Effect of Brief Guided Imagery on Short-Term Outcomes in Patients Undergoing First Elective Total Knee Arthroplasty: Randomized Controlled Trial

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Given the very interesting topic and its potential practical implications, I reviewed the paper with particular interest and attention. In general, I think the material contains good elements that need to be better contextualized with a contemporary approach to pain and rehabilitation and more precisely supported by adequate statistical procedures. I have some specific comments, questions and suggestions:

The standard is to use keywords different from those in the title, or at least synonyms.

Line 136 - You can list references more briefly: [15-18]

Chart 1. Flowchart of the study: you should use “Orthopedic surgeon” instead of “Doctor’s”.

Paragraph from line 193 to line 200: I see no reason for the contents to be expressed in the future tense. This makes it seem as if this passage was written as part of a research proposal or for consideration by an ethics committee, rather than as content that has been fully developed, measured, and completed. This particularly applies to lines 196-198; was the distribution shown to be normal or not? Have you performed a statistical analysis of the normality of the distribution (e.g. Kolmogorov-Smirnov test, visual inspection of histograms and Q-Q plots)? Later you state (line 221, line 258) that you used repeated measures ANOVA; however, perhaps you should have applied its nonparametric equivalent - the Friedman test. With such a small sample, I find it hard to believe that the distribution was normal. Please check, calculate, and provide evidence in the material; it is now an unwritten rule that this is necessary, as well as reporting effect sizes with statistical significance, which you did well and consistently in your paper.

In order to be consistent with the contemporary approach to pain science and therapy, please include a paragraph in the Discussion that places your research and results in the context of a biopsychosocial approach. There is a significant amount of recent literature on the biopsychosocial approach to pain, e.g.:

van Dijk, H.; Köke, A.J.A.; Elbers, S.; Mollema, J.; Smeets, R.J.E.M.; Wittink, H. Physiotherapists Using the Biopsychosocial Model for Chronic Pain: Barriers and Facilitators—A Scoping Review. Int. J. Environ. Res. Public Health 2023, 20, 1634. https://doi.org/10.3390/ijerph20021634

Samoborec S, Ruseckaite R, Ayton D, Evans S. Biopsychosocial factors associated with non-recovery after a minor transportrelated injury: a systematic review. PLoS One 2018; 13: e0198352.

Wijma A.J., Wilgen van , C.P., Meeus, M. & Nijs, J. (2015) Clinical biopsychosocial physiotherapy assessment of patients with chronic pain: the first step in pain neuroscience education, Physiotherapy theory and practice, (32) 368-384. https://doi.org/10.1080/09593985.2016.1194651 

Overall, I must recommend major revisions, primarily based on potentially inappropriate statistical analysis. 

Author Response

Comments and Suggestions for Authors

Given the very interesting topic and its potential practical implications, I reviewed the paper with particular interest and attention.

Reply: We thank the reviewer for their thoughtful and encouraging feedback on the topic and its potential clinical relevance.

 

In general, I think the material contains good elements that need to be better contextualized with a contemporary approach to pain and rehabilitation and more precisely supported by adequate statistical procedures.

Reply: We significantly revised the paper, including the contemporary approach to pain and the description of the statistical analysis. We hope that it is now suitable for publication.

 

The standard is to use keywords different from those in the title, or at least synonyms.

Reply: We changed most keywords; the only one uncaged was brief guided imagery.

 

Line 136 - You can list references more briefly: [15-18]

Reply: Changed

 

Chart 1. Flowchart of the study: you should use “Orthopedic surgeon” instead of “Doctor’s”.

Reply: Changed

 

Paragraph from line 193 to line 200: I see no reason for the contents to be expressed in the future tense. This makes it seem as if this passage was written as part of a research proposal or for consideration by an ethics committee, rather than as content that has been fully developed, measured, and completed.

Reply: We apologize for this mistake. We changed the tense of this paragraph to past.

 

This particularly applies to lines 196-198; was the distribution shown to be normal or not? Have you performed a statistical analysis of the normality of the distribution (e.g. Kolmogorov-Smirnov test, visual inspection of histograms and Q-Q plots)? Later you state (line 221, line 258) that you used repeated measures ANOVA; however, perhaps you should have applied its nonparametric equivalent - the Friedman test. With such a small sample, I find it hard to believe that the distribution was normal. Please check, calculate, and provide evidence in the material; it is now an unwritten rule that this is necessary, as well as reporting effect sizes with statistical significance, which you did well and consistently in your paper.

