Title: Effectiveness of an app-based walking program for obese patients with inflammatory
bowel disease in Korea: a single-blind parallel-group randomized clinical trial
Version: 2 Date: 20 Jan 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-The manuscript mentions that the trial is “single-blind,” but it does not clearly explain who
was blinded. Given that participants in the control group were not provided with educational
videos or support, it seems they might be aware of their group assignment. Therefore, it would be
important to clarify whether the outcome assessors were blinded, as this would affect the study’s
internal validity. Additionally, the term “case random sampling” is used in the randomization
process, which is not commonly understood. Please clarify this method (e.g., was it simple
randomization or stratified randomization?).
-The sample size was calculated using G*Power, with an effect size of f=0.25f = 0.25f=0.25,
which is considered moderate. However, it would be helpful to briefly justify this choice of
effect size, especially since previous studies on similar interventions might offer insight into
expected effect sizes. Further, while the study accounts for a 20% dropout rate, the actual dropout
was around 9%, suggesting that the sample size could potentially have been smaller. Consider
discussing this discrepancy and its implications for the study’s power.
-The major difference between the intervention and control groups seems to be the educational
content and the motivational features offered to the IG (e.g., weekly videos, rewards, step-
count rankings). However, the control group received the same mobile app and wearable
devices to track their steps and body composition, which introduces the possibility that any
differences observed are due to these added features rather than physical activity alone. An
“active control” group that receives general walking advice, but without the educational and
motivational components, would help isolate the effects of the walking program from other
psychological factors.
-Adherence to the walking program (i.e., the 7,000 steps per day goal) is not fully addressed.
Did participants in the IG achieve the prescribed step count, and if not, how was this accounted
for? Did the study examine factors that influenced adherence, such as motivation, technology
usability, or barriers to exercise? A detailed analysis of these factors would be valuable to
understand the feasibility of such programs in real-world clinical settings.
-While statistical significance (p-values) is provided for perceived stress, fatigue, and step count,
the manuscript does not mention effect sizes for these outcomes (e.g., Cohen's d or partial eta-
squared). Given that p-values alone do not convey the practical significance or strength of the
findings, the inclusion of effect sizes would offer a clearer picture of the intervention's clinical
relevance.
-The discussion notes that no significant changes were observed in the IBDQ, which measures
disease-specific quality of life. While the authors correctly point out that the exercise program
was 10 weeks long, it would be useful to discuss why a program of this length might still
fail to produce changes in the IBDQ score. Could other factors, such as disease activity or
treatment regimens, have affected the results? This area could benefit from a deeper exploration,
particularly in light of other studies that have shown improvements in HRQoL with similar
interventions.
-The authors note that participants in both groups had relatively high baseline IBDQ scores,
which might explain the lack of improvement. However, a more detailed explanation of how
baseline quality of life scores influence the capacity for improvement would be valuable. Are
the relatively high scores reflective of participants' disease activity at the time of recruitment?
Could baseline differences in disease activity potentially explain why there were no changes in
quality of life despite improvements in other outcomes?
-The authors acknowledge that the control group may have increased their physical activity
levels due to access to the app and devices. This is an important limitation, and it would be
beneficial to discuss in more detail how this might have confounded the results, especially in
relation to secondary outcomes like perceived stress and fatigue. How might the additional
motivation or awareness generated by the app have influenced the results?
Title: Effectiveness of an app-based walking program for obese patients with inflammatory
bowel disease in Korea: a single-blind parallel-group randomized clinical trial
Version: 2 Date: 20 Jan 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-The manuscript mentions that the trial is “single-blind,” but it does not clearly explain who
was blinded. Given that participants in the control group were not provided with educational
videos or support, it seems they might be aware of their group assignment. Therefore, it would be
important to clarify whether the outcome assessors were blinded, as this would affect the study’s
internal validity. Additionally, the term “case random sampling” is used in the randomization
process, which is not commonly understood. Please clarify this method (e.g., was it simple
randomization or stratified randomization?).
-The sample size was calculated using G*Power, with an effect size of f=0.25f = 0.25f=0.25,
which is considered moderate. However, it would be helpful to briefly justify this choice of
effect size, especially since previous studies on similar interventions might offer insight into
expected effect sizes. Further, while the study accounts for a 20% dropout rate, the actual dropout
was around 9%, suggesting that the sample size could potentially have been smaller. Consider
discussing this discrepancy and its implications for the study’s power.
-The major difference between the intervention and control groups seems to be the educational
content and the motivational features offered to the IG (e.g., weekly videos, rewards, step-
count rankings). However, the control group received the same mobile app and wearable
devices to track their steps and body composition, which introduces the possibility that any
differences observed are due to these added features rather than physical activity alone. An
“active control” group that receives general walking advice, but without the educational and
motivational components, would help isolate the effects of the walking program from other
psychological factors.
-Adherence to the walking program (i.e., the 7,000 steps per day goal) is not fully addressed.
