Effects of nicotine compared to placebo gum on sensitivity to pain and mediating effects of peak alpha frequency

Reviewer #2 (Public review):

Summary:

The study by Millard et al. investigates the effects of nicotine on peak alpha frequency and pain using a highly elaborate experimental design. According to the statistical analysis, the authors found a small covariate-corrected effect for prolonged heat pain and a small effect on global peak alpha frequency in response to nicotine treatment. However, the effect on heat pain was not found for pressure pain, was not mediated by peak alpha frequency, and appears mainly based on a worsening in the placebo condition rather than a clear reduction of pain after nicotine.

Strengths:

I very much like the study design and that the authors followed their research line by aiming to provide a complete picture of the pain-related cortical impact of peak alpha frequency. This is important work, even in the absence of clear statistical or mechanistic support for the main hypothesis. I also appreciate the preregistration of the study, the well-written and balanced introduction, and the additional analyses added during revision.

Weaknesses:

The weakness of the study revolves around two main aspects:

(1) Source separation would still have been more appropriate than electrode regions or global peak alpha frequency to extract the alpha signal. The added ICA analysis is appreciated, but in my view, it does not fully solve the problem. Different alpha sources, such as mu rhythm, occipital alpha, and lateralised alpha activity, are still not clearly disentangled. The main peak alpha frequency effect remains a small global, wide-band, sensor-space effect rather than a clearly source-specific sensorimotor effect.

(2) I still think the choice of nicotine is a major weakness of the study. The rationale for using nicotine as an intervention rests partly on previous reports of nicotine effects on experimental pain, but the most relevant cited meta-analysis already suggested that these effects are small and may be affected by publication bias. It is therefore not a clean way to test whether peak alpha frequency has a causal role in pain. The heat-pain result is also difficult to interpret as analgesia. Statistically, the placebo-controlled contrast may be significant, but in practice, the nicotine condition changed very little, and the effect seems mainly driven by worsening in the placebo group. In a real intervention, one gives the drug, not the difference between drug and placebo.

Impact:

The impact of the study could be to show what did not work to answer the authors' research question. The study is valuable because it provides a careful and largely negative mechanistic test: nicotine produced at most small effects, peak alpha frequency did not mediate pain, and pressure pain was not affected. The study would have more impact with a more direct intervention model and an analysis strategy that more clearly untangles the different alpha sources.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, Millard and colleagues investigated if the analgesic effect of nicotine on pain sensitivity, assessed with two pain models, is mediated by Peak Alpha Frequency (PAF) recorded with resting state EEG. The authors found indeed that nicotine (4 mg, gum) reduced pain ratings during phasic heat pain but not cuff pressor algometry compared to placebo conditions. Nicotine also increased PAF (globally). However, mediation analysis revealed that the reduction in pain ratings elicited by the phasic heat pain after taking nicotine was not mediated by the changes in PAF. Also, the authors only partially replicated the correlation between PAF and pain sensitivity at baseline (before nicotine treatment). At the group-level no correlation was found, but an exploratory analysis showed that the negative correlation (lower PAF, higher pain sensitivity) was present in males but not in females. The authors discuss the lack of correlation.

In general, the study is rigorous, methodology is sound and the paper is well-written. Results are compelling and sufficiently discussed.

Strengths:

Strengths of this study are the pre-registration, proper sample size calculation, and data analysis. But also the presence of the analgesic effect of nicotine and the change in PAF.

Weaknesses:

It would even be more convincing if they had manipulated PAF directly.

We thank Reviewer #1 for their positive and constructive comments regarding our study. We appreciate the view that the study was rigorous and methodologically sound, that the paper was well-written, and that the strengths included our pre-registration, sample size calculation, and data analysis.

In response to the reviewer's comment about more directly manipulating Peak Alpha Frequency (PAF), we agree that such an approach could provide a more direct investigation of the role of PAF in pain processing. We chose nicotine to modulate PAF as the literature suggested it was associated with a reliable increase in PAF speed. As mentioned in our Discussion, there are several alternative methods to manipulate PAF, such as non-invasive brain stimulation techniques (NIBS) like transcranial alternating current stimulation (tACS) or neurofeedback training. These approaches could help clarify whether a causal relationship exists between PAF and pain sensitivity. Although methods such as NIBS still require further investigation as there is little evidence for these approaches changing PAF (Millard et al., 2024).

Reviewer #2 (Public Review):

Summary:

The study by Millard et al. investigates the effect of nicotine on alpha peak frequency and pain in a very elaborate experimental design. According to the statistical analysis, the authors found a factor-corrected significant effect for prolonged heat pain but not for alpha peak frequency in response to the nicotine treatment.

Strengths:

I very much like the study design and that the authors followed their research line by aiming to provide a complete picture of the pain-related cortical impact of alpha peak frequency. This is very important work, even in the absence of any statistical significance. I also appreciate the preregistration of the study and the well-written and balanced introduction. However, it is important to give access to the preregistration beforehand.

Comment on latest version:

I thank the authors for their efforts to respond to my previous concerns. I appreciate the additional analyses and the more cautious wording in several places. However, I still think the manuscript would benefit from a more direct interpretation of the findings.

Reviewer #3 (Public Review):

In this manuscript, Millard et al. investigate the effects of nicotine on pain sensitivity and peak alpha frequency (PAF) in resting state EEG. To this end, they ran a pre-registered, randomized, double-blind, placebo-controlled experiment involving 62 healthy adults who received either 4 mg nicotine gum (n=29) or placebo (n=33). Prolonged heat and pressure were used as pain models. Resting state EEG and pain intensity (assessed with a visual analog scale) were measured before and after the intervention. Additionally, several covariates (sex at birth, depression and anxiety symptoms, stress, sleep quality, among others) were recorded. Data was analyzed using ANCOVAequivalent two-wave latent change score models, as well as repeated measures analysis of variance. Results do not show ‘experimentally relevant’ changes of PAF or pain intensity scores for either of the prolonged pain models due to nicotine intake.

