About Face: Is Virtual Group Delivery of Clinical Emotional Freedom Techniques (EFT) as Effective as Face-to-Face Group Delivery in Improving Psychological and Physiological Markers of Health?

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Abstract: (6 lines from end) - would rephrase as “...are similar to those found during in-person delivery, though not as large or clinically significant.”

Page 2 – rewrite first sentence for clarity: “Over 100 studies, including randomized control trials, have shown EFT to be effective....”

End of first para – if possible, cite something other than Church 2022, as it has already been cited multiple times. Something by Ortner?

Para 5 (and elsewhere in paper, ie Table 4): p<0.000 literally means a negative number. Should be p<0.001. Also, it would be useful to know how many sessions resulted in these outcomes.

Para 6 – the Bach et al study doesn’t need a full citation each time it is mentioned. After the first citation, can simply say “In the Bach study....”

Para 6 – it would be more helpful to explain here why two different scales were used, rather than waiting several paragraphs later.

Page 3 – line 13, “.... is considered clinically significant. However...”

P3, last sentence of Methodology: the dropout rate should be specified.

P4, Table 1 would be much easier to read if a vertical line separated the Virtual from the Face-to-Face data sets. Same with Tables 4 and 5. Also, the demographic differences between the two groups seem significant enough to wonder whether the groups are at all comparable: 42% with post-grad training vs. 20% (two very non-random samples). Also, are these clinicians – MSW, PhD – and if so, how might that skew the results?

P5, para 1 – although HADS and PHQ are not directly comparable, it might be interesting to compare the % change that was shown by each measure. Maybe not air-tight from the statistical POV, but comparison would be informative.

Page 5 – Why no F2F data in Tables parallel to Tables 2 and 3 for Virtual?  You could then go on to do the F2F vs. Virtual comparison; Tables 4 and 5 could include a comparison of the % changes from F2F versus Virtual for each of those five outcomes, as all seem to favor F2F by a significant amount that is not reflected in the stats, but are by % changes.

Page 7, para 1 – the section starting “However, this should be contextualized by the fact that...” belongs in the discussion section.

Page 7, para 2 – at first glance, the differences between the two group does appear to be quite significant; an approximately 35% reduction for F2F vs. 23% for virtual. Same for para 2 re: PTSD – a 23% drop in F2F vs a 10% drop in Virtual.

Page 8, para 4: A 50% response rate does not inspire confidence. These are not large epidemiological cohorts with an N in the 1000s, but a much smaller convenience sample where important skewing factors may not get balanced out. I think this problem has been minimized by the authors (despite the citations), and should be acknowledged more directly.

Page 8, para 5 – please clarify how participants were chosen, as this might impact why so many younger people chose Virtual. Page 3 doesn’t mention how the Bach study participants were chosen – were they psych grad students?  

Page 8, final para – “very brief subjective self-report measures” may have facilitated completion and compliance, but a 2-item PTSD scale, for example, is not likely to have strong validity. More information documenting the scales’ validity would be helpful.

Summary:
Overall, this is an important comparison study but it is limited in impact because of significant methodologic shortcomings dictated by the unavoidable realities of when and where the study took place. These are acknowledged by the authors, though their impact seems to have been minimized somewhat. By briefly outlining an ideal comparison study, the authors could help to contextualize their results. With these minor revisions, the paper will be worthy of publication.

 

Author Response

Reviewer 1

Abstract: (6 lines from end) - would rephrase as “...are similar to those found during in-person delivery, though not as large or clinically significant.”

Response to Reviewer: This phrase has been added.

Page 2 – rewrite first sentence for clarity: “Over 100 studies, including randomized control trials, have shown EFT to be effective....”

Response to Reviewer: This phrase has been added and the numbers updated.

End of first para – if possible, cite something other than Church 2022, as it has already been cited multiple times. Something by Ortner?

Response to Reviewer: We have selected an alternate reference.

Para 5 (and elsewhere in paper, ie Table 4): p<0.000 literally means a negative number. Should be p<0.001. Also, it would be useful to know how many sessions resulted in these outcomes.

Response to Reviewer: We have added a detailed description to the Methods section. And we have corrected the p value throughout the paper.

Para 6 – the Bach et al study doesn’t need a full citation each time it is mentioned. After the first citation, can simply say “In the Bach study....”

Response to Reviewer: We have made the suggested update to the references involved.

Para 6 – it would be more helpful to explain here why two different scales were used, rather than waiting several paragraphs later.

