Author response:
The following is the authors’ response to the original reviews
Public Reviews:
Reviewer #1 (Public review):
Summary
In this review paper, the authors describe the concept of neural correlates of consciousness (NCC) and explain how noninvasive neuroimaging methods fall short of being able to properly characterise an unconfounded NCC. They argue that intracranial research is a means to address this gap and provide a review of many intracranial neuroimaging studies that have sought to answer questions regarding the neural basis of perceptual consciousness.
Strengths
The authors have provided an in-depth, timely, and scholarly contribution to the study of NCCs. First and foremost, the review surveys a vast array of literature. The authors synthesise findings such that a coherent narrative of what invasive electrophysiology studies have revealed about the neural basis of consciousness can be easily grasped by the reader. The review is also, to the best of my knowledge, the first review to specifically target intracranial approaches to consciousness and to describe their results in a single article. This is a credit to the authors, as it becomes ever harder to apply strict tests to theories of consciousness using methods such as fMRI and M/EEG it is important to have informative resources describing the results of human intracranial research so that theorists will have to constrain their theories further in accordance with such data. As far as the authors were aiming to provide a complete and coherent overview of intracranial approaches to the study of NCCs, I believe they have achieved their aim.
We appreciate the reviewer's positive feedback on our work.
Weaknesses
Overall, I feel positive about this paper. However, there are a couple of aspects to the manuscript that I think could be improved.
(1) Distinguishing NCCs from their prerequisites or consequences
This section in the introduction was particularly confusing to me. Namely, in this section, the authors' aim is to explain how intracranial recordings can help distinguish 'pure' NCCs from their antecedents and consequences. However, the authors almost exclusively describe different tasks (e.g., no-report tasks) that have been used to help solve this problem, rather than elaborating on how intracranial recordings may resolve this issue. The authors claim that no-report designs rely on null findings, and invasive recordings can be more sensitive to smaller effects, which can help in such cases. However, this motivation pertains to the previous sub-section (limits of noninvasive methods), since it is primarily concerned with the lack of temporal and spatial resolution of fMRI and M/EEG. It is not, in and of itself, a means to distinguish NCCs from their confounds.
As such, in its current formulation, I do not find the argument that intracranial recordings are better suited to identifying pure NCCs (i.e. separating them from pre- or post-processing) convincing. To me, this is a problem solved through novel paradigms and better-developed theories. As it stands, the paper justifies my position by highlighting task developments that help to distinguish NCCs from prerequisites and consequences, rather than giving a novel argument as to why intracranial recordings outperform noninvasive methods beyond the reasons they explained in the previous section. Again, this position is justified when, from lines 505-506, the authors describe how none of the reported single-cell studies were able to dissociate NCCs from post-perceptual processing. As such, it seems as if, even with intracranial recording, NCCs and their confounds cannot be disentangled without appropriate tasks.
The section 'Towards Better Behavioural Paradigms' is a clear attempt to address these issues and, as such, I am sure the authors share the same concerns as I am raising. Still, I remain unconvinced that the distinguishing of NCCs from pre-/post- processing is a fair motivation for using intracranial over noninvasive measures.
We agree that distinguishing proper NCCs from their prerequisites or consequences is primarily a matter of experimental design and theoretical framework, not merely of recording modality. We did not mean to imply that intracranial recordings inherently solve this dissociation.This is now explicitly stated that at the beginning of this section. Instead, we argued that the high signal-to-noise ratio and spatiotemporal accuracy of sEEG offer a stronger "testing ground" for the null findings often relied on by no-report paradigms. This is now also further clarified in the revised section “Limits of noninvasive measures”.
We also explicitly acknowledge, as the reviewer noted, that even the most precise recordings require careful task dissociations to distinguish NCCs from their prerequisites and consequences.
(2) Drawing misleading conclusions from certain studies
There are passages of the manuscript where the authors draw conclusions from studies that are not necessarily warranted by the studies they cite. For instance:
Lines 265 - 271: "The results of these two studies revealed a complex pattern: on the one hand, HGA in the lateral occipitotemporal cortex and the ventral visual cortex correlated with stimulus strength. On the other hand, it also correlated with another factor that does not appear to play a role in visibility (repetition suppression), and did not correlate with a non-sensory factor that affects visibility reports (prior exposure). These results suggest that activity in occipitotemporal cortex regions reflecting higher-order visual processing may be a precursor to the NCC but not an NCC proper."