The main strengths of the manuscript are its solid conceptual framework and the thorough experimental design. The researchers make a good case in the introduction and discussion for the need to further investigate the association of PAF and pain sensitivity. Furthermore, they proceed to carefully describe every aspect of the experiment in great detail, which is excellent for reproducibility purposes. Finally, they analyse the data from almost every possible angle and provide an extensive report of their results.

The main weakness of the manuscript is the interpretation of these results. Even though some of the differences are statistically significant (e.g., global PAF, pain intensity ratings during heat pain), these differences are far from being experimentally or clinically relevant. The effect sizes observed are not sufficiently large to consider that pain sensitivity was modulated by the nicotine intake, which puts into question all the answers to the research questions posed in the study.

We would like to express our gratitude to Reviewer #3 for their thoughtful and constructive review, including the positive feedback on the strengths of our study's conceptual framework, experimental design, and thorough methodological descriptions.

We acknowledge the concern regarding the experimental and clinical relevance of some statistically significant results (e.g., global PAF and pain intensity during heat pain) and agree that small effect sizes may limit their practical implications. However, our primary goal was to assess whether nicotine-induced changes in PAF mediate pain changes, rather than to demonstrate large direct effects on pain sensitivity. Nicotine was chosen for its known ability to modulate PAF, and our focus was on the mechanistic role of PAF in pain perception. To clarify this, we have revised the discussion to better differentiate between statistical significance, experimental relevance, and clinical applicability. We emphasize that this study represents a preliminary step towards understanding PAF’s mechanistic role in pain, rather than a direct clinical application.

We appreciate the suggestion to refine our interpretation. We have adjusted our language to ensure it aligns with the effect sizes observed and made recommendations for future research, such as testing different nicotine doses, to potentially uncover stronger or more clinically relevant effects.

Although modest, we believe these findings offer valuable insights into the potential mechanisms by which nicotine affects alpha oscillations and pain. We have also discussed how these small effects could become more pronounced in different populations (e.g., chronic pain patients) and over time, offering guidance for future research on PAF modulation and pain sensitivity.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

I thank the authors for their efforts to respond to my concerns. I very much admire the thoughts and effort that the authors have put into this study. This is a great study design, a fantastic research idea and an important path to study the neurophysiology of pain.

I also understand that some of my suggestions are not compatible with the authors' current line of analysing their data. Since the authors did not change the analysis procedure and obviously could not change their experimental design, I would largely keep my public review.

However, acknowledge the different opinions and have a few remarks and suggestions.

(1) In agreement with reviewer 3, I would not consider the effect of nicotine to be meaningful. The random effect mentioned by the authors could have been addressed with a crossover design. In this case, the placebo and intervention could have been directly compared. Interindividual differences in pain perception are at least partially controlled for by analysing the difference between pre and post-gum. The distribution of the pre-post difference separately for placebo and nicotine would be a valuable addition to the manuscript. I still think the minimal effect of nicotine on pain is not meaningful and not interpretable. The relevance of any explanatory variable like stress could be by chance (PMID: 35296861). Reviewer 3 had a valid point (comment 6) and this is something that should be mentioned as clearly as possible: there was no effect of nicotine. For PHP the comparison with the placebo is irrelevant if there is no pre vs. post-effect.

It is fair to say that some issues could have been resolved using a cross-over design, however, the choice of a parallel design was made, in part, due to the desire to mask the presence of a placebo gum. Having a single session per participant allowed us to produce a deception that all participants were receiving nicotine gum, which was later revealed during a debrief. This aspect is far less feasible in a cross-over design. In future, different approaches could be used. And we appreciated the reviewers recognition that this cannot, of course, be changed at this stage.

Regarding the comments of 1) ’I would not consider the effect of nicotine to be meaningful’, 2) the minimal effect of nicotine on pain is not meaningful and not interpretable’, and 3) ’there was no effect of nicotine’, we discern that the latter differs considerably from the first two points. We would like to address this point by first calling into question what the reviewer(s) mean by meaningful, and highlighting that discerning this varies by context. Edenberg (2021) highlights that meaning can be situated within several contexts: statistical, biological (mechanistic), clinical, and public policy. We show the statistical context, and therefore would like to emphasise that we cannot state number 3) ’there was no effect of nicotine’.

Although the complexity of our analysis is not at the same scale, we appreciate the need for thousands of participants for brain-wide associations, as cited (PMID: 35296861 = Marek et al., 2022). The article referenced states that reproducible brain-wide association studies require thousands of individuals, and thus we would like to highlight that our work indicating the potential relevance of sex/stress greatly differs from this. Though it may be by chance, the potential for that chance is 0.05 from a statistical significance perspective. Certainly, no finding should be taken as truth without replication, but that does not mean we should not report our finding of a statistically significant effect of stress on change in PAF in our model.

Then, the question becomes, are we already at the point where the issue of ’how to go beyond statistical significance’ should be addressed? One could argue no, as this is the first study to assess this question of nicotine’s effect on PAF and pain at the same time. But we would like to argue yes, although only to the mechanistic/biological level, because the question of what is meaningful is dependent on the study goals (Edenberg, 2021). We aimed to gain mechanistic insight into the PAF-pain relationship.

We hoped to achieve some biological/mechanistic meaning in the present study, however, as outlined in the discussion, with small effect sizes for nicotine on PAF and nicotine on heat pain, and lack of a mediating effect, we may not have achieved this. Although, if replicated, even small magnitude effects can shape our understanding of relevant mechanisms underlying pain and aid future clinical perspectives (Edenberg, 2021; Ross & Bassett, 2024). Meaningfulness in clinical or public policy contexts should of course be in mind, but were clearly not the focus of this present work.