Response to Reviewer: We have moved the explanation to the recommended location.

Page 3 – line 13, “.... is considered clinically significant. However...”

Response to Reviewer: We have updated as recommended.

P3, last sentence of Methodology: the dropout rate should be specified.

Response to Reviewer: We have now specified the dropout rate in that location in the paper.

P4, Table 1 would be much easier to read if a vertical line separated the Virtual from the Face-to-Face data sets. Same with Tables 4 and 5. Also, the demographic differences between the two groups seem significant enough to wonder whether the groups are at all comparable: 42% with post-grad training vs. 20% (two very non-random samples). Also, are these clinicians – MSW, PhD – and if so, how might that skew the results?

Response to Reviewer: We have added this to the Tables. We have also clarified the demographics of the two samples. We have added further clarification to the Discussion section.

P5, para 1 – although HADS and PHQ are not directly comparable, it might be interesting to compare the % change that was shown by each measure. Maybe not air-tight from the statistical POV, but comparison would be informative.

Response to Reviewer: You are correct in that while this is not a direct comparison it is clinically useful, so we have added the % change.

Page 5 – Why no F2F data in Tables parallel to Tables 2 and 3 for Virtual?  You could then go on to do the F2F vs. Virtual comparison; Tables 4 and 5 could include a comparison of the % changes from F2F versus Virtual for each of those five outcomes, as all seem to favor F2F by a significant amount that is not reflected in the stats, but are by % changes.

Response to Reviewer: We have provided detailed data of the results of the virtual study in Tables 2 and 3, followed by summary data comparing F2F with virtual in Tables 4 and 5.

Page 7, para 1 – the section starting “However, this should be contextualized by the fact that...” belongs in the discussion section.

Response to Reviewer: We have moved this section to the Discussion.

Page 7, para 2 – at first glance, the differences between the two group does appear to be quite significant; an approximately 35% reduction for F2F vs. 23% for virtual. Same for para 2 re: PTSD – a 23% drop in F2F vs a 10% drop in Virtual.

Response to Reviewer: We have added statements in the Discussion section to underline this difference, and we discuss the possible reasons in that section too. 

Page 8, para 4: A 50% response rate does not inspire confidence. These are not large epidemiological cohorts with an N in the 1000s, but a much smaller convenience sample where important skewing factors may not get balanced out. I think this problem has been minimized by the authors (despite the citations), and should be acknowledged more directly.

Response to Reviewer: We have provided additional evidence contextualizing the dropout rate to the Discussion section.

Page 8, para 5 – please clarify how participants were chosen, as this might impact why so many younger people chose Virtual. Page 3 doesn’t mention how the Bach study participants were chosen – were they psych grad students?  

Response to Reviewer: We added these explanations to the Methods section and amplified them in the Discussion section. 

Page 8, final para – “very brief subjective self-report measures” may have facilitated completion and compliance, but a 2-item PTSD scale, for example, is not likely to have strong validity. More information documenting the scales’ validity would be helpful.

Response to Reviewer: Regarding the 2-item PTSD scale. Lang, the investigator who developed the 2-item PTSD scale, is a senior researcher at the US Veterans Administration, which was looking for a very brief instrument. She performed a meticulous study, and describes her methodology clearly in her paper that we reference. The brief version is valid and reliable, and has been used in many other studies.

Summary:

Overall, this is an important comparison study but it is limited in impact because of significant methodologic shortcomings dictated by the unavoidable realities of when and where the study took place. These are acknowledged by the authors, though their impact seems to have been minimized somewhat. By briefly outlining an ideal comparison study, the authors could help to contextualize their results. With these minor revisions, the paper will be worthy of publication.

Response to Reviewer: Thank you for this acknowledgment. We have endeavored to state the impact of these limitations clearly, and have added additional language in the Discussion section accordingly.

Reviewer 2 Report

Comments and Suggestions for Authors

Congratulations. The study is very interesting and deals with an important research area.

The abstract is too long; the most important results and characteristics of the study should be summarized much more concisely (e.g., participants, measurements).

The theoretical background is superficial; much deeper connections should be described based on previous research, which will help in interpreting the results. The theoretical background definitely needs to be expanded and interpreted. The same applies to the intervention section, which is also too short and not detailed enough.

A research permit is required, this needs to be added.