Reply: We changed the description of data analysis in accord with reviewer's recommendations.

 

In order to be consistent with the contemporary approach to pain science and therapy, please include a paragraph in the Discussion that places your research and results in the context of a biopsychosocial approach. There is a significant amount of recent literature on the biopsychosocial approach to pain, e.g.:

• van Dijk, H.; Köke, A.J.A.; Elbers, S.; Mollema, J.; Smeets, R.J.E.M.; Wittink, H. Physiotherapists Using the Biopsychosocial Model for Chronic Pain: Barriers and Facilitators—A Scoping Review. Int. J. Environ. Res. Public Health 2023, 20, 1634. https://doi.org/10.3390/ijerph20021634
• Samoborec S, Ruseckaite R, Ayton D, Evans S. Biopsychosocial factors associated with non-recovery after a minor transportrelated injury: a systematic review. PLoS One 2018; 13: e0198352.
• Wijma A.J., Wilgen van, C.P., Meeus, M. & Nijs, J. (2015) Clinical biopsychosocial physiotherapy assessment of patients with chronic pain: the first step in pain neuroscience education, Physiotherapy theory and practice, (32) 368-384. https://doi.org/10.1080/09593985.2016.1194651 

Reply: We added the requested paragraph to the Discussion section.

Reviewer 2 Report

Comments and Suggestions for Authors

In the attached file

Comments for author File: Comments.pdf

Comments on the Quality of English Language

Passages allowing for identification of the study site and usage the Hebrew language should be either modified or removed.

Author Response

Higlights

Long dashes usually used by AI are visible.

Reply: In the original text submitted to the journal there were no long dashes. They probably were added during conversion of the text to the journal format. During the preparation of the manuscript, we used AI tools to edit and improve grammar of the paper. Therefore, it was clearly stated in the declaration of AI used at the end of the manuscript.

 

Abstract

 “Brief GI involved daily 2-minute visualisation exercises delivered via audio recordings” – The duration of the intervention is not specified (i.e. for how many days the exercises were performed).

Reply: We added missing information to the Abstract.

 

In addition, the phrase “visualisation … delivered via audio recordings” is imprecise and should be replaced with “visualisation guided via audio recordings” to more accurately reflect the nature of the intervention.

Reply: Corrected.

 

“…assessed preoperatively and up to 6 weeks postoperatively” – This statement requires clarification. The authors should specify the exact number and timing of postoperative assessments conducted within the 6-week period (e.g. at 2, 4, and 6 weeks postoperatively).

Reply: We changed the abstract to meet the reviewer's recommendations.

 

If addressing the above issues results in exceeding the abstract word limit, the sentence “Further research is needed to explore long-term effects and optimal implementation strategies” may be omitted from the Abstract.

Reply: Omitted.

 

Introduction

In paragraph 4, if the three cited studies represent all available studies of adequate quality on guided imagery, this should be explicitly stated to indicate that the existing evidence base is limited.

Reply: We agree that the current evidence base for brief guided imagery in musculoskeletal and postoperative pain is limited. The three studies we cited represent the primary available investigations of adequate methodological quality examining brief guided imagery in chronic pain populations. To address this, we have revised the relevant section of the Introduction to explicitly state that the existing literature is sparse and that current findings should be interpreted within the context of a limited but emerging evidence base. The revised text now clarifies that only a small number of studies have evaluated brief guided imagery and that further research is needed to strengthen the evidence supporting its use.

 

In this case, the first sentence of paragraph 4 should be revised to read: “There is also limited information on the effect of GI on postoperative pain.”

Reply: We added this sentence.

 

Matrial and methods

Sample

The manuscript specifies the exact study location (“Barzilai University Medical Center, Ashkelon, Israel”). The authors should consider removing information that allows direct identification of the study site, as this may influence readers’ interpretation of the results. This issue applies not only to the Sample section, but also to the Abstract, Ethical considerations, and Intervention sections, where the study location is likewise identifiable.