We have edited the manuscript to demonstrate the fact that our effect size is small.

We corrected the rounding to 2 decimals, and now also refer the reader to the supplementary materials table:

“Change in pain was reduced by a factor of -0.68 for the nicotine group compared to the placebo group when controlling for confounding variables (Figure 3). See Supplementary Material 3.2, Table 5, for full model output.”

We edited the abstract and the first paragraph of the discussion to make clear to the reader that the effect sizes were small. In our desire to keep the text clear and readable, we did not intend to overstretch our claims, and apologise if the manuscript was unintentionally portraying this overstretch. These are very important sections of the manuscript in which to mention such nuances, as these are the parts viewed most when readers do not wish to read the entire manuscript.

Abstract

“The nicotine group showed a small decrease in heat-pain ratings compared to placebo group when controlling confounders, and a small increase in PAF across the scalp from pre- to post-gum, both with and without confounder adjustment. These effects were most pronounced in the central-parietal and right-frontal electrodes.”

Discussion first paragraph

“Compared to placebo, our data demonstrate three key findings: 1) nicotine increased PAF speed; 2) nicotine reduced prolonged heat pain intensity but only when controlling for confounding and not for the prolonged pressure pain model, and 3) decreases in prolonged heat pain intensity were not mediated by changes in PAF. This suggests that changes in heat pain due to nicotine occur through mechanisms unrelated to change in PAF and require replication as the effects required control for confounding and the reduction was small in magnitude.”

Discussion section on effect of nicotine on PAF:

“In line with previous literature in non-smokers [38,47,48], we contribute additional evidence that chewing 4 mg of nicotine gum produces a statistically significant increase in PAF speed in non-smoking, nicotine-gum-naïve, pain-free, adult participants. An exploratory cluster-based permutation analysis indicated that the change in wide-window PAF (8–12 Hz) produced by nicotine, was most pronounced in a cluster of electrodes in the central-parietal region and a separate cluster of electrodes in the right-frontal region, rather than in the pre-registered sensorimotor ROI (i.e., Cz, C1, C2, C3, C4).”

Discussion section on the effect of nicotine on pain:

“While acknowledging the modest effect size, it’s essential to consider the context of our study’s focus. Assessing the clinical relevance of pain reduction is pertinent in applications involving the use of any intervention for pain management [71]. However, from a mechanistic standpoint, particularly in understanding the implications of and relation to PAF, the specific magnitude of the pain effect becomes less pivotal, as small effects can still have mechanistic or biological meaning without establishing clinical meaning [72]. Nevertheless, future research should examine whether effects on pain increase in magnitude with different nicotine administration regimens (i.e. dose and frequency).” 

Discussion section on relationship between PAF and pain:

“However, as this is the first study attempting to directly manipulate PAF, observing only small effects on pain, we cannot confidently state that a causal relationship between PAF and pain sensitivity does not exist, and future research should explore these relationships with larger sample sizes, larger doses of nicotine, and alternative PAF modulators.”

Discussion final paragraph:

“We have shown that, compared to placebo, nicotine gum produced statistically significant increases global PAF speed and decreases pain ratings during prolonged heat pain. However, the effects of nicotine on heat pain were not mediated by changes in PAF. Therefore, we find no evidence that PAF is causally related to pain. The implication of this is that changing PAF may not be a useful target for pain modulation, because pain sensitivity may not be dependent on state changes in PAF. However, this is the first study to test modulation of PAF as a mechanism for reducing pain intensity. Moreover, while effects on PAF appear small but robust, effects on heat pain required control for confounding to be observed. More randomised experiments on the effects of nicotine that use larger sample sizes, higher nicotine doses, and pharmacokinetic tracking, whilst also reducing mediator measurement error are needed to confirm the present findings and uncover whether these factors account for the lack of mediation effect seen here.”

(2) I still think the authors made a mistake in using nicotine. Their new wording did not convince me, and I doubt that any reader would buy the "mediation by design" phrase.

We addressed the reviewers previous comment (comment 1) on nicotine being a ‘mistake’, and no longer suggest there is a “large body of evidence suggests that nicotine is an ideal choice for manipulating PAF”. We have been clearer about our intention to assess mediation-by-design, with the manipulation of PAF being out primary aim. For example, this edit in the discussion:

“The choice of nicotine was driven by its potential to change PAF, but also, short-term nicotine use is thought to have acute analgesic properties in experimental settings, with a review reporting that nicotine increased pain thresholds and pain tolerance [51].”

In addition, we discussed the ’direct’ manipulation of PAF using non-invasive brain stimulation methods, and have now added further future research directions using methods other than nicotine or NIBS:

“Furthermore, there may have been other mediators that suppress the mediating effects of PAF within our model [66,82,83]. This is plausible, as nicotine is thought to act on pain through multiple pathways [52,54,84], and more direct PAF modulation could more definitively evaluate whether PAF is mechanistically linked to pain sensitivity. Future interventions to modulate PAF could use non-invasive brain stimulation (NIBS), such as transcranial alternating current stimulation (tACS) or repetitive transcranial magnetic stimulation (rTMS), to influence neuronal firing and thereby directly target the brain mechanisms theorised to generate PAF [85–87]. This approach has since been investigated following the initial preprint of

the present manuscript [88,89]. In addition, other approaches to modulating approaches could be considered, such as exercise [32–34], visual stimulation [35,36], cannabis [90,91], and neurofeedback [92,93], while considering their viability in terms of blinding, tolerability, and scalability.”

