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Journal of Experimental Psychology:
Human Perception and Performance
2009, Vol. 35, No. 5, 1542–1549
© 2009 American Psychological Association
0096-1523/09/$12.00 DOI: 10.1037/a0014492
Magnitude Estimation Reveals Temporal Binding
at Super-Second Intervals
Gruffydd R. Humphreys and Marc J. Buehner
Cardiff University
Several recent studies (e.g., Haggard, Aschersleben, Gehrke, & Prinz, 2002; Haggard & Clark, 2003;
Haggard, Clark, & Kalogeras, 2002) have demonstrated a “Temporal Binding” effect in which the
interval between an intentional action and its consequent outcome is subjectively shorter compared to
equivalent intervals that do not involve intentional action. The bulk of the literature has relied on the
“Libet Clock” (Libet, Gleason, Wright, & Pearl, 1983; but see also Engbert & Wohlschläger, 2007;
Engbert, Wohlschläger, Thomas, & Haggard, 2007; Engbert, Wohlschläger, & Haggard, 2008). Here we
demonstrate that Temporal Binding is a robust finding that can also be reliably achieved with a
Magnitude Estimation procedure, and that occurs over intervals far greater than those previously
explored. Implications for the underlying mechanisms are discussed.
Keywords: interval estimation, temporal binding, time perception
action and result. This efferent binding, Haggard, Aschersleben et
al. argued, should result in perceptual attraction between intention,
action, and effect: The stronger the association between action and
effect, the shorter the subjective experience of time elapsing between them should be. In contrast, when the efferent copy does not
accurately predict the effect, the mechanism does not bind the two
representations and the sense of agency does not arise.
Haggard, Aschersleben et al. (2002) used the “Libet Clock”
paradigm (Libet, Gleason, Wright, & Pearl, 1983) to test their
efferent binding hypothesis. Participants were instructed to judge
the time at which various events occurred. Judgments were made,
with reference to a fast-moving hand on a clock face, and participants indicated where the hand was when the event of interest
occurred. To establish a baseline of judgment error, participants
were asked to report the times of either their own key press, or of
an auditory stimulus (beep). Of interest, however, were Operant
trials on which participants’ key presses produced the beep 200 ms
later. In these trials, participants were asked to either report the
time of their action (key press) or of the resultant beep. Haggard,
Aschersleben et al. calculated a shift in judgment error by subtracting participants’ judgment of button press or tone in single
event Baseline trials from their respective Operant judgments.
During Operant trials participants’ perceived timings of volitional
actions and tones were shifted in time relative to the baseline; more
specifically, actions that were followed by an effect were perceived to have occurred later than actions that did not produce a
beep, and beeps that were the result of an earlier intentional action
were perceived to have occurred earlier than beeps that occurred
on their own: the Temporal Binding phenomenon.
Haggard, Aschersleben, et al. (2002) argued that the critical
factor for the appearance of Temporal Binding is the agent’s
intention to make the resultant movement. A direct test of this
intentionality-based efferent binding hypothesis involved an experiment in which neither stimulus involved intentional action: the
participants’ button presses were replaced by another tone, and no
One of the key ingredients towards a sense of agency (Wegner,
2002), is temporal contiguity between one’s action and the resultant effects: If I extend my arm to knock down a domino, the effect
must happen soon after my arm movement for me to feel that I was
a causal agent in the chain of events. The immediacy 3 agency
postulate parallels David Hume’s (Hume, 1739/1888) analysis of
causal inference: Our sensory input does not contain direct information about either agency or causality. All that is available is
information about the presence and absence of events in our
environment, and the temporal and spatial relations between them.
Temporal contiguity between our actions and consequent outcomes thus simultaneously serves to create impressions of causality (e.g. “the action resulted in the outcome”) and a sense of
agency (“I produced the outcome”).
