Introduction

A prominent view amongst philosophers of mind is that the ‘self,’ as we experience it, is merely an illusion of our conscious minds1. While it is the case, in this view, that all of our conscious experiences are constructions insofar as we experience, for instance, unified perceptions of objects rather than the raw responses of our sensory receptors, the self is distinct from ordinary (non-hallucinatory) perceptions in that it does not correspond to anything that persists outside of conscious awareness. While the (non-)reality of selfhood is not a settled issue in philosophy2,3, varying forms of this illusionist view have been endorsed4, with some empirical evidence5,6, in the broader cognitive sciences. However, we would argue this view is implicitly assumed more often than it is explicitly stated. For example, when Benjamin Libet famously presented evidence that the earliest neural activity associated with movement temporally preceded subjects’ conscious awareness of intending to move7, his findings were interpreted as a challenge to free will, as the conscious self seemed to be retroactively claiming credit for actions it did not initiate. While this interpretation of the Libet study has been thoroughly disputed on methodological grounds8, the fundamental assumption that the unconscious process that initiated the action is clearly separable from the conscious self is rarely questioned9. That is, many scientists have tacitly ruled out the possible alternative that the core set of neural and cognitive processes that constitute that self may be able to operate independently of consciousness, and we become ‘self-aware’ when those processes meet the same conditions that allow any other process or percept to appear in awareness10,11—thus, any sense of agency (SoA) we consciously experience over an unconsciously initiated action must be illusory.

To be clear, what we are calling the ‘illusionist view’ does not necessarily hold that no self-referential processes occur outside of awareness; the existence of implicit, unconscious self-monitoring processes—as for neuromuscular control or allostatic regulation—is typically acknowledged but differentiated from explicit processes that appear in and require consciousness12. Critically, the processes which are considered sufficient for ‘minimal self-awareness’—most often said to be the SoA, the experience of authoring actions and their consequences, and the sense of ownership (SoO)13, the experience of having a body, though other ingredients have been argued to be necessary for explaining anomalous experiences of self14—must in some way require consciousness in the illusionist view. Conversely, the alternative we will call the ‘independence view’ does not necessarily hold that all processes that make up the self can occur outside of conscious awareness, nor does it hold that the self is not constructed by a biophysical process. It merely posits that some of the processes that constitute the minimal self may not require consciousness to operate per se. This view extends from a sentiment in the wider natural sciences that a meaningful notion of self, particularly of agency, emerges from the same characteristics of biophysical organisation that differentiate life, i.e. agentic material, from non-life; thus SoA is a legitimate awareness of an agentic capacity that exists at the scale of the organism rather than merely a confabulation of the conscious organism15,16. Most first-order theories of consciousness would be compatible with (but not imply) the independence view10,11, as has been argued explicitly by some first-order theorists to justify how consciousness can be studied independently of self-awareness17. Other approaches to understanding consciousness, such as embodied or enactivist theories18 and higher-order theories19 of consciousness—some of which argue that the first-person perspective is what makes a percept conscious—may even require that a notion of self is a precondition for consciousness, rather than the other way around as in the illusionist view.

The critical distinction, then, is that for the illusionist, awareness is a precondition to self, not just to the awareness of self. Thus, were the illusionist to speculate how an organism first came to acquire self-awareness, they would say that the first self-aware organism must have first been aware and then subsequently developed SoA and SoO. In contrast, the independence view would allow for the possibility that some of these self-referential processes of which that organism became aware could have been inherited from an ancestor without conscious awareness. Becoming aware of these extant processes that generate the minimal self could ‘jump start’ self-awareness. Even ‘high level’ self-awareness that presumably does require consciousness may be influenced by these low-level processes, as evidenced by the finding that individual differences in the propensity to make positive SoA judgements in a sensorimotor task can predict a non-negligible amount of variance in subjects’ narrative beliefs about one’s own agency (although this relationship seems to be mediated by explicit metacognition)20.

Until recently, findings in the SoA and SoO literatures have been largely compatible with the illusionist separation between unconscious, implicit self-monitoring and conscious, explicit self-monitoring. For instance, it is widely held that effective neuromuscular control requires an internal model of one’s body to compensate for intrinsic delays in sensory systems, and that these internal models are updated by predicting the sensory feedback from one’s own movement and cancelling out predicted sensations—such that non-suppressed sensations constitute prediction errors21. This comparator model accounts for the observation that, for instance, people cannot tickle themselves22, and thus it can be said to discriminate between self- and other-caused sensations at a low level. As SoA is the phenomenological experience of a self-other distinction during action, this sort of predictive cancellation was one of the earliest proposed mechanisms for SoA23,24, which would have conflicted with the illusionist view, as this sort of sensory suppression based on sensorimotor contingency operates largely unconsciously and in essentially all organisms with a nervous system25,26. However, while neural markers of sensory suppression indeed objectively discriminate between self- and other-caused sensations27, numerous studies have failed to find an association between these markers and subjective reports of agency27,28,29,30. This dissociation seems to support a division between unconscious and conscious self-monitoring processes, with only higher-level, abstract comparators and their prediction errors—which may not necessarily correspond to any obvious sensory suppression—informing SoA24,31.

