Effects of Si Target Power on the Mechanical Properties and Antioxidation and Antiablation Properties of Magnetron-Sputtered (WMoTaNb)SiN Refractory High-Entropy Nitride Films

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

This paper discusses the effect of Si on the properties of the magnetron sputtered RHEA nitride films. The manuscript is well structured and presents comprehensive results. However, the manuscript requires a major revision. The authors can find my comments below:

1. In the introduction, the authors state „The incorporation of Si into nitride films has been extensively explored as an effective microstructural design strategy“ and provide only two references [18] and [12]. This does not look like „extensively exproled“. The authors are encouraged to provide more references and discuss them.

2. Film preparation: it is not clear how an RF+DC sputtering was utilized. What target was deposited in the RF mode?

3. XRD: what database was used to identify the phases? Also, it is not clear what phases FCC and BCC actually are. Are they nitrides? The authors should be clear what exact phases form. In Figure 1, the authors should provide theoretical XRD patterns of both FCC and BCC phases and indicate the exact composition of the theoretical XRD patterns. The peak at ~62° does not look like FCC, and it is just Si. The same peak in Figure 10 is identified only as Si. The authors are encouraged to perform a Rietveld refinement to obtain an approximate quantitative phase analysis. While the Si substrate contributes to the diffraction pattern and may influence the absolute phase fractions, this limitation is common to all samples. Therefore, a relative comparison of phase fractions between samples would still be meaningful and informative. It will also help see any lattice distortions caused by the Si addition.

4. The authors state „The cross-sectional morphologies of the films showed typical columnar growth structures.“ and then „The transition trend from a disordered structure to a columnar structure is significantly altered.“ The second statement is not clear. Figure 2 shows columnar structures for all specimens, and the second statement contradicts the first. The authors should clarify what they wanted to state.

5. “However, the introduction of Si improves crystal compatibility between the film and substrate, thereby modifying the initial structure at the film‒substrate interface.” This statement is currently speculative and requires quantitative support. The authors are encouraged to calculate or estimate the stresses in the films (e.g., residual or misfit stresses) or to provide other direct or indirect evidence supporting improved crystal compatibility at the film-substrate interface. In addition, relevant literature references should be added to substantiate this claim.

6. Figure 3 shows that the EDS elemental map of N clearly indicates its absence in certain regions of the cross-section (possibly along grain boundaries). However, this observation is not discussed in the manuscript. Therefore, the statement “elements were homogeneously distributed throughout the microstructure of the films” is not supported by the presented EDS data and should be either revised or properly justified. The authors are encouraged to discuss the observed inhomogeneity and clarify its origin and implications for the film microstructure and properties.

7. The statement “This can be attributed to the introduction of Si, which suppresses grain growth and facilitates the formation of an amorphous phase. Under the combined effects of grain refinement and interface strengthening, the film achieves optimal mechanical properties.” is not sufficiently supported by the presented results.

First, the implied mechanism suggests that Si segregates to grain boundaries and suppresses grain growth by GB pinning. However, Figure 3 indicates a largely homogeneous Si distribution, which does not support this interpretation.
Second, no quantitative evidence is provided to demonstrate grain size refinement with increasing Si content. The manuscript lacks a systematic grain size analysis.
Third, the role of the amorphous phase in enhancing hardness is not clearly justified. In general, hardness is associated with strong interatomic bonding and effective impediment of plastic deformation, whereas the contribution of an amorphous phase requires explicit discussion and supporting evidence.
The authors are therefore encouraged to provide quantitative and mechanistic support for this claim. This may include, among other evidence, grain size refinement analysis based on XRD results (e.g., peak broadening analysis), as well as a clearer discussion of how the amorphous phase contributes to the measured mechanical properties. 

8. The authors are encouraged to provide hardness measurements for the oxidized films to prove their statement regarding the role of Si in enhancing oxidation resistance.

Minor:
Page 12, Line 264. “owing to the low Si tareget power“ – should be „target“

Author Response

Comments 1:In the introduction, the authors state „The incorporation of Si into nitride films has been extensively explored as an effective microstructural design strategy“ and provide only two references [18] and [12]. This does not look like „extensively exproled“. The authors are encouraged to provide more references and discuss them.

