Identifying Early Responders to Dry Needling for Lower-Limb Spasticity in Multiple Sclerosis: A Secondary Responder Analysis of a Pilot Randomized Controlled Trial

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The authors are presenting a secondary responder analysis of dry-needeling in patients with lower limb spasticity due to multiple sclerosis. The method of dry needeling is not yet very well in neurorehabilitation, so this manuscript is relevant and interesting, but it needs to be improved:

Major revisions:

1. The severity of the patients' clinical picture must be described in greater detail. It would be desirable to specify the EDSS and either the FIM or the Barthel Index. The patients in the intervention group and the sham group should be similarly affected.

 

2. It is absolutely necessary to mention the anti-spasticity medication of the patients in detail! Furthermore it is necessary, that medication changes during the therapy period are described in detail. Antispastic drugs like baclofen or tizanidine are highly effectiv in ms and naturally influence the study results. Maybe the medication can be mentioned i a table.

3. A main point is, that multiple sclerosis is neither a neuromuscular nor a musculoskeletal disorder!! The topic is newsworthy, but in my opinion it does not fit into this special issue at all. I suggest submitting the manuscript in revised form to a more suitable special issue, for example one that deals with neurorehabilitation in general or with multiple sclerosis or demyelinating CNS diseases.

Author Response

Dear Reviewer,

Thank you very much for your valuable recommendations. We address each of your comments individually below.

Recommendation 1: The severity of the patients' clinical picture must be described in greater detail. It would be desirable to specify the EDSS and either the FIM or the Barthel Index. The patients in the intervention group and the sham group should be similarly affected

Response 1: We agree that an accurate description of baseline disability is essential. Disability severity was characterized using the EDSS total score and pyramidal subscore, together with validated functional mobility outcomes (TUG, T25FW, MSWS-12), which are widely used in ambulatory MS populations. Functional Independence Measure or Barthel Index were not included, as these instruments are less sensitive in ambulatory patients with moderate disability and gait-related impairment. Baseline characteristics were comparable between groups (Table 1).

Recommendation 2: It is absolutely necessary to mention the anti-spasticity medication of the patients in detail! Furthermore it is necessary, that medication changes during the therapy period are described in detail. Antispastic drugs like baclofen or tizanidine are highly effectiv in ms and naturally influence the study results. Maybe the medication can be mentioned i a table.

Response 2: We fully agree with the reviewer. Antispastic medication was recorded for all participants at baseline, and no changes in antispastic treatment (including baclofen) occurred during the study period, as per the inclusion criteria. This information has now been added to the Methods section to improve transparency.

Recommendation 3: A main point is, that multiple sclerosis is neither a neuromuscular nor a musculoskeletal disorder!! The topic is newsworthy, but in my opinion it does not fit into this special issue at all. I suggest submitting the manuscript in revised form to a more suitable special issue, for example one that deals with neurorehabilitation in general or with multiple sclerosis or demyelinating CNS diseases.

Response 3: We appreciate this important observation. While multiple sclerosis is a central nervous system disorder, dry needling targets peripheral neuromuscular structures and their interaction with central motor control. The present work is therefore framed within neurorehabilitation, focusing on the modulation of spasticity-related neuromuscular dysfunction in MS. We believe this perspective aligns with the scope of the Special Issue; however, we are open to editorial guidance regarding suitability.

Best wishes,

 

 

Reviewer 2 Report

Comments and Suggestions for Authors

The study titled “Identifying Early Responders to Dry Needling for Lower-Limb Spasticity in Multiple Sclerosis: A Secondary Responder Analysis of a Pilot Randomized Controlled Trial” aims to explore which people with multiple sclerosis (MS) show early clinically meaningful benefit after a single dry needling session for lower-limb spasticity and which baseline factors may predict this response.

my comments:

• The abstract overstates the clinical relevance of findings for a very small, underpowered sample
• The introduction provides a thorough rationale for responder analyses and heterogeneity in MS but risks overselling responder-based methods as a solution to variability without equally stressing the dangers of post hoc subgrouping
• The design is a secondary responder analysis of a small, single-center pilot RCT (n = 18), yet the Methods section reads as if it were adequately powered for responder detection; the limitations of sample size and post hoc power should be flagged more prominently
• The discussion leans strongly toward a positive, clinically meaningful interpretation despite non-significant group differences, broad CIs, and highly exploratory design; this optimism should be tempered and the possibility of false-positive patterns openly acknowledged
• Comparisons with responder rates from botulinum toxin or other interventions (30–50%) may unintentionally suggest equivalence of effect sizes, which is not supported given the minimal dose (single muscle, single session) and tiny sample

 

Author Response

Dear Reviewer,

Thank you very much for your valuable recommendations. We address each of your comments individually below.

