Author response:
The following is the authors’ response to the original reviews.
Reviewer #1 (Public review):
Summary:
Is peristimulus alpha (8-14 Hz) frequency and/or phase involved in shaping the length of visual and audio-visual temporal binding windows, as posited by the discrete sampling hypothesis? If so, to what extent and perceptual scenario are they functionally relevant? The authors addressed such questions by collecting EEG data during the completion of the widely known 2-flash fusion paradigm, administered both in a standard (i.e., visual only, F2) and audio-visual (i.e., 2 flashes and 1 beep, F2B1) fashion. Instantaneous frequency estimation performed over parieto-occipital sensors revealed slower alpha rhythms right after stimulus onset in the F2B1 condition, as compared to the F2, a pattern found to correlate with the difference between modality-specific ISIs (F2B1-F2). Of note, peristimulus alpha frequency differed also between 1- vs 2-flash reports, although in the visual modality only (i.e., faster alpha oscillations in 2-flash percept vs 1-flash). This pattern of results was reinvigorated in a causal manner via occipital tACS, which was capable of, respectively, narrowing down vs enlarging the temporal binding window of individuals undergoing 13 Hz vs 8 Hz stimulation in the F2 modality alone. To elucidate what the oscillatory signatures of cross-modal integration might be, the authors further focused on the phase of posterior alpha rhythms. Accordingly, the Phase Opposition Sum proved to significantly differ between modalities (F2B1 vs F2) during the prestimulus time window, suggesting that audio-visual signals undergo finer processing based on the ongoing phase of occipital alpha oscillations, rather than the speed at which these rhythms cycle. As a last bit of information, a computational model factoring in the electrophysiological assumptions of both the discrete sampling hypothesis and auditory-induced phase-resetting was devised. Analyses run on such synthetic data were partially able to reproduce the patterns witnessed in the empirical dataset. While faster frequency rates broadly provide a higher probability to detect 2 flashes instead of 1, the occurrence of a concurrent auditory signal in cross-modal trials should cause a transient elongation (i.e. slower frequency rate) of the ongoing alpha cycle due to phase-reset dynamics (as revealed via inter-trial phase clustering), prompting larger ISIs during F2B1 trials. Conversely, the model provides that alpha oscillatory phase might predict how well an observer dissociates sensory information from noise (i.e., perceptual clarity), with the second flash clearly perceived as such as long as it falls within specific phase windows along the alpha cycle.
Strengths:
The authors leveraged complementary approaches (EEG, tACS, and computational modelling), the results thereof not only integrate, but depict an overarching mechanistic scenario elegantly framing phase-resetting dynamics into the broader theoretical architecture posited by the discrete sampling hypothesis. Analyses on brain oscillations (either via frequency sliding and phase opposition sum) mostly appear to be methodologically sound, and very well supported by tACS results. Under this perspective, the modelling approach serves as a convenient tool to reconcile and shed more light on the pieces of evidence gathered on empirical data, returning an appealing account on how cross-modal stimuli interplay with ongoing alpha rhythms and differentially affect multisensory processing in humans.
Weaknesses:
Some information relative to the task and the analyses is missing. For instance, it is not entirely clear from the text what the number of flashes actually displayed in explicit short trials is (1 or 2?). We believe it is always two, but it should be explicitly stated.
Moreover, the sample size might be an issue. As highlighted by a recent meta-analysis on the matter (Samaha & Romei, 2024), an underpowered sample size may very well drive null findings relative to tACS data in F2B1 trials, in interplay with broad and un-individualised frequency targets.
Some criticality arises regarding the actual "bistability" of bistable trials, as the statistics relative to the main task (i.e., the actual means and SEMs are missing) broadly point toward a higher proclivity to report 2 instead of 1 flash in both F2B1 and F2 trials. This makes sense to some extent, given that 2 flashes have always been displayed (at least in bistable trials), yet tells about something botched during the pretest titration procedure.
Coming to the analyses on brain waves, one main concern relates to the phase-reset-induced slow-down of posterior alpha rhythms being of true oscillatory nature, rather than a mere evoked (i.e., not sustained over time). Another question calling for some further scrutiny regards the overlooked pattern linking the temporal extent of the IAF differences between F2 and F2B1 trials with the ISIs across experimental conditions (explicit short, bistable, and explicit long). That is, the wider the ISI, the longer the temporal extent of the IAF difference between sensory modalities. Although neglected by the authors, such a trend speaks in favour of a rather nuanced scenario stemming from not only auditory-induced phase-reset alpha cycle elongation, but also some non-linear and perhaps super-additive contribution of flash-induced phase-resetting. This consideration introduces some of the issues about the computational simulation, which was modelled around the assumption of phase-resetting being triggered by acoustic stimuli alone. Given how appealing the model already is, I wonder whether the authors might refine the model accordingly and integrate the phase-resetting impact of visual stimuli upon synthetic alpha rhythms. Relatedly, I would also suggest the authors to throw in a few more simulations to explore the parameter space and assay, to which quantitative extent the model still holds (e.g. allowing alpha frequency to randomly change within a range between 8 and 13 Hz, or pivoting the phase delay around 10 or 50 ms). As a last remark, I would avoid, or at least tone down, concluding that the results hereby presented might reconcile and/or explain the null effects in Buergers & Noppeney, 2022; as the relationship between IAFs and audiovisual abilities still holds when examining other cross-modal paradigms such as the Sound-Induced Flash-Illusion (Noguchi, 2022), and the aforementioned patterns might be due to other factors, such as a too small sample size (Samaha & Romei, 2024).
We thank Reviewer 1 for the detailed and constructive comments. The main revisions are summarized below:
(1) We clarified the task design, the definition of the temporal integration window, and the interpretation of the bistable reports.
(2) We expanded the Methods to specify the POS time-frequency decomposition, posterior ROI, label-permutation procedure, leakage control, non-aligned KL analysis, and the complete simulation workflow and parameters.
(3) We corrected the bistable-report calculation using the actual valid-trial counts and added the corresponding frequentist and Bayesian results, together with the alpha-peak estimate, multiple-comparison corrections, and ITC/power controls.
(4) We revised the tACS interpretation so that the interaction is the primary result and the F2B1 null finding is treated cautiously.
(5) We expanded the computational model description and added the requested time-resolved simulated IAF and POS analyses.
Reviewer #1 (Recommendations for the authors):
(1) Line 64 - “Temporal windows, a fundamental attribute of the visual system, refer to time intervals during which discrete stimuli interact to influence perception”. I would delve a little deeper into the notion of temporal binding windows, given their relevance throughout the manuscript. Although the definition provided is broadly right, the way stimuli interact is dictated by the observer's degree of perceptual tolerance and/or sensitivity to noise. Hence the term “windows”.
We thank the reviewer for the suggestion. The Introduction now defines the temporal integration window and clarifies how its width is quantified in the double-flash paradigm. Specifically, a higher fusion-threshold ISI indicates that two flashes can remain susceptible to fusion across a longer temporal separation.
We have therefore added the following text to the Introduction: “The temporal integration window defines the range of separations over which distinct visual events can interact and be fused into a single percept (Samaha and Romei, 2024). Sensory uncertainty influences audiovisual simultaneity judgments, and stimulus reliability affects the temporal integration of successive visual inputs (Cary et al., 2024; Rangelov et al., 2021). In the double-flash paradigm, its width is indexed by the fusion-threshold ISI, defined as the separation at which one-flash and two-flash reports are equally likely. A higher threshold therefore indicates a wider integration window.”
(2) Line 107 - “Upon comparing different conditions, our investigation revealed that the introduction of auditory stimuli effectively prolonged the temporal window of integration by reducing the instantaneous frequency of alpha oscillations.” This sentence is a bit difficult to follow. It is not clear how the temporal window of integration prolongation has been measured. Moreover, it is not clear what you mean by the reduction of instantaneous frequency. Is it a reduction in the frequency of alpha?
We thank the reviewer for identifying this ambiguity. The temporal integration window was quantified behaviourally using the fusion threshold, defined as the interstimulus interval (ISI) at which one- and two-flash reports were equally likely. This threshold shifted from 52.68 ± 12.25 ms in F2 to 65.19 ± 13.17 ms in F2B1, indicating an extended integration window.
Instantaneous alpha frequency was calculated from the local temporal derivative of the unwrapped alpha phase. A lower value therefore indicates slower local phase progression. In F2B1, this slowing occurred transiently during the 0–280-ms post-stimulus interval and should not be interpreted as a sustained change in trait-like individual alpha frequency. We have therefore added the following sentences to the Introduction: “Behaviourally, the auditory beep shifted the fusion threshold to longer ISIs, indicating an extended temporal integration window. This behavioural extension was accompanied by a transient post-stimulus reduction in instantaneous alpha frequency.”
We have also clarified the correlation analysis to specify that the auditory-induced increase in post-stimulus alpha-cycle length (ΔCycle, F2B1 − F2; defined as the inverse of mean instantaneous frequency) was positively associated with the increase in fusion threshold across participants (Pearson’s r = .45, p = .008; Figure 2D–E). Thus, participants showing greater auditory-induced alpha-cycle lengthening also showed a larger extension of the temporal integration window.
These changes have been incorporated into the Psychophysical Results, the alpha-frequency Results, and the correlation analysis.
(3) Line 117 - “Our simulation results indicate that the introduction of auditory input resets the phase of alpha oscillations, subsequently extending the temporal window through a reduction in alpha frequency. This modification significantly influences the predictive roles of both phase and frequency.” Here you imply that phase reset is accompanied also by a slowdown of the frequency following the phase reset? Just want to make sure I get this right, and if so it should be more clearly stated.
We thank the reviewer for requesting this clarification. Yes, in our model, the auditory-induced phase reset is accompanied by a transient slowing of instantaneous alpha frequency. The phase reset delays the ongoing phase trajectory and temporarily lengthens the current cycle. Because instantaneous frequency is defined as the local temporal derivative of phase, this perturbation appears as a brief reduction in instantaneous frequency. Importantly, the slowing is time-limited and does not represent a sustained change in trait-like alpha frequency.
