Optimizing Hoffmann Reflex Rate-Dependent Depression: A Feasible Protocol for Assessing Spinal Inhibition in Upper and Lower Limbs

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The article addresses an important methodological problem related to the lack of standardization in measurements of rate-dependent depression of the Hoffmann reflex (RDD-HR) and proposes a simplified protocol intended to enhance its clinical applicability. Despite a solid theoretical background and a properly conducted experiment, the manuscript contains several significant limitations that, in its current form, weaken the strength of its conclusions and require revision.

The most serious issue is the discrepancy between the strongly emphasized clinical narrative and the actual scope of the study. The authors repeatedly highlight the potential of RDD-HR as a biomarker in neuropathies, neurodegenerative diseases, and spinal cord injuries; however, all analyses were conducted exclusively in healthy volunteers. As a result, the proposed simplified protocol has not been verified in terms of its ability to discriminate pathological states, and its sensitivity and specificity remain unknown. In its present form, the study does not provide evidence that the abbreviated measurement scheme preserves the diagnostic value attributed to more extensive protocols used previously. Consequently, the clinical narrative should be clearly restrained or supplemented with at least pilot data from patient populations.

Another important concern relates to interpretative inconsistencies regarding the magnitude of Hoffmann reflex depression. The authors report maximal depression of approximately 30% in the lower limbs, which clearly differs from values commonly reported in the literature, where reductions often reach 60–90%. At the same time, statements appear indicating that stimulation at 1 Hz achieves approximately 90% of maximal depression, which may be misleading when considered alongside the numerical data presented. This issue likely arises from normalization to the first response and the use of median area under the curve rather than peak amplitude; however, these methodological implications are not explained with sufficient clarity. A more precise definition of “maximal depression” is required, along with a clear distinction between percentage reduction relative to H1 and the proportion of the asymptotic plateau reached.

A further limitation of the study is the absence of any assessment of measurement reliability. Although the authors focus on statistical precision through bootstrap procedures and confidence intervals, they provide no information on the repeatability of the measurements over time. There is no test–retest analysis, no intraclass correlation coefficients, and no evaluation of between-day variability. Given that the manuscript proposes a standardized clinical protocol, this omission represents a substantial weakness, as temporal stability is a fundamental requirement for any biomarker.

Additionally, although the sample was carefully selected, it included participants across a relatively broad age range and of both sexes, without any analysis of the potential influence of these variables on the results. This is problematic because the authors themselves cite literature demonstrating that age and sex significantly modulate RDD-HR. The absence of stratified or even exploratory analyses limits the generalizability of the findings and should be more explicitly acknowledged as a study limitation.

The conclusions regarding upper limb measurements also appear overly optimistic. While the authors convincingly demonstrate the technical feasibility of recording RDD-HR from the flexor carpi radialis muscle, the observed depression is clearly smaller and more variable than that recorded in the lower limbs. Nevertheless, upper and lower limb measurements are treated as functionally equivalent, without sufficient evidence that their diagnostic value is comparable. Greater interpretative caution would be warranted in this regard.

At the narrative level, the discussion at times resembles a review article rather than a focused analysis of the presented data. Considerable space is devoted to general GABAergic mechanisms and potential clinical applications that are not directly supported by the study’s results. At the same time, the study’s limitations, although mentioned, are not emphasized strongly enough, which weakens the critical balance of the manuscript.

In summary, the article represents a methodologically sound and potentially useful contribution to efforts aimed at simplifying RDD-HR protocols; however, in its current form, it overstates its clinical implications. The conclusions should be regarded as preliminary rather than definitive. With clearer definitions, a more restrained clinical narrative, and the inclusion of missing validation analyses, the manuscript could become a valuable foundation for future translational research.

Comments on the Quality of English Language

The English could be improved to more clearly express the research.

Author Response

Comments 1: The article addresses an important methodological problem related to the lack of standardization in measurements of rate-dependent depression of the Hoffmann reflex (RDD-HR) and proposes a simplified protocol intended to enhance its clinical applicability. Despite a solid theoretical background and a properly conducted experiment, the manuscript contains several significant limitations that, in its current form, weaken the strength of its conclusions and require revision.

Response 1: We thank the Reviewer for the careful evaluation of our manuscript and for recognizing the clinical relevance of addressing methodological standardization in RDD-HR assessment. We acknowledge the concerns raised regarding the limitations of the study. In response, we have revised the manuscript to address these points where possible and to clarify the scope and interpretation of our findings. All modifications have been incorporated into the revised version, and the corresponding changes are highlighted in red.

