Reducing Choice-Blindness? An Experimental Study Comparing Experienced Meditators to Non-Meditators

Round 1

Reviewer 1 Report

This paper overall studied an interesting question. I want to make the following comments for the authors to improve this manuscript.

1. The introduction section is not well written. Not having done research does not constitute a motivation for your research. Why your research is important? Please revise this section to prove the necessity and Importance of this study.

2. What is your research question？Can you formulate a hypothesis or draw a diagram?

3. The study was conducted in each subject's home, not in a consenting laboratory. How do you ensure that other environmental factors, such as noise, are excluded?

4. Can you report the T-tests of focal variables between the two groups in Table 1?

5. Could report the BIC value in Table 2?

6. The Discussion section should be divided into two sub-sections. i.e., conclusion and limitation.

7. The references are rather outdated, especially lacking in the last two or three years of research, so please revise them to reflect the cutting edge of your research.

Author Response

Dear Sir or Madam,

 

We thank you warmly for all your comments which we found very constructive. They have been useful to us in improving our manuscript. We have made a number of changes to the document based on your suggestions. Below you will find our responses to your comments. We hope that they will clear any confusion and that the modifications we have made will meet your expectations.

 

1. The introduction section is not well written. Not having done research does not constitute a motivation for your research. Why your research is important? Please revise this section to prove the necessity and Importance of this study.

 

We have added four paragraphs in the introduction (see ll.22-57). We clarified the motivations and possible implications of our research and mentioned a new study reporting research similar to ours (see Petitmengin et al., 2013).

 

2. What is your research question？ Can you formulate a hypothesis or draw a diagram?

 

We have added a paragraph in the introduction (see ll.139-145) to clarify the research question and assumptions: “The main hypothesis is that the mindfulness meditators should be less sensitive to the CB effect compared to the non-meditators. Thus, we suppose experienced mindfulness meditators will be able to detect more manipulations in this CB context compared to non-meditators. To investigate this, we conducted a comparative and correlational study including two groups: a group of experienced mindfulness meditators (experimental group) and a group of non-meditators (control group). We count the number of times participants in each group report detecting a manipulation.)”.

 

3. The study was conducted in each subject's home, not in a consenting laboratory. How do you ensure that other environmental factors, such as noise, are excluded?

 

In order to minimize the possibility of participants being disturbed during the experiment, they were instructed to carry out the experiment at home in a quiet place and to ensure that they were not disturbed for 30 minutes (duration of the experiment). In addition, participants were asked at the end of the experiment to report any disturbances they may have experienced during the experiment. A paragraph has been added in the manuscript to clarify this (see ll.188-192).

 

4. Can you report the T-tests of focal variables between the two groups in Table 1?

 

We did not perform a T-test on the demographic variables because some of them contain a small number of subjects (ex. DUG : 0 vs. 2). The values presented in Table 1 are indicative and correspond to a descriptive statistics paragraph. Only one T-test was performed on the FMI score (presented at the end of the table). This test is reported in the endnote (3) (ll.430-433) and is mentioned in the "Definition of the groups" section (l.174) : "The two groups were found to be significantly different (t64 = -2.594, p = .012) with a medium effect size (with d = .64)."

 

5. Could report the BIC value in Table 2?

 

Thank you for the suggestion to add the BIC in table 2. We have reported it (p.8) and also added a paragraph that discusses the choice of AIC rather than BIC (ll. 369-381): “Another potential limitation of our study is the disagreement between the model selection criteria (AIC and BIC) which could indicate ambiguous models. Each criterion has a different purpose. AIC aims at selecting the best model which predicts the data, while BIC aims at selecting the true model which generated the data. As a consequence, AIC has the tendency of favoring too complex models, while BIC has the opposite tendency of favoring too simple models when the true model is not in the list of tested models. Much debate exists concerning the criterion that should be used, and for what purpose (Kuha, 2004). In this paper, we decided to focus on AIC as we do not claim that a model containing only the practice of mindfulness as a predictor of the detection of manipulation can really be the true model which generated the data. Moreover, BIC converges toward selecting the true model when the quantity of samples goes toward infinity. With a limited number of samples here, we considered AIC to be the better criterion.”

 

6. The Discussion section should be divided into two sub-sections. i.e., conclusion and limitation.

A subsection "Interpretations" has been added to the "Discussion" section (l.275).

 

7. The references are rather outdated, especially lacking in the last two or three years of research, so please revise them to reflect the cutting edge of your research.