Recently, however, it has been demonstrated that when experimentally manipulating agency over a muscle movement using electrical stimulation (and opposed to over a downstream sensory consequence of movement as in typical paradigms), neural patterns indicative of pre-conscious sensory suppression are indeed predictive of subjective agency judgements32, consistent with recent behavioural modelling results that suggest control detection processes may operate unconsciously33. Of course, a pre-conscious process—in which the subject eventually becomes conscious of the sensory stimulus and can report on it—is not the same as a fully unconscious process in which the subject will never become aware of the stimulus; it may be that this mechanism would never result in what we experience as SoA if not for some subsequent consciousness-dependent processing. However, this finding adds to a growing body of evidence that, while inconclusive, gives reason to doubt the illusionist account of self-awareness. For instance, it has been consistently reported that images of one’s own face break through interocular suppression into awareness faster than other faces34, as do arbitrary self-associated images35—although see a non-replication of the latter by Stein and colleagues36—suggesting that some process differentiates self- and other-related visual stimuli before they enter conscious awareness, potentially overlapping with the process that results in conscious SoO. Additionally, neural correlates of conscious own-face recognition37,38,39,40 and own-name recognition41 persist in the absence of conscious awareness of the visual stimulus. However, much like sensory suppression need not result in SoA, these self-other distinguishing neural signals may not result in SoO. Consider the zebra finch, in which a certain population of neurons is highly selective for the bird’s own song, even when the bird is asleep or anesthetized42; without causal/behavioural evidence that the bird itself recognises a song as their own when this population is responsive, it would be fallacious to conclude that the bird is self-aware based on neural data alone. Pfister and colleagues, in this vein, go on to demonstrate that own-name subliminal primes bias participant responses more than other-names in a speeded discrimination task43, providing convincing evidence that these discriminations do have behavioural consequences but arguably falling short of demonstrating a self-ownership judgement (of the sort that, were we aware of it, we would experience as SoO) can be fully contained within an unconscious process. This is a natural limitation of studies of unconscious self-ownership discriminations, since it is particularly difficult to make claims about perceived ownership without taking self-report measures.

In contrast, the SoA is often measured not via self-report but via intentional binding, which can be measured if the subject is aware of either the action or the outcome – but not necessarily both. In a typical intentional binding paradigm, subjects make a button press, which is followed by a sensory stimulus—typically a tone but also a visual stimulus44,45,46,47—in an operant condition and not followed by anything in a baseline condition. They are then asked to report (e.g. by adjusting the hand of a clock that was spinning during the trial) the time the button press or the sensory consequence occurred. Haggard and colleagues were the first to report that the perceived time of an action was biased toward the time of its outcome and vice versa, shortening the subjective interval between them48. Since then, this bias in temporal perception for intentional action has been shown to be a special case of a temporal binding that occurs between any two events perceived as a causal sequence49. The fact that this bias in the reported time of an action toward the time of its outcome interpretably tracks the perceived experience that a subject’s action caused the outcome has made the intentional binding effect the gold-standard measurement of SoA literature, so much so that studies often do not solicit for self-report judgements at all47,50,51.

Since the perceived time of the button press in an intentional binding paradigm (i.e. ‘action binding‘) is usually measured independently of the time of the sensory consequence52, this paradigm presents an intriguing opportunity: it is possible to measure temporal bias in the time of a button press, even if the subject is not consciously aware of the sensory consequence. To the extent that intentional binding is taken as a measure of SoA, this would suggest that subjects can implicitly attribute an action-contingent stimulus to their own action even when they are unaware of the stimulus. This would either provide evidence of that self-attributions of the sort we would consciously experience as SoA can occur outside of awareness, indicating that a core process underpinning minimal self-awareness does not itself require awareness, or it would require a reinterpretation of the highly influential intentional binding effect. To this end, we asked subjects to complete a typical intentional binding paradigm in which they estimated the perceived time of their button press in both an operant and a baseline condition. In the first half of the experiment, however, we masked the operant stimulus using continuous flash suppression (CFS), a form of interocular suppression (as in binocular rivalry) that allows stimuli presented to one eye to be robustly suppressed from awareness by presenting a dynamic stimulus to the opposite eye53, though we do note the limitations of CFS (regs. 54,55,56 and see ‘Methods: Design’ for specific steps we have taken to account for these limitations) and the possibility of strongly reduced, rather than totally eliminated, awareness resulting from the manipulation. If subjects showed evidence of action binding in conditions that suppress conscious awareness of the consequent stimulus (Hypothesis 1, see Table 1), this would have supported the view that intentional binding, and thus an implicit linking of action and outcome, does not require conscious awareness of the outcome. However, the action binding effect measured in the unmasked condition was greater than that in the masked conditions (Hypothesis 2, see Table 1), as expected to occur in the event that Hypothesis 1 was false; thus, we conclude that the intentional binding effect is facilitated by conscious awareness. The present study sheds light on the illusive relationship between action-monitoring, self, and awareness in human beings.

Table 1 Design Table
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It is worth elaborating on what exactly was under test here. Specifically, if Hypothesis 1 were indeed true, it would still not have implied the existence of an ‘unconscious SoA’ that is ontologically equivalent to conscious SoA. (Whether the idea of a sense or feeling being unconscious even makes sense is, perhaps, a question best left to philosophers.) While intentional binding is frequently used as an implicit marker of SoA, it is not equivalent to the SoA itself; binding has been observed between cause-effect events in the absence of any intentional action49. In our case then, we would argue that an IB effect should be more conservatively interpreted as evidence that the brain has linked the action and the outcome, and under the independence view, one may experience SoA when they are conscious of this link. This finding would have still corroborated a crucial prediction of the independence view, which does not hold that there is an ‘unconscious sense of agency’ necessarily. Rather, it merely stipulates that SoA is a sense of something that exists regardless of whether one senses it, much like in ordinary sensory perception. For example, an experience of ‘pipe’ normally refers to some referent that exists whether you are aware of it or not—namely, a physical object. This referent does not need to actually be a pipe for the perception to be non-hallucinatory; it could instead be a picture of a pipe, just as the referent for conscious SoA does not need to be an equivalent unconscious SoA. An unconscious causal link between action and outcome, suggested by an IB effect for an operant stimulus of which the subject is unaware, would constitute such a referent for agency. Such a finding would challenge illusionist perspectives, which seem to take the lack of a plausible referent outside of consciousness as their premise1,5, though some more nuanced illusionist perspectives may still be able to argue that the fact a potential referent is available does not mean it is actually referred to by conscious SoA. For example, Seth’s 4 account of self-awareness is rooted in a predictive coding account in which all perception is considered a ‘controlled hallucination’4. Such a possibility would be akin to a situation in which one failed to perceive an actual pipe, but nonetheless hallucinated an unrelated pipe, either by coincidence or because other sensory cues suggested an unobserved pipe was present. This is a particularly difficult argument to rebut empirically, and we do not think any possible outcome of the present experiment would do so conclusively. Nonetheless, results promise to place meaningful constraints on theories of self-awareness with respect to the contrast between illusionism and independence.

