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): 

Review of manuscript “The effect of military training on the sense of agency and outcome processing 
under coercion” by Caspar et al. 

This is an impressive paper and behavioral approach on a highly relevant topic. The authors extended 
their previous important work and methodology on the sense of agency under coercion to a new topic 
that is difficult to study: agency in different conditions of hierarchical organization. In particular 
military conditions/situations and how military training may alter the sense of agency and its 
dependence on coercion. For this the authors carried out two studies in carefully selected large groups 
of people differing in their military training and profession and compared them to non-military 
controls. They used intentional binding, embedded within the classical Milgram paradigm. Additional 
data were recorded using EEG. 

The authors find that coercion and differences in military experience modulate intentional binding and 
that military training can correct/alter such effects. It is argued that their data provide insights on a 
dynamical process underlying sense of agency by showing how specific military training effects 
modulate agency. 

Below I list several questions and concerns I have about the results and discussion and the manuscript 
more generally that the authors should take into account when preparing a revised version of the 
manuscript. 

Subjective sense of agency and intentional binding: Following their work on intentional binding and 
coercion in civilian volunteers (reference 13), the authors here use the elegant measure of intentional 
binding to gauge the sense of agency and extend to responsibility and the sense of agency in the 
military context. This is, of course, a valid and interesting approach. However, I am concerned how a 
behavioural measurement, based on interval estimates, is sufficient to estimate the subjective sense 
of agency. I agree that, as the authors mention, that explicit reports of the sense of agency may be 
problematic, but additional data using explicit measures on the subjective sense of agency need to be 
added to the intentional binding data, on a trial by trial basis. Such additional would confirm/extend 
the existing intentional binding data and allow authors to directly relate their data to aspects involving 
the subjective aspects of agency, especially since these latter aspects figure prominently the 
manuscript text (in introduction and discussion). Such additional data should ideally be measured on a 
trial by trial basis and not at the end of the experiment. Did the explicit data that the authors recorded 
(i.e. p6) correlate with the intentional binding data? 

EEG data: 
Whereas the experimental paradigm, the recruited groups, and the findings on intentional binding are 
solid (but see my previous comment), it is not clear what the EEG study and the recorded data add to 
the overall story. What was the main scientific reason to add this analysis? 

In addition, the authors recorded 64 channel EEG, but only minimally analyzed their data and focus 
only on analysis of the N1 auditory component. In my opinion, the quality of the paper and reported 
data would be improved by deleting the EEG data. For example, it was not clear to me what Fig.3b 
and 5b (topo plots) are adding to the manuscript. 

There is much previous work on the N1 component and more complete approaches exist to fully 

analyze multichannel EEG data. If the authors decide to leave the EEG data in the manuscript, more 
extensive EEG analysis about the involved brain processes should be added. 

Finally, in both studies, the EEG data do not confirm the behavioural intentional binding findings and 
even seem to contradict them? This holds especially for the results of study 2. 

The experimental manipulation of intentional binding and its integration into a complex behavioural 
paradigm (Milgram paradigm) was carried out across very relevant and carefully selected 
conditions/groups. This is an important achievement and based on excellent previous work from this 
team of authors. However, the authors only briefly refer to Milgram’s original paper in the 
introduction. Have other groups confirmed these results? Have other related paradigms been 
developed and tested? 
Results study 1: Authors used z-transformed data, which is fine. Yet, they should also report original 
data (for example as supplemental data). This would also be important in order to be able to compare 
the magnitude of intentional binding in the present data with previously reported data. 

The normalized data plotted in Fig.2 for the junior cadets are 0. Does this suggest that people in this 
group have on average no agency or intentional binding in this group (free choice condition)? 

For the data on intentional binding from study 2, do the number of years of military training that have 
been received correlate with the differential findings and the magnitude of intentional binding in junior 
and/versus senior cadets? Are such correlations different from those in privates? 

The general discussion is quite long and should be shortened (moving less scientific parts to the 
supplemental). Yet, I was missing a section on the limitations of the study. The authors should be 
more careful when discussing subjective sense of agency versus intentional binding. 

Reviewer #2 (Remarks to the Author): 

Comments to the authors 

The present manuscript reports results from two studies investigating the effects of social coercion, 
i.e. following orders, as compared to deciding freely on the sense of agency (SoA) as well as 
electrophysiological measures of sensory outcome processing. Further, the authors test whether 
individuals working in contexts marked by different levels of social hierarchical structure (i.e. civilians 
and differently ranked individuals in the military), are impacted differently by social coercion. In both 
studies, participants (civilian students and junior cadets in study 1; privates, junior cadets, and senior 
cadets in study 2) took turns in a task in which they can increase their own monetary benefit by 
applying painful electric shocks to the other person in the dyad, and hear a tone after choosing to 
apply electric shocks (or not) to the other individual. In one condition, subjects were free to choose 
whether or not to apply electric shocks (free choice condition) and in the other, they are ordered to do 
so by a third individual (coercion condition). 