We have therefore stated this more clearly in the Results on the phase-resetting model: “In the model, the auditory event delays the ongoing phase trajectory; because instantaneous frequency is the local temporal derivative of phase, this delay temporarily lengthens the current cycle and appears as a brief reduction in instantaneous frequency shortly after the auditory event. The slowing is time-limited, recovering as the trajectory continues, and is distinct from a sustained change in trait-like individual alpha frequency.”
(4) Line 692 - Although reasonable, the sample size (34 and 30 participants, respectively) might turn out to be slightly underpowered in light of a recent meta-analysis on the matter (around 50 participants according to Samaha & Romei, 2024). That is, there might be some chances that weaker and more subtle effects exerted by alpha frequency effects in F2B1 trials have been overshadowed due to an underpowered sample size.
We thank the reviewer for raising this important point. We agree that the sample sizes of the EEG and tACS experiments may have limited sensitivity to small condition-specific effects, particularly in the F2B1 condition. We have therefore interpreted the corresponding null findings cautiously.
In the EEG experiment, the absence of an alpha-frequency difference between one- and two-flash reports in F2B1 was accompanied by a Bayes factor of BBFF<sub>(01)</sub> = 4.88. In the tACS experiment, the principal finding was the stimulation-frequency × sensory-condition interaction rather than the F2B1 contrast considered in isolation; the latter yielded BBFF<sub>(01)</sub> = 5.05. These Bayes factors provide moderate evidence for the null under the present design, but do not exclude smaller effects that may require larger samples to detect. We have therefore revised the Discussion to describe the influence of alpha frequency as reduced in F2B1 relative to F2, rather than concluding that alpha frequency plays no role in the audiovisual condition. We also acknowledge that larger studies using individualized stimulation frequencies would provide a stronger test.
The corresponding interpretation and limitations have been clarified in the Discussion.
(5) Line 717 - 90% accuracy in explicit short trials (30ms ISI)? How did participant bistable ISIs (50% 2-flash report) range between 55–65 ms across modalities then?
Accuracy in the practice/explicit trials was scored against the predominant report (one flash at 30 ms and two flashes at 100 ms), although two physical flashes were always displayed. The condition-specific fusion threshold is instead the fitted ISI at which one- and two-flash reports are equally likely. The two measures answer different questions: the 90% criterion confirms task comprehension at the easy extreme ISIs, whereas the titration locates the point of maximal ambiguity, so there is no contradiction between them.
We have clarified this distinction in the Methods.
(6) Line 723 - For the sake of clarity, it should be outlined what kind of logistic function (along with a brief description of the relative parameters) and fitting algorithm were employed (for both the pretest psychometric procedure and tACS protocols), and whether any constraint to said parameters was applied to allow better fits (higher R<sup>2</sup>). On the same rationale, it would also be helpful to explicitly add the resulting ISIs on each participant's panel (Supplementary Figure 1).
We thank the reviewer for requesting further clarification of the psychometric fitting procedure. Both the pretest and tACS data were fitted using the same two-parameter binomial logistic model. In this model, ββ<sub>0</sub> represents the intercept and ββ<sub>1</sub> represents the change in the log odds of a two-flash report per millisecond. The parameters were estimated by maximum likelihood using MATLAB glmfit, and the fusion threshold was defined as the ISI corresponding to a two-flash probability of 0.5.
No parameter constraints were imposed during fitting. Because the dependent variable consisted of binomial counts, model fitting was based on the binomial likelihood rather than ordinary least-squares R2. We have also added the fitted fusion-threshold ISIs to the corresponding participant panels in Figure 1—figure supplement 1.
We have therefore revised the Methods subsection “Psychophysical pretest and threshold estimation” accordingly.
(7) Line 735 - Germane to what is underlined at 5, the employment of explicit long vs short trials seems to somehow gainsay the concurrent psychometric approach. For instance, to participants displaying narrow vs enlarged temporal window (short vs long ISIs), explicit short trial should turn out to be less (if not) vs more challenging (and vice versa), while the adoption of individually-titrated ISIs rules out such inter-individual perceptual variability, which may jeopardize the way the associated neural effects are interpreted. However, if the authors deem these analyses relevant (and not redundant) to the manuscript, I suggest that they at least move their relative results and charts into the Supplementary Information.
We thank the reviewer for raising this important distinction. We agree that the fixed short- and long-ISI trials were not designed to equate subjective difficulty across participants. Instead, they served as physical-ISI controls: within each fixed-ISI trial type, the visual sequence was identical between F2 and F2B1, allowing us to assess the effect of the auditory input while holding visual timing constant.
By contrast, the individually titrated bistable trials were used for the primary analyses relating neural activity to alternative perceptual outcomes. Because the fusion threshold was estimated separately for each participant and sensory condition, these trials approximately equated perceptual ambiguity and reduced the influence of inter-individual differences in temporal integration.
Following the reviewer’s suggestion, we have clarified the distinction between the fixed-ISI and individually titrated trials in the Results. The fixed-ISI behavioural analyses are presented in Figure 1—figure supplement 3, and the corresponding detailed neural analyses are presented in Figure 2—figure supplement 1.
(8) Line 738–739 - It has not been thoroughly clarified whether, for each trial type (explicit short and long, plus bistable), the same amount of F2 and F2B1 conditions occurred
We thank the reviewer for requesting this clarification. Yes, within each trial type—explicit short-ISI, explicit long-ISI, and individually titrated bistable trials—F2 and F2B1 trials were scheduled in equal numbers. Thus, the two sensory conditions were equally represented within each trial type by design.
Following artifact rejection, the number of retained trials could differ slightly between conditions. All artifact-free trials were retained for the explicit short- and long-ISI analyses, whereas trial counts were matched across the sensory-condition × perceptual-report cells for the primary bistable IAF and POS analyses. We have clarified both the experimental allocation and the subsequent trial-count handling in the Methods.
(9) Line 751–753 - What kind of low-pass and high-pass, or band-pass filters have been used, besides the notch filter? More importantly, at line 738, you have mentioned that the fixation time ranged randomly between 500 and 1500 secs. Such a time window turned out to be the prestimulus interval after trial epoching (since there is no mention of any inter-trial jitter), spanning from −1300ms to stimulus onset. How then have you dealt with trials wherein the fixation time (i.e., to-be prestimulus interval) was < 1300 ms?
We thank the reviewer for raising this concern. We apologize that the original description did not make the complete trial timing sufficiently clear. Following the second flash, each trial contained a fixed 2,000-ms interval. This interval always elapsed in full, regardless of how quickly the participant responded, and the 500–1,500-ms fixation period of the next trial began only after this interval had ended. Thus, the interval between the end of one stimulus sequence and the onset of the next was 2,500–3,500 ms.
Because the EEG data were epoched from −1,300 to 1,000 ms relative to first-flash onset, even the earliest sample of each epoch occurred at least 1,200 ms after the preceding stimulus sequence. Moreover, the observed times were substantially shorter than this interval (condition means of approximately 0.73 s; Figure 1—figure supplement 4), and the observed response-time range confirmed that responses were completed before the next epoch began. Therefore, the extracted epochs did not temporally overlap with either the stimulus presentation or the behavioural of the preceding trial, including on trials with the shortest fixation duration.
Regarding filtering, the only filter applied during initial preprocessing was a 49.5–50.5-Hz bandstop filter; no broadband high-pass, low-pass, or band-pass filter was used. Band-pass filtering was applied only for the analysis-specific extraction of alpha activity (8–13 Hz; least-squares finite impulse filter, forward–reverse).
To make the temporal structure of the paradigm explicit, we have also revised Figure 1B to show the fixed 2,000-ms interval and to clarify that the fixation period of the subsequent trial began only after this interval had elapsed.
(10) Line 758 - On a broader level, it appears that no visual inspection allowing rejection of trials characterized with excessive noise or residual artifacts has been carried out. Does this imply that you retained each and every trial from all participants? On the same vein, no interpolation of a bad channel seems to have been performed.
We thank the reviewer for requesting this clarification. No, we did not retain every recorded trial without inspection. Bad channels were identified for individual participants and interpolated using a weighted average of neighbouring electrodes. Independent component analysis was then used to identify and remove components associated with ocular, muscular, and other stereotyped artifacts. Following ICA, the cleaned data were visually inspected, and trials containing residual artifacts or excessive noise were excluded. We have clarified these preprocessing and artifact-rejection procedures in the revised Methods.
(11) Line 768 - Using a fixed frequency output during the tACS protocol might have been troublesome in many ways. Entrainment-induced shifts to posterior alpha oscillations are known to be maximally effective when tailored around the individual alpha frequency peak (IAF, Cecere et al., 2015; Di Gregorio et al., 2022; Trajkovic et al., 2024). Let's take, for instance, the case of a participant whose on-task oscillatory speed cycled at 12 Hz. In such a case, 8Hz stimulation might have resulted in null effects due to the wide distance between the tACS output and an “optimal” target frequency, which should be ~ 10 or 11 Hz. Conversely, 13 Hz stimulation administered to a participant with an on-task IAF around 9 Hz would not be as beneficial as one delivered at 10 or 11 Hz. These issues, along with a slightly underpowered sample size (see 1), might have yielded null effects with regard to the F2B1 condition.
We thank the reviewer for this important point. We agree that fixed-frequency stimulation does not account for inter-individual variation in alpha frequency and may therefore be less effective than stimulation tailored to each participant’s alpha frequency. Because the tACS experiment was conducted in an independent sample for whom individual alpha-frequency estimates were not available, the two stimulation frequencies were selected to sample the lower and upper portions of the alpha range around the group-level alpha peak. This design allowed us to test whether the effect of stimulation frequency differed between the visual-only and audiovisual conditions, but it did not provide an individualized test of frequency-specific entrainment.
The primary tACS finding was the significant stimulation-frequency × sensory-condition interaction, indicating that stimulation frequency affected fusion thresholds differently in F2 and F2B1. The F2B1 contrast yielded BF<sub>01</sub> = 5.05, providing moderate evidence for the null under the present design; however, this does not exclude smaller effects or effects that may emerge with stimulation tailored to individual alpha frequency. We have acknowledged this limitation and now state that individualized stimulation would provide a stronger test of the role of alpha frequency in audiovisual temporal integration in the revised Discussion.