Methods

Protocol registration

The Stage 1 protocol for this Registered Report was accepted in principle on August 9, 2024. The protocol, as accepted by the journal, can be found at https://doi.org/10.6084/m9.figshare.26540077.v1.

Ethics information

Study protocols were in accordance with relevant safety and ethics guidelines for human subject research and were approved by the Social and Behavioural Sciences Institutional Review Board at the University of Chicago (IRB23-1353). Informed consent was obtained from each participant, and participants were compensated for their participation with a credit that could be used to satisfy the research participation requirement of any course in Psychology offered at the university.

Pilot data

To assess the feasibility of the protocol as proposed in our Stage 1 manuscript, we had collected a small pilot sample consisting of n = 5 subjects to test our experimental procedures. Of the five subjects, all of them met the inclusion criteria outlined in Sampling Plan, which is to say that no subject reporting seeing significantly more masked stimuli on the operant-masked block than on the baseline-masked block, in which no masked stimuli were actually presented (Fisher’s exact test, p > 0.615 for all subjects; see Table 2 for subject-by subject hit and false alarm rates). If the prevalence of subjects that would trigger our exclusion criteria (i.e. hit rate > false alarm rate with p < 0.05) in the sampled population is γ, then the number out of n subjects that trigger our exclusion criteria is distributed according to \({\mbox{Binomial}}(n,\,0.05\left(1-\gamma \right)+\gamma )\); using this likelihood and a uniform prior on prevalence γ, we estimated that that the prevalence of subjects who would be excluded by the specified criteria is less than 39.3% with 95% posterior probability (estimated with the bayesprev Python package57) according to Bayes’ rule. In other words, a majority of subjects were expected to survive our exclusion criteria with high probability. Even with this small number of subjects, we could already detect an intentional binding effect in the unmasked blocks (t(4) = 2.96, p = 0.027, median = 0.028 s); in fact, all five subjects individually showed a nominal intentional binding effect. Tests of Hypothesis 1 (t(4) = −1.51, p = 0.897, median = −0.011 s) and of Hypothesis 2 (t(4) = 2.04, p = 0.055, difference in medians = 0.039 s) were both non-significant at the significance levels we specify in Table 1, which is expected given the substantially higher sample size our power analyses (based on separate effect size measurements, see ‘Sampling Plan’) indicated are needed to detect (or estimate) either effect reliably. Rather, these pilot data were just to verify our task design works as intended. (Due to the very small pilot sample size, we report median effect sizes instead of means with confidence intervals, as we intended to report in a Stage 2 manuscript as described in ‘Preregistered analysis plan’).

Table 2 Per-subject detection rates in pilot sample
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Design

The experiment consisted of five within-subject blocks: (1) a calibration block, (2–3) operant-masked and baseline-masked blocks, in random order, and (4–5) operant-unmasked and a baseline-unmasked blocks, in the same order as Blocks 2–3. Randomisation of the order in which subjects complete operant and baseline blocks ensured that intentional binding measurements were not systematically influenced by temporal drift in estimation bias.

During the experiment, subjects wore red-blue anaglyph glasses for the presentation of stereoscopic visual stimuli, such that stimuli presented in red only appeared to the left eye and blue stimuli only appeared to the right eye. We achieved suppression of the operant stimulus by presenting masks composed of many small squares, which update at a rate of 10 Hz, to the left eye, while the operant stimulus (a circle) was presented to the right eye for 200 ms. Our intent was that the masks presented to the left eye totally suppressed the competing image in awareness (see Fig. 1a). However, any manipulation of interocular dominance—particularly those using anaglyph glasses, since red-blue light filtering is not perfect—must tune the contrast of the masked stimulus to ensure complete suppression, as ‘breakthrough’ trials can occur during CFS58. Complete suppression could be verified by ensuring that participants were sufficiently close to chance performance when asked what was presented to the suppressed eye58,59. Thus, in our calibration block, subjects completed 100 trials of a discrimination task in which CFS masks were presented to the left eye for two seconds, during which a circle was presented to the right eye, in a random corner of the masked area, anytime between 0.25 and 1.75 s after CFS onset and remaining on screen for 200 ms. After each trial, subjects were asked which side of the screen the blue circle had appeared on. After each trial, we computed a Bayesian posterior for the log10-contrast threshold at which subjects could achieve 52.5% accuracy on the discrimination task using the QUEST algorithm with a Weibull psychometric function (with lapse rate = 0.01 and default slope = 3.5)60. Once the posterior was fit, we drew a random sample from the mean-truncated posterior distribution (see Fig. 1b) and used it as the stimulus contrast for the next trial; this is a modified version of Thompson sampling61, a state-of-the-art method for efficiently sampling when learning Bayesian posteriors. After 100 trials, we used the 5th percentile of the posterior distribution as the contrast for the remainder of the experiment, corresponding to a 95% posterior probability that discrimination accuracy at this threshold is below 52.5%. Assuming subjects got the answer right (100% accuracy) when they are aware of the stimulus and guess (50% accuracy), then this corresponds to a 95% probability that the rate of ‘breakthrough’ trials in which subjects are aware of the masked stimulus is less than 5%. (See ‘Sampling plan’ for consideration of why 5% is an acceptable breakthrough rate.) Notably, the use of an accuracy/discrimination threshold was more useful for our purposes than simply asking our subjects whether they see the circle stimulus, since it controls for the possibility that subjects may have had an experience of the stimulus that fell above their threshold for minimal awareness but still below their certainty criterion for positively responding that they have seen it59. While using this addressed this potential confound during calibration, we should note that the additional controls we use in later blocks (i.e. asking subjects to report when they see a circle) do not account for this problem. We do not think there is any reason to believe that the nature of the main task (see below) would cause sensitivity thresholds to shift from where they were in the control block, but if this did occur, subjects may have experienced a quantitative (as opposed to a qualitative or complete) suppression of the operant stimulus from awareness. Minimally, CFS in this experiment serves to severely attenuate subjects’ awareness of the stimulus to the point that they would not report that it is present when prompted.