 

Three additional recent references have been added to the text:

• Morris, A. (2021). Invisible gorillas in the mind: Internal inattentional blindness and the prospect of introspection training. (l.295)
• Arora, J., Gupta, M., & Parnami, A. (2019). Choose a lift and walk into it: Manifesting Choice Blindness in Real-life Scenarios using
  Immersive Virtual Reality. In The Adjunct Publication of the 32nd Annual ACM Symposium on User Interface Software and Technology (pp.84–86). (l.134)
• Brandtner, A., et al. (2022). A preregistered, systematic review considering mindfulness-based interventions and neurofeedback for targeting affective and cognitive processes in behavioral addictions. Clinical Psychology: Science and Practice. (l.95)

 

We have also added the following reference:

• Kuha, J. (2004). AIC and BIC: Comparisons of assumptions and performance. Sociological methods & research, 33(2), 188-229.
• Petitmengin, C., Remillieux, A., Cahour, B., & Carter-Thomas, S. (2013). A gap in Nisbett and Wilson’s findings? A first-person access to our cognitive processes. Consciousness and cognition, 22(2), 654-669.
• Vermersch, P. (1999). Introspection as practice. Journal of consciousness studies, 6(2-3), 17-42.
• Vermersch, P. (1994). L'entretien d'explicitation. ESF Sciences humaines.

 

 

We thank you once again for all your pertinent remarks, and hope that these answers will satisfy you and improve the understanding of our article.

 

Yours sincerely,

Léa Lachaud, Baptiste Jacquet, and Jean Baratgin

Author Response File: Author Response.docx

Reviewer 2 Report

I think this paper is great and should be published. I'm really glad somebody did this study. I just had a few minor suggestions.     - There's an important paper anticipating this work that I think the authors missed. It's: Petitmengin, C., Remillieux, A., Cahour, B., & Carter-Thomas, S. (2013). A gap in Nisbett and Wilson’s findings? A first-person access to our cognitive processes. Consciousness and cognition, 22(2), 654-669. (Link: https://www.sciencedirect.com/science/article/abs/pii/S1053810013000275.) They do a mindfulness-related intervention during a choice blindness study and find that it dramatically reduces CB. I think the present experiment is different and presents a novel contribution, but the authors definitely need to cite and discuss this past work (and remove/modify their claim that "This study is the first of its kind to explore the potential link between mindfulness and CB").     - I think the authors oversell their findings in the general discussion, and underemphasize the fact that this is just a correlational study and there are many other alternative explanations for the results that do not involve meditation improving introspection. They only consider one alternative explanation, in the paragraph starting on line 309 ("It could be argued that an alternative interpretation of our results would be that experienced meditators could have already had a greater ability for introspection even before practicing mindfulness.") -- but then they quickly dismiss this explanation because the FMI scores don't predict choice blindness. This logic does not make sense to me. There are lots of reasons that the FMI scores don't predict choice blindness (as the authors themselves discuss in the next section) -- that doesn't mean that the meditators were not better at introspection before starting meditation! Moreover, there are many other potential differences between meditators and non-meditators that could explain the results. Maybe meditators are smarter? More educated? Less susceptible to deception? Etc etc. The authors need to be far more careful in the inferences that they can draw from this correlational data.     - The authors only compare meditators vs. non-meditators, but they could also look at whether the amount of time spent meditating among the meditators predicts choice blindness. If it does, that would strengthen their case. If it doesn't, the authors need to give an explanation for why not.     - The authors are too quick to claim that meditation for sure improves introspection. That's certainly what many meditators claim, but the amount of existing, objective evidence for it is very limited. See Morris, A. (2021, September 26). Invisible gorillas in the mind: Internal inattentional blindness and the prospect of introspection training. https://psyarxiv.com/4nf5c. (The papers that the authors cite to back up this claim either rely entirely on self-report data, or are about interoception into bodily sensations and not introspection into mental processes.) Rather, the authors should frame this as a hypothesis which their paper helps to test.   - The whole paragraph starting on line 83 about the relationship between FMI scores and meditation didn't make sense to me. If meditation increases FMI scores, how can FMI scores not be related to meditation? I think the authors either need to clarify this paragraph or remove it (it didn't seem super necessary for their argument, and just confused me).   The last thing is that this paper could really use some editing from a native or fluent English speaker; there were many sentences that were not very grammatical, or were confusingly worded. I don't want to count that against the authors, but getting some editing by a native English speaker would help the paper reach a wider audience :).

Author Response

Dear Sir or Madam,

We thank you warmly for all your comments which we found very constructive. They have been useful to us in improving our manuscript. We have made a number of changes to the document based on your suggestions. Below you will find our responses to your comments. We hope that they will clear out any confusion and that they will meet your expectations.

1. There's an important paper anticipating this work that I think the authors missed. It's: Petitmengin, C., Remillieux, A., Cahour, B., & Carter-Thomas, S. (2013). A gap in Nisbett and Wilson’s findings? A first-person access to our cognitive processes. Consciousness and cognition, 22(2), 654-669. (Link: https://www.sciencedirect.com/science/article/abs/pii/S1053810013000275.) They do a mindfulness-related intervention during a choice blindness study and find that it dramatically reduces CB. I think the present experiment is different and presents a novel contribution, but the authors definitely need to cite and discuss this past work (and remove/modify their claim that "This study is the first of its kind to explore the potential link between mindfulness and CB").