(12) Line 776 - I reckon that the fitting procedure employed the same logistic function and parameters implemented on data relative to the titration session. This should be specified, and it may be useful to display the fitting curves resulting from this procedure in separate charts (F2 vs F2B1), perhaps in the Supplementary section, akin to what has been done for the fitting curves relative to the titration session (Supplementary Figure 1).
We thank the reviewer for this suggestion. In our reply to Comment 6, we described the psychometric fitting procedure for the pretest in detail; the tACS curves were fitted with the same two-parameter binomial logistic model and 50% threshold definition as the pretest, separately for each participant, stimulation session, and sensory condition. The individual fitted curves are provided in Figure 5—figure supplements 2 and 3.
We have clarified the fitting procedure in the Methods and Results.
(13) Line 779–787 - Many technical details regarding the FFT are missing (what kind of tapering was applied to the data? Zero-padding?). Please add a few explanations to amend this.
We thank the reviewer for requesting these methodological details. For each trial, the power spectrum was computed over the −600 to 600 ms interval using a Hanning taper. The 1.2-s data segments were zero-padded to 10 s, yielding a frequency-bin spacing of 0.1 Hz. We clarify that zero-padding increased the frequency-bin density but did not increase the intrinsic spectral resolution determined by the original data segment. These details have now been added to the Methods.
We have revised the EEG analysis section in the Methods accordingly.
(14) Line 803–807 - Given that in the bistable condition the number of types (1 flash vs 2 flashes) issued by each participant should be roughly the same, I guess something during the psychophysical titration procedure went wrong. However, can the authors articulate a bit further on the specific approach adopted to match the number of trials across type?
We thank the reviewer for raising this point. The fusion threshold was defined as the ISI at which one- and two-flash reports were equally likely. Because this threshold was estimated in a separate psychophysical session, modest deviations from an exactly equal report distribution could arise from trial-to-trial sampling variability and changes in perceptual state between sessions. Nevertheless, the proportions of two- and one-flash reports remained comparable in both the F2 condition (54.8% ± 4.1% versus 45.2% ± 4.1% (mean ± SEM), t<sub>(33)</sub> = 1.18, p = .248, two-tailed, BF<sub>01</sub> = 2.89) and the F2B1 condition (53.8% ± 3.3% versus 46.2% ± 3.3%, t<sub>(33)</sub> = 1.16, p = .255, two-tailed, BF<sub>01</sub> = 2.94; Figure 1E).
To prevent these modest differences in report frequency from affecting the EEG comparisons, artefact-free bistable trials from each participant were divided into four sensory-condition × report cells: F2 with one-flash reports, F2 with two-flash reports, F2B1 with one-flash reports, and F2B1 with two-flash reports. We identified the smallest trial count among these four cells and randomly subsampled each cell to this number. Thus, all four cells contributed an equal number of trials to the primary bistable IAF and POS-map analyses.
We have therefore clarified this in the revised Results and Methods.
(15) Line 829 - Comment 13 applies to the POS analyses as well.
Thank you for identifying that the POS method needed a more transparent account. We introduce the complex time-frequency coefficient, normalize it to a unit phase vector, define ITC for each report group and their pooled trials, and then define POS as ITC (one flash) + ITC (two flashes) − 2 × ITC (pooled). A positive POS therefore requires the two report groups to be phase concentrated around different angles; it is not merely a larger phase-locking value. The inferential test permutes report labels within participant while preserving group sizes and applies the cluster procedure to the resulting POS maps.
We thank the reviewer for pointing this out. Unlike the FFT analysis described in to Comment 13, the POS analysis was based on wavelet time–frequency decomposition; therefore, no separate taper was applied. Specifically, complex time–frequency coefficients were obtained using FieldTrip with wavelets whose number of cycles increased logarithmically from 2 at the lowest frequency to 7 at the highest frequency. The analysis included 60 logarithmically spaced frequencies from 2 to 50 Hz, evaluated from −600 to 400 ms in 20-ms steps, with zero-padding to 10 s. The resulting complex coefficients were normalized to unit phase vectors and used to calculate POS. These methodological details have now been clarified in the Methods.
We have revised the POS analysis subsection accordingly.
(16) Line 859–870 - This is a suggestion rather than a comment, but I would appreciate the information about the POS statistics to be moved into the “statistical analyses” section. In doing so, I believe they would improve the overall clarity of the analysis pipeline.
We thank the reviewer for this helpful suggestion. As recommended, we have moved the POS-specific inferential procedures, including label permutation, pointwise significance estimation, cluster correction, and the direct F2B1−F2 comparison, to the Statistical analyses section. The Alpha oscillation analysis subsection now focuses on the time–frequency decomposition and definition of POS. This reorganization separates the computation of POS from its statistical inference and clarifies the overall analysis pipeline.
We have revised the Statistical analyses section accordingly.
(17) Line 872 - All the information regarding the statistics adopted to test the behavioural data is missing. Although pretty much intuitive, adding a few lines that specify whether any normality check was performed, and what kind of t-tests and correlation metrics were employed, would greatly benefit the quality of the manuscript from a formal standpoint.
We thank the reviewer for this helpful suggestion. We have expanded the Statistical analyses section to clarify the procedures used for the behavioural data. Factorial comparisons were evaluated using repeated-measures ANOVAs, whereas pairwise comparisons used two-tailed paired-samples t-tests unless a directional contrast had been specified a priori. Before applying parametric pairwise tests, the corresponding within-participant difference scores were assessed using Shapiro–Wilk tests together with Q–Q plots. When normality was rejected, the parametric result was supplemented with a Wilcoxon signed-rank test and a bias-corrected bootstrap confidence interval. Between-participant associations were assessed using Pearson’s r. We also clarify that this normality screening was not applied to permutation, circular, or cluster-based analyses, whose inference does not rely on the same parametric normality assumption.
We have revised the Statistical analyses section accordingly.
(18) Line 887 - Given the relevance the computational model retains, I would add a detailed explanation of the steps performed to build it (i.e., those nicely rendered in Supplementary Figure 8), the parameters involved in the equations, as well as the rationale behind them. For instance, why have you opted for normally-distributed noise (line 893)? Why was the phase delay set to be centred around 25 ms (with ± 25 ms random variability, line 900)? Further, it would perhaps be interesting to explore the parameters space, in order to compare, for instance, what kind of outcome the simulation produces as the frequency of these synthetic alpha oscillations changes (i.e. 8, 10 and 12 Hz, thereby incorporating widely known interindividual differences relative to the IAF), not to mention the phase delay.
We thank the reviewer for this constructive suggestion. We have substantially expanded the description of the computational model to clarify its construction, the role of each model component, and the procedure used to derive the simulated perceptual outcomes. In particular, we now distinguish the generation of the underlying oscillatory signal, the introduction of the auditory perturbation, the assignment of the latent perceptual outcome, and the phase-dependent reliability of the simulated report. The complete model workflow is illustrated in Figure 8—figure supplement 1.
We also clarify that the independent, zero-mean Gaussian innovation was used as a simple neutral representation of stochastic variability, without introducing a systematic temporal drift. The temporal jitter and phase-shift parameters were intended as phenomenological representations of variability in the timing and magnitude of the auditory perturbation, rather than as precise estimates of a physiological auditory latency.
Finally, following the reviewer’s suggestion, we conducted sensitivity analyses across a range of oscillator frequencies and perturbation delays while holding the remainder of the model pipeline constant. The frequency-sensitivity results are presented in Figure 8—figure supplement 3, and the delay-sensitivity results are presented in Figure 8—figure supplement 4. These analyses characterize how the simulated outcomes vary across parameter settings and show that the principal model behavior is not restricted to a single arbitrary parameter choice.
We have expanded the Simulations of EEG data subsection accordingly and added the model workflow and parameter-sensitivity results to Figure 8—figure supplements 1, 3, and 4.
(19) Line 909 - The authors need to emphasize a bit more the conceptual difference between perceptual outcome (alpha frequency) and perceptual clarity (alpha phase). Along this line of reasoning, the model provides that the phase at which the second flash occurs should dictate the higher vs lower probability of issuing an incorrect response, regardless of whether the “synthetic” outcome hits 1 vs 2 flashes. If so, this needs to be clearly stated in the manuscript.
We thank the reviewer for highlighting this important conceptual distinction. In the model, alpha frequency determines the latent perceptual outcome by determining whether the two flashes fall within the same or different alpha cycle. By contrast, the phase at which the second flash occurs does not change this latent outcome; instead, it determines how reliably the latent outcome is translated into the simulated report.
Importantly, this phase-dependent reliability applies symmetrically to both latent outcomes. An unfavorable phase increases the probability that the reported does not match the latent cycle-based outcome, regardless of whether that outcome is one flash or two flashes. Thus, frequency determines perceptual outcome, whereas phase determines perceptual clarity rather than favoring a particular category. This distinction is now explicitly stated in the Results and simulation Methods and is illustrated in the model workflow (Figure 6 and Figure 8—figure supplement 1).
We have revised the Results section on the phase-resetting model and the Simulations of EEG data subsection.
(20) Line 919 - The approach through which Hit Rates and False Alarms are defined is quite convoluted and a bit detached from the formal assumptions of signal detection theory. If the overall scope of this analysis was highlighting a link between subjective perception and reported outcome, the authors might very well compute subjective Hits and False Alarms, and then employ their ratio without assuming an equal-variance scenario. Plus, I would rather avoid using the term d', which I feel is somehow misleading in this context.
We thank the reviewer for pointing out that the original signal-detection terminology could be misleading. We agree that the conventional notation d' may imply an empirical estimate of participants’ perceptual sensitivity under the assumptions of standard signal detection theory, which was not the purpose of this model-based analysis.