Fig. 1: Calibration block.
figure 1

a In continuous flash suppression (CFS), high-contrast masks consisting of many squares varying in red pixel values were presented at 10 Hz to one eye, after which a single, static mask was displayed for 100 ms to reduce visual aftereffects. During CFS, a low-contrast blue circle was presented to the opposite eye, with the intent that it would be suppressed from awareness when the visual system resolves the conflict between eyes. b, c During the calibration block, subjects reported which side of the CFS mask they thought the blue circle was presented on each trial. A Bayesian posterior was calculated for the stimulus contrast at which their discrimination accuracy is 52.5%, and the contrast for the next trial was drawn from the upper part of the posterior as in the example run illustrated here. At the end of the block, the 5th percentile of this posterior was used as the stimulus contrast for the remainder of the experiment, ensuring that subjects were aware of the stimulus on sufficiently few trials. The calibration curves shown here are from a single pilot subject.

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Once we had determined the contrast for the main experiment, subjects completed either the baseline-masked block (see Fig. 2a) or the operant-masked block (Fig. 2b), randomly selected, and then they completed the other. In the baseline-masked block, CFS masks were presented in the middle of an on-screen clock with a hand rotating around the outside. Any time following the first rotation of the clock, subjects pressed the space bar on their keyboard, after which the CFS masks ended and the clock stopped rotating 1–2 s later, the clock hand disappeared for an additional second, and then it reappeared at a random location 45–60° away from where it was when the key was pressed. Subjects were then asked to adjust the clock hand back to where it was when they pressed the space bar. In the operant block only, a circle identical to that in the calibration block appeared in a corner of the masked area (which is randomly chosen on a per-subject basis but the same across all operant trials) 150 ms after the subjects’ key press or on the next screen refresh and persisted for 200 ms. As an additional check to ensure subjects were not aware of the operant stimulus—in case, for instance, sensorimotor contingency altered the breakthrough threshold26—we asked subjects after each masked trial whether they saw a blue circle, and we randomly inserted a few ‘decoy’ trials in which a full-contrast circle appeared on the first rotation of the clock. Each block had 5 practice trials, 5 decoy trials, and 40 real trials (only real trials were analysed).

Fig. 2: Intentional binding task.
figure 2

a In the baseline-masked block, CFS masks were presented to one eye in the middle of a rotating on-screen clock. The subject chose when to press a button, 1–2 s after which CFS ended and the clock stopped. The clock hand disappeared for 1 s and reappeared in a random location, after which subjects were prompted to adjust it back to its position when they had pressed the button. b In the operant-masked condition, a circle was presented to the suppressed eye 150 ms after the subject made the button press. c, d The baseline-unmasked and operant-unmasked conditions were identical to the masked versions, but without CFS so subjects were consciously aware of the operant stimulus.

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After the masked blocks, subjects completed baseline and operant blocks, consisting of 5 practice trials and 40 real trials (again, only real trials were analysed), with no CFS masking (see Fig. 2c, d). Baseline and operant blocks were completed in the same order as the masked versions were completed so potential order effects were matched between masked and unmasked conditions. While no masks were presented to the left eye in these blocks, the operant stimulus was still only be presented to the right eye and at the same contrast as in the masked blocks to ensure visual stimulation was otherwise identical. Thus, the unmasked blocks functioned as a positive control; estimation bias should differ between the operant-unmasked and baseline-unmasked blocks regardless of whether Hypothesis 1 or 2 is true, or we would have had to conclude our paradigm was ineffective at eliciting the intentional binding effect.

The experimenter was blind to the order in which the operant and baseline conditions were presented; randomisation was handled entirely by the experiment code (see ‘Code availability’), which fully implemented the procedures described in this section.

Sampling plan

We performed sample size calculations to ensure that tests of Hypothesis 1, Hypothesis 2, and our positive control (see ‘Preregistered Analysis Plan’) all had statistical power of greater than 95%. Sample size calculations were performed using the statsmodels package in Python. In conjunction with these power analyses, we also conducted simulations to ensure that positive results for Hypothesis 1 are unlikely to be caused by ‘breakthrough’ trials in which subjects were spuriously aware of the operant stimulus (though these simulations do not substitute for an in-task manipulation check, see ‘Design’ and the last paragraph of this section).