Response 1:We thank the reviewer for this valuable comment. We agree that the original statement was insufficiently supported by only two references. In the revised manuscript, we expanded the relevant part of the Introduction by adding more representative studies on Si-alloyed nitride films and briefly discussing their reported effects on microstructure, hardness, adhesion, tribological behavior, and oxidation-related performance. This revision better supports the statement that Si incorporation has been extensively explored as a microstructural design strategy in nitride films.

Comments 2:Film preparation: it is not clear how an RF+DC sputtering was utilized. What target was deposited in the RF mode?

Response 2:We thank the reviewer for pointing this out. We have revised the Experimental section to clarify the sputtering power supply configuration. In the present work, the refractory alloy target (WMoTaNb) was operated in RF mode, whereas the Si target was operated in DC mode during co-sputtering. We also clarified that the Si target power was varied (0, 15, 30, and 45 W) to regulate the Si incorporation level, while the WMoTaNb target power was kept constant.

Comments 3:XRD: what database was used to identify the phases? Also, it is not clear what phases FCC and BCC actually are. Are they nitrides? The authors should be clear what exact phases form. In Figure 1, the authors should provide theoretical XRD patterns of both FCC and BCC phases and indicate the exact composition of the theoretical XRD patterns. The peak at ~62° does not look like FCC, and it is just Si. The same peak in Figure 10 is identified only as Si. The authors are encouraged to perform a Rietveld refinement to obtain an approximate quantitative phase analysis. While the Si substrate contributes to the diffraction pattern and may influence the absolute phase fractions, this limitation is common to all samples. Therefore, a relative comparison of phase fractions between samples would still be meaningful and informative. It will also help see any lattice distortions caused by the Si addition.

Response 3:We thank the reviewer for the detailed and insightful comments on the XRD analysis. In the revised manuscript, we clarified that phase indexing was performed by matching the diffraction peaks against the ICDD PDF-4+ database. We also revised the XRD discussion to clearly state that the observed FCC and BCC features are attributed to crystalline nitride-related phases in the films (rather than substrate peaks), while the reflections labeled as Si originate from the Si substrate. In particular, we explicitly clarified that the intense peak at approximately 62° and other Si-labeled reflections are substrate contributions, consistent with the interpretation in Fig. 10.

Following the reviewer’s suggestion, we strengthened the textual discussion of phase evolution, including the coexistence of FCC-dominant and weak BCC features, the effect of increasing Si target power on diffraction intensity evolution, and the structural implication of the diffuse hump (amorphous contribution). We also added text to clarify that the XRD patterns shown in Fig. 1 were collected on Si substrates to reduce interference from metallic substrate diffraction.

Regarding Rietveld refinement, we appreciate the reviewer’s recommendation. However, in the present work we did not perform Rietveld refinement. Because of the strong substrate contribution, partial peak overlap, thin-film signal limitations, and the absence of a dedicated measurement configuration for reliable quantitative refinement, we considered the resulting absolute phase fractions to be insufficiently robust. Instead, we revised the manuscript to present a more cautious qualitative to semi-quantitative interpretation based on directly observed diffraction features (peak evolution and diffuse hump), and we explicitly note this limitation.

Comments 4:The authors state „The cross-sectional morphologies of the films showed typical columnar growth structures.“ and then „The transition trend from a disordered structure to a columnar structure is significantly altered.“ The second statement is not clear. Figure 2 shows columnar structures for all specimens, and the second statement contradicts the first. The authors should clarify what they wanted to state.

Response 4:We thank the reviewer for identifying this inconsistency. We agree that the original wording was ambiguous and could be interpreted as contradictory. In the revised manuscript, we removed the confusing statement and rephrased the description to consistently state that all films exhibit columnar growth in cross-section. The discussion now focuses on changes in the compactness and morphological characteristics of the columnar structure with increasing Si target power, rather than implying a transition from disordered to columnar growth.