In the simulation, the model-defined latent one-flash and two-flash states provide the reference categories, and the simulated one-flash and two-flash reports provide the corresponding categories. We therefore define the hit rate as the proportion of latent two-flash trials reported as two flashes and the false-alarm rate as the proportion of latent one-flash trials reported as two flashes. The standardized difference between these two rates is used only to summarize how reliably simulated reports discriminate the model-defined latent states.
To avoid implying a conventional behavioural d', we have renamed this quantity the model-based discriminability index, denoted DD<sub>mmmmmmmmmm</sub>, throughout the manuscript. This index should not be interpreted as an estimate of participants’ perceptual sensitivity, criterion, or underlying equal-variance sensory distributions. This terminological revision does not alter the calculation or conclusions of the simulation. The corresponding labels have also been updated in Figure 8F and Figure 8—figure supplement 4.
We have revised the Simulations of EEG data subsection accordingly, together with the corresponding equation, figure labels, and legends.
(21) Line 157 - “In the main EEG experiment, each condition comprised three types of trials: the explicit short-ISI trials (30 ms, typically reported as one flash), the explicit long-ISI trials (100 ms, typically reported as two flashes)”. However, in the Methods section (lines 716–717) there is no mention of short vs long explicit trials differing in terms of number of flashed displayed, implying that 2 flashes were always emitted [.. prior to the psychophysical pretest, participants completed a practice block consisting solely of explicit short (30 ms) and long trials (100 ms) until accuracy reached at least 90%..], in line also with lines 737–741 [..Each trial began with a central fixation lasting 500 to 1500 ms, followed by a 10 ms presentation of the first visual stimulus, accompanied by an auditory beep or not. After a variable ISI (30 ms, 100 ms, or the participant's individual fusion threshold), the second frame was displayed for 10 ms,.], and Figures 1A and B. This point should be promptly addressed (see also 5 within the “Methods” comments), as it is hard to reconcile around 90% accuracy rates in explicit short trials wherein 2-flashes were always displayed, with bistable ISIs (50% accuracy rates) centred around 55 - 65ms.
We thank the reviewer for identifying this ambiguity. Two physical flashes were presented in every trial; the labels “short” and “long” refer exclusively to the ISI between the two flashes, rather than to the number of physical flashes presented. At the short ISI, the two flashes were typically integrated and reported as one flash, whereas at the long ISI they were typically resolved and reported as two flashes.
Accordingly, accuracy in the explicit trials was operationally defined relative to the predominant percept expected at each ISI: a one-flash report was scored as correct for the explicit short-ISI trials, whereas a two-flash report was scored as correct for the explicit long-ISI trials. This explains why accuracy could approach 90% even though two physical flashes were presented in both trial types. In contrast, the bistable trials used each participant’s fusion-threshold ISI, at which one- and two-flash reports were approximately equally likely.
We have therefore revised the psychophysical Results and clarified the physical stimulus sequence and operational definition of accuracy in the psychophysical Methods.
(22) Line 162 - Stating that 1 vs 2 flash reports were comparable across modalities (F2 vs F2B1) in the bistable condition is somehow misleading, as both t-tests proved to be marginally significant (all p-values < .075), suggesting a subtle trend that should be accounted for when interpreting the results. That is, participants appear to more often report 2 flashes, rather than 1. Approaching this via Bayesian t-tests might help the reader in understanding how actually comparable trials were in terms of perceptual ambiguity. For the sake of clarity, it would also be useful to add means and S.E.M. for each condition across sensory modality in the main text, as well as change Figure 1E into a double raincloud plot (with mean point and S.E.M. error bars), similar to that in Figure 1D. Related to the above, looking at Figure 1E, it is not clear what the y-axis stands for by saying percentage of percepts. Do you mean percentage of 2-flash percept? This should be clarified. It clearly seems that the two conditions are not completely balanced even in ambiguous trials. And I wonder whether the veridical 1 flash condition could be used as a catch trial for computing d prime and criterion measures to test for the impact of sensitivity and bias in this type of effect.
We thank the reviewer for raising these points. During revision, we recalculated the bistable-report proportions using the actual number of valid trials retained for each participant and condition. Reinspection of the raw log files revealed that the trial counts used in the initial analysis did not match the actual valid-trial counts for a number of participants: the first nine participants had completed 520 rather than 560 trials (fewer bistable trials per condition), and for two further participants, whose sessions had been interrupted and split across log files, the counts included missed trials. We apologize for this counting error. In the revised analysis, two-flash reports were numerically more frequent than one-flash reports, but the imbalance was not statistically reliable in either F2 (54.8% ± 4.1% versus 45.2% ± 4.1% (mean ± SEM), t<sub>(33)</sub> = 1.18, p = .248, two-tailed, BF<sub>01</sub> = 2.89) or F2B1 (53.8% ± 3.3% versus 46.2% ± 3.3%, t<sub>(33)</sub> = 1.16, p = .255, two-tailed, BF<sub>01</sub> = 2.94; Figure 1E). The Bayes factors modestly favored the null hypothesis over the presence of a systematic report imbalance. Moreover, the percentage of two-flash reports did not differ between F2 and F2B1, t<sub>(33)</sub> = 0.21, p = .834. We have therefore revised the text to describe the report proportions as approximately, rather than completely, balanced.
The requested means and SEMs are now reported in the main text. We retained the paired distribution plot in Figure 1E because it displays all participant-level observations, their within-participant pairing, and the distribution summary for each report category. However, we clarified the y-axis and figure legend to indicate that the values represent the percentage of valid bistable trials assigned to each perceptual report.
A conventional behavioural d' and criterion analysis cannot be calculated from this experiment because every physical trial contained two flashes. In particular, the explicit short-ISI trials were not veridical one-flash catch trials; they also contained two physical flashes that were typically fused into a one-flash percept. Consequently, there is no physically defined signal-absent category from which standard hit and false-alarm rates could be constructed. The separate model-based discriminability index uses model-defined latent states and should not be interpreted as a behavioural d'.
We have revised the psychophysical Results, clarified the physical stimulus sequence in the psychophysical Methods, and revised Figure 1E and its legend accordingly.
(23) Line 168 - Can the authors report the mean Hz of such a clear peak (along with the associated S.E.M)?
The mean participant-level alpha peak was 10.12 ± 0.24 Hz (mean ± SEM), obtained as the 8–13 Hz maximum of each participant's trial-averaged FFT spectrum.
We have therefore revised the Results.
(24) Line 174 -“Building upon our behavioral observations, we noted a significant extension in the temporal window for visual integration when auditory input was introduced.” Germane to point 1 within the “Introduction” comments, I see the authors use this concept of extended temporal window of integration without describing what it means. I think this should be defined clearly. The authors may define it as the proportion of time within which the fusion effect takes place by inducing the participants to report one visual flash when in fact two flashes were presented. In the two-flash conditions, this window seems to last much less than in the two-flash one-beep condition. So, I suggest that the authors explicitly define what they mean by temporal window of integration (period where the fusion takes place).
We thank the reviewer for requesting a clearer definition. In the present study, the temporal window of integration refers to the range of ISIs over which two physically presented flashes tend to be integrated and reported as a single flash. We operationalized the boundary of this window as the fusion threshold—the ISI at which one- and two-flash reports were equally likely, as estimated from the psychometric curve.
Accordingly, a rightward shift of the fusion threshold indicates that fusion remains likely over longer temporal separations between the two flashes and therefore reflects an extended temporal integration window. This operational definition and the corresponding threshold estimates are illustrated in Figure 1C–D and Figure 1—figure supplement 1.
We have clarified this definition in the Psychophysical Results.
(25) Line 176–178 - “If we assume that alpha frequency serves as an indicator of the temporal window within the visual cortex, it is plausible to hypothesize that alpha frequency in the F2B1 condition might decrease compared to the F2 condition.” Or that a phase reset takes place without calling alpha frequency into account. As a matter of fact, phase reset may be the mechanism by which integration is prolonged, and considering this as a slowed alpha frequency may be an artefact, unless you demonstrate that it is more sustained in time than just the period around the sound is played. The authors use instantaneous alpha frequency, which may be, paradoxically, less sensitive to sustained effects and read change in phase as a change in frequency. Unless one says that a change in phase is by definition a change in frequency, and the fact that it is induced by an external stimulus, doesn't diminish the fact that it results in a slowing down of the ongoing alpha frequency. My question is rather whether this effect is evoked by the stimulus and ends with the stimulus or whether it reverberates over a few cycles, which would make it more of an oscillation and less of an evoked to the external stimulus. I wonder whether the effect would still be there for longer time windows or by using a more classical FFT over a longer time window post-stimulus? Distinguishing between these two conditions could tell us more about the effects found here of a lack of correlation between IAF and F2B1, which may have to do with stimulus-evoked phase modulation rather than the slowing down of IAF. This does not diminish the impact of IAF on time integration, as it clearly appears in more sustained conditions, such as the 2F for example, but doesn't account for the fusion illusion when the auditory input is presented. This is intriguing, as previous research has also attempted to find a relationship between the auditory-induced fusion effect and IAF with no success. However, it should be mentioned that work by Noguchi has recently shown that the change in the beta frequency may account for this effect. Maybe the authors may want to comment on this and I wonder whether they might test whether changes in the beta band frequency may alternatively explain the effects?
We thank the reviewer for raising this important distinction. Instantaneous alpha frequency was calculated from the local temporal derivative of the unwrapped phase. Consequently, a stimulus-induced phase reset can manifest as a transient reduction in instantaneous frequency. We have therefore clarified that the present finding reflects a transient poststimulus slowing of alpha-phase progression, rather than a sustained or trait-like change in individual alpha frequency. The difference between F2B1 and F2 was detected during the 0–280-ms poststimulus interval and was not evident beyond this interval (Figure 2B), consistent with a time-limited perturbation spanning a few alpha cycles.
As a complementary analysis, we estimated peak alpha frequency using a conventional FFT over the poststimulus interval. This analysis also showed a lower alpha peak in F2B1 than in F2 (Figure 2—figure supplement 2A). However, because the FFT summarizes spectral content across the analysis window, it cannot by itself distinguish a sustained change in the underlying oscillator frequency from a transient phase perturbation. We therefore treat this result as convergent evidence for an alpha-frequency difference during the poststimulus interval, rather than as evidence for a lasting frequency change. The accompanying increase in intertrial phase coherence without a corresponding increase in alpha power is also consistent with stimulus-induced phase reorganization rather than a simple additive evoked (Figure 7A, C).