Comment 1: The abstract overstates the clinical relevance of findings for a very small, underpowered sample

Response 1: We agree with the reviewer and appreciate this important observation. The abstract has been revised to temper the clinical interpretation of the findings and to clearly emphasize the exploratory and hypothesis-generating nature of the study. Statements suggesting clinical relevance have been rephrased to avoid overinterpretation, and the limitations related to the small, underpowered sample are now explicitly acknowledged.

Comment 2: The introduction provides a thorough rationale for responder analyses and heterogeneity in MS but risks overselling responder-based methods as a solution to variability without equally stressing the dangers of post hoc subgrouping

Response 2: We thank the reviewer for this insightful comment. The Introduction has been revised to provide a more balanced perspective on responder-based analyses. Specifically, we now explicitly acknowledge the methodological risks associated with post hoc subgrouping, including the potential for false-positive findings and reduced generalizability, particularly in small samples. The text has been adjusted to frame responder analyses as an exploratory tool rather than a definitive solution to clinical heterogeneity.

Comment 3: The design is a secondary responder analysis of a small, single-center pilot RCT (n = 18), yet the Methods section reads as if it were adequately powered for responder detection; the limitations of sample size and post hoc power should be flagged more prominently

Response 3: We fully agree with this concern. The Methods section has been revised to explicitly state that this work represents a secondary responder analysis of a pilot randomized controlled trial that was not designed or powered to detect responder profiles or predictors of response. Additional clarification has been added to emphasize that all analyses are exploratory, and that post hoc power considerations are provided only for contextual interpretation rather than inferential purposes.

Comment 4: The discussion leans strongly toward a positive, clinically meaningful interpretation despite non-significant group differences, broad CIs, and highly exploratory design; this optimism should be tempered and the possibility of false-positive patterns openly acknowledged

Response 4: We appreciate this important point and have revised the Discussion accordingly. Interpretive language has been softened throughout to avoid overstating clinical significance. We now more explicitly acknowledge the presence of non-significant group differences, wide confidence intervals, and the exploratory nature of the analyses. In addition, the possibility of false-positive response patterns inherent to small-sample exploratory analyses is now clearly discussed as a key limitation.

Comment 5: Comparisons with responder rates from botulinum toxin or other interventions (30–50%) may unintentionally suggest equivalence of effect sizes, which is not supported given the minimal dose (single muscle, single session) and tiny sample

Response 5: We thank the reviewer for highlighting this potential source of misinterpretation. The Discussion has been revised to clarify that comparisons with responder rates reported for other interventions, such as botulinum toxin, are intended solely for contextualization and not to imply equivalence of effect sizes or clinical efficacy. We now explicitly note the fundamental differences in intervention dose, treatment scope, and study design, and emphasize that such comparisons should be interpreted with caution.

 

Reviewer 3 Report

Comments and Suggestions for Authors

 Dear Editor,

Thank you very much for your invitation to review the manuscript entitled “Identifying Early Responders to Dry Needling for Lower-Limb Spasticity in Multiple Sclerosis: A Secondary Responder Analysis of a Pilot Randomized Controlled Trial.”

This study presents a secondary responder analysis of a pilot randomized controlled trial investigating dry needling for lower-limb spasticity in people with multiple sclerosis. It makes a meaningful contribution to the growing literature on personalized rehabilitation approaches, which are increasingly important in heterogeneous conditions such as MS. In particular, the identification of early responders provides valuable insight for clinical decision-making in a diverse MS population.

The study is methodologically well designed, and the use of blinding and a sham-controlled approach represents a major strength. However, given the limited sample size and the responder definitions used, the findings should be more clearly emphasized as exploratory in nature.

My comments and suggestions to improve the manuscript are outlined below.

Title and Abstract
The title and abstract are appropriately written.
In the abstract, it is not necessary to specify the names of the statistical tests.
As EDSS is mentioned only once, it may not be necessary to provide its abbreviation.
Keywords could be revised using MeSH terms.