The main outcome measures in both studies are 1) an implicit measure of SoA, i.e. subjective 
estimates of the temporal interval between choice and tone and 2) the auditory N1, which is 
associated with auditory outcome processing. Generally, reductions of the estimated temporal interval 

for actions perceived to be one’s own actions (or in the present case: free choices) are termed 
intentional binding (IB). The N1 has been shown to be reduced under conditions of coercion in a 
previous study from the same group. 

The central claim that the authors make is that strict hierarchical social contexts such as the military 
can impede the differentiation of free and non-free choices (reduced coercion effect on IB) for those 
subjects whose environment is not marked by high responsibility or accountability (i.e. privates and 
junior cadets in the present case). Furthermore, the authors argue for an impact of military training 
on electrophysiological measures of outcome processing. Precisely, they state that senior cadets, i.e. 
individuals who are trained to give orders and be held accountable for their actions present generally 
increased markers of outcome processing (higher N1 amplitudes), while individuals who are used to 
following orders show generally reduced N1 amplitudes. Thus, hierarchical social environments are 
claimed to impact both SoA as well as neural outcome processing. 

The present work is embedded into a theoretical, historical, and philosophical context that is highly 
interesting and aims at fundamental questions of social determinants of responsibility, human agency, 
and morality. I believe that the description of methods is detailed enough in order for other 
researchers to reproduce the studies reported. However, while I find the ideas and questions 
highlighted by this manuscript interesting, I am not convinced that all of the conclusions drawn are 
valid. I detail my concerns in the Major points below. Furthermore, some aspects of the manuscript 
were not clear to me, some of which might be due to wording, others due to unclear or missing 
information (Minor points below). 

Major points: 

A central claim the authors make is that upon entering the military, the strict hierarchical organization 
and need to follow orders leads junior cadets to show a reduction of SoA, measurable as a diminished 
coercion effect on IB. The authors argue that the nevertheless observable N1 reduction under coercion 
in study 1 (as in civilian students) might be due to the short period of time junior cadets have so far 
spent in the military and imply that structural brain changes underlying such an effect could require a 
longer time spent in this environment. As I take it, this is one reason for comparing junior cadets to 
senior cadets in study 2, as the latter will have spent a longer time in the military than the former, 
and hence, alterations in the N1 component might be observed after this longer time of training. 
However, I am not convinced that the observed effects are necessarily attributable to years spent in 
such environments, as claimed by the authors. The authors themselves state (in the reporting 
summary) that senior cadets are “even more limited in number than junior cadets”, implying a 
selection process taking place between being a junior and a senior cadet. Thus, it is possible that the 
differences observed between these groups are due to other factors (personality, etc.) that are 
already evident in those junior cadets who will later become senior cadets, but not in those who will 
not achieve this status. In study 1, several psychometric instruments were completed by the 
participants, and results on these are reported in order to test whether the results of study 1 could be 
due to any differences in these measures. However, it is unclear whether any such differences exist in 
study 2, and whether the results could be explained by such differences. Could the authors provide 
this information so that any potential confounds with regard to personality differences can be ruled 
out? 

Related to my previous point, I would like to note that I think the usage of the word “regain” or 
“regained” in the context of the observed effects in senior cadets is perhaps too far-reaching, since it 
implies that those subjects in the group of senior cadets have in fact experienced a sense of agency 
reduction upon entering the military, which they have later regained. However, we do not know 
whether the effect observed in junior cadets is due to entering the military or whether it was pre-

existing in those individuals choosing to become officers (although the authors show that some 
relevant psychometric scales do not correlate with the effects of interest in study 1). Additionally, the 
term “regain” implies that such a reduction in SoA was later reversed, possibly but not necessarily due 
to the emphasis on accountability during officer training, as argued by the authors. Yet, the conclusion 
that this process actually takes place is not warranted, since (self-)selection processes might allow 
certain individuals to eventually become senior cadets (who were more difficult to recruit than junior 
cadets), while others (perhaps those who showed lower sense of agency and accountability for own 
actions before starting their officer training) might not be selected for senior cadet. Hence, I think the 
authors’ claims, while tempting, are to be taken with a grain of salt and this should be reflected in the 
wording. While this might seem like a minor point, it is part of the larger question regarding the 
validity of some of the conclusions drawn. 