Thank you for bringing this reference to our attention. The experience presented in it is closely related to our own. We have added a paragraph mentioning this study in the introduction (ll.32-48) and have quoted it in another paragraph (l.322).

2. I think the authors oversell their findings in the general discussion, and underemphasize the fact that this is just a correlational study and there are many other alternative explanations for the results that do not involve meditation improving introspection. They only consider one alternative explanation, in the paragraph starting on line 309 ("It could be argued that an alternative interpretation of our results would be that experienced meditators could have already had a greater ability for introspection even before practicing mindfulness.") -- but then they quickly dismiss this explanation because the FMI scores don't predict choice blindness. This logic does not make sense to me. There are lots of reasons that the FMI scores don't predict choice blindness (as the authors themselves discuss in the next section) -- that doesn't mean that the meditators were not better at introspection before starting meditation!

We thank you for this interesting remark. We had wanted to test whether the FMI items corresponding to introspection items alone had an influence on the manipulation detection score. It turned out that this was not the case. You are correct in noting that this does not support the claim that the meditator group did not have a predisposition to introspection before they began meditating as we could not measure their scores before they began their practice, which is why we ultimately chose to delete this paragraph. We have also added that this study is correlational, which does not allow us to assert a causal link (see ll. 342-345 and l.142).

3. Moreover, there are many other potential differences between meditators and non-meditators that could explain the results. Maybe meditators are smarter? More educated? Less susceptible to deception? Etc etc. The authors need to be far more careful in the inferences that they can draw from this correlational data.     

We have written an additional discussion paragraph about the implicit trust in the experimenter that might inhibit detection of manipulation (see l.319-322).

4. The authors only compare meditators vs. non-meditators, but they could also look at whether the amount of time spent meditating among the meditators predicts choice blindness. If it does, that would strengthen their case. If it doesn't, the authors need to give an explanation for why not.     

The amount of time spent meditating by the group of meditators is unknown. We only know that the participants had been practicing mindfulness at least several times a week for at least 1 year. We have added this information in the conclusion as an opening for a future study (see ll.388-394).

5. The authors are too quick to claim that meditation for sure improves introspection. That's certainly what many meditators claim, but the amount of existing, objective evidence for it is very limited. See Morris, A. (2021, September 26). Invisible gorillas in the mind: Internal inattentional blindness and the prospect of introspection training. https://psyarxiv.com/4nf5c. (The papers that the authors cite to back up this claim either rely entirely on self-report data, or are about interoception into bodily sensations and not introspection into mental processes.) Rather, the authors should frame this as a hypothesis which their paper helps to test.

It is true that it is not certain that mindfulness objectively improves introspection. We had used language that we felt was moderate, such as "the results of this study suggest that...". We have further modulated our words by emphasizing that the studies cited do not objectively affirm the improvement of introspection (see l.22, l.29, l.47). We have also added the reference you provided (Morris, 2021) in a paragraph discussing the notion of "pre-conscious" processes (see ll.295-302).

6. The whole paragraph starting on line 83 about the relationship between FMI scores and meditation didn't make sense to me. If meditation increases FMI scores, how can FMI scores not be related to meditation? I think the authors either need to clarify this paragraph or remove it (it didn't seem super necessary for their argument, and just confused me).  

We wanted to express the fact that the FMI does not measure all aspects of meditation practice. It is very common for people who have never practiced mindfulness to get a high FMI score while people who have practiced for many years get a lower score. It seems to us that if this is possible, it is because the FMI fails to measure certain aspects of mindfulness that can only develop with practice. It is partly for this reason that the IMF score generally reflects well the average level of groups formed but is not always reliable when reflecting individual practice. Because this paragraph adds too much complexity to the scope of this article, we have chosen to delete the subsection "Difficulty in measuring the mindfulness trait." We have then slightly reworded the end of the subsection "The mindful personality trait" (l.81).

7. The last thing is that this paper could really use some editing from a native or fluent English speaker; there were many sentences that were not very grammatical, or were confusingly worded. I don't want to count that against the authors, but getting some editing by a native English speaker would help the paper reach a wider audience :).

An American member of our team has proofread the manuscript. We made further changes to improve the English level of the manuscript. I hope it will be more suitable now.

We thank you once again for all your useful remarks, and hope that these answers will satisfy you and improve the understanding of our article.

Yours sincerely,

Léa Lachaud, Baptiste Jacquet, and Jean Baratgin

Author Response File: Author Response.docx