It’s the Sound, not the Pulse: Peripheral Magnetic Stimulation Reduces Central Sensitization through Auditory Modulatory Effects

Reviewer #1 (Public review):

Summary:

This study from Abssy et al. aims to determine if different non-invasive peripheral stimulation techniques - such as magnetic and electrical stimulations - may influence pain intensity, unpleasantness, and secondary hyperalgesia using a 4-arm parallel-group study. They observed no effect on pain intensity and unpleasantness. Also, they reported that only the TENS (electrical stimulation) did not impact secondary hyperalgesia. They hypothesized that the effects were probably due to the sound emitted by RPMS (magnetic stimulation). In a follow-up study, they tried to determine if covering the sound of RPMS would abolish the effect on secondary hyperalgesia using a single-arm design. They observed no effect of RPMS.

Strengths:

(1) The research team recruited a relatively large sample size for this type of study.

(2) The phasic heat pain protocol appears rigorous and well-described.

(3) The Figures are helpful in facilitating the understanding of the study design and results.

(4) The statistical analyses appear sound.

Weaknesses:

(1) The proposed design is not sufficient to answer the research question. The rationale of the study proposed in the introduction is that auditory stimulation may explain the analgesic effects of RPMS. To answer this question, the authors should have used a factorial design using 4 groups (active RPMS + sound; active RPMS + no sound; sham RPMS + sound; sham RPMS + no sound). Using this design, it would have been possible to determine if the sound, the afferent stimulation, or both are necessary to produce analgesia. Rather, they tested two types of RPMS (iTBS, cTBS) without real rationale, one electrical stimulation and a placebo.

(2) There are multiple ways that the current design could have introduced biases. The study was not randomized but pseudo-randomised. What does that mean? Was their allocation concealment? Was the assessor and data analyst blinded to group allocation? Did an intention to treat analyses were performed? Did the participants were adequately blinded (was it measured)?

(3) The TENS parameters used were not optimal and are not those commonly used in clinical practice. This could have explained the lack of TENS effects. The lack of TENS effects has not been discussed and it is concerning. If TENS had been effective (as expected), the story about the auditory effects would not have been presented as the primary mechanisms underlying the current results.

(4) No primary outcome has been identified. It is important to mention that the interpretation of results is based on the presence of only one statistically significant result. Pain intensity and pain unpleasantness are not affected. This was not properly addressed in the Discussion. What does that mean that secondary hyperalgesia is affected but not pain?

(5) The use of secondary hyperalgesia as a variable requires further clarification. How is it possible to measure secondary hyperalgesia if there is no lesioned tissue? If heat creates secondary hyperalgesia without lesion, what does that mean physiologically? Is it a valid and reliable "pain" variable?

(6) The follow-up study has been designed to cover the RPMS sound using pink noise. However, the pink noise was also present during the PHP measurement. How can we determine whether the absence of change is due to the pink noise during the RPMS or the presence of pink noise during PHP? I don't think this is possible to discriminate.

Appraisal:

(7) Despite all these potential issues, authors interpret their data with high confidence and with several overstatements in the Title, Abstract, and Discussion. The results do not support their conclusions. The fact that auditory stimulation may produce an analgesic effect is a hypothesis, but the current study cannot ascertain it.

Reviewer #2 (Public review):

Summary:

In this article, Abssy, Osokin, Osborne, et al. aimed to demonstrate the effect of Peripheral Magnetic Stimulation (PMS) as a pain relief tool, studying its effects in an experimentally induced pain paradigm applied over healthy subjects. This is a relevant objective, as it will give a proxy indication of its utility as a clinical intervention to treat pain. Shockingly, in the first experiment, the authors found that this effect existed, not only in the active PMS groups but also in the sham PMS. With a clever second experiment, the authors used pink noise to mask the clicking sound and the PMS: this modification abolished the hypoalgesic effect of PMS.

Strengths:

This study presents an adequately calculated sample size (n = 100 for study 1 and n = 32 for study 2). This gives trustability to the results and allows for a correct disaggregated analysis to assess gender effects, which correct execution does not often occur. Nuisance variables are adequately addressed, figures and writing are clear, and I especially liked figures 4 and 5 for their easiness of interpretation. They explore two different stimulation protocols for the PMS, extending their results beyond parametrization. Secondary hyperalgesia is a particularly relevant measurement, as it is a common symptom in many relevant painful conditions. Pseudorandomization and counterbalanced design are also appreciated, as well as reinforcement of the results through Bayesian statistical approaches. Regarding the scientific content, the main result (auditory modulation of pain in PMS) is exciting and very interesting by itself and will be relevant for the pain community, granting further research, both from a fundamental and clinical perspective. Personally, I respect that they recognize that results did not match their a priori hypothesis, instead of committing HARKing. And it is a very thrilling mismatch for sure!