Comments 5:“However, the introduction of Si improves crystal compatibility between the film and substrate, thereby modifying the initial structure at the film‒substrate interface.” This statement is currently speculative and requires quantitative support. The authors are encouraged to calculate or estimate the stresses in the films (e.g., residual or misfit stresses) or to provide other direct or indirect evidence supporting improved crystal compatibility at the film-substrate interface. In addition, relevant literature references should be added to substantiate this claim.

Response 5:We thank the reviewer for this important comment. We agree that the statement on “improved crystal compatibility” at the film–substrate interface was overly speculative and not sufficiently supported by direct evidence in the present study. In the revised manuscript, we removed (or substantially softened) this statement and avoided attributing the observed structural evolution to interfacial crystal compatibility without quantitative support. The revised discussion now emphasizes experimentally supported factors such as changes in growth behavior under different Si target powers and the resulting microstructural evolution, while refraining from unsupported assertions regarding interfacial matching and stress. We also acknowledge in the manuscript that residual-stress quantification was not performed in this work.

Comments 6:Figure 3 shows that the EDS elemental map of N clearly indicates its absence in certain regions of the cross-section (possibly along grain boundaries). However, this observation is not discussed in the manuscript. Therefore, the statement “elements were homogeneously distributed throughout the microstructure of the films” is not supported by the presented EDS data and should be either revised or properly justified. The authors are encouraged to discuss the observed inhomogeneity and clarify its origin and implications for the film microstructure and properties.

Response 6:We thank the reviewer for this careful observation. We agree that the original statement describing all elements as “homogeneously distributed” was too strong in light of the EDS maps, particularly for nitrogen. In the revised manuscript, we revised the wording to avoid overgeneralization and explicitly noted that the elemental maps indicate an overall distribution of the constituent elements within the film region, while local contrast variations (especially in the N map) are present. We also added a brief discussion that such local variations may arise from microstructural contrast, local density differences, and the intrinsic limitations of EDS mapping in thin-film cross-sectional analysis, and therefore should be interpreted cautiously.

Comments 7:The statement “This can be attributed to the introduction of Si, which suppresses grain growth and facilitates the formation of an amorphous phase. Under the combined effects of grain refinement and interface strengthening, the film achieves optimal mechanical properties.” is not sufficiently supported by the presented results.

First, the implied mechanism suggests that Si segregates to grain boundaries and suppresses grain growth by GB pinning. However, Figure 3 indicates a largely homogeneous Si distribution, which does not support this interpretation.
Second, no quantitative evidence is provided to demonstrate grain size refinement with increasing Si content. The manuscript lacks a systematic grain size analysis.
Third, the role of the amorphous phase in enhancing hardness is not clearly justified. In general, hardness is associated with strong interatomic bonding and effective impediment of plastic deformation, whereas the contribution of an amorphous phase requires explicit discussion and supporting evidence.
The authors are therefore encouraged to provide quantitative and mechanistic support for this claim. This may include, among other evidence, grain size refinement analysis based on XRD results (e.g., peak broadening analysis), as well as a clearer discussion of how the amorphous phase contributes to the measured mechanical properties. 

Response 7:We thank the reviewer for the valuable comments on the strengthening mechanism. We agree that the previous discussion overemphasized grain-boundary pinning by Si and grain refinement without direct evidence. In the revised manuscript, we removed the speculative statements regarding Si segregation to grain boundaries and rewrote the mechanism discussion based on the experimental observations. Specifically, we now correlate the hardness evolution with (i) the increased amorphous contribution indicated by the progressively intensified diffuse hump in XRD and (ii) the lattice-parameter variation implied by the peak-position shifts of FCC reflections, suggesting enhanced lattice distortion in the FCC nitride solid solution. We further clarify that the hardness maximum at an intermediate Si target power can be rationalized by lattice distortion strengthening together with an interface-rich amorphous component that constrains plastic flow, whereas excessive amorphization at higher Si target power may reduce the effective load-bearing crystalline fraction, leading to a hardness decrease.