It's possible to imagine a theory that would predict HGA could correlate with stimulus strength and repetition suppression, or that it would not correlate with prior exposure (e.g. prior exposure could impact response bias without affecting subjective visibility itself). The authors describe this exact ambiguity in interpretation later in the article (line 664), but in its current form, at least in line 270 (when the study is most extensively discussed), the manuscript heavily implies that HGA is not an NCC proper. This generates a false impression that intracranial recordings have conclusively determined that occipitotemporal HGA is not a pure NCC, which is certainly a premature conclusion.
We agree that our interpretation of these studies (lines 265–271 of the previous version of the manuscript) was presented too definitively. We have modified the text (now lines 314-317) to soften this conclusion and align it with the more nuanced discussion later in the manuscript. Specifically, we now frame this as a "suggested dissociation" rather than a conclusive finding (line 730), and we explicitly acknowledge that alternative interpretations remain viable.
Line 243: "Altogether, these early human intracranial studies indicate that early-latency visual processing steps, reflected in broadband and low gamma activity, occur irrespective of whether a stimulus is consciously perceived or not. They also identified a candidate NCC: later (>200 ms) activity in the occipitotemporal region responsible for higher-order visual processing."
The authors claim in this section that later (>200ms) activity in occipitotemporal regions may be a candidate for an NCC. However, the Fisch et al. (2009) study they describe in support of this conclusion found that early (~150ms) activity could dissociate conscious and unconscious processing. This would suggest that it is early processing that lays claim to perceptual consciousness. The authors explicitly describe the Fisch et al results as showing evidence for early markers of consciousness (line 240: '...exhibited an early...response following recognized vs unrecognised stimuli.) Yet only a few lines later they use this to support the conclusion that a candidate NCC is 'later (>200ms) activity in the occipitotemporal region' (line 245). As such, I am not sure what conclusion the authors want me to make from these studies.
This problem is repeated in lines 386-387: "Altogether, studies that investigated the cortical correlates of visual consciousness point to a role of neural responses starting ~250 ms after stimulus onset in the non-primary visual cortex and prefrontal cortex."
This seems to be directly in conflict with the Fisch et al results, which show that correlates of consciousness can begin ~100ms earlier than the authors state in this passage.
We thank the reviewer for pointing out this inconsistency. We agree that stating ">200 ms" conflicts with the findings of Fisch et al. (2009), who observed dissociations as early as ~150 ms. Our goal was to contrast the very early, stimulus-driven responses with the later responses that reflect consciousness. However, as the reviewer correctly notes, the exact "onset" of these signals varies across studies and paradigms. To address this, we have removed the specific ">200 ms" mentioned in line 245 of the previous version of the manuscript and updated the timing in line 284 to "starting 150 ms" to better reflect the results of Fisch et al. We also clarify that while the exact latency depends on the paradigm, a consistent finding is that activity representing conscious contents in higher-order visual cortex follows an initial wave of unconscious processes (lines 809-810).
(3) Justifying single-neuron cortical correlates of consciousness
The purpose of the present manuscript is to highlight why and how intracortical measures of neural activity can help reveal the neural correlates of perceptual consciousness. As such, in the section 'Single-neuron cortical correlates of perceptual consciousness', I think the paper is lacking an argument as to why single-neuron research is useful when searching for the NCC. Most theories of consciousness are based around circuit or system-level analyses (e.g., global ignition, recurrent feedback, prefrontal indexing, etc.) and usually do not make predictions about single cells. Without any elaboration or argument as to why single-cell research is necessary for a science of consciousness, the research described in this section, although excellent and valuable in its own right, seems out of place in the broader discussion of NCCs. A particularly strong interpretation here could be that intracranial recordings mislead researchers into studying single cells simply because it is the finest level of analysis, rather than because it offers helpful insight into the NCCs.