 

Comments 2: The most serious issue is the discrepancy between the strongly emphasized clinical narrative and the actual scope of the study. The authors repeatedly highlight the potential of RDD-HR as a biomarker in neuropathies, neurodegenerative diseases, and spinal cord injuries; however, all analyses were conducted exclusively in healthy volunteers. As a result, the proposed simplified protocol has not been verified in terms of its ability to discriminate pathological states, and its sensitivity and specificity remain unknown. In its present form, the study does not provide evidence that the abbreviated measurement scheme preserves the diagnostic value attributed to more extensive protocols used previously. Consequently, the clinical narrative should be clearly restrained or supplemented with at least pilot data from patient populations.

Response 2: We agree that the present study was conducted exclusively in healthy volunteers and, therefore, does not provide direct evidence regarding diagnostic sensitivity, specificity, or discriminative performance in clinical populations. The references to neuropathic and neurodegenerative conditions in the Introduction were intended to justify the clinical relevance and translational motivation for standardizing RDD-HR methodology, rather than to imply that clinical validation was achieved within this study. To address this concern, we have revised the manuscript to explicitly delimit the scope of the work, clarifying that the primary objective was methodological optimization under controlled physiological conditions. Importantly, performing this optimization in healthy individuals is a necessary and methodologically sound first step. Establishing reliability, minimal stimulus requirements, frequency sensitivity, and train effects in the absence of pathological variability is essential before meaningful clinical validation can be undertaken. Without such baseline standardization, it would be difficult to determine whether observed differences in patient populations reflect true disease-related spinal disinhibition or are instead driven by protocol-dependent measurement noise. In response to the Reviewer’s comment, we have tempered the clinical narrative in the Introduction (lines 103–113) and Conclusions (lines 418–421) to avoid over-interpretation, expanded the Limitations paragraph (lines 386–407) on the Discussion to explicitly state that sensitivity, specificity, and diagnostic discrimination remain to be established in clinical populations, and clearly framed the proposed protocol as a foundational, feasibility-driven methodological framework intended to enable, and not replace, future clinical validation studies.

We also note that validation of this optimized protocol in patient populations is currently ongoing; however, no pilot clinical data were sufficiently complete to be included at this stage.

 

Comments 3: Another important concern relates to interpretative inconsistencies regarding the magnitude of Hoffmann reflex depression. The authors report maximal depression of approximately 30% in the lower limbs, which clearly differs from values commonly reported in the literature, where reductions often reach 60–90%. At the same time, statements appear indicating that stimulation at 1 Hz achieves approximately 90% of maximal depression, which may be misleading when considered alongside the numerical data presented. This issue likely arises from normalization to the first response and the use of median area under the curve rather than peak amplitude; however, these methodological implications are not explained with sufficient clarity. A more precise definition of “maximal depression” is required, along with a clear distinction between percentage reduction relative to H1 and the proportion of the asymptotic plateau reached.

Response 3: We thank the Reviewer for identifying this important issue regarding the interpretation of Hoffmann reflex depression magnitude. We agree that, in the original version, the distinction between absolute depression relative to the first response and proximity to the asymptotic plateau of the frequency–response curve was not sufficiently explicit and could lead to misinterpretation. In the revised manuscript, we have addressed this concern comprehensively.

First, we now provide a clear and explicit definition of H-reflex depression in the Methods (lines 196–197), specifying that reflex responses are quantified as the H-reflex area normalized to the first response (H/H1 × 100), with lower values indicating greater depression. This definition establishes a single, consistent reporting convention across the manuscript. Second, we have clarified the meaning of “maximum depression,” defining it as the asymptotic reduction relative to H1 derived from the fitted sigmoid frequency–response curves (lines 200–201). Correspondingly, references to “~90% of maximum depression at 1 Hz” have been revised to make clear that this refers to the proportion of the asymptotic plateau captured at that frequency, rather than a 90% reduction relative to H1. All such statements are now explicitly anchored to the fitted curves, and the Abstract, Results, tables, and figure legends have been revised accordingly.

Finally, we acknowledge that differences from some published reports describing larger percentage reductions (60–90%) likely reflect differences in reporting convention rather than true physiological discrepancies. The reported values in the present study (e.g., ~30% in the lower limbs) arise directly from the definition of depression used here. Under this definition, a value of ~30% corresponds to a ~70% reduction relative to H1 when expressed using the alternative formulation (100 − [H/H1 × 100]). By contrast, many reports describing 60–90% depression use this latter expression directly, reporting the percentage reduction from H1 rather than the percentage of H1 remaining.

 

Comments 4: A further limitation of the study is the absence of any assessment of measurement reliability. Although the authors focus on statistical precision through bootstrap procedures and confidence intervals, they provide no information on the repeatability of the measurements over time. There is no test–retest analysis, no intraclass correlation coefficients, and no evaluation of between-day variability. Given that the manuscript proposes a standardized clinical protocol, this omission represents a substantial weakness, as temporal stability is a fundamental requirement for any biomarker.