Reply: We appreciate the reviewer’s thoughtful comment regarding the identification of the study site. To address this concern, we removed the hospital name from the Abstract and Intervention to avoid unnecessary emphasis on the specific institution. However, we believe it is important to retain the study site in the Methods and Ethical Considerations sections. Reporting the exact location is consistent with standard research transparency requirements, including CONSORT guidelines, and is necessary for reproducibility, contextual interpretation of the clinical setting, and accurate reporting of institutional ethics approval. We therefore kept the site information in these sections while ensuring it does not influence the interpretation of the study outcomes.

 

In addition, in the Inclusion criteria, the term “Hebrew” should be replaced with “native language” to avoid unnecessary specification of a particular language. The same issue applies to the description of the WOMAC scale in the Questionnaires section.

Reply: Thank you for this comment. We agree that unnecessary language‑based exclusion should be avoided; however, in this study the specification of “Hebrew” is intentional and methodologically required. All outcome measures used in the trial (NPRS, NFRS, WOMAC, STAI) were administered in their validated Hebrew versions, and the psychometric properties we report refer specifically to these Hebrew adaptations. Because Israel is a multilingual country, replacing “Hebrew” with “native language” would not ensure that participants could reliably complete the validated Hebrew questionnaires used in this study. For this reason, the inclusion criterion “ability to communicate in Hebrew” is necessary and appropriate. To improve clarity, we added a brief explanation in the Methods section indicating that all study instruments were administered in Hebrew.

 

Inclusion and exclusion criteria

The inclusion and exclusion criteria are described insufficiently. For example, it is unclear how functional independence was assessed prior to the operation. It is also highly likely that the exclusion criteria included “other factors preventing surgery,” but this is not explicitly stated. Furthermore, the rationale for the chosen age limits is not provided; while readers can infer the reasoning, a clear explanation would greatly improve transparency and the interpretability of the study.

Reply: Thank you for this important comment. We have expanded the Inclusion and Exclusion criteria to clarify how functional independence was assessed, to specify that patients unable to undergo surgery for medical or surgical reasons were excluded, and to explain the rationale for the age limits. Functional independence was determined based on the orthopedic surgeon’s preoperative clinical evaluation and patient self‑report regarding independent ambulation and activities of daily living. We also added a brief justification for the 50–85 age range, which reflects the typical demographic of patients undergoing elective TKA and ensures the use of validated outcome measures in this age group. These clarifications have now been incorporated into the Methods section to improve transparency and interpretability.

 

“…and having a smartphone with a voice app” – This selection criterion appears arbitrary and unnecessarily restrictive. If a participant does not own a smartphone, it would be feasible in the context of a controlled trial to provide an alternative audio-playing device, ensuring inclusivity without compromising the intervention.

Reply: In our setting, the vast majority of adults undergoing elective TKA routinely use smartphones, and all study materials, including the guided imagery audio recordings, were designed for smartphone delivery. Because the study had no external funding, it was not feasible to purchase or supply alternative audio‑playing devices. For this reason, smartphone ownership was included as a practical requirement to ensure participants could reliably access the intervention. Importantly, no eligible patient was excluded solely due to lack of a smartphone, as all individuals approached during recruitment owned one. We have clarified this rationale in the Methods section to improve transparency.

 

Sample size estimation

The sample size calculation is useful. However, if the authors undertook this effort, it is unclear why it was not performed for all outcome measures. Instead, they appear to assume that 20 participants per group are sufficient for WOMAC and STAI. Why? The authors should present sample size estimations for all outcome measures used in the study. Only this approach would allow a meaningful and reliable interpretation of all results.

Reply: In clinical trials, sample size calculations are conventionally performed for the primary outcome measure, which in our study was postoperative pain assessed by the NPRS. This approach is consistent with CONSORT recommendations and standard methodological practice, as powering a study for multiple secondary outcomes is generally not required and is often not feasible. The WOMAC and STAI were included as secondary exploratory outcomes, and the study was not designed or intended to be powered specifically for these measures. Our goal was to ensure adequate power to detect clinically meaningful differences in the primary outcome, while evaluating secondary outcomes to generate preliminary insights. We have clarified this rationale in the Methods section to improve transparency.