(3) I acknowledge the work of the authors on SNR, the frequency spectrum looks smooth enough to detect peaks. However, the problem of different alpha sources is not solved. This can be seen in the frequency spectrum, where some participants show two peaks. This is not the first time I have suggested this to the authors; the idea is not new. The fMRI analogue would be to average all GM voxels; instead of global alpha it would be "global brain activity". Some suggestions for a future approach that the authors might consider:

Run a group ICA and select topographies from there. This should simplify the (potentially arbitrary) selection process.

Consider filtering the data before running the ICA, at least >20 Hz to exclude muscle artefacts.

We respectfully note that the reviewer’s comment appears to overlook the substantial revisions we have already made in direct response to this issue. Specifically, we implemented ICA in the revised manuscript, using an automated, objective pipeline to identify components with a clear alpha peak and a topography aligned with a predefined sensorimotor template. This was explicitly done to address concerns about overlapping alpha sources and improve anatomical specificity.

Contrary to the reviewer’s implication, we did not rely solely on global analyses in the original or revised manuscript, as we also included pre-defined ROIs and data-driven ROIs from cluster-based permutation analysis. The additional ICA-based analyses—included in the first revision—produced results that were consistent with the original sensor-space ROI findings, supporting the robustness of the PAF–pain mediation effect regardless of the method used to isolate sensorimotor alpha.

We agree that group ICA could be a valuable complementary approach. However, it is not without limitations, particularly in EEG where inter-individual variability in source topographies is high. Our choice to perform ICA at the individual level and apply an automated selection criterion based on spectral and spatial features was deliberate, data-driven, and avoids the subjectivity involved in manual selection or group-level back-projection.

We have added a discussion of this point and fully acknowledge that future work may benefit from comparing multiple alpha sources (e.g., mu vs. occipital) more explicitly. However, we must emphasise that this is not a missing analysis—it is already included in the revised manuscript. In this second revision, we have added an additional reference to this supplementary analysis within the section previously titled “Exploratory cluster-based permutation anlaysis”, now titled “Exploratory data-driven analysis of alpha”, in case the previous reference to it was in a sub-optimal location:

“Lastly, use of in-house code developed to automatically extract a sensorimotor alpha component using independent component analysis (ICA) showed similar results to the sensorimotor ROI mediation analysis (Supplementary Material 3.11). This supports the robustness of the PAF-pain effect regardless of the method used to isolate sensorimotor alpha.”

We strongly disagree with the suggestion to apply a low-pass filter below 20 Hz prior to ICA. This would remove high-frequency content, including muscle activity—the very signals ICA is designed to isolate and separate from neural activity.

By removing muscle-related frequencies before ICA, the reviewer’s proposed approach would prevent ICA from identifying muscle components in the data. This is methodologically flawed. as ICA works best when it has access to the full spectral range of the signal, allowing it to separate statistically independent sources— including muscle, eye movements, and neural oscillations—based on their spatial and temporal structure (Onton et al., 2006). Thus the desired sensorimotor alpha component would be more distinct if the full spectral range is included. Low-pass filtering the data before ICA designed to identify alpha would severely compromise artifact removal, degrade component separation, and reduce the effectiveness of our preprocessing pipeline.

References for responses to reviewer 2

Edenberg HJ. Perspective on beyond statistical significance: Finding meaningful effects. Complex Psychiatry 2021;7:1–8. https://doi.org/10.1159/000517237.

Marek S, Tervo-Clemmens B, Calabro FJ, Montez DF, Kay BP, Hatoum AS, Donohue MR, Foran W, Miller RL, Hendrickson TJ, Malone SM. Reproducible brain-wide association studies require thousands of individuals. Nature. 2022 Mar 24;603(7902):654-60.

Ross LN, Bassett DS. Causation in neuroscience: keeping mechanism meaningful. Nature Reviews Neuroscience. 2024 Feb;25(2):81-90.

Reviewer #3 (Recommendations for the authors):

I would like to thank the authors for the time and dedication that they clearly put into addressing the reviewer's comments. As researchers, we alternate between both sides (as authors and reviewers) and we are all privy of how difficult these tasks can be.

For me as a reviewer, this is one of the tough times. I wanted to support this manuscript because it is clear that conducting the study had to be a monumental effort, and there were early indications that it was rigorously carried out. Specifically referring to rigor, I value preregistration as a tool to assess the strength of the hypothesis posed before conducting the study, and the severity with which the claims are tested. During my first review, I tried to access the preregistration and even provided my email address as a sign of transparency, but access was not granted. During my second review, the main file in the submission system contained two versions of the same manuscript (the first one corresponding to the old version with the wrong preregistration link). I was not initially aware of this and I apologize for the misunderstanding.

With respect to the rest of my observations, I see that the authors made concessions on small and less relevant issues (e.g. comments #1, #2, #3), but did not satisfactorily address the main ones (#4, #5, #6, #7, #8 and #9). Addressing those comments (which are in line with the issues noted by other reviewers), would probably have lead to a different interpretation of the results compared with what they state in the first paragraph of the discussion.

The main claims (abstract and first paragraph of the discussion) are " 1) nicotine increased PAF speed; 2) nicotine reduced prolonged heat pain intensity but not prolonged pressure pain intensity compared to placebo gum". Just by reading and contrasting the claims with the results, my assessment is that the strength of evidence is inadequate.

I was now able to review the analysis plan, which did not contain an estimation of the effect sizes (only effect directions) and did not have a proper sample size estimation (comment #4) and the main outcome was not, to my understanding, based in terms of the beta coefficients (as you replied to reviewer #1). I also do not think that the possibility of no effect or a false positive (comment #5) is fairly weighed in relation to these main claims in the abstract an first paragraph of the discussion.