Haggard, Aschersleben, Gehrke, and Prinz (2002) proposed that
a CNS based mechanism, similar to a “Forward Model” of motor
command (Wolpert, 1997) aids in learning the relationships between intended actions and their effects (Miall & Wolpert, 1996;
Wolpert & Kawato, 1998). According to this forward model theory, a motor command creates an efferent copy of itself at the
moment of movement, which in turn is processed by a dedicated
neural circuit that predicts (utilizing prior knowledge of the relationship, if available) the action’s effect. When efferent copy and
motor reafference are identical, the association between them
strengthens, thus promoting learning of the relationship between
Gruffydd R. Humphreys and Marc J. Buehner, School of Psychology,
Cardiff University.
The research reported in this article is part of GRH’s doctoral dissertation under the supervision of MJB, and was funded by EPSRC grant
EP/C004469/1 awarded to MJB. We thank Tom Freeman for discussing
potential implications of range effects on our results.
Correspondence concerning this article should be addressed to
Gruffydd R. Humphreys, School of Psychology, Cardiff University,
Park Place, Tower Building, Cardiff, CF10 3AT. E-mail: [email protected]
binding occurred. In addition, when participants observe the experimenter press the button, Temporal Binding still appears, but
not when the button depresses of its own accord (Wohlschläger,
Haggard, Gesierich, & Prinz, 2003) or is depressed by a rubber
hand (Wohlschläger, Engbert, & Haggard, 2003), because neither
presumably displays intentionality. This dependence of temporal
binding on intentionality was repeated when the voluntary action
was perceived to be involuntary through hypnotic suggestion
(Haggard, Cartledge, Dafydd, & Oakley, 2004). The enforcing of
an involuntary action via Transcranial Magnetic Stimulation (Haggard, Clark, & Kalogeras, 2002; Haggard & Clark, 2003) produced
a temporal repulsion: relative to baseline participant judgments of
action and effect onset were shifted away from each other in time.
Furthermore, the magnitude of the effect has been shown to
influence the extent of binding, with more intense tones eliciting a
larger shift relative to baseline (Engbert, 2005).
A more general appraisal of the temporal binding effect was
offered by Eagleman and Holcombe (2002), who argued that the
causal relationship between action and effect is the crucial ingredient. Harking back to Hume (1739/1888) they pointed out that
temporal contiguity is a well-established cue towards causality.
They conjectured that the mind utilizes the temporal contiguity cue
in a bidirectional manner: Not only are we likely to consider
contiguous event pairings as causal, but we may also consider
causal event pairings as more contiguous. In situations in which
there is some uncertainty in temporal measurement, the binding
together of two events that are known to be causally related can be
seen as an adaptive process that reconstructs the relationship
between these events (Stetson, Xu, Montague, & Eagleman, 2006).
Note that the causal analysis of temporal binding is not in contradiction with the intentional analysis. Rather, according to this
view, intentional binding is simply a special case of causal binding, such that the cause happens to be an intentional action.
The finding of a TMS repulsion effect (Haggard, Clark et al.,
2002) mentioned above might appear to contradict Eagleman and
Holcombe’s (2002) analysis. However, close inspection of the
experimental protocol in this condition reveals that in fact there
was no causal relation between the TMS-induced muscle twitch
and the beep that followed; rather, both the TMS stimulation and
the delivery of the tone were controlled by an experimental program. Presumably, participants were acutely aware that no causal
link existed between their muscle twitch and the tone that followed
it, and hence no binding would be expected under either an
intentional or a causal perspective.
This paper, however, is not designed to investigate the intentionality/causality dichotomy. Our further use of the terms intentional and causal in this paper thus does not indicate a selective
endorsement of either hypothesis. We intended to follow up on
what we saw as a main shortcoming in the wealth of evidence in
support of Temporal Binding outlined above: the almost exclusive
usage of the Libet Clock paradigm. The method itself has over
many years received much in the way of both support and criticism
(Libet, 1985, 2002; Pockett & Miller, 2007). In the current context
of temporal binding, we see two main limitations or problems.
