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Thanks for addressing the reviewers' concerns.
# PeerJ Staff Note - this decision was reviewed and approved by Stephen Macknik, a PeerJ Section Editor covering this Section #
Rev. 3 felt the paper was acceptable.
Rev. 1's key complaint was that the scale you use has not been validated separately and that therefore the use of the total score is in appropriate; individual item scores are preferred, with an appreciation of the potential for Type 1 error rate inflation.
Rev. 2's remaining issue is similar in direction but proposes as a solution, "The study findings and implications need to be couched in much more tentative terms throughout the whole paper (i.e. not just in the Limitations section)."
My view is that if you hypothesized a priori that the total score on your scale would predict psychological well-being or willingness to consider PEG or NIV, and you show that, the validity of the scale is not relevant to that tightly focused question. However, the validity of the scale is important for drawing more general conclusions, such as "RFT may be helpful [in] ALS" [abstract]. Furthermore, to satisfy Rev. 1, you need to present the individual item correlations. This can be supplementary material.
The abstract needs to briefly address the limitations, including the issue above and the fact that you asked about expected acceptance rather than observing actual (later) acceptance. Similarly please address the requirement of Rev. 2.
These changes are required for acceptance but I can check a revised version for compliance without troubling the reviewers further.
Also, at line 60 you write, "there has not been any research into applied RFT and people with ALS," and in Discussion you now point to the COMMEND study in the UK. The Dutch study at PubMed PMID: 29716660 may also be relevant. Would it be appropriate to soften the assertion at line 60 to say, "no published RCT results" or similar?
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The authors have addressed all of my comments well. However, I have one point that needs to be addressed in relation to their response to one of my questions:
1) Line 245: Was the Understanding and Acceptance of Interventions scale that was designed for the purpose of the study piloted or validated outside of the study? This scale should be presented in the Appendix so that readers can actually see what the 9 items are…
REPLY: The questionnaires have now been added as requested.
RESPONSE: First, the authors have not addressed my original question “Was the Understanding and Acceptance of Interventions scale that was designed for the purpose of the study piloted or validated outside of the study?”. Second, I can’t seem to find the questionnaires – they have not been uploaded as part of the manuscript or as supplemental documents.
REPLY R2: It was validated for the purpose of the present study this is stated in the method section but the wording has now been made clearer “Understanding and Acceptance of Interventions. For the purpose of the present study, a 9-item scale measuring understanding and acceptance of PEGs and a 4-item scale measuring understanding and acceptance of NIV were designed.” Also, the scale should now definitely be included as a supplementary material.
RESPONSE 2: The authors note that the questionnaire was not piloted or validated outside of the study, and was designed specifically for the study. The fact that the scale is unvalidated and the resulting impact on study findings needs to be mentioned as a limitation in the discussion. This may explain why the internal reliability of the measure of psychological flexibility was relatively low in the current study. The study findings and implications need to be couched in much more tentative terms throughout the whole paper (i.e. not just in the Limitations section) given that the questionnaire is not validated outside of the study. This may go some way towards responding to Reviewer 1's concerns, who does not think the paper is of publishable quality at present, and whose comments have not been properly addressed.
If you would like to address the comments by the reviewers, please do.
No comment
Despite several improvements in the text, following the reviewers' suggestions, the authors have failed to address the methodological shortcomings that were previously highlighted. In my opinion, the methodology does not meet the standards for a scientific publication.
Given the methodological issues that have remained unaddressed, the findings are not valid. There are great risks in publishing a flawed study, including the fact that readers may overlook the methodological shortcomings, and just go straight to the results and implications.
The authors, despite improving several sections of the paper, have not addressed the core methodological issues.
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The authors have addressed the majority of my comments well. However, there are a number of comments that still need to be addressed or require further clarification, as noted below:
1) Line 81: Why is there a difference in the take up rates of PEG feeding in the US vs. UK and Australia?
REPLY: It is presumed that the reasons for variations in take-up rates is similar to the story with NIV (as described in line 95 – 97).
RESPONSE: Then this presumption should be noted in the manuscript.
2) Line 279: The authors should correct for the number of statistical calculations that are conducted (e.g. by adjusting the alpha level)… if you perform enough calculations then you’re going to find a statistically significant result somewhere.
REPLY: Statistical analyses testing the a priori hypotheses are not adjust. However, adjustments should be made for ‘fishing expeditions’ such as might happen in tables reporting a correlation matrix. That said, we are not engaging in ‘fishing expeditions’ in our correlation tables and have now added a warning in the note section of each table regarding this matter. It is also important to focus on effect size criterion for such expeditions as p values are a simple function of effect size thus not a reliable criterion from one study to the next.