We also acknowledge that a rigorous grain-size quantification was not provided and clarify that quantitative grain-size and amorphous-fraction determination requires TEM-based statistics, which is beyond the scope of the present study and will be addressed in future work. Regarding the reviewer’s suggestion on XRD peak broadening analysis, we note that a rigorous grain-size extraction from peak widths is non-trivial for the present thin films due to the strong Si substrate contribution, partial peak overlap, and the lack of instrumental broadening calibration. Therefore, we did not include Scherrer or Williamson–Hall quantification in this revision. Instead, we revised the mechanism discussion to rely on directly observed structural indicators (diffuse-hump evolution and FCC peak-position variations), and we explicitly state this limitation in the manuscript.

Comments 8:The authors are encouraged to provide hardness measurements for the oxidized films to prove their statement regarding the role of Si in enhancing oxidation resistance.

Response 8:We thank the reviewer for the helpful suggestion. We attempted to evaluate the post-oxidation mechanical integrity by nanoindentation; however, after oxidation in air at 1000 °C for 2 h followed by air cooling, the oxidized surfaces were discontinuous and mechanically unstable. Under such conditions, nanoindentation cannot provide reliable hardness values because the indenter may probe loose surface regions, voided areas, or locally exposed substrate, leading to non-representative measurements. Therefore, we did not include post-oxidation hardness data in the revision. Instead, we strengthened the oxidation-resistance assessment using complementary evidence that remains valid in the presence of surface discontinuity, including the oxide-phase evolution from XRD, the surface morphology from SEM, and the cross-sectional oxide-scale thickness measurements. We have also stated this limitation in the revised manuscript and indicated that quantifying post-oxidation mechanical properties requires mechanically intact surfaces, which will be addressed in future work.

Comments 9:Minor:Page 12, Line 264. “owing to the low Si tareget power“ – should be „target“

Response 9:We thank the reviewer for catching this typographical error. It has been corrected in the revised manuscript.

Reviewer 2 Report

Comments and Suggestions for Authors

The article is devoted to the topical problem of creating protective coatings for operation in extreme conditions (high temperatures, mechanical wear, ablation). The study of high-entropy nitride films (RHEN) of the (WMoTaNb)SiN system is of scientific interest because it combines the concept of high-entropy alloys with nanostructuring through the addition of silicon. The work contributes to the understanding of the synergistic effect of the high-entropy matrix and the amorphous phase of SiNx. The results on ablation resistance have direct practical significance for the aerospace industry.

The article is logically structured. However, the article can be improved with the following corrections:

1. The text mentions a two-phase structure of HSC + OSC. However, the X-ray diffraction patterns (Fig. 1) and the discussion also refer to an amorphous phase caused by the introduction of Si. It is necessary to more accurately quantify the ratio of crystalline and amorphous phases, for example, using transmission electron microscopy (TEM), as this is critical for explaining the strengthening mechanism.
2. The text states that the inclusion of Si reduced roughness, but at the same time, the CTE for films with Si (0.85 and 0.82) is higher than for films without Si (0.71). This contradiction requires a more in-depth explanation: why does the friction coefficient increase when roughness and wear are reduced?
3. The description of the ablation process (8 cycles of 0.5 s) is brief. It is recommended to add data on the surface temperature during ablation and to analyze in more detail the “local destruction” mentioned in the conclusions.
4. The table of chemical composition after oxidation shows a very low content of W and Mo (less than 4%), which is explained by their evaporation. However, it is worth adding a comment on how deep this depletion occurs and how it correlates with the thickness of the oxide layer.
5. The authors note a decrease in adhesion at high Si power due to lattice distortion. It would be useful to correlate this with internal stresses in films, which often increase with an increase in the proportion of the amorphous phase in nitrides.
6. Give the description of abbreviations (DC, FCC, DСС, EDS, XRD, SEM)
7. Indicate the limitations of the study

The article requires minor revisions.

Author Response

Response to Reviewer 2, We sincerely thank Reviewer 2 for the constructive comments and the positive evaluation of the scientific significance and practical relevance of this work. We have carefully revised the manuscript accordingly. Our point-by-point responses are provided below.

Comments 1:The text mentions a two-phase structure of HSC + OSC. However, the X-ray diffraction patterns (Fig. 1) and the discussion also refer to an amorphous phase caused by the introduction of Si. It is necessary to more accurately quantify the ratio of crystalline and amorphous phases, for example, using transmission electron microscopy (TEM), as this is critical for explaining the strengthening mechanism.

