Peer review of: The effect of military training on the sense of agency and outcome processing (2020)



Reviewers' comments: 

Reviewer #1 (Remarks to the Author): 

I reiterate that this is an impressive study and behavioural approach on a highly relevant topic. The 
authors responded to many of my comments. However, I am still concerned about the evaluation of 
the sense of agency (explicit and implicit), the N1 erp data (and the variable relation to behavioural 
measures) and how this presented in the revised manuscript. Despite the unresolved concerns listed 
below, I encourage the authors to make another effort in revising the manuscript. 

C1 
I am not convinced by the authors answer and still concerned how interval estimates can be sufficient 
to estimate the subjective sense of agency, especially given the prominent discussion of the subjective 
aspects of agency in the manuscript. A measure of the sense of agency by an explicit measure is still 
missing and I disagree that such a measure would be uninformative. 
I was actually not asking the authors to alter their paradigm by adding different action consequences 
with for example incongruent trials (which may be an entirely new project, requiring very careful 
ethics). Without changing any action outcome, I wondered whether explicit agency ratings may show 
a coercion modulation on the subjective sense of agency (that may additionally differ across tested 
populations)? This evaluation would be important to add. Otherwise the authors should modify the 
manuscript more strongly and avoid emphasis on subjective and sense of agency. 
I had asked whether the authors had performed correlation analysis between explicit judgements 
(those they had already measured as I had understood) and time estimates? Could not finds this in 
their response. 

C2-3-4 
The authors added a short helpful statement to the revised introduction. I am concerned though that 
they responded to my question C3 as if a more detailed analysis of the N1 would amount to a “fishing 
expedition”. Again, the N1 component in ERPs has been linked to many other perceptual, motor and 
cognitive aspects beyond outcome processing. It may not reflect outcome processing, but any of the 
other processes. In addition, not many readers may be familiar with the term outcome processing. 
This should be clearly expressed in the revision. Please clarify these issues in a re-revision. 
Has the present study been pre-registered? 
Finally, the variable relationship between N1 and intentional binding (C4) remains unclear, and adds 
to the complexity of factors likely at work in this study. 

Reviewer #2 (Remarks to the Author): 

Comments to authors 

I appreciate the authors’ efforts to improve the manuscript and to address the concerns raised by 
reviewer 1 and myself. Below, I will first comment on the extent to which I believe the authors 
responses and extensions to the manuscript satisfy the old concerns raised. Second, I shortly note a 
point regarding the discussion section that I could not entirely follow. 

Old concerns: 

Regarding the potential limitations due to possible selection biases, I appreciate the authors’ efforts in 
explaining why they were not able to conduct the study suggested by the editorial team. I also 
appreciate the efforts shown by re-contacting the civilian participants in order to gather more data and 
for the additional analyses that are now contained in the manuscript with the goal of ruling out – as 
far as possible – the possibility of selection biases. I do think that these analyses have added to the 
quality of the manuscript and provide relevant evidence in support of the authors’ main claims. 

Regarding the concern raised by reviewer 1, i.e. whether there is a need for explicit, trial-by-trial 
sense of agency (SoA) ratings, I can follow the authors’ reasoning that ethical limitations on the study 
design (subjects need to be able not to shock, if they don’t want to) impede the usefulness of such 
ratings for the present experimental protocol. Yet, a closer understanding of the exact relationship 
between intentional binding, explicit ratings of sense of agency and outcome processing would indeed 
be desirable (both on conceptual levels and with regard to biological correlates and mechanisms), but 
I take it that it is not the focus of the presented experiments to provide deeper insights into this. 
Thus, I think that the present data suffice for demonstrating that (implicit) sense of agency and 
outcome processing can be impacted by (extreme forms of) social hierarchies such as the military. Put 
differently, the data demonstrate that the previously introduced “coercion effect”, i.e. the parallel 
reduction of N1 amplitude and “stretching” of perceived time intervals (intentional binding), are 
influenced by one’s social environment. However, I assume the exact 
(psychological/conceptual/biological) mechanisms linking (explicit and implicit) measures of sense of 
agency to neural outcome processing need to be addressed in other studies. I think that the 
manuscript would profit from a at least a short statement in the discussion that reiterates this point, 
picking up the one in the introduction (lines 134-137), and again pointing to relevant literature or 
open research questions. Otherwise, sense of agency and outcome processing appear somewhat side-
by-side, with some implied link between them, that however remains unresolved at the end of the 
draft. 

Related to the previous point, I think that the N1 data serve to demonstrate that neural outcome 
processing may potentially be affected by environments marked by strong hierarchical organization. 
Yet, I agree with reviewer 1 that it is not clear what the topographic plots add to the story of the 
manuscript. Perhaps, in order to reduce the impression that the topographies are of central relevance, 
moving them to the supplements or reducing their size in relation to the N1 bar plots could help 
streamlining the appearance of the draft and aid pointing the readers in the right direction. 

I believe that removing the paragraph on neural cost from the general discussion has improved the 
clarity of the manuscript. 

I would like to thank the authors for addressing my remaining criticisms by clarifying several points 
that irritated me in the first review round. 

New comment: 

In the second-to last paragraph of the discussion of study 2 (lines 394-402), the authors, to my 
understanding, are arguing the possibility that N1 effects are due to differences in education levels 
between groups. First, they say that differences between privates and seniors could be due to 
differences in education. Next, they state that despite differences in education between seniors and 
juniors, there was no difference in the N1 amplitude. Together, I take it, they argue that these 
disparate findings argue against the possibility that education differences dominantly influenced the 
results (because then, juniors and privates should be more similar, because they both have 
considerably lower education than seniors). However, the last sentence of the paragraph appears to 

state the opposite (specifically, in lines 401-402): “It is thus more likely that differences between our 
groups is the mere results of difference in education degree”. Shouldn’t it rather be: “… it is thus 
unlikely that the observed differences between these groups are the mere result of differences in 
education degree”? If the sentence is in fact correct in the way it is currently written in the draft, this 
would mean that the authors think the N1 effects are due to education, and not to military training. 

Best regards, 
David S Stolz