We also agree that alpha may not be the only frequency mechanism contributing to audiovisual fusion. In particular, Noguchi (2022) reported that lower prestimulus beta frequency was associated with greater susceptibility to audiovisual fusion. We now discuss this finding as a potentially complementary beta-band timing mechanism when auditory input contributes to fusion. A systematic beta-band analysis would require a separate set of beta-focused hypotheses and validation analyses and is therefore beyond the alpha-focused scope of the present study. We have identified this as an important direction for future work rather than implying that the observed effect is exclusively mediated by alpha activity.
Corresponding revisions have been made in the Results section and the Discussion section. The complementary FFT analysis is presented in Figure 2—figure supplement 2A.
(26) Line 180 - It is still not entirely clear to me the reason why you need to ensure an equal number of trials in each condition (F2 vs F2B1), since this number should already be as such (see 6 within the “Methods” comments).
We thank the reviewer for highlighting the need to clarify this distinction. F2 and F2B1 trials were indeed scheduled in equal numbers within each trial type. However, the relevant EEG analyses were performed after artifact rejection and, for the bistable trials, after further separating trials according to one-flash and two-flash reports. Consequently, the numbers of valid trials could differ across the four sensory-condition × report cells, even though the two sensory conditions had been equally represented in the original design.
Trial-number matching was therefore not intended to correct an imbalance in the experimental design. Rather, it ensured that the F2–F2B1 comparisons were not influenced by differences in perceptual-report composition or by trial-count-dependent differences in the precision of the neural estimates, particularly the POS/ITC measures. We have revised the Methods to make clear that this matching was applied specifically to the primary bistable IAF and POS-map analyses.
The relevant experimental-design information is provided in the EEG experimental procedures, and the trial-matching procedure is described in the Recording and preprocessing subsection. The corresponding IAF comparison is reported in the Results.
(27) Line 194 - The correlation results seem pretty robust. However, upon inspecting the psychometric curves at Supplementary Figure 1, I wonder whether the same pattern of results holds when removing a few participants displaying too huge (and not much plausible) ISI differences across modalities (e.g., sub03, sub08, sub11, sub18).
We thank the reviewer for this helpful suggestion. We performed the requested sensitivity analysis by excluding sub03, sub08, sub11, and sub18. The correlation between the auditory-induced change in poststimulus alpha-cycle length and the change in fusion threshold was attenuated and was no longer statistically significant after their exclusion (r = .21, p = .271, n = 30; full sample: r = .45, p = .008, n = 34).
We have reported this result transparently, but we did not adopt this exclusion for the primary analysis. These participants were identified on the basis of relatively large F2B1−F2 fusion-threshold differences, which constitute the behavioural variable being correlated. In the absence of an independent indication that their data were invalid, excluding participants according to the magnitude of this variable would selectively remove the upper end of its distribution and impose range restriction.
We therefore assessed the influence of individual observations using complementary procedures that retained the full sample. The full-sample correlation remained significant in a permutation test (p = .006) and had a bootstrap 95% confidence interval that excluded zero [.08, .68]. A bisquare robust regression, which down-weighted observations deviating from the overall trend, also showed a positive association (slope = 4.30, p = .033). In addition, leave-one-participant-out correlations were positive in all 34 iterations (r = .29–.50) and remained significant in 33 of them; only the exclusion of sub18 produced a non-significant result (Figure 2—figure supplement 3). Thus, although the association is attenuated when the four participants with the largest behavioural differences are jointly removed, it is not attributable to any single participant.
The robustness analyses are reported in the Results and Figure 2—figure supplement 3.
(28) Line 211 - The results hereby reported aligns with those relative to bistable trials, but I suggest the authors to perform a few more correlation analyses (which may eventually be added to the Supplementary section) relating the differences in accuracy rates between F2B1 vs F2 (∆Accuracy F2B1-F2, in %) to those in alpha cycle length (∆Cycle Lengths F2B1-F2, in ms) per each trial type (explicit long vs short). This is also in light of an interesting trend toward a double dissociation across trial types and sensory modality in terms of accuracy rates (see lines 158–159), which has not been further investigated nor graphically depicted.
We thank the reviewer for this suggestion. We performed the requested between-participant correlation analyses separately for the explicit short- and long-ISI trials. The auditory-induced change in accuracy (ΔAccuracy, F2B1 − F2) was not significantly associated with the auditory-induced change in poststimulus alpha-cycle length (ΔCycle length, F2B1 − F2) at either the short ISI (r = -.01, p = .946) or the long ISI (r = -.08, p = .671; n = 34). These correlations are now shown in Figure 1—figure supplement 3B–C, together with the explicit-trial accuracy results in Figure 1—figure supplement 3A.
We agree that the accuracy interaction warrants clarification. We do not interpret it as evidence for a double dissociation involving two independent auditory effects. Rather, the auditory beep shifted perception in the same direction—toward fusion—at both ISIs. At the short ISI, where a one-flash report was scored as correct, this shift increased accuracy; at the long ISI, where a two-flash report was scored as correct, the same shift reduced accuracy. Thus, the opposite directions in the accuracy measure can arise from a single fusion-directed effect because the expected differs between the two ISIs.
The absence of significant correlations indicates that we found no evidence that individual differences in the auditory-induced accuracy changes at the fixed ISIs covaried with changes in poststimulus alpha-cycle length. Because performance in these explicit conditions was generally close to the respective behavioural extremes, we interpret these null correlations cautiously. By contrast, in the bistable condition, the more sensitive fusion-threshold measure was associated with the auditory-induced change in alpha-cycle length.
The fixed-ISI behavioural pattern is summarized in the Results. The accuracy interaction and the additional correlation analyses are reported in the Supplementary Results subsection “Explicit-trial accuracy” and Figure 1—figure supplement 3A–C.
(29) Line 216 - To broadly summarize, instantaneous frequency estimation yielded the same pattern of results across different trial types, i.e., a post-stimulus frequency decrease in F2B1 trials, as compared to F2 trials. The authors construe this oscillatory slowdown as a transient elongation of the ongoing alpha cycle, engendered by auditory-induced phase-reset mechanisms. As far as I agree with such interpretation, I do believe there is more to speculate about. Specifically, there is no mention or remark commenting on the post-stimulus significant windows length (e.g. 0-180ms, 0280ms, 0-370ms) being somehow intertwined with the ISI duration. That is, the larger the ISIs, the longer the time window in which the IAF appears to significantly differ between conditions (F2B1 vs F2), depicting an underexplored scenario where auditory-triggered phase-reset mechanisms may only partially contribute to the alpha frequency decrease (i.e. cycle “elongation”), perhaps along with an additional role putatively played by flash-induced phase resetting dynamics.
We thank the reviewer for this insightful observation. We agree that the progressively longer significant F2B1−F2 intervals should be reported descriptively rather than interpreted as evidence that the auditory–visual interaction itself lengthens with ISI. We now state that the temporal extent of a significant cluster depends on the magnitude and variability of the condition difference and on the statistical threshold.
Because F2 and F2B1 contained identical visual sequences within each ISI, the F2B1−F2 contrast controls for the direct visual-sequence effect while retaining the beep contribution. The contrast therefore identifies the interval over which the two conditions are statistically distinguishable; how that interval relates to the duration of phase reorganization remains uncertain.
We revised the Discussion accordingly and removed the mechanistic explanation that the significant window should lengthen because the later second flash interacts with the auditory perturbation.
The relevant empirical results are reported in the Results and Figure 2—figure supplement 1A– C. The interpretation of the cluster durations has been revised in the Discussion, and the limitation concerning visual-stimulus-induced resetting is stated in the Discussion.
(30) Lines 235–250 - The results hereby reported are quite straightforward, although I can't help but wonder whether we should witness the same patterns when comparing 1 vs 2 flashes report in explicit long and explicit short trials (perhaps via the counterbalancing approach mentioned at lines 803–805, to match the different number of trials per each report type).
We thank the reviewer for this suggestion. We considered performing the corresponding one-flash versus two-flash report comparisons in the explicit short- and long-ISI trials. However, the non-predominant report was rare in these conditions and was entirely absent for some participants. Trial-number matching can control unequal group sizes when both report categories contain sufficient trials, but it cannot recover a report category that is absent. Moreover, matching the two report categories to the small number of non-predominant reports would discard most of the available trials and produce unstable participant-level neural estimates.
Such an analysis would also require excluding participants who never produced the non-predominant report, leaving a selected subset of participants for whom the explicit trials were relatively ambiguous. The resulting comparison would therefore differ systematically from the full-sample, within-participant analysis used for the bistable trials.
We consequently retained the report-specific IAF comparison for the individually titrated bistable trials, which were designed to provide sufficient numbers of both perceptual outcomes. The explicit short- and long-ISI trials instead serve as physical-ISI controls and are analyzed according to sensory condition and ISI. We believe that presenting an underpowered and selectively sampled report-specific analysis of the explicit trials would be less informative than clearly explaining why it was not performed.
The role of the explicit trials as physical-ISI controls is described in the Results, and the trial number matching procedure for the primary bistable analyses is described in the Recording and preprocessing subsection.
(31) Lines 260–261 - What kind of statistical correction has been implemented for the post-hoc tests?
Thank you for requesting this clarification. The two condition-specific follow-up comparisons— one-flash versus two-flash reports within F2 and within F2B1—were treated as a single family and corrected using the Benjamini–Hochberg false-discovery-rate procedure at q = .05. Both comparisons were evaluated using two-tailed paired-samples t-tests.
