Adult neural stem cells and neurogenesis are resilient to intermittent fasting

  1. Rut Gabarró‐Solanas
  2. Amarbayasgalan Davaatseren
  3. Justus Kleifeld
  4. Tatjana Kepčija
  5. Thomas Köcher
  6. Albert Giralt
  7. Iván Crespo‐Enríquez
  8. Noelia Urbán

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Abstract

Intermittent fasting (IF) is a promising strategy to counteract ageing shown to increase the number of adult‐born neurons in the dentate gyrus of mice. However, it is unclear which steps of the adult neurogenesis process are regulated by IF. The number of adult neural stem cells (NSCs) decreases with age in an activation‐dependent manner and, to counteract this loss, adult NSCs are found in a quiescent state which ensures their long‐term maintenance. We aimed to determine if and how IF affects adult NSCs in the hippocampus. To identify the effects of every‐other‐day IF on NSCs and all following steps in the neurogenic lineage, we combined fasting with lineage tracing and label retention assays. We show here that IF does not affect NSC activation or maintenance and, that contrary to previous reports, IF does not increase neurogenesis. The same results are obtained regardless of strain, sex, diet length, tamoxifen administration or new‐born neuron identification method. Our data suggest that NSCs maintain homeostasis upon IF and that this intervention is not a reliable strategy to increase adult neurogenesis.

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  1. Version published to 10.15252/embr.202357268
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    Reply to the reviewers

    Reviewer #1 (Evidence, reproducibility and clarity (Required)):

    Summary:

    In this study, mice were exposed to a specific form of so-called Intermittent Fasting (IF) and the effects of IF on adult neogenesis in the hippocampus were determined. The specific IF protocol used had no effect on activation, proliferation, or maintenance of adult Neural Stem Cells (aNSCs) and displayed a decrease in number of new neurons in the neurogenic niche but only after 1 month of the IF protocol. These results contrast previously published results from multiple studies that concluded that IF promotes survival of new neurons and by extension promote adult neurogenesis. The unresponsiveness of aNSCs or their immediate cell progeny, the Intermediate Neural Progenitors (IPCs), to IF is a novel finding. The authors make several relevant points in the discussion about the publication bias towards positive results (or omission of negative results), which may reinforce established dogmas. However, the presented results did not convincingly demonstrate that the absence of effects of IF on aNSCs or adult neurogenesis is simply not a result of a specific IF paradigm, which is not robust enough to elicit changes in adult neurogenesis. In other words, there is a lack of positive controls and alternative protocols that would rule out that the observed absence of effects is not a consequence of type II error (the error of omission), or more colloquially, a consequence of false negatives.

    We thank the reviewer for acknowledging the importance and novelty of our findings. On them being the result of a specific IF paradigm, we must point out that we used the same IF paradigm as in previous studies that had shown changes in neurogenesis upon IF. We do not claim that IF is unable to increase neurogenesis in all conditions, but report that IF is not a reliable method to increase adult neurogenesis (in particular, every-other-day intermittent fasting with food re-administration in the evening). We have repeated the experiment multiple times in different strains, always with enough animals to make our experiments conclusive and we never observed an increase in adult neurogenesis, effectively ruling out that our results are a false negative. Of note, even if other protocols might indeed increase neurogenesis (which we never claimed cannot) that would not make our results a false negative.

    Major Comments:

    Protocol-driven absence of effects: The absence of IF effects on aNSCs and IPCs observed in this study does not lend it the authority to conclude that aNSCs are resilient to IF or all IF paradigms and protocols. The absence of IF effects on aNSCs and neurogenesis could be specifically related to the chosen IF paradigm. Indeed, not all previous studies that observed IF-driven effects on adult neurogenesis used the same "night-time every-other-day fasting" protocol chosen in this study. For example, Brandhorst et al., 2015 (cited in this paper) used 4 days of IF 2x per month and observed an increase of DCX+BrdU+ cells. On the other hand, certain previous studies used the same or similar IF protocol used here, but often with longer duration or with a post-fasting ad libitum feeding period, which may be responsible for the pro-neurogenic or pro-survival effects. In fact, the authors acknowledge this in the discussion (page 7, lines 289-290 and 292-294). Why would the authors then not include similar feeding/IF paradigm in their study and determine if these would generate effects on survival of new neurons but also on aNSCs and/or IPCs?

    As just stated above, we never claimed that aNSCs are resilient to all IF paradigms. We refer to fasting in general in the introduction but quickly focus on every-other-day fasting throughout the paper and directly compare our results only to similar IF paradigms. We chose the most commonly used IF paradigm that had been shown to increase adult neurogenesis. As the reviewer points out, we speculate in the discussion that a refeeding period may explain the differences between our results and others. This is because a post-fasting ad libitum period was introduced in the study published in Dias et al. 2021. We are currently analysing a new experiment in which we replicate the IF protocol in that study, which we will include in our revised version.

    In addition, the authors acknowledge that the chosen IF paradigm may have affected the stress levels or behaviour of mice (page 9, lines 372-378). Why did they not test if their IF protocol does not increase stress or anxiety of mice by simple behaviour tests such as open field or elevated T maze?

    While testing all possible causes for the lack of positive results in our experiments is not viable, we do agree with the reviewer that stress levels might indeed influence the outcome of the experiments. We will collect blood from ad libitum-fed and fasted mice to analyse the levels of stress hormones (e.g. corticosterone). The results will be included in our revised version. These measurements will give us a more accurate reading of stress levels than behavioural tests. Of note, regardless of the outcome of this experiment, our conclusions will remain identical. We will not be able to compare stress levels with previous publications, as they were not tested. And if the protocol did increase stress levels, it would still argue that IF is not a reliable method to increase neurogenesis (as presumably might or might not increase stress to levels that affect neurogenesis).

    Alarmingly, the used IF protocol does not result in changes in final weight or growth curves (S.Fig.2), which is surprising and raises a question the used IF protocol is robust enough or appropriate.

    We were also surprised by the lack of change in the final weight our IF mice respect to control. Differences in final weight between different labs despite using the exact same protocol are one of the reasons why we conclude that this IF paradigm is not a robust intervention. However, we are not the first ones to report little or no difference in weight upon IF in C57BL6/J mice (Goodrick et al., 1990 and Anson et al., 2003) and this would not be a reason to dismiss the experiment since the benefits in crucial circulating factors induced by IF seem to be independent of weight loss (Anson et al., 2003).

    Finally, the authors acknowledge that their own results do not support well-established findings such as aging-related reduction in number of aNSCs (page 4, lines 177-179). This again questions whether the selected protocols and treatments are appropriate.

    As we already discuss, we believe this might be due to a difference between strains in the time when aNSC numbers decline. Nevertheless, we will complement our current data by counting the number of aNSCs at 1 and 3 months post-tamoxifen (3 and 5 month old mice) using GFAP, Sox2 and Nestin triple stainings (as suggested by another reviewer).

    Lack of topic-specific positive controls: The authors successfully demonstrated that the used IF protocol differentially impacts the adipose tissue and liver, while also inducing body weight fluctuations synchronized with the fasting periods. However, these peripheral effects outside the CNS do not directly imply that the chosen IF protocol is robust enough to elicit cellular or molecular changes in the hippocampus. The authors need to demonstrate that their IF protocol affects previously well-established CNS parameters associated with fasting such as astrocyte reactivity, inflammation or microglia activation, among other factors. In fact, they acknowledge this systemic problem in the discussion (page 8, lines 359-360).