The presentation of the measuring instruments is not thorough, examples are needed, as well as the psychometric indicators of the instruments from previous samples, if available, or those obtained during the present research. This section also needs to be written much more precisely. 

I cannot interpret the P value in the table (it should be p) (Table 1). This is a revised version, but I cannot see what has been revised. 

A lot of data is presented, but its presentation and interpretation in the discussion are less deep. The data should be interpreted in a much more focused way.

Please include a separate section on limitations, covering both the methodology and the sample.

This study is a very good foundation, but it is not yet complete. A lot of work needs to be done to make it accessible to the reader and to highlight the work that has gone into it (which is considerable!) and its international significance.

Comments on the Quality of English Language

good

Author Response

Reviewer 2

Congratulations. The study is very interesting and deals with an important research area.

The abstract is too long; the most important results and characteristics of the study should be summarized much more concisely (e.g., participants, measurements).

Response to Reviewer: The abstract has been significantly shortened, and revised to present participants and measurements more concisely.

The theoretical background is superficial; much deeper connections should be described based on previous research, which will help in interpreting the results. The theoretical background definitely needs to be expanded and interpreted. The same applies to the intervention section, which is also too short and not detailed enough.

Response to Reviewer: We especially appreciated this review comment. It led us to recognized that our Background section was too short so we included theoretical underpinnings and summaries of previous research. We also expanded the intervention section to provide additional detail.

A research permit is required, this needs to be added.

Response to Reviewer: We have added the approval number.

The presentation of the measuring instruments is not thorough, examples are needed, as well as the psychometric indicators of the instruments from previous samples, if available, or those obtained during the present research. This section also needs to be written much more precisely. 

Response to Reviewer: We have added Chronbach’s alpha values and statatements of validity and reliability for all instruments. We have rewritten the section to be more precisely focused.

I cannot interpret the P value in the table (it should be p) (Table 1). This is a revised version, but I cannot see what has been revised. 

Response to Reviewer: The letter p has been lowercased, and the p values are clearly shown in the final column.

A lot of data is presented, but its presentation and interpretation in the discussion are less deep. The data should be interpreted in a much more focused way.

Response to Reviewer: We have revised the data presentation to focus on the results of the virtual group in two tables, followed by a comparison of virtual to face-to-face in the following two tables, plus the addition of figures to provide a focused graphical representation of the data.

Please include a separate section on limitations, covering both the methodology and the sample.

Response to Reviewer: We have significantly expanded the Limitations section to cover the primary limitations of the study in terms of both methodology and sample.

This study is a very good foundation, but it is not yet complete. A lot of work needs to be done to make it accessible to the reader and to highlight the work that has gone into it (which is considerable!) and its international significance.

Response to Reviewer: Thank you for those positive comments. In this revision, with the assistance of three able reviewers, we have striven to make it more accessible to the reader, and expanded, in the Discussion section, its international significance.

Reviewer 3 Report

Comments and Suggestions for Authors

The paper is a prospective study about the efficacy of virtual group administration of Clinical Emotional Freedom Techniques (EFT) as compared to face-to-face group administration and psychological outcomes such as PTSD, anxiety, depression, pain, and happiness. The study makes use of the data of online EFT workshop sessions organized during the COVID-19 epidemic and contrasts it with an older face-to-face study (Bach et al., 2019). The topic is actual and topical, since the shift to virtual therapies was made after 2020, and the findings show that virtual EFT can lead to a significant benefit, but it is not as substantial as face-to-face presentation, which is most likely to be justified by the factors of COVID-19. Overall, the quality of writing is high, and the tables and statistical analyses are well understood, and constraints (lack of randomization and control groups) are acknowledged. Still, several significant points could be amended, such as the methodology (e.g. convenience samples, lack of blinding but different types of scales were administered to each group), the interpretation of the findings (with potential confounders like the impact of COVID-19 on mental health across the world), and a more balanced discussion of the findings (with contradictory evidence in the greater literature on the topic of virtual therapies). In addition, the article has failed to explicitly indicate a theoretical framework either in support of EFT or its virtual version. EFT uses the concepts of cognitive-behavioral therapy, exposure therapy, and acupoint stimulation, which are not discussed here in any theoretical way. I would strongly suggest adding a dedicated section on the theoretical framework, possibly informed by models of energy psychology or biopsychosocial theories, to explain how EFT mechanisms (e.g., how somatic tapping can help deactivate the amygdala) can be extended to the virtual environment. This will strengthen the conceptual basis of the manuscript and could be employed to justify why virtual delivery may be as effective as face-to-face delivery. Generally, I would recommend some crucial amendments to address these gaps, enhance the transparency of the techniques, and tighten the discussion with critical analysis before the manuscript is ready to be published.

