Intraoperative Electromyographic Evaluation of Brachial Plexus Decompression During the Roos Surgical Procedure for Thoracic Outlet Syndrome

Round 1

Reviewer 1 Report (New Reviewer)

Comments and Suggestions for Authors

Congratulations on the study. The report of this technique is interesting.

I would recommend addressing the following points:

In cases of thoracic outlet syndrome without neurogenic involvement, or when neurogenic involvement is not corroborated by electromyography, intraoperative EMG cannot be used as a measure of the effectiveness of “decompression.” This issue should be corrected in the manuscript.

In the Methods section, the neuromonitoring protocol applied to each patient should be clearly described. It is necessary to specify whether this protocol was homogeneous and predefined across all cases.

Minor revision:

The stimulus should be reported either in volts (V) or milliamperes (mA). Please revise the text accordingly (e.g., line 120).

Finally, categorical or definitive statements should be modified, as no comparative study was performed.

Comments on the Quality of English Language

Typographical errors and some excessively long sentences with terminological inconsistency.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report (New Reviewer)

Comments and Suggestions for Authors

Thank you for the possibility to review the manuscript titled: “Intraoperative Electromyographic Evaluation of Brachial Plexus Decompression During the Roos Surgical Procedure for Thoracic Outlet Syndrome”. The study represents retrospective single center research. This is an interesting study of a rare entity and I believe this should be underlined in the article. There are a few minor recommendations:

-“Gender” is a psychological term, please change it to “sex” which is a biological term

-“Cervical ribs tend to occur in approximately 0.5 to 1% of the population. “ I believe this should be mentioned in the article as this is a rare developmental variation.

-Please indicate if patients had unilateral cervical ribs or bilateral cervical ribs.

-The discussion section could be improved with a classification of cervical ribs. It is also possible to add an analysis of the available data in the research section.

There are four types of cervical ribs:

• Type 1: Complete rib that articulates with the first rib or manubrium
• Type 2: Incomplete rib with a free distal tip
• Type 3: Incomplete rib with a distal fibrous band attachment
• Type 4: Short piece of bone extending beyond the C7 transverse process

-Conclusion section should not contain references. Please move reference 32 to the discussion section

Overall, this is an interesting study. The small number of cases can be supported by the fact that this is a rare developmental variation.

Please take into account the recommendations in the spirit of improving the quality of the submission

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 3 Report (New Reviewer)

Comments and Suggestions for Authors

This manuscript presents the first intraoperative electromyographic documentation of brachial plexus decompression during staged thoracic outlet syndrome surgery, which is a genuinely novel contribution. I think with some methodological clarifications and more careful interpretation of your findings, this could make a valuable addition to the literature.

The main structural issue I noticed is a mismatch between your described protocol and what appears in your analysis. You describe a five-stage measurement protocol: resting preoperative neutral, position at 90 degrees, after anterior scalenectomy at 90 degrees, after first rib resection at 90 degrees, and resting postoperative neutral (lines 163-164). This sequential approach is central to your stated aim of assessing decompression "throughout the sequential stages of the Roos procedure" (lines 30-31). However, your tables and statistical models appear to analyze only three timepoints: initial neutral, post-scalenectomy, and final neutral. The 90 degree measurements before and after rib resection don't appear in your results. Without these intermediate stages, it's difficult to separate positioning effects from decompression effects, which limits your ability to claim you've assessed sequential staged decompression. I'd suggest either presenting and analyzing all five stages as described, or revising your aims and methods to accurately reflect what you actually analyzed. If only three stages were captured reliably, that's fine, but the description of the protocol should match the analyzed dataset.

Regarding study design, you describe this as retrospective (line 98) but mention that patients "were enrolled" (line 33), which usually implies prospective recruitment. This may just be a wording issue, but I'd recommend clarifying whether EMG monitoring was performed as protocolized routine care on consecutive surgical patients or was selectively applied, and whether any analyses were pre-specified versus decided post hoc. Then make sure the language is consistent throughout the manuscript.

More substantively, I think your conclusions need to be aligned more carefully with what your study design can actually demonstrate. Every patient received the same surgical intervention, so without a comparison group receiving scalenectomy alone or a different approach, you can show that decompression occurs with the complete Roos procedure, but not that first rib resection is necessary or superior to alternatives. Lines 366-374 claim to demonstrate the "pivotal role" of first rib resection and "reinforce the established superiority" of this approach, but a single-arm study can show that a technique works without proving it works better than alternatives. I'd suggest reframing these claims throughout the manuscript to better match your study design.