    We fully agree with the reviewer in that even though the chosen IF protocol induces peripheral effects, it is not robust enough to elicit cellular or molecular changes in the hippocampus, and this is precisely the message of our paper. We have looked for references showing the influence of IF on astrocyte reactivity or microglia activation, but the studies we found so far look at the effects of IF and other forms of fasting in the CNS in combination with pathologies such as Alzheimer’s disease, Multiple Sclerosis, physical insults or aging (Anson et al., 2003; Chignarella et al., 2018; Rangan et al., 2022; Dai et al., 2022. Reviewed in Bok et al., 2019 and Gudden et al., 2021). Fasting seems to reduce astrocyte reactivity, inflammation or microglia activation in these pathological situations respect to the same pathology in ad libitum mice, but its effect in control, healthy mice is far less clear. In fact, the only reference that we could find where healthy mice were included in the analysis showed that these benefits only happened in the context of the injury (Song et al., 2022).

    Problematic cell analyses: Cell quantification should be performed under stereological principles. However, the presented results did not adhere to stereological quantification. Instead, the authors chose to quantify specific cell phenotypes only in subjectively selected subsets of regions of interest, i.e., the Subgranular Zone (SGZ). This subjective pre-selection may have been responsible for the absence of effects, especially if these are either relatively small or dependent on anatomical sections of SGZ. For example, IF may exert effects on caudal SGZ more than on rostral SGZ. But if the authors quantified only (or predominantly) rostral SGZ, they may have missed these effects by biasing one segment of SGZ versus other. The authors should apply stereological quantification at least to the quantification of new neurons and test if this approach replicated previously observed pro-survival effects of IF. Also, the authors should describe how they pre-selected the ROI for cell quantification in greater details.

    We did analyse only the more septal region of the hippocampus, which we will make clear in the text. As also suggested by other reviewers, we will include stereological counts of the neuronal output of aNSCs in the revised version. As for selecting the SGZ for aNSC counts, this is the standard in the field, as one of the criteria to identify aNSCs is precisely the location of their nucleus in the SGZ. Neuroblasts and new neurons were counted both in the SGZ and the granule cell layer. There was no subjective pre-selection of areas of interest since we counted the whole DG in each section and not a specific random region.

    Alarming exclusion of data points: There appears to be different number of data points in different graphs that are constructed from same data sets. For example, in the 3-month IF data set in Figure 4, there are 14 data points for the graph of Ki67+ cells (Fig.4B), but 16 (or 17) data points for the graph of DCX+ cells (Fig.4D). How is that possible? If data points were excluded, what objective and statistical criteria were applied to make sure that such exclusion is not subjective and biased? In fact, the authors state that "Samples with poor staining quality were also excluded from quantifications" (page 12, line 528-529). Poor preparation of tissue is not only suboptimal but not a valid objective reason for data point exclusion. This major issue needs to be explained and corrected.

    As we disclose in the methods, those stainings that did not work were excluded. This was done always before counting. Different samples were used in different counts because of the variability of staining quality between different antibodies. We will look back into the samples that failed in at least one of the stainings and exclude them from all counts, so that only samples for which all stainings worked are considered. These revised graphs will be provided in our revised version of the manuscript.

    Different pulse-and-chase time-points: One of the reasons why this study has found that aNSCs may not be responsive to IF could be the use of less appropriate pulse-and-chase time-points either after EdU or after Tamoxifen for cell lineage tracing. The authors observed that IF has negative effects on new neurons initially (Fig.4F). Similarly, it is well established that voluntary physical exercise affects SGZ adult neurogenesis only during the first 2 weeks. After this period, the neurogenic effects of exercise are diminished beyond observational detection (i.e., van Praag's and Kempermann's papers in the past 25 years). These two arguments suggest that the observed absence of aNSC responsiveness might be a consequence of the chosen EdU administration and the EdU pulse should not be administered 15 days after Tamoxifen/IF protocol start but earlier, in the first week of the IF protocol. In fact, the decreased number of new neurons during the initial IF phase may not be only a consequence of reduced survival but of higher aNSC quiescence during the first week of the IF protocol.

    We fully agree with the reviewer that BrdU or EdU pulses can give a biased view of the effects of any intervention on neurogenesis and that the EdU and Tamoxifen protocols would not allow us to detect an increase in neurogenesis during the first few days of IF. We cannot rule out that IF has a transient effect on aNSCs at some point of the treatment, but this hypothetical effect does not seem to have any consequences on neuronal output or aNSC maintenance. As for the effects on neurogenesis in the longer IF treatments, we used the same EdU protocol as in previous publications: administration after 2/3 months of IF and analysis after one month of chase.

    Discussion needs more specificity and clarity: The authors claim that the absence of IF effects on neurogenesis is multi-layered (including the influence of age, sex, specific cell labelling protocols etc.) but they do not specifically address why certain studies did find IF-driven neurogenic effects while they did not. In addition, some statements and points in the discussion are not clear. For example, when the authors refer to their own experiments (page 8, lines 331-334), it is not clear, which experiments they have in mind.

    We will double check our discussion and improve its clarity and direct comparison to other studies.

    Minor comments:

    Change in the title: The authors have shown that a very specific IF protocol does not affect aNSCs but initially decreases number of new neurons in SGZ. The title should reflect this. For example, it could state "Specific (night-time every-other-day) fasting does not affect aNSCs but initially decreases survival of new neurons in the SGZ".

    We find our title, together with the abstract, clearly and faithfully represent our findings and would rather prefer to keep our current title unmodified.

    Data depiction: Data in 3 datasets were found not normally distributed (Fig. S5A, B and S6A) and were correctly analysed with non-parametric tests. However, the corresponding graphs wrongly depict the data as mean +/- SD while they should depict median +/- IQR (or similar adequate value) because non-parametric statistical tests do not compare means but medians.

    We thank the reviewer for spotting this, we will correct the graphs in Fig. S5A, B and S6A.

    Statistical analysis: For ANOVA, the F and p values are not listed anywhere. The presented asterisks in the graphs are only for non-ANOVA or ANOVA post-hoc tests. This does not allow to judge statistical significance well and should be corrected.

    Again, thanks for spotting this, we will include them.

    Asymmetric vs Symmetric cell divisions: Representative images in Fig.2B suggest that IF may affect the plane of cell division for the Type-1 aNSCs. The plane of cell division is an indirect indicator of symmetric vs asymmetric (exhaustive vs maintaining) modes of cell division. Is it possible, IF influences this, especially during the first week of IF (see major comment 5)?

    This is an interesting hypothesis. However, since we do not see any effects on aNSC maintenance, it is unlikely that IF produces any long-lasting effects on the mode of division of aNSCs. In general, we did not notice a difference in the plane of division of aNSCs between control and IF mice, although we did not systematically test for this (would require specific short EdU pulses to capture aNSCs in M-phase). In Figure 2B, the two stem cells shown in the control are unlikely to be the two daughter cells after the division of one aNSC, as one of them is positive and the other negative for Ki67. We only pointed to the second one to show a Ki67-negative aNSC. We will emphasize this in the figure legend.

    Improved and more accurate citations: Some references are not properly formatted (e.g., "Dias", page 7, line 288). Some references are included in generalizing statements when they do not contain data to support such statements. For example, Kitamura et al., 2006 did not determine the number of new neurons (only BrdU+ cells) in the SGZ, yet this reference is included among sources supporting that IF "promote survival of newly born neurons" (page 2, line 60). Authors should be more careful how the cite the references.

    Thanks for spotting these mistakes, we will correct them and check again all our references. As for the sentence where the Kitamura paper is cited, most of the other references also use only BrdU+ cells while concluding that IF enhances the survival of new neurons. We will change new neurons for new cells to reflect this, which we already bring up in the discussion (see also extended discussion in previous BioRxiv version).

    How do the authors explain that they observe 73-80% caloric restriction and yet the final body weight is not different between IF and control animals? Would it suggest that the selected IF protocol or selected diet are not appropriate (see major point 4)?

    We also found this surprising and were expecting a change in overall activity in IF mice, which we did not observe. Many factors might play a role, like, as the reviewer suggests, changes in stress levels, which we will measure and show in the revised version.