Introduction
The introduction is well written and provides appropriate background information, as well as clearly stating the study aim and hypothesis.

Methods
A power analysis related to sample size could be provided.
Please further detail the intervention procedures and outcome assessments (particularly those beginning at line 142) to improve clarity for readers.

Regarding the sensitivity and clinical relevance of the responder definition, the criterion of defining a “global responder” as meeting ≥1 outcome threshold is highly sensitive but has low specificity. This approach is debatable, particularly because some individuals in the sham group showed improvement in the T25FW yet were not classified as responders, and because meeting a single patient-reported outcome (MSQOL-54) alone was sufficient to define response.

Was dry needling applied only to the gastrocnemius muscle, and was this muscle selected as the one with the highest spasticity? Please clarify this point in more detail.

The application of dry needling to only the gastrocnemius medialis and the use of a single treatment session may be limiting for a multifactorial condition such as spasticity, potentially reducing the generalizability of the findings.

In the Discussion, the “test-dose” approach is well explained; however, the rationale for excluding multi-muscle or multi-session protocols and the differences from routine clinical practice could be more explicitly addressed.

I also note the lack of objective spasticity measures. While the use of the EDSS pyramidal subscore is understandable, direct spasticity assessments such as the Modified Ashworth Scale, EMG, or reflex-based measures were not included. This limitation should be more strongly emphasized.

Including an image of the intervention procedure could improve the clarity and interpretability of the methods.

In the CONSORT flow diagram, the number of participants “assessed for eligibility” could be reported more clearly.

Results
For results with p > 0.05, terms such as “trend” or “moderate correlation” may appear overly optimistic. In particular, interpretations of findings such as r = 0.52 with p = 0.150 should be more cautious.

In Table 1, EDSS total is reported as “Median ± SD,” which is not appropriate; it should be reported as either Mean ± SD or Median [IQR].
Additionally, the unit for disease duration (years or months) should be specified in Table 1.

For Figure 2, it may be helpful to note that interpretation is limited due to the small sample size.

Discussion
In this section, I recommend avoiding the use of p-values and focusing instead on comparing the study’s findings with results from previous literature.
Please avoid definitive or conclusive statements and maintain a cautious interpretive tone appropriate for an exploratory analysis.

There are also some minor typographical errors in the text that should be corrected (e.g., “improvement ≥10% intime,” “global responder ” with extra spacing).

Overall, this is a scientifically sound and original study that fits well within the scope of the journal. Addressing the points above—particularly those related to responder definition, statistical interpretation, and methodological limitations—would further strengthen the manuscript.

I congratulate the authors on their work.

 

Author Response

Dear Reviewer,

Thank you very much for your valuable recommendations. We address each of your comments individually below.

Comment 1: In the abstract, it is not necessary to specify the names of the statistical tests. EDSS abbreviation may not be necessary. Keywords could be revised using MeSH terms.

Response 1: We agree with the reviewer. The names of statistical tests have been removed from the abstract, and the abbreviation for EDSS has been avoided where it was not strictly necessary. The keywords have been revised to better align with MeSH terminology.

Comment 2: The introduction is well written and appropriate.

Response 2: We thank the reviewer for this positive assessment. No changes were made to this section.

Comment 3: A power analysis related to sample size could be provided.

Response 3: We agree and have clarified this point in the Methods section. Given the pilot nature of the parent trial, the study was not designed to be adequately powered to detect responder differences or predictors of response. A post-hoc power analysis has been retained and is now explicitly framed as contextual information rather than as evidence of adequacy.

Comment 4: Please further detail the intervention procedures and outcome assessments.

Response 4: We have expanded the description of the intervention procedures and outcome assessments to improve clarity and reproducibility, particularly regarding the timing, application, and assessment sequence.

Comment 5: The definition of “global responder” as meeting ≥1 criterion is highly sensitive but has low specificity and is debatable. This approach is debatable, particularly because some individuals in the sham group showed improvement in the T25FW yet were not classified as responders, and because meeting a single patient-reported outcome (MSQOL-54) alone was sufficient to define response.

Response 5: We appreciate this important observation. The rationale for prioritizing sensitivity over specificity has now been more clearly articulated in the Methods section. We explicitly acknowledge that defining response based on ≥1 criterion may increase the risk of false-positive classification, particularly in small samples. This approach was intentionally selected to detect early response signals in an exploratory, hypothesis-generating context, and this limitation is now emphasized more clearly in both the Methods and Discussion sections.

