Reviewer's report
Title:Management of Irritable Bowel Syndrome in Primary Care: An Exploratory
Randomised Controlled Trial of Mebeverine, Methylcellulose, Placebo and a
Self-management website.
Version: 2Date:28 November 2012
Reviewer: Jeffrey Lackner
Reviewer's report:
This is an interesting article that attempts to address an important topic, namely
the delivery of a treatment program for patients with IBS using a combination of
medications, support and web based psychological counseling. There are a
number of strengths to this study. The research team is well known, their track
record is established. They use, for the most part, established outcome
measures. There are however serious flaws with this study some of which are
described below
Major Compulsory Revisions
1. The review of research on the efficacy of CBT could be more authoritatively
discussed by referencing some of the stronger clinical trials vs. narrative reviews
(primary citations). The Drossman et al trial was not to my knowledge found to be
“helpful ….in reducing [IBS] symptoms scores”. There are methodologically
stronger CBT trials that have done this and their inclusion would support the
conceptual argument for this present study. Writing is not acceptable
2. A major conceptual problem concerns the inclusion of a drug arm. If as the
researchers argue there is a “lack of evidence for …current drug management”
then what is the rationale for necessarily including an antispasmodic or bulking
agent?
3. With respect to exclusionary criteria, is it accurate that patients with major
mental illness (e.g. thought disorder, active suicidal ideation) were not excluded?
With respect to inclusionary criteria, it is not clear why patients with mild
symptoms were included. It is customary to restrict behavioral treatments to
patients with more severely affected patients as these patients are unlikely to
respond to conventional medical, dietary, and lifestyle treatments. Why was
severity not an eligibility criteria? Why are mildly severe IBS subjects included?
4. Compliance measures seem very crude and of questionable validity. How do
the researchers know whether patients worked through programs and complied
with the technical demands of CBT? So if patients completed the first four
sessions and not did anything else in the program they would be regarded as
compliant with treatment as someone who worked through home exercises etc?
It is odd that the researchers used proportion of patients who STOPPED
medication as a compliance metric. Is this validated measure? This is an indirect
measure of compliance which by definition should be based on adherence to
treatment. Whether patients stopped taking an agent is a rather low criteria for
compliance
5. There does not appear to be any test for treatment compliance / expectancy of
improvement for assigned arms; thus it is unclear whether treatment effect is
nonspecific. The fact that there is such a dramatic erosion on primary outcome
variable from session 6 to 12 argues that the effect is placebo on nature and due
to nonspecific factors (eg treatment expectancy) which should have been
assessed
6. A major problem with the paper is their use of the subjective global
assessment scale (Muller-Lissner et al, 2003). The researchers defined
responders as those who score 1-3 (i.e. completely relieves, considerably
relieved, somewhat relieved). This differs from the way the SGA was designed
and the way global improvement scales have been used in IBS and non IBS
trials (ie patients who describe themselves as somewhat or slightly improved
register as non responders). In the case of the SGA for IBS, somewhat relieved
is only registered as a positive treatment response of it occurs 100% of the time.
The researchers should look to the work by other functional GI researchers for
appropriate use of global improvement scales. In the meantime, these data need
to be reanalyzed so that patients who derive clinically unremarkable
improvement (slightly improved) are not registered as responders. The comment
that patients “significantly improved” is premature if the subjects who are counted
as responders included those who were slightly improved. Further, the SGA is a
five point scale with three items reflecting positive treatment response and two
items reflecting negative treatment response. This measure has been criticized
as biasing patients in favor of positive response. In other words the outcome data
may be based on format of scale vs therapeutic benefit of treatment procedures.
7. Please specify the primary outcome measure. It is either the IBS-SSS or the
IBS-QOL but not both. The researchers should consult IBS clinical trial guidelines
which regards quality of life as an important secondary outcome. A rationale for
defining it as a primary outcome is necessary
8. The researchers make much of the change scores from baseline to 6 weeks
but the more important change score is between baseline and 12 weeks. The
pre- post treatment scores were 35 for the IBSSS and 5 for the IBSQOL neither
of which are clinically significant. These data raise questions about the
therapeutic benefit of featured treatments. A major question is whether any
treatment gain is (1) clinically significant and (2) whether it can be confidently
attributed to the experimental conditions. The authors do not make this case
which is a major limitation if not fatal flaw of the study
9. It is unclear where an expectation of a 20% drop out rate was based. I believe
the dropout rate for the Drossman trial was about 35%. Sample size seems
based on inaccurate estimations of sample size. By their own acknowledgement,
the researchers concede in the discussion that the study is underpowered
10. The researchers are on shaky ground to argue that “patent with access to
Regul8 website felt better able to cope with their symptoms with their symptoms”
when no coping measure was administered. This reflects a general tendency to
make conclusions that go beyond data.