It will be especially interesting for those among us dedicated to neural stimulation for pain treatment.

Weaknesses:

Although the study presents solid results, some specific concerns make me reluctant to accept the interpretations that the authors take from said results. I list the most important here.

(1) My biggest concern in this paper is that the stimulation protocols are not applied after pain was induced in the subjects, but before. This is not bad in itself, but as the paper presents the stimulations as potential "treatments" it generates a severe mismatch between the objective, context (introduction), and impact (discussion) presented for the experiments, and how they are actually designed. This adds to the fact that healthy volunteers are used here to generate a study with low translational capability, that aims to be translational and provide an indication for clinics (maybe this is why the reduction in pain intensity caused by PMS when applied in patients, reported in references [29, 35 and 39], is not observed here).

(2) TENS treatment duration is simply too short (90s) to be considered a therapeutic TENS intervention. I get that this duration was chosen to match the one of PMS, but TENS is never applied like this in the clinics, in which the duration varies from 10 minutes to an hour (or more). This specific study comparing different durations recommends 40 minutes for knee osteoarthritis pain relief (PMID: 12691335). Under these conditions, this stimulation is more similar to a sham TENS than to a real TENS treatment: I would suggest interpreting it as such. As the paper is right now, it could give the impression that PMS could produce clinical effects not observed in TENS, but while the PMS application resembles a clinical one, the TENS application does not (due to its extremely short duration). As an example, giving paracetamol at a dose 10 times below its effective dose is a placebo, not a paracetamol treatment.

(3) This study measured pain, not central sensitization. Specifically, the effects refer to the area of secondary hyperalgesia. The IASP definition for central sensitization is "Increased responsiveness of nociceptive neurons in the central nervous system to their normal or subthreshold afferent input." (PMID: 32694387). No neuronal results are reported in this article. Therefore, central sensitization is not measured here, and we do not know if it is reduced by sound. This frontally clashes with the title of the article and with many interpretations of the results. For a deep review on this topic, I recommend PMID: 39278607 and the short article PMID: 30416715.

(4) There is no mention of blinding/masking/concealing in this manuscript. Was the therapist blind to whether they applied one protocol, another, or a placebo? Were the evaluators blind, as this can heavily influence their measurements? And the volunteers? Was allocation concealed? Was this blinding measured afterwards? Blinding is, together with randomization, the most important methodological feature for those interventional studies. For example, not introducing blinding and concealing directly makes a study lose 4 out of 10 points in the PEDro scale, failing to fulfill criteria 3, 5, 6, and 7 (https://pedro.org.au/english/resources/pedro-scale/). Continuing with methodological considerations, the dropout percentage is high (18% for the first and 25% for the second study), both above the 15% cutoff for criterion 8 of the PEDro, losing another point. It is not mentioned whether the statistical analysis was intention-to-treat or per-protocol. Assuming the second, criterion 9 is failed too. Also, although between-group comparisons are done for study 1, they are not for study 2. Criterion 10 depends on this, so I would recommend doing it to avoid failing it. As it is right now, the study will be a 3/10 on the PEDro scale, being therefore considered "low-quality level evidence". As some of these criteria can be fulfilled in this study, I will recommend doing so to increase its quality level to medium (more in "recommendations for authors").

(5) Data reporting and statistical treatment can be improved, as only differences are reported and regression to the mean is not accounted for in this study. Moreover, baseline levels for the dependent variables (control session) are not accessible for evaluation and they are not compared statistically, making it impossible to know if the groups were similar at baseline. This will imply failing criterion 3 of the PEDro, for a total of 2/10 points.

Author response:

Reviewer 1 (Public Review)

(1) The proposed design is not sufficient to answer the research question. The rationale of the study proposed in the introduction is that auditory stimulation may explain the analgesic effects of RPMS. To answer this question, the authors should have used a factorial design using 4 groups (active RPMS + sound; active RPMS + no sound; sham RPMS + sound; sham RPMS + no sound). Using this design, it would have been possible to determine if the sound, the afferent stimulation, or both are necessary to produce analgesia. Rather, they tested two types of RPMS (iTBS, cTBS) without real rationale, one electrical stimulation and a placebo.

We will clarify that the study design employed was originally designed to determine whether iTBS or cTBS would be more effective to reduce pain. We included TENS as a positive control, and sham as a negative control. We were indeed surprised by the findings, and present them herein. Future RCTs should be performed to reproduce these findings.

(2) There are multiple ways that the current design could have introduced biases. The study was not randomized but pseudo-randomised. What does that mean? Was their allocation concealment? Was the assessor and data analyst blinded to group allocation? Did an intention to treat analyses were performed? Did the participants were adequately blinded (was it measured)?

