The 5:2 diet does not increase adult hippocampal neurogenesis or enhance spatial memory in mice

  1. Luke D Roberts
  2. Amanda KE Hornsby
  3. Alanna Thomas
  4. Martina Sassi
  5. Aimee Kinzett
  6. Nathan Hsiao
  7. Bethan R David
  8. Mark Good
  9. Timothy Wells
  10. Jeffrey S Davies

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Abstract

New neurones are generated throughout life in the mammalian brain in a process known as adult hippocampal neurogenesis (AHN). Since this phenomenon grants a high degree of neuroplasticity influencing learning and memory, identifying factors that regulate AHN may be important for ameliorating age‐related cognitive decline. Calorie restriction (CR) has been shown to enhance AHN and improve memory, mediated by the stomach hormone, ghrelin. Intermittent fasting (IF), a dietary strategy offering more flexibility than conventional CR, has also been shown to promote aspects of AHN. The 5:2 diet is a popular form of IF; however, its effects on AHN are not well characterised. To address this, we quantified AHN in adolescent and adult wild‐type and ghrelin‐receptor‐deficient mice following 6 weeks on a 5:2 diet. We report an age‐related decline in neurogenic processes. However, the 5:2 diet does not increase AHN nor enhance memory performance, suggesting that this specific form of IF is ineffective in promoting brain plasticity to support learning.

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  1. Version published to 10.15252/embr.202357269
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    Reply to the reviewers

    __Reviewer #1 __(Evidence, reproducibility and clarity (Required)):

    Summary:

    In this manuscript, Roberts et al. hypothesised that the 5:2 diet (a popular form of IF, a dietary strategy within the Intermittent fasting that is thought to increase adult hippocampal neurogenesis - AHN) would enhance AHN in a ghrelin-dependent manner. To do this, the Authors used immunohistochemistry to quantify new adult-born neurons and new neural stem cells in the hippocampal dentate gyrus of adolescent and adult wild-type mice and mice lacking the ghrelin receptor, following six weeks on a 5:2 diet. They report an age-related decline in neurogenic processes and identify a novel role for ghrelin-receptor in regulating the formation of new adult

    born neural stem cells in an age-dependent manner. However, the 5:2 diet did not affect new neuron or neural stem cell formation in the dentate gyrus, nor did alter performance on a spatial learning and memory task. They conclude that the 5:2 diet used in their study does not increase AHN or improve associated spatial memory function.

    Major comments:

    One criticism might be the fact that many aspects are addressed at the same time. For instance it is not fully clear the role of ghrelin with respect to testing the DR effects on AHN. Although the link between ghrelin, CR and AHN is explained by citing several previous studies, it is difficult to identify the main focus of the study. Maybe this is due to the fact that the Authors analyse and comment throughout the paper the different experimental approaches used by different

    Authors to study effect of DR to AHN. This is not bad in principle, since I think the Authors have a deep knowledge of this complex matter, but all this results in a difficulty to follow the flow of the rationale in the manuscript.

    We appreciate the reviewer’s critique regarding the rationale of the studies presented in the manuscript.

    The role of ghrelin in the regulation of AHN by dietary interventions such as CR and IF is a major interest of our lab and is the main focus of the study. We, and others, have shown that ghrelin mediates the beneficial effects of CR on AHN. It is often assumed that ghrelin will elicit similar effects in other DR paradigms. We selected the 5:2 diet since it is widely practiced by humans, but it has not been well tested experimentally.

    We sought to empirically test how the neurogenic response to 5:2 differed between mice with functional and impaired ghrelin signaling.

    Given that plasma ghrelin levels and AHN are reduced during ageing, we also wanted to determine if 5:2 diet could slow or even prevent neurogenic decline in ageing mice.

    We will re-write the manuscript to ensure that our primary aim is clearly presented. We will also reanalyze the data, with genotype and 5:2 diet as key variables. To help maintain focus, the variable of age will be analyzed separately. This amendment will, we hope, help the reader follow the narrative of our manuscript.