    Given that aNSCs rely more on de novo lipogenesis and fatty acids for their metabolism as shown by Knobloch et al., Nature 2013 and given the interesting changes in RER with the IF shown in this study, it would be interesting to see whether there are differences in Fasn expression in aNSCs between control and IF animals (see minor point 4).

    This is an interesting suggestion but given that we see no effect on aNSCs, we find it’s unlikely and unnecessary to test for Fasn expression differences in our IF protocol.

    Determining apoptosis in the SGZ by picnotic nuclei (Figure S6A) should be supplemented by determining the number and/or proportion of YFP+ cells positive for the Activated Caspase 3.

    We previously found that counting picnotic nuclei is a more accurate and sensitive readout of cell death in the DG, as cells positive for caspase 3 are extremely rare due to the high efficiency of phagocytosis of apoptotic cells by microglia (see Urbán et al., 2016).

    Reviewer #1 (Significance (Required)):

    General assessment:

    This study concludes that aNSCs do not respond to the intermittent fasting. This expands and supplements previous findings that suggest that the intermittent fasting promotes adult neurogenesis by increasing survival and/or proliferation in the Subgranural Zone. The study is well designed, however, over-extends its conclusions beyond a specific fasting paradigm and does not acknowledge serious limitations in the experimental design and analyses. In fact, until major revision is done, which would rule out that the absence of effects of fasting on aNSCs is not due to false negative results, many conclusions from this study cannot be accepted as valid.

    Advance:

    As mentioned above, the study has a potential to advance our understanding of how fasting affects neurogenesis and fills the knowledge gap of how fasting specifically affects the stem cells. However, unless the study addresses its limitations, its conclusions are not convincing.

    Audience:

    This study would be particularly interesting for the niche readers from the neurogenesis field. However, the study can also be interesting for researchers in metabolomics and dietology.

    My expertise:

    adult neurogenesis, neural stem cells, dietology, metabolism

    We disagree with the reviewer and find our conclusions well balanced, as we acknowledge our results are to be compared only with similar IF protocols. We also do not believe our results can be attributed to a false negative, as we consistently observe the same with different strains and protocols, always with sufficient animals to make our counts conclusive.

    We nevertheless thank the reviewer for assessing our paper and for the advice to improve it. We hope that the reviewer will maintain the same level of scrutiny and scepticism with all IF-related papers.

    Reviewer #2 (Evidence, reproducibility and clarity (Required)):

    In this manuscript, Gabarro-Solanas et al. question the suitability of IF (Intermittent fasting - non-pharmacological strategy to counteract ageing, which has been previously shown to increase the number of adult-born neurons in the dentate gyrus of mice) as a pro-neurogenic intervention, since IF treatment did not stimulate adult hippocampal neurogenesis, neither at the stem cell level nor on immature and/or dividing neurons. The Authors used a tamoxifen inducible transgenic model (Glast-CreERT2;RYFP mice) to trace neural stem cell lineage and found that IF did not enhance neural stem cell proliferation, nor the abundance of immature, DCX+ neurons. Three-months of IF failed to increase the number of new adult-born neurons (NeuN+/YFP+), while one month of IF significantly reduced the number of new adult-born neurons.

    The study appears technically sound, including many different approaches in order to reach its conclusions.

    For instance, tamoxifen has been reported to impair various physiological processes, including neurogenesis (Smith et al., 2022), and most studies on adult hippocampal neurogenesis use the C57BL/6J strain of mice; hence, the use of Tamoxifen or that of the GlastCreERT2;RYFP model may have underscored these observations. However, to account for this potentially confounding factor, the Authors characterised the effect of their IF treatment in C57BL/6j mice, also reporting no evident effects of IF as a pro-neurogenic intervention.

    I think the study was carefully planned and the analyses well done. Several possible variables were considered, including sex, labelling method, strain, tamoxifen usage or diet length. Several controls were performed in other organs and tissues (liver, fat) to establish the fasting protocol and to check its effects.

    Data are presented in a clear way. Quality of images is high level.

    In general, it appears as a highly reliable paper reaching an authoritative conclusion for the absence of effect of IF on adult neurogenesis.

    Major comments:

    I think that the key conclusions are convincing and no further experiments are required.

    The methods are presented in such a way that they can be reproduced, and the experiments adequately replicated with proper statistical analysis.

    We thank the reviewer for the encouraging remarks and the appreciation of our efforts.

    Minor comments:

    Prior studies are referenced appropriately, both regarding the IF protocols and the adult neurogenesis modulation.

    Line 288 - a reference is incomplete (Dias); integrate with: (Dias et al., 2021)

    We will re-format the reference, thanks for spotting the mistake.

    There is one concept that is not expressed in the manuscript. Maybe it is not strictly necessary, but I think can be useful to mention it here. It is the fact that most information currently available strongly indicates that adult neurogenesis in humans is not present after adolescence. Of course the research described here is carried out on mice, and in the manuscript it is stated many times that adult hippocampal neurogenesis is strongly decreasing with age, also due to age-related stem cell depletion. Yet, it seems that in humans the exhaustion of such a process can start after adolescence. We know that a sort of controversy is currently present on this subjects, because DCX+ neurons can be detected in adult and old human hippocampi. Yet, it is also clear that there is no substantial cell division (stem cells are depleted) to sustain such hypothetical neurogenesis. Hence, it has been hypothesized that non-newlyborn, "immature" neurons can persist in the absence of cell division, as it has been well demonstrated in the cerebral cortex (see La Rosa et al., 2020 Front Neurosci; Rotheneichner et al., 2018, Cereb Cortex).

    This point can be important in the case someone want to use dietary approached such as IF (or any other pharmacological treatment) to stimulate neurogenesis in humans.

    We agree with the reviewer and also find this a very interesting and timely topic. However, we find it a bit far from our results and would prefer not to comment on it in the context of the current paper.

    Reviewer #2 (Significance (Required)):

    The significance of this study relies on the fact that adult neurogenesis field (AN) has been often damaged by the search of "positive" results, aiming at showing that AN does occur "always and everywhere" and that most internal/external stimuli do increase it. This attitude created a bias in the field, persuading many scientists that a result in AN is worthy of publication (or of high impact factor publication) only when a positive result is found.

    Personally, I found particularly meaninful the last sentences of the Discussion (reported below), which might seem "off topic" in a research paper, while - I think - underline the real significance of the manuscript:

    "In addition, publication bias might be playing a role in skewing the literature on fasting and neurogenesis towards reporting positive results.

    In some reviews, even studies reporting no effect are cited as evidence for improved neurogenesis upon IF. Reporting of negative results, especially those challenging accepted dogmas, and a careful and rigorous evaluation of the publications cited in reviews are crucial to avoid unnecessary waste of resources and to promote the advancement of science."

    Reviewer field of expertise - keywords: adult neurogenesis, brain structural plasticity, non-newly born immature neurons, comparative neuroplasticity.

    We are very happy that the reviewer shares our concern with the biased publication of positive results in the field. We hope our work (and that of Roberts et al., 2022) will encourage other labs to publish their negative results.

    Reviewer #3 (Evidence, reproducibility and clarity (Required)):

    In this manuscript, Gabarro-Solanas et al. investigate the effects of intermittent fasting (IF) on adult hippocampal neurogenesis in young adult mice. IF has been reported to increase the number of adult-born neuron in the hippocampus, a region that is important for learning and memory. However, it is not well understood what stages of adult neurogenesis are regulated by IF. To address this, the authors utilized lineage tracing and label retention assays in mice undergoing an IF diet. The authors used 2 months old Glast-CreERT2;RYFP mice in combination with Edu label retention to characterize adult NSCs and placed these mice on 1 and 3 months of IF. Despite seeing a decrease in neural stem cell proliferation with age, the authors did not observe a change due to diet. The authors then used immunohistochemistry to characterize changes in cell proliferation, neuroblasts, and new neurons following 1 month and 3 months of IF. Only 1 month of IF seemed to decrease the number of new neurons; however, by 3 months the neuronal output was the same. There were no differences in neuroblasts or cell proliferation due to diet. Gabarro-Solanas et al. conclude that IF transiently and mildly inhibits neurogenesis. Due to contradicting results, the authors then try to determine what variables (sex, labeling method, strain, tamoxifen usage, or diet length) could be affecting their data. The authors saw no substantial differences due to any of their variables.