In F2, instantaneous alpha frequency was higher for two-flash than for one-flash reports (t<sub>(33)</sub> = 3.11, uncorrected p = .004, FDR-corrected p = .008). In F2B1, the corresponding comparison was not significant (t<sub>(33)</sub> = −0.49, uncorrected p = .630, FDR-corrected p = .630). We now report both the uncorrected and FDR-adjusted values in the Results and specify in the Figure 3 caption that the within-condition follow-up comparisons use FDR-adjusted two-tailed paired tests, whereas the interaction uses a repeated-measures ANOVA with an uncorrected p-value.
The Results report both uncorrected and FDR-adjusted values, the general correction procedure is specified in the Statistical analyses subsection, and the Figure 3 caption distinguishes the repeated-measures ANOVA interaction from the FDR-adjusted two-tailed paired comparisons within conditions.
(32) Line 265 - I believe a raincloud plot would be a better graphical option for Figure 3C.
We thank the reviewer for this helpful suggestion. We agree that the revised panel should show the participant-level distribution rather than only a group summary. Figure 3C therefore displays every participant, the within-participant pairing, the median and interquartile range, the non-outlier range, and the mean. We retained this paired box-and-dot presentation rather than adding a kernel-density layer because the central comparison is within participant and the sample comprises 34 paired observations. The revised legend now describes each distributional element explicitly.
(33) Line 283 - Phase-based measures are known to be more prone than other EEG metrics to temporal smearing. That is because computing the oscillatory phase at a given time-point via wavelet decomposition ends up collapsing into said time-point electrophysiological information gathered all along the kernel, which might be hundreds of milliseconds long at lower frequencies. This means that the oscillatory phase at a prestimulus time-point within the low-frequency range might also contain information relative to post-stimulus time-points (see Williams et al., 2024, Curr Bio). Have the authors addressed and/or factored in this issue?
We thank the reviewer for raising the issue of temporal smearing in phase-based analyses. To address this concern, we repeated the complete phase-opposition analysis using one-cycle wavelets, which provide substantially improved temporal resolution. We additionally plotted the frequency-specific half-cycle boundary to identify estimates whose wavelet support could extend beyond stimulus onset (Figure 4—figure supplement 1).
The one-cycle maps showed a similar prestimulus F2B1 alpha-band pattern without a comparable F2 pattern. This control reduces concern that the result was driven solely by wavelet support extending beyond stimulus onset. Because no cluster-level inference was applied to the one-cycle control, we use it as a descriptive temporal-smearing check rather than as an independent significance test.
(34) Line 297–304 - Have the authors employed linear statistical tests or circular statistical tests (e.g., Watson-Williams, etc)?
We thank the reviewer for requesting this clarification. Circular rather than linear statistics were used to analyse the phase-direction data. For each participant, the circular mean phase direction was calculated separately for one-flash and two-flash reports. The resulting distributions of participant-level mean directions were then compared using the Watson–Williams test. We have clarified the statistical details in the revised Results and Methods and in the Figure 4 legend.
(35) Line 325 - Using circular statistics, rather than looking for quadratic effects via standard ANOVA, may turn out to be a better way to address the experimental question the authors are asking.
We thank the reviewer for this important suggestion. We agree that circular statistics are appropriate when the inferential variable is the raw phase direction. Accordingly, as clarified in our to Comment 34, participant-level mean phase directions for one-flash and two-flash reports were compared using the Watson–Williams circular test.
The quadratic contrast addresses a different aspect of the phase–percept relationship. After each participant’s phase profile was circularly aligned to their preferred phase, the dependent variable was the proportion of two-flash reports across bins of relative phase distance, rather than a set of raw angular observations. A Watson–Williams test is therefore not applicable to this aligned response-probability profile. The quadratic contrast was used to characterize whether the probability declined as phase moved away from the participant-specific preferred phase.
Nevertheless, to ensure that the conclusion did not depend on either the alignment procedure or the assumed quadratic profile, we added a complementary non-aligned analysis. For each participant and sensory condition, we quantified the divergence of the complete phase-profile from uniformity using Kullback–Leibler divergence and standardized the result against a participant-specific response-label permutation distribution. Phase-dependent modulation was significant in F2B1 (permutation p = .009) but not in F2 (permutation p = .819), and modulation was significantly stronger in F2B1 than in F2 (paired permutation p = .014; Figure 4—figure supplement 3). We now state this alongside the POS permutation procedure in Statistical analyses: KL z scores were tested against zero with right-tailed sign-flip permutations within each condition, and the F2B1−F2 difference was tested with a two-tailed paired sign-flip permutation.
Thus, the conclusion is supported both by circular analysis of the original phase directions and by a non-aligned permutation analysis that does not assume a common preferred phase or a quadratic profile. We have clarified the respective roles of these analyses in the revised manuscript.
(36) Line 362 - Would it be possible for the authors to provide (perhaps as additional figures in the supplementary materials) each participant's psychometric curves resulting from the different tACS protocols and conditions?
We thank the reviewer for this suggestion. Participant-level psychometric curves for all participants are provided in Figure 5—figure supplement 2 (F2) and 3 (F2B1), showing the observed and fitted responses under the 13 Hz, 8 Hz, and sham conditions.
(37) Lines 377 - Issues raised at 31 apply to these post-hoc tests as well.
We thank the reviewer for raising this point. The two planned condition-specific comparisons between 8 Hz and 13 Hz stimulation were treated as one family and corrected using the Benjamini– Hochberg FDR procedure at q = .05. Both uncorrected and corrected p values are now reported (F2: p = .023, FDR-corrected p = .045; F2B1: p = .578, FDR-corrected p = .578). Because the interaction difference scores were not normally distributed, we additionally confirmed the interaction using a Wilcoxon signed-rank test and a bootstrap confidence interval. We have clarified these procedures in the revised Results and Methods.
(38) Lines 420–421 - Keeping in mind the results shown in Figure 2 (B, D, E) and remarks at 29, the choice of modelling the data without accounting for any flash-induced phase-reset mechanism might be the main limitation of the approach hereby implemented. I wonder whether it might be feasible for the authors to update the model accordingly, and simulate not only bistable trials, but also explicit short and long ones.
We thank the reviewer for this important suggestion. We agree that a visual-stimulus-induced phase reset could contribute to the absolute oscillatory dynamics. Because the visual stimuli were identical in F2 and F2B1, the present model was designed to isolate the additional perturbation produced by the auditory input. This simplified account assumes that any shared visual reset contributes similarly to both conditions; possible non-additive interactions between visual- and auditory-induced resets are not captured and represent an important direction for extending the model.
We also clarify that the model already simulated all eight ISIs from 30 to 100 ms, including the explicit short- and long-ISI trials, as shown by the simulated psychometric curves in Figure 8A. The report-dependent frequency and phase analyses were performed at the condition-specific fusion threshold because the explicit trials produced near-floor or near-ceiling distributions and therefore provided too few trials from both perceptual categories for stable within-condition comparisons.
We have clarified these points in the revised Methods.
(39) Lines 451 - For visualization purposes, it would be interesting to plot time-resolved simulated IAFs (from −600 to 600 ms), beside time-collapsed IAFs (Figure 7C).
We thank the reviewer for this suggestion. We have added time-resolved simulated IAF traces from −600 to 600 ms for one- and two-flash percepts in both F2 and F2B1 (Figure 8—figure supplement 2). The traces show a transient decrease in simulated IAF around stimulus onset in F2B1, followed by recovery within approximately 200 ms, complementing the time-collapsed results.
(40) Lines 457 - Based on what the authors mentioned, a POS analysis on synthetic data was performed. However, beside the permutation histogram (Figure 7D), nothing more about it from a quantitative standpoint has been reported. Plus, such analysis seems to have been run on data at stimulus onset (line 483), while POS significant differences uncovered in the empirical dataset are associated with a prestimulus (earlier) time window. This is a critical point suggesting how the model, although insightful, struggles in capturing some of the core patterns embedded within the empirical data. A possible way to shed some further light on the issue would be plotting the simulated time-resolved phase-based metrics (i.e., ITC, Supplementary Figure 7) from −600ms to 600ms, as a function not only of sensory modality (F2B1 vs F2), but also the number of flashes reported (1 vs 2). As long as some kind of difference emerges over the prestimulus time window between the 1 vs 2 flash reports relative to F2B1 trials only, it could be stated that the model simulates quite faithfully the predictive role of prestimulus alpha phase in audiovisual trials (i.e., as uncovered in the empirical dataset).
We thank the reviewer for this important suggestion. To address this concern, we performed time-resolved phase-opposition analyses separately for F2B1 and F2 after balancing the numbers of one- and two-flash trials. We applied the same analysis pipeline and time–frequency parameters as in the empirical analysis, with 100,000 response-label permutations for the simulated POS analysis. The resulting time–frequency p-value maps are presented in Figure 8—figure supplement 5. The simulated F2B1–F2 POS difference at stimulus onset also exceeded the 97.5th percentile of the permutation distribution (Figure 8D).
The time-resolved analysis showed report-dependent phase opposition around stimulus onset in both conditions, with a stronger effect in F2B1. Thus, the model captures the relative enhancement of phase-dependent perceptual modulation in F2B1. However, it does not reproduce the empirical finding of significant phase opposition only in F2B1 or its earlier prestimulus timing. We now state this limitation explicitly and describe the model as a qualitative account of condition-dependent phase sensitivity rather than an exact reproduction of the empirical temporal POS pattern.
We have revised the simulated phase-analysis Results and Methods accordingly.
(41) Line 622 - Concerning the interpretations of a reconciliation with Buergess and Noppeney, I disagree on the extent that while they might have found the same null findings as in this work concerning the relationship between IAF and fusion effect, this is not the case for the sound-induced flash illusion. Other factors may play a role, notably the number of participants employed, the details of the experimental design, and as more in detail described in the meta-analysis by Samaha and Romei 2024.
We thank the reviewer for highlighting the limits of this comparison. We agree that our original use of “reconciles” was too strong. The distinction between fusion threshold and two-flash discrimination sensitivity may provide one explanation for the difference from Buergers and Noppeney (2022), but it cannot fully account for the divergent findings across audiovisual paradigms. Differences in sample size, stimulus and task design, psychometric measures, and IAF estimation may also contribute, as discussed by Samaha and Romei (2024). We have therefore revised the Discussion to present our model-based interpretation as one possible explanation specific to the present two-flash fusion paradigm.