The authors argue that strict hierarchical social situations, like being a private in the military, should 
impact both implicit measures of SoA, i.e. the intentional binding (IB) effect, as well as 
electrophysiological measures of sensory outcome processing, i.e. the amplitude of the N1 component. 
While the authors provide separate statistical tests regarding effects of the experimental factors on 
these measures (i.e. ANOVAs), they do not elaborate on the question of whether these measures 
should be correlated in any way and do not report correlations between the central outcome measures 
within experimental groups. I would assume that subjects experiencing stronger differences in SoA 
between conditions (larger IB effect) might also display more differentiated neural outcome processing 
in response to outcomes that are due to freely chose actions vs actions due to commands from others. 
If no correlations between these measures are to be expected, what are the reasons for this? Are 
there any arguments speaking against the assumption that SoA and IB should be correlated or are 
there any methodological reasons impeding tests of this hypothesis? 

In the general discussion, the authors relate their findings to results from a study showing that 
disobeying an expert’s advice leads to stronger activity in anterior cingulate cortex (ACC) and superior 
frontal gyrus than disobeying a non-experts advice (SFG, Suen, Brown, Morck, & Silverstone, 2014). 
They draw on this study to argue for a potential effect of neural attenuation and neural cost on the 
dynamics of whether and why certain individuals might be more or less prone to defy authority. 
However, I could not fully follow their reasoning. One cause of this is that it was not clear to me what 
general psychological (or physiological) process the authors assume to link the N1 effects observed in 
the present study (which are responses to auditory action outcomes) to the MRI effects observed by 
Suen and colleagues, that were observed during choosing to follow or not follow the advice of another 
person (i.e. not necessarily linked to the outcome). Could the authors please 1) try to clarify this point 
to help readers follow the reasoning more easily and 2) elaborate on their concept of “neural cost” and 
the precise processes they assume to underlie social (dis)obedience? 

The authors note that in study 2, all three groups (i.e. privates, junior cadets and senior cadets) were 
tested by what the authors call “another senior captain”. I find this somewhat confusing, as the term 
captain is used before, but not introduced, and it is therefore unclear whether “senior captain” is 
equivalent to “senior cadet”, especially due to the word “another” in the methods section of study 2. 
For readers who are not familiar with the exact terminology of military ranks it therefore seems like in 
study 2, the group of “senior cadets” was tested by “another” individual with the same rank, which 
raises the question of whether the experimental condition was comparable to that of the other two 
groups where an individual of a higher rank was running the experiment and giving orders. Precisely, 
if in fact “senior cadet” and “senior captain” are equivalent ranks, the group of senior cadets in study 
2 would have been coerced by an individual with the same rank, while junior cadets and privates 
would have been coerced by an individual with a higher rank, which in the logic of the manuscript, 
could well impact the results. Perhaps, the issue I am raising here boils down to something negligible 
that can be resolved by a clear differentiation of the ranks “senior captain” and “senior cadet”, in 

which case I would retract this criticism. Otherwise, I think it would be beneficial to the manuscript if 
the authors could argue why they think that equivalence of ranks is not relevant to the results of the 
study and their interpretation (NB: We do see that there is a coercion effect on IB in the group of 
senior cadets in study 2, which provides evidence that despite a potential equivalence of military ranks 
of senior cadets and senior captains, coercion still impacts SoA). 

Minor points: 

As stated in the methods section to study 1, agents were asked to wait 2 seconds before pressing a 
key. Did this apply to both conditions, i.e. in the coercive condition were agents instructed to wait 2 
seconds after being told to apply a shock or not in order to obtain a noise free baseline? Otherwise, 
auditory processing could influence the baseline in the coercive condition (although I am aware that 
this would not have an effect on between-group comparisons). 

In line 424, what do the authors mean by “similar personnel strategy issues”? Does this formulation 
mean that different groups of individuals might make different use of the scale of 1-1000 ms for rating 
temporal intervals? 

In lines 425-426 the authors note that the type of experimenter did not influence the results in study 
1, and hence “we decided not to include these two factors in the analyses of Study 2”. With type of 
experimenter being one factor, which is the other factor? Or is this simply a mistake in wording? 

In line 463, the authors state that they applied Bonferroni correction to correlations. However, no 
correlations are reported, so it is not clear what this information relates to. 

In line 542, the term "evoked-related" should be "event-related" or "evoked", I assume. 

Were any measures taken in order to remove artifacts from the EEG data, such as visual inspection 
and manual removal of epochs or ICA? 

The article by Suen, Brown, Morck, and Silverstone (2014) that is cited in the discussion is not 
included in the bibliography. 

In the reporting summary, it is stated that 32 electrodes were used for EEG recordings, which conflicts 
with the statement in the main manuscript, where it states that 64 electrodes were used. 

In the sampling strategy, there is an error regarding the power of study 2. It says that power was 
increased to .09, which should be .90, I assume. 

In line 247, does the word “similar” in fact mean that the order of conditions was the same for both 
individuals in a dyad? 
On p. 15, line 648, the word “neurally” is misspelled (“neutrally”). 

Best regards, 
David S Stolz