    Another major point: the Discussion is too long. The Authors analyse all the possible reasons why different studies obtained different results concerning the effectiveness of DR in stimulating adult neurogenesis. Thus, the Discussion seems more as a review article dealing with different methods/experimental approaches to evaluate DR effects. We know that sometimes different results are due to different experimental approaches, yet, when an effect is strong and clear, it occurs in different situations. Thus, I think that the Authors must be less shy in expressing their conclusions, also reducing the methodological considerations. It is also well known that sometimes different results can be due to a study not well performed, or to biases from the Authors.

    In our discussion, we felt that it was particularly important to be as rigorous as possible in contextualizing our findings with other published data, whilst highlighting methodological differences. Our aim was to be as precise as possible when comparing findings across studies, however, this resulted in the narrative drifting from the key objectives of our study – namely, to determine the effect of 5:2 diet on neurogenesis and whether or not ghrelin-signalling regulated the process. We will amend the text of the discussion to ensure that the key points of our study are only compared and contrasted with relevant studies in the field. We thank the reviewer for their candid comment.

    Minor comments:

    • This sentence: "There is an age-related decline in adult hippocampal neurogenesis" cannot be put in the HIGHLIGHTS, since is a well known aspect of adult hippocampal neurogenesis

    The reviewer is correct to state this. Our study replicates this interesting age-related phenomenon. However, we will remove it from the ‘Highlights’ section.

    • Images in Figure 5 are not good quality.

    We apologise for this oversight. We will review each figure and panel to ensure that high-resolution images, that are appropriately annotated, are used throughout the manuscript.

    • In general, there are not a lot of images referring to microscopic/confocal photographs across the entire manuscript.

    We structured the manuscript with a limited number of figures and associated microscope captured panels, with the aim of presenting representative images to illustrate the nature and quality of the IHC protocols. However, we will amend the figures for the revised manuscript to provide representative microscopy images, with each group included and clearly annotated.

    • The last sentence of the Discussion "These findings suggest that distinct DR regimens differentially regulate neurogenesis in the adult hippocampus and that further studies are required to identify optimal protocols to support cognition during ageing" is meaningless in the context of the study, and in contrast with the main results. Honestly, my impression is that the Authors do not want to disappoint the conclusions of the previous studies; an alternative is that other Reviewers asked for this previously.

    We do not believe that this statement is contradictory to our findings, as distinct DR paradigms do appear to regulate AHN in different ways. However, we agree that we can be more explicit with regards to our own study findings and will prioritize the conclusions of our study over those of the entire field during revision.

    Reviewer #1 (Significance (Required)):

    value the significance of publishing studies that will advance the field.

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

    In this manuscript, Roberts et al. investigate the effect of the 5:2 diet on adult hippocampal neurogenesis (AHN) in mice via the ghrelin receptor. Many studies have reported benefits of dietary restriction (DR) on the brain that include increasing neurogenesis and enhancing cognitive function. However, neither the mechanisms underlying the effects of the 5:2 diet, nor potential benefits on the brain, are well understood. The authors hypothesize that the 5:2 diet enhances AHN and cognitive function via ghrelin-receptor signaling. To test this, they placedadolescent and adult ghrelin receptor knockout or wild type mice on either the 5:2 or ad libitum (AL) diet for 6 weeks, followed by spatial memory testing using an object in place (OIP) task. The authors also assessed changes in AHN via IHC using multiple markers for cell proliferation and neural stem cells. The authors observed a decrease in AHN due to age (from adolescent to adult), but not due to diet or ghrelin-receptor signaling. While loss of the ghrelin-receptor impaired spatial memory, the 5:2 diet did not affect cognitive function. The authors conclude that the 5:2 diet does not enhance AHN or spatial memory.

    We thank the reviewer for this summary. We note that there was a significant reduction in new neurones (BrdU+/NeuN+) cells in GHS-R null animals, regardless of age or diet (3 way ANOVA of age, genotype and diet (sexes pooled): Genotype P = 0.0290). These data suggest that the loss of ghrelin receptor signalling does impair AHN. However, we will re-analyse our data in light of reviewer 1 comments to remove ‘age’ as a variable. The new analyses and associated discussion will be presented in our revised manuscript.