Response 4: We agree that assessment of temporal stability (e.g., test–retest reliability, intraclass correlation coefficients, and between-day variability) is a critical requirement for the clinical deployment of any biomarker. The present study was not designed a priori to evaluate those reliability metrics, as its primary objective was to establish a feasible and statistically robust protocol for RDD-HR acquisition in upper and lower limbs and parameter optimization under controlled physiological conditions. Accordingly, our analyses focused on within-session precision, using bootstrap procedures and confidence interval–based approaches to identify optimal stimulation frequencies and minimal stimulus requirements. In response to the Reviewer’s comment, we have expanded the Limitations paragraph (lines 386–407) to explicitly acknowledge the absence of formal reliability metrics and to clarify that temporal repeatability was beyond the scope of the current study. We have also added a corresponding statement outlining test–retest reliability, intraclass correlation analysis, and between-day variability as essential next steps and a central focus of future work.

 

Comments 5: Additionally, although the sample was carefully selected, it included participants across a relatively broad age range and of both sexes, without any analysis of the potential influence of these variables on the results. This is problematic because the authors themselves cite literature demonstrating that age and sex significantly modulate RDD-HR. The absence of stratified or even exploratory analyses limits the generalizability of the findings and should be more explicitly acknowledged as a study limitation.

Response 5: We thank the Reviewer for this pertinent observation regarding the potential influence of age and sex on RDD-HR measurements. We agree that both variables have been shown to modulate spinal excitability and RDD-HR in prior studies and therefore merit careful consideration. The present study was not designed a priori to evaluate age- or sex-related effects, nor was it powered to support stratified analyses or the inclusion of these variables as covariates in multivariable models. Accordingly, we deliberately avoided conducting post hoc or exploratory subgroup analyses, as these could yield spurious associations or misleading trends in the absence of appropriate study design and statistical power. In response to the Reviewer’s comment, we have expanded and clarified the Limitations paragraph (lines 386–407) to explicitly acknowledge that the lack of stratification by age and sex limits the generalizability of the findings. We now emphasize that future studies should be specifically designed to examine the effects of demographic and physiological factors—including age, sex, and physical activity—on RDD-HR measurements, using appropriately powered and stratified cohorts.

 

Comments 6: The conclusions regarding upper limb measurements also appear overly optimistic. While the authors convincingly demonstrate the technical feasibility of recording RDD-HR from the flexor carpi radialis muscle, the observed depression is clearly smaller and more variable than that recorded in the lower limbs. Nevertheless, upper and lower limb measurements are treated as functionally equivalent, without sufficient evidence that their diagnostic value is comparable. Greater interpretative caution would be warranted in this regard.

Response 6: In the revised manuscript, we have substantially tempered the interpretation of upper limb RDD-HR to address this concern. Specifically, we now explicitly acknowledge in the Discussion (lines 361–374) that upper limb measurements exhibit smaller maximal depression and greater variability than lower limb recordings. We clarify that, despite similar frequency–response behavior and comparable S₅₀ values, upper and lower limb RDD-HR should not be assumed to be diagnostically equivalent unless further tested in clinical populations. Correspondingly, the Conclusions have been revised to avoid treating upper and lower limb measurements as functionally interchangeable. Upper limb RDD-HR is now framed as technically feasible and practically advantageous in selected contexts, rather than as a substitute for lower limb assessment. We also explicitly state that establishing the comparative diagnostic value of upper versus lower limb RDD-HR requires future validation in clinical cohorts.

 

Comments 7: At the narrative level, the discussion at times resembles a review article rather than a focused analysis of the presented data. Considerable space is devoted to general GABAergic mechanisms and potential clinical applications that are not directly supported by the study’s results. At the same time, the study’s limitations, although mentioned, are not emphasized strongly enough, which weakens the critical balance of the manuscript.

Response 7: We thank the Reviewer for this constructive comment regarding the narrative balance of the Discussion. We agree that, in the original version, some sections placed disproportionate emphasis on broader clinical implications. In the revised manuscript, we have streamlined the Discussion to focus primarily on interpretation of the presented data, explicitly contextualizing our findings through direct comparison with prior methodological studies. We have also strengthened and expanded the Limitations paragraph (lines 386–407) to clearly delineate the scope of inference, emphasizing that the present work represents methodological optimization in healthy individuals rather than clinical validation.

 

Comments 8: In summary, the article represents a methodologically sound and potentially useful contribution to efforts aimed at simplifying RDD-HR protocols; however, in its current form, it overstates its clinical implications. The conclusions should be regarded as preliminary rather than definitive. With clearer definitions, a more restrained clinical narrative, and the inclusion of missing validation analyses, the manuscript could become a valuable foundation for future translational research.

