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  1. Author Response

    Reviewer #1 (Public Review):

    In this article, the authors investigated the role of sleep and brain oscillations in visual cortical plasticity in adult humans. The authors tested the effect of 2 hours of monocular deprivation (MD) on ocular dominance measured by binocular rivalry. In the main MDN session, MD was performed in the late evening, followed by 2 hours of sleep, during which EEG was measured. After the sleep session, ocular dominance was measured, which was followed by 4 hours of sleep, then ocular dominance was measured again in the morning. The results show that the effect of MD was preserved 6 hours after MD. The effect of MD correlated with sleep spindle and slow oscillation measures. The questions asked by the study are timely and findings are important in understanding the visual cortical plasticity in human adults, but I have some concerns regarding the experimental design, analysis, and interpretation of the results, which are listed below.

    Thank you for the positive summary of our results.

    • The authors investigated EEG activities in the central and occipital regions. The results of the relationship between slow oscillations / sleep spindles and deprivation index are very interesting. However, it appears that the activities were averaged across hemispheres in the occipital region. Previous studies (e.g. Lunghi et al., 2011; Binda et al., 2018) have demonstrated that MD is associated with up-scaling of the deprived eye and with down-scaling of the non-deprived eye (page 11). I wonder whether sleep slow oscillations and / or spindles are modulated locally in the deprived occipital region? To answer the first question raised by the authors (how MD affects subsequent sleep), wouldn't it be important to compare between deprived vs. non-deprived regions?

    In humans, the pure monocular recipient cortical regions are very small and represent only very far visual periphery. These regions are impossible to be located by EEG and they are also difficult to locate also with high resolution fMRI (ref to Koulla CB). Visual cortical organization is based on the visual field map: neurons whose visu.al receptive fields lie next to one another in visual space are located next to one another in cortex, forming one complete representation of contralateral visual space, independently of the eye from which the visual information comes. However, at finer scales ocular dominance columns exist and Binda et al (2018) showed that in adult humans MD boosts the BOLD response to the deprived eye, changing ocular dominance of V1 vertices, consistent with homeostatic plasticity. All these are well known facts to the visual community, and we believe are not worthwhile to discuss them.

    • To answer the second question (how sleep contributes to consolidation of visual homeostatic plasticity), the authors compared the deprivation index between two sessions, the main MDN and a control MDM session. The experimental designs for these two sessions were quite different. For example, MD was conducted in the evening in MDN, whereas it was conducted in the morning in MDM. Since there may be circadian effects on plasticity (Frank, 2016), the comparisons between these sessions may not be sufficient in investigating the effect of sleep itself (it could be merely due to circadian effect).

    Thank you for raising this important issue. We performed the dark exposure experiment in the morning because we wanted to minimize the occurrence of sleep during the two hours spent by participants lying down in complete darkness. Preventing sleep under these conditions in the late evening would have been extremely challenging. In order to investigate a possible influence of the circadian rhythm on visual homeostatic plasticity and its decay over time, we have performed an additional experiment. In this experiment, we have tested the effect of 2h of monocular deprivation in the same participants either early in the morning or late at night (at a time of the day comparable to the MDnight and MDmorn conditions in the main study). We report the results of this control experiment in the supplementary materials (Figure S2). We found that the effect of monocular deprivation follows a similar timecourse for the two conditions (ocular dominance returns to baseline levels within 120 minutes after eye-patch removal). Moreover, we also report that the effect of MD is slightly (but significantly) larger in the morning, compared to the evening. The results of this experiment rules out a contribution of circadian effects and reinforces the evidence of a specific effect of sleep in maintaining visual homeostatic plasticity.

    • The authors argue that NREM sleep consolidates the effect of MD. However, consolidation may last days to months or even years (Dudai et al., 2015). Since the effect is gone in 6 hours or so, it may be difficult to interpret it as consolidation. Although the findings of the effects of sleep on ocular dominance plasticity are interesting, the interpretations of the results may need to be clarified or revised.

    We thank the reviewer for raising this issue. We agree that the data show a substantial delay in the decay process of the MD effects after the removal of the patch. The present data indicate that specifically the sleep condition and not merely darkness would be responsible for the maintenance of the MD-induced effect during the night. Therefore, we gladly adhere to the request and propose to say that sleep stabilizes/maintains the effects of MD as long as sleep itself persists. Having said that, we would like to point out that the MD boost in amblyopic patients gets consolidated for up to one year and increases across night sleep as we reported in Lunghi, Sframeli et al (2019). Although these data strongly suggest that real consolidation may occur, we agree with the reviewer that our data did not directly address this question and changed accordingly the manuscript.