It is true that many prominent theories of consciousness were developed based on macroscopic observations, largely due to the prevalence of non-invasive recordings in humans. However, we argue that recording single-unit activity is important for several reasons, and we made this clearer in the revised version. First, signals like fMRI, EEG (or even LFP) often conflate multiple distinct neural populations. SUA allows us to dissociate neurons representing the percept from neighboring neurons involved in task-related confounds (e.g., motor preparation or arousal) that would otherwise be blurred together. Therefore, some percepts might be represented by sparse coding involving a small, specific population of "concept" or "percept" cells. Electrophysiological studies in animal models reveal that various cognitive processes are encoded within neuronal subspaces that only emerge when single-unit activity is analyzed as lower-dimensional projections of the broader neural activity manifold (Mante et al., 2013; Ebitz & Hayden, 2021; Jayazeri & Afraz, 2017). Importantly, many neural computations are only discernible through the lens of population dynamics (i.e. with single neuron activity) (Vyas et al., 2021). We believe that providing high granularity through SUA recordings prevents over-aggregation of data, ensuring that even system-level theories can build on biologically accurate foundations.
Moreover, some theories are defined at the cellular level. For instance, the Dendritic Integration Theory (Bachmann et al., 2020) posits that the integration of feedforward and feedback signals occurs at the level of individual pyramidal neurons. Without SUA, these cellular mechanisms remain untestable. Beyond spatial granularity, SUA also provides excellent temporal granularity, which is crucial for testing theories that rely on the precise timing of spikes (e.g., neural synchrony). As LFPs reflect average activity across populations, only SUA can confirm whether individual neurons lock their spikes to a specific phase, a mechanism hypothesized to bind features into a conscious whole.
We added these points to a new section in the revised manuscript.
References:
Bachmann, T., Suzuki, M., & Aru, J. (2020). Dendritic integration theory: A thalamo-cortical theory of state and content of consciousness. Philosophy and the Mind Sciences, 1(II).
Ebitz, R. B., & Hayden, B. Y. (2021). The population doctrine in cognitive neuroscience. Neuron, 109(19), 3055-3068.
Jazayeri, M., & Afraz, A. (2017). Navigating the neural space in search of the neural code. Neuron, 93(5), 1003-1014.
Mante, V., Sussillo, D., Shenoy, K. V., & Newsome, W. T. (2013). Context-dependent computation by recurrent dynamics in prefrontal cortex. nature, 503(7474), 78-84.
Vyas, S., Golub, M. D., Sussillo, D., & Shenoy, K. V. (2020). Computation Through Neural Population Dynamics. Annual Review of Neuroscience, 43(1), 249-275.
(4) No mention of combined fMRI-EEG research
A minor point, but I was surprised that the authors did not mention any combined fMRI-EEG research when they were discussing the limits of noninvasive recordings. Intracortical recordings are one way to surpass the spatial and temporal resolution limits of M/EEG and fMRI respectively, but studies that combine fMRI and EEG are also an alternative means to solve this problem: by combining the spatial resolution of fMRI with the temporal resolution of EEG, researchers can - in theory - compare when and where certain activity patterns (be they univariate ERPs or multivariate patterns) arise. The authors do cite one paper (Dellert et al., 2021 JNeuro) that used this kind of setup, but they discuss it only with respect to the task and ignore the recording method. The argument for using intracranial recordings is weaker for not mentioning a viable, noninvasive alternative that resolves the same issues.
We thank the reviewer for this point. We have added a discussion of fMRI-EEG to the "Limits of noninvasive measures" section (lines 167-171). While we acknowledge that fMRI-EEG is a powerful non-invasive tool for bridging spatial and temporal scales, we note that it relies on merging an indirect metabolic signal with a weak electrophysiological one filtered by the skull, which is computationally complex and often noisy. In contrast, intracranial recordings provide direct measures of both local field potentials and spiking activity within the same neural population, offering interpretability and signal-to-noise ratio that non-invasive combinations cannot match. In our view, this is not just an alternative to these methods, but a unique means of accessing the underlying neuronal ground truth.
Reviewer #2 (Public review):
Summary:
In this work, the authors review the study of the neural correlates of consciousness (NCCs). They discuss several of the difficulties that researchers must face when studying NCCs, and argue that several of these difficulties can be alleviated by using intracranial recordings in humans.