Response 8: We reiterate our thanks to the Reviewer for the careful evaluation of our work, for the thoughtful and constructive critiques provided throughout the review process, and for the time devoted to improving the quality of the manuscript. We agree that the original version placed excessive emphasis on clinical implications and that the conclusions required more cautious framing. We have revised the manuscript to clarify definitions, restrain the clinical narrative, and explicitly frame the conclusions as preliminary and methodological rather than definitive. The Discussion and Conclusions now emphasize that the proposed protocol represents a foundation for future translational research, with clinical validation, reliability assessment, and diagnostic performance analyses clearly identified as essential next steps. The Limitations paragraph has been expanded accordingly to delineate the scope of inference and the boundaries of the present findings.

We hope that these revisions adequately address the Reviewer’s concerns and have enhanced the rigor, balance, and clarity of the manuscript.

Reviewer 2 Report

Comments and Suggestions for Authors

The manuscript is well-structured and addresses a relevant methodological issue in neurophysiology: the optimization and standardization of frequency-based assessment of Hoffmann reflex depression. The study is carefully designed and the experimental protocol is clearly and reproducibly described.

The abstract effectively summarizes the rationale, methods, key findings, and clinical implications. The study objectives are clearly defined and aligned with the analyses presented.

The introduction provides a solid overview of the physiological basis of the Hoffmann reflex and its relevance as a marker of spinal inhibitory function. The authors clearly justify the need to standardize the protocol and extend the assessment to the upper limbs, which represents a practical and clinically significant contribution.

The materials and methods section is a strength of the manuscript: participant selection, electrophysiological setup, stimulation protocols, and data analysis procedures are described in detail. The statistical approach is appropriate. Ethics approval and informed consent are stated.

The results are presented clearly and logically, supported by well-structured figures and tables.

The discussion adequately interprets the results in the context of the existing literature and highlights the practical implications of a simplified protocol of the reflex. Also, the authors carefully avoid overinterpretation and clearly acknowledge that the study was conducted only on healthy participants.

The main limitation of the manuscript lies in the relatively limited number of studies available in the literature, which limits broader contextualization. While this may reflect the state of the field rather than a weakness of the study itself, it would be helpful to more explicitly emphasize that the limited literature is due to the niche nature of reflex research and the lack of standardized protocols to date. 

Author Response

Comments 1: The manuscript is well-structured and addresses a relevant methodological issue in neurophysiology: the optimization and standardization of frequency-based assessment of Hoffmann reflex depression. The study is carefully designed and the experimental protocol is clearly and reproducibly described.

The abstract effectively summarizes the rationale, methods, key findings, and clinical implications. The study objectives are clearly defined and aligned with the analyses presented.

The introduction provides a solid overview of the physiological basis of the Hoffmann reflex and its relevance as a marker of spinal inhibitory function. The authors clearly justify the need to standardize the protocol and extend the assessment to the upper limbs, which represents a practical and clinically significant contribution.

The materials and methods section is a strength of the manuscript: participant selection, electrophysiological setup, stimulation protocols, and data analysis procedures are described in detail. The statistical approach is appropriate. Ethics approval and informed consent are stated.

The results are presented clearly and logically, supported by well-structured figures and tables.

The discussion adequately interprets the results in the context of the existing literature and highlights the practical implications of a simplified protocol of the reflex. Also, the authors carefully avoid overinterpretation and clearly acknowledge that the study was conducted only on healthy participants.

The main limitation of the manuscript lies in the relatively limited number of studies available in the literature, which limits broader contextualization. While this may reflect the state of the field rather than a weakness of the study itself, it would be helpful to more explicitly emphasize that the limited literature is due to the niche nature of reflex research and the lack of standardized protocols to date.

 

Response 1: We thank the Reviewer for the thorough evaluation of our manuscript and for the very positive assessment of its structure, methodological rigor, and clarity.

We agree with the Reviewer’s observation regarding the relatively limited number of available studies addressing RDD-HR, particularly in the context of standardized protocols and upper limb assessments. In response, we have revised the Discussion (lines 381–385) to more explicitly emphasize that the modest size of the existing literature reflects the niche nature of reflex-based assessments and the historical lack of standardized methodologies, as suggested. We now clarify that this gap in the literature further underscores the need for protocol optimization and standardization, which was a central motivation for the present work.

We believe this clarification improves the contextual framing of our findings and better situates the contribution of the study within the current state of the field. All corresponding changes are highlighted in red in the revised manuscript.