    Reviewer #2 (Public Review):

    This manuscript is an interesting follow up on a substantial literature on the role of sleep in promoting critical period ocular dominance plasticity, and the role of sleep in promoting adult V1 plasticity following presentation of a novel visual stimulus. For nearly all of that literature (i.e. coming from cats and mice), the focus has mainly been on Hebbian mechanisms. The authors here propose to advance the field by investigating plasticity in adult human V1, which the authors consider to be homeostatic rather than Hebbian, and which the authors consider to be a form of sleep-dependent consolidation. This is an exciting goal, and the overall study designs and control will test the effects of brief MD and subsequent sleep or wake in the dark on V1 processing for the two eyes.

    Thank you for the positive commentary on our study.

    However, the outcomes of the study suggest that the changes observed in V1 across sleep may actually be the opposite of consolidation - rather it is decay of an effect on V1 function caused by prior wake experience (MD), which disappears over subsequent hours.

    We thank the reviewer for raising this issue. We agree that the data show a substantial delay in the decay process of the MD effects after the removal of the patch. The present data indicate that specifically the sleep condition and not merely darkness would be responsible for the maintenance of the MD-induced effect during the night. Therefore, we gladly adhere to the request and propose to say that sleep stabilizes/maintains the effects of MD as long as sleep itself persists. We have revised the entire MS through the various sections to handle this important aspect and to consider that a classic correlate of memory consolidation during sleep (spindles density) also turns out to be associated with maintenance of the MD-induced ocular dominance effect.

    The authors claim differences due to sleep, but there is not a direct statistical comparison between sleep and awake-in-the-dark controls.

    We now directly compare the effect of monocular deprivation and its decay after two hours in the sleep vs dark exposure condition (MDnight vs MDmor). We now plot the results of the two conditions in the same graph (Figure 2). We found a significant interaction effect between the factors TIME (before and after) and CONDITION (MDnight and MDmor), indicating a specific role of sleep in prolonging the decay of short-term monocular deprivation.

    There is also no quantification of sleep architecture across the sleep period, to determine whether REM or NREM play a role.

    We have provided a summary table of sleep architecture in the revised version of the Supplementary Materials. The table shows descriptive statistics of sleep architecture on MDnight and CN. Also, we report the result of the paired comparison between the nights and the Spearman correlations between the deprivation indices (DI before and DI after) and the changes between the nights in sleep architecture. Tests indicate that MD does not produce any main effect on the sleep architecture and that there are no substantial associations found between sleep architecture parameters and deprivation indices. Thus, it appears that changes in SSO and spindle frequency and amplitude did not lead to an alteration in the amount of N2 or N3 sleep, as we might expect. At the beginning of the Results section we refer to the table and to the lack of statistically significant effects.

    Finally, while there are tests of changes in NREM oscillations with previous plasticity in wake, there are no direct tests of changes across sleep - i.e. the very changes that could be considered consolidation.

    We thank the reviewer for stimulating us to investigate whether there are any NREM parameters whose change within the sleep cycle can be related to the degree of plasticity maintenance observed at the end of the two hours of sleep.

    For this aim, we 1) partitioned SSO and spindle events into tertiles according to their occurrence time, 2) estimated the average measures of events belonging to the first and last tertile, and considered the variation between tertiles as an estimate of the changes across sleep. We then tested whether there is a consistent relationship between measures of individual retained plasticity (DI after) and changes in SSO and sleep spindles across sleep.

    We did the across sleep analysis of the SSO and spindles measurements and as previously explained none of the parameters showed associations across sleep with the individual DI after sleep. We report these results in the supplementary materials (Figure S8).

    Finally is also not clear that the decay of response changes is due to homeostatic plasticity - it could be just that- decay of plasticity that occurred previously. The terminology used - e.g. consolidation, homeostatic vs. Hebbian - don't seem well founded based on data.

    Thank you for raising an important point. In our study homeostatic plasticity refers to the effect of short-term monocular deprivation (so the plasticity occurred before sleep). We have rephrased the interpretation of our results in terms of stabilization/maintenance rather than consolidation of plasticity

    About homeostatic vs Hebbian plasticity, there is a quite large agreement in the literature stating that indeed the effects are different. Now we make clear in the text that Hebbian plasticity is usually associated to the boost of most successful signals in driving a neuronal response or a behavior. Here the MD produced a boost of the unused, and probably silent, eye and as such the boost it is very difficult to explain in term of Hebbian plasticity. We make now this clear in the introduction.

    Reviewer #3 (Public Review):

    In this study, Menicucci et al. induced plastic changes in ocular dominance by applying an eye-patch to the dominant eye (monocular deprivation, MD). This manipulation resulted in a shift toward even more dominance of the deprived eye, as assessed though a binocular rivalry protocol. This effect was stabilized during sleep whereas it quickly decreases in waking (in the dark). The authors interpret the MD effect as the resultant of cortical plasticity over primary visual areas and its maintenance during sleep as the consolidation of these changes. The authors thus connect their work to the literature on sleep consolidation. They further show that the magnitude of the MD effect is positively correlated with sleep markers that are involved in memory consolidation (slow oscillations and sleep spindles).