They describe what constitutes an NCC, and the difficulties to distinguish between an NCC proper from the prerequisites and consequences of conscious processing.
They also describe the two main types of experimental designs used to study NCCs. These are the contrastive approach (with its report and non-report variants), and the supraliminal approach, each with its own merits and pitfalls.
They discuss the limitations of non-invasive methods, such as fMRI, EEG and MEG, as well as the limitations of the use of invasive recordings in non-human animals.
After setting the stage in this way, the authors provide an extensive review of the knowledge acquired by using invasive recordings in humans. This included population-level measurements in vision and in other sensory modalities, as well as single-neuron level studies. The authors also discuss studies of subcortical NCCs.
The second half of this work discusses the theoretical insights gained through the use of intracranial recordings, as well as their limitations, and a perspective for future work.
Strengths:
This work offers an impressive review, which will serve as a useful reference document, both for newcomers to the study of NCC and for experienced researchers. The inclusion of non-visual and subcortical NCCs is of particular merit, as these have been understudied.
Besides serving as a review, this work includes a perspective, exploring several directions to pursue for the progress of the field.
We thank the reviewer for acknowledging the strength of our work.
Weaknesses:
The intention of the authors is to argue how some of the problems faced when studying NCCs are alleviated by the use of intracranial recordings in humans. But in some cases, the link between the problems related to the study of NCCs and the advantages of intracranial recordings over non-invasive methods is not clear.
For example, the authors explain the difficulties in distinguishing between true NCCs from their prerequisites and consequences. This constitutes a difficult conceptual problems that plague all recording techniques. The authors don't provide a convincing explanation of how intracranial recordings offer advantages over EEG or MEG when dealing with these problems.
We agree that the distinction between proper NCCs and their prerequisites or consequences is a fundamental challenge that affects all recording modalities. We did not intend to imply that intracranial recordings are a "silver bullet" for solving this conceptual problem in isolation, and we now explicitly state that at the beginning of this section (line 101).
We have revised the section on "Distinguishing NCCs from their prerequisites or consequences" to clarify that intracranial recordings are a powerful tool when used in conjunction with appropriate experimental designs, rather than a standalone solution to these conceptual difficulties.
For example, the authors explain how the use of non-report designs to rule out post-perceptual processing relies on null results, which, according to them, are harder to interpret given the low resolution of non-invasive methods. But the interpretation of null results is actually more complicated in the case of intracranial recordings. As the coverage achieved by the electrodes is sparse, if a null result is attested, it remains possible that a true effect was present in a nearby patch of cortex out of coverage.
It is true that a null result in an intracranial study may simply reflect that the relevant neural population was not sampled by the specific electrode implantation scheme. However, we argue that interpreting null results is equally, if not more, complicated in non-invasive methods, albeit for different reasons. While M/EEG offers broader coverage, it is blind to many cortical sources because of their orientation (radial sources in MEG) or their location in deep sulci and subcortical structures. The signal-to-noise ratio of M/EEG is also much lower than that of intracranial EEG, making it more likely that null results obscure the existence of subtle effects (Parvizi & Kastner, 2018).
To address this, we revised the manuscript to clarify that intracranial recordings provide high local certainty within the sampled regions (lines 224-227), whereas non-invasive methods provide broader coverage (lines 247-249). We now explicitly emphasize that drawing conclusions from null results based on intracranial recordings requires caution regarding electrode placement. We also point out that these approaches are complementary: M/EEG can identify large regions of interest, while sEEG can then provide high-resolution "ground truth" to confirm whether those regions are part of the NCC.
Reference: Parvizi, J., & Kastner, S. (2018). Promises and limitations of human intracranial electroencephalography. Nature Neuroscience, 21(4), 474-483. https://doi.org/10.1038/s41593-018-0108-2
The authors argue that the spatial resolution of intracranial recordings is better than that of EEG and MEG. While this is technically true (especially compared to EEG), the true spatial scale of the NCCs is unknown. If NCCs' span is in the mm range, then the additional spatial resolution of intracranial recordings might not be an advantage.