Reviewer 3 Report

Comments and Suggestions for Authors

This manuscript addresses an important methodological gap by proposing a simplified and standardized protocol for assessing RDD-HR in upper and lower limbs in healthy adults. The study is well designed, technically detailed, and statistically thoughtful, particularly in its use of sigmoid fitting and confidence interval–based determination of the minimal pulse number. The work has clear translational potential as a foundation for biomarker use in spinal inhibitory dysfunction, although claims about clinical utility should remain cautiously framed given the exclusively healthy sample and the stringent exclusion criteria.​

Major Comments:

1. The Abstract states that depression is greater in lower limbs (~70%) than upper limbs (~53%), whereas Table 1 and the Results text report maximum depression of approximately 30% in lower limbs and 44–51% in upper limbs. This discrepancy could confuse readers and affect the interpretation of limb-specific physiology.​
2. You define RDD-HR as the “median percentage reduction in reflex AUC relative to the first response,” but later refer to “maximum depression expressed as percentage of H1” and plot “HR amplitude expressed as percentage of H1.” Please state clearly whether you report: (a) percentage of H1 remaining (H/H1×100) or (b) percentage reduction from H1, and ensure that all text, figures, and table headings use the same convention. This will improve reproducibility and avoid misinterpretation of the magnitude of depression.​
3. You cite many conditions with altered RDD-HR (diabetes, obesity, SCI, ALS, stroke, PD, psychiatric disorders), but readers may not see a primary target application. Please state explicitly whether this protocol is intended first as a reference standard for metabolic neuropathies, central lesions, or as a generic normative template for multiple conditions. Then, align the Discussion and Conclusions with that emphasis while still acknowledging broader applicability.​
4. Clarify the statistical approach for determining the minimal number of stimuli and how you define “100% probability” of being within the 95% confidence interval. Please specify whether the reference CI (based on responses 2–10) was computed per participant and then summarized, or at the group level. Also, explain whether you required the “100% probability” criterion separately for each limb and frequency, or across pooled conditions. A brief note on whether you tested sensitivity to CI width (e.g., 90%) or to mean vs median would further support the robustness of the six-pulse recommendation.​
5. You note differences in maximum depression and S50 between upper and lower limbs and briefly suggest motor unit composition or functional demand as possible explanations. Please add a short paragraph that links these observations more concretely to known segmental circuitry (e.g., differences in Ia afferent input, presynaptic inhibition, or descending modulation) while clearly labeling these points as hypotheses. This will enhance the physiological interest of the work without overstating causality.​
6. Your sample excludes common conditions such as diabetes, hypertension, dyslipidemia, obesity (BMI > 30), and neurological disease, and includes adults aged 24–47 years with BMI 18.8–27.0 kg/m². Please add a brief section in the Discussion that acknowledges that these data represent an “optimally healthy” cohort and that future work must assess whether the same parameters and thresholds hold in older, more diverse, and comorbid populations. If available, indicate hand dominance and whether limb laterality was considered.​
7. You show that six pulses (responses 2–7) from a single train yield RDD-HR values statistically indistinguishable from longer and repeated trains at S50 and 1 Hz. Emphasize that this demonstrates equivalence rather than superiority and that the main advantage is reduced acquisition time and burden. This small wording adjustment will keep the claims appropriately conservative.​

Minor Comments:

1. The Conclusions specify “two key stimulation frequencies (1 Hz and 0.35 Hz for upper limbs or 0.6 Hz for lower limbs), a single train of seven stimuli, and feasibility of upper limb evaluations.” Please verify that these exact values and their derivation from S50 and ~90% depression at 1 Hz are clearly stated and consistent in the Abstract and Results.​
2. You highlight seated posture, lower current, and likely better tolerance, but you do not formally quantify feasibility or comfort. Consider either adding any available practical indicators (e.g., absence of aborted trials, shorter preparation time) or rephrasing to “practically advantageous and likely more comfortable, given lower stimulation intensities and seated positioning.”​
3. Figure 2: You state that upper limbs required significantly lower stimulation currents than lower limbs, with a mean difference of 4.4 ± 2.2 mA. Consider adding approximate mean values for upper and lower limbs in the text so readers can understand the scale without looking at the figure.​
4. Figure 3: Explicitly state in the legend that traces represent “mean normalized HR AUC across subjects, expressed as percentage of the first response (H1),” and that blue lines represent the 2–10 response median across three trains, while green lines represent the 2–7 response median from a single train.
5. Describe briefly whether and how you excluded trials with artifacts or signs of voluntary activation (e.g., predefined amplitude criteria or visual inspection) to reinforce that RDD-HR estimates are free of contamination.​
6. Ensure consistent use of “Hoffmann reflex (HR)” vs “H-reflex” and avoid switching between terms within the same section. Also, standardize use of “rate-dependent depression of the Hoffmann reflex (RDD-HR)” after first definition.​

