Humans have remarkable cognitive control abilities, which allow them to safely navigate complex everyday situations. For example, when crossing a street, humans can rapidly stop themselves from continuing to walk when they suddenly notice a rapidly approaching car. The process underlying this ability to stop an already-initiated action is inhibitory control. In the laboratory, inhibitory control is typically tested in the stop-signal task (Verbruggen et al., 2019), in which an initial go-signal (i.e., a cue to initiate a movement) is sometimes followed by a subsequent stop-signal, prompting the cancellation of that movement. The processes underlying behavior in the stop-signal task are described in a well-characterized cognitive model – the horse-race model (Logan and Cowan, 1984). This model purports that on each trial, the inhibitory process triggered by the stop-signal races with the movement-initiation process triggered by the go-signal, thereby determining whether an action can be successfully stopped. The assumptions of the horse-race model allow the calculation of stop-signal reaction time (SSRT) – a latent variable that expresses the speed of the stopping process, which is not otherwise overtly observable (as successful stopping is defined by the absence of a response). In a seminal study on the neural basis of inhibitory control, Aron et al., 2003 showed that lesions to the right inferior frontal gyrus (rIFG) are associated with an elongation of SSRT, prompting the proposal that 'response inhibition can be localized to a discrete region of the PFC,' namely, the rIFG. This finding has spawned a wider, highly influential theory of inhibitory control, which, in its most recent iteration, holds that 'rIFG implements a brake over response tendencies' (Aron et al., 2014). While some subsequent lesion studies have cast some doubt upon specific claims of this theory (e.g., by demonstrating that other regions outside of rIFG lead to comparable deficits, e.g., Picton et al., 2007; Swick et al., 2008; Yeung et al., 2021) or have reported conflicting findings (Floden and Stuss, 2006), the crucial role of rIFG in action-stopping, indicated by the increase in SSRT in rIFC lesion populations, is still widely prevalent in current-day neuroscientific theory.

However, the SSRT method underlying this (and other) seminal work has recently undergone several substantial challenges (e.g., Bissett et al., 2021; Matzke et al., 2017b). One of the most prominent shortcomings of SSRT is that it does not account for trigger failures (Band et al., 2003) – trials with stop-signals in which inhibitory control process was never initiated to begin with. On such trials, erroneously executed responses do not result from an insufficiently fast stop-process losing the horse race, but from the mere fact that inhibitory control never ‘entered the race.’ Crucially, including such trials in the SSRT calculation leads to artificially inflated SSRT estimates and – in the worst case – can produce fictitious group differences in inhibitory control speed, which are instead more likely due to attentional lapses (e.g., Matzke et al., 2017a). In other words, in the abovementioned example of crossing a street, a trigger failure could be indicative of a deficit in noticing the approaching car, rather than in intercepting the walking movement fast enough.

In light of this confound, it is necessary to reassess the causal link between stop-signal performance and rIFG damage. Therefore, we here repeated the original lesion study by Aron et al., 2003 with a stop-signal task that was optimized to implement a hierarchical Bayesian technique for the identification of trigger failures (Matzke et al., 2017b). We specifically tested whether rIFG lesion patients show increased trigger failure rates, especially in light of the fact that rIFG is a key region that is often implicated in stimulus-driven attention more generally (Corbetta and Shulman, 2002). Moreover, we extended the behavioral investigation by Aron and colleagues by measuring scalp-EEG. Specifically, we aimed to investigate the influence of rIFG lesions on stop-related β-bursts dynamics. β-Bursts are a recently discovered neurophysiological signature of inhibitory control (Diesburg et al., 2021; Wessel, 2020) and can provide additional insights into the distinction between the initiation and the implementation of inhibitory control. Specifically, β-burst rates over frontal cortex are increased on stop- compared to go-trials (Enz et al., 2021; Wessel, 2020; Jana et al., 2020), which has been proposed to reflect the initial stage of the inhibitory control cascade that ultimately results in action-stopping. In other words, frontal β-bursts purportedly reflect the initiation of inhibitory control. At the other end of the cascade, β-bursts over sensorimotor areas can be used to measure the successful implementation of inhibitory control. Sensorimotor β activity reflects an inhibited state of the motor system at baseline (Kilavik et al., 2013; Soh et al., 2021), and stop-related frontal β-bursts are followed by a rapid re-instantiation of these sensorimotor bursts (Wessel, 2020). This purportedly reflects the successful implementation of the inhibitory cascade and a return to an inhibited motor system (Diesburg et al., 2021).

Hence, in line with our behavioral hypothesis, we predicted that if rIFG lesion patients showed increased trigger failure rates, they would also show reduced frontal β-burst rates compared to both non-rIFG patients and healthy adult comparisons, reflecting a deficit in triggering/initiating inhibitory control. However, we furthermore predicted that when a frontal β-burst does take place in rIFG legion patients (i.e., when the cascade is successfully triggered), sensorimotor β-burst rates would be appropriately upregulated, reflecting a retained ability to implement inhibitory control, despite damage to rIFG.

In this study, we re-examined the role that rIFG plays in action-stopping and inhibitory control. rIFG has been at the center of what is arguably the most influential current neural theory of inhibitory control. The proposal that ‘response inhibition can be localized to a discrete region within of the PFC’ (Aron et al., 2003) has been highly influential (Aron et al., 2004). In its most recent iteration, the theory states that rIFG ‘implements a brake over response tendencies’ (Aron et al., 2014). Our work shows that this theory needs further revision. Indeed, rIFG does not seem to be primarily responsible for the implementation of inhibitory control. Instead, its role appears to be the triggering or initiation of the cascade that ultimately leads to the stopping of action. Concomitantly, in this study, rIFG patients showed more than fivefold increase in stop-signal trigger failures compared to matched healthy comparisons, as well as a significant reduction in stop-related β-bursts over frontal cortex (in fact, there did not seem to be any increase in frontal β-bursts in the rIFG group on stop compared to go-trials, strongly suggesting a causal role for rIFG in their generation). However, the implementation of inhibitory control itself appears to take place in other regions – and appears to remain intact in the rIFG group. In this study, this was suggested by the fact that in all groups (crucially, including rIFG patients), sensorimotor β-bursts were upregulated when a β-burst over frontal cortex did occur (i.e., when a purported initiation signal from frontal cortex was successfully sent).