I also do not consider the response to comment #6 as satisfactory, first because it is a mistake to consider that we (as reviewers) only interpret the 'mean results'. As we have detailed access to the data, we interpret these results in terms of signal-to-noise ratio, i.e., how large is the effect (signal) compared with the intra and interindividual variance (noise), and it should be clear for anyone working on this fields (pain and EEG) that not only the main effect is not experimentally relevant to support the claims (comments #6 and #7), but in some cases it is likely to have arisen from the unjustified inclusion of covariates (comment #8 and #9). I only raise the final strength of evidence in my assessment from 'inadequate' to 'incomplete', because of the additions to the discussion.

As a final thought, I would have been more than happy to support and recommend the reading of a manuscript that described a carefully designed and preregistered study, but in which the hypothesis were not corroborated by the data. I would have even marked the strength of evidence as compelling. Unfortunately, the preregistered hypothesis cannot be severely tested (at least not in terms of a frequentist framework) because the effects sizes were not predefined and the required sample size was not estimated, and what I see from the manuscript is that there is an effort to maintain claims that are not properly supported by the data and the final analysis. I recognized that I myself can also be in the wrong, so it will be left for eLife readers to make up their own minds.

We respectfully disagree with the assertion that our preregistered hypotheses "cannot be severely tested" due to the absence of predefined effect sizes and sample size estimation. First, the primary purpose of preregistration is to increase transparency and reduce analytical flexibility—not necessarily to formalize power calculations, especially when reliable effect size estimates are unavailable, as is the case in emerging areas of research such as this one (Nosek et al., 2018). Predefining effect sizes based on speculative or contextually irrelevant prior studies would have introduced unjustified assumptions and potentially distorted interpretation. In this case, we made the scientifically responsible choice to avoid anchoring our design on uncertain estimates. 

Second, our sample size is comparable to or larger than those used in prior published studies addressing similar questions, and our analytic pipeline followed the preregistered plan. The reviewer suggests that we are attempting to maintain unsupported claims; however, our discussion is careful to reflect the limitations of the findings, including their statistical uncertainty, and we do not overstate conclusions. Where effects were weak or absent, we reported this transparently and interpreted them cautiously.

Finally, while formal power calculations are useful under certain conditions, they are not a prerequisite for a study to be considered a "severe test" of a hypothesis—especially when the statistical approach is preregistered, data are handled transparently, and null results are acknowledged rather than hidden. The sample size was informed by resource and feasibility constraints (Lakens, 2022) and aligns with or exceeds that of comparable studies in the field (Bowers et al., 2015). We have now made this rationale explicit in the manuscript.

“The sample size was informed by resource and feasibility constraints [98] and aligns with or exceeds that of comparable studies in the field [38], covering 60 participants in total, with two extra in case of incomplete data identified during later data analysis.”

We therefore maintain that the study is a valid and informative contribution, regardless of whether the observed results confirm or disconfirm the hypotheses.

Nonetheless, below we have revisited previous comments (#4, #5, #6, #7, #8 and #9) that reviewer 3 stated were not satisfactorily addressed.

Previous comment 4) Availability of the pre-registration

We consider this point now addressed, as access to the OSF pre-registration was resolved. Moreover, we can assure the reviewer that their identity was not revealed, as the request for access was not received/seen.

Previous comment 5) Magnitude of pain change – possibility of a type 1 error.

Previous comment 5) To be perfectly clear, I trust the results of this study more than some of the cited studies regarding nicotine and pain because it was preregistered, the sample size is considerably larger, and it seems carefully controlled. I just do not agree with the interpretation of the results, stated in the first paragraph of the Discussion. Quoting J. Cohen, "The primary product of a research inquiry is one or more measures of effect size, not P values" (Cohen, 1990). As I am sure the authors are aware of, even tiny differences between conditions, treatments or groups will eventually be statistically significant given arbitrarily large sample sizes. What really matters then is the magnitude of these differences. In general, the authors hypothesize on why there were no differences on the pressure pain model, and why decreases in heat pain were not mediated by PAF, but do not seem to consider the possibility that the intervention just did not cause the intended effect on the nociceptive system, which would be a much more straightforward explanations for all observations.

Our previous response included the fact that N=62 is not an arbitrarily large sample size and our consideration of the possibility of a false positive. In addition, we agree that conclusions should not be made based on p-values alone. Therefore, we have added more careful descriptions to highlight the nuances of our findings to the reader.

We edited the abstract and the first paragraph of the discussion to make clear to the reader that the effect sizes were small. In our desire to keep the text clear and readable, we did not intend to overstretch our claims, and apologise if the manuscript was unintentionally portraying this overstretch. These are very important sections of the manuscript in which to mention such nuances, as these are the parts viewed most when readers do not wish to read the entire manuscript.

Abstract

“The nicotine group showed a small decrease in heat-pain ratings compared to placebo group when controlling confounders, and a small increase in PAF across the scalp from pre- to post-gum, both with and without confounder adjustment. These effects were most pronounced in the central-parietal and right-frontal electrodes.”

Discussion first paragraph

“Compared to placebo, our data demonstrate three key findings: 1) nicotine increased PAF speed; 2) nicotine reduced prolonged heat pain intensity but only when controlling for confounding and not for the prolonged pressure pain model, and 3) decreases in prolonged heat pain intensity were not mediated by changes in PAF. This suggests that changes in heat pain due to nicotine occur through mechanisms unrelated to change in PAF and require replication as the effects required control for confounding and the reduction was small in magnitude.”

Discussion section on effect of nicotine on PAF:

“In line with previous literature in non-smokers [38,47,48], we contribute additional evidence that chewing 4 mg of nicotine gum produces a statistically significant increase in PAF speed in non-smoking, nicotine-gum-naïve, pain-free, adult participants. An exploratory cluster-based permutation analysis indicated that the change in wide-window PAF (8–12 Hz) produced by nicotine, was most pronounced in a cluster of electrodes in the central-parietal region and a separate cluster of electrodes in the right-frontal region, rather than in the pre-registered sensorimotor ROI (i.e., Cz, C1, C2, C3, C4).”