Author Response

Comments 1: This manuscript addresses an important methodological gap by proposing a simplified and standardized protocol for assessing RDD-HR in upper and lower limbs in healthy adults. The study is well designed, technically detailed, and statistically thoughtful, particularly in its use of sigmoid fitting and confidence interval–based determination of the minimal pulse number. The work has clear translational potential as a foundation for biomarker use in spinal inhibitory dysfunction, although claims about clinical utility should remain cautiously framed given the exclusively healthy sample and the stringent exclusion criteria.​

Response 1: We thank the Reviewer for the careful evaluation of our manuscript and for the positive assessment of its methodological rigor and translational relevance. We acknowledge the Reviewer’s recommendation to maintain a cautious framing of clinical utility given the exclusively healthy sample and the exclusion criteria. In response, we have revised the manuscript to further clarify the methodological scope of the study and to appropriately restrain clinical claims. All modifications have been incorporated into the revised version and are highlighted in red.

 

Comments 2: The Abstract states that depression is greater in lower limbs (~70%) than upper limbs (~53%), whereas Table 1 and the Results text report maximum depression of approximately 30% in lower limbs and 44–51% in upper limbs. This discrepancy could confuse readers and affect the interpretation of limb-specific physiology.​

Response 2: We thank the Reviewer for pointing out this discrepancy in the Abstract. We agree that the originally reported values (~70% in lower limbs and ~53% in upper limbs) were inconsistent with the values presented in Table 1 and the Results section and could lead to confusion. This inconsistency arose from the use of two different but mathematically related expressions of Hoffmann reflex depression. In the original Abstract, depression was inadvertently reported as the percentage reduction relative to the first response (i.e., 100 − [H/H1 × 100]), whereas Table 1 and the Results consistently reported depression based on the normalized H-reflex value expressed as a percentage of the first response (H/H1 × 100), with lower values indicating greater depression. In the revised manuscript, we have corrected the Abstract (lines 30–31 and 36)  to ensure full consistency with the Methods, Results, tables, and figures. The Abstract now reports depression values using the same normalization convention applied throughout the manuscript (H/H1 × 100), resulting in values of approximately ~30% for the lower limbs and ~44–51% for the upper limbs. In addition, we have clarified the definition and interpretation of H-reflex depression in the Methods (lines 196–197) to prevent ambiguity and to ensure consistent interpretation across all sections.

 

Comments 3: You define RDD-HR as the “median percentage reduction in reflex AUC relative to the first response,” but later refer to “maximum depression expressed as percentage of H1” and plot “HR amplitude expressed as percentage of H1.” Please state clearly whether you report: (a) percentage of H1 remaining (H/H1×100) or (b) percentage reduction from H1, and ensure that all text, figures, and table headings use the same convention. This will improve reproducibility and avoid misinterpretation of the magnitude of depression.​

Response 3: We agree that, in the original version of the manuscript, the description of RDD-HR alternated between percentage reduction from the first response and percentage of the first response remaining, which could lead to ambiguity and misinterpretation. In the revised manuscript, we have addressed this concern by adopting a single, explicit reporting convention throughout. RDD-HR is now consistently reported as the H-reflex area normalized to the first response, expressed as a percentage of H1 (H/H1 × 100), with lower values indicating greater reflex depression. This definition is stated explicitly in the Methods (lines 196–197) and is used uniformly across the Abstract, Results, tables, and figures. We have revised all instances of “percentage reduction” language to align with this convention, clarified the interpretation of “maximum depression” as the asymptotic reduction relative to H1 derived from fitted sigmoid curves, and harmonized all figure legends, and table headings accordingly.

 

Comments 4: You cite many conditions with altered RDD-HR (diabetes, obesity, SCI, ALS, stroke, PD, psychiatric disorders), but readers may not see a primary target application. Please state explicitly whether this protocol is intended first as a reference standard for metabolic neuropathies, central lesions, or as a generic normative template for multiple conditions. Then, align the Discussion and Conclusions with that emphasis while still acknowledging broader applicability.​

Response 4: We agree that, in the original version, the discussion of multiple conditions associated with altered RDD-HR could give the impression of a disease-specific focus. In the revised manuscript, we have addressed this concern by clarifying throughout the Abstract, Discussion, Conclusions, and Limitations that the present study is methodological in nature and confined to healthy individuals. The protocol is now consistently framed as a standardized reference approach derived under controlled physiological conditions, rather than as a tool targeting any specific disease category at this stage. References to metabolic, neurological, and psychiatric conditions are retained solely to provide translational motivation and context for the need for standardization, not to define a primary target population. Accordingly, the Discussion and Conclusions have been aligned to emphasize that the proposed protocol is intended to serve as a foundational framework for subsequent condition-specific validation studies, while avoiding preferential emphasis on metabolic neuropathies, central lesions, or any single clinical group.