Firstly, the effect could simply be an artifact of the method. For
example, the Libet Clock has previously been subject to some
criticism based on the “Flash Lag” effect (Nijhawan, 1994), in
which a moving stimulus and a flash appearing at the same
location are judged to be spatially separate. It has been argued that
a fundamental flaw of the Libet Clock may be its vulnerability to
this effect (e.g., Gomes, 2002, Pockett, 2002). Although it may be
that the appropriation of baselines acts to cancel out any flash-lag
specific effects pertaining to the reality of Temporal Binding (cf.
Moore & Haggard, 2008) this contention is sufficient to lead us to
seek a new paradigm. Secondly, the Libet Clock examines the
timing of one event per trial relative to a baseline, and does not
measure the relative interval between events. Clearly, if one is
interested in studying temporal binding, a more direct measure
would be to study changes in the perceived length of elapsed time
between events. The Libet Clock method at best offers a very
indirect route to obtain this measure.
Therefore, our first goal was to investigate whether Temporal
Binding is a robust phenomenon that can be demonstrated with
methods other than the Libet Clock; more specifically, we employed a free numerical temporal estimation method to measure
the subjective interval between intentional actions and their subsequent effects. A recent series of experiments have demonstrated
a binding effect with a magnitude estimation method at intervals of
200 to 300 ms (Engbert & Wohlschläger, 2007; Engbert,
Wohlschläger, & Haggard, 2008, Engbert, Wohlschläger, Thomas,
& Haggard, 2007). However, we intended to replicate temporal
binding with a magnitude estimation procedure, and the intervals
used in Haggard, Aschersleben et al’s (2002) original report (Experiment 1a). Haggard, Aschersleben et al. investigated binding at
intervals up to 650 ms, and reported that the size of the binding
effect diminished as the temporal interval increased. This could
either reflect a natural limitation of the binding effect, or be rooted
in artificial constraints of the Libet Clock method. Consequently,
we also aimed to investigate whether binding occurs at intervals
longer than 650 ms (Experiments 1b-e). To foreshadow our results:
we were surprised to find that Experiment 1a suggested that the
temporal binding effect increased with interval size. Based on
Haggard, Aschersleben et al.’s results, we had predicted a decrease. Inspired by this surprise result, we proceeded to push
Temporal Binding to its limits, and increased the temporal intervals under investigation up to 4 s, where we still found reliable
Experiments 1a-e
All Experiments involved the same basic method. Participants
were presented with Operant and Observational trials. On Operant
trials, participants pressed a button at a time of their choosing,
which resulted in the delivery of a 100-ms, 1-kHz pure tone after
a set interval. On Observational trials, participants did not perform
any intentional or causal actions; instead, they were presented with
an audible click, which was followed by the same 100-ms, 1-kHz
pure tone after a set interval. The click in these trials was recorded
from the button box used on Operant trials, and thus was identical
to the noise made by the microswitch when participants pressed
the button in the Operant trials. At the end of each trial, participants had to estimate the length of the interval between their button
press and the tone (Operant trials), or the click and the tone
(Observational trials). Because Operant trials involved intentional
causal action and Observational trials did not, we hypothesized
that participants would judge the interevent intervals to be shorter
in Operant trials than in relative Observational trials.
Participants. Sixteen different Cardiff University undergraduate students participated in each of Experiments 1a-d, and seventeen in Experiment 1e, either to partially fulfill a course requirement, or to receive £4. Each participant served in one experiment
only, so each experiment had a different cohort of participants.
Materials and apparatus. The experiments were conducted on
an Apple iMac, and programmed with Psyscope (Cohen, Macwhinney, Flatt, & Provost, 1993); the psyscope “Button Box” was
used for timing of stimulus delivery and as an input device in the
Operant trials. Temporal estimates were entered via the keyboard.
Each experimental trial contained two events, separated by an
interval. The first was a button press in Operant, and a click in
Observational trials; the second was a 100-ms, 1-kHz pure tone. A
green or red fixation cross at the centre of the screen denoted
Operant or Observational trials, respectively. Crosses were removed at the beginning of the first event of each trial.