Discussion section on the effect of nicotine on pain:

“While acknowledging the modest effect size, it’s essential to consider the context of our study’s focus. Assessing the clinical relevance of pain reduction is pertinent in applications involving the use of any intervention for pain management [71]. However, from a mechanistic standpoint, particularly in understanding the implications of and relation to PAF, the specific magnitude of the pain effect becomes less pivotal, as small effects can still have mechanistic or biological meaning without establishing clinical meaning [72]. Nevertheless, future research should examine whether effects on pain increase in magnitude with different nicotine administration regimens (i.e. dose and frequency).”

Discussion section on relationship between PAF and pain:

“However, as this is the first study attempting to directly manipulate PAF, observing only small effects on pain, we cannot confidently state that a causal relationship between PAF and pain sensitivity does not exist, and future research should explore these relationships with larger sample sizes, larger doses of nicotine, and alternative PAF modulators.”

Discussion final paragraph:

“We have shown that, compared to placebo, nicotine gum produced statistically significant increases global PAF speed and decreases pain ratings during prolonged heat pain. However, the effects of nicotine on heat pain were not mediated by changes in PAF. Therefore, we find no evidence that PAF is causally related to pain. The implication of this is that changing PAF may not be a useful target for pain modulation, because pain sensitivity may not be dependent on state changes in PAF. However, this is the first study to test modulation of PAF as a mechanism for reducing pain intensity. Moreover, while effects on PAF appear small but robust, effects on heat pain required control for confounding to be observed. More randomised experiments on the effects of nicotine that use larger sample sizes, higher nicotine doses, and pharmacokinetic tracking, whilst also reducing mediator measurement error are needed to confirm the present findings and uncover whether these factors account for the lack of mediation effect seen here.”

Previous comment 6) Magnitude of pain change

Previous comment (6) In this regard, I do not believe that an average *increase* of 0.05 / 10 (Nicotine post pre) can be considered a "reduction of pain ratings", regardless of the contrast with placebo (average increase of 0.24 / 10). This tiny effect size is more relevant in the context of the considerable inter-individual variation, in which subjects scored the same heat pain model anywhere from 1 to 10, and the same pressure pain model anywhere from 1 to 8.5. In this regard, the minimum clinically or experimentally important differences (MID) in pain ratings varies from study to study and across painful conditions but is rarely below 1 / 10 in a VAS or NRS scale, see f. ex. (Olsen et al., 2017). It is not my intention to question whether nicotine can function as an acute analgesic in general (as stated in the Discussion), but instead, if it worked as such under these very specific experimental conditions. I also acknowledge that the authors note this issue in two lines in the Discussion, but I believe that this is not weighed properly.

Our previous response included discussion of interpreting mean values, a correction to a table that showed the ”increase” erroneously displayed previously due to list-wise deletion in the analysis. We have further attempted to weigh this issue more thoroughly and to always highlight the nuances of our results, as seen in our response to your previous comment 5 above. In further consideration of the effect size, note that the bootstrapped 95% CI for the effect of gum on change in pain was [-1.28, -0.16], which indicates that the overall difference falls within this range when controlling for other factors in the model. Of course this means the difference may be as small as -0.16, but also may be as large as -1.28. Such an effect might have be considered clinically relevant. Replication of the results is therefore warranted.

Also, as outlined in our response to reviewer 2 comment 1, our intention was not to establish a clinical utility at this stage. We hoped to achieve some biological/mechanistic meaning in the present study, and if our present findings are replicated in future, even these small-magnitude effects can shape our understanding of relevant mechanisms underlying pain and aid the direction of future clinical perspectives (Edenberg, 2021; Ross & Bassett, 2024). Meaningfulness in clinical (e.g., MID) or public policy contexts should of course be in mind, but were not the focus of this present work.

Several additional changes were made to the manuscript to emphasise these points to the reader, which are also outlined in the second round of response to your first comment 5 above, as both this comment 6 and 5 focus on magnitude of pain change. We hope this point is now considered to be weighed properly.

Previous comment 7) Magnitude of PAF change

Previous comment (7) In line with the topic of effect sizes, average effect sizes for PAF in the study cited in the manuscript range from around 1 Hz (Boord et al., 2008; Wydenkeller et al., 2009; Lim et al., 2016), to 2 Hz (Foulds et al., 1994), compared with changes of 0.06 Hz (Nicotine post - pre) or -0.01 Hz (Placebo post - pre). MIDs are not so clearly established for peak frequencies in EEG bands, but they should be certainly larger than some fractions of a Hertz (which is considerably below the reliability of the measurement).

In our first response to this comment, we acknowledged this difference in magnitude, agreed that MIDs for PAF are not established, discussed the potential impact of bin size, and highlighted this issue in the revised manuscript text. Although, note that we have now slightly reduced the emphasis on the bin size:

“The ability to detect changes in PAF could be considerably impacted by the frequency resolution used during Fourier Transformations, an element that is overlooked in recent methodological studies on PAF calculation [16,95].”

In addition, we would now like to highlight some more details regarding the prior studies.

We aimed to determine whether nicotine gum could increase PAF in healthy, pain-free, non-smokers. In line with previous literature in non-smokers (Foulds et al., 1994; Harkrider and Champlin, 2001; Bowers et al., 2015), we contribute additional evidence that chewing 4 mg of nicotine gum produces small increases in PAF speed in non-smoking, nicotine-gum-naïve, pain-free, adult participants. The other three papers mentioned by the reviewer are not cited in our manuscript and compare healthy individuals to chronic pain patients (Boord et al., 2008; Wydenkeller et al., 2009; Lim et al., 2016), and are thus not relevant to this discussion on the effect of nicotine on PAF.