RESPONSE: This warning in the note section of each table needs to be added to Table S1.
3) Line 245: Was the Understanding and Acceptance of Interventions scale that was designed for the purpose of the study piloted or validated outside of the study? This scale should be presented in the Appendix so that readers can actually see what the 9 items are…
REPLY: The questionnaires have now been added as requested.
RESPONSE: First, the authors have not addressed my original question “Was the Understanding and Acceptance of Interventions scale that was designed for the purpose of the study piloted or validated outside of the study?”. Second, I can’t seem to find the questionnaires – they have not been uploaded as part of the manuscript or as supplemental documents.
4) Line 186: What criteria were used to diagnose ALS (e.g. El Escorial criteria) and who made the diagnosis? Did the authors ask participants what type of MND they had? Different types of MND vary in disease progression rates (with some being much more rapid and others being much slower), which may affect the relationship between psychological flexibility and acceptance of life-prolonging interventions.
REPLY: As per Line 186, verification of diagnosis was not requested. The participants weren’t asked what type of MND they had. It was considered at the time of constructing the questionnaire. In an effort to minimise participant fatigue, the value of this question in the context of this research was seen as limited.
RESPONSE: The issue of not verifying diagnosis and not asking participants what type of MND they had needs to be discussed as a limitation of the study. The issue of acceptance in different types of MND that vary with respect to rate of disease progression also needs to be discussed. It may be more difficult for participants to accept interventions when the disease is rapidly progressive as they are constantly having to adjust to physical changes and associated losses. Anecdotally, clinicians report that patients struggle more with acceptance issues if the disease is rapidly progressive as they do not have sufficient time to adjust to or come to terms with the physical changes (or they just about come to terms with one physical change and the associated decisions in relation to interventions and then something else changes, which renders the previous decision no longer applicable).
5) Lines 287-289: How many of the sample had actually accepted/rejected PEG feeding? And how many had actually accepted/rejected NIV?
REPLY: This data was not collected. The capturing of actual acceptance and rejection status was strongly considered at the time of designing the research, in fact it was the starting point to work from this position. However, we opted not to ask this question for a number of reasons. We expected that most participants may not yet be at the point where they had to accept once of these interventions. Given expectations on the number of participants, we believed setting the dependent variable at this point could leave the study grossly under-powered. Therefore, the study focussed on intentions rather that behaviour. The survey was designed so that all participants could provide answers reflective of their position, irrespective of acceptance or rejection status.
RESPONSE: Then this needs to be discussed as a limitation of the study. The fact that the authors cannot comment on whether intentions actually affect behaviour is something that should be considered further.
6) The impact of type of MND on psychological flexibility and acceptance of life-prolonging interventions. The authors noted that psychological flexibility (action) was associated with time since diagnosis (r = .450, p < .01, two-tailed) and time since first symptoms (r = .361, p < .05, two-tailed), but failed to discuss this further.
REPLY: Point acknowledged. The following has been added to the discussion sections…
“The data also suggested that a patient’s ability to take action in line with chosen goals is positively related to the time they have had ALS. This relationship may be somewhat intuitive. As time passes, patients develop a better understanding of the nature of their disease as well as the options available to them that can support their goals. Consequently, they may become better equipped to evaluate options and make decisions, as time progresses.”
RESPONSE: The issue of type of MND and rate of disease progression also needs to be discussed here. It may be more difficult for participants to accept interventions when the disease is rapidly progressive, for reasons as noted above.
7) The effect of cognition on decision-making in ALS (mild cognitive changes are common, with mild deficits being typically seen in executive functioning, attention, social cognition and language).
REPLY: The influence of Fronto Temporal Dementia (FTD) was not included in the scope of this study. Consequently, it was not included in the discussion.
RESPONSE: The issue here is not FTD, but the mild cognitive changes that are seen in executive functioning, attention, social cognition and language in 30-50% of people with MND (Massman et al., 1996; Ringholz et al., 2005). The potential impact of these deficits on decision making with respect to health interventions should be discussed further.
8) Lines 290-291: Please give an indication of what the correlation actually means for those who don’t know the AAQ e.g. “However, psychological flexibility (action) was associated with time since diagnosis (r = .450, p < .01, two-tailed) and time since first symptoms (r = .361, p < .05, two-tailed). That is, the greater X, the greater Y.”
REPLY: This should now be covered as a result of changes made in response to point 4a.
RESPONSE: I can’t seem to find this in the manuscript as the authors have not indicated where they have made the changes in the document.