    Major Points

    The authors analyze NSCs homeostasis and neurogenesis in young adult mice and do not observe any significant changes with their chosen alternate day intermittent fasting paradigm. However, a lot of the data and cell counts appears to be highly variable between animals in the same group. At times, there is an order of magnitude difference between the highest and lowest counts (e.g. Figure 2C,E). According to the method section, it appears that the authors predominantly analyzed a single DG (section?) for most immunostainings, which may explain the large variability in their data. If this is indeed the case, it is insufficient to quantify only a single section for each animal. The authors should quantify several DG sections for each mouse from a pre-defined range along the rostral-caudal axis of the hippocampus in accordance with a standard brain reference atlas. There are also several quantifications, especially of Ki67 where several individuals appear to have no Ki67+ (Figure 3B, 6D) NSCs. These findings are surprising given the still young age of these mice and may be another reflection of the limited brain sections that were analyzed.

    The counts are indeed very variable. The counts were made on 1 to 4 DG sections (counted in full), depending on the staining. We will more clearly disclose this information in the revised version. In addition, we will re-count the neuronal output after fasting using stereology. Regarding the very low number of Ki67+ aNSCs, our counts are lower than those in other publications because we are much more stringent with our aNSC identification. Instead of using merely Sox2 (which also labels IPCs), we rely on the presence of a radial GFAP+ process.

    There appear to be significant cutting or imaging artifacts across most fluorescent images further raising concerns regarding the accuracy of the quantifications (e.g. Figure 3D, 4C,E, 6B) and publication quality of the images and data. Importantly, uneven section thickness, either from cutting artifacts or imaging issues, may lead to inaccurate cell quantifications a could, possibly, account for the high variability. This issue would further exacerbate concerns regarding the quantification of a single DG section for each animal.

    We only processed those samples that passed our QC after sectioning, meaning any unevenly cut brains were never considered (or stained). The stitched images do show artifacts (lower signal in the image junctions), particularly in the NeuN staining. However, this did not affect quantifications, as the measured levels were always clearly above the threshold to consider a cell positive, regardless of the position within the image. The images were cropped to improve the visualisation of NSCs, and to avoid the display of empty tiles. A low magnification image will be provided in the revised version to show that there were no staining artifacts.

    It is unclear how NSCs were counted in the B6 mice (Fig 6D,E). The authors only provide a description for the Glast-CRE mice, where they used YFP labeling and GFAP. We assume they performed Sox2/GFAP or Nestin labeling, however, this is not clear at all. The authors should describe their methodology and provide representative images.

    We used GFAP, location and morphology to count aNSCs in non-YFP mice. We will make this clear in the text and will also add one more count using Sox2, GFAP and Nestin to identify aNSCs.

    NSC populations represent a heterogenous group of stem cells with different replicative properties. As such, the Glast-Cre approach used for the majority of this study may represent a specific subset of NSCs. In line with the previous point, we recommend the authors complement their NSC counts with Sox2/GFAP and Nestin immunostainings.

    aNSCs labelled with Glast-Cre are the great majority of aNSCs (>90%) in both ad libitum fed and fasted mice. The data will be included in the revised version. Nevertheless, we will add counts using Sox2, GFAP and Nestin for key experiments.

    Stress is a significant negative regulator of neurogenesis. Is it possible that the IF mice display higher stress level which could counteract any beneficial effects of the IF intervention. The authors should provide some measures of stress markers to rule out this potential confounding factor in their IF paradigm.

    This is a great suggestion. We will collect blood from control and fasted mice and measure the levels of stress factors (e.g. corticosterone). We will include the data in our revised version.

    Minor Point

    The authors state that "Experimental groups were formed by randomly assigning mice from different litters within each mouse strain and all experiments were conducted in male and female mice". Given that neurogenesis, especially at young ages, is highly sensitive to the exact age of the mice, the authors should provide a rationale why animals from different litters instead of littermate controls were used in these experiments.

    Littermate controls were always used in the experiments. But also, more than one litter was used for each experiment, since one litter was never generating enough mice for the experiments. We will clarify this point in text.

    Currently, the statistical tests are only described in the method section, however it would be helpful if this information to be integrated into the figure legend as well. Additionally, the authors provide individual data points for some but not all bar graphs (eg Figure 1D).

    We will consider including the statistical information in the figure legend, provided there is not a maximum length for figure legends. In the case of figure 1D, data points are not shown because of how the food intake was calculated: as an average per cage instead of per animal (included in the materials and methods). We therefore do not consider it useful to show the datapoints in the final version of the manuscript, but will provide them for the reviewer.

    Cell counts per AU is a rather unorthodox unit. With a representative selection of tissue for each animal, the authors could avoid the need to normalize to the DG length and may be able to extrapolate an estimate of cell counts for the entire DG instead.

    Thanks for the suggestion. Our arbitrary units (AU) were in fact already equivalent to cells per mm of DG, and we have updated our graphs to reflect this.

    In Figure 4D, the authors highlight a few NSC with arrowheads. At a quick glance this is rather confusing as it appears that the authors only counted 3 NSCs in each picture. It may be a better option to show a zoomed in picture to highlight an example of a representative NSC.

    Examples of representative NSCs are already shown in Fig 2. With this image, we intended to show a larger number of NSCs. We realise the arrows only pointed to some of them, making the message confusing. We will consider removing them from the figure in the revised version.

    In Supplementary Figure S6, the authors should complement the quantification of the nuclei with representative images.

    We will include representative images in Figure S6.

    For the daytime IF, did the authors assess weights, food intake, RER as well liver/fat measurements similar to night-time IF? If so, this data should be provided in the supplement.

    We do have data for the daytime IF in the metabolic cages, which was taken from mice housed in groups (during the preliminary phase of our study). We also have the weight and data on neurogenesis, which we will show as a supplement.

    Reviewer #3 (Significance (Required)):

    The authors are commended for compiling a manuscript on what is commonly considered 'negative data', that, at the same time, are also contradicting independent reports on the effects of IF on neurogenesis. The studies outlined in this manuscript are comprehensive and mostly well designed. Given the broad, growing interest in dietary restriction as an aging intervention the study is timely.

    We thank the reviewer for the positive assessment of the significance of our work.

    __Reviewer #4 __(Evidence, reproducibility and clarity (Required)):

    Summary:

    In this manuscript, Gabarró-Solanas et al. tested the effect of intermitted fasting (IF, every-other-day fasting) on adult neural stem cells and neurogenesis. They demonstrate that the paradigm they have used does not affect NSC activation or maintenance, and does also not promote neurogenesis. As previous reports showed increased neurogenesis with IF, the authors controlled for various parameters such as mouse strain, sex, and diet length. They also used different methods of identification of newborn neurons, such as tamoxifen-induced lineage-tracing versus birth-dating with thymidine-analogues to substantiate their findings.

    Major comments:

    This study is very well done with carefully designed and controlled experiments. The manuscript reads nicely and the data are presented in a clear way, making it easy to follow. The authors have done a "tour-de force" to rule out confounding factors that might influence their findings that IF does not affect NSCs nor neurogenesis.

    The claims and conclusions are supported by the data. The methods are clearly described and should allow to reproduce the data independently. The number of replicates (i.e. the number of mice analyzed) is impressive and statistical analysis is adequate.