We have revised the Discussion accordingly.
Reviewer #2 (Public review):
Summary:
The authors used a visual flash discrimination task in which two flashes are presented one after another with different inter-stimulus intervals. Participants either perceive one flash or two flashes. The authors show that the simultaneous presence of an auditory input extends the temporal window of integration, meaning that two flashes presented shortly after one another are more likely to be perceived as a single flash. Auditory inputs are accompanied by a reduction in alpha frequency over visual areas. Prestimulus alpha frequency predicts perceptual outcomes in the absence of auditory stimuli, whereas prestimulus alpha phase becomes the dominant predictor when auditory input is present. A computational model based on phase-resetting theory supports these findings. Additionally, a transcranial stimulation experiment confirms the causal role of alpha frequency in unimodal visual perception but not in cross-modal contexts.
Strengths:
The authors elegantly combined several approaches-from behavior to computational modeling and EEG-to provide a comprehensive overview of the mechanisms involved in visual integration in the presence or absence of auditory input. The methods used are state-of-the-art, and the authors attempted to address possible pitfalls.
Weaknesses:
The use of Bayesian statistics could further strengthen the paper, especially given that a few p-values are close to the significance threshold (lines 162 & 258), but they are interpreted differently in different cases (absence of effect vs. trend).
Overall, these results provide new insights into the role of alpha oscillations in visual processing and offer an interesting perspective on the current debate regarding the roles of alpha phase and frequency in visual perception. More generally, they contribute to our understanding of the neural dynamics of multisensory integration.
We thank Reviewer 2 for the constructive suggestions. The main revisions are summarized below:
(1) We corrected the bistable-report calculation using the actual valid-trial counts, added Bayesian tests for the revised comparisons, and made the interpretation of non-significant results consistent.
(2) We moved the ITC and power-control evidence into the main Results, added a focused power-by-phase control, and retained the RT analysis as a supplementary behavioural check.
(3) We clarified trial exclusion, trial balancing, instantaneous-frequency estimation, and the use of the term characterize.
(1) The use of Bayesian statistics could further strengthen the paper, especially given that a few p-values are close to the significance threshold (lines 162 & 258), but they are interpreted differently in different cases (absence of effect vs. trend).
We thank the reviewer for this helpful suggestion. We agree that non-significant p values should not be interpreted inconsistently as either evidence for the absence of an effect or as a “trend.” To distinguish a lack of statistical significance from positive evidence favoring the null hypothesis, we have added Bayes factors to the key comparisons for which the absence of a difference is relevant to our interpretation.
For the bistable percept proportions, the evidence modestly favored the null hypothesis (F2, BF<sub>01</sub> = 2.89; F2B1, BF<sub>01</sub> = 2.94); we therefore describe the report proportions as comparable rather than claiming definitive equivalence. The evidence favoring the null was stronger for the bistable reaction-time comparison (BF<sub>01</sub> = 3.60), the one- versus two-flash instantaneous-frequency comparison in F2B1 (BF<sub>01</sub> = 4.88), the instantaneous alpha-power comparisons (F2, BF<sub>01</sub>= 5.14; F2B1, BF<sub>01</sub> = 3.31), and the stimulation-frequency comparison in F2B1 (BF<sub>01</sub> = 5.05).
Conversely, where the Bayes factor was insensitive—for example, the nonsignificant main effect of sensory condition on instantaneous alpha frequency (BF<sub>01</sub> = 0.83)—we report the result as inconclusive and interpret it as neither evidence for the null nor a statistical trend. We have revised the wording throughout the Results to apply this distinction consistently. Bayes factors were calculated using a default Cauchy prior (r = 0.707), with the directionality of the tests specified in the Statistical analyses subsection.
We have revised the Results on bistable percept proportions and reaction times (Figure 1E and Figure 1—figure supplement 4), the perceptual-report analysis (Figure 3C), the instantaneous alpha-power control (Figure 3—figure supplement 2), and the tACS results (Figure 5). The Bayes-factor procedure has also been clarified in the Statistical analyses subsection.
Reviewer #2 (Recommendations for the authors):
(2) The authors did not find any significant effect of alpha power. Given that excitability is dependent on both power and phase, did the authors analyze the interaction between the two? This might offer an additional layer of explanation for the phase-related findings.
We thank the reviewer for this important suggestion. Alpha power and phase are closely related but not redundant: power reflects how strongly the oscillation is expressed, whereas phase indicates the position of the cortex within its excitability cycle (Jensen and Mazaheri, 2010; Mathewson et al., 2011, 2009). Both have been linked to visual perception, raising the possibility that phase-dependent perceptual modulation may be more clearly expressed when ongoing alpha power is high (van Dijk et al., 2008; Williams et al., 2024).
We therefore recomputed phase opposition separately for high- and low-power trial subsets, using a median split of posterior prestimulus alpha power within each participant, sensory condition, and perceptual-report category while maintaining balanced trial numbers. The Results now state concisely that the F2B1 alpha-band cluster was significant in the high-power subset (cluster p = .004, −420 to −20 ms, 5.96–16.79 Hz) but not in the low-power subset; neither F2 subset showed an alpha-band cluster, and the high-minus-low contrasts were non-significant (Figure 4—figure supplement 2).
Importantly, the direct high-versus-low contrast was not significant in either condition (F2B1, p = .088; F2, p = .328). Thus, the presence of a significant cluster in the high-power subset but not in the low-power subset does not by itself establish a difference between power levels. Nevertheless, the concentration of the F2B1 phase-opposition effect in high-power trials is consistent with the pulsed-inhibition account, according to which phase-dependent modulation should be most detectable when the underlying oscillation is strongly expressed (Mathewson et al., 2011), and it echoes previous evidence that prestimulus alpha power and phase jointly shape visual perception (van Dijk et al., 2008; Williams et al., 2024). We therefore present this analysis as an exploratory control rather than evidence for a formal power × phase interaction.
We have added this analysis to the Results (Figure 4—figure supplement 2), described the power stratification and permutation procedures in the Methods, and revised the corresponding theoretical interpretation in the Discussion.
(3) Additionally, the analysis of reaction times might be of interest, as slower RTs could indicate increased ambiguity. This could reveal more about how alpha power (which has sometimes been related to RTs in attention tasks), phase, and frequency in the different conditions influence decision-making processes (see Samaha et al. 2020).
We thank the reviewer for this helpful suggestion. We examined reaction times in the bistable trials, because these were the trials in which the perceptual outcome was maximally ambiguous and perceptual ambiguity was equated between F2 and F2B1 using condition-specific fusion thresholds. Reaction times did not differ between the two conditions (F2, 725.29 ± 19.19 ms; F2B1, 733.35 ± 19.39 ms; t<sub>(33)</sub> = −0.95, p = .350, BF<sub>01</sub> = 3.60; Wilcoxon signed-rank p = .174; Figure 1—figure supplement 4). Thus, there was no evidence for a systematic condition-level difference in decision time.
We agree that the absence of a mean reaction-time difference does not exclude possible trial-level relationships between reaction time and alpha power, phase, or frequency. However, comprehensively testing these relationships would require multiple exploratory, trial-level models across several neural measures and temporal windows, without a pre-specified hypothesis regarding their direction. Such analyses would extend beyond the central question of the present study and would require a separate analysis framework with appropriate control for multiple comparisons. We therefore report the reaction-time comparison as a supplementary behavioural check and restrict our interpretation to the absence of a systematic condition-level difference in decision time.
We have added the reaction-time results to the main Results and present the participant-level data in Figure 1—figure supplement 4.
(4) The phase reset results, currently in the supplemental material, are crucial for understanding the proposed model. Moving them to the main text would provide a clearer narrative and strengthen the model presentation.
We agree that this evidence is central to the model. The poststimulus ITC and alpha-power control, which provide the phase-reorganization evidence underlying the model, are presented in the main text as Figure 7.
(5) Although the authors state that trials were balanced and some were excluded (lines 805, 829), the details of how this was done are unclear. It would be helpful to explain the criteria for trial exclusion and the exact balancing process.
We thank the reviewer for requesting this clarification. Trials containing blinks, muscular activity, or other EEG artifacts were first corrected using independent component analysis. The data were then visually inspected, and trials containing residual artifacts or excessive noise were excluded.
After artifact rejection, the primary bistable IAF and POS-map analyses used a common balanced trial set. Within each participant, the F2B1 one-flash, F2B1 two-flash, F2 one-flash, and F2 two-flash cells were randomly subsampled to the size of the smallest cell. This prevented unequal report frequencies or valid-trial counts from influencing comparisons across conditions and perceptual outcomes.
The phase-bin and KL analyses retained all artifact-free bistable trials because they estimate each participant’s within-condition phase–report function rather than comparing cell means. Retaining all valid trials improves the precision of these response-proportion estimates, while the label permutation procedures preserve the original report counts.
We have revised the Recording and preprocessing subsection, the aligned phase-bin analysis, and the non-aligned KL analysis.
(6) Is the observed decrease in frequency compared to the baseline significant in the F2 condition, especially for long ISI trials? If it is the case, how do the authors interpret this result?
We thank the reviewer for raising this point. Relative to the prestimulus baseline, instantaneous alpha frequency decreased reliably in F2 at the long ISI (Δ = −0.076 Hz, t<sub>(33)</sub> = −2.82, p = .004, FDR-corrected p = .012), but not in the short-ISI or bistable trials after correction. In F2B1, the decrease was reliable in the bistable trials (Figure 2C) and at both fixed ISIs (Figure 2—figure supplement 1C).
The F2 long-ISI result indicates that the visual sequence itself can also produce transient alpha slowing, particularly when the two flashes are separated by a longer interval. The beep is therefore not the only possible source of poststimulus slowing. Because F2 and F2B1 contained identical visual sequences, the direct F2B1−F2 comparison isolates the additional auditory contribution. Thus, the F2 result complements rather than contradicts our interpretation: auditory input adds to a visually induced slowing and makes it more consistent across trial types.