Abstract

The abstract includes a short overview of the introduction, objectives, methods, results, and conclusions of the study that are written in the conventional form. It is fair work highlighting the novelty of the virtual compared to face-to-face group EFT delivery, especially under the conditions of the COVID-19 shift to online learning, and specifies the use of such validated tools as PHQ-4, PCL, Happiness Scale, and Quick DASH. The results given are accompanied by adequate statistical significance (e.g., p-values of PTSD, anxiety, etc. improvements), and the findings are accompanied by references to the clinical applicability of the virtual EFT as a cost-effective alternative. However, the abstract can be improved by mentioning the key limitations directly, i.e., the inability to take physiological measures due to the COVID-19 lockdown and the use of a different anxiety/depression scale (HADS versus PHQ-4) that cannot be compared at all. That would be a less one-sided summary. We also have the percent changes in symptoms, which are given qualitatively, but an exact value can be given to correspond to the results section. The research question is well expressed, yet the abstract does not indicate the possibility of the pandemic that confounds the overall level of baseline symptoms, which is represented in the data (e.g., the lower level of baseline happiness in the virtual group). It would be more open to make an amendment to include a brief mention of these confounders so that the readers may place the results in perspective.

Background (Introduction)

The background section clearly indicates that the evidence base of EFT has been appropriately formulated by citing more than 100 studies, meta-analyses, and replication trials, which makes it evident that it is effective in both psychological (e.g., depression, PTSD) and physiological disorders. As such, it situates the study within the gap of insufficient investigations into virtual EFT, as the bulk of past investigations are in in-person delivery, and the study establishes the clinical significance of virtual delivery based on access and cost-efficiency. It is sensible and logical to substitute the discourse of the pivot to online platforms of the COVID-19 pandemic, and it is reasonable to duplicate Bach et al. (2019). However, this section is not so much in detail that it outlines how tapping of the acupoints along with cognitive reframing can work, and does not provide a theoretical framework, e.g., the polyvagal theory or stress response models, to buttress the justification of the potential equivalence of the virtual delivery. This omission makes the background look quite descriptive as opposed to analytical. In addition, it mentions the shift to virtual therapy during COVID-19, yet it may also have more global sources on the effectiveness of virtual psychotherapy (e.g., meta-analyses that report the effectiveness of CBT or group therapy) to enhance the argument. These are clear objectives, and the hypotheses (e.g., expecting a similar efficacy) are not clearly mentioned. I would include a subsection on theoretical underpinnings that could relate EFT to models of somatic experiencing or emotional regulation, and which could hypothesize potential virtual versus in-person differences in the consideration of interpersonal dynamics.

Methodology

The study design is a prospective study of convenience where 172 virtual participants took four online EFT workshops as compared to the past in-person sample (N=203). Ethical approval and informed consent are present, and measures (PHQ-4 to evaluate anxiety/depression, PCL on PTSD, Happiness Scale, QuickDASH on pain) are appropriate and well explained, and scoring information was given. The use of Wilcoxon signed-rank tests is suitable to analyze non-normal data, and the inability to involve physiological measurement due to COVID-19 is taken into account. Nevertheless, the design needs considerable amendments because of several reasons: the design is not randomized and lacks a control or wait-list group, which makes it impossible to conclude what causes EFT (e.g., such improvements may be a consequence of extraneous factors such as group support). It is a convenience sample that is prone to bias towards EFT enthusiasts and demographics (e.g., younger virtual group) are reported but not controlled in the analyses. The switch from HADS (in-person) to PHQ-4 (virtual) prevents direct comparisons of anxiety/depression. The p-values and percent changes in the manuscript are not accompanied by the statistical comparisons between the groups; it is not statistically tested, this should be stated, or it will need to be explained or indirectly compare the magnitude of effect (e.g., Cohen's d). Response rates are not bad (53 percent virtual, 50 percent in-person), although they can be biased by attrition; there is no dropout analysis. I would give additional details regarding the recruitment and inclusion/exclusion criteria and power calculations (i.e., was N=172 sufficient to detect differences? As a way of strengthening, suggest applying the sensitivity analyses method of confounders like COVID stress.