    The major findings, namely that the chosen IF does not affect NSCs and neurogenesis is not in line with some previous studies. Despite a careful ruling out of potentially confounding factors (see also "significance" below), it remains unclear why other studies have found an increase in neurogenesis with IF. As each of these studies has some specific experimental design, it is difficult to judge these data in the context of previous data without going through all the details of the other studies. It would thus be a great help for the reader if the authors could provide a table or schematic, which lists the major parameters of each of these studies, such as detailed paradigm of IF, age of mice at start, sex, duration of the intervention, method of identification of NSCs and neurogenesis etc.

    This is a very good suggestion, and we had already created such a table. We, however, consider that it might be better suited for a review on the effects of IF on neurogenesis than for this work. We will include the table in our response to the reviewers together with our revised version.

    Two points that the authors have not discussed might also be worth mentioning in the discussion part:

    1.) The mice in the night-time IF were single caged, could there be a potential negative effect on neurogenesis that would mask the presumably beneficial effect of IF? Although the controls were also single caged, the stress of social isolation might play a role?

    The mice were only single caged for the metabolic phenotyping, but not for the neurogenic counts. We will make this clearer in the text. In any case, we do agree that stress might play a role and we will measure stress levels in the control and fasted mice and will include this data in the revised version.

    2.) The IF mice gained the same weight over time (Fig. S2), but had a ~20% reduction in overall calory intake. This would be explainable by a reduction in energy expenditure, but the overall activity was also not significantly changed (Fig. S1). Can the authors speculate why they reach the same weight with less calories?

    We also found this surprising and were expecting a reduction in the overall activity of the fasted mice. We do not have an explanation for this discrepancy, but perhaps stress levels might explain part of it (we will check stress levels in the revised version). We will also look at whether energy expenditure and activity levels changed over time.

    Minor comments:

    1.) It would be nice to replace the arbitrary units (AU) in the graphs were this is used (e.g. Fig. 2F, 3C, 4B, D and F etc) to the actual number of cells per a certain µm DG, so that the number of cells can be put in context and compared between the figures.

    Yes, our AU already corresponded to mm and we will update our figures accordingly.

    2.) Fig 3 D: can the authors also show the Ki67 channel to illustrate how it looks after a 3 month IF?

    We find it does not help much, as Ki67+ cells are mostly IPCs and that data is already shown in Fig. 4A. We will nevertheless include the image in our response to the reviewers together with our revised version.

    3.) Fig.4E: the NeuN staining looks strangely interrupted, this might be due to tile-stitching? In that case, it would be better to either only show one segment or to try to get a better stitching algorhythm.

    It is indeed because of the tile-stitching and uneven illumination. However, this did not affect the counts, as already discussed in the response to reviewer #3 (major point #2).

    4.) Fig.6 D shows a minus axis in Y-axis, this should only been shown from 0 to positive values, as it is a percentage of cells and cannot be negative.

    True, thanks for spotting this. We will correct the graphs in the revised version.

    5.) Fig.6 B: the same problem with the NeuN staining as mentioned under point 3. This should be improved.

    As with point 3, the stitching did not affect the quantification. We find it more accurate to show the image with the stitching, as that was the one used for quantification. We will provide a new picture with lower magnification to better show the quality of the staining.

    6.) Fig. S6B: maybe add a comment in the result part or in the figure legend that a 10 day chase after an EdU pulse is not the classical protocol to look at mature NeuN positive neurons. But apparently enough newborn neurons were already NeuN positive for this quantification.

    We fully agree 10 days is not the standard for neuronal identification. We did find neurons after the 10-day chase but in low numbers. We will add a comment in the text of the revised version to clarify this.

    7.) The authors refer to personal communications with M. Mattson and S. Thuret to underline that circadian disruption is not enough to explain the differences (line 367 onwards). Can they refer the reader to published data instead?

    While the results are published in their papers, the methods did not specify the time at which the food was added/removed for the IF protocol. That is why we refer to personal communication.

    Further showing that disruption of circadian rhythms is not enough to explain the difference in outcome of the IF protocol, we will show the data for the 1-month daytime IF, which again does not increase adult neurogenesis (reviewer #3, minor point #6).

    Reviewer #4 (Significance (Required)):

    Given the great interest in the seemingly positive effects on health of IF in general, and also for increasing neurogenesis, it is important to better understand the mechanism of this intervention. The study by Gabarró-Solanas et al. clearly demonstrates that IF is not a universal, "works all the time" way of increasing neurogenesis. The study is very well done, with well controlled and measured parameters. It shows that a physiological interference such as IF might depend on many factors and might be less robust across laboratories than anticipated. This study is a very good example that all the details of the experimental settings need to be taken into consideration and are ideally reported with every IF study. It is also a good example how to follow up "no effect" data in a way that they are conclusive.

    The significance of this study is to point out that IF as a strategy to increase neurogenesis needs to be reconsidered. It raises the questions how IF can be beneficial in some studies and not in others, asking for more experiments to better understand the detailed mechanisms of IF action. In a systematic approach, this study rules out some of the potentially confounding factors and shows that at least with the chosen IF paradigm, these factors are not the reason for not seeing increased neurogenesis. The study is thus of clear interest for the neurogenesis field and will also need to be considered by the broader field of IF research, although it speaks against the beneficial effects of IF. It might have the potential to bring together the different study authors who did or did not see increased neurogenesis with IF and discuss together the non-published details of their study design to advance the field.

    We thank the reviewer for the positive assessment of our work and for acknowledging its importance for the broader field of IF research.

    List of references used in the response to reviewers:

    Anson, R. M. et al. Intermittent fasting dissociates beneficial effects of dietary restriction on glucose metabolism and neuronal resistance to injury from calorie intake. Proceedings of the National Academy of Sciences 100, 6216–6220 (2003).

    Bok, E. et al. Dietary Restriction and Neuroinflammation: A Potential Mechanistic Link. International Journal of Molecular Sciences 20, 464 (2019).

    Cignarella, F. et al. Intermittent Fasting Confers Protection in CNS Autoimmunity by Altering the Gut Microbiota. Cell Metabolism 27, 1222-1235.e6 (2018).

    Dai, S. et al. Intermittent fasting reduces neuroinflammation in intracerebral hemorrhage through the Sirt3/Nrf2/HO-1 pathway. Journal of Neuroinflammation 19, 122 (2022).

    Dias, G. P. et al. Intermittent fasting enhances long-term memory consolidation, adult hippocampal neurogenesis, and expression of longevity gene Klotho. Mol Psychiatry 1–15 (2021).

    Goodrick, C. L., Ingram, D. K., Reynolds, M. A., Freeman, J. R. & Cider, N. Effects of intermittent feeding upon body weight and lifespan in inbred mice: interaction of genotype and age. Mechanisms of Ageing and Development 55, 69–87 (1990).

    Gudden, J., Arias Vasquez, A. & Bloemendaal, M. The Effects of Intermittent Fasting on Brain and Cognitive Function. Nutrients 13, 3166 (2021).

    Lee, J., Seroogy, K. B. & Mattson, M. P. Dietary restriction enhances neurotrophin expression and neurogenesis in the hippocampus of adult mice. Journal of Neurochemistry 80, 539–547 (2002).

    Rangan, P. et al. Fasting-mimicking diet cycles reduce neuroinflammation to attenuate cognitive decline in Alzheimer’s models. Cell Reports 40, 111417 (2022).

    Roberts, L. D. et al. The 5:2 diet does not increase adult hippocampal neurogenesis or enhance spatial memory in mice. 2022.10.03.510613 BioRxiv Preprint (2022).

    Song, M.-Y. et al. Energy restriction induced SIRT6 inhibits microglia activation and promotes angiogenesis in cerebral ischemia via transcriptional inhibition of TXNIP. Cell Death Dis 13, 449 (2022).