    However, I have first conceptual issues with this study. Indeed, previous findings on the replay of memories during sleep and their consolidation were mostly obtained in hippocampus-dependent forms of learning. Here, I do not really see what is it that would be replayed. Thus, I struggle understanding how rhythms, such as sleep spindles, that have been linked to the transfer of hippocampal memories to the neocortex, would be mechanistically associated with low-level plastic changes restricted to primary visual areas. In addition, the effects were observed over occipital electrodes, where sleep spindles are far fewer and lower in amplitude than other cortical regions. Furthermore, the association between MD-related plasticity and slow oscillations is interesting but, since these slow oscillations organize sleep slow waves, the lack of correlation with slow wave is surprising.

    We agree with the review that many of our results are indeed surprising, especially those related to the involvement of the spindles and for these reasons we believe that eLife would be the appropriate journal to present our work. At present the fact that sleep spindles have been associated manly in mediating transfer of memory does not exclude a more general involvement in other sensory functions.

    Connected to these conceptual issues, I think the present work has some important methodological limitations. First of all, the analyses included a rather small number of participants, which could make some analyses, in particular correlational analyses, severely underpowered.

    We thank you for stimulating us to emphasize this limitation. In the section Participants within Materials and methods we pointed out that the complexity of the experimental design and the need to take into account the complexity of sleep expressed through different parameters, the sample size used and the need for corrections for multiple tests led to highlight only associations characterized by strong effect size.

    Secondly, the approach used to explore the correlation between plasticity and sleep features focused on subset of electrodes (ROI) defined a priori. It is therefore difficult to conclude on the specificity of the results. Given the topographical maps provided by the authors, I am wondering if a more exhaustive analysis of the effect at the electrode level could not yield more robust findings.

    The need for ROIs is based on the interindividual variability of brain structures, in particular the large anatomical variability of V1 orientation implying a variably oriented dipole and a variable maximal representation of visual potentials over electrodes from Oz to CPz. Moreover, we have to cope with the volume conduction effect that limits EEG spatial resolution.

    With these limitations in mind, we very gladly adhere to the reviewer's request to evaluate the effects on individual electrodes in more detail. To this end we have prepared supplementary figures which show boxplots and scatterplots for the electrodes inside the ROIs to evaluate main effects and associations, respectively.

    Finally, given the number of features tested, I think it is important to clarify the strategy used to correct for multiple comparisons.

    We thank the reviewer for highlighting an unclear point. In the revised version of the Statistical analyses section, we have provided missing details of the procedure used for handling false positives due to multiple testing. Basically, we applied the FDR correction for each question we asked.

    For example, “at which time points does dominance remain significantly different from baseline?” or, “which EEG feature and in which area of the scalp shows changes significantly dependent on plasticity induced by monocular deprivation?” For each of these questions, we made a group of tests (for the first example, dependent on the number of points at which ocular dominance was assessed until the morning; for the second example, on the number of EEG features examined multiplied by the number of areas in which they were assessed) to which Benjamini & Hochberg's FDR correction was then applied.

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  2. Evaluation Summary:

    Menicucci et al. investigate the implication of sleep in the maintenance of ocular dominance plasticity in adult humans. This is an interesting study as it shows that sleep can maintain the changes in ocular dominance obtained after applying an eye-path on the dominant eye for two hours. This contrasts with the rapid decline of these changes during quiet wake in darkness. The authors further report correlations between sleep oscillations and the magnitude of the plasticity effect. These results highlight a possible implication of sleep in a new form of plasticity

    (This preprint has been reviewed by eLife. We include the public reviews from the reviewers here; the authors also receive private feedback with suggested changes to the manuscript. The reviewers remained anonymous to the authors.)

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  3. Reviewer #1 (Public Review):

    In this article, the authors investigated the role of sleep and brain oscillations in visual cortical plasticity in adult humans. The authors tested the effect of 2 hours of monocular deprivation (MD) on ocular dominance measured by binocular rivalry. In the main MDN session, MD was performed in the late evening, followed by 2 hours of sleep, during which EEG was measured. After the sleep session, ocular dominance was measured, which was followed by 4 hours of sleep, then ocular dominance was measured again in the morning. The results show that the effect of MD was preserved 6 hours after MD. The effect of MD correlated with sleep spindle and slow oscillation measures. The questions asked by the study are timely and findings are important in understanding the visual cortical plasticity in human adults, but I have some concerns regarding the experimental design, analysis, and interpretation of the results, which are listed below.