There are at least two possible explanations for the finding that lesions to the rIFG cause such a substantial increase in stop-signal trigger failures. Both explanations imply substantially different roles for rIFG in cognitive control, and cognition more broadly. The first possible explanation is that the function of rIFG is to specifically trigger inhibitory control during action-stopping or braking (e.g., in the types of situations that are simulated in the stop-signal task). In this framework, rIFG would still have an inhibition-specific role – though not in the actual implementation of the underlying process, but merely in its initiation. A different, competing explanation is that the function of rIFG is to detect any salient signal, and that it fulfills no role that is specific to inhibitory control. In the stop-signal task, rIFG would therefore merely be activated because of the saliency of the stop-signal, but not specifically because of the associated inhibitory requirements. In other words, it is up for debate whether the rIFG fulfills a role that is specific to inhibitory control or stopping/braking, or one that is more domain-general.

Along the lines of the latter explanation, rIFG is prominently at the core of another influential theory, which proposes that rIFG is part of a ventral attention network that functions as a ‘circuit breaker.’ In this framework, rIFG’s role is to orient attention toward salient events – which would include, but not be limited to – stop-signals (Corbetta et al., 2008; Corbetta and Shulman, 2002). In line with this theory, fMRI work has shown that similar regions of rIFG are activated not just after stop-signals, but after any sort of salient, infrequent event (Erika-Florence et al., 2014; Sharp et al., 2010). As such, it is possible that the role of rIFG in stop-signal performance is indeed not specific to inhibitory control situations, but instead, that it merely detects the saliency of the stop-signal. In that scenario, the increase in trigger failures in the rIFG lesion group would reflect a more general attentional deficit, which – in the specific case of the stop-signal task – would express itself in the impaired detection of the stop-signal. However, while this impaired detection of the stop-signal would increase SSRT estimates, the underlying cause of that increase would be unrelated to the implementation of inhibitory control.

Crucially, however, any attempt to disentangle the domain-general detection of a salient stimulus from the stopping-specific implementation of inhibitory control is complicated by another factor. Namely, all salient stimuli, even those presented outside of stop-signal contexts, lead to an automatic, physiological inhibition of the motor system (Dutra et al., 2018; Tatz et al., 2021; Wessel, 2018; Wessel and Aron, 2017). For example, salient stimuli lead to a non-selective inhibition of cortico-motor excitability (Iacullo et al., 2020), activate basal ganglia regions involved in inhibitory pathways (Wessel et al., 2016), reduce isometrically exerted force (Novembre et al., 2018; Novembre et al., 2019), and increase motoric response times (e.g., Parmentier, 2008). Indeed, it appears as if inhibitory control is a ubiquitous part of an organism’s orienting response to salient stimuli (Sokolov, 1963). As such, inhibition and attention may be inextricably linked. If that is indeed the case, both competing theories of rIFG may be partially correct: the role of rIFG in cognitive control may indeed be domain-general, but its domain-general role may include the triggering of inhibitory control following any type of salient stimulus, specifically as part of a stereotypic and ubiquitous orienting response (Wessel and Aron, 2017). This possibility is explicitly taken into account in recent two-stage models of action-stopping (Schmidt and Berke, 2017; Diesburg et al., 2021). Either way, while it still remains to be seen whether the rIFG does have a specific role in inhibitory control or not, it seems safe to conclude that its role is not in the implementation of that process.

This latter fact is evident in this study by the fact rIFG patients could appropriately implement inhibitory control on the subset of trials in which it was ostensibly triggered successfully. This is primarily supported by the EEG-derived β-burst patterns. β activity in the LFP has long been linked to movement regulation (e.g., Kilavik et al., 2013; Swann et al., 2009; Swann et al., 2011). Recent work has shown that β activity in the human (and non-human) local field potential occurs in clearly demarcated, transient bursts (Feingold et al., 2015; Sherman et al., 2016; Shin et al., 2017). In acute stopping situations, a short-latency increase in such β-bursts over frontal cortex takes place (cf., Figure 3, see also Enz et al., 2021; Jana et al., 2020; Wessel, 2020). These frontal bursts are then followed by a short-latency increase in β-burst rates over sensorimotor cortex (cf., Figure 4, see also Diesburg et al., 2021; Wessel, 2020). Sensorimotor β has been long proposed to reflect an inhibited state of the motor system at rest (Kilavik et al., 2013; Soh et al., 2021). A re-instantiation of this sensorimotor β-bursting after frontal β-bursts has therefore been proposed to reflect the final stage of the inhibitory cascade during rapid action-stopping – the return of the motor system to its inhibited default state (Wessel, 2020). In the current study, we found that the initial frontal β-bursts immediately after the stop-signal were substantially reduced in the rIFG lesion group – both compared to healthy comparisons and compared to non-rIFG lesion patients. Conversely, however, all groups – notably including rIFG lesion patients – showed a significant increase in sensorimotor β-bursting immediately after frontal β-bursts. In other words, in cases in which a frontal β-burst did take place in rIFG patients, their motor system was successfully returned to its inhibited state.