 

Comments 5: Clarify the statistical approach for determining the minimal number of stimuli and how you define “100% probability” of being within the 95% confidence interval. Please specify whether the reference CI (based on responses 2–10) was computed per participant and then summarized, or at the group level. Also, explain whether you required the “100% probability” criterion separately for each limb and frequency, or across pooled conditions. A brief note on whether you tested sensitivity to CI width (e.g., 90%) or to mean vs median would further support the robustness of the six-pulse recommendation.​

Response 5: We agree that a more explicit description improves transparency and reproducibility. As noted in the manuscript, our approach was adapted from a statistical method previously validated in transcranial magnetic stimulation studies (Cuypers et al., 2014). Briefly, the analysis was performed separately for each limb and each stimulation frequency. For each condition, the median H-reflex depression calculated from all available responses (reflexes 2–10) was defined as the reference value. Bootstrap resampling was then applied to this full-response dataset to generate a 95% confidence interval (CI) around the reference median. Subsequently, reduced reflex subsets were analyzed sequentially. Specifically, subsets included only the 2nd response alone, the median of responses 2–3, 2–4, and so on, up to the median of responses 2–10. For each subset, we evaluated whether the resulting estimate fell within the predefined 95% CI of the reference value. A binary outcome was assigned (1 = within CI; 0 = outside CI). The “100% probability” criterion was defined as the minimum number of stimuli for which the reduced-subset estimate fell within the reference CI for all participants, across all limbs and all stimulation frequencies. Thus, the criterion was intentionally conservative and required consistency across all experimental conditions rather than being satisfied for pooled or averaged data only.

To assess robustness, we repeated the full procedure using the mean instead of the median as the reference statistic. The resulting minimum stimulus number was unchanged, indicating that the recommendation was not sensitive to the choice of central tendency. For clarity and simplicity, only the median-based results were reported in the manuscript.

We have revised the Methods section (lines 208–218) to improve the clarity of these points, including how the confidence intervals were constructed, how the binary probability criterion was defined, and how the requirement was applied across limbs and frequencies.

 

Comments 6: You note differences in maximum depression and S50 between upper and lower limbs and briefly suggest motor unit composition or functional demand as possible explanations. Please add a short paragraph that links these observations more concretely to known segmental circuitry (e.g., differences in Ia afferent input, presynaptic inhibition, or descending modulation) while clearly labeling these points as hypotheses. This will enhance the physiological interest of the work without overstating causality.​

Response 6: We agree that the observed differences in maximum depression and S50 between upper and lower limbs warrant a more explicit but cautious discussion of potential underlying mechanisms. In the revised manuscript, we have added a short hypothesis-driven paragraph to the Discussion (lines 307–327) that links these limb-specific differences to known features of segmental spinal circuitry. Specifically, we discuss possible contributions of differences in Ia afferent input, presynaptic inhibitory control, and descending modulation between cervical and lumbosacral segments, while explicitly emphasizing that these interpretations are speculative and not directly tested in the present study.

 

Comments 7: Your sample excludes common conditions such as diabetes, hypertension, dyslipidemia, obesity (BMI > 30), and neurological disease, and includes adults aged 24–47 years with BMI 18.8–27.0 kg/m². Please add a brief section in the Discussion that acknowledges that these data represent an “optimally healthy” cohort and that future work must assess whether the same parameters and thresholds hold in older, more diverse, and comorbid populations. If available, indicate hand dominance and whether limb laterality was considered.​

Response 7: We agree that the present cohort represents an optimally healthy population, selected intentionally to minimize physiological and pathological confounders during protocol optimization. In response, we have expanded the Limitations paragraph (lines 386–407) of the Discussion to explicitly acknowledge that the findings were derived from a narrowly defined, healthy adult cohort and that future studies will be required to determine whether the same stimulation parameters, thresholds, and reliability metrics generalize to older individuals, more diverse populations, and patients with metabolic, cardiovascular, or neurological comorbidities.

We have also clarified in the Limitations that hand dominance and limb laterality were not explicitly assessed or controlled for in the present study, and therefore their potential influence on RDD-HR measurements could not be evaluated. This aspect has now been identified as an additional limitation and an important consideration for future investigations.

 

Comments 8: You show that six pulses (responses 2–7) from a single train yield RDD-HR values statistically indistinguishable from longer and repeated trains at S50 and 1 Hz. Emphasize that this demonstrates equivalence rather than superiority and that the main advantage is reduced acquisition time and burden. This small wording adjustment will keep the claims appropriately conservative.​

Response 8: In the revised manuscript, we have adjusted the wording in the Results and Discussion to explicitly state that the abbreviated protocol yields RDD-HR estimates statistically indistinguishable from those obtained with longer and repeated stimulation schemes. We now emphasize that the primary advantage of this approach is reduced acquisition time and procedural burden, rather than improved measurement performance.