    - The authors investigated EEG activities in the central and occipital regions. The results of the relationship between slow oscillations / sleep spindles and deprivation index are very interesting. However, it appears that the activities were averaged across hemispheres in the occipital region. Previous studies (e.g. Lunghi et al., 2011; Binda et al., 2018) have demonstrated that MD is associated with up-scaling of the deprived eye and with down-scaling of the non-deprived eye (page 11). I wonder whether sleep slow oscillations and / or spindles are modulated locally in the deprived occipital region? To answer the first question raised by the authors (how MD affects subsequent sleep), wouldn't it be important to compare between deprived vs. non-deprived regions?

    - To answer the second question (how sleep contributes to consolidation of visual homeostatic plasticity), the authors compared the deprivation index between two sessions, the main MDN and a control MDM session. The experimental designs for these two sessions were quite different. For example, MD was conducted in the evening in MDN, whereas it was conducted in the morning in MDM. Since there may be circadian effects on plasticity (Frank, 2016), the comparisons between these sessions may not be sufficient in investigating the effect of sleep itself (it could be merely due to circadian effect).

    - The authors argue that NREM sleep consolidates the effect of MD. However, consolidation may last days to months or even years (Dudai et al., 2015). Since the effect is gone in 6 hours or so, it may be difficult to interpret it as consolidation. Although the findings of the effects of sleep on ocular dominance plasticity are interesting, the interpretations of the results may need to be clarified or revised.

    Was this evaluation helpful?
  4. Reviewer #2 (Public Review):

    This manuscript is an interesting follow up on a substantial literature on the role of sleep in promoting critical period ocular dominance plasticity, and the role of sleep in promoting adult V1 plasticity following presentation of a novel visual stimulus. For nearly all of that literature (i.e. coming from cats and mice), the focus has mainly been on Hebbian mechanisms. The authors here propose to advance the field by investigating plasticity in adult human V1, which the authors consider to be homeostatic rather than Hebbian, and which the authors consider to be a form of sleep-dependent consolidation. This is an exciting goal, and the overall study designs and control will test the effects of brief MD and subsequent sleep or wake in the dark on V1 processing for the two eyes. However, the outcomes of the study suggest that the changes observed in V1 across sleep may actually be the opposite of consolidation - rather it is decay of an effect on V1 function caused by prior wake experience (MD), which disappears over subsequent hours. The authors claim differences due to sleep, but there is not a direct statistical comparison between sleep and awake-in-the-dark controls. There is also no quantification of sleep architecture across the sleep period, to determine whether REM or NREM play a role. Finally, while there are tests of changes in NREM oscillations with previous plasticity in wake, there are no direct tests of changes across sleep - i.e. the very changes that could be considered consolidation. Finally is also not clear that the decay of response changes is due to homeostatic plasticity - it could be just that- decay of plasticity that occurred previously. The terminology used - e.g. consolidation, homeostatic vs. Hebbian - don't seem well founded based on data.

    Was this evaluation helpful?
  5. Reviewer #3 (Public Review):

    In this study, Menicucci et al. induced plastic changes in ocular dominance by applying an eye-patch to the dominant eye (monocular deprivation, MD). This manipulation resulted in a shift toward even more dominance of the deprived eye, as assessed though a binocular rivalry protocol. This effect was stabilized during sleep whereas it quickly decreases in waking (in the dark). The authors interpret the MD effect as the resultant of cortical plasticity over primary visual areas and its maintenance during sleep as the consolidation of these changes. The authors thus connect their work to the literature on sleep consolidation. They further show that the magnitude of the MD effect is positively correlated with sleep markers that are involved in memory consolidation (slow oscillations and sleep spindles).

    However, I have first conceptual issues with this study. Indeed, previous findings on the replay of memories during sleep and their consolidation were mostly obtained in hippocampus-dependent forms of learning. Here, I do not really see what is it that would be replayed. Thus, I struggle understanding how rhythms, such as sleep spindles, that have been linked to the transfer of hippocampal memories to the neocortex, would be mechanistically associated with low-level plastic changes restricted to primary visual areas. In addition, the effects were observed over occipital electrodes, where sleep spindles are far fewer and lower in amplitude than other cortical regions. Furthermore, the association between MD-related plasticity and slow oscillations is interesting but, since these slow oscillations organize sleep slow waves, the lack of correlation with slow wave is surprising.

    Connected to these conceptual issues, I think the present work has some important methodological limitations. First of all, the analyses included a rather small number of participants, which could make some analyses, in particular correlational analyses, severely underpowered. Secondly, the approach used to explore the correlation between plasticity and sleep features focused on subset of electrodes (ROI) defined a priori. It is therefore difficult to conclude on the specificity of the results. Given the topographical maps provided by the authors, I am wondering if a more exhaustive analysis of the effect at the electrode level could not yield more robust findings. Finally, given the number of features tested, I think it is important to clarify the strategy used to correct for multiple comparisons.

    Was this evaluation helpful?