A cluster-based permutation analysis indicated that the change in wide window PAF (8-12 Hz) produced by nicotine, was most pronounced in a cluster of electrodes in the central-parietal region and a separate cluster of electrodes in the right-frontal region, rather than in the pre-registered sensorimotor ROI (i.e., Cz, C1, C2, C3, C4). The mediation analysis results showed minimal differences when these clusters of electrodes were used compared to global results (global: b = 0.085, p < .018), except for the expected stronger effect of nicotine on change in PAF alongside greater confidence in this effect (bs = 0.11-0.14, ps < .003). See Supplementary Material 3.8-3.10.

Previous work examining nicotine-induced changes in PAF in healthy non-smokers have used small samples (i.e. <= 20) with nicotine injections or patches (Foulds et al., 1994; Harkrider and Champlin, 2001), while a later investigation used 62 male participants and nicotine gum (Bowers et al., 2015). Therefore, the present study is the largest study to date on nicotine and PAF including non-smoking male and female participants. Bowers didn’t see effects as large as 1 or 2 Hz (approx. 10 or 20% increases) seen in studies with fewer participants, such as n=4 (Foulds et al., 1994) and n=20 (Harkrider & Champlin, 2001), and the magnitude and location of effect depended on the COMT (Bowers et al., 2015).

Bowers et al (2015) showed that the Met allele was related to nicotine-induced increases in PAF, whereas Val/Val homozygotes did not demonstrate PAF changes. In addition, the distribution of PAF increases varied depending on whether Met allele carriers were heterozygotes (i.e. Val/Met: frontal, central, and occipital electrodes) or homozygotes (i.e. Met/Met: parietal electrode). The largest difference between placebo and nicotine gum was 0.51 Hz (a 5.8% increase) at the Fz electrode for the Val/Met group and the smallest significant difference was 0.34 Hz (a 3.5% increase) at the Pz electrode for the Met/Met group.

This study from Bowers used 6mg of nicotine gum, whereas we used 4mg, which may contribute to the lower effect size seen in our study. Dose-dependent effects have not been assessed in non-smokers, but given the dose-dependent changes seen in smokers who abstained from cigarettes prior to EEG recording (Pickworth et al., 1989; Pickworth et al., 1988; Pickworth et al., 1986), the smaller effect sizes seen in the present study may be in line with Bowers study.

Though genetic analysis was not included in the present work, the use of a lower nicotine dose, inclusion of male and female participants, use of more electrodes (64 rather than 8), and unmeasured genetic variations in PAF’s response to nicotine could explain the smaller effect sizes compared to (Bowers et al., 2015).

We have written a condensed summary of this to include in the manuscript discussion:

”Research on nicotine-induced changes in PAF in healthy non-smokers has largely relied on small samples (≤20) using injections or patches [47,48], with Bowers and colleagues [38] providing the only larger study (n= 62 males) using 6 mg nicotine gum. Their results showed modest PAF increases (~0.34–0.51 Hz; 3.5– 5.8%) compared to the larger effects (1–2 Hz; ~10–20%) reported in earlier small-sample studies, with magnitude and scalp distribution influenced by COMT genotype: Met allele carriers exhibited nicotineinduced increases (Val/Met: frontal, central, occipital; Met/Met: parietal), while Val/Val homozygotes showed no change. The present study now the largest to include both male and female non-smokers found smaller effects, likely due to the lower nicotine dose (4 mg), consistent with dose-dependent PAF modulation reported in abstinent smokers [69]. Broader EEG coverage (64 vs. 8 electrodes), sex inclusion, and unmeasured genetic variation may also account for differences between the present study and Bowers and colleagues [38]. Interestingly, beyond nicotine’s main effect on PAF, our 2W-LCS mediation model indicated a significant influence of sex, with females showing greater PAF increases than males. Given that female participants were significantly lighter than males (Supplementary Material 3.4) and the model did not test the interaction between sex at birth and gum group, these finding should be interpreted cautiously and warrant further investigation.”

Previous comment 8) removing confounders calls to question robustness of the findings. Simmons paper

Previous comment (8) The authors also ran alternative statistical models to analyze the data and did not find consistent results in terms of PHP ratings (PAF modulation was still statistically significantly different). The authors attribute this to the necessity of controlling for covariates. Now, considering the effects sizes, aren't these statistically significant differences just artifacts stemming from the inclusion of too many covariates (Simmons et al., 2011)? How much influence should be attributable to depression and anxiety symptoms, stress, sleep quality and past pain, considering that these are healthy volunteers? Should these contrasting differences call the authors to question the robustness of the findings (i.e., whether the same data subjected to different analysis provides the same results), particularly when the results do not align with the preregistered hypothesis (PAF modulation should occur on sensorimotor ROIs)?

In addition to our previous response, we would like to add the following: Although we were previously unaware of the author recommendations from Simmons et al (2011) during initial preparation of this manuscript, we find we cover all points and have added a few improvements to ensure our adherence to this guideline is clear.

We cover all six recommendations for authors suggested in Simmons et al (2011):

(1) We decided to collect 62 participants prior to commencing data collection, this covered 60 participants in total, with two extra in case of incomplete data identified during data analysis.

(2) We had more than 20 participants per group. We have now outlined this decision in the methods section:

“The sample size was informed by resource and feasibility constraints [98] and aligns with or exceeds that of comparable studies in the field [38], covering 60 participants in total, with two extra in case of incomplete data identified during later data analysis.”

(3) We provide detailed methods, which outlines all the variables collected.

(4) We report all experimental conditions, and had no failed manipulations to report. We have now slightly adjusted the wording of our experimental protocol within the methods section to make this clear:

“Participants were randomly assigned to one of only two conditions, thus after the second resting-state EEG, either nicotine or placebo gum was administered with the chew procedure. Following completion of the chew procedure, the third resting state, the second pain assessments, and the fouth resting state were conducted.”