Together, this suggests that inhibitory control, while perhaps triggered in rIFG, is implemented in other areas. While there has been vigorous debate about the role of the rIFG (and other cortical regions, such as the pre-Supplementary Motor Area (SMA); Nachev et al., 2007) in action-stopping and inhibitory control, there seems to be some degree of consensus that the final steps on the way to successful action-stopping involve an interruption of thalamocortical motor representations via the output nuclei of the basal ganglia (see Jahanshahi et al., 2015 for a review). This interruption is likely caused by the subthalamic nucleus (which is part of two long-hypothesized anti-kinetic cortico-basal ganglia-thalamocortical pathways: indirect and hyper-direct, cf., Nambu et al., 2002; Parent and Hazrati, 1995). In line with this, recent work has tracked the abovementioned β-burst dynamics further along the basal ganglia regions that are purportedly involved in the implementation of inhibitory control. Indeed, similar to the frontal β-burst rates report here and elsewhere, β-burst rates are also increased after stop-signals in both the subthalamic nucleus and the motor regions of the thalamus (Diesburg et al., 2021). Moreover, subthalamic bursts in particular are also followed by short-latency upregulations of β-bursts in sensorimotor areas, just like the frontal bursts in this study (and others). As such, it seems likely that while the rIFG is not directly involved in implementing inhibitory control, that function is fulfilled by the basal ganglia regions of the hyper and/or indirect pathways (Schmidt et al., 2013). To this point, recent work using electrical stimulation has shown that there is a direct, monosynaptic connection between rIFG and the subthalamic nucleus, and that this connection is highly relevant for the speed of inhibitory control (Chen et al., 2020). Indeed, even in healthy humans, variance in the integrity of this fiber tract directly map onto SSRT differences (Coxon et al., 2012). Together, a coherent picture emerges according to which rIFG, once activated by a salient signal (such as a stop-signal), triggers a multi-step cascade that culminates in successful action-stopping. At a minimum, this cascade involves the subthalamic nucleus, the output nuclei of the basal ganglia, and the motor thalamus, with the implementation of inhibitory control taking place in this subcortical chain. As these subcortical areas were intact in our rIFG lesion patients, it makes sense for the implementation of inhibitory control – once triggered – to be unimpaired in this population.

Due to its nature as a lesion study, the current work has some obvious limitations. First, while we believe that our lesions very closely resemble those in the original Aron et al., 2003 study, no two samples of lesion patients are exactly the same. While the lesion in this study was somewhat more rostral compared to the Aron et al. work, both centers of gravity fell within the pars triangularis of rIFG. As such, we believe that our sample is as comparable as is possible within the constraints of human brain lesion studies. Second, as in every lesion study, damage was not limited to the region of interest. Regarding studies of rIFG in particular, other neighboring regions are typically affected by lesions as well – in particular, the anterior insula. That same region is notably active during action-stopping as well (e.g., Boehler et al., 2010), though recent work has shown that it has a more prominent role in failed rather than Successful-stop-trials (Cai et al., 2014). This is perhaps sensible, given the anterior insula’s known role in action error processing (Ullsperger et al., 2010). On Successful-stop-trials, intracranial recordings have shown that anterior insula activity trails that of rIFG and likely occurs after SSRT (Bartoli et al., 2018). Together, these factors make it unlikely that coincidental damage to the anterior insula can account for the current set of findings.

Taken together, our data show that the dominant model of inhibitory control in the human brain needs to be fundamentally revised. Rather than the rIFG ‘implementing a brake over response tendencies,’ it appears as though its primary role is to detect salient signals (such as stop-signals), leading to the triggering of an inhibitory control process, with the implementation of the latter taking place in other areas.

All data and analysis scripts can be downloaded at the following URL: https://osf.io/ck5zd/.

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Decision letter after peer review:

Thank you for submitting your article "Right inferior frontal cortex damage impairs the initiation of inhibitory control, but not its implementation" for consideration by eLife. Your article has been reviewed by 2 peer reviewers, and the evaluation has been overseen by David Badre as the Reviewing Editor and Michael Frank as the Senior Editor. The following individual involved in the review of your submission has agreed to reveal their identity: Lesley K Fellows (Reviewer #1).

The reviewers found this to be a strong, hypothesis-driven study that makes fresh progress on an important topic. They were in consensus that it may be suitable for eLife with appropriate revision. They did agree on several points that should be addressed. They focus on three broad issues related to the characterization of the lesions, a fuller picture of the data, and some points of clarity in the discussion. The reviewers have discussed their reviews with one another, and the Reviewing Editor has drafted this summary to help you prepare a revised submission.

Essential revisions:

As this is a lesion study, it is crucial to take care in the interpretation of the lesion. There were several points to consider in this regard:

(1) The paper sets up as a follow-up to the Aron et al. (2003) paper, but it was not fully clear whether the location of the present lesion if rIFC is in the same region of IFC that was the region of interest of focus in Aron. Indeed, to some extent looks somewhat rostral to that lesion, but it is difficult to tell with certainty.

(2) The term right inferior frontal cortex is used throughout regarding the region of interest. However, the lesions under study here are not solely cortical. I think it would be preferable to describe this as right inferior frontal gyrus, or right ventrolateral frontal lobe. Or at least discuss this issue, if the authors prefer to stick with the current terminology.

(3) The lesion overlap is as extensive in the insula as in the right ventral frontal lobe (not surprising, as damage tends to covary in these regions). This warrants comment, particularly given that insula is also frequently implicated in fMRI studies of the stop-signal task.

(4) Reviewers may have missed it, but the causes of the lesions should be provided. Were patients taking psychoactive medications?

(5) Table 1 should include an indication of variance for chronicity, such as IQR or range. Some comment seems warranted on the seemingly very large difference in chronicity between the IFC and lesioned control groups. The IFC lesions seem to be very chronic indeed; were some of these lesions in adolescence or early adulthood? Effects at those developmental stages might be quite different than acquired brain injury in middle- or old-age, with implications for interpretation of the main results.

Reviewers noted a number of places where the analyses were unclear or they were unsure how dependent the results are on the particular abstract analysis being conducted; though preregistration was noted as a strength. They had several requests for analysis to get a fuller picture of the data. I provide the specific comments along these lines here:

(6) Figure 3 is a challenge to follow. I'm not sure about showing key findings 'normalized' to baseline, what is the justification for showing a ratio rather than the raw data? The statistical test approach for the β burst result is not easy to follow. If I understand correctly, a difference between the rIFC group and their control group is present, while no difference is detected between the other lesion group and (different) controls. This is pretty indirect evidence for lesion location specificity; the mean β burst rate seems quite (numerically) different in the non-frontal lesion-control group compared to all other groups, and there is generally a lot of variability. The second analysis involving subtraction of normalized β burst rates seemed potentially unjustified arithmetic. It would be great to see something a little closer to the raw data to get a better sense of this part of the results. Were all of these analyses pre-registered?