This study was not designed as an RCT, but rather as experimental study. The study was pseudo-randomized to ensure that the groups had equal allocation and distribution of sexes.

The groups were blinded to the other stimulations (they were not informed of the various arms of the study, through different consent forms).

It was not possible to blind the experimenter as the iTBS and cTBS protocols are very different: iTBS has multiple bursts separated by brief intervals, whereas cTBS is continuous). The data were masked for analysis, and only unblinded at the final stage. We will update the manuscript to reflect these changes.

(3) The TENS parameters used were not optimal and are not those commonly used in clinical practice. This could have explained the lack of TENS effects. The lack of TENS effects has not been discussed and it is concerning. If TENS had been effective (as expected), the story about the auditory effects would not have been presented as the primary mechanisms underlying the current results.

We acknowledge that this is a limitation of the study. A future study should address this. However, we will not remove the arm for transparency.

(4) No primary outcome has been identified. It is important to mention that the interpretation of results is based on the presence of only one statistically significant result. Pain intensity and pain unpleasantness are not affected. This was not properly addressed in the Discussion. What does that mean that secondary hyperalgesia is affected but not pain?

We reiterate that this study was not designed as an RCT, but rather an experimental study with The primary outcomes measures that capture change in were measures of pain sensitivity (pain intensity NRS, pain unpleasantness NRS, and secondary hyperalgesia). We will clarify this in the revised manuscript.

We will now include discussion of the effects being solely on secondary hyperalgesia, and not on pain intensity and unpleasantness.

(5a) The use of secondary hyperalgesia variable is concerning. How is it possible to measure secondary hyperalgesia if there is no lesioned tissue?

Secondary hyperalgesia refers to hyperalgesia assessed in an area adjacent to or remote of the site of stimulation. In general, it is not required to lesion a tissue to activate the nociceptive system or to induce pain. We have cited other studies that have employed secondary hyperalgesia as a pain outcome measure without inducing a lesion.

Hyperalgesia reflects increased pain on suprathreshold stimulation. Then, one measures the subjective response to a painful (i.e. suprathreshold) stimulation, then applies a conditioning stimulation (e.g. heat), and measures the subjective response to the same original stimulus. If the response after conditioning is higher than the baseline measure, hyperalgesia has been induced. Secondary hyperalgesia just refers to hyperalgesia assessed in an area adjacent to or remote of the site of stimulation. In general, it is not required to lesion a tissue to activate the nociceptive system or to induce pain.

(5b) If heat creates secondary hyperalgesia without lesion, what does that mean physiologically?

Secondary hyperalgesia is normally interpreted as a perceptual correlate of central sensitization.

(5c) Is it a valid and reliable "pain" variable?

Yes and yes. A noxious heat stimulus can reliably elicit secondary hyperalgesia (see section 3.2 from Quesada et al. 2021). We also cite several studies that have used secondary hyperalgesia as an outcome measure of central sensitization in pain.

(6) The follow-up study has been designed to cover the RPMS sound using pink noise. However, the pink noise was also present during the PHP measurement. How can we determine whether the absence of change is due to the pink noise during the RPMS or the presence of pink noise during PHP? I don't think this is possible to discriminate.

We will add a third study that performs the control analysis with the sound of the rPMS masked, but no pink noise otherwise. The study will be performed in two groups: one with pink noise, and one without pink noise.

Appraisal

(7) Despite all these potential issues, authors interpret their data with high confidence and with several overstatements in the Title, Abstract, and Discussion. The results do not support their conclusions. The fact that auditory stimulation may produce an analgesic effect is a hypothesis, but the current study cannot ascertain it.

We believe that the chief concern with the interpretation lies with concerns with the second study. The proposed third experiment will address these concerns.

Reviewer 2 (Public Review):

(1) My biggest concern in this paper is that the stimulation protocols are not applied after pain was induced in the subjects, but before. This is not bad in itself, but as the paper presents the stimulations as potential "treatments" it generates a severe mismatch between the objective, context (introduction), and impact (discussion) presented for the experiments, and how they are actually designed. This adds to the fact that healthy volunteers are used here to generate a study with low translational capability, that aims to be translational and provide an indication for clinics (maybe this is why the reduction in pain intensity caused by PMS when applied in patients, reported in references [29, 35 and 39], is not observed here).

We will reframe these as prophylaxis, rather than treatment. This study was an experimental study originally designed to determine which stimulation parameters (cTBS or iTBS) would be better suited to modulate pain. We performed the study in healthy individuals undergoing acute pain, akin to a person undergoing painful procedure, which could lead to central sensitization and pain persistence (e.g., post-surgical pain). However, before testing this in individuals undergoing actual procedures, it is essential to determine efficacy in people before translation.