Response 1:We thank the reviewer for the insightful suggestion. We agree that the description of a “two-phase structure (HSC + OSC)” may be confusing when an amorphous contribution is also discussed. In the revised manuscript, we clarified the structural description to indicate that the films exhibit a mixed microstructure consisting of crystalline components (FCC-dominant with weak BCC features) together with an amorphous contribution, as evidenced by the diffuse hump in the XRD patterns. We also acknowledge that rigorous quantification of the crystalline-to-amorphous fraction requires TEM-based characterization, which is beyond the scope of the present work. This limitation has been explicitly stated, and TEM quantification will be considered in future work.

Comments 2:The text states that the inclusion of Si reduced roughness, but at the same time, the CTE for films with Si (0.85 and 0.82) is higher than for films without Si (0.71). This contradiction requires a more in-depth explanation: why does the friction coefficient increase when roughness and wear are reduced?

Response 2:We thank the reviewer for pointing out this apparent inconsistency. In the revised manuscript, we clarified that the friction coefficient and wear rate are not necessarily positively correlated because they are governed by different controlling factors. A smoother and denser surface can reduce material removal by suppressing stress concentration and brittle fracture, thereby improving wear resistance. In contrast, the friction coefficient is strongly affected by interfacial shear strength and tribochemical reactions. In our case, the oxygen distribution in the wear tracks indicates tribo-oxidation, and an oxide-rich tribolayer may increase interfacial shear resistance (leading to a higher friction coefficient) while simultaneously acting as a protective third body that reduces direct damage to the film and lowers the wear rate. We revised the tribological discussion accordingly to explicitly distinguish friction behavior from wear resistance.

Comments 3:The description of the ablation process (8 cycles of 0.5 s) is brief. It is recommended to add data on the surface temperature during ablation and to analyze in more detail the “local destruction” mentioned in the conclusions.

Response 3:We thank the reviewer for the constructive comments. We agree that real-time surface-temperature monitoring during oxyhydrogen-flame exposure would further enrich the ablation analysis. However, such measurements were not performed in the present experimental setup and therefore cannot be added in this revision. To address the reviewer’s concern, we have expanded the ablation discussion based on the available evidence, including macroscopic morphology, laser confocal ablation profiles, mass changes after repeated cycles, and EDS point analyses. In particular, we clarified that the “local destruction” refers to localized film removal and substrate exposure in the ablation center, as indicated by the high Fe signal (originating from the substrate) and the contrast between film-covered and film-depleted regions. This provides a more explicit and evidence-based description of ablation damage evolution. We also state in the manuscript that real-time temperature monitoring will be considered in future work.

Comments 4:The table of chemical composition after oxidation shows a very low content of W and Mo (less than 4%), which is explained by their evaporation. However, it is worth adding a comment on how deep this depletion occurs and how it correlates with the thickness of the oxide layer.

Response 4:We thank the reviewer for this important comment. In the revised manuscript, we clarified that the reported EDS point-analysis data after oxidation represent local compositions of the outer oxide regions, rather than the bulk composition of the underlying film. The very low W and Mo contents in these surface oxide products are consistent with the volatilization tendency of WO₃ and MoO₃ at high temperature, leaving Nb- and Ta-rich oxides as dominant residual phases. We further relate this observation to the measured oxide-scale thickness (approximately 2.218–3.353 μm), indicating that the depletion phenomenon discussed here is associated with the oxide scale. At the same time, we acknowledge that a quantitative depth-resolved depletion profile would require dedicated depth-profiling methods or cross-sectional compositional line scans, which were not performed in the present work. This limitation has been stated in the revised manuscript.

Comments 5:The authors note a decrease in adhesion at high Si power due to lattice distortion. It would be useful to correlate this with internal stresses in films, which often increase with an increase in the proportion of the amorphous phase in nitrides.

Response 5:We thank the reviewer for this valuable suggestion. We agree that internal stress is an important factor affecting the adhesion behavior of nitride films, particularly when the amorphous contribution increases. In the revised manuscript, we have rephrased the relevant discussion to avoid over-assertive attribution of the adhesion decrease solely to lattice distortion. The text now states that the reduced adhesion at high Si target power may be associated with increased structural disorder and potentially elevated residual stress, while also emphasizing that residual stress was not directly measured in the present work. This revision makes the interpretation more cautious and evidence-based.