9) Line 338: Please make reference to Acceptance and Commitment Therapy (ACT) when discussing what might be helpful for clients with ALS. Please also mention the ongoing studies that are looking at ACT in people with ALS and their caregivers.
REPLY: I have used the term “applied RFT” throughout the paper. This is interchangeable with ACT. Given the heavy usage of acronyms I was reluctant to introduce another.
RESPONSE: Whether or not the authors use ACT or RFT, the authors should mention ongoing studies that are looking at ACT in people with ALS and their caregivers (such as the COMMEND study in the UK).
The authors have addressed the concerns raised in my previous review. Thank you.
Unable to comment on design.
Unable to comment on validity.
From my perspective, the authors have suitably addressed the concerns raised. I look forward to seeing this manuscript as a publication.
The reviewers found the work interesting but give clear, specific suggestions to improve the introduction, analysis, reporting and conclusions. Please address each of the points raised.
The authors present an interesting, cross-sectional online study about the relationship between flexibility and the intention to adopt NIV and PEG. They also considered QOL, anxiety, and depression. The paper addresses a relevant clinical and scientific question, and I commend the authors for these efforts. However, before being considered for publication, there are some shortcomings and issues (including a major one) that should be addressed.
First, there is a problem with the title, which is misleading. The paper is not about the “adoption of”, but rather about the intentions. A title like the current one suggests a longitudinal (or, maybe, a retrospective) design, which is not the case. Please change it accordingly.
At the beginning of the introduction, please spell ALS, PEG, NIV, and RFT. Authors should re-write the beginning of the introduction with the idea that readers may not know what these concepts (especially RFT) are.
When discussing the use of NIV and PEG across different countries, please consider the role of welfare state support. For example, Italy has a very different percentage of NIV usage then the UK.
There are various theoretical frameworks around psychological flexibility, RFT is only one of these. Authors should tone down the emphasis on the theoretical model to remain more adherent to the data, which are interesting. However, the attempts to interpret everything on the light of this model reads somehow forced (it sounds like a spot or an advertisement of the model!). I suggest to re-write the aims section referring to the main construct that is explored, which is psychological flexibility.
In the methods section, authors write: “A sample size of 37 participants was recommended based on R2 = .15, power = .80, α = .05, Cohen’s f = 0.176, and six predictors.” – however, 37 was the number of participants who remained in the study. Please report this as a post-hoc power analysis (which is fine, just to be clear).
Now, the major issue. The assessment of NIV and PEG acceptance is problematic. The items have not been validated, and 37 participants are not many to validate the scale. Therefore, using an aggregated score is not the correct way to go, as there is no data that indicate the presence of a single factor. The alpha is a good indicator, but that does tell anything about the factor structure of the scale. The only way to handle this new instrument without validation is to use the items individually, with non-parametric statistics. Of course, that means to account for multiple analysis, using a Bonferroni correction or a similar technique. Most of the results section should therefore be re-written.
The reviewer will be happy to provide comments on discussion and conclusion sections, once proper analyses will be implemented.
Major comments:
1. Discussion of RFT in the Introduction is confusing and needs clarifying further:
a. Lines 53-54: What is RFT? A brief description needs to be given here… also please provide a reference for it.
b. Lines 57-63: The study by Greenaway is mentioned in the second paragraph, but no attempt is made to link this to RFT, which is discussed in the same paragraph. Furthermore, on Line 108, readers should not have to navigate back to page 1 to see details about the Greenaway study. Please remove reference to this study on lines 57-63 and move it to Line 108 onwards.
c. Line 130: What is a comparative frame?
d. Lines 136-137: What is a frame of coordination between two relational networks?
e. Lines 140-142: Please explain further.
2. Lines 103-104: There might not be studies investigating the relationship between general psychological well-being and decision-making in people with ALS, but there are definitely studies in people with other chronic health conditions. These should be mentioned here rather than studies in health people.
3. Line 146: What have studies of psychological flexibility in other chronic health conditions found? Again, there have been studies conducted in other relevant chronic health conditions (such as muscle disorders) that should be discussed.
a. Graham CD, Gouick J, Ferreira N, Gillanders D. The influence of psychological flexibility on life satisfaction and mood in muscle disorders. Rehabil Psychol. 2016;61(2):210-7.
Minor comments:
1. Line 81: Why is there a difference in the take up rates of PEG feeding in the US vs. UK and Australia?
2. Line 91: Please spell out BiPAP abbreviation in full and abbreviate thereafter.
3. Lines 108-112: A 5-line sentence is taxing for the reader. Please separate long sentences such as these into shorter sentences.