For the statistical analysis, I'd recommend addressing a few things. You performed multiple comparisons (five muscles, three timepoint contrasts each) without discussing multiple testing. I understand strict Bonferroni correction can be overly conservative, but consider either declaring a primary endpoint and contrast (for example, ADM muscle 1 comparing final neutral to post-scalenectomy) with other muscles treated as secondary or exploratory, or providing adjusted p-values using false discovery rate methods as a sensitivity analysis. Several of your p-values are just below 0.05, and it would strengthen your findings to show they hold up with appropriate correction.

Your sample sizes vary from 26 to 34 across timepoints without explanation. Could you explain why electrodes weren't placed on all patients at all timepoints, and what assumptions you're making about the missing data mechanism? For mixed linear models, whether data are missing at random, missing completely at random, or missing not at random affects the validity of your estimates.

I would also recommend reporting 95 percent confidence intervals rather than just standard errors in Table 4. Since your beta coefficients are on the log scale, consider exponentiating them and reporting as percent changes or geometric mean ratios for easier clinical interpretation. For example, instead of beta equals 0.570, you could say deltoid EMG increased by X percent from initial to final position.

That said, I want to clarify what I mean by clinical interpretation. Intraoperative EMG amplitude isn't the same as functional outcome. You can certainly interpret the physiologic meaning of these changes, but connecting them directly to patient function would require correlation with postoperative symptom resolution, strength measurements, or patient-reported outcomes. If you have any such data, it would strengthen the manuscript to include it. If not, I'd suggest acknowledging explicitly that correlation between intraoperative EMG improvement and clinical outcomes remains to be established.

One finding that I think deserves more discussion is the abductor digiti minimi at recording site 1, which shows beta equals negative 0.431 with p equals 0.056 after anterior scalenectomy compared to baseline. This is a trend toward worsening after scalenectomy alone. You mention this briefly (lines 202-203, 361-363) but I think it's actually one of your more interesting findings. It doesn't contradict the idea that complete decompression is necessary. If anything, it could support that argument by suggesting scalenectomy alone may transiently worsen compression of certain nerve elements, possibly because dividing the anterior scalene increases traction on the inferior trunk when the arm is elevated and the first rib is still present. It does contradict your repeated statement that there's "no significant difference" or "no change" after scalenectomy, so I'd suggest discussing this finding more prominently and exploring its potential physiologic meaning.

Your patient population includes subgroups that could confound your results and should be analyzed separately. Six patients (17.6%) were reoperations with prior surgery elsewhere. These patients have altered anatomy from adhesions and previous dissection, so their baseline EMG values and response to decompression likely differ systematically from primary cases. Six patients (17.6%) had Double Crush Phenomenon with two compression sites. Their EMG improvements may not solely reflect thoracic outlet decompression. You also pooled neurogenic, vascular, arterial, and combined TOS types without subgroup analysis. These may respond differently to surgical stages. Perform sensitivity analyses excluding reoperation and double crush patients, or analyze them as separate subgroups.

For the methodology section, a few additional details would help with reproducibility. When exactly were measurements taken after each surgical step? Immediately after completing the maneuver, after achieving hemostasis, or after a standardized waiting period? How did you ensure identical patient positioning at each stage? How did you confirm complete reversal of neuromuscular blockade from intubation? You mention cortical stimulation and somatosensory evoked potential monitoring in your methods (lines 110-113) but don't report any results, so I'd suggest either explaining how these were used or removing them from the methods. It would also be helpful to include basic neurophysiology parameters like amplifier gain, filter settings, impedance values, and quality checks.

Regarding trapezius muscle: this is innervated by the spinal accessory nerve (cranial nerve XI), not the brachial plexus, so its inclusion in a brachial plexus decompression study seems odd. However, there could be value in using it as a negative control or internal reference to detect global anesthetic effects, equipment drift, or technical artifacts that would affect all recordings rather than just plexus-innervated muscles. If this was your rationale, state it explicitly and interpret the trapezius results in that context. If you cannot justify its inclusion, remove it from the analysis.

The abstract states that statistical analysis was performed "in accordance to established analytical principles" (lines 37-38). This is uninformative and unsuitable for an abstract. Specify the actual methods used, such as "Mixed linear models with log-transformed data were used to compare muscle EMG values across surgical stages, with statistical significance at p less than 0.05."

Lines 54-56 describe scalene muscles as "critical anatomical structures," but your surgical technique involves complete removal of the anterior scalene. Consider either removing scalene muscles from this list or clarifying that you mean critical in the sense that their pathologic role necessitates removal, unlike structures that must be preserved like the phrenic nerve and brachial plexus itself.