In addition to the statistical Type 1 error inherent to null hypothesis significance tests, the possibility that the subject may become aware of the operant stimulus on some trials despite CFS masking introduces another source of false positives when testing Hypothesis 1. Thus, if we were to use the typical significance level of 0.05 for our statistical test, then the total false positive rate would necessarily be higher than 0.05. In this vein, we set the significance level for Hypothesis 1 to 0.01 to leave some cushion for error due to breakthrough trials. After we determined the sample size for the experiment, we conducted simulations to ensure the total false positive rate (Type I + awareness confound) would remain below 5%.

For Hypothesis 1, we performed power calculations using the meta-analytic effect size for action binding (i.e. difference in mean temporal estimation bias between operant and baseline conditions), Cohen’s d = 0.45162. For our planned statistical test (see ‘Preregistered analysis plan’) to have 95% power at a significance level of 0.01, calculations showed that we would need 80 subjects.

For Hypothesis 2, we aimed for 95% power in the event that Hypothesis 1 is false. That is, we wanted 95% power for concluding that the intentional binding effect is stronger in the unmasked conditions than in the masked conditions when the effect size is \({d}_{{\mathrm{main}}}=0.451\) (as above) in the unmasked conditions and \({d}_{{\mathrm{null}}}=0\) in the masked conditions. If we know the within-subject variance \({\sigma }_{{wi}}\) and the between-subject variance \({\sigma }_{{bw}}\) in the paired (operant – baseline) differences, then we can compute \({d}_{{\mathrm{interaction}}}={d}_{{\mathrm{main}}}/\sqrt{1+\,{\sigma }_{{\mathrm{wi}}}^{2}/{\sigma }_{{\mathrm{bw}}}^{2}}\), which amounts to doubling the within-subject variance (since a difference-in-differences required four paired measurements instead of two). Since between-subject and within-subject variances are not available from the meta-analysis from which we drew the main effect size, we computed point estimates of these quantities from a 192 subject intentional binding dataset we have reported previously and made available on Open Science Framework20. We first computed the trial-by-trial within-subject variance as the mean of the variances of responses within each subjects’ baseline block \({\sigma }_{{\mathrm{trial}}}=92.8\), then the per-block variance as \({\sigma }_{{\mathrm{block}}}=\frac{{\sigma }_{{\mathrm{trial}}}}{\sqrt{40}}\) by the central limit theorem. Finally, we computed within-subject variance for the paired differences (between two blocks) as \({\sigma }_{{\mathrm{wi}}}^{2}=2{\sigma }_{{\mathrm{block}}}^{2}\), and the between-subject variance as \({\sigma }_{{\mathrm{bw}}}^{2}={\sigma }_{{\mathrm{total}}}^{2}-{\sigma }_{{\mathrm{wi}}}^{2}={(78.8)}^{2}\). With these estimates in hand, we computed an effect size of \({d}_{{\mathrm{interaction}}}=0.44\), for which we would need 58 subjects to detect with 95% power at a significance level of 0.05.

For our positive control, the meta-analytic effect size is the same as for Hypothesis 1 but the significance level is set higher, at 0.05. Therefore, if we had 95% power to test Hypothesis 1, then we would have greater than 95% power for our positive control. Since Hypothesis 1 required more subjects to test than Hypothesis 2, we used the sample size computed for Hypothesis 1 as our final sample size. Thus, we aimed to collect n = 80 subjects with normal colour vision from the University of Chicago student community.

Lastly, we wanted to verify that a 5% rate of breakthrough trials (see ‘Design’ for how we contain that rate) is not enough to unduly inflate our false positive rate for Hypothesis 1. To do this, we used \({\sigma }_{{bw}}\) and \({\sigma }_{{trial}}\) as calculated above to simulate two sets of 40 trials for 80 subjects. The simulated baseline-masked block had a mean estimation bias of zero, but timing estimates on each trial had standard deviation \({\sigma }_{{trial}}\). As we were simulating data under the null hypothesis, the simulated operant-masked block also had mean 0 and scale \({\sigma }_{{trial}}\), but a subject i would become ‘aware’ of the operant stimulus on k~Binomial(40, 0.05) trials, which had mean \({\mu }_{i} \sim N(\mu ,\,{\sigma }_{{bw}}^{2})\), where \(\mu =25.7\) ms is the mean paired difference in estimation bias observed in our previous binding dataset20. We then test Hypothesis 1 on this simulated data as in ‘Preregistered Analysis Plan’. Repeating this simulation procedure 10,000 times, we find that we falsely reject the null hypothesis 3.79% of the time, 1% of which is accounted for by the error rate of our statistical test, suggesting that breakthrough trials only inflate the false positive rate by about 2.79%.

As an additional quality check to ensure breakthrough trials do not confound our results (e.g. if threshold drops subsequent to initial measurement), we compared the rate at which subjects reported seeing a blue circle in the operant-masked block to that in which they reported seeing a circle in the baseline-masked block, not including practice or decoy trials. Since the baseline block did not have an operant stimulus, its observed detection rate is a false alarm rate. If a subject’s detection rate on the operant block exceeded their false alarm rate according to Fisher’s exact test with a significance level of 0.05, we concluded that they were aware of the operant stimulus on an unacceptable proportion of trials and excluded them from analysis. Such subjects were replaced so that the usable sample size still reached n = 80.

Preregistered analysis plan from Stage 1 manuscript

For each subject, we planned to compute the Huber mean of the estimation bias (estimated event time minus true event time) within each block, excluding any trial in which subjects reported being aware of an operant stimulus. The Huber mean is an outlier-robust estimate of central tendency, eliminating the need to trim outlier trials from the data63. Paired differences \({\triangle }_{{\mathrm{masked}}}\) between the operant-masked and baseline-masked conditions would be calculated, as would paired differences \({\triangle }_{{\mathrm{unmasked}}}\) between the operant-unmasked and the baseline-unmasked conditions.