    The authors use a 5:2 diet but fail to provide a basic characterization of this dietary intervention. For example, was the food intake assessed? In addition to the time restriction of the feeding, does this intervention also represent an overall caloric restriction or not? According to the provided results, the 5:2 diet does not appear to regulate adult hippocampal neurogenesis contrary to the authors' original hypothesis. Did the authors measure the effects of the 5:2 diet on any other organ system? Do they have any evidence that the intervention itself resulted in any well documented benefits in other cell types? Such data would provide a critical positive control for their intervention.

    This is an important point raised by the reviewer. Currently, we carefully quantified weight change across the duration of the study. However, we do not know whether the 5:2 diet reduced overall food intake or whether it impacted the timing of feeding events. To overcome this limitation, we will now test what impact the 5:2 dietary regime has on food intake and the timing of feeding. This study will allow us to correlate any changes with 5:2 diet. In addition, we have collected tibiae to quantify skeletal growth and have collected both liver and plasma (end point) samples which will be used to assess changes in the GH-IGF-1 axis. These additional studies will allow us to characterise the effects of the 5:2 paradigm on key indicators of physiological growth. These new data will be incorporated into the revised manuscript.

    Based on the effects of ghrelin in other dietary interventions, the authors speculate that the effect of the 5:2 diet is similarly mediated through ghrelin. However, the authors do not provide any basic characterization of ghrelin signaling to warrant this strong focus on the GSH-R mice. While the GSH-R mice display changes in NSC homeostasis and neurogenesis, none of these effects appear to be modified by the 5:2 diet. Thus, the inclusion of the GSH-R mice does not seem warranted and detracts from the main 5:2 diet focus of the manuscript.

    The role of ghrelin signalling via its receptor, GHSR, is a central tenet of our hypothesis. The loxTB-GHS-R null mouse is a well validated model of impaired ghrelin signalling, in which insertion of a transcriptional blocking cassette prevents expression of the ghrelin receptor (ZIgman et al.2005 JCI). We have previously shown that this mouse model is insensitive to calorie restriction (CR) mediated stimulation of AHN, in contrast to WT mice (Hornsby et al. 2016), justifying its suitability as a model for assessing the role of ghrelin signalling in response to DR interventions, such as the 5:2 paradigm. Whilst our findings do not support a role for ghrelin signalling in the context of the 5:2 diet studied, we did follow the scientific method to empirically test the stated hypothesis. While critiques of experimental design are welcome, the removal of these data may perpetuate publication bias in favour of positive outcomes and is something we wish to avoid.

    Neurogenesis is highly sensitive to stress. The 5:2 diet may be associated with stress which could counteract any benefits on neurogenesis in this experimental paradigm. Did the authors assess any measures of stress in their cohorts? Were the mice group housed or single housed?

    We thank the reviewer for raising this point. We have open-field recordings that will now be analysed to assess general locomotor activity, anxiety and exploration behaviour. Additionally, we will assess levels of the stress hormone, ACTH, in end point plasma samples. These datasets will be incorporated into the revised manuscript.

    The authors state that the 5:2 diet led to a greater reduction in body weight (31%) in adolescent males compared to other groups. However, it appears that the cohorts were not evenly balanced and the adolescent 5:2 male mice started out with a significantly higher starting weight (Supplementary Figure 1). The difference in starting weight at such a young age is significantly confounding the conclusion that the 5:2 diet is more effective at limiting weight gain specifically in this group.

    We thank the reviewer for highlighting this limitation. In the revision we will re-focus our discussion around the Δ Body weight repeated measures data, which compares the daily body weight of each group to its baseline value - thereby normalising any intergroup differences in starting weight. Furthermore, we will restructure figures 1 and S1 so that figure 1 presents only the repeated measure Δ Body weight data, while data for body weight both at baseline and on the final day of the study will be presented in figure S1.

    The authors count NSCs as Sox2+S100b- cells. However, the representative S100b staining does not look very convincing. Instead, it would be more appropriate to count Sox2+GFAP+ cells with a single vertical GFAP+ projection. Alternatively, the authors could also count Nestin-positive cells. Additionally, the authors label BrdU+ Sox2+ S100B- cells as "new NSCs". However, it appears that the BrdU labeling was performed approximately 6 weeks before the tissue was collected (Figure 1A). Thus, these BrdU-positive NSCs most likely represent label retaining/quiescent NSCs that divided during the labeling 6 weeks prior but have not proliferated since. As such, the term "new NSC" is misleading and would suggest an NSC that was actively dividing at the time of tissue collection.