Regarding recommendation (5), listwise deletion was used, as already stated in the manuscript (see Methods, Statistical analysis, Mediation analysis, Assumptions), to exclude participants for whom only one timepoint was available in either the pain or PAF measures, and thus it is not possible to conduct analysis on participants with this missing data. Otherwise, no participants were removed for other reasons. 6) As we conducted analyses using pre-registered covariates determined based on a DAG, we repeated analyses without including these covariates in the form of RM-ANOVAs. The effect on PAF remains, however, as Simmons et al (2011) suggests, the fact we no longer observed a significant effect of gum on heat pain ratings may indicate that the finding is reliant on the presence of a covariate, which does not necessarily mean that the finding is not relevant. However, as reviewer 3 suggests, this should also cause us to question the robustness of the findings and the possibility of type 1 error. Therefore, we have adjusted text in the discussion as follows:

“This underscores the necessity of controlling for confounding variables, as nicotine may only produce pain reduction for those with higher stress, and calls for further investigation into the robustness of the effect of nicotine on heat pain ratings.”

Lastly, regarding the influence that should be attributable to our confounding health-related measures, given the healthy population, we still observe variation in several of these confounders. ’Healthy’ populations still score across a range on these scales, with cut-offs acting as suggestions for problematic symptomology. Assumptions testing confirmed the normality of these covariates, and lack of collinearity so that they could be included in our analyses. We have added a sentence to the Sample Characteristics in Results to outline the ranges reported for the confounding variables:

“Depressive symptoms ranged from 0-4 (out of a maximum of 6), anxiety from 0-6 (out of a maximum of 6), perceived stress from 2-18 (out of a maximum of 40), and sleep quality from 2-10 (out of a maximum of 10; i.e. “excellent sleep quality”).”

Previous comment 9) Exploratory sex analysis?

(9) Beyond that, I believe in some cases that the authors overreach in an attempt to provide explanations for their results. While I agree that sex might be a relevant covariate, I cannot say whether the authors are confirming a pre-registered hypothesis regarding the gender-specific correlation of PAF and pain, or if this is just a post hoc subgroup analysis. Given the large number of analyses performed (considering the main document and the supplementary files), caution should be exercised on the selective interpretation of those that align with the researchers' hypotheses.

To reiterate our previous response to this comment, we stated that sex was an exploratory analysis in the results and was chosen based on other PAF-pain literature, and had also adjusted part of the discussion to align with this. However, we have now seen the first paragraph of the discussion was not adjusted. Therefore, we hope the below edit has now adequately address the previous reviewer 3 comment 9:

“In addition, when assessing the whole sample, we found inconclusive evidence for 4) slower PAF speed at baseline being associated with higher pain ratings for both the heat and pressure pain models. However, during exploratory analysis we found moderate evidence that slower PAF speed at baseline is associated with higher heat pain ratings at baseline in males but not females. In contrast PAF was not associated with pressure pain ratings for males or females.”

References for response to reviewer 3

Boord P, Siddall PJ, Tran Y, Herbert D, Middleton J, Craig A. Electroencephalographic slowing and reduced reactivity in neuropathic pain following spinal cord injury. Spinal cord. 2008 Feb;46(2):118-23.

Bowers H, Smith D, De La Salle S, Choueiry J, Impey D, Philippe T, et al. COMT polymorphism modulates the resting-state EEG alpha oscillatory response to acute nicotine in male non-smokers. Genes, Brain and Behavior 2015;14:466–76.

Edenberg HJ. Perspective on beyond statistical significance: Finding meaningful effects. Complex Psychiatry 2021;7:1–8. https://doi.org/10.1159/000517237.

Foulds J, McSorley K, Sneddon J, Feyerabend C, Jarvis MJ, Russell MA. Effect of subcutaneous nicotine injections on EEG alpha frequency in non-smokers: A placebo-controlled pilot study. Psychopharmacology 1994;115:163–6.

Harkrider AW, Champlin CA. Acute effect of nicotine on non-smokers: III. LLRs and EEGs. Hearing Research 2001;160:99–110.

Lakens D. Sample size justification. Collabra: psychology. 2022 Mar 22;8(1):33267.

Lim M, Kim JS, Kim DJ, Chung CK. Increased low-and high-frequency oscillatory activity in the prefrontal cortex of fibromyalgia patients. Frontiers in human neuroscience. 2016 Mar 14;10:111.

Nosek BA, Ebersole CR, DeHaven AC, Mellor DT. The preregistration revolution. Proceedings of the National Academy of Sciences. 2018 Mar 13;115(11):2600-6.

Pickworth WB, Herning RI, Henningfield JE. Electroencephalographic effects of nicotine chewing gum in humans. Pharmacology Biochemistry and Behavior 1986;25:879–82.

Pickworth WB, Herning RI, Henningfield JE. Mecamylamine reduces some EEG effects of nicotine chewing gum in humans. Pharmacology, Biochemistry, and Behavior 1988;30:149–53.

Pickworth WB, Herning RI, Henningfield JE. Spontaneous EEG changes during tobacco abstinence and nicotine substitution in human volunteers. Journal of Pharmacology and Experimental Therapeutics 1989;251:976–82.

Ross LN, Bassett DS. Causation in neuroscience: keeping mechanism meaningful. Nature Reviews Neuroscience. 2024 Feb;25(2):81-90.

Simmons JP, Nelson LD, Simonsohn U. False-positive psychology: Undisclosed flexibility in data collection and analysis allows presenting anything as significant. Psychological science. 2011 Nov;22(11):1359-66.

Wydenkeller S, Maurizio S, Dietz V, Halder P. Neuropathic pain in spinal cord injury: significance of clinical and electrophysiological measures. European Journal of Neuroscience. 2009 Jul;30(1):91-9.