Clinical EFT Intervention

The section describes the intervention where those who teach have been trained in Clinical EFT and the EFT Manual, third edition (Church, 2013). The Borrowing Benefits protocol has been outlined with emphasis on peer-to-peer coaching and group self-application, with 12 hours being allocated to demonstrations and practice. It purports adherence to the manual and assumes that the virtual presentation is the mirror image of the face-to-face presentation. This provides a repeatable overview, and that is an advantage. The description, though, is not particular to the way the virtual delivery was adjusted- e.g., what platform was employed (Zoom?), the way technical issues were addressed, or how to make participation happen in a digital environment. It does not discuss the organization of the sessions (e.g., breakout rooms to practice) or the maintenance of fidelity (e.g., recording or checklists). The theoretical basis of the postulation of Borrowing Benefits (e.g., lessened cortisol through vicarious learning) is stated but not discussed. Because the study is virtual versus in-person, the section should elaborate on the potential differences, e.g., lack of nonverbal cues on the internet. I would recommend that it be updated to include a protocol flowchart, details of virtual modifications, and versioning with a theoretical model (e.g., social learning theory of group effects) to explain why the same benefits would be sustained in a virtual environment.

Results

The results are presented in a conversational form with tables of the results at the baseline (Table 1), comparison of changes before and after (Tables 2-5), and comparison of group results during a period of time (Table 6). Statistical tests (i.e., Wilcoxon, Mann-Whitney, etc.) are appropriate, and significant results (i.e., decreases in PTSD, pain; increases in happiness) are presented with p-values and percent changes. It has been noted that baseline differences exist (e.g., more pain/PTSD in the in-person group), and the effects of the gains are well-documented at six months. However, effect size could be used in the section to interpret clinical significance as opposed to p-values since percent changes do not match (ex, 60% in-person versus -36% virtual). No visual aids (e.g., line graphs of symptom curves) are used, and these could be used to interpret them. The effect of COVID on virtual baselines (e.g., worse happiness) is mentioned briefly and is not further examined - e.g., no subgroup by country or degree of the pandemic. The problem of follow-up attrition is not covered here (but is discussed below). Provide effect size, graphical, and exploratory confounder analysis to ensure results are stronger and interpretable.

Discussion

The findings are summarized in the discussion, noting that both types of delivery have made significant progress, and that the comparatively less critical virtual implications can be placed into a context about the mental impact of COVID-19 (e.g., alluding to Greyling et al., 2020). Limitations are openly debated, including the absence of randomization, self-reporting bias, scale discrepancies, and pandemic confounding, and some speculate on how the future study would look (e.g., qualitative perceptions, epigenetic testing). It can have significant implications for EFT training and cost-effectiveness. However, this section makes an overgeneralization of equivalence between virtual and in-person without supplying sufficient evidence- e.g., percent changes are lower virtually, but that is explained by COVID-19 without considering alternative possibilities of worse therapeutic alliance online (cite more on this, e.g., Connolly et al., 2020). Negative evidence (e.g., some studies that show inferior virtual performance of group therapies) is not discussed and, therefore, can lead to bias. Lack of a theoretical guide undermines explanations of mechanisms. Check to reconcile positives and critical evaluation, integrate contradictory evidence, and provide a paragraph that ties the findings to the theory (e.g., how virtual EFT still activates somatic-emotional systems).

Conclusion

The conclusion briefly reiterates the key findings, with a particular focus on the efficacy of virtual EFT in the treatment of common symptoms and its potential to be used as a first-line intervention. It holds more implications for the delivery of mental health following COVID-19. However, it may be less categorical, taking into consideration that virtual effects were usually minor and proposing more RCTs. The argument to implement virtual EFT in primary care is convincing, yet it should refer to guidelines in a more distinct way. Add a wink to the proposed theoretical framework to put future directions in perspective.

References

The sources are widespread in scope, as they refer to EFT-specific studies and overall COVID-19/therapy sources. That list is, however, incomplete in the given document (until reference 30), so it was not entirely revised. Change the publications to include the latest publications on virtual group therapy up to the year 2022.