(7) I was struggling with the very strong focus on TF basically being the only relevant behavioral observation here. A five-fold increase is certainly a lot, but it is also a five-fold increase of a very low number. Additionally, a residual SSRT effect of 35 ms, in fact, is also still a pretty large effect with regard to earlier group-difference observations. This residual effect is put into perspective some (concerning mu vs. tau), but rather in passing, as also being more in line with an attentional account, but this was hard to follow, and I am not sure how legitimate this is. I would down-tone this exclusivity a bit, and/or explore the residual SSRT effect some more (see below). Since I would also recommend providing the non-parametric SSRT estimate for reference (see below), I also think that a better metric might be how much of the SSRT group effect is explained by TF vs. what remains after accounting for it (say that the integration-approach SSRT would be 300 for the rIFG group and 240 for the control group, then accounting for TF would reduce this difference by approximately 30 ms, and still leave a residual difference of again approximately 30 ms). Maybe this is also not a perfect metric, but I think it would be significantly more intuitive, as far as the respective contributions of TF vs. residual SSRT go.

(8) Further, related to the preceding point, I noticed that the TF rate for all other groups is also really low in an absolute sense. Do the authors share the opinion that e.g. the 2% TF rate for the non-rIFC patients is surprisingly low, given what has usually been found in the literature? If yes, what might be the reason?

(9) As already stated, I would find it useful to also provide SSRT estimates from the hitherto pretty ubiquitous non-parametric approach for reference? Also, it would be reassuring to see that the assumptions of that approach are met, just to get another viewing angle on data quality. Relatedly, I had the impression that some information that is recommended to be provided in the cited consensus paper (e.g., average SSDs, p(inhibit), SRRT, etc.) is not available. Please add this. This is also true for Go misses, which I realize likely also contain some slow responses, but it would nonetheless be important to see this data. If need be, the data of the groups that do not have the time-out issue could also be limited to a 1000-ms deadline, in order to match this feature.

(10) Sometimes the patient groups are only compared to their respective control group, and sometimes directly with each other. I am wondering what the rationale is to sometimes also do the latter, and sometimes not. Again, maybe a more complete set of analyses (a lot of which could go to the supplementary material) would likely be good.

(11) Maybe you could discuss a bit more that the rIFG group has no condition effect whatsoever for mid-frontal β bursts in the sense that there are pretty exactly as many in successful and failed inhibition trials as in Go trials. I assume that this is still relevant from an inferential standpoint, and could furthermore be further explored empirically, e.g. in the sense of doing an analysis akin to what is presented in Figure 4 for Go-trials, in which there happened to be a (early) β burst. Should/does this then also lead to an increased likelihood of a β burst over the motor cortex?

(12) Related to this, I was expecting a similar analysis also for failed stop trials. Would such an analysis not also potentially be relevant (e.g., motor-cortex β bursts might be triggered, but too late, or not triggered at all, etc.). I appreciate that this dataset is not of the size and quality of a well-powered study in healthy participants, but this could probably be explored (again, no problem to do so in the supplementary material).

(13) I was unclear about how the manuscript dealt with the misfit in the supplementary material. What was the rationale for excluding the short SSDs and how does the improved fit after exclusion speak to the validity of the findings? I did read the respective section in the method section, but it was not sufficiently clear to me. I would certainly appreciate some more explanation.

(14) Related to the fact that short SSDs are found to be an issue here, and the recent publication by Bissett et al. (which is also cited here), highlighting the possibly important confounding role of short SSDs via context-independence violations, I think it would be good to systematically test for such violations, as prescribed in their paper. Again, pretty certainly just material for the supplementary material!

Reviewers also highlighted several places where the text could be clarified, its contact with the literature broadened, and its underlying assumptions more explicitly acknowledged.

(15) The paper addresses only the influential Aron et al. lesion study. However, there have been other lesion studies examining frontal contributions to stop-signal task performance and more addressing inhibitory control more generally, i.e. using go-no go tasks, for example (Swick et al. 2008; Picton et al. 2007). Even before considering the issue raised in the present study, the lesion evidence for a specific role for right IFG in inhibitory control was weak (Floden & Stuss, 2006; Yeung et al., JOCN, 2021). More generally, the positioning of this study made me feel I was being dropped into a very 'insider club' issue-a somewhat broader approach to both the introduction and discussion would be helpful in situating this study beyond the research groups that are deeply engaged in stop-signal task research.

(16) I found the frequently used concept of "implementation of inhibitory control" a bit difficult and would appreciate some further elaboration. I suppose there could also be a view in which the triggering of inhibition is in fact basically already its implementation, with everything downstream following a ballistic/stereotypical course. As such, I would be extremely curious whether the authors could somehow pinpoint what the remaining SSRT effect (or rather variance thereof) is related to. If the variance in the residual SSRT would be related to differential timing of the triggering of the stop process (via β bursts in the IFG), it would feel more (to me) like the right IFG still being a key structure for response inhibition. If in turn, it is a simple on/off switch, with no relevance beyond whether it is triggered or not (i.e., no relationship to the residual SSRT, which would be explained by other/later processes), I would agree yet more with the need for a fundamental reinterpretation of its role.

(17) Figure 2A seems to have garbled text; I was not clear about the proportion of stop signal trials or whatever other design features might or might not make this version of the task comparable to the existing literature. I guess this must have been explained in that figure before it was garbled, perhaps in pdf-production? It might be worth explaining how the task is 'optimized' for this particular modeling approach in the text-concretely, what is different from widely-used versions of the SST?

