Reviewer #2 (Public review):

Summary:

The current study aims to shed light on why previous work on perceptual rhythmicity has led to inconsistent results. They propose that the differences may stem from conceptual and methodological issues. In a series of experiments, the current study reports perceptual rhythmicity in different frequency bands that differ between different ear stimulations and behavioral measures. The study suggests challenges regarding the idea of universal perceptual rhythmicity in hearing.

Strengths:

The study aims to address differences observed in previous studies about perceptual rhythmicity. This is important and timely because the existing literature provides quite inconsistent findings. Several experiments were conducted to assess perceptual rhythmicity in hearing from different angles. The authors use sophisticated approaches to address the research questions.

Weaknesses:

(1) Conceptional concerns:

The authors place their research in the context of a rhythmic mode of perception. They also discuss continuous vs rhythmic mode processing. Their study further follows a design that seems to be based on paradigms that assume a recent phase in neural oscillations that subsequently influence perception (e.g., Fiebelkorn et al.; Landau & Fries). In my view, these are different facets in the neural oscillation research space that require a bit more nuanced separation. Continuous mode processing is associated with vigilance tasks (work by Schroeder and Lakatos; reduction of low frequency oscillations and sustained gamma activity), whereas the authors of this study seem to link it to hearing tasks specifically (e.g., line 694). Rhythmic mode processing is associated with rhythmic stimulation by which neural oscillations entrain and influence perception (also, Schroeder and Lakatos; greater low-frequency fluctuations and more rhythmic gamma activity). The current study mirrors the continuous rather than the rhythmic mode (i.e., there was no rhythmic stimulation), but even the former seems not fully fitting, because trials are 1.8 s short and do not really reflect a vigilance task. Finally, previous paradigms on phase-resetting reflect more closely the design of the current study (i.e., different times of a target stimulus relative to the reset of an oscillation). This is the work by Fiebelkorn et al., Landau & Fries, and others, which do not seem to be cited here, which I find surprising. Moreover, the authors would want to discuss the role of the background noise in resetting the phase of an oscillation, and the role of the fixation cross also possibly resetting the phase of an oscillation. Regardless, the conceptional mixture of all these facets makes interpretations really challenging. The phase-reset nature of the paradigm is not (or not well) explained, and the discussion mixes the different concepts and approaches. I recommend that the authors frame their work more clearly in the context of these different concepts (affecting large portions of the manuscript).

(2) Methodological concerns:

The authors use a relatively unorthodox approach to statistical testing. I understand that they try to capture and characterize the sensitivity of the different analysis approaches to rhythmic behavioral effects. However, it is a bit unclear what meaningful effects are in the study. For example, the bootstrapping approach that identifies the percentage of significant variations of sample selections is rather descriptive (Figures 5-7). The authors seem to suggest that 50% of the samples are meaningful (given the dashed line in the figure), even though this is rarely reached in any of the analyses. Perhaps >80% of samples should show a significant effect to be meaningful (at least to my subjective mind). To me, the low percentage rather suggests that there is not too much meaningful rhythmicity present. I suggest that the authors also present more traditional, perhaps multi-level, analyses: Calculation of spectra, binning, or single-trial analysis for each participant and condition, and the respective calculation of the surrogate data analysis, and then comparison of the surrogate data to the original data on the second (participant) level using t-tests. I also thought the statistical approach undertaken here could have been a bit more clearly/didactically described as well.

The authors used an adaptive procedure during the experimental blocks such that the stimulus intensity was adjusted throughout. In practice, this can be a disadvantage relative to keeping the intensity constant throughout, because, on average, correct trials will be associated with a higher intensity than incorrect trials, potentially making observations of perceptual rhythmicity more challenging. The authors would want to discuss this potential issue. Intensity adjustments could perhaps contribute to the observed rhythmicity effects. Perhaps the rhythmicity of the stimulus intensity could be analyzed as well. In any case, the adaptive procedure may add variance to the data.

Additional methodological concerns relate to Figure 8. Figures 8A and C seem to indicate that a baseline correction for a very short time window was calculated (I could not find anything about this in the methods section). The data seem very variable and artificially constrained in the baseline time window. It was unclear what the reader might take from Figure 8.

Motivation and discussion of eye-movement/pupillometry and motor activity: The dual task paradigm of Experiment 4 and the reasons for assessing eye metrics in the current study could have been better motivated. The experiment somehow does not fit in very well. There is recent evidence that eye movements decrease during effortful tasks (e.g., Contadini-Wright et al. 2023 J Neurosci; Herrmann & Ryan 2024 J Cog Neurosci), which appears to contradict the results presented in the current study. Moreover, by appealing to active sensing frameworks, the authors suggest that active movements can facilitate listening outcomes (line 677; they should provide a reference for this claim), but it is unclear how this would relate to eye movements. Certainly, a person may move their head closer to a sound source in the presence of competing sound to increase the signal-to-noise ratio, but this is not really the active movements that are measured here. A more detailed discussion may be important. The authors further frame the difference between Experiments 1 and 2 as being related to participants' motor activity. However, there are other factors that could explain differences between experiments. Self-paced trials give participants the opportunity to rest more (inter-trial durations were likely longer in Experiment 2), perhaps affecting attentional engagement. I think a more nuanced discussion may be warranted.

Discussion:

The main data in Figure 3 showed little rhythmicity. The authors seem to glance over this fact by simply stating that the same phase is not necessary for their statistical analysis. Previous work, however, showed rhythmicity in the across-participant average (e.g., Fiebelkorn's and similar work). Moreover, one would expect that some of the effects in the low-frequency band (e.g., 2-4 Hz) are somewhat similar across participants. Conduction delays in the auditory system are much smaller than the 0.25-0.5 s associated with 2-4 Hz. The authors would want to discuss why different participants would express so vastly different phases that the across-participant average does not show any rhythmicity, and what this would mean neurophysiologically.

An additional point that may require more nuanced discussion is related to the rhythmicity of response bias versus sensitivity. The authors could discuss what the rhythmicity of these different measures in different frequency bands means, with respect to underlying neural oscillations.

Figures:

Much of the text in the figures seems really small. Perhaps the authors would want to ensure it is readable even for those with low vision abilities. Moreover, Figure 1A is not as intuitive as it could be and may perhaps be made clearer. I also suggest the authors discuss a bit more the potential monoaural vs binaural issues, because the perceptual rhythmicity is much slower than any conduction delays in the auditory system that could lead to interference.

Figures and data

Experimental design and rationale.

Calibration of analysis approaches on simulated data.

Illustration of the data for experiments 1-3.

Significance of rhythmicity in the behavioural data.

Prevalence of significant effects across random variations in the participant sample.

Averaged prevalence across experiments 1-3.

Influence of dual task and eye metrics on rhythmicity in experiment 4.

Illustration of eye tracking data for experiment 4.