    Urbán, N. et al. Return to quiescence of mouse neural stem cells by degradation of a proactivation protein. Science 353, 292–295 (2016).

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    Referee #4

    Evidence, reproducibility and clarity

    Summary:

    In this manuscript, Gabarró-Solanas et al. tested the effect of intermitted fasting (IF, every-other-day fasting) on adult neural stem cells and neurogenesis. They demonstrate that the paradigm they have used does not affect NSC activation or maintenance, and does also not promote neurogenesis. As previous reports showed increased neurogenesis with IF, the authors controlled for various parameters such as mouse strain, sex, and diet length. They also used different methods of identification of newborn neurons, such as tamoxifen-induced lineage-tracing versus birth-dating with thymidine-analogues to substantiate their findings.

    Major comments:

    This study is very well done with carefully designed and controlled experiments. The manuscript reads nicely and the data are presented in a clear way, making it easy to follow. The authors have done a "tour-de force" to rule out confounding factors that might influence their findings that IF does not affect NSCs nor neurogenesis. The claims and conclusions are supported by the data. The methods are clearly described and should allow to reproduce the data independently. The number of replicates (i.e. the number of mice analyzed) is impressive and statistical analysis is adequate.

    The major findings, namely that the chosen IF does not affect NSCs and neurogenesis is not in line with some previous studies. Despite a careful ruling out of potentially confounding factors (see also "significance" below), it remains unclear why other studies have found an increase in neurogenesis with IF. As each of these studies has some specific experimental design, it is difficult to judge these data in the context of previous data without going through all the details of the other studies. It would thus be a great help for the reader if the authors could provide a table or schematic, which lists the major parameters of each of these studies, such as detailed paradigm of IF, age of mice at start, sex, duration of the intervention, method of identification of NSCs and neurogenesis etc.

    Two points that the authors have not discussed might also be worth mentioning in the discussion part:

    1. The mice in the night-time IF were single caged, could there be a potential negative effect on neurogenesis that would mask the presumably beneficial effect of IF? Although the controls were also single caged, the stress of social isolation might play a role?
    2. The IF mice gained the same weight over time (Fig. S2), but had a ~20% reduction in overall calory intake. This would be explainable by a reduction in energy expenditure, but the overall activity was also not significantly changed (Fig. S1). Can the authors speculate why they reach the same weight with less calories?

    Minor comments:

    1. It would be nice to replace the arbitrary units (AU) in the graphs were this is used (e.g. Fig. 2F, 3C, 4B, D and F etc) to the actual number of cells per a certain µm DG, so that the number of cells can be put in context and compared between the figures.
    2. Fig 3 D: can the authors also show the Ki67 channel to illustrate how it looks after a 3 month IF?
    3. Fig.4E: the NeuN staining looks strangely interrupted, this might be due to tile-stitching? In that case, it would be better to either only show one segment or to try to get a better stitching algorhythm.
    4. Fig.6 D shows a minus axis in Y-axis, this should only been shown from 0 to positive values, as it is a percentage of cells and cannot be negative.
    5. Fig.6 B: the same problem with the NeuN staining as mentioned under point 3. This should be improved.
    6. Fig. S6B: maybe add a comment in the result part or in the figure legend that a 10 day chase after an EdU pulse is not the classical protocol to look at mature NeuN positive neurons. But apparently enough newborn neurons were already NeuN positive for this quantification.
    7. The authors refer to personal communications with M. Mattson and S. Thuret to underline that circadian disruption is not enough to explain the differences (line 367 onwards). Can they refer the reader to published data instead?

    Significance

    Given the great interest in the seemingly positive effects on health of IF in general, and also for increasing neurogenesis, it is important to better understand the mechanism of this intervention. The study by Gabarró-Solanas et al. clearly demonstrates that IF is not a universal, "works all the time" way of increasing neurogenesis. The study is very well done, with well controlled and measured parameters. It shows that a physiological interference such as IF might depend on many factors and might be less robust across laboratories than anticipated. This study is a very good example that all the details of the experimental settings need to be taken into consideration and are ideally reported with every IF study. It is also a good example how to follow up "no effect" data in a way that they are conclusive.

    The significance of this study is to point out that IF as a strategy to increase neurogenesis needs to be reconsidered. It raises the questions how IF can be beneficial in some studies and not in others, asking for more experiments to better understand the detailed mechanisms of IF action. In a systematic approach, this study rules out some of the potentially confounding factors and shows that at least with the chosen IF paradigm, these factors are not the reason for not seeing increased neurogenesis. The study is thus of clear interest for the neurogenesis field and will also need to be considered by the broader field of IF research, although it speaks against the beneficial effects of IF. It might have the potential to bring together the different study authors who did or did not see increased neurogenesis with IF and discuss together the non-published details of their study design to advance the field.

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    Referee #3

    Evidence, reproducibility and clarity

    In this manuscript, Gabarro-Solanas et al. investigate the effects of intermittent fasting (IF) on adult hippocampal neurogenesis in young adult mice. IF has been reported to increase the number of adult-born neuron in the hippocampus, a region that is important for learning and memory. However, it is not well understood what stages of adult neurogenesis are regulated by IF. To address this, the authors utilized lineage tracing and label retention assays in mice undergoing an IF diet. The authors used 2 months old Glast-CreERT2;RYFP mice in combination with Edu label retention to characterize adult NSCs and placed these mice on 1 and 3 months of IF. Despite seeing a decrease in neural stem cell proliferation with age, the authors did not observe a change due to diet. The authors then used immunohistochemistry to characterize changes in cell proliferation, neuroblasts, and new neurons following 1 month and 3 months of IF. Only 1 month of IF seemed to decrease the number of new neurons; however, by 3 months the neuronal output was the same. There were no differences in neuroblasts or cell proliferation due to diet. Gabarro-Solanas et al. conclude that IF transiently and mildly inhibits neurogenesis. Due to contradicting results, the authors then try to determine what variables (sex, labeling method, strain, tamoxifen usage, or diet length) could be affecting their data. The authors saw no substantial differences due to any of their variables.

    Major Points

    1. The authors analyze NSCs homeostasis and neurogenesis in young adult mice and do not observe any significant changes with their chosen alternate day intermittent fasting paradigm. However, a lot of the data and cell counts appears to be highly variable between animals in the same group. At times, there is an order of magnitude difference between the highest and lowest counts (e.g. Figure 2C,E). According to the method section, it appears that the authors predominantly analyzed a single DG (section?) for most immunostainings, which may explain the large variability in their data. If this is indeed the case, it is insufficient to quantify only a single section for each animal. The authors should quantify several DG sections for each mouse from a pre-defined range along the rostral-caudal axis of the hippocampus in accordance with a standard brain reference atlas. There are also several quantifications, especially of Ki67 where several individuals appear to have no Ki67+ (Figure 3B, 6D) NSCs. These findings are surprising given the still young age of these mice and may be another reflection of the limited brain sections that were analyzed.
    2. There appear to be significant cutting or imaging artifacts across most fluorescent images further raising concerns regarding the accuracy of the quantifications (e.g. Figure 3D, 4C,E, 6B) and publication quality of the images and data. Importantly, uneven section thickness, either from cutting artifacts or imaging issues, may lead to inaccurate cell quantifications a could, possibly, account for the high variability. This issue would further exacerbate concerns regarding the quantification of a single DG section for each animal.
    3. It is unclear how NSCs were counted in the B6 mice (Fig 6D,E). The authors only provide a description for the Glast-CRE mice, where they used YFP labeling and GFAP. We assume they performed Sox2/GFAP or Nestin labeling, however, this is not clear at all. The authors should describe their methodology and provide representative images.
    4. NSC populations represent a heterogenous group of stem cells with different replicative properties. As such, the Glast-Cre approach used for the majority of this study may represent a specific subset of NSCs. In line with the previous point, we recommend the authors complement their NSC counts with Sox2/GFAP and Nestin immunostainings.
    5. Stress is a significant negative regulator of neurogenesis. Is it possible that the IF mice display higher stress level which could counteract any beneficial effects of the IF intervention. The authors should provide some measures of stress markers to rule out this potential confounding factor in their IF paradigm.