(18) Table 2 might be easier to appreciate (and relate to the literature) if it was divided into the conventional SST outcomes measures and the hierarchical model parameters, rather than mixing them. Did the groups differ on error rate?

Finally, the reviewers offered some minor points that you may choose to consider in your revision.

– I would find it helpful if the authors could overlay the borders of the different IFG subregions, as well as of the anterior insula in Figure 1A. I appreciate that spatial specificity is limited here, but given the numerous indications of dissociations between these areas, I would still appreciate easily being able to see this in reference to the overlap map of the lesions.

– Just out of curiosity: is chronicity (Tab. 1) possibly relevant? I don't really think so, but the difference between the patient groups is very pronounced.

– Maybe I am mistaken, but I didn't see any stats underlying the finding illustrated in Figure 4A. Also, I would find it relevant to know how many trials have gone into these various (elegant) analyses.

– In the Discussion section, would an explicit reference to the pause-then-cancel model not be relevant?

Essential revisions:

As this is a lesion study, it is crucial to take care in the interpretation of the lesion. There were several points to consider in this regard:

(1) The paper sets up as a follow-up to the Aron et al. (2003) paper, but it was not fully clear whether the location of the present lesion if rIFC is in the same region of IFC that was the region of interest of focus in Aron. Indeed, to some extent looks somewhat rostral to that lesion, but it is difficult to tell with certainty.

We appreciate the question. We have added anatomical labels to the lesion overlap figure (Figure 1) in the revised version of the manuscript.

It is correct that the lesion is slightly more rostral than the Aron et al. lesion, but both centers of gravity were predominantly located in pars triangularis of the right inferior gyrus. Within the constraints of lesion experimentation, we believe that this is about as close of an overlap as can be expected by a replication in an independent sample. We hope the reviewers agree. We have included the new figure (which also includes labels for the anterior insula to address a later point; see above) in the revised version of the manuscript.

(2) The term right inferior frontal cortex is used throughout regarding the region of interest. However, the lesions under study here are not solely cortical. I think it would be preferable to describe this as right inferior frontal gyrus, or right ventrolateral frontal lobe. Or at least discuss this issue, if the authors prefer to stick with the current terminology.

We agree. We have changed the nomenclature to “right inferior frontal gyrus” throughout.

(3) The lesion overlap is as extensive in the insula as in the right ventral frontal lobe (not surprising, as damage tends to covary in these regions). This warrants comment, particularly given that insula is also frequently implicated in fMRI studies of the stop-signal task.

Indeed. As in most (or all) lesion studies of the ventrolateral frontal lobe, there was some damage to the anterior insula.

With regard to the insula’s role in stopping, previous work has shown that the anterior insula seems to be primarily activated on unsuccessful stop trials (Cai et al., J Neuro 2014), in line with its purported role in error processing (Ullsperger et al., Brain Structure and Function 2010). Moreover, intracranial recordings have shown that the insula tends to be active after rIFG, and indeed after SSRT (i.e., probably does not contribute to stopping itself, Bartoli et al., HBM 2018), which also makes sense in this context. It is hence unlikely to account for the findings in the current study. We discuss these implications in the revised version of the manuscript on p. 22.

(4) Reviewers may have missed it, but the causes of the lesions should be provided. Were patients taking psychoactive medications?

Agreed. We have added the following statement about lesion etiology into the revised version of our manuscript on p. 22: “Lesion etiologies included: ischemic stroke (n=13), hemorrhagic stroke (n=4), focal contusion (n=2), AVM or cavernoma resection (n=5), benign tumor resection (n=3), herpes simplex encephalitis (n=2), cyst resection (n=1), abscess resection (n=1), and epilepsy resection (n=1).”

Finally, some patients in the database were indeed taking psychoactive medication, as is to be expected given their etiology and age. However, patients were excluded from participation if they were taking medication at dosages that can cause cognitive side effects. We have included a statement to that effect into the revised version of the manuscript on p. 22.

(5) Table 1 should include an indication of variance for chronicity, such as IQR or range. Some comment seems warranted on the seemingly very large difference in chronicity between the IFC and lesioned control groups. The IFC lesions seem to be very chronic indeed; were some of these lesions in adolescence or early adulthood? Effects at those developmental stages might be quite different than acquired brain injury in middle- or old-age, with implications for interpretation of the main results.

Indeed. The variance in chronicity is a side effect of our attempts to achieve sufficient statistical power (i.e., sample size) while maintaining a very constrained lesion location. IQR information for chronicity was included in the revised table 1. Moreover, there was a calculation mistake in our initial chronicity estimates that has been corrected, and we apologize for the oversight (the original pattern of longer chronicity in the lesion group remains in place, though). Indeed, three individuals in the rIFG group did have developmental onset lesions. We have repeated the main analyses of interest with these participants removed and have found that both the trigger failure parameter differences and the β burst differences remained highly significant.

rIFG vs. matched healthy comparison N = 13

Trigger failure parameter, probit scale, mean(SEM)

-1.3498 (0.26447) vs. -3.5261 (0.19955); t(12) = 5.5029, p * = 0.00013562, d = 1.5262 (For simplicity’s sake, this analysis was performed using standard frequentist t-testing on the individual model parameters from the BEESTS model that was fit to all participants’ data (i.e., the one reported in the main manuscript). We acknowledge that using point estimates of participant-level parameters from hierarchical Bayesian models in frequentist tests can inflate Type-I error rates as a result of hierarchical shrinkage. Due to the relatively low sample size, and hence modest shrinkage, this effect is expected to be relatively small for the present analysis. We would be willing to re-fit the model using only these participants and calculate exact Bayesian p-values (as was done for the full analysis in the main manuscript), but given the quite sizable group differences in the parameter estimates and since this is merely a control analysis, we held off on doing so at this point, as the full model would take a very long time to run.)

β burst rates for SS-GO at FCz, mean(SEM) with normalization

-0.019724 (0.033792) vs. 0.1296 (0.044518); t(12) = -4.0767, p * = 0.0015351, d = -1.1307.