 

Recruitment

The manuscript states that patients were randomized to the intervention and control groups using concealed allocation by the research assistant. However, this description of the randomisation procedure is insufficient and requires further detail. The authors should specify the method used to generate the random sequence, how allocation concealment was ensured, and whether any steps were taken to prevent selection bias.

Reply: Thank you for this important comment. We have expanded the description of the randomization procedure to clarify the method used to generate the random sequence, the process of allocation concealment, and the steps taken to minimize selection bias. The random sequence was generated using a computer‑based random number generator, and group assignments were placed in sequentially numbered, opaque, sealed envelopes prepared by a researcher not involved in recruitment. The research assistant opened the next envelope only after the participant had consented and completed baseline assessments, ensuring allocation concealment. These details have now been added to the Methods section to improve transparency and methodological clarity.

 

Intervention

The term “kinematic TKA” is used without explanation. A brief definition or a reference to the relevant literature is required to clarify this term for readers who may not be familiar with it.

Reply: Thank you for this comment. We agree that the term may not be familiar to all readers. We have added a brief clarification in the Methods section. Kinematic TKA refers to a surgical alignment philosophy that aims to restore the patient’s pre‑arthritic, native knee kinematics by aligning the components to the individual’s anatomical axes rather than using a standardized mechanical alignment. This short explanation improves clarity without requiring an additional reference.

 

Participants received an audio recording of the exercises on their cell phones and were asked to practise brief GI exercises regularly, at least once daily, before and after surgery. It is unclear whether adherence to the intervention was monitored, for example via a GI session diary. If adherence was monitored, the degree of compliance should be reported in the Results section. If not, this represents a fundamental methodological flaw that critically affects the quality and interpretability of the study. De facto, we do not know to what extent the intervention was actually delivered or followed. Even minimal controls – such as daily reminders via SMS – could have been implemented, particularly as the intervention was delivered via smartphones. While the Data collection section notes that the researcher reminded participants once weekly, this is clearly insufficient for reliable adherence monitoring. Without proper adherence control, the observed outcomes may be attributable to other uncontrolled factors present in the intervention group. At a minimum, this limitation should be acknowledged in the

Limitations section, although any discerning reader will recognise that the results may therefore be uninterpretable.

Reply: Thank you for raising this important point. Participants were instructed to practice the guided imagery (GI) exercise daily, and adherence was supported through weekly telephone contacts during which the researcher reminded participants to continue their daily practice and confirmed that they were engaging with the audio recording. However, adherence was not systematically monitored using a daily diary or automated tracking tool. We agree that this limits our ability to quantify the exact frequency of GI practice, and we have now acknowledged this in the Limitations section.

At the same time, we respectfully disagree that the absence of a daily adherence log renders the results uninterpretable or introduces uncontrolled group differences. The purpose of randomization is precisely to balance both measured and unmeasured factors, including variability in adherence, between groups. All participants in the intervention arm received the same instructions, the same audio file, and the same weekly reminders, and no additional co‑interventions were introduced. Therefore, while the lack of precise adherence quantification is a limitation, it does not constitute a fundamental methodological flaw nor invalidate the randomized comparison.

We have revised the manuscript to clarify the adherence procedures and to explicitly note the absence of systematic adherence monitoring as a study limitation.

 

Data collection and outcome measures

These sections require complete restructuring. Outcome measures should come first, providing clear information on the instruments used to assess pain, function, and anxiety. Data collection should follow, specifying exactly what was assessed at each time point. It should be noted that the demographic questionnaire does not constitute an outcome measure and should not be included in the Outcome measures section.

Reply: We have restructured the Methods section to clearly separate (1) the outcome measures and (2) the data collection schedule. The Outcome Measures subsection now includes only the validated instruments used to assess pain, function, and anxiety (NPRS, NFRS/WOMAC, STAI). The demographic questionnaire has been removed from this section and is now described solely under Participant Characteristics. A revised Data Collection subsection follows the outcome measures and specifies exactly which instruments were administered at each time point (T1–T8), with an explanation of the clinical and logistical constraints that shaped the schedule. This restructuring improves clarity, consistency, and alignment with standard reporting practices.

 

It is unclear why the authors adopted the current structure for data collection, which appears inconsistent. All outcomes were measured at T1 and T8, but at T2 only NPRS and SATI were assessed. At T3–T7, only NPRS and NFRS were assessed. If this measurement schedule is justified, a clear explanation should be provided to the reader, as the current presentation raises questions about the rationale and consistency of outcome assessment.