Design and procedure. The factors Interval (see below) and
Trial Type (Observational vs. Operant) were factorially combined
in a within-subjects procedure. The Intervals used across the four
experiments were as follows. Experiment 1a: 150, 250, 350, 450,
550, and 650 ms; Experiment 1b: 750, 850, 950, 1,050, 1,150, and
1,250 ms; Experiment 1c: 0, 250, 500, 750, 1,000, 1,250, 1,500,
1,750, and 2,000 ms; Experiments 1d and 1e: 0, 500, 1,000, 1,500,
2,000, 2,500, 3,000, 3,500, and 4,000 ms.1
Operant and Observational trials were blocked so that participants experienced one trial of each interval per block. The
order of intervals within a block was random, and Operant and
Observational blocks alternated. Each participant worked on 10
Operant and 10 Observational blocks, thus providing 20 separate temporal estimates for each interval, 10 of which involved
Operant, and 10 Observational trials. The nature of the first
block (Operant vs. Observational) was counterbalanced between participants.
Each interval began with a display of a fixation cross at the
center of the screen. The cross was green on Operant and red on
Observational trials. On Operant trials, pressing the green button on the response box cleared the fixation cross from the
screen and triggered the relevant interval, after which the tone
was delivered. On Observational trials, the red cross remained
on the screen for a random interval between 1,500 and 2,000
ms, after which the click was presented and the cross disappeared; the pure tone was then delivered after the appropriate
interval. Although participants were asked to judge the interval
between events, it was possible that participants would begin
interval timing sometime during this (⬃120 ms) click stimulus.
As such, we adopted a highly conservative timing criterion, and
programmed the experiment such that the timing of this interval
commenced at the beginning of the presented click, thus potentially shortening the Observational interval for our participants,
and working against our hypothesis.
Each trial ended with an onscreen prompt to provide an estimate
for the interevent interval. The response range was restricted from
0 to 999 ms in Experiment 1a, from 0 to 1,999 ms in Experiment
1b from 0 to 2,000 ms in Experiment 1c, from 0 to 4,000 ms in
Experiment 1d, and from 0 to 5,000 ms in Experiment 1e. Once the
Return key was depressed, the response was entered the next trial
began after a random interval between 750 to 1,000 ms.
Participants were informed that they would be partaking in a
study of time perception. After giving written consent to participate in the study participants were provided with a general outline
of the experimental procedure, followed by written instructions
specific to Operant or Observational blocks. At the start of Operant
blocks, participants were informed that the appearance of the tone
was wholly dependent on their actions: Pressing the green button
on the Button Box would produce a tone after a set interval.
Instructions suggested that participants could delay their button
press: The absence of a tone during this duration demonstrated that
the delivery of the tone was wholly dependent on their action.
Before Observational blocks, instructions emphasized that participants were not required to press the key but would passively
observe two unrelated events. These instructions were presented at
the beginning of each block, to facilitate clear discrimination
between Operant and Observational blocks.
Results and Discussion
Median temporal judgments. Each participant returned 10 temporal judgments per Trial Type ⫻ Interval combination in each
Experiment. Participants’ median temporal judgments served as the
primary units of analysis, and are displayed in Figures 1 through 5.
Median judgments more than two standard deviations from the
mean of all median judgments for a particular Trial Type ⫻
Interval combination were considered outliers, and participants
contributing one or more outliers were removed from the analyses.
This criterion led to the exclusion of 2 participants in Experiment
1a, 1 participant in Experiment 1b, 3 participants in Experiment 1c,
3 participants in Experiment 1d, and 4 participants in Experiment
1e. All statistical analyses adopted a significance level of 0.05
except where otherwise noted.