11. It is not clear whether a manualized protocol guided treatment.
12. How was missing data dealt with?
13. The methodology of the trial could be strengthened with a blind assessor
Minor Essential Revisions
1. The manuscript in general is not as well written as it should be. There are
many mechanical problems that are distracting and undermine the readability of
the paper. Sentences are incompletely structured; spelling mistakes are many;
and the paper in general has a rushed quality that demands tighter editorial
review.
2. It would be helpful for authors to paginate the pages
3. The CONSORT diagram should be reformatted so it fits on one sheet of paper
not 3
4. The discussion of web based CBT for non IBS problems needs beefing up.
There are a number of areas that highlight the promise of eCBT (e.g. insomnia).
The researchers should look for support beyond he work of one investigative
team in a culturally and geographically unique setting.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Declaration of competing interests:
'I declare that I have no competing interests' below. If your reply is yes to any,
please give details below.
Reviewer's report
Title:Management of Irritable Bowel Syndrome in Primary Care: An Exploratory
Randomised Controlled Trial of Mebeverine, Methylcellulose, Placebo and a
Self-management website.
Version: 2Date:28 November 2012
Reviewer: Jeffrey Lackner
Reviewer's report:
This is an interesting article that attempts to address an important topic, namely
the delivery of a treatment program for patients with IBS using a combination of
medications, support and web based psychological counseling. There are a
number of strengths to this study. The research team is well known, their track
record is established. They use, for the most part, established outcome
measures. There are however serious flaws with this study some of which are
described below
Major Compulsory Revisions
1. The review of research on the efficacy of CBT could be more authoritatively
discussed by referencing some of the stronger clinical trials vs. narrative reviews
(primary citations). The Drossman et al trial was not to my knowledge found to be
“helpful ….in reducing [IBS] symptoms scores”. There are methodologically
stronger CBT trials that have done this and their inclusion would support the
conceptual argument for this present study. Writing is not acceptable
2. A major conceptual problem concerns the inclusion of a drug arm. If as the
researchers argue there is a “lack of evidence for …current drug management”
then what is the rationale for necessarily including an antispasmodic or bulking
agent?
3. With respect to exclusionary criteria, is it accurate that patients with major
mental illness (e.g. thought disorder, active suicidal ideation) were not excluded?
With respect to inclusionary criteria, it is not clear why patients with mild
symptoms were included. It is customary to restrict behavioral treatments to
patients with more severely affected patients as these patients are unlikely to
respond to conventional medical, dietary, and lifestyle treatments. Why was
severity not an eligibility criteria? Why are mildly severe IBS subjects included?
4. Compliance measures seem very crude and of questionable validity. How do
the researchers know whether patients worked through programs and complied
with the technical demands of CBT? So if patients completed the first four
sessions and not did anything else in the program they would be regarded as
compliant with treatment as someone who worked through home exercises etc?
It is odd that the researchers used proportion of patients who STOPPED
medication as a compliance metric. Is this validated measure? This is an indirect
measure of compliance which by definition should be based on adherence to
treatment. Whether patients stopped taking an agent is a rather low criteria for
compliance
5. There does not appear to be any test for treatment compliance / expectancy of
improvement for assigned arms; thus it is unclear whether treatment effect is
nonspecific. The fact that there is such a dramatic erosion on primary outcome
variable from session 6 to 12 argues that the effect is placebo on nature and due
to nonspecific factors (eg treatment expectancy) which should have been
assessed
6. A major problem with the paper is their use of the subjective global
assessment scale (Muller-Lissner et al, 2003). The researchers defined
responders as those who score 1-3 (i.e. completely relieves, considerably
relieved, somewhat relieved). This differs from the way the SGA was designed
and the way global improvement scales have been used in IBS and non IBS
trials (ie patients who describe themselves as somewhat or slightly improved
register as non responders). In the case of the SGA for IBS, somewhat relieved
is only registered as a positive treatment response of it occurs 100% of the time.