Lines 102-105 contain a sentence about how assessment "could, through an alternative approach, demonstrate the contribution of first rib resection" that I found confusing. Consider rewriting this for clarity.

In the discussion, you review various surgical approaches and their complication rates (lines 217-295), but most cited studies report clinical outcomes rather than intraoperative physiology. More discussion of the anatomical and physiologic mechanisms by which first rib resection achieves decompression would strengthen this section. You acknowledge that no comparable intraoperative EMG documentation exists in prior literature (lines 345-351), which highlights your study's novelty. Just be careful not to claim your results "support" or "reinforce" superiority without comparative data. You're showing that a technique works, which is valuable, but establishing that it works better than alternatives requires a different study design.

Consider also whether 90 degree arm positioning itself might cause temporary plexopathy that resolves when the arm returns to neutral, independent of surgical decompression. Including the 90 degree stage data would help address this alternative explanation and would strengthen your mechanistic interpretation.

For revision, reframe your conclusions to match what your study design can actually demonstrate. You provide the first intraoperative physiologic documentation of brachial plexus function during the staged Roos procedure. That is valuable. You show that EMG values improve significantly after the complete procedure including rib resection, with minimal or possibly negative changes after scalenectomy alone. That is consistent with / provides physiologic support for comprehensive decompression within this staged approach. But you cannot claim this proves first rib resection is necessary or superior without comparative data from patients undergoing alternative approaches. A more appropriate conclusion would be: "Intraoperative electromyographic monitoring demonstrates significant improvement in brachial plexus function following first rib resection in the Roos procedure, with minimal EMG change or possible transient worsening after anterior scalenectomy alone in the surgical position. These findings provide physiologic evidence supporting the practice of comprehensive thoracic outlet decompression including first rib resection, though comparative studies with alternative surgical approaches are needed to definitively establish relative efficacy. This monitoring technique may have value for intraoperative assessment of decompression adequacy."

Comments on the Quality of English Language

The English is generally clear and acceptable for publication. There are a few awkward phrasings (for example, "limited widespread applicability" on line 278, and the confusing sentence at lines 102-105) that should be cleaned up, but overall the language does not present a barrier to understanding. Minor copyediting during production should be sufficient.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report (New Reviewer)

Comments and Suggestions for Authors

Major changes:

 

They must correct the stimulus unit and modality, as “450 mA” is physiologically implausible; they should specify whether the stimulus was delivered in volts, in true peak milliamperes, or in device-specific output units, since this value is not consistent with currents reported in previous studies and standard neuromonitoring practice.

 

They must state in both the Methods and the Discussion that what is being measured are changes in MEP amplitude as an indirect marker of neural conduction across the brachial plexus, rather than a direct measure of “brachial plexus decompression.”

 

Erratum in the abstract:

“abductor digitiminimi muscles” → should be abductor digiti minimi.

 

The terminology should be reviewed throughout the manuscript and unified, as scalenotomy ≠ scalenectomy.

Comments on the Quality of English Language

None

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 3 Report (New Reviewer)

Comments and Suggestions for Authors

Thank you for revising the manuscript and addressing the comments. I am satisfied with the rigour of the manuscript, and gladly endorse it for submission. Good job. 

Comments on the Quality of English Language

The English is generally clear and acceptable for publication. There are a few awkward phrasings (for example, "limited widespread applicability" on line 278, and the confusing sentence at lines 102-105) that should be cleaned up, but overall the language does not present a barrier to understanding. Minor copyediting during production should be sufficient.

Author Response

Please see the attachment.

Author Response File: Author Response.docx

This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Title of the study: Transaxillary first rib resection plus anterior scalenectomy versus anterior scalenectomy alone in thoracic outlet syndrome: A comparative analysis based on intraoperative monitoring of brachial plexus decompression

 

 

Technical review:

 

The subject is important and relevant to medicine, especially since there is still a lot of debate about whether or not rib resection is necessary for treating TOS. The technique, statistical analysis, and intraoperative measurements are well-considered; yet, there are numerous problems regarding study design, interpretation, clarity, and limitations. The title can be revised to reflect the actual study.

 

Cons:

 

Line 36: The title and abstract suggest a comparative study between "first rib resection + scalenectomy" and "scalenectomy alone," but all patients underwent both procedures. There is no control group undergoing only anterior scalenectomy.

 

Introduction:

Lines 58-62: please add references.

Add a paragraph focusing on current treatment options and complication rates.

 

Methodology:

Add a sentence to describe when the study years are (for example, between 2020 and 2024).

 

Line 177: Does this information belong to another reviewer*??

(This section may be divided by subheadings. It should provide a concise and precise description of the experimental results and their interpretation, as well as the experimental conclusions that can be drawn. )

 

The study does not include randomization and comparison, which makes it more challenging to make conclusions about causality.