This shows that our results do not seem to be attributable the presence of developmental onset lesions or the differences in chronicity (which were negligible after the removal of the three subjects in the above analysis). We made mention of these analyses in the revised version of the manuscript on p. 23.

Reviewers noted a number of places where the analyses were unclear or they were unsure how dependent the results are on the particular abstract analysis being conducted; though preregistration was noted as a strength. They had several requests for analysis to get a fuller picture of the data. I provide the specific comments along these lines here:

(6) Figure 3 is a challenge to follow. I'm not sure about showing key findings 'normalized' to baseline, what is the justification for showing a ratio rather than the raw data? The statistical test approach for the β burst result is not easy to follow. If I understand correctly, a difference between the rIFC group and their control group is present, while no difference is detected between the other lesion group and (different) controls. This is pretty indirect evidence for lesion location specificity; the mean β burst rate seems quite (numerically) different in the non-frontal lesion-control group compared to all other groups, and there is generally a lot of variability. The second analysis involving subtraction of normalized β burst rates seemed potentially unjustified arithmetic. It would be great to see something a little closer to the raw data to get a better sense of this part of the results. Were all of these analyses pre-registered?

To answer the last question first: the β burst analyses were not pre-registered, only the behavioral/computational modeling analyses and hypotheses were, as indicated by the statement in the manuscript. That is simply because the pre-registration and beginning of data collection predate the ‘discovery’ of the importance of scalp-recorded β bursts for motor inhibition in Wessel (J Neuro 2020) and Jana and colleagues (eLife 2020).

With regards to the β burst metrics themselves: they were directly adapted from the latter paper (Jana et al., eLife 2020), including the exact normalization procedure. For the sake of completion, here are the results of the non-normalized burst count analysis:

First, and most importantly, the pattern of significance remains exactly the same. Second, the basic rate of β bursts does not appear to differ dramatically between the groups. We have included a mention of these additional analyses (and the rationale for the normalization procedure) in the revised version of the manuscript on p. 31.

Finally, with regards to the question of lesion specificity: The reviewers may have missed that we did actually directly test whether there was a difference in stop-related β bursts between the rIFG and non-rIFG lesion groups (cf., p. 13 of the revised manuscript). That test revealed a significant difference.

(7) I was struggling with the very strong focus on TF basically being the only relevant behavioral observation here. A five-fold increase is certainly a lot, but it is also a five-fold increase of a very low number. Additionally, a residual SSRT effect of 35 ms, in fact, is also still a pretty large effect with regard to earlier group-difference observations. This residual effect is put into perspective some (concerning mu vs. tau), but rather in passing, as also being more in line with an attentional account, but this was hard to follow, and I am not sure how legitimate this is. I would down-tone this exclusivity a bit, and/or explore the residual SSRT effect some more (see below). Since I would also recommend providing the non-parametric SSRT estimate for reference (see below), I also think that a better metric might be how much of the SSRT group effect is explained by TF vs. what remains after accounting for it (say that the integration-approach SSRT would be 300 for the rIFG group and 240 for the control group, then accounting for TF would reduce this difference by approximately 30 ms, and still leave a residual difference of again approximately 30 ms). Maybe this is also not a perfect metric, but I think it would be significantly more intuitive, as far as the respective contributions of TF vs. residual SSRT go.

The suggested approach is intuitively appealing, but has the potential to confound genuine differences in SSRTs resulting from the presence of trigger failures with differences resulting from using different estimation methods (i.e., non-parametric individual level vs. parametric hierarchical) that rely on different assumptions. Moreover, this approach assumes that P(TF) reflects attention and SSRT purely reflects inhibition. The BEESTS model subscribes to the former, but not to the latter: in line with the standard race model, BEESTS assumes that SSRT captures the duration of a chain of processes that contribute to stopping, such as attentional/perceptual, decisional, and (inhibitory) motor-related processes (e.g., Logan et al. 2014; for an overview, see Matzke et al., 2018). Our aim with the model-based analysis of the stopping data is to disentangle the relative contribution of these processes using a fine-grained analysis of SSRT distributions. In particular, the reason we argue for a mostly attentional deficit is not because the SSRT difference was small after accounting for trigger failures, but because of the particular pattern of parameter differences where P(TF) and μ_stop were larger in the rIFG lesion group than in the matched comparison group whereas τ_stop was the same. Matzke et al. (2017) argued, based on earlier results in the RT modeling literature, that this pattern in SSRT distributions is consistent with differences in the speed of encoding the stop signal and not with differences in the decisional/inhibitory component of SSRT. As we now point out in the revised manuscript, this is the reasoning we relied on in the present work.

(8) Further, related to the preceding point, I noticed that the TF rate for all other groups is also really low in an absolute sense. Do the authors share the opinion that e.g. the 2% TF rate for the non-rIFC patients is surprisingly low, given what has usually been found in the literature? If yes, what might be the reason?

Our trigger failure estimates are indeed on the low side, but the 95% credible intervals in the two control groups overlap with other studies with similar easy choice-based SSTs. For instance, Matzke et al. 2017 (APP) reported TF credible intervals for control participants ranging between [0.04,0.12] for data originally reported in Hughes et al. (2012) and [0.06,0.16] for data originally reported in Badcock et al. (2002). Our credible intervals in the current study were [0,0.12] for the rIFC comparisons and [0.02,0.08] for the non-rIFC comparisons. The only papers that reported substantially higher rates of trigger failures were by Skippen and colleagues, who used a very unconventional task that involved a complicated go-choice and was specifically designed to induce fatigue (and hence, increase trigger failure probability).

(9) As already stated, I would find it useful to also provide SSRT estimates from the hitherto pretty ubiquitous non-parametric approach for reference? Also, it would be reassuring to see that the assumptions of that approach are met, just to get another viewing angle on data quality. Relatedly, I had the impression that some information that is recommended to be provided in the cited consensus paper (e.g., average SSDs, p(inhibit), SRRT, etc.) is not available. Please add this. This is also true for Go misses, which I realize likely also contain some slow responses, but it would nonetheless be important to see this data. If need be, the data of the groups that do not have the time-out issue could also be limited to a 1000-ms deadline, in order to match this feature.