    We apologise for presenting low-resolution images – these will be replaced by high-resolution images in the revised manuscript. In this study we have quantified the actively dividing BrdU+/Sox2+/S100B- cells that represent type II NSCs (rather than GFAP+ or Nestin+ type I NSCs) that have incorporated BrdU within the time period of the 6-week intervention. We appreciate the reviewer’s comments concerning the “new NSCs” terminology. We agree that we should be more specific in clarifying that the NSCs identified are those labelled during the 1st week of the 6-week intervention. We will amend this throughout the revised manuscript by re-naming these cells as 6-week old NSCs.

    Overall, this manuscript lacks a clear focus and narrative. Due to a lack of an affect by the 5:2 diet on hippocampal neurogenesis, the authors mostly highlight already well-known effects of aging and Grehlin/GSH-R on neurogenesis. Moreover, the authors repeatedly use age-related decline and morbidities as a rational for their study. However, they assess the effects of the 5:2 diet on neurogenesis only in adolescent and young mature but not aged mice.

    To provide greater clarity, and in accordance with reviewer 1’s comments, we will amend the text throughout to provide a focus on the data obtained. The objective of the changes will be to re-enforce the original study narrative. In relation to the use of the term ‘age-related decline’ or ‘age-related changes’, we think that these are appropriate to our study. Physiological ageing doesn’t begin at a specific point of chronological time, but is a process that is continuously ongoing. Indeed, our data is in agreement with previous studies reporting an age-related reduction in AHN at 6 months of age (e.g Kuhn et al.1996).

    Minor Points

    The authors combine the data from both male and female mice for most bar graphs. While this does not appear to matter for neurogenesis or behavioral readouts, there are very significant sexually dimorphic differences with respect to body size and weight. As such, male and female mice in Figure 1D,F should not be plotted in the same bar graph.

    We agree that sexual dimorphism exists with respect to body size and weight. We used distinct male and female symbols for each individual animal on these bar graphs, but do agree with the reviewer that sexual dimorphic differences should be emphasized. To achieve this, we will include additional supplementary graphs presenting the sex differences in starting weight, final weight, and weight change versus starting weight.

    The Figure legends are very brief and should be expanded to include basic information of the experimental design, statistical analyses etc.

    We thank the reviewer for this comment. We will provide specific experimental detaisl in the revised figure legends.

    Many figures include a representative image. However, it is often unclear if that is a representative image of a WT or mutant mouse, or a 5:2 or control group (Figure 2A, 3A, 4A, 5A).

    We structured the manuscript with a limited number of figures and associated microscope captured panels, with the aim of presenting representative images to illustrate the nature and quality of the IHC protocols. However, we will amend the figures for the revised manuscript to provide representative microscopy images, with each group included and clearly annotated.

    It would be helpful to provide representative images of DCX-positive cells in Figure 3A-F. Additionally, the authors should include a more extensive description of how this quantification was performed in the method section.

    We will revise the manuscript to provide representative high-resolution Dcx+ images displaying cells of each category. The method will also be revised to include a detailed description of how the quantification and classification was performed.

    The authors state "the hippocampal rostro-caudal axis (also known as the dorsoventral[] axis". However, the rostral-caudal and dorsal-central axis are usually considered perpendicular to one another.

    We agree that the dorso-ventral and rostral-caudal axes are anatomically distinct. The terms are often used interchangeably in the literature, which can lead misinterpretations (e.g the caudal portion of dorsal hippocampus is often mislabelled as ventral hippocampus). To avoid ambiguity, mislabelling or misidentification, we will include a supplementary figure detailing our anatomical definitions of the rostral and caudal poles of the hippocampus, alongside representative images and the bregma coordinates.