 

Please define exclusion/inclusion criteria.

 

 

Results:

What is the mean time of the symptoms? If there is a control group, please specify mean times according to the groups.

Add clinical outcome measurements (such as the DASH score and VAS scales) after surgery to show that adjustments made during surgery lead to actual improvements.

 

 

Discussion:

Indications for neuromonitorization, except brachial plexus injuries, can also be mentioned.

Add a paragraph focusing on the limitations of this study. What are the weak and strong sides of your study? Please mention them.

Failure rates of conservative treatment prior to surgery should be discussed.

 

Conclusion:

Should be revised according to the comparative study design in retrospective design.

 

References:

The number of references is not sufficient. Please enrich the discussion and add more recent references.

 

Contributions to clinical practice:

A graphical abstract for clinical patient management from diagnosis to surgery may also be helpful. (A treatment guide will make your paper interesting after including clinical outcomes of this study.

Needs to be revised and improved. But the topic is very unique and attractive. Please focus on revising the study design. I believe that paper has a value but needs to be well-prepared.

 

Decision: Major revisions are needed.

 

Thank you for the opportunity to review this well-designed and thoroughly detailed study.

Comments on the Quality of English Language

NEED TO BE EDITED. 

Reviewer 2 Report

Comments and Suggestions for Authors

This is a case study investigating, from an electrophysiological perspective, whether to perform first rib resection in addition to anterior scalenectomy, or not. However, the manuscript has several critical flaws that must be addressed before it could be considered for publication.

1. Lack of knowledge gap in the introduction; unclear study objectiveThe introduction does not describe the existing knowledge gap, making the study objective unclear. The introduction contains textbook-like descriptions of thoracic outlet syndrome (TOS) up to line 74, followed abruptly at line 75 by the statement of the study’s objective. This will likely confuse readers. The authors should clearly summarize previous studies to identify the knowledge gap regarding decision-making for first rib resection in TOS treatment, and then explain how their study design addresses it.
2. Indications for first rib resection depend on TOS pathologyThe indication for first rib resection should vary depending on the pathophysiology of TOS. For cases where compression at the scalene muscle region is the main pathology, rib resection is unnecessary. In contrast, cases with a narrowed costoclavicular space are generally considered appropriate candidates for rib resection. In so-called true neurogenic TOS, characterized by paralysis of the abductor digiti minimi and the medial antebrachial cutaneous nerve, the cause is typically constriction band entrapment, and rib resection is unnecessary. However, in this study, the authors did not evaluate each patient’s costoclavicular space by imaging, did not describe intraoperative findings related to pathology, and did not explain diagnostic methods or surgical indications. Thus, it is impossible for readers to judge whether rib resection was indicated in these cases. Furthermore, the authors grouped together patients with diverse TOS pathologies—ranging from scalene muscle to pectoralis minor involvement—without distinction. This makes it impossible to determine appropriate indications for first rib resection based on their results.
3. Electromyography methodology issuesThe EMG results are reported only in microvolts (μV), suggesting that the authors measured resting amplitude using surface EMG. However, simple pre- and postoperative comparisons of resting surface EMG amplitude are generally not acceptable, as they are highly susceptible to physiological fluctuations—such as changes in bleeding, extracellular fluid volume, and edema—which can cause significant measurement error. The authors should normalize the measurements or analyze additional parameters such as frequency.
4. Flawed conclusion regarding the effectiveness of rib resectionThe study concludes that first rib resection is effective because EMG amplitude improved after surgery. However, the observed amplitude change may simply be due to the release of constriction band compression following rib resection, rather than proof that rib resection itself is an appropriate intervention. This conclusion is therefore overstated.
5. Table 4 issuesThe rationale for presenting both mean and median values is unclear. If the data are not normally distributed, the mean has no meaningful interpretive value. Moreover, the number of patients varies across measurements, making it inappropriate to aggregate results into a single summary.
6. Lines 177–179These lines are unnecessary and should be deleted.
7. Potential malpractice in “multiple pressure syndrome” casesPerforming anterior scalenectomy or first rib resection in six cases of “multiple pressure syndrome” may represent potential malpractice if other pathological sites were ignored. The authors need to explain why brachial plexus surgery was prioritized over addressing other lesions.
8. Discussion content misaligned with study objectivesThe discussion section focuses primarily on general aspects of TOS treatment, rather than on decision-making regarding first rib resection—the most important issue in this study. In academic writing, it is essential to compare the results with those of similar studies, but no such comparison is provided. A substantial revision of the discussion is strongly recommended.