Reply: Thank you for this important comment. We have clarified the rationale for the timing of outcome assessments. All outcomes were collected at T1 (baseline) and T8 (5–6‑week follow‑up), when full in‑person assessment was feasible. On the first postoperative day (T2), only NPRS and STAI were collected because patients were in the immediate postoperative recovery phase, and additional questionnaires (e.g., WOMAC/NFRS) were not clinically appropriate or feasible. During T3–T7, data were collected by telephone, which allowed assessment of NPRS and NFRS but not longer, self‑administered instruments such as the WOMAC or STAI. This schedule reflects both clinical constraints and the need to minimize participant burden during early recovery. We have added this explanation to the Methods section to ensure transparency and consistency.

 

Additionally, Chart 1 uses inconsistent fonts, which looks unprofessional.)

Reply: We corrected the fonts in Chart 1.

 

As a side note, there is confusion regarding the abbreviation: is it SATI or STAI?

Reply: We corrected the text. Now everywhere is STAI.

 

 

Data analysis

In paragraph 2, the text inexplicably switches to the future tense, which is inconsistent with standard reporting of methods. The term “satisfaction rate” is introduced without explanation and does not appear to correspond to any previously defined outcome measure. Furthermore, the post hoc test should be explicitly linked to the ANOVA analysis. In its current form, it appears as if the Mann-Whitney test also requires a post hoc analysis, which is misleading and needs clarification.

Reply: We agree that there were lots of mistakes in the data analysis section, and therefore, we completely changed the description of data analysis.

 

Results

In the Participant characteristics section, many variables reported should instead be included in the selection criteria, for example postsurgical complications.

Reply: Thank you for this comment. We would like to clarify that the variables presented in the Participant Characteristics section (including postoperative complications) are descriptive characteristics of the enrolled sample and not eligibility criteria. Inclusion and exclusion criteria were applied before surgery and before randomization, whereas postoperative complications occur after enrollment and therefore cannot be used as selection criteria. These postoperative variables were reported solely to describe the clinical course of participants and to allow readers to interpret the sample’s postoperative profile. To improve clarity, we have added a brief note in the Participant Characteristics section indicating that these variables reflect postoperative outcomes rather than eligibility criteria.

 

Table 1 – Outcome measure results should be separated from demographic characteristics, as NPRS and NFRS will be discussed in subsequent sections of the Results.

Reply: We deleted this information from the Table 1.

 

Information regarding country of origin must be removed entirely; the manuscript contains an excessive number of elements suggestive of nationality, which are unnecessary and inappropriate. It is also unclear why variables such as marital status, education, number of children (particularly in men), and physical activity are included, as their relevance to the study is not explained. They should be excluded, in my opinion.

Reply: We agree that country of origin is not essential for interpreting the study outcomes, and we have removed this variable from Table 1 to avoid unnecessary emphasis on nationality. Regarding marital status, education, number of children, and physical activity, these variables were originally included as standard demographic descriptors commonly reported in clinical trials to characterize the sample. However, as they are not directly related to the study hypotheses or analyses, we agree that removing them will improve clarity and focus. We have therefore revised Table 1 to include only variables relevant to the clinical and methodological context of the study. This change streamlines the presentation and avoids unnecessary demographic detail.

 

The inclusion of WOMAC, STAI, and NFRS data in the section entitled Pain outcomes is confusing. Overall, the structure of the results presentation is inconsistent, which significantly impedes the reader’s ability to interpret the findings.

Reply: WOMAC and NFRS were included under heading Functional Outcomes (NFRS and WOMAC). STAI data was included under heading Anxiety Outcomes (STAI).

 

Table 2 – There are formatting problems, which may be due to the manuscript version provided.

Reply: In the original version of the manuscript, Table 2 did not contain any formatting problems. It appears that the issue arose during the conversion of the file for the review system. We have now resubmitted the revised manuscript using the original formatting to ensure that Table 2 displays correctly and avoids any additional formatting inconsistencies.