We agree with the reviewer that the exact spatial scale of the NCC remains a topic of ongoing debate. However, we believe that the advantage of intracranial recordings holds true whether the NCC spans millimeters or centimeters. The main spatial limitation of non-invasive electrophysiology (M/EEG) is not just its spatial resolution but also the inverse problem. Since scalp sensors detect a mixture of signals from across the brain, different cortical configurations can produce identical scalp patterns. This makes it challenging to precisely locate the NCC or distinguish it from nearby activity (e.g., motor or attentional signals). When recording intracortically, a widespread NCC could be captured across multiple adjacent channels with high accuracy. Conversely, if the NCC is focal, it can be isolated with high spatial resolution. In either case, intracranial recordings eliminate the spatial ambiguity inherent in scalp recordings. We have revised the Introduction (lines 158-164) to clarify that the "spatial advantage" of intracranial recordings also pertains to the inverse problem, not merely to the ability to record from smaller cortical areas.
Another factor that should be taken into consideration when assessing the spatial resolution of intracranial recordings is that while the listening zone of individual intracranial contacts is small, coverage is sparse and defined by clinical criteria (something that the authors discuss). In practice, the activity recorded by contacts is usually attributed to anatomically defined ROIs with a scale in the cm range. Given the sparse and uneven (across regions and patients) coverage afforded by intracranial recordings, the advantage of intracranial recordings in terms of spatial resolution is overstated.
We thank the reviewer for raising this point regarding how intracranial data is often aggregated into regions of interest. We agree that if researchers generalize findings to large anatomical regions without accounting for single-channel recordings, some of the spatial benefits of intracranial recordings are indeed mitigated. We toned down some of the original claims accordingly, and acknowledged more clearly that clinical constraints of sEEG lead to sparse coverage (245-249).
However, we maintain that even when using an ROI-based approach, intracranial recordings offer a clear advantage over non-invasive methods, in that they represent a direct measure from a specific patch of tissue, rather than a statistical estimate that may be contaminated by "leakage" from distant sources. To address the reviewer’s concern, we have updated the manuscript (lines 244-245) to emphasize the importance of relying on MNI coordinates and individual anatomy rather than solely on broad ROI labels.
Appraisal of whether the authors achieved their aims:
In this work, the authors have gathered an impressive review and have discussed several important problems in the field of study of NCCs, as well as provided a perspective on how the field could move forward.
What is less clear is how the use of intracranial recordings per se holds potential to overcome problems such as the distinction between true NCCs and the prerequisites and consequences of conscious processing.
Discussion of the likely impact of the work on the field:
This work has the potential of becoming a must-read for anyone working in the field of consciousness research.
Reviewer #3 (Public review):
Summary:
This narrative review provides a clear, well-structured, and comprehensive synthesis of intracerebral recording work on the neural correlates of consciousness. It is written in an accessible manner that will be useful to a broad community of researchers, from those new to iEEG to specialists in the field.
Strengths:
The manuscript successfully integrates methodological and theoretical perspectives and offers a balanced overview of current, sometimes contradicting evidence. As such, the manuscript is important as it calls for a concerted and better exploration of NCCs using iEEG in the future.
We thank the reviewer for stating the importance of our work and its potential contribution to the field.
Weaknesses:
The manuscript extensively discusses the use of "report" as a criterion for identifying conscious perception and its limitations for separating between correlates of consciousness and post-consciousness processes, yet the term is not defined at the outset. The authors should specify what they mean by "report" (e.g., verbal report, nonverbal self-report, or any meta-cognitive indication of experience). Importantly, this definition should be explicitly linked to the theoretical landscape: whether the authors adopt an access-consciousness perspective in which (self) reportability is central, or whether the review also aims to address phenomenal consciousness. Making this conceptual grounding explicit at the beginning will help readers interpret the empirical work surveyed throughout the review.
We agree that a clear definition of report is essential for the reader to interpret the empirical findings presented. We have added a definition to the Introduction (lines 108-111), specifying that we use "report" to refer to any explicit behavioral response (whether verbal, manual, or otherwise) that communicates a subject’s subjective state.