 

Comments 9: The Conclusions specify “two key stimulation frequencies (1 Hz and 0.35 Hz for upper limbs or 0.6 Hz for lower limbs), a single train of seven stimuli, and feasibility of upper limb evaluations.” Please verify that these exact values and their derivation from S50 and ~90% depression at 1 Hz are clearly stated and consistent in the Abstract and Results.​

Response 9: In the revised version, we have verified and harmonized the presentation of these values in the Abstract, Results, and Conclusions. Specifically, we now state consistently that 1 Hz was selected as the primary stimulation frequency because it captures approximately 90% of the asymptotic RDD-HR depression based on the fitted frequency–response curves, and the secondary frequencies (~0.35 Hz for upper limbs and ~0.6 Hz for lower limbs) correspond to the S50 values derived from the sigmoidal fits. The derivation of these frequencies from the fitted curves is explicitly described in the Results, and the same values and terminology are used in the Abstract and Conclusions.

 

Comments 10: You highlight seated posture, lower current, and likely better tolerance, but you do not formally quantify feasibility or comfort. Consider either adding any available practical indicators (e.g., absence of aborted trials, shorter preparation time) or rephrasing to “practically advantageous and likely more comfortable, given lower stimulation intensities and seated positioning.”​

Response 10: In the revised manuscript, we have edited the wording in the Discussion and Conclusions to avoid implying formally assessed comfort outcomes. Descriptions of upper limb testing now emphasize that it is practically advantageous and likely more comfortable, based on objective procedural features such as lower stimulation intensities and seated positioning, rather than on quantified comfort measures. In addition, we have expanded the Limitations paragraph (lines 386–407) to explicitly acknowledge that discomfort, pain, and feasibility metrics were not systematically assessed and should be incorporated into future studies.

 

Comments 11: Figure 2: You state that upper limbs required significantly lower stimulation currents than lower limbs, with a mean difference of 4.4 ± 2.2 mA. Consider adding approximate mean values for upper and lower limbs in the text so readers can understand the scale without looking at the figure.​

Response 11: In the revised manuscript, we have added the mean stimulation current values for upper and lower limbs directly in the Results text when describing Figure 2 (lines 234–235), alongside the reported mean difference.

 

Comments 12: Figure 3: Explicitly state in the legend that traces represent “mean normalized HR AUC across subjects, expressed as percentage of the first response (H1),” and that blue lines represent the 2–10 response median across three trains, while green lines represent the 2–7 response median from a single train.

Response 12: We thank the Reviewer for this helpful suggestion. We have edited the legend of Figure 3 to clearly specify that the traces represent the mean normalized H-reflex area under the curve (AUC) across subjects, expressed as a percentage of the first response (H1). We now also explicitly indicate that blue traces correspond to the median of responses 2–10 averaged across three stimulus trains, whereas green traces correspond to the median of responses 2–7 derived from a single stimulus train.

 

Comments 14: Describe briefly whether and how you excluded trials with artifacts or signs of voluntary activation (e.g., predefined amplitude criteria or visual inspection) to reinforce that RDD-HR estimates are free of contamination.​

Response 14: We thank the Reviewer for this important comment regarding potential signal contamination by artifacts or voluntary activation. In the present work, no trials were excluded post hoc on the basis of artifacts or voluntary activation, as one of the explicit aims was to test the robustness of the proposed simplified protocol under realistic acquisition conditions, including the comparison of a single stimulus train versus the average of three trains despite the possibility of occasional signal variability. This approach allowed us to evaluate whether a single-train protocol yields RDD-HR estimates equivalent to those obtained by averaging multiple trains in practice, which may reduce the influence of occasional signal variability or artifacts.

Voluntary activation artifacts were controlled procedurally rather than by trial rejection, by carefully standardizing limb positioning, providing clear instructions for participants to remain fully relaxed, and continuously monitoring posture and muscle relaxation throughout the recording. These procedures are consistent with standard H-reflex acquisition practices and were applied uniformly across all participants and conditions.

We have now added a clarifying statement to the Methods section (lines 156–161) explicitly noting that no trials were excluded based on artifact criteria and describing how voluntary activation was minimized during data acquisition.

 

Comments 15: Ensure consistent use of “Hoffmann reflex (HR)” vs “H-reflex” and avoid switching between terms within the same section. Also, standardize use of “rate-dependent depression of the Hoffmann reflex (RDD-HR)” after first definition.​

Response 15: We have standardized terminology throughout. After the first definition of Hoffmann reflex, we now consistently use the term “H-reflex” when referring to the reflex itself and avoid the abbreviation “HR.” Similarly, after its initial definition, we use “rate-dependent depression of the Hoffmann reflex (RDD-HR)” consistently across all sections, figures, tables, and legends. All instances of inconsistent or abbreviated usage have been corrected accordingly.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

I accept the article