 

Charts 2–3 – These charts are redundant as they repeat information already presented in Table 2. Additionally, Chart 2 raises several issues: it is unclear what “trial” refers to (intervention group?), what the “pain scale” is (NPRS? – please use a single abbreviation consistently), what the units on the Y-axis are, and what “time” represents (presumably T1–T8 data collection points). In Chart 3, it is unclear what “function” refers to (NFRS?), what the units on the Y-axis are, and what “time” represents. Moreover, the label “intervention” appears now correctly but inconsistently instead of former “trial,” making the presentation confusing and misleading.

Reply: Thank you for this detailed and helpful feedback. We agree that Charts 2 and 3 repeat information already presented in Table 2 and that the current labeling may cause confusion. To improve clarity and avoid redundancy, we have removed both charts from the manuscript. Table 2 now serves as the primary presentation of the NPRS and NFRS outcomes, ensuring consistency and eliminating any ambiguity regarding terminology, units, or time points. This revision streamlines the Results section and prevents duplication of data.

 

There are two summaries of findings that are redundant. Only one summary should be presented, either in the Results or the Discussion section, to avoid duplication.

Reply: Thank you for this helpful observation. We agree that presenting two summaries may create unnecessary repetition. To address this, we removed the summary paragraph from the Results section and retained the more integrative summary in the Discussion, where the findings are interpreted in context. This eliminates redundancy while preserving clarity and flow.

 

Discussion

Limitations

The first limitation noted could have been avoided if the authors had performed sample size estimations for all key outcome measures, including WOMAC and STAI.

Reply: We agree that sample size estimation is essential for ensuring adequate statistical power. In clinical trials, however, it is standard practice to calculate the sample size based on the primary outcome measure, rather than powering the study for all secondary outcomes. Our study was designed with NPRS as the primary endpoint, and the sample size calculation was performed accordingly. WOMAC and STAI were included as secondary exploratory outcomes, and the study was not intended or powered to detect small or medium effects in these measures. We have clarified this point in the Limitations section to avoid any misunderstanding about the scope and intent of the sample size calculation.

 

The sentence: “Second, the 6-week follow-up period restricts conclusions about long-term outcomes, as TKA recovery often extends beyond this timeframe [4]” is misleading. Reference [4] presents outcomes of TKA, not GI; therefore, it would be risky or unnecessary to infer potential GI effects e.g. six months after the six-week intervention.

Reply: We agree that the original wording may unintentionally imply expectations about long‑term effects of the guided imagery intervention, which was not our intention. Our aim was simply to acknowledge that the study assessed outcomes only during the early postoperative period. To avoid any suggestion that GI effects should extend beyond the intervention window, we have revised the sentence to focus solely on the limited duration of follow‑up without referencing long‑term TKA recovery trajectories. The reference to [4] has been removed.

 

The sentence: “Third, the single-center design and requirement for Hebrew proficiency and smartphone access limit generalizability to diverse populations” requires revision. The reference to Hebrew should be removed. Regarding smartphone access, if this is a limitation, it calls into question why a smartphone-based intervention was chosen in the first place; alternative low-cost audio devices could have been provided. Following this logic, lack of mobile network coverage could also be considered a limitation, which is clearly absurd.

Reply: We agree that Hebrew proficiency should not be presented as a limitation, as it reflects the language of the validated instruments used in this study rather than a restriction on generalizability. We have therefore removed this reference. Regarding smartphone access, the intervention was intentionally designed as a smartphone‑based protocol because smartphone ownership is nearly universal in our patient population, and the study had no external funding to provide alternative devices. Since no eligible patient lacked a smartphone, this requirement did not restrict participation in practice. We have revised the limitation to focus on the true methodological constraint, the single‑center design, without implying unnecessary or artificial limitations.

 

ADHERENCE TO DAILY GI PRACTICE WAS NOT SYSTEMATICALLY MEASURED, WHICH MAY HAVE COMPLETELY COMPROMISED THE FINDINGS!!!!! This issue is critical and could entirely undermine the validity of the results. It should be placed as the first and most important limitation.

The sentence: “Fourth, adherence to daily GI practice was not systematically measured, which may have influenced the variability of outcomes” is correct, but this limitation should be emphasised as noted above – first and most prominent – because it could completely invalidate the results.