Comment 6: Was dry needling applied only to the gastrocnemius muscle, and was this muscle selected as the one with the highest spasticity? Please clarify this point in more detail.

Response 6: Yes, dry needling was applied exclusively to the gastrocnemius medialis. This muscle was selected based on its frequent involvement in lower-limb spasticity in MS and its relevance for gait-related impairment. We have clarified this rationale in the Methods section.

Comment 7: The application of dry needling to only the gastrocnemius medialis and the use of a single treatment session may be limiting for a multifactorial condition such as spasticity, potentially reducing the generalizability of the findings.

Response 7: We agree and have strengthened the discussion of this limitation. The single-muscle, single-session approach was deliberately chosen as a “test-dose” strategy to explore early responsiveness while minimizing intervention burden in a pilot context. We now more explicitly acknowledge that this approach differs from routine clinical practice and may limit generalizability.

Comment 8: I also note the lack of objective spasticity measures. While the use of the EDSS pyramidal subscore is understandable, direct spasticity assessments such as the Modified Ashworth Scale, EMG, or reflex-based measures were not included. This limitation should be more strongly emphasized.

Response 8: We fully agree. While the EDSS pyramidal subscore provides a clinically meaningful estimate of spasticity-related impairment in MS, the absence of direct spasticity measures (e.g., Modified Ashworth Scale, EMG, or reflex-based assessments) limits mechanistic interpretation. This limitation has now been more explicitly highlighted in the Discussion.

Comment 9: Including an image of the intervention procedure could improve the clarity and interpretability of the methods.

Response 9: We agree that a visual representation may improve interpretability and have added an image illustrating the dry needling procedure to the Methods section.

Comment 10: In the CONSORT flow diagram, the number of participants “assessed for eligibility” could be reported more clearly.

Response 10: We have revised the CONSORT flow diagram to clearly indicate the number of participants assessed for eligibility and reasons for exclusion.

Comment 11: Results
For results with p > 0.05, terms such as “trend” or “moderate correlation” may appear overly optimistic. In particular, interpretations of findings such as r = 0.52 with p = 0.150 should be more cautious.

Response 11: We agree and have revised the Results section to adopt a more cautious tone. Descriptive language implying strength of association has been tempered, and interpretations of non-significant findings are now explicitly framed as exploratory and limited by sample size. For Figure 2, we have added a note indicating that interpretation is constrained by the small sample.

Comment 12: In Table 1, EDSS total is reported as “Median ± SD,” which is not appropriate; it should be reported as either Mean ± SD or Median [IQR].
Additionally, the unit for disease duration (years or months) should be specified in Table 1.

Response 12: Done. Thanks

Comment 13: For Figure 2, it may be helpful to note that interpretation is limited due to the small sample size.

Response 13: Done

Comment 14: Discussion
In this section, I recommend avoiding the use of p-values and focusing instead on comparing the study’s findings with results from previous literature.
Please avoid definitive or conclusive statements and maintain a cautious interpretive tone appropriate for an exploratory analysis.

Response 14: We agree and have revised the Discussion to focus on qualitative comparison with existing literature rather than on p-values. Interpretations have been further tempered to reflect the exploratory nature of the analysis, and definitive or conclusive statements have been avoided.

Comment 15: There are also some minor typographical errors in the text that should be corrected (e.g., “improvement ≥10% intime,” “global responder ” with extra spacing).

Response 15: Done

We thank the reviewer for the thoughtful and constructive feedback, which has substantially improved the clarity, rigor, and transparency of the manuscript. We believe that the revisions made in response to these comments have strengthened the work and better aligned it with the exploratory aims of the study.

 

 

 

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The quality of this manuscript improved after revision, but I still don't think it's appropriate for this special issuebut I still don't think it's appropriate for this special issue. It should be submitted to the general section of this jounral in my opinion. 

Reviewer 2 Report

Comments and Suggestions for Authors

The authors now explicitly state what I suggested before: this is an "underpowered pilot analysis."

I think that authors had this data and are trying to publish them. But sadly, not all data can and should be published. 

If this research is "underpowered pilot analysis", I suggest to conduct a future research with adequate power and then report the results.