Regarding the conceptual distinction between Phenomenal and Access consciousness, we refer to recent work from some of the co-authors (Mudrik et al., 2025), which suggests that P and A should not be seen as two types of consciousness, but rather as two necessary conditions for conscious experience. While a full discussion of this distinction is beyond the scope of this review, we now clearly state that our focus is on identifying neural activity that reflects the subjective experience itself, regardless of the downstream requirements of report.
Reference: Mudrik, L., Faivre, N., Pitts, M., & Schurger, A. (2025). On a confusion about there being two types of consciousness. Trends in Cognitive Sciences. https://doi.org/10.1016/j.tics.2025.11.012
In addition, the review would benefit from an earlier introduction of the distinction between states and contents of consciousness. This distinction becomes important in the later section on anaesthesia, sleep, and epileptic seizures, where the focus shifts from content-specific NCCs to alterations in global states. Presenting these definitions upfront and briefly explaining how states and contents interact would strengthen the coherence of the manuscript.
We agree that clarifying the distinction between contents and levels of consciousness early on provides a stronger framework for the paper.
We have added a brief clarification in the Introduction (lines 63-76): "It is also helpful to distinguish between levels of consciousness, defined as a global level of arousal or wakefulness (e.g., being awake vs. under anesthesia), and the contents of consciousness, defined as the specific subjective experiences one has while conscious (e.g., perceiving a visual stimulus; Bayne et al., 2016; Laureys, 2005). While the majority of this review focuses on 'content-specific' NCCs, the two dimensions are intrinsically linked, as global states typically set the conditions for the occurrence of specific conscious contents."
Overall, this is an excellent and timely review. With clearer initial theoretical definitions of consciousness, the manuscript will offer an even stronger conceptual framework for interpreting intracerebral studies of consciousness.
We thank the reviewer again for this highly positive assessment of the manuscript.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
I would like to reiterate that I believe this is a very scholarly piece of writing, and I congratulate the authors on producing such a useful and timely manuscript. Below, I suggest just a few ways the authors may resolve some of the issues I raised in the public review. However, I would like to emphasise that these are merely suggestions - the authors may think of different and better ways to address these comments that are more in line with either their thinking or writing style, and I would certainly encourage the authors to follow their own preferences if they feel they are at odds with my suggestions.
For the longer comment questioning whether intracranial recordings are really a way to isolate NCCs from their pre- and post-processing, there are two ways the authors could resolve this. One is that they collapse the section distinguishing NCCs from their prerequisites and consequences into the previous section regarding limits of noninvasive measures. For instance, they could make the point that null results are easier to interpret with intracranial recordings in this previous section. Then they could discuss how specific intracranial studies have been able to resolve questions of pre-/post- processing confounds when they introduce studies later in the manuscript. At the moment, the Distinguishing NCCs from their prerequisites and consequences section, at least to me, undermines the argument of why intracranial recordings are important because it spends too much time describing how tasks are the core component of isolating pure NCCs, and not the recording method.
Alternatively, the authors could keep the structure as it is. In this case, I would urge the authors to emphasise the role of intracortical recordings here and to make the argument that this is a problem that intracortical recordings (rather than novel tasks) can solve more convincingly. Citing specific studies that combined intracortical recordings with no-report paradigms and emphasising how the invasive recording allowed the researchers to reach a conclusion that would not have been possible with noninvasive measures would also be helpful.
We thank the reviewer for these useful suggestions and agree that we would not want readers to take from this paper that design issues can be fixed by using invasive recordings. Because confounding issues are crucial in research on the NCC, we believe it is important to include a section on this topic in the Introduction. However, as we explained in our response to the public review, we revised the section introducing Human intracranial electrophysiology to reflect that intracranial recordings are a complementary tool that improves the interpretability of no-report paradigms, rather than a “silver bullet” solution for confound issues. We also explicitly say now that this problem is relevant to all techniques in the study of consciousness, including intracranial recordings (line 101). Additionally, based on the reviewer’s suggestion, we have added a more detailed explanation of how studies that pair intracranial recordings with no-report paradigms provide a unique insight in the Temporal Insights section (lines 822-823).