Comments 6:Give the description of abbreviations (DC, FCC, DСС, EDS, XRD, SEM)

Response 6:We thank the reviewer for this helpful comment. In the revised manuscript, we added explicit descriptions of the key abbreviations used throughout the text, including DC, RF, FCC, BCC (the reviewer’s “DСС” is understood as BCC), EDS, XRD, and SEM. This revision improves readability and avoids ambiguity for readers from different backgrounds.

Comments 7:Indicate the limitations of the study

Response 7:We thank the reviewer for this important suggestion. In the revised manuscript, we explicitly added a limitations statement to improve transparency and to define the scope of the present conclusions. The limitations now described include: (i) the absence of TEM-based quantitative analysis of crystalline and amorphous fractions, (ii) the absence of residual-stress measurements, (iii) the lack of depth-resolved compositional profiling for oxidized/ablated regions, and (iv) the absence of real-time surface-temperature monitoring during oxyhydrogen-flame ablation. These points are now clearly stated, and related future work directions are briefly indicated.

Reviewer 3 Report

Comments and Suggestions for Authors

This manuscript presents the results of extensive research. However, it appears that some errors have been made, as noted below. These errors must be corrected because they do not render the results credible. Therefore, I recommend major corrections.

The authors deposited a thin film on silicon and M2 steel. Experience and literature indicate that the substrate influences the chemical and phase composition, as well as the crystallite size, of the thin films formed. The authors do not mention this.

Figure 1 shows an XRD plot of the film formed on a silicon substrate, but it is unclear where the Si originated. Why is the XRD plot of the film on a steel substrate not also presented?

The energy resolution of the EDS method is 120-140 eV. When analyzing the chemical composition of tungsten and silicon, there is a strong overlap of lines: W Mα (1.775 keV) ≈ Si Kα (1.740 keV). The difference is 0.035 keV = 35 eV. In this case, the silicon line is masked by the tungsten line, making the EDS analysis unreliable, especially when it comes to determining the silicon concentration?

Figure 4 is not commented on in the manuscript. It provides valuable information about the Si content depending on the magnetron power. Furthermore, the Si content increases slightly with increasing power. It seems that this increase should be much larger.. This is certainly related to the silicon being obscured by the tungsten line.

A similar note applies to Tables 2 and 4 regarding the energy resolution of the EDS microanalyzer for W Ma and Si Ka.

Was the wear of the steel ball taken into account when determining the wear rate?

Author Response

Response to Reviewer 3，We sincerely thank Reviewer 3 for the careful evaluation and for pointing out several important issues related to substrate effects, XRD interpretation, EDS quantification, and wear-rate calculation. We have revised the manuscript accordingly and clarified the corresponding limitations. Our point-by-point responses are provided below.

Comments 1：The authors deposited a thin film on silicon and M2 steel. Experience and literature indicate that the substrate influences the chemical and phase composition, as well as the crystallite size, of the thin films formed. The authors do not mention this.

Response 1：We thank the reviewer for this important comment. We agree that the substrate can influence thin-film nucleation and early-stage growth behavior, which may affect the microstructure and related structural features. In the revised manuscript, we have added a clarification on the use of two different substrates in this study. Specifically, Si substrates were employed for XRD and microstructural characterization to reduce interference from strong metallic substrate diffraction, whereas M2 steel substrates were used for mechanical and tribological testing to reflect practical application conditions. We also added a statement noting that substrate effects may influence the initial growth region, while the phase-evolution discussion with varying Si target power is based on the film-related diffraction features after excluding substrate reflections. This clarification improves the rigor and transparency of the manuscript.

Comments 2：Figure 1 shows an XRD plot of the film formed on a silicon substrate, but it is unclear where the Si originated. Why is the XRD plot of the film on a steel substrate not also presented?