Did participants in the IG achieve the prescribed step count, and if not, how was this accounted
for? Did the study examine factors that influenced adherence, such as motivation, technology
usability, or barriers to exercise? A detailed analysis of these factors would be valuable to
understand the feasibility of such programs in real-world clinical settings.
-While statistical significance (p-values) is provided for perceived stress, fatigue, and step count,
the manuscript does not mention effect sizes for these outcomes (e.g., Cohen's d or partial eta-
squared). Given that p-values alone do not convey the practical significance or strength of the
findings, the inclusion of effect sizes would offer a clearer picture of the intervention's clinical
relevance.
-The discussion notes that no significant changes were observed in the IBDQ, which measures
disease-specific quality of life. While the authors correctly point out that the exercise program
was 10 weeks long, it would be useful to discuss why a program of this length might still
fail to produce changes in the IBDQ score. Could other factors, such as disease activity or
treatment regimens, have affected the results? This area could benefit from a deeper exploration,
particularly in light of other studies that have shown improvements in HRQoL with similar
interventions.
-The authors note that participants in both groups had relatively high baseline IBDQ scores,
which might explain the lack of improvement. However, a more detailed explanation of how
baseline quality of life scores influence the capacity for improvement would be valuable. Are
the relatively high scores reflective of participants' disease activity at the time of recruitment?
Could baseline differences in disease activity potentially explain why there were no changes in
quality of life despite improvements in other outcomes?
-The authors acknowledge that the control group may have increased their physical activity
levels due to access to the app and devices. This is an important limitation, and it would be
beneficial to discuss in more detail how this might have confounded the results, especially in
relation to secondary outcomes like perceived stress and fatigue. How might the additional
motivation or awareness generated by the app have influenced the results?
Please review this paper.
user
Title: Effectiveness of an app-based walking program for obese patients with inflammatory
bowel disease in Korea: a single-blind parallel-group randomized clinical trial
Version: 2 Date: 20 Jan 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-The manuscript mentions that the trial is “single-blind,” but it does not clearly explain who
was blinded. Given that participants in the control group were not provided with educational
videos or support, it seems they might be aware of their group assignment. Therefore, it would be
important to clarify whether the outcome assessors were blinded, as this would affect the study’s
internal validity. Additionally, the term “case random sampling” is used in the randomization
process, which is not commonly understood. Please clarify this method (e.g., was it simple
randomization or stratified randomization?).
-The sample size was calculated using G*Power, with an effect size of f=0.25f = 0.25f=0.25,
which is considered moderate. However, it would be helpful to briefly justify this choice of
effect size, especially since previous studies on similar interventions might offer insight into
expected effect sizes. Further, while the study accounts for a 20% dropout rate, the actual dropout
was around 9%, suggesting that the sample size could potentially have been smaller. Consider
discussing this discrepancy and its implications for the study’s power.
-The major difference between the intervention and control groups seems to be the educational
content and the motivational features offered to the IG (e.g., weekly videos, rewards, step-
count rankings). However, the control group received the same mobile app and wearable
devices to track their steps and body composition, which introduces the possibility that any
differences observed are due to these added features rather than physical activity alone. An
“active control” group that receives general walking advice, but without the educational and
motivational components, would help isolate the effects of the walking program from other
psychological factors.
-Adherence to the walking program (i.e., the 7,000 steps per day goal) is not fully addressed.
Did participants in the IG achieve the prescribed step count, and if not, how was this accounted
for? Did the study examine factors that influenced adherence, such as motivation, technology
usability, or barriers to exercise? A detailed analysis of these factors would be valuable to
understand the feasibility of such programs in real-world clinical settings.
-While statistical significance (p-values) is provided for perceived stress, fatigue, and step count,
the manuscript does not mention effect sizes for these outcomes (e.g., Cohen's d or partial eta-
squared). Given that p-values alone do not convey the practical significance or strength of the
findings, the inclusion of effect sizes would offer a clearer picture of the intervention's clinical
relevance.
-The discussion notes that no significant changes were observed in the IBDQ, which measures
disease-specific quality of life. While the authors correctly point out that the exercise program
was 10 weeks long, it would be useful to discuss why a program of this length might still
fail to produce changes in the IBDQ score. Could other factors, such as disease activity or
treatment regimens, have affected the results? This area could benefit from a deeper exploration,
particularly in light of other studies that have shown improvements in HRQoL with similar
interventions.
-The authors note that participants in both groups had relatively high baseline IBDQ scores,
which might explain the lack of improvement. However, a more detailed explanation of how
baseline quality of life scores influence the capacity for improvement would be valuable. Are
the relatively high scores reflective of participants' disease activity at the time of recruitment?
Could baseline differences in disease activity potentially explain why there were no changes in
quality of life despite improvements in other outcomes?
-The authors acknowledge that the control group may have increased their physical activity
levels due to access to the app and devices. This is an important limitation, and it would be
beneficial to discuss in more detail how this might have confounded the results, especially in
relation to secondary outcomes like perceived stress and fatigue. How might the additional
motivation or awareness generated by the app have influenced the results?
assistant