As a positive control, we would compare \({\triangle }_{{unmasked}}\) to the null hypothesis \({H}_{0}:{\triangle }_{{\mathrm{unmasked}}}=0\) using a one-tailed t-test at significance level 0.05. Then, to test Hypothesis 1, we would compare \({\triangle }_{{\mathrm{masked}}}\) to the null hypothesis \({H}_{0}:{\triangle }_{{\mathrm{masked}}}=0\) using a one-tailed t-test at significance level 0.01 (see ‘Sampling Plan’ for explanation of reduced significance level).

To test Hypothesis 2, i.e. that \({\triangle }_{{\mathrm{unmasked}}}\) is greater than \({\triangle }_{{\mathrm{masked}}}\), we would compute the paired difference-in-differences \({\Delta }_{\Delta }={\Delta }_{{\mathrm{unmasked}}}-{\Delta }_{{\mathrm{masked}}}\), and we would again compare this quantity to chance using a one-tailed t-test.

We would then generate bootstrapped distributions (5000 samples) for \({\triangle }_{{\mathrm{unmasked}}}\), \({\triangle }_{{\mathrm{masked}}}\), and \({\Delta }_{\Delta }\) from which we would obtain 95% confidence intervals for each quantity, as well as Cohen’s d estimates and confidence intervals for \({\triangle }_{{\mathrm{unmasked}}}\) and \({\triangle }_{{\mathrm{masked}}}\), using the DABEST package for estimation statistics. (DABEST does not currently implement Cohen’s d for differences-in-differences.) Confidence intervals would then be visualised as are the hypothetical results shown in Fig. 3.

Fig. 3: Hypothetical outcomes (simulated data).
figure 3

a If intentional binding requires conscious awareness of the operant stimulus, i.e. Hypothesis 1 is false, then estimation bias should be the same in both masked blocks, but should be positively biased in the operant-unmasked block. The difference-in-differences, then, will be positive as per Hypothesis 2. b Alternatively, if Hypothesis 1 is true, evidence of binding should be found in both blocks, and the difference-in-differences is unlikely to be very different from zero, i.e. Hypothesis 2 is false. The experiment was designed such that, if one hypothesis were strictly false (i.e. zero effect size), we would be well-powered to detect the competing hypothesis.

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Deviation from Stage 1 protocol and updated power analyses

Upon the conclusion of data collection, we noted that a non-negligible number of participants who satisfied our preregistered participant-level inclusion criteria (that their detection rate for the masked operant stimulus did not significantly exceed their false alarm rate; see ‘Sampling Plan’) had quite high false alarm rates. In other words, some participants reported seeing the masked circle stimulus often even on trials where it objectively did not appear. Due to the presence of such participants, removing trials in which they reported seeing a masked stimulus, as specified in our trial-level exclusion criteria (see ‘Preregistered Analysis Plan’), resulted in trial counts varying across participants to an unexpectedly large degree. Thus, participants’ conditions means were non-identically distributed (since the variance of the condition mean is inversely related to the number of trials), violating the assumptions of the preregistered main analyses using paired t-tests. We brought this issue to the attention of the editor, who consulted with the reviewers; following interim peer review, the paired t-tests we had originally planned for our main analyses in our Stage 1 manuscript have been replaced with a linear mixed model (see Table 1), modelling the data at the trial level. We use the following model specification for our main analyses:

$${{\mbox{reported}}}\, {{\rm{time}}}\, {{\rm{of}}}\, {{\rm{action}}}_{i} = \, \alpha +{\beta }_{{\mbox{operant}}}\cdot {{\mbox{operant}}}_{i}+{\beta }_{{\mbox{unmasked}}}\cdot {{\mbox{unmasked}}}_{i}\\ +{\beta }_{{\mbox{interaction}}}\cdot {{\mbox{operant}}}_{i}\cdot {{\mbox{unmasked}}}_{i}+{\varepsilon }_{i}+{\epsilon }_{j}$$

for trial \(i\) and subject \(j\), with \({{\mbox{unmasked}}}_{i}=1\) in only the unmasked conditions and \({{\mbox{operant}}}_{i}=1\) only in the operant conditions (both equal to zero otherwise). Thus, \({\beta }_{{\mbox{operant}}}\) is interpreted as the difference in the perceived time of an action due to that action being followed by a sensory consequence in the masked conditions (i.e. \({\beta }_{{\mbox{operant}}}{\approx \Delta }_{{\mathrm{masked}}}\)), and \({\beta }_{{\mbox{interaction}}}\) is the additional difference when one is also aware of that sensory consequence (i.e. \({\beta }_{{\mbox{interaction}}}\approx {\Delta }_{\Delta }={\Delta }_{{\mathrm{unmasked}}}-{\Delta }_{{\mathrm{masked}}}\)). Hypothesis 1 was evaluated with a one-tailed test of the null hypothesis that \({\beta }_{{\mbox{operant}}}=0\), and Hypothesis 2 was evaluated with a one-tailed test of the null hypothesis that \({\beta }_{{\mbox{interaction}}}=0\). In both cases, the alternative hypothesis for the one-tailed test is that the regression coefficient is greater than zero, corresponding to the directional predictions preregistered in our Stage 1 manuscript. We report confidence intervals for these effect sizes in milliseconds from mixed linear model output. Though a t-test is still used for the unmasked/canonical intentional binding effect (positive control) as preregistered, since the trial exclusion criteria that warranted deviation from the Stage 1 protocol for the main analyses does not apply to the unmasked blocks, we generate 95% confidence intervals for the unmasked effect size in milliseconds using a mixed linear model as well to facilitate direct comparison between masked and unmasked conditions. For all contrasts, we still report bootstrap confidence intervals for paired Cohen’s d as described in the preregistered protocol, in the interest of providing an effect size estimate useful for power analyses and easily comparable to other studies using the intentional binding paradigm (where paired t-tests are the standard analysis approach); however, these Cohen’s d estimates (unlike our more conservative main analysis) use all trials in each condition to preserve balanced trial counts and satisfy the assumptions of a t-test.