Inspection of Figures 1 through 5 shows that participants
clearly distinguished between the various intervals, and suggests that Operant intervals were consistently judged shorter
than equivalent Observational intervals. Furthermore, it appears
that this difference increased as a function of interval duration
in Experiments 1a, b, c, and e. Statistical analyses corroborate
this impression. We performed repeated measures Trial Type ⫻
Interval ANOVAs for each experiment separately and found
consistent and robust effects of Trial Type, Experiment 1a: F(1,
13) ⫽ 10.60, MSE ⫽ 35022.11, ␩2 ⫽ .45; Experiment 1b: F(1,
14) ⫽ 19.58, MSE ⫽ 49923.16, ␩2 ⫽ .58; Experiment 1c:
F(1, 12) ⫽ 13.28, MSE ⫽ 85354.86, ␩2 ⫽ .53; Experiment 1d:
F(1, 12) ⫽ 5.44, MSE ⫽ 52229.87, ␩2 ⫽ .31, and Experiment
1e: F(1, 12) ⫽ 5.36, MSE ⫽ 113482.62, ␩2 ⫽ .039. This result
indicates that judgments derived from Operant intervals were
overall judged to be shorter than judgments from Observational
Experiment 1e is a replication of Experiment 1d, but with a wider
response range, aimed at ruling out a concern raised by an anonymous
reviewer that limiting the response range to the maximum interval (4,000
ms) might have biased the results. Our replication shows that this was not
the case.
Interevent Intervals (milliseconds)
Figure 1. Experiment 1a: Mean median temporal judgments as a function of Interval Length and Trial Type.
Error bars indicate standard errors of the mean.
intervals.2 As would be expected, the main effect of Interval
was also significant in each experiment, indicating that participants successfully discriminated different interval lengths, Experiment 1a: F(5, 65) ⫽ 23.52, MSE ⫽ 18485.60, ␩2 ⫽ .64;
Experiment 1b: F(5, 70) ⫽ 24.12, MSE ⫽ 41883.41, ␩2 ⫽
.63; Experiment 1c: F(8, 96) ⫽ 133.67, MSE ⫽ 47421.25, ␩2 ⫽ .92;
Experiment 1d: F(8, 96) ⫽ 217.38, MSE ⫽ 174139.16, ␩2 ⫽ .95;
Experiment 1e: F(8, 96) ⫽ 187.037, MSE ⫽ 212799.528, ␩2 ⫽ .94.
The Trial Type ⫻ Interval interaction was significant in Experiment 1a, F(5, 65) ⫽ 6.54, MSE ⫽ 3287.46, ␩2 ⫽ .34, Experiment 1b, F(5, 70) ⫽ 3.38, MSE ⫽ 9622.14, ␩2 ⫽ .19, and
Experiment 1c, F(8, 96) ⫽ 4.37, MSE ⫽ 20154.47, ␩2 ⫽ .27 but
not in Experiments 1d, F(8, 96) ⫽ 0.55, n.s. or 1e, F(8, 96) ⫽
0.85, n.s.3
Slope analysis. To better understand how the Operant/
Observational effect changes with increasing intervals we additionally conducted Slope Analyses, as previously employed in
experiments involving numerical estimation of duration (PentonVoak, Edwards, Percival, & Wearden, 1996; Wearden, Edwards,
Fakhri, & Percival, 1998). To this end, we calculated for each
participant an individual regression slope across his or her median
temporal judgments of the Operant and Observational intervals
within a given experiment. We then compared Operant and Observational slopes with Wilcoxon Signed Rank tests, because of
the nonnormal distribution of slopes.4
The slope from Operant interval estimations was significantly
less steep in Experiment 1a, Z ⫽ 3.411, with 15 of 16 participants
returning a shallower slope for the Operant interval (one tie). The
same was true in Experiment 1b, Z ⫽ 2.54, with 12 participants
returning a shallower slope, 2 a steeper one, and 1 tie,5 and in
Experiment 1c, Z ⫽ 3.10, with 13 participants returning a shal-
lower slope and 3 a steeper one. The slopes in Experiment 1d did
not differ reliably, Z ⫽ 1.02, with 8 participants returning a
shallower slope, 7 a steeper one, and 1 tie. However, the same
intervals produced reliably different slopes (one-tailed) in Experiment 1e, Z ⫽ 1.70, with 11 participants returning a shallower
slope, 4 a steeper one, and 1 tie. When data from both Experiment
One anonymous reviewer expressed concern that when comparing
Experiments 1a and 1b to Experiments 1c-e, the size of the interval
range and the absolute interval values over which that range spans are
partially confounded, and that because of this, our experiments cannot
shed light on a possible contribution of range effects on participants
estimates (e.g. Poulton, 1979). Range effects may well have biased
participants’ judgments differently across these two groups of experiments. Importantly, however, any bias induced by range effects would
have affected Operant and Observational conditions equally because
they employed exactly the same intervals and ranges. Furthermore,
since these conditions were varied within participants, our central
finding of a robust main effect of Trial Type could not be compromised
by different range effects across these studies.