The researchers should look to the work by other functional GI researchers for
appropriate use of global improvement scales. In the meantime, these data need
to be reanalyzed so that patients who derive clinically unremarkable
improvement (slightly improved) are not registered as responders. The comment
that patients “significantly improved” is premature if the subjects who are counted
as responders included those who were slightly improved. Further, the SGA is a
five point scale with three items reflecting positive treatment response and two
items reflecting negative treatment response. This measure has been criticized
as biasing patients in favor of positive response. In other words the outcome data
may be based on format of scale vs therapeutic benefit of treatment procedures.
7. Please specify the primary outcome measure. It is either the IBS-SSS or the
IBS-QOL but not both. The researchers should consult IBS clinical trial guidelines
which regards quality of life as an important secondary outcome. A rationale for
defining it as a primary outcome is necessary
8. The researchers make much of the change scores from baseline to 6 weeks
but the more important change score is between baseline and 12 weeks. The
pre- post treatment scores were 35 for the IBSSS and 5 for the IBSQOL neither
of which are clinically significant. These data raise questions about the
therapeutic benefit of featured treatments. A major question is whether any
treatment gain is (1) clinically significant and (2) whether it can be confidently
attributed to the experimental conditions. The authors do not make this case
which is a major limitation if not fatal flaw of the study
9. It is unclear where an expectation of a 20% drop out rate was based. I believe
the dropout rate for the Drossman trial was about 35%. Sample size seems
based on inaccurate estimations of sample size. By their own acknowledgement,
the researchers concede in the discussion that the study is underpowered
10. The researchers are on shaky ground to argue that “patent with access to
Regul8 website felt better able to cope with their symptoms with their symptoms”
when no coping measure was administered. This reflects a general tendency to
make conclusions that go beyond data.
11. It is not clear whether a manualized protocol guided treatment.
12. How was missing data dealt with?
13. The methodology of the trial could be strengthened with a blind assessor
Minor Essential Revisions
1. The manuscript in general is not as well written as it should be. There are
many mechanical problems that are distracting and undermine the readability of
the paper. Sentences are incompletely structured; spelling mistakes are many;
and the paper in general has a rushed quality that demands tighter editorial
review.
2. It would be helpful for authors to paginate the pages
3. The CONSORT diagram should be reformatted so it fits on one sheet of paper
not 3
4. The discussion of web based CBT for non IBS problems needs beefing up.
There are a number of areas that highlight the promise of eCBT (e.g. insomnia).
The researchers should look for support beyond he work of one investigative
team in a culturally and geographically unique setting.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Declaration of competing interests:
'I declare that I have no competing interests' below. If your reply is yes to any,
please give details below.
Please review this paper.
user
Reviewer's report
Title:Management of Irritable Bowel Syndrome in Primary Care: An Exploratory
Randomised Controlled Trial of Mebeverine, Methylcellulose, Placebo and a
Self-management website.
Version: 2Date:28 November 2012
Reviewer: Jeffrey Lackner
Reviewer's report:
This is an interesting article that attempts to address an important topic, namely
the delivery of a treatment program for patients with IBS using a combination of
medications, support and web based psychological counseling. There are a
number of strengths to this study. The research team is well known, their track
record is established. They use, for the most part, established outcome
measures. There are however serious flaws with this study some of which are
described below
Major Compulsory Revisions
1. The review of research on the efficacy of CBT could be more authoritatively
discussed by referencing some of the stronger clinical trials vs. narrative reviews
(primary citations). The Drossman et al trial was not to my knowledge found to be
“helpful ….in reducing [IBS] symptoms scores”. There are methodologically
stronger CBT trials that have done this and their inclusion would support the
conceptual argument for this present study. Writing is not acceptable
2. A major conceptual problem concerns the inclusion of a drug arm. If as the
researchers argue there is a “lack of evidence for …current drug management”
then what is the rationale for necessarily including an antispasmodic or bulking
agent?
3. With respect to exclusionary criteria, is it accurate that patients with major
mental illness (e.g. thought disorder, active suicidal ideation) were not excluded?