Reply: We agree that adherence to the guided imagery (GI) protocol was not systematically quantified using a daily log or automated monitoring tool. Participants were instructed to practice daily, and adherence was supported through weekly telephone contacts during which the researcher reminded participants to continue daily practice and confirmed ongoing use of the audio recording. We acknowledge that this approach does not provide precise adherence data, and we have now emphasized this as a key limitation.

At the same time, we respectfully disagree that the absence of a daily adherence diary “completely compromises” the findings or invalidates the randomized comparison. In randomized controlled trials, randomization is specifically intended to balance both measured and unmeasured factors—including variability in adherence—between groups. All participants in the intervention arm received the same instructions, the same audio file, and the same weekly reminders, and no additional co‑interventions were introduced. Therefore, while the lack of systematic adherence measurement limits our ability to quantify dose–response relationships, it does not undermine the internal validity of the trial or render the results uninterpretable.

We have revised the Limitations section to place this point earlier and to describe it more prominently, while maintaining an accurate methodological interpretation.

 

Future directions

Extending the follow-up to 6 or 12 months after an uncontrolled, brief 2-minute daily intervention over six weeks appears unreasonable. The suggested timeframe is excessive given the limited and uncontrolled nature of the intervention.

Reply: We agree that suggesting 6–12‑month follow‑up may imply expectations that exceed the scope and intensity of the current brief intervention. Our intention was not to propose long‑term follow‑up as a direct test of sustained treatment effects, but rather to note that future studies could examine whether early postoperative psychological or behavioral interventions have any downstream influence on longer‑term recovery trajectories. To avoid misinterpretation, we have revised the text to reflect a more appropriate and proportionate future direction focused on evaluating the intervention within a controlled design and exploring its short‑ to medium‑term effects.

 

Conclusion

The conclusion is fundamentally undermined by the most important limitation: lack of control over intervention adherence. This critical point should be explicitly reiterated in the Conclusion, as it casts doubt on the validity of all reported findings.

Reply: Thank you for this comment. We agree that the absence of systematic adherence monitoring is an important limitation and have already emphasized it as the first limitation in the revised manuscript. We also agree that this point should be acknowledged briefly in the Conclusion to ensure transparency.

At the same time, we respectfully disagree that this limitation “fundamentally undermines” the validity of the findings. In a randomized controlled design, randomization is intended to balance both measured and unmeasured factors—including variability in adherence—between groups. All participants in the intervention arm received the same instructions, the same audio file, and the same weekly reminders, and no additional co‑interventions were introduced. Therefore, while the exact frequency of daily practice cannot be quantified, this does not invalidate the randomized comparison or prevent meaningful interpretation of the results. It does, however, limit our ability to draw conclusions about dose–response relationships or the precise extent of engagement with the intervention.

We have revised the Conclusion to reflect this limitation clearly and proportionately.

 

 

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors have answered most of my comments. Thank you for considering my suggestions. I suggest publishing this work. 

Author Response

The authors have answered most of my comments. Thank you for considering my suggestions. I suggest publishing this work. 

Reply: We sincerely thank the reviewer for the positive evaluation and supportive recommendation. We appreciate the time and care invested in reviewing our manuscript.

Reviewer 2 Report

Comments and Suggestions for Authors

All of my comments have received appropriate responses. I have one small suggestion which may be considered, although its implementation is not essential. If the authors state that their main outcome measure was the NPRS, it might be worth presenting the NPRS results first in Table 2 (in the left-hand columns), followed by the NFRS, STAI and WOMAC results. This would also be consistent with the order of data presentation in the Results section and would improve clarity and ease of interpretation.

Author Response

All of my comments have received appropriate responses. I have one small suggestion which may be considered, although its implementation is not essential. If the authors state that their main outcome measure was the NPRS, it might be worth presenting the NPRS results first in Table 2 (in the left-hand columns), followed by the NFRS, STAI and WOMAC results. This would also be consistent with the order of data presentation in the Results section and would improve clarity and ease of interpretation.

Reply: We thank the reviewer for this thoughtful suggestion aimed at improving clarity and consistency. We agree that presenting the NPRS results first in Table 2 aligns well with the structure of the Results section and highlights the primary outcome measure. We have revised Table 2 accordingly. We appreciate the reviewer’s careful attention to detail and constructive feedback.