Pooling the data from Experiments 1d and e (and applying outlier
criteria on the merged dataset) reveals the same results: A significant main
effect of Trial Type, F(1, 26) ⫽ 7.77, MSE ⫽ 198470.72, ␩2 ⫽ .23; a
significant main effect of Interval, F(8, 208) ⫽ 514.21, MSE ⫽ 159817.14,
␩2 ⫽ .95, but no interaction, F(8, 208) ⫽ 1.20, MSE ⫽ 31191.51, ␩2 ⫽ .04.
The slope analyses reported here include all regression slopes, irrespective
of whether each individual participant’s model reached significance. In Experiment 1a, one model was nonsignificant; and in Experiment 1b, five models
were nonsignificant. In these cases, we also calculated the analyses based on
just the significant regression models. The results do not change.
One participant was excluded from slope analysis because he or she
returned the same judgment for each interval.
Interevent Intervals (milliseconds)
Figure 2. Experiment 1b: Mean median temporal judgments as a function of Interval Length and Trial Type.
Error bars indicate standard errors of the mean.
1d and e is merged, the overall analysis also indicates reliably
shallower slopes for Operant than Observational intervals, Z ⫽
1.90, with 19 participants returning a shallower, 12 a steeper slope,
and 2 ties.
General Discussion
We set out to replicate Haggard, Aschersleben et al.’s (2002)
results with a magnitude estimation method. Experiment 1a dem-
Mean of Median Temporal Judgments
Interevent Intervals (milliseconds)
Figure 3. Experiment 1c: Mean median temporal judgments as a function of Interval Length and Trial Type.
Error bars indicate standard errors of the mean.
Interevent Intervals (milliseconds)
Figure 4. Experiment 1d: Mean median temporal judgments in ms as a function of Interval Length and Trial
Type. Error bars indicate standard errors of the mean.
onstrated that operant intervals were reliably underestimated compared to equivalent observational intervals within the interval
range used by Haggard, Aschersleben et al. (up to 650 ms).
Importantly, this result was obtained using a direct measure of
interval length–magnitude estimation. Thus, the temporal binding
effect reported by Haggard, Aschersleben et al. is an empirically
robust phenomenon, that occurs not only when indirect measures
(temporal shifts calculated from single-event subjective timestamps) are employed, but also when participants have to report
their temporal percepts directly. The robust nature of the effect
and, more specifically, its apparent increase with interval size was
at variance with Haggard, Aschersleben et al.’s finding of a decrease. Thus, we set out to investigate whether temporal binding
might also occur over substantially longer intervals, and have
demonstrated, for the first time, that binding is steady across
intervals up to 4 s.
How can we reconcile this latter aspect of our results with
earlier work of Haggard, Aschersleben et al. (2002) and Haggard,
Clark et al. (2002) who reported a steady decrease in binding as the
interval size increased from 250 to 650 ms? A tempting suggestion
would be that the answer lies in the different experimental
methods. Whereas the Libet Clock method is dependent on taking
the judged onset of an event and comparing it to a baseline, the
Temporal Judgment method offers a direct examination of the
subjective interval. Directly examining the subjective interval between cause and effect thus might be more sensitive to the binding
effect at longer intervals.