4. Figure 1 is unnecessary and therefore should be dropped. It is a simple model that does not add much to the paper beyond the description that is already given in the text.
5. The Abstract fails to mention the lack of findings for NIV.
Major comments:
1. Line 279: The authors should correct for the number of statistical calculations that are conducted (e.g. by adjusting the alpha level)… if you perform enough calculations then you’re going to find a statistically significant result somewhere.
2. Line 245: Was the Understanding and Acceptance of Interventions scale that was designed for the purpose of the study piloted or validated outside of the study? This scale should be presented in the Appendix so that readers can actually see what the 9 items are…
Minor comments:
1. Line 186: What criteria were used to diagnose ALS (e.g. El Escorial criteria) and who made the diagnosis? Did the authors ask participants what type of MND they had? Different types of MND vary in disease progression rates (with some being much more rapid and others being much slower), which may affect the relationship between psychological flexibility and acceptance of life-prolonging interventions.
Major comments:
1. Lines 287-289: How many of the sample had actually accepted/rejected PEG feeding? And how many had actually accepted/rejected NIV?
2. Lines 298-300: Interpretation of the results should occur in the Discussion and not the Results. Also, no reference was made to the fact that the lack of internal reliability for willingness in the current study (Cronbach’s alpha = 0.47) is probably the biggest factor here, rather than “willingness… may not be an influential variable”.
3. Lines 358-364: There is not enough discussion of the lack of findings for NIV with respect to psychological flexibility. This needs to be discussed more.
4. Line 330: There are a number of issues that need discussing further:
a. The impact of type of MND on psychological flexibility and acceptance of life-prolonging interventions. The authors noted that psychological flexibility (action) was associated with time since diagnosis (r = .450, p < .01, two-tailed) and time since first symptoms (r = .361, p < .05, two-tailed), but failed to discuss this further.
b. Whether participants had actually accepted/rejected PEG feeding or NIV.
c. The effect of cognition on decision-making in ALS (mild cognitive changes are common, with mild deficits being typically seen in executive functioning, attention, social cognition and language).
5. Lines 366-378: Please discuss the limitation that this is a cross-sectional and not longitudinal study and the implications of this with respect to the findings. Please also discuss the limitation that N=10 participants per predictor variable is typically recommended, making this study underpowered given that there 6 variables.
Minor comments:
1. Lines 290-291: Please give an indication of what the correlation actually means for those who don’t know the AAQ e.g. “However, psychological flexibility (action) was associated with time since diagnosis (r = .450, p < .01, two-tailed) and time since first symptoms (r = .361, p < .05, two-tailed). That is, the greater X, the greater Y.”
2. Lines 315-317: No mention is made of the fact that the overall model was not significant (p > 0.05).
3. Line 338: Please make reference to Acceptance and Commitment Therapy (ACT) when discussing what might be helpful for clients with ALS. Please also mention the ongoing studies that are looking at ACT in people with ALS and their caregivers.
4. Line 372: Please discuss other studies that have identified problems with the AAQ… there’s a reason why the AAQ-2 was developed!
This was a small cross-sectional study (N=35) that examined the relationship between psychological flexibility, psychological wellbeing and understanding and acceptance of life-prolonging interventions in people with ALS. This is an interesting topic in an under-researched area, and so represents a novel study. The paper was generally well-written, but requires major amendment in light of the specific comments.
Thank you to the authors for this enjoyable and interesting manuscript. It will add to our understanding of the difficulties patients face when considering NIV.
My comments on the reporting of the study focus on terminology, and better explaining the concepts raised to a non-psychology audience.
In the first paragraph of the introduction, please expand all the acronyms used. Although they are given in the abstract, they should also be present in teh manuscript body
RTF is raised in the second paragraph of the introduction, but no explanation is given for the acronym, or the theory at this point. I suggest you give an explanation of RTF at this point. Your manuscript requires that readers understand this theory very early.
The details of the method are all included and reported sufficiently. The significance of the work is stated and justified sufficiently.
I am unable to comment on the statistical analysis.
The Discussion is generally well stated and referenced.
Even so, the expression of last statement of the discussion might need reconsideration -the complexity of PEG decision-making definitely differs from that of NIV.
The Limitations section covers a good range of points. Also consider any possible cultural differences/attitudes towards NIV between participant groups.(See Andersen et al (2018)Therapeutic decisions in ALS patients: cross-cultural differences and clinical implications.)
This manuscript forms a basis for future work, both qualitative and quantitative.
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