Author Response

The paper is a prospective study about the efficacy of virtual group administration of Clinical Emotional Freedom Techniques (EFT) as compared to face-to-face group administration and psychological outcomes such as PTSD, anxiety, depression, pain, and happiness. The study makes use of the data of online EFT workshop sessions organized during the COVID-19 epidemic and contrasts it with an older face-to-face study (Bach et al., 2019). The topic is actual and topical, since the shift to virtual therapies was made after 2020, and the findings show that virtual EFT can lead to a significant benefit, but it is not as substantial as face-to-face presentation, which is most likely to be justified by the factors of COVID-19. Overall, the quality of writing is high, and the tables and statistical analyses are well understood, and constraints (lack of randomization and control groups) are acknowledged. Still, several significant points could be amended, such as the methodology (e.g. convenience samples, lack of blinding but different types of scales were administered to each group), the interpretation of the findings (with potential confounders like the impact of COVID-19 on mental health across the world), and a more balanced discussion of the findings (with contradictory evidence in the greater literature on the topic of virtual therapies). In addition, the article has failed to explicitly indicate a theoretical framework either in support of EFT or its virtual version. EFT uses the concepts of cognitive-behavioral therapy, exposure therapy, and acupoint stimulation, which are not discussed here in any theoretical way. I would strongly suggest adding a dedicated section on the theoretical framework, possibly informed by models of energy psychology or biopsychosocial theories, to explain how EFT mechanisms (e.g., how somatic tapping can help deactivate the amygdala) can be extended to the virtual environment. This will strengthen the conceptual basis of the manuscript and could be employed to justify why virtual delivery may be as effective as face-to-face delivery. Generally, I would recommend some crucial amendments to address these gaps, enhance the transparency of the techniques, and tighten the discussion with critical analysis before the manuscript is ready to be published.

Response to Reviewer: We have adjusted the language as suggested, to emphasize that this was a convenience sample, that different scales were used for anxiety and depression, and underline the limitations such as the lack of a control group, blinding and randomization. We have added extra material on potential confounders especially COVID-19. We have added a dedicated section to EFTs theoretical framework in the Background section that introduces the paper. This includes a summary of its physiological mechanisms of action, as well as adding the research question of whether this theoretical framework carries over to the virtual environment.

Abstract

The abstract includes a short overview of the introduction, objectives, methods, results, and conclusions of the study that are written in the conventional form. It is fair work highlighting the novelty of the virtual compared to face-to-face group EFT delivery, especially under the conditions of the COVID-19 shift to online learning, and specifies the use of such validated tools as PHQ-4, PCL, Happiness Scale, and Quick DASH. The results given are accompanied by adequate statistical significance (e.g., p-values of PTSD, anxiety, etc. improvements), and the findings are accompanied by references to the clinical applicability of the virtual EFT as a cost-effective alternative. However, the abstract can be improved by mentioning the key limitations directly, i.e., the inability to take physiological measures due to the COVID-19 lockdown and the use of a different anxiety/depression scale (HADS versus PHQ-4) that cannot be compared at all. That would be a less one-sided summary. We also have the percent changes in symptoms, which are given qualitatively, but an exact value can be given to correspond to the results section. The research question is well expressed, yet the abstract does not indicate the possibility of the pandemic that confounds the overall level of baseline symptoms, which is represented in the data (e.g., the lower level of baseline happiness in the virtual group). It would be more open to make an amendment to include a brief mention of these confounders so that the readers may place the results in perspective.

Response to Reviewer: We have covered the above points briefly in the Abstract. However, the other reviewers requested a briefer rather than a more expansive Abstract. We could not do both, so we opted to abridge the Abstract and address these points in the body of the paper.

Background (Introduction)

The background section clearly indicates that the evidence base of EFT has been appropriately formulated by citing more than 100 studies, meta-analyses, and replication trials, which makes it evident that it is effective in both psychological (e.g., depression, PTSD) and physiological disorders. As such, it situates the study within the gap of insufficient investigations into virtual EFT, as the bulk of past investigations are in in-person delivery, and the study establishes the clinical significance of virtual delivery based on access and cost-efficiency. It is sensible and logical to substitute the discourse of the pivot to online platforms of the COVID-19 pandemic, and it is reasonable to duplicate Bach et al. (2019). However, this section is not so much in detail that it outlines how tapping of the acupoints along with cognitive reframing can work, and does not provide a theoretical framework, e.g., the polyvagal theory or stress response models, to buttress the justification of the potential equivalence of the virtual delivery. This omission makes the background look quite descriptive as opposed to analytical. In addition, it mentions the shift to virtual therapy during COVID-19, yet it may also have more global sources on the effectiveness of virtual psychotherapy (e.g., meta-analyses that report the effectiveness of CBT or group therapy) to enhance the argument. These are clear objectives, and the hypotheses (e.g., expecting a similar efficacy) are not clearly mentioned. I would include a subsection on theoretical underpinnings that could relate EFT to models of somatic experiencing or emotional regulation, and which could hypothesize potential virtual versus in-person differences in the consideration of interpersonal dynamics.