A more satisfying, and theoretically interesting explanation
arises when we consider the potential processes underlying temporal binding. If temporal judgments reflect the processes of an
internal clock with a pacemaker (see for example Wearden, 2001
for an overview), our results, and in particular the reliable differences in slopes, would suggest that the pacemaker runs slower
during periods where people anticipate the consequences of their
intentional causal actions. Although a stable difference between
Operant and Observational trials could be explained by a delay in
the switch of the accumulator at the onset of Operant trials, or an
anticipatory, early switching off at the end of Operant trials, the
steady increase and differences in slopes are more suggestive of
different pacemaker speeds. A slower pacemaker would mean that
fewer pulses are accumulated, which in turn implies that the
Operant/Observational difference increases with longer intervals.
Indeed the general pattern of our results in Figures 1 through 5
closely resemble the results of other articles in which the disparity
in numerical estimations of the duration of two stimuli have been
explained in terms of a modulation in the speed of a pacemaker
(e.g. Penton-Voak et al., 1996; Wearden, 2008; Wearden et al.,
1998). The timing literature lists various determinants of pacemaker speed, including stimulus modality, interval content,
arousal, etc. (for an overview see Wearden, 2001), and it may well
be that causality and/or intentionality will need to be added into
this canon.
An additional explanation for our results, and in particular our
finding of temporal binding at Super-Second intervals, would be
that at least part of the effect is postdictive in nature. Moore and
Haggard (2008) have argued that intentional binding involves both
pre- and postdictive components. Their task manipulated the probability with which an intentional action led to the expected result.
Using the Libet Clock, Moore and Haggard found that intentional
actions were judged later relative to baseline in both high- and
Interevent Intervals (milliseconds)
Figure 5. Experiment 1e: Mean median temporal judgments in ms as a function of Interval Length and Trial
Type. Error bars indicate standard errors of the mean.
low-contingency conditions on “successful” trials where a key
press was followed by a tone, thus displaying the familiar perceptual shift underlying temporal binding. In contrast, when considering “unsuccessful” trials, where a key press did not produce the
tone, the shift was apparent only in the high-contingency condition. Taken together, these results suggest that a strong expectation
of the effect (in successful, and— critically—also in unsuccessful
trials of the high-contingency condition), led to a predictive perceptual shift, and that the observation of the effect (in successful
trials of the low-contingency condition) led to a postdictive perceptual shift. Moore and Haggard referred to the predictive component as sensory based, and to the postdictive component as
inference based, and suggested that both are integrated in a Bayesian manner. This distinction between, and integration of, sensory
and inferential processes is pertinent to our results.
Whereas sensory-based shifts are very short lived and might not
outlast the execution of an action (cf. Moore & Haggard, 2008),
there is no a priori reason why inferential shifts could not operate
over longer timescales. The Libet Clock method, of course, taps
largely into sensory processes, and thus might be less sensitive to
inferential processes than magnitude estimation. This would explain the Libet Clock’s failure to detect binding at longer intervals.
Moreover, it is well known that magnitude estimation is susceptible to a range of cognitive biases (e.g., see Poulton, 1979). Our
results of binding at super-second intervals could thus equally
reflect the operation of inferential processes, subject to postdictive
In conclusion, we have expanded upon earlier demonstrations of
intentional causal binding, and could show that the effect is robust
when measured directly via verbal judgments, and stable across
intervals as long as 4 s. Inferential, postdictive judgment biases
and a slower pacemaker speed during anticipation of intentionally
caused outcomes can both account for the effect. The trademark
signature of different pacemaker speeds—reliable differences in
slope— however suggests that pacemaker speed will have to considered in future research on temporal binding.
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Received January 15, 2008
Revision received September 23, 2008
Accepted September 24, 2008 䡲