We agree. We have added this information in the revised version of the manuscript in Table 4 and in Appendix 1.

(10) Sometimes the patient groups are only compared to their respective control group, and sometimes directly with each other. I am wondering what the rationale is to sometimes also do the latter, and sometimes not. Again, maybe a more complete set of analyses (a lot of which could go to the supplementary material) would likely be good.

As far as we know, the only analysis that was not run in the initial version of the paper was the direct comparison between the BEESTS parameters of the rIFG lesion group vs. non-rIFG lesion group. That analysis has now been included in the revised version of the manuscript (Table 3). The results are very similar to the primary result of rIFG lesion group vs. matched healthy comparison group (Table 2). The rest of β burst analysis for Stop vs. Go difference between group-comparisons were reported in Appendix figure 14. Thank you for pointing this out.

(11) Maybe you could discuss a bit more that the rIFG group has no condition effect whatsoever for mid-frontal β bursts in the sense that there are pretty exactly as many in successful and failed inhibition trials as in Go trials. I assume that this is still relevant from an inferential standpoint, and could furthermore be further explored empirically, e.g. in the sense of doing an analysis akin to what is presented in Figure 4 for Go-trials, in which there happened to be a (early) β burst. Should/does this then also lead to an increased likelihood of a β burst over the motor cortex?

We now make mention of the fact that there was no increase of β bursts at all in the rIFG lesion group (p. 17), though we want to be cautious about such statements, as they technically imply the confirmation of the null hypothesis in a (relatively) small sample. Moreover, if we understand the question correctly, the reviewer is wondering whether β bursts on go-trials are also followed by increase sensorimotor β bursts. That was generally the case, though to a lesser extent than for STOP trials:

This analysis was added to Appendix 1 for the revised manuscript.

(12) Related to this, I was expecting a similar analysis also for failed stop trials. Would such an analysis not also potentially be relevant (e.g., motor-cortex β bursts might be triggered, but too late, or not triggered at all, etc.). I appreciate that this dataset is not of the size and quality of a well-powered study in healthy participants, but this could probably be explored (again, no problem to do so in the supplementary material).

As for the go-trials, frontal β bursts on failed stop-trials also lead to an increase in sensorimotor β bursting. However, as the reviewer correctly surmises, the main difference between failed stop-trials and successful stop-trials is in the timing of the frontal β bursts, which occurs later on failed vs. successful stop trials (Jana et al., eLife 2020), leading to reduced β burst counts prior to SSRT (Wessel, JNeuro 2020). The same was true for our sample: t(31) = -2.93, p * = 0.003, d = -.518.

This analysis has been added to Appendix 1 as well.

(13) I was unclear about how the manuscript dealt with the misfit in the supplementary material. What was the rationale for excluding the short SSDs and how does the improved fit after exclusion speak to the validity of the findings? I did read the respective section in the method section, but it was not sufficiently clear to me. I would certainly appreciate some more explanation.

As we explained in the main text and illustrated in the Appendix 1, the BEESTS model showed a quantitatively small misfit (i.e., underprediction) to the average inhibition function at short SSDs in the non-rIFG lesion patients and their matched comparisons (see Appendix figure 6 and 8). To examine the robustness of the results to a possible model misspecification, we sequentially removed all stop-signal trials from the data of the non-rIFG lesion and the matched comparison group at SSDs of 0, 50, 100, 150, and 250 ms (i.e., SSDs where the misfit occurred), re-fit the model, and re-assessed the model’s descriptive accuracy. As shown in Appendix 1, descriptive accuracy improved as stop-signal trials on short SSDs were removed (Appendix figure 10 and 12): after removing stop trials at SSDs with 0 to 250 ms, the model was able to accurately account for the observed inhibition function in both groups. Importantly, qualitative conclusions about group differences were the same whether or not stop trials with short SSDs were included in the analysis. This demonstrates the robustness of the results and the validity of our conclusions. We now explain this more clearly in the revision.

(14) Related to the fact that short SSDs are found to be an issue here, and the recent publication by Bissett et al. (which is also cited here), highlighting the possibly important confounding role of short SSDs via context-independence violations, I think it would be good to systematically test for such violations, as prescribed in their paper. Again, pretty certainly just material for the supplementary material!

We included the test of context independent violations proposed by Bissett et al. (2021) in the Appendix 1 (Appendix figure 13). There was no evidence of the type of independence violation reported by Bissett et al. (2021); Bissett et al. found that violations were manifest in the signal-respond RTs on short SSDs, whereas the misfit in our data was restricted to response rates. We would like to emphasize again that this misfit was quantitatively small and did not influence our conclusions.

Reviewers also highlighted several places where the text could be clarified, its contact with the literature broadened, and its underlying assumptions more explicitly acknowledged.

(15) The paper addresses only the influential Aron et al. lesion study. However, there have been other lesion studies examining frontal contributions to stop-signal task performance and more addressing inhibitory control more generally, i.e. using go-no go tasks, for example (Swick et al. 2008; Picton et al. 2007). Even before considering the issue raised in the present study, the lesion evidence for a specific role for right IFG in inhibitory control was weak (Floden & Stuss, 2006; Yeung et al., JOCN, 2021). More generally, the positioning of this study made me feel I was being dropped into a very 'insider club' issue-a somewhat broader approach to both the introduction and discussion would be helpful in situating this study beyond the research groups that are deeply engaged in stop-signal task research.

We agree. The downside of having a pre-registered study with a very circumscribed approach and a clear replication target is that one runs the risk of being too narrow in scope in framing the work. We re-written the introduction of the paper to hopefully do the wider literature more justice (p. 3-4).