We have clarified this interpretation in the main Results, where the bistable baseline comparisons are reported with Figure 2C. The fixed-ISI baseline comparisons are detailed in the Supplementary Results and Figure 2—figure supplement 1C.
(7) Line 799–801: The description of the filtering process (median filtered ten times with 10-time windows) is unclear to me. Could the authors rephrase or provide a visual explanation?
We thank the reviewer for pointing out this ambiguity. The signal was not median-filtered ten times using a 10-ms window. At each time point, local medians were calculated separately within ten centred windows spanning widths from 10 to 400 ms, and the final estimate was the median of these ten window-specific values. This multiscale procedure reduces the high-frequency noise introduced by phase differentiation while limiting dependence on any single smoothing window. We have rephrased the Methods accordingly.
We have revised the instantaneous-frequency analysis subsection of the Methods.
(8) Line 87: Replace “confirm” with “characterize” to better reflect the exploratory nature of the study.
We thank the reviewer for this suggestion. We agree that “characterised” more appropriately reflects the scope of the study. We have revised the Introduction.
Reviewer #3 (Public review):
Summary:
The authors investigated the impact of an auditory stimulus on visual integration at the behavioral, electrophysiological, and mechanistic levels. Although the role of alpha brain oscillations on visual perception has been widely studied, how the brain dynamics in the visual cortices are influenced by a cross-modal stimulus remains ill-defined. The authors demonstrated that auditory stimulation systematically induced a drop in visual alpha frequency, increasing the time window for audio-visual integration, while in the unimodal condition, visual integration was modulated by small variations within the alpha frequency range. In addition, they only found a role of the phase of alpha brain oscillations on visual perception in the cross-modal condition. Based on the perceptual cycles' theory framework, the authors developed a model allowing them to describe their results according to a phase resetting induced by the auditory stimulation. These results showed that the influence of well-known brain dynamics on one modality can be disrupted by another modality. They provided insights into the importance of investigating cross-modal brain dynamics, and an interesting model that extends the perceptual cycle framework.
Strengths:
The results are supported by a combination of various, established experimental and analysis approaches (e.g., two-flash fusion task, psychometric curves, phase opposition), ensuring strong methodological bases and allowing direct comparisons with related findings in the literature.
The model the authors proposed is an extension and an improvement of the perceptual cycle's framework. Interestingly, this model could then be tested in other experimental approaches.
Weaknesses:
There is an increasing number of studies in cognitive neuroscience showing the importance of considering inter-individual variability. The individual alpha frequency (IAF) varied from 8 to 13 Hz with a huge variability across participants, and studies have shown that the IAF influenced visual perception. Investigating inter-individual variations of the IAF in the reported results would be of great interest, especially for the model.
Although the use of non-invasive brain stimulation to infer causality is a method of great interest, the use of tACS in the presented work is not optimal. Instead of inducing alpha brain oscillations in visual cortices, the use of tACS to activate the auditory cortex instead of the actual auditory stimulation would have presented more interest.
We thank Reviewer 3 for the helpful comments. The main revisions are summarized below:
(1) We specified how participant-level alpha peaks were extracted from the FFT spectra.
(2) We clarified the rationale for the posterior tACS montage and the group-level scope of the model.
(3) We clarified the operational relation between perceptual reports and responses, added the instantaneous-frequency equation, and specified the circular test used for the participant-level phase-angle analysis.
(1) There is an increasing number of studies in cognitive neuroscience showing the importance of considering inter-individual variability. The individual alpha frequency (IAF) varied from 8 to 13 Hz with a huge variability across participants, and studies have shown that the IAF influenced visual perception. Investigating inter-individual variations of the IAF in the reported results would be of great interest, especially for the model.
We thank the reviewer for this important suggestion. We now report how participant-level alpha peaks were extracted and show the individual estimates in Figure 2—figure supplement 2. Each participant’s alpha peak was defined as the frequency with maximal power within 8–13 Hz after averaging the trial-level spectra. The group mean was 10.12 ± 0.24 Hz (mean ± SEM), corresponding to a between-participant SD of approximately 1.40 Hz. The condition- and report-specific FFT comparisons were also performed at the participant level, thereby retaining individual variability.
We agree that participant-specific model fitting would be valuable. However, the present model was designed as a group-level proof of principle, and its parameters were not fitted separately to individual participants. Individual fitting would require estimating participant-specific frequency and phase-reset parameters and therefore represents a substantial extension beyond the scope of the present model.
We have revised the alpha-peak extraction procedure in the Methods, the corresponding Results, and Figure 2—figure supplement 2.
(2) Although the use of non-invasive brain stimulation to infer causality is a method of great interest, the use of tACS in the presented work is not optimal. Instead of inducing alpha brain oscillations in visual cortices, the use of tACS to activate the auditory cortex instead of the actual auditory stimulation would have presented more interest.
We thank the reviewer for this constructive suggestion. We agree that auditory-cortex stimulation would provide an informative complementary experiment. However, the posterior montage was chosen to address the central hypothesis of the present study: that alpha oscillations in the visual cortex determine the temporal window of visual integration. Posterior tACS therefore directly tests the causal role of the proposed oscillatory mechanism. Previous stimulation studies show that alpha-frequency stimulation can alter oscillatory activity and phase-dependent perception (Neuling et al., 2012) and that posterior alpha frequency predicts audiovisual temporal illusions (Cecere et al., 2015).
In contrast, auditory-cortex stimulation would test whether engaging the auditory pathway is necessary for the effect of the beep, rather than directly testing the downstream visual-alpha mechanism. We therefore view the two approaches as complementary and have noted auditory-cortex stimulation as a valuable direction for future research.
We have clarified this distinction in the Discussion.
Reviewer #3 (Recommendations for the authors):
(3) Lines 150–153: I did not understand how the authors disentangle the choice/from the perception per se. Clarification would be valuable.
We thank the reviewer for this question. We did not attempt to recover a veridical percept independently of the participant’s response. Instead, the perceptual outcome was operationalized as the participant’s two-alternative report of perceiving one or two flashes, which is the standard psychophysical definition used in the present study. The relevant concern is therefore whether or decision biases could account for the reported condition effects.
The counterbalanced mapping reduces systematic key or motor preferences, and the within-participant comparison uses identical requirements in F2 and F2B1. These controls argue against a simple bias that remains constant across sensory conditions. A constant criterion would not by itself explain the difference between F2 and F2B1 (Green and Swets, 1966). We therefore interpret the findings as consistent with an auditory influence on perceptual integration, while acknowledging that a condition-specific shift in criterion cannot be excluded (Knotts and Shams, 2016).
We have revised the Results to clarify why the findings argue against a simple, condition-independent bias and have stated the remaining limitation in the Methods.
(4) Instantaneous frequency computation: Could the authors provide the mathematical equation and the theoretical explanation, i.e., in which manner the temporal derivative of the phase indicates the instantaneous frequency?
We thank the reviewer for requesting this clarification. Instantaneous frequency was calculated from the temporal derivative of the unwrapped Hilbert phase:

where φφ<sub>uu</sub>(tt) is the unwrapped phase of the alpha-band signal. Phase is measured in radians, and its temporal derivative represents the instantaneous angular velocity in radians per second. Dividing by 2ππ converts angular velocity into cycles per second, or hertz (Boashash, 1992; Cohen, 2014). Thus, a lower instantaneous-frequency value indicates slower local phase progression rather than necessarily reflecting a sustained change in trait-like individual alpha frequency.
We have added the equation and theoretical explanation to the instantaneous-frequency analysis subsection of the Methods.
(5) I suggest replacing Figure 4 with Supplementary Figure 4, and only presenting in the text the results and statistics from Supplementary Figure 4.
We thank the reviewer for this suggestion, and we take it to refer to Figure 3 (instantaneous alpha frequency and perceptual report); Supplementary Figure 4 of the original submission showed the same analysis after removal of the 1/f component, whereas Figure 4 presented the prestimulus phase results, which are addressed in Comment 6 below. We have repeated the 1/f-removal analysis in full and report it as Figure 3—figure supplement 1, with its statistics in the Supplementary Results, but we have retained the original analysis as the main figure. The 1/f-attenuated data do not eliminate the F2 frequency effect: in F2 the two-flash versus one-flash difference was, if anything, slightly larger after 1/f removal (0.079 Hz) than before (0.071 Hz), so the frequency effect cannot be attributed to the aperiodic component. What changed was the precision of the estimate, whose standard error approximately doubled (0.043 vs. 0.023 Hz), and the condition × percept interaction did not survive 1/f removal (F<sub>(1, 33)</sub> = 0.64, p = .430, versus p = .004 in the main analysis). This loss of precision is an expected property of the transform rather than of the data: the anti-1/f modulator divides, rather than subtracts, the log spectrum, so it compresses the alpha peak relative to its neighbours. A measure that flattens the very feature being quantified is therefore not, in our view, the appropriate primary analysis.
We also provide a more direct test of the concern that motivates the suggestion: mean instantaneous alpha power did not differ between perceptual reports in either condition (F2, p = .727; F2B1, p = .308), so neither the aperiodic slope nor oscillatory amplitude offers an alternative account of the frequency effect. We therefore report the 1/f-removed analysis completely and transparently in the supplement, including the non-significant interaction, and discuss the discrepancy explicitly.
(6) What are the statistical tests used in Figure 4B?
We thank the reviewer for requesting this clarification. Figure 4B was analysed using circular statistics. For each participant, we calculated the circular mean phase direction separately for one-flash and two-flash reports at the illustrative maximum-effect point (−300 ms, 10.28 Hz, Oz). The participant-level mean directions were then compared using Watson–Williams tests (Berens, 2009). The preferred-phase directions differed significantly between perceptual reports in F2B1, F<sub>(1, 66)</sub> = 15.31, p < .001, but not in F2, F<sub>(1, 66)</sub> = 3.30, p = .074. We have now specified this statistical test in the Results, Methods, and Figure 4 legend.
We have revised the Results section on the polar-angle analysis, the Methods section describing the phase analyses, and the Figure 4 legend.