With respect to inclusionary criteria, it is not clear why patients with mild
symptoms were included. It is customary to restrict behavioral treatments to
patients with more severely affected patients as these patients are unlikely to
respond to conventional medical, dietary, and lifestyle treatments. Why was
severity not an eligibility criteria? Why are mildly severe IBS subjects included?
4. Compliance measures seem very crude and of questionable validity. How do
the researchers know whether patients worked through programs and complied
with the technical demands of CBT? So if patients completed the first four
sessions and not did anything else in the program they would be regarded as
compliant with treatment as someone who worked through home exercises etc?
It is odd that the researchers used proportion of patients who STOPPED
medication as a compliance metric. Is this validated measure? This is an indirect
measure of compliance which by definition should be based on adherence to
treatment. Whether patients stopped taking an agent is a rather low criteria for
compliance
5. There does not appear to be any test for treatment compliance / expectancy of
improvement for assigned arms; thus it is unclear whether treatment effect is
nonspecific. The fact that there is such a dramatic erosion on primary outcome
variable from session 6 to 12 argues that the effect is placebo on nature and due
to nonspecific factors (eg treatment expectancy) which should have been
assessed
6. A major problem with the paper is their use of the subjective global
assessment scale (Muller-Lissner et al, 2003). The researchers defined
responders as those who score 1-3 (i.e. completely relieves, considerably
relieved, somewhat relieved). This differs from the way the SGA was designed
and the way global improvement scales have been used in IBS and non IBS
trials (ie patients who describe themselves as somewhat or slightly improved
register as non responders). In the case of the SGA for IBS, somewhat relieved
is only registered as a positive treatment response of it occurs 100% of the time.
The researchers should look to the work by other functional GI researchers for
appropriate use of global improvement scales. In the meantime, these data need
to be reanalyzed so that patients who derive clinically unremarkable
improvement (slightly improved) are not registered as responders. The comment
that patients “significantly improved” is premature if the subjects who are counted
as responders included those who were slightly improved. Further, the SGA is a
five point scale with three items reflecting positive treatment response and two
items reflecting negative treatment response. This measure has been criticized
as biasing patients in favor of positive response. In other words the outcome data
may be based on format of scale vs therapeutic benefit of treatment procedures.
7. Please specify the primary outcome measure. It is either the IBS-SSS or the
IBS-QOL but not both. The researchers should consult IBS clinical trial guidelines
which regards quality of life as an important secondary outcome. A rationale for
defining it as a primary outcome is necessary
8. The researchers make much of the change scores from baseline to 6 weeks
but the more important change score is between baseline and 12 weeks. The
pre- post treatment scores were 35 for the IBSSS and 5 for the IBSQOL neither
of which are clinically significant. These data raise questions about the
therapeutic benefit of featured treatments. A major question is whether any
treatment gain is (1) clinically significant and (2) whether it can be confidently
attributed to the experimental conditions. The authors do not make this case
which is a major limitation if not fatal flaw of the study
9. It is unclear where an expectation of a 20% drop out rate was based. I believe
the dropout rate for the Drossman trial was about 35%. Sample size seems
based on inaccurate estimations of sample size. By their own acknowledgement,
the researchers concede in the discussion that the study is underpowered
10. The researchers are on shaky ground to argue that “patent with access to
Regul8 website felt better able to cope with their symptoms with their symptoms”
when no coping measure was administered. This reflects a general tendency to
make conclusions that go beyond data.
11. It is not clear whether a manualized protocol guided treatment.
12. How was missing data dealt with?
13. The methodology of the trial could be strengthened with a blind assessor
Minor Essential Revisions
1. The manuscript in general is not as well written as it should be. There are
many mechanical problems that are distracting and undermine the readability of
the paper. Sentences are incompletely structured; spelling mistakes are many;
and the paper in general has a rushed quality that demands tighter editorial
review.
2. It would be helpful for authors to paginate the pages
3. The CONSORT diagram should be reformatted so it fits on one sheet of paper
not 3
4. The discussion of web based CBT for non IBS problems needs beefing up.
There are a number of areas that highlight the promise of eCBT (e.g. insomnia).
The researchers should look for support beyond he work of one investigative
team in a culturally and geographically unique setting.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Declaration of competing interests:
'I declare that I have no competing interests' below. If your reply is yes to any,
please give details below.
assistant