested, this sentence is rephrased to ‘it can be tentatively inferred from the above observations that wind effects measured in a comparatively more complicated flow field obtained by linearly superposing two basic sinusoidal wave flow fields approximately equal to the averages of wind effects measured in the individual basic sinusoidal wave flow fields’.

(k) P16 L393-396 "Finally, the results ... they are completed": The statement here is speculative - and it may not be appropriate here to describe results not yet reported (that is perhaps an editorial matter).

Response: Thank you. As suggested, this part is deleted to avoid misleading the readers.

(l) Fig. 12: Why do these plots appear to have discontinuities? Is this just noise? If so, I'd highlight that the noise is a significant proportion of the differences in the signals themselves, so that my confidence in these would be rather low. Again, a discussion of uncertainty is needed.

Response: Thank you for the comment. This issue has been discussed in the revised manuscript (see the last sentence before Fig. 13).

(m) Just to be clear - the authors don't seem to be reporting any experimental wind-tunnel) evidence of the superposition independent waves. This renders their claims about approximating results from linear superpositions of modes even more weak.

Response: Thank you for the comment. Section 4 just presents a new method conceived for actively controlled wind tunnel tests. We are now preparing the physical model tests in TJ-6 wind tunnel following the new method conceived. However, these works are undergoing. We beg your permission for us to complete them in the near future and report them in another article.

(m) Fig. 13 does not really provide any additional information. If included, this figure should be in the methodology/setup section.

Response: Thank you for the comment. As suggested, this figure has been deleted.

Round 2

Reviewer 2 Report

In their revision, the authors have addressed most of my points of concern. By limiting their claims to the specific case of their particular cooling tower, they now have direct evidence for all of their findings. I am now pleased to recommend this article for publication, subject to minor revisions at the authors' discretion. My recommendation is not conditional upon these revisions - they are recommendations only.

My only remaining concern is over the statement of uncertainties: I think the authors may have misunderstood my original comment. An estimate of overall uncertainty from field measurements is not reasonable to expect – but a simple inclusion of quantitative justifiable estimates of uncertainty from their measurement chain or numerical processes is normally a minimum requirement for most journals. I will allow that there may be discipline-to-discipline variability here.

The paper will need careful proofing ahead of publication.

Author Response

Reviewer 2

In their revision, the authors have addressed most of my points of concern. By limiting their claims to the specific case of their particular cooling tower, they now have direct evidence for all of their findings. I am now pleased to recommend this article for publication, subject to minor revisions at the authors' discretion. My recommendation is not conditional upon these revisions - they are recommendations only.

My only remaining concern is over the statement of uncertainties: I think the authors may have misunderstood my original comment. An estimate of overall uncertainty from field measurements is not reasonable to expect – but a simple inclusion of quantitative justifiable estimates of uncertainty from their measurement chain or numerical processes is normally a minimum requirement for most journals. I will allow that there may be discipline-to-discipline variability here.

Response: Thank you for the comment. We are so sorry for our misunderstanding, and we have got your meaning for now. As suggested, a simple quantitative estimate of the uncertainty due to the initial state of calculation from the numerical process presented in subsection 3.2 is included in subsection 3.4. By changing the initial phase of all components in the original senior sinusoidal function (Eqn. (3)), three other senior sinusoidal functions are obtained as inlet velocity samples. By inputting these three inlet velocity samples into the numerical program, simulations are redone on Fluent platform in flow field B, and the results for the three additional cases are added in Fig. 10 (the three dash lines). Comparing the results of 2nd~4th runs of numerical analyses with the initial numerical data, it can be seen they are basically close together, and the uncertainties in relative errors calculated are in the accepted range [0, 60%], suggesting that the uncertainty from the initial state of calculation is insignificant for the present study. We hope these added analyses can help address the issue of uncertainty in part. Thank you again for helping us to improve the quality of our research.