As the power analyses used to determine our sample size (see ‘Sampling Plan’) pertained to the originally planned t-tests, we conducted additional power analyses to ensure the sample size is still adequate for the new mixed linear modelling approach. We conducted power analyses by simulation, using the same simulation parameters we had previously used to simulate trial-level data when assessing the possibility of breakthrough trials assessing results (see ‘Sampling Plan’). Statistical power was estimated as the proportion of 10,000 simulations in which the null hypothesis was rejected. With a sample size of 80 participants, we found that the new test should yield power 0.984 at a significance level of 0.01 for Hypothesis 1, and it should yield power 0.982 at a significance level of 0.05 for Hypothesis 2. We additionally verified, as before (see ‘Sampling Plan’), that a 5% rate of ‘breakthrough’ trials was unlikely to result in a false positive; such trials caused a false positive result on just 2.87% of simulations, leading to an acceptable combined (statistical and breakthrough-confounding) false positive rate of just 3.87% for Hypothesis 1.

Results

Sample composition

We reached our target of 80 usable participants (i.e. participants who satisfied our criteria for inclusion in analyses involving masked conditions, see ‘Sampling Plan’) after collecting data from 98 volunteers. By this time, two additional volunteers who had already signed up were allowed to participate in the experiment as well, bringing the final sample size to 100 participants (biological sex, self-reported: 33 male participants/67 female participants; age range: 17–32; mean age: 19.95; median age: 20), but only n = 80 were used in the main analyses evaluating Hypothesis 1 and Hypothesis 2 as per our Stage 1 protocol. No data on race/ethnicity were collected.

Canonical intentional binding effect

The canonical intentional binding effect was replicated in the unmasked conditions, where participants were aware of the operant stimulus (or lack thereof). Participants’ reported action times were, on average, later in the operant-unmasked conditions than they were in the baseline-unmasked conditions (\({\beta }_{{\mbox{operant|aware}}}\) = 5.26 ms, 95% CI: [0.45, 10.06]). This difference was statistically significant (t(99) = 1.69, one-tailed p = 0.047), although the effect size was lower than the expected size used for our original power analyses (Cohen’s d = 0.13, bootstrap 95% CI: [−0.02, 0.30]).

Hypothesis 1: No evidence for masked intentional binding

We did not find statistically significant evidence in favour of Hypothesis 1 (Z = −2.15, one-tailed p = 0.984). In fact, rather than a mere lack of positive bias in participants’ action timing estimates on operant trials, there was unexpectedly a negative bias (\({\beta }_{{\mbox{operant}}}\) = −6.91 ms, 95% CI: [−13.21, −0.61]); in other words, an operant stimulus presented outside of awareness seemingly caused repulsion of the perceived action time rather than binding (Cohen’s d = −0.25, bootstrap 95% CI [−0.46, −0.03] including all trials; Cohen’s d = −0.03 [−0.32, 0.23] excluding trials with false positive reports). Note that the preregistered test was one-tailed, sensitive only to positive biases; the inference that there was, in fact, a negative bias is an exploratory finding based on interpretation of the confidence interval of the bias estimate/linear model coefficient.

Hypothesis 2: Intentional binding effect differs depending on awareness of the operant stimulus

Results supported Hypothesis 2 (see Fig. 4); the presence of an operant stimulus caused a substantially more positive bias in action timing estimates in the unmasked than in the masked conditions (\({\beta }_{{\mbox{interaction}}}\) = 10.66 ms, 95% CI: [1.98, 19.35]), which was statistically significant (Z = 2.41, one-tailed p = 0.008). As per our preregistered predictions (see ‘Introduction’ or Table 1), we interpret this result as evidence that the canonical intentional binding effect depends on conscious awareness.

Fig. 4: Results.
figure 4

Huber means of action time estimates, quantified as error relative to the objective time, for each participant in each condition are shown on top. Bootstrap distributions, 90% confidence intervals, and means for paired effect sizes (including interaction ‘delta-delta’ on far right) are shown on bottom. Consistent with Hypothesis 2, the bias in action time estimates induced by an operant stimulus (i.e. sensory consequence) is substantially more positive when participants are aware of the operant stimulus. To our surprise, the mean bias when participants were unaware of the operant stimulus was negative (rather than merely zero as in the hypothetical outcomes we illustrated in Fig. 3), indicating that the perceived time of an action was actually repelled from the time of its unconsciously perceived sensory consequence.

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Discussion

Results definitively supported Hypothesis 2; the intentional binding effect, in the direction it is typically observed, depends on conscious awareness of the sensory consequence. This finding is consistent with what we have called, in the Introduction, the ‘illusionist’ view of self. The perception that our actions cause events in the sensory world, which is consciously experienced as the SoA, is understood to be a critical cognitive process subserving minimal self-awareness13. That the intentional binding effect, an implicit signature that an action has been linked to a sensory outcome, is disturbed when the operant stimulus fails to enter conscious awareness indicates that this critical process of self-attribution does not continue to operate outside of awareness in the same manner as it does when one is aware of both action and consequence. In other words, results are consistent with the illusionist account in which consciousness is a precondition to the component neural and cognitive processes, which, together, constitute the self. Conversely, results failed to support the independence view in which some core processes which constitute the self can operate outside of conscious awareness as they do within awareness.