For my comment: Drawing misleading conclusions from certain studies, I think the public review speaks for itself. I would recommend that the authors make sure they are drawing correct conclusions from the studies they cite, and make clear from the outset where there is ambiguity in interpretation.
We thank the reviewer for bringing these ambiguities to our attention. As explained in the response to the public review, we have modified the text accordingly.
Finally, with regard to the single-cell analyses, I would imagine that most readers will share at least some scepticism around single neurons being the appropriate level of analysis for revealing the basis of perceptual experience. As such, I think it would strengthen the manuscript greatly if the authors could provide a brief argument as to how such work can either inform theories of consciousness or contribute more generally to the study of NCCs, given that the field and its theories are mostly biased towards studying system-level neural processes. I think single-cell analyses are extremely valuable to NCC research, and the authors have a good opportunity to frame these studies accordingly.
We agree. As detailed in the response to the public review, we now specify (1) how a higher level of granularity in electrophysiological measurements can distinguish between awareness-related signals and confounds, (2) that these measurements provide an opportunity to study neuronal population dynamics where various cognitive processes have been shown to emerge in animals and (3) that single-neuron measurements are necessary to test predictions of theories that are defined at the cellular level
Reviewer #2 (Recommendations for the authors):
Recommendations for improving the writing and presentation:
My compliments for having written an impressive review. Overall, I think that this is a beautiful piece of work that will be of great use to the community. My only concern is that the advantages of intracranial recordings over non-invasive methods in solving the difficulties faced in the study of NCCs are overstated.
Here I provide more precise comments for your consideration.
(1) On page 5, lines 100 to 102, you argue that "Scalp EEG and MEG have limitedanatomical resolution due to the overlap of deep and superficial brain signals at the scalp level and, in the case of EEG, the scattering of the adjacent electrical signals through the scalp". It would be good to provide precise estimates of the spatial resolutions of EEG, MEG and intracranial recordings, with accompanying references. Consider also that MEG is relatively insensitive to deep sources. I recommend this paper: Piastra et al. 2020 https://onlinelibrary.wiley.com/doi/10.1002/hbm.25272
We thank the reviewer once again for their positive evaluation of our work. As detailed in the response to the public reviews, we now clarify that intracranial recordings provide high local certainty within the sampled regions (lines 224-227), whereas non-invasive methods provide broader coverage (lines 247-249). We thank the reviewer for their additional suggestions and have clarified our concern about the anatomical conclusions that can be drawn from scalp EEG and MEG data (lines 158-164).
(2) On page 11, you describe work showing that activity in the occipitotemporal cortex mightreflect a precursor to consciousness, but not an NCC proper, except for the case of faces, in which the fusiform seems to behave like a true NCC. Could you discuss how these seemingly contradictory results could be reconciled?
One possibility is that activity in some parts of the occipitotemporal cortex instantiates content-specific NCCs, i.e., correlates that are only specific to certain stimulus types (in this case: faces), while activity in other parts instantiates precursors of the NCCs. Because faces have been extensively studied, we might have uncovered the content-specific NCCs for these stimuli but not for others. This is now discussed in the text on lines 342-344. Based on reviewer 1’s suggestion, we have also toned down our claim about occipitotemporal activity being a precursor to the NCC.
(3) From line 322, you start to discuss connectivity analyses. Adding a subheading mightimprove readability.
We appreciate the suggestion; however, adding a subheading to a single paragraph would require restructuring the entire section, which could disrupt the flow. We believe the current format maintains clarity and cohesion.
(4) In line 329, you write "It remains unclear to what extent these connectivity patterns reflectpost-perceptual processing and how the signals associated with perceptual consciousness in the occipitotemporal cortex interact with frontoparietal regions." But it's not clear why this is the case.
We meant to make two separate points: (1) these studies did not control for report-related activity using no-report paradigms and (2) there has been no investigation so far of the interaction between occipitotemporal and frontoparietal signals associated with perceptual consciousness. These two points have been clarified in the text (lines 378-381).
(5) In line 692, it would be good to clarify that Pereira 2021 is a single-neuron study.
This has been clarified in the text.
(6) The phrase "more research/work is needed" is repeated several times.
Thank you for pointing this out. To avoid redundancy, we have deleted the second mention of this phrase.