Response 2：We thank the reviewer for this valuable comment. In the revised manuscript, we explicitly clarify that the reflections labeled as Si in Fig. 1 originate from the Si substrate rather than the films. In particular, the intense peak near approximately 62° and the other Si-labeled reflections are substrate peaks, consistent with the interpretation used in the oxidation XRD patterns (Fig. 10). We also clarified why XRD patterns on M2 steel substrates were not presented: under conventional θ–2θ geometry, the diffraction from the steel substrate is strong and can obscure the relatively weak diffraction signals from the thin films, making comparative analysis of film-related peaks less reliable. Therefore, Si substrates were used for structural phase identification and comparison. We note in the revised text that grazing-incidence XRD would be more suitable for resolving film diffraction on steel substrates and may be considered in future work.

Comments 3：The energy resolution of the EDS method is 120-140 eV. When analyzing the chemical composition of tungsten and silicon, there is a strong overlap of lines: W Mα (1.775 keV) ≈ Si Kα (1.740 keV). The difference is 0.035 keV = 35 eV. In this case, the silicon line is masked by the tungsten line, making the EDS analysis unreliable, especially when it comes to determining the silicon concentration?

Response 3：We thank the reviewer for raising this important point regarding the potential spectral overlap between W Mα and Si Kα in EDS analysis. We agree that this spectral proximity can introduce uncertainty in Si quantification for W-containing systems. In the revised manuscript, we explicitly acknowledge this limitation and clarify that the EDS-derived Si contents are used primarily to reflect the relative variation trend with increasing Si target power, rather than absolute values with high precision. We also note that the EDS quantification in the present study should be regarded as semi-quantitative for Si in W-containing regions. More accurate Si quantification would require higher-resolution techniques, such as WDS, XPS, or other dedicated compositional analyses, which are beyond the scope of the present work. This clarification has been incorporated into the compositional discussion and table notes.

Comments 4：Figure 4 is not commented on in the manuscript. It provides valuable information about the Si content depending on the magnetron power. Furthermore, the Si content increases slightly with increasing power. It seems that this increase should be much larger.. This is certainly related to the silicon being obscured by the tungsten line.

Response 4：We thank the reviewer for this important comment. We agree that Fig. 4 should be explicitly discussed in the manuscript. In the revised version, we added a dedicated paragraph describing the compositional evolution shown in Fig. 4. The measured Si content increases monotonically with increasing Si target power, confirming that Si incorporation can be regulated by adjusting Si target power during co-sputtering. At the same time, we acknowledge that the absolute Si values obtained by EDS in W-containing films may carry uncertainty due to the potential spectral proximity between W Mα and Si Kα. Therefore, the revised discussion emphasizes the monotonic compositional trend rather than the absolute magnitude of the Si concentration. We also note that the moderate increase in measured Si content may reflect both the EDS limitation and the incorporation efficiency under the present reactive co-sputtering conditions.

Comments 5：A similar note applies to Tables 2 and 4 regarding the energy resolution of the EDS microanalyzer for W Ma and Si Ka.

Response 5：We thank the reviewer for this consistent and important observation. We agree that the same potential overlap issue between W Mα and Si Kα is relevant to the EDS point-analysis data reported in Tables 2 and 4. In the revised manuscript, we added explicit notes to Tables 2 and 4 clarifying that the Si values in W-containing regions should be interpreted as semi-quantitative and are used mainly for comparative analysis among different areas and samples. This revision improves the transparency and rigor of the EDS-based compositional interpretation.

Comments 6：Was the wear of the steel ball taken into account when determining the wear rate?

Response 6：We thank the reviewer for this helpful question. In the present work, the reported specific wear rate was calculated from the wear volume loss of the film-coated specimen based on the wear-track geometry/profile. The wear of the GCr15 steel ball counterface was not included in the reported wear-rate value, which is consistent with the conventional definition of specimen-specific wear rate used in tribological evaluation. We have clarified this point in the revised manuscript. We also acknowledge that counterface wear may contribute to third-body debris and can influence friction behavior, and this has been briefly noted in the tribological discussion.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript can be accepted in its present form.

Reviewer 3 Report

Comments and Suggestions for Authors

The authors have added some content to the manuscript that was essential for understanding. This has improved the quality of the manuscript. The explanations are also satisfactory.