(16) I found the frequently used concept of "implementation of inhibitory control" a bit difficult and would appreciate some further elaboration. I suppose there could also be a view in which the triggering of inhibition is in fact basically already its implementation, with everything downstream following a ballistic/stereotypical course. As such, I would be extremely curious whether the authors could somehow pinpoint what the remaining SSRT effect (or rather variance thereof) is related to. If the variance in the residual SSRT would be related to differential timing of the triggering of the stop process (via β bursts in the IFG), it would feel more (to me) like the right IFG still being a key structure for response inhibition. If in turn, it is a simple on/off switch, with no relevance beyond whether it is triggered or not (i.e., no relationship to the residual SSRT, which would be explained by other/later processes), I would agree yet more with the need for a fundamental reinterpretation of its role.

To us, the residual variance in SSRT is likely due to the processing speed in the fiber tracts downstream from rIFC, including in the basal ganglia. The integrity of white matter connections from rIFC to STN predict stopping speed (Coxon et al., J Neuro 2012), which has recently been confirmed using intracranial direct electrical stimulation as well (Chen et al., Neuron 2020). We have expanded on this thought in the revised version of the discussion on p. 21.

(17) Figure 2A seems to have garbled text; I was not clear about the proportion of stop signal trials or whatever other design features might or might not make this version of the task comparable to the existing literature. I guess this must have been explained in that figure before it was garbled, perhaps in pdf-production? It might be worth explaining how the task is 'optimized' for this particular modeling approach in the text-concretely, what is different from widely-used versions of the SST?

We apologize for the oversight with regards to the figure, the PDF conversion did not go as planned and this was not detected prior to submission. We have fixed this figure in the revised version of the manuscript.

In terms of ‘optimizing’ the task for the purpose of BEESTS: this solely meant a higher trial count than perhaps typical, as well as an ‘open’ response window that detected responses made even after the deadline (so as to not truncate the RT distribution). Other than that, the task is identical to the typical versions in the literature. This has been explicitly pointed out in the revised version of the manuscript.

(18) Table 2 might be easier to appreciate (and relate to the literature) if it was divided into the conventional SST outcomes measures and the hierarchical model parameters, rather than mixing them. Did the groups differ on error rate?

We apologize for the misunderstanding – Table 2 only includes the model parameters from the BEESTS analysis (in the revision, we have now added the standard measurements in Table 4 as well). Of course, there is some overlap between the naming of variables. However, we hope that our presentation in two separate tables in the revised manuscript avoids this confusion.

In terms of error rate, the rIFG lesion group had a significantly increased error rate compared to all other three groups (ps <.05), but the overall rates were very low (1.62% in the rIFG lesion group,.49% in the non-rIFG lesion group,.14% in healthy comparison for rIFG lesion and.43% in the healthy comparison for the non-rIFG lesion group).

Finally, the reviewers offered some minor points that you may choose to consider in your revision.

– I would find it helpful if the authors could overlay the borders of the different IFG subregions, as well as of the anterior insula in Figure 1A. I appreciate that spatial specificity is limited here, but given the numerous indications of dissociations between these areas, I would still appreciate easily being able to see this in reference to the overlap map of the lesions.

See above.

– Just out of curiosity: is chronicity (Tab. 1) possibly relevant? I don't really think so, but the difference between the patient groups is very pronounced.

See above.

– Maybe I am mistaken, but I didn't see any stats underlying the finding illustrated in Figure 4A. Also, I would find it relevant to know how many trials have gone into these various (elegant) analyses.

Trial numbers for Figure 4A were as follows:

Trials with bursts: M = 60.734, SD = 10.310

Trials without bursts: M = 14.797, SD = 7.458

However, the more relevant counts are for the between-groups comparisons (Figure 4B), as Figure 4A is merely a replication of prior work.

rIFG lesion: M = 57.688, SD = 14.263

matched healthy for rIFG lesion: M = 63.50, SD = 7.118

non-rIFG lesion: M = 61.50, SD = 7.729

matched healthy for non-rIFG lesion: M = 60.25, SD = 10.662

There was no significant difference in trials included in group comparison.

We have made mention of these trial counts in the revised version of the manuscript on p. 16.

– In the Discussion section, would an explicit reference to the pause-then-cancel model not be relevant?

Indeed. We have made reference to this work in the revised version of the discussion.

Author details

1. Yoojeong Choo

   1. Department of Psychological and Brain Sciences, University of Iowa, Iowa City, United States
   2. Cognitive Control Collaborative, University of Iowa, Iowa City, United States

   Contribution

   Formal analysis, Investigation, Visualization, Writing - review and editing

   Competing interests

   No competing interests declared

   "This ORCID iD identifies the author of this article:" 0000-0003-1261-9129

2. Dora Matzke

   Department of Psychology, University of Amsterdam, Amsterdam, Netherlands

   Contribution

   Conceptualization, Software, Formal analysis, Investigation, Methodology, Writing - review and editing

   Competing interests

   No competing interests declared

3. Mark D Bowren Jr

   Department of Clinical and Health Psychology, University of Florida, Gainesville, United States

   Contribution

   Formal analysis, Investigation, Visualization

   Competing interests

   No competing interests declared

4. Daniel Tranel

   1. Department of Psychological and Brain Sciences, University of Iowa, Iowa City, United States
   2. Department of Neurology, University of Iowa Hospitals and Clinics, Iowa City, United States

   Contribution

   Data curation, Validation, Methodology, Writing - review and editing

   Competing interests

   No competing interests declared

5. Jan R Wessel

   1. Department of Psychological and Brain Sciences, University of Iowa, Iowa City, United States
   2. Cognitive Control Collaborative, University of Iowa, Iowa City, United States
   3. Department of Neurology, University of Iowa Hospitals and Clinics, Iowa City, United States

   Contribution

   Conceptualization, Supervision, Funding acquisition, Investigation, Methodology, Writing - original draft, Project administration, Writing - review and editing

   For correspondence

   jan-wessel@uiowa.edu

   Competing interests

   No competing interests declared

   "This ORCID iD identifies the author of this article:" 0000-0002-7298-6601

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