We maintain, consistent with the theoretical commitments we detailed in the Introduction (written at the time of our Stage 1 manuscript), that our experimental outcome indeed is most compatible with the illusionist view. However, the unexpected finding that the intentional binding effect is reversed when the sensory consequence of action is masked from awareness, rather than simply abolished, adds substantial nuance to this conclusion. As mentioned in the Introduction, independence accounts would posit that the SoA is the conscious experience of some referent process which would still exist regardless of whether it were consciously perceived. The fact that the perceived time of an action seems to be repelled from the time of an unconsciously perceived outcome, though distinct from the canonical presentation of the intentional binding effect, suggests that the brain has indeed linked the action and its outcome, implying the existence of a potential referent. However, the consequence of making this causal link outside of awareness on the perceived time of the action differs markedly from when participants are aware of both action and outcome, suggesting that a potential referent for SoA is present but is never actually consciously perceived as such (i.e. the processes that give rise to conscious binding and unconscious repulsion are distinct) or, alternatively, the operating characteristics of the referent process are substantively altered when interacting with awareness. While both possibilities would constitute illusionist accounts, as operating characteristics that typically coincide with the SoA would depend upon consciousness, the latter possibility salvages certain appealing features of independence views. Specifically, neural machinery already known to differentiate self-caused from externally-caused sensations outside of awareness (e.g. corollary discharge22) could still be parsimoniously reused rather than replaced by a separate mechanism for conscious self-attributions.

Contemporary explanations for previously observed temporal repulsion effects may support such a compromise position. The first study to report the intentional binding effect was also the first, and still one of few, to report an action-outcome repulsion effect; in a separate condition in which transcranial magnetic stimulation (TMS) was used to elicit the button-pressing muscle movement that caused (or did not cause) a sensory outcome, the estimated time of the button press was repelled from, rather than biased toward, the time of the operant stimulus48. This result was taken to support the specificity of the binding effect to intentional action, as unintentional action elicited by TMS resulted in a directionally opposite effect. However, it is now clear that intentional binding can occur in the absence of intentional action, making the name ‘intentional binding’ somewhat of a misnomer49. However, this empirical development left the originally reported repulsion effect for TMS-induced movements without a consensus theoretical explanation. One ambitious proposal explains intentional binding results across a range of studies within a unifying Bayesian cue integration framework; Legaspi and Toyoizumi have shown their simple model—where when a sensory event is judged as being caused by some action, the perceived time between the events is biased toward some prior on plausible action-outcome time intervals, resulting in binding when the temporal interval between two internal representations/responses is longer than the prior and repulsion when it is shorter—reproduces both intentional binding and unintentional repulsion if one assumes that the internal/neural representation of a TMS-induced movement lags behind the internal representation of a movement that is initiated in the central nervous system64. Since the temporal interval between internal representations of movement and outcome is shorter in this case, biasing the perceived action-outcome interval toward a prior requires expanding the temporal interval (repulsion) rather than shrinking it (binding). In our case, if we assume that the neural activity corresponding to a conscious percept is delayed relative to the initial/unconscious sensory response to the same operant stimulus65, then the temporal interval between conscious action and unconscious outcome representations would again be shorter than that between the actual action and outcome themselves and, if smaller than the action-outcome interval prior, would more likely result in repulsion. This model could also explain the recent finding that a small but non-negligible minority of people show repulsion, even in the standard intentional binding paradigm66, as a result of individual differences in the prior on action-outcome intervals.

Of course, whether the Legaspi and Toyoizumi model explains the present findings is purely speculative and untested in the present study. If applicable, however, it would suggest the following: the same cognitive machinery that drives intentional binding when two events are processed on the same timescale may result in repulsion when processed on different timescales (e.g. if conscious processing occurs later relative to a sensory event than unconscious processing as in global neuronal workspace theory65). Consequently, binding may occur between two unconsciously or two consciously processed events, but not when two events straddle the boundary of awareness as in the present study. This account, though quite speculative, would predict the separation between conscious and unconscious processing of sensorimotor contingencies characteristic of illusionist views, but it would do so without requiring separate neurocognitive mechanisms for conscious and unconscious sensorimotor processing. We suggest that exploring this possibility, which would resolve many of our own hesitations about the illusionist view for which we presently find evidence should it extend to other core cognitive processes subserving self-awareness, could be a fruitful avenue for future research. It is our opinion that the mysteries of human self-awareness can only be unravelled through a research program that aims to comprehensively characterise specific functional consequences of conscious awareness on self-related cognitive processes.

Limitations

Another unexpected feature of the data was that some participants had quite high false positive rates for detecting a masked stimulus, evident in their reporting seeing a stimulus at high rates even in the block in which no masked stimulus was actually presented. As participants were led to believe there would indeed be a masked stimulus on some trials but were not told how many, these participants might have simply been guessing in the absence of any actual conscious percept and individual differences in false positive rates merely reflected their prior expectation about the rate of masked stimulus presentations. Speculatively, it is also a possibility that highly motivated participants could have actually conjured an illusory percept in the absence of a physical stimulus; the ability to create perceptual experiences for oneself—sometimes called ‘phenomenological control’67—is known to correlate with individual differences in the magnitude of the intentional binding effect68, so we advise participants’ false positive rates be taken into account in any secondary analyses of our open dataset. However, as our preregistered main analyses were purely within-subject, false positive trials were conservatively excluded from analyses (though we note that results remain directionally consistent even if they are included, as in the bootstrap effect size distributions visualised in Fig. 4), and there is no reason to believe that any illusory percept would have been time locked to the action in any case, the present results are highly unlikely to have been affected by this sort of confound.