    Minor Point

    1. The authors state that "Experimental groups were formed by randomly assigning mice from different litters within each mouse strain and all experiments were conducted in male and female mice". Given that neurogenesis, especially at young ages, is highly sensitive to the exact age of the mice, the authors should provide a rationale why animals from different litters instead of littermate controls were used in these experiments.
    2. Currently, the statistical tests are only described in the method section, however it would be helpful if this information to be integrated into the figure legend as well. Additionally, the authors provide individual data points for some but not all bar graphs (eg Figure 1D).
    3. Cell counts per AU is a rather unorthodox unit. With a representative selection of tissue for each animal, the authors could avoid the need to normalize to the DG length and may be able to extrapolate an estimate of cell counts for the entire DG instead.
    4. In Figure 4D, the authors highlight a few NSC with arrowheads. At a quick glance this is rather confusing as it appears that the authors only counted 3 NSCs in each picture. It may be a better option to show a zoomed in picture to highlight an example of a representative NSC.
    5. In Supplementary Figure S6, the authors should complement the quantification of the nuclei with representative images.
    6. For the daytime IF, did the authors assess weights, food intake, RER as well liver/fat measurements similar to night-time IF? If so, this data should be provided in the supplement.

    Significance

    The authors are commended for compiling a manuscript on what is commonly considered 'negative data', that, at the same time, are also contradicting independent reports on the effects of IF on neurogenesis. The studies outlined in this manuscript are comprehensive and mostly well designed. Given the broad, growing interest in dietary restriction as an aging intervention the study is timely.

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    Referee #2

    Evidence, reproducibility and clarity

    In this manuscript, Gabarro-Solanas et al. question the suitability of IF (Intermittent fasting - non-pharmacological strategy to counteract ageing, which has been previously shown to increase the number of adult-born neurons in the dentate gyrus of mice) as a pro-neurogenic intervention, since IF treatment did not stimulate adult hippocampal neurogenesis, neither at the stem cell level nor on immature and/or dividing neurons. The Authors used a tamoxifen inducible transgenic model (Glast-CreERT2;RYFP mice) to trace neural stem cell lineage and found that IF did not enhance neural stem cell proliferation, nor the abundance of immature, DCX+ neurons. Three-months of IF failed to increase the number of new adult-born neurons (NeuN+/YFP+), while one month of IF significantly reduced the number of new adult-born neurons.

    The study appers technically sound, including many different approaches in order to reach its conclusions. For instance, tamoxifen has been reported to impair various physiological processes, including neurogenesis (Smith et al., 2022), and most studies on adult hippocampal neurogenesis use the C57BL/6J strain of mice; hence, the use of Tamoxifen or that of the GlastCreERT2;RYFP model may have underscored these observations. However, to account for this potentially confounding factor, the Authors characterised the effect of their IF treatment in C57BL/6j mice, also reporting no evident effects of IF as a pro-neurogenic intervention. I think the study was carefully planned and the analyses well done. Several possible variables were considered, including sex, labelling method, strain, tamoxifen usage or diet length. Several controls were performed in other organs and tissues (liver, fat) to establish the fasting protocol and to check its effects. Data are presented in a clear way. Quality of images is high level. In general, it appears as a highly reliable paper reaching an authoritative conclusion for the absence of effect of IF on adult neurogenesis.

    Major comments:

    I think that the key conclusions are convincing and no further experiments are required. The methods are presented in such a way that they can be reproduced, and the experiments adequately replicated with proper statistical analysis.

    Minor comments:

    Prior studies are referenced appropriately, both regarding the IF protocols and the adult neurogenesis modulation. Line 288 - a reference is incomplete (Dias); integrate with: (Dias et al., 2021) There is one concept that is not expressed in the manuscript. Maybe it is not strictly necessary, but I think can be useful to mention it here. It is the fact that most information currently available strongly indicates that adult neurogenesis in humans is not present after adolescence. Of course the research described here is carried out on mice, and in the manuscript it is stated many times that adult hippocampal neurogenesis is strongly decreasing with age, also due to age-related stem cell depletion. Yet, it seems that in humans the exhaustion of such a process can start after adolescence. We know that a sort of controversy is currently present on this subjects, because DCX+ neurons can be detected in adult and old human hippocampi. Yet, it is also clear that there is no substantial cell division (stem cells are depleted) to sustain such hypothetical neurogenesis. Hence, it has been hypothesized that non-newlyborn, "immature" neurons can persist in the absence of cell division, as it has been well demonstrated in the cerebral cortex (see La Rosa et al., 2020 Front Neurosci; Rotheneichner et al., 2018, Cereb Cortex). This point can be important in the case someone want to use dietary approached such as IF (or any other pharmacological treatment) to stimulate neurogenesis in humans.

    Significance

    The significance of this study relies on the fact that adult neurogenesis field (AN) has been often damaged by the search of "positive" results, aiming at showing that AN does occur "always and everywhere" and that most internal/external stimuli do increase it. This attitude created a bias in the field, persuading many scientists that a result in AN is worthy of publication (or of high impact factor publication) only when a positive result is found.

    Personally, I found particularly meaninful the last sentences of the Discussion (reported below), which might seem "off topic" in a research paper, while - I think - underline the real significance of the manuscript: "In addition, publication bias might be playing a role in skewing the literature on fasting and neurogenesis towards reporting positive results.

    In some reviews, even studies reporting no effect are cited as evidence for improved neurogenesis upon IF. Reporting of negative results, especially those challenging accepted dogmas, and a careful and rigorous evaluation of the publications cited in reviews are crucial to avoid unnecessary waste of resources and to promote the advancement of science."

    Reviewer field of expertise - keywords: adult neurogenesis, brain structural plasticity, non-newly born immature neurons, comparative neuroplasticity.

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    Referee #1

    Evidence, reproducibility and clarity

    Summary:

    In this study, mice were exposed to a specific form of so-called Intermittent Fasting (IF) and the effects of IF on adult neogenesis in the hippocampus were determined. The specific IF protocol used had no effect on activation, proliferation, or maintenance of adult Neural Stem Cells (aNSCs) and displayed a decrease in number of new neurons in the neurogenic niche but only after 1 month of the IF protocol. These results contrast previously published results from multiple studies that concluded that IF promotes survival of new neurons and by extension promote adult neurogenesis. The unresponsiveness of aNSCs or their immediate cell progeny, the Intermediate Neural Progenitors (IPCs), to IF is a novel finding. The authors make several relevant points in the discussion about the publication bias towards positive results (or omission of negative results), which may reinforce established dogmas. However, the presented results did not convincingly demonstrate that the absence of effects of IF on aNSCs or adult neurogenesis is simply not a result of a specific IF paradigm, which is not robust enough to elicit changes in adult neurogenesis. In other words, there is a lack of positive controls and alternative protocols that would rule out that the observed absence of effects is not a consequence of type II error (the error of omission), or more colloquially, a consequence of false negatives.