Khan et al [29] is a case study with neuropathic pain, whereas our study uses a nociceptive pain model. Lim et al [35] employed 10 sessions of rPMS stimulation in patients with acute low back pain. Similar to our study, the change in VAS driven by rPMS was no different than the sham stimulation. We notice that there is no reference 39, and will correct this.

(2) TENS treatment duration is simply too short (90s) to be considered a therapeutic TENS intervention. I get that this duration was chosen to match the one of PMS, but TENS is never applied like this in the clinics, in which the duration varies from 10 minutes to an hour (or more). This specific study comparing different durations recommends 40 minutes for knee osteoarthritis pain relief (PMID: 12691335). Under these conditions, this stimulation is more similar to a sham TENS than to a real TENS treatment: I would suggest interpreting it as such. As the paper is right now, it could give the impression that PMS could produce clinical effects not observed in TENS, but while the PMS application resembles a clinical one, the TENS application does not (due to its extremely short duration). As an example, giving paracetamol at a dose 10 times below its effective dose is a placebo, not a paracetamol treatment.

We acknowledge that this is a limitation, and will address this in the Discussion of the revised manuscript.

(3) This study measured pain, not central sensitization. Specifically, the effects refer to the area of secondary hyperalgesia. The IASP definition for central sensitization is "Increased responsiveness of nociceptive neurons in the central nervous system to their normal or subthreshold afferent input." (PMID: 32694387). No neuronal results are reported in this article. Therefore, central sensitization is not measured here, and we do not know if it is reduced by sound. This frontally clashes with the title of the article and with many interpretations of the results. For a deep review on this topic, I recommend PMID: 39278607 and the short article PMID: 30416715.

It is widely accepted that central sensitization is the neurophysiological basis of secondary hyperalgesia (see PMID: 11313449; PMID: 10581220).

The reviewer is conflating secondary hyperalgesia due to central sensitization and chronic pain. Whether chronic pain is driven or maintained by central sensitization is not the goal of our study. However, there is ample evidence that nociceptive drive can induce plasticity in the CNS, which alters pain sensitivity, and that these changes facilitate pain.

(4a) There is no mention of blinding/masking/concealing in this manuscript. Was the therapist blind to whether they applied one protocol, another, or a placebo? Were the evaluators blind, as this can heavily influence their measurements? And the volunteers? Was allocation concealed? Was this blinding measured afterwards? Blinding is, together with randomization, the most important methodological feature for those interventional studies. For example, not introducing blinding and concealing directly makes a study lose 4 out of 10 points in the PEDro scale, failing to fulfill criteria 3, 5, 6, and 7 (https://pedro.org.au/english/resources/pedro-scale/).

This study was not designed as an RCT, but rather as experimental study. The study was pseudo-randomized to ensure that the groups had equal allocation and distribution of sexes.

The groups were blinded to the other stimulations (they were not informed of the various arms of the study, through different consent forms). However, blinding was not measured afterwards (again, this was not meant to be an RCT).

It was not possible to blind the experimenter as the iTBS and cTBS protocols are very different: iTBS has multiple bursts separated by brief intervals, whereas cTBS is continuous). The data were masked for analysis, and only unblinded at the final stage. We will update the manuscript to reflect these changes.

(4b) Continuing with methodological considerations, the dropout percentage is high (18% for the first and 25% for the second study), both above the 15% cutoff for criterion 8 of the PEDro, losing another point.

In the study, only 2 withdrew after feeling the heat, 2 were lost to follow up, and 2 had incomplete data. That totals 6/123 in Study 1. In study 2, none of the participants that met inclusion/exclusion criteria, and who were ‘allocated’ to the study were included (0% dropout/data loss).

We are unsure how to address this point, as we had clear inclusion/exclusion criteria, and these could only be measured after consenting. As this is an experimental study performed on healthy individuals in a university setting, we are not able to collect any study related data prior to consent.

We openly reported individuals who did not meet the criteria, and thus were excluded. These criteria are a combination of what is required to collect good quality data, and what we are ethically permitted to do. We understand that in an interventional trial where >15% drop out due to intolerance, or adverse events would indeed be concerning.

(5) Data reporting and statistical treatment can be improved, as only differences are reported and regression to the mean is not accounted for in this study. Moreover, baseline levels for the dependent variables (control session) are not accessible for evaluation and they are not compared statistically, making it impossible to know if the groups were similar at baseline. This will imply failing criterion 3 of the PEDro, for a total of 2/10 points.

This only concerns study 1, as study 2 is a within subject study design. Study 1 provides the raw data in Figure 4. We will provide the raw data for each of the primary outcome measures in a supplemental table in the revision.