Response to Reviewer: We have added a section about the recommended stress models, the theoretical and biophysical underpinnings of EFT and other somatic therapies, as well as an explicit hypothesis related to investigating whether virtual treatment can produce a similar calming effect. We have added a summary of the most recent systematic review and meta-analysis comparing virtual CBT to in-person treatment.

Methodology

The study design is a prospective study of convenience where 172 virtual participants took four online EFT workshops as compared to the past in-person sample (N=203). Ethical approval and informed consent are present, and measures (PHQ-4 to evaluate anxiety/depression, PCL on PTSD, Happiness Scale, QuickDASH on pain) are appropriate and well explained, and scoring information was given. The use of Wilcoxon signed-rank tests is suitable to analyze non-normal data, and the inability to involve physiological measurement due to COVID-19 is taken into account. Nevertheless, the design needs considerable amendments because of several reasons: the design is not randomized and lacks a control or wait-list group, which makes it impossible to conclude what causes EFT (e.g., such improvements may be a consequence of extraneous factors such as group support). It is a convenience sample that is prone to bias towards EFT enthusiasts and demographics (e.g., younger virtual group) are reported but not controlled in the analyses. The switch from HADS (in-person) to PHQ-4 (virtual) prevents direct comparisons of anxiety/depression. The p-values and percent changes in the manuscript are not accompanied by the statistical comparisons between the groups; it is not statistically tested, this should be stated, or it will need to be explained or indirectly compare the magnitude of effect (e.g., Cohen's d). Response rates are not bad (53 percent virtual, 50 percent in-person), although they can be biased by attrition; there is no dropout analysis. I would give additional details regarding the recruitment and inclusion/exclusion criteria and power calculations (i.e., was N=172 sufficient to detect differences? As a way of strengthening, suggest applying the sensitivity analyses method of confounders like COVID stress.

Response to Reviewer: We agree that the absence of randomization and a control or wait-list group precludes causal attribution of observed improvements exclusively to EFT. Accordingly, the study was designed and is interpreted as a prospective, pragmatic effectiveness study, focused on within-participant change following EFT workshops delivered under real-world conditions, rather than as a randomized efficacy trial. This limitation is now stated explicitly in the Design and Limitations sections. 

We appreciate the suggestion to conduct sensitivity analyses for contextual confounders such as COVID-related stress. However, specific measures of COVID-related stressors were not collected prospectively, precluding formal sensitivity modeling. Instead, COVID-19 is treated as a shared contextual factor influencing the virtual cohort, and its potential impact is discussed as a limitation.

Importantly, the primary focus of the study was on within-participant change over time within each delivery modality, rather than on causal attribution or adjustment for time-varying external stressors. Future studies incorporating dedicated measures of pandemic-related stress and other confounders would allow more formal sensitivity analyses, and we have recommended this in the Discussion section.

We have added a power calculation as well as Cohen’s d.

Clinical EFT Intervention

The section describes the intervention where those who teach have been trained in Clinical EFT and the EFT Manual, third edition (Church, 2013). The Borrowing Benefits protocol has been outlined with emphasis on peer-to-peer coaching and group self-application, with 12 hours being allocated to demonstrations and practice. It purports adherence to the manual and assumes that the virtual presentation is the mirror image of the face-to-face presentation. This provides a repeatable overview, and that is an advantage. The description, though, is not particular to the way the virtual delivery was adjusted- e.g., what platform was employed (Zoom?), the way technical issues were addressed, or how to make participation happen in a digital environment. It does not discuss the organization of the sessions (e.g., breakout rooms to practice) or the maintenance of fidelity (e.g., recording or checklists). The theoretical basis of the postulation of Borrowing Benefits (e.g., lessened cortisol through vicarious learning) is stated but not discussed. Because the study is virtual versus in-person, the section should elaborate on the potential differences, e.g., lack of nonverbal cues on the internet. I would recommend that it be updated to include a protocol flowchart, details of virtual modifications, and versioning with a theoretical model (e.g., social learning theory of group effects) to explain why the same benefits would be sustained in a virtual environment.