    Major Comments:

    1. Protocol-driven absence of effects: The absence of IF effects on aNSCs and IPCs observed in this study does not lend it the authority to conclude that aNSCs are resilient to IF or all IF paradigms and protocols. The absence of IF effects on aNSCs and neurogenesis could be specifically related to the chosen IF paradigm. Indeed, not all previous studies that observed IF-driven effects on adult neurogenesis used the same "night-time every-other-day fasting" protocol chosen in this study. For example, Brandhorst et al., 2015 (cited in this paper) used 4 days of IF 2x per month and observed an increase of DCX+BrdU+ cells. On the other hand, certain previous studies used the same or similar IF protocol used here, but often with longer duration or with a post-fasting ad libitum feeding period, which may be responsible for the pro-neurogenic or pro-survival effects. In fact, the authors acknowledge this in the discussion (page 7, lines 289-290 and 292-294). Why would the authors then not include similar feeding/IF paradigm in their study and determine if these would generate effects on survival of new neurons but also on aNSCs and/or IPCs? In addition, the authors acknowledge that the chosen IF paradigm may have affected the stress levels or behaviour of mice (page 9, lines 372-378). Why did they not test if their IF protocol does not increase stress or anxiety of mice by simple behaviour tests such as open field or elevated T maze? Alarmingly, the used IF protocol does not result in changes in final weight or growth curves (S.Fig.2), which is surprising and raises a question the used IF protocol is robust enough or appropriate. Finally, the authors acknowledge that their own results do not support well-established findings such as aging-related reduction in number of aNSCs (page 4, lines 177-179). This again questions whether the selected protocols and treatments are appropriate.
    2. Lack of topic-specific positive controls: The authors successfully demonstrated that the used IF protocol differentially impacts the adipose tissue and liver, while also inducing body weight fluctuations synchronized with the fasting periods. However, these peripheral effects outside the CNS do not directly imply that the chosen IF protocol is robust enough to elicit cellular or molecular changes in the hippocampus. The authors need to demonstrate that their IF protocol affects previously well-established CNS parameters associated with fasting such as astrocyte reactivity, inflammation or microglia activation, among other factors. In fact, they acknowledge this systemic problem in the discussion (page 8, lines 359-360).
    3. Problematic cell analyses: Cell quantification should be performed under stereological principles. However, the presented results did not adhere to stereological quantification. Instead, the authors chose to quantify specific cell phenotypes only in subjectively selected subsets of regions of interest, i.e., the Subgranular Zone (SGZ). This subjective pre-selection may have been responsible for the absence of effects, especially if these are either relatively small or dependent on anatomical sections of SGZ. For example, IF may exert effects on caudal SGZ more than on rostral SGZ. But if the authors quantified only (or predominantly) rostral SGZ, they may have missed these effects by biasing one segment of SGZ versus other. The authors should apply stereological quantification at least to the quantification of new neurons and test if this approach replicated previously observed pro-survival effects of IF. Also, the authors should describe how they pre-selected the ROI for cell quantification in greater details.
    4. Alarming exclusion of data points: There appears to be different number of data points in different graphs that are constructed from same data sets. For example, in the 3-month IF data set in Figure 4, there are 14 data points for the graph of Ki67+ cells (Fig.4B), but 16 (or 17) data points for the graph of DCX+ cells (Fig.4D). How is that possible? If data points were excluded, what objective and statistical criteria were applied to make sure that such exclusion is not subjective and biased? In fact, the authors state that "Samples with poor staining quality were also excluded from quantifications" (page 12, line 528-529). Poor preparation of tissue is not only suboptimal but not a valid objective reason for data point exclusion. This major issue needs to be explained and corrected.
    5. Different pulse-and-chase time-points: One of the reasons why this study has found that aNSCs may not be responsive to IF could be the use of less appropriate pulse-and-chase time-points either after EdU or after Tamoxifen for cell lineage tracing. The authors observed that IF has negative effects on new neurons initially (Fig.4F). Similarly, it is well established that voluntary physical exercise affects SGZ adult neurogenesis only during the first 2 weeks. After this period, the neurogenic effects of exercise are diminished beyond observational detection (i.e., van Praag's and Kempermann's papers in the past 25 years). These two arguments suggest that the observed absence of aNSC responsiveness might be a consequence of the chosen EdU administration and the EdU pulse should not be administered 15 days after Tamoxifen/IF protocol start but earlier, in the first week of the IF protocol. In fact, the decreased number of new neurons during the initial IF phase may not be only a consequence of reduced survival but of higher aNSC quiescence during the first week of the IF protocol.
    6. Discussion needs more specificity and clarity: The authors claim that the absence of IF effects on neurogenesis is multi-layered (including the influence of age, sex, specific cell labelling protocols etc.) but they do not specifically address why certain studies did find IF-driven neurogenic effects while they did not. In addition, some statements and points in the discussion are not clear. For example, when the authors refer to their own experiments (page 8, lines 331-334), it is not clear, which experiments they have in mind.

    Minor comments:

    1. Change in the title: The authors have shown that a very specific IF protocol does not affect aNSCs but initially decreases number of new neurons in SGZ. The title should reflect this. For example, it could state "Specific (night-time every-other-day) fasting does not affect aNSCs but initially decreases survival of new neurons in the SGZ".
    2. Data depiction: Data in 3 datasets were found not normally distributed (Fig. S5A, B and S6A) and were correctly analysed with non-parametric tests. However, the corresponding graphs wrongly depict the data as mean +/- SD while they should depict median +/- IQR (or similar adequate value) because non-parametric statistical tests do not compare means but medians.
    3. Statistical analysis: For ANOVA, the F and p values are not listed anywhere. The presented asterisks in the graphs are only for non-ANOVA or ANOVA post-hoc tests. This does not allow to judge statistical significance well and should be corrected.
    4. Asymmetric vs Symmetric cell divisions: Representative images in Fig.2B suggest that IF may affect the plane of cell division for the Type-1 aNSCs. The plane of cell division is an indirect indicator of symmetric vs asymmetric (exhaustive vs maintaining) modes of cell division. Is it possible, IF influences this, especially during the first week of IF (see major comment 5)?
    5. Improved and more accurate citations: Some references are not properly formatted (e.g., "Dias", page 7, line 288). Some references are included in generalizing statements when they do not contain data to support such statements. For example, Kitamura et al., 2006 did not determine the number of new neurons (only BrdU+ cells) in the SGZ, yet this reference is included among sources supporting that IF "promote survival of newly born neurons" (page 2, line 60). Authors should be more careful how the cite the references.
    6. How do the authors explain that they observe 73-80% caloric restriction and yet the final body weight is not different between IF and control animals? Would it suggest that the selected IF protocol or selected diet are not appropriate (see major point 4)?
    7. Given that aNSCs rely more on de novo lipogenesis and fatty acids for their metabolism as shown by Knobloch et al., Nature 2013 and given the interesting changes in RER with the IF shown in this study, it would be interesting to see whether there are differences in Fasn expression in aNSCs between control and IF animals (see minor point 4).
    8. Determining apoptosis in the SGZ by picnotic nuclei (Figure S6A) should be supplemented by determining the number and/or proportion of YFP+ cells positive for the Activated Caspase 3.

    Significance

    General assessment:

    This study concludes that aNSCs do not respond to the intermittent fasting. This expands and supplements previous findings that suggest that the intermittent fasting promotes adult neurogenesis by increasing survival and/or proliferation in the Subgranural Zone. The study is well designed, however, over-extends its conclusions beyond a specific fasting paradigm and does not acknowledge serious limitations in the experimental design and analyses. In fact, until major revision is done, which would rule out that the absence of effects of fasting on aNSCs is not due to false negative results, many conclusions from this study cannot be accepted as valid.

    Advance:

    As mentioned above, the study has a potential to advance our understanding of how fasting affects neurogenesis and fills the knowledge gap of how fasting specifically affects the stem cells. However, unless the study addresses its limitations, its conclusions are not convincing.

    Audience:

    This study would be particularly interesting for the niche readers from the neurogenesis field. However, the study can also be interesting for researchers in metabolomics and dietology.

    My expertise:

    adult neurogenesis, neural stem cells, dietology, metabolism

  7. Version published to 10.1101/2022.07.08.499318 on bioRxiv