Response to Reviewer: We have added the information about fidelity checking, the Zoom platform, and about how technical issues were addressed. In the Discussion, we have covered the reviewer’s recommended review of how we encouraged engaged participation, as well as virtual modifications, and a discussion of group effects. We have also added the most recent meta-analytical data on the social learning theory of group effects in a virtual environment to the Discussion.

Results

The results are presented in a conversational form with tables of the results at the baseline (Table 1), comparison of changes before and after (Tables 2-5), and comparison of group results during a period of time (Table 6). Statistical tests (i.e., Wilcoxon, Mann-Whitney, etc.) are appropriate, and significant results (i.e., decreases in PTSD, pain; increases in happiness) are presented with p-values and percent changes. It has been noted that baseline differences exist (e.g., more pain/PTSD in the in-person group), and the effects of the gains are well-documented at six months. However, effect size could be used in the section to interpret clinical significance as opposed to p-values since percent changes do not match (ex, 60% in-person versus -36% virtual). No visual aids (e.g., line graphs of symptom curves) are used, and these could be used to interpret them. The effect of COVID on virtual baselines (e.g., worse happiness) is mentioned briefly and is not further examined - e.g., no subgroup by country or degree of the pandemic. The problem of follow-up attrition is not covered here (but is discussed below). Provide effect size, graphical, and exploratory confounder analysis to ensure results are stronger and interpretable.

Response to Reviewer: We have added effect size calculations as both statistics and graphics. Two figures have been added, one showing symptom trajectories by delivery modality, and secondly effect sizes by outcome and group. Individual participant country labels were not available for all participants in the original dataset from the original Bach et al. study, so inferential baseline comparisons with virtual treatment by country (e.g., Kruskal–Wallis) could not be conducted. The Discussion now includes the effect of COVID on baseline mental health. It also has an extended section on follow-up attrition.

Discussion

The findings are summarized in the discussion, noting that both types of delivery have made significant progress, and that the comparatively less critical virtual implications can be placed into a context about the mental impact of COVID-19 (e.g., alluding to Greyling et al., 2020). Limitations are openly debated, including the absence of randomization, self-reporting bias, scale discrepancies, and pandemic confounding, and some speculate on how the future study would look (e.g., qualitative perceptions, epigenetic testing). It can have significant implications for EFT training and cost-effectiveness. However, this section makes an overgeneralization of equivalence between virtual and in-person without supplying sufficient evidence- e.g., percent changes are lower virtually, but that is explained by COVID-19 without considering alternative possibilities of worse therapeutic alliance online (cite more on this, e.g., Connolly et al., 2020). Negative evidence (e.g., some studies that show inferior virtual performance of group therapies) is not discussed and, therefore, can lead to bias. Lack of a theoretical guide undermines explanations of mechanisms. Check to reconcile positives and critical evaluation, integrate contradictory evidence, and provide a paragraph that ties the findings to the theory (e.g., how virtual EFT still activates somatic-emotional systems).

Response to Reviewer: We have updated our review of percent changes as recommended by the reviewer. We have cited additional research on the relative efficacy of virtual versus online treatment. We have also added negative evidence on inferior virtual performance when Zoom is used. We have tied the Discussion back into the theoretical underpinnings of EFT introduced into the Background section of the paper.

Conclusion

The conclusion briefly reiterates the key findings, with a particular focus on the efficacy of virtual EFT in the treatment of common symptoms and its potential to be used as a first-line intervention. It holds more implications for the delivery of mental health following COVID-19. However, it may be less categorical, taking into consideration that virtual effects were usually minor and proposing more RCTs. The argument to implement virtual EFT in primary care is convincing, yet it should refer to guidelines in a more distinct way. Add a wink to the proposed theoretical framework to put future directions in perspective.

Response to Reviewer: We have made the conclusions less categorical. We have also proposed RCTs as well as studies to test the theoretical underpinnings of EFT and develop consensus treatment guidelines.

References

The sources are widespread in scope, as they refer to EFT-specific studies and overall COVID-19/therapy sources. That list is, however, incomplete in the given document (until reference 30), so it was not entirely revised. Change the publications to include the latest publications on virtual group therapy up to the year 2022.

Response to Reviewer: We have updated the paper to include several studies of virtual group and individual therapy, plus the relevant references.

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

The necessary modifications and repairs have been carried out. 

Accepted. 

Reviewer 3 Report

Comments and Suggestions for Authors

I gave very detailed comments, but the authors didn't take them seriously to address the issues.