    Reviewer #2 (Significance (Required)):

    Understanding the mechanisms of a popular form of intermittent fasting (5:2 diet) that is not well understood is an interesting topic. Moreover, examining the effect of this form of intermittent fasting on the brain is timely. Notwithstanding, while the authors use multiple markers to validate the effect of the 5:2 diet on adult hippocampal neurogenesis, concerns regarding experimental design, validation, and data analysis weaken the conclusions being drawn.

    We thank reviewer 2 for this significance statement. We will revise the manuscript, as mentioned above, to clarify the experimental design, improve presentation of the data, and re-focus the narrative of the primary aims of the study.

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

    Summary

    In this study, Roberts and colleagues used a specific paradigm of intermitted fasting, the 5:2 diet, meaning 5 days ad libitum food and 2 non-consecutive days of fasting. They exposed adolescent and adult wild-type mice and ghrelin receptor knockout mice (GHS-R-/-) for 6 weeks to this paradigm, followed by 1 week ad libitum food. They further used the "object in place task" (OIP) to assess spatial memory performance. At the end of the dietary regime, the authors quantified newborn neurons and neural stem cells (NSCs) by immunohistochemistry. Roberts

    et al. show that the 5:2 diet does not change the proliferation of cells in the hippocampus, but report an increased number of immature neurons (based on DCX) in all the mice exposed to the 5:2 diet. This change however did not result in an increased number of mature adult-born neurons, as assessed by a BrdU birthdating paradigm. The authors further show diet-independent effects of the ghrelin receptor knockout, leading to less adult born neurons, but more NSCs in the adolescent mice and a lower performance in the OIP task.

    Major comments:

    The main conclusion of this study is that a specific type of intermitted fasting (5:2 diet) has no effects on NSC proliferation and neurogenesis. As there are several studies showing beneficial effects of intermitted fasting on adult neurogenesis, while other studies found no effects, it is important to better understand the effects of such a dietary paradigm.

    The experimental approaches used in this manuscript are mostly well explained, but it is overall rather difficult to follow the results part, as the authors always show the 4 experimental groups together (adolescent vs adult and wt vs GHS-R-/-). They highlight the main effects comparing all the groups, which most of the time is the factor "age". Age is a well-known and thus not surprising negative influencer of adult neurogenesis. Instead of focusing on the main tested factor, namely the difference in diet, the authors show example images of the two age classes

    (adolescent vs adult), which does not underly the major point they are making. Most of the time, they do not provide a post hoc analysis, so it is difficult to judge if the results with a significant main effect would be significant in a direct 1 to 1 comparison of the corresponding groups. The authors point out themselves that previous rodent studies did not use such a 5:2 feeding pattern, so having diet, age and genotype as factors at the same time makes the assessment of the diet effect more difficult.

    The manuscript would improve if the authors restructure their data to compare first the diet groups (adolescent wt AL vs 5:2 and in a separate comparison adult wt AL vs 5:2) and only in a later part of the results check if the Ghrelin receptor plays a role or not in this paradigm.

    We thank the reviewer for these comments. In line with comments from the other reviewers we will re-formulate the presentation of our datasets. We will remove ‘age’ as a key variable as age related changes are to be expected. For the revision, we will separate the adolescent and adult mouse data sets, plotting individual graphs for both. This should provide a clearer focus on 5:2 responses in both assessed genotypes.

    This re-configuration will impact the data being analysed and, therefore, the statistical analysis presented. In our original manuscript post hoc analyses were performed, however, only significant post hoc comparisons were highlighted (e.g figure 5). Non-significant post hoc comparisons have not been presented. In the method section of the revised manuscript, we will clarify that we’ll report post hoc differences when they are observed.

    During our study design, we decided to assess diet and genotype in parallel - as part of the same analysis. This seemed to us to be the most appropriate statistical method, so that we assessed dietary responses in both WT and GHS-R null mice.

    As this 5:2 is a very specific paradigm, it is furthermore difficult to compare these results to other studies and the conclusions are only valid for this specific pattern and timing of the intervention (6 weeks). It remains unclear why the authors have not first tried to establish a study with wildtype mice and a similar duration as in previous studies observing beneficial effects of intermitted fasting on neurogenesis. Like this, it would have been possible to make a statement if the 5:2 per se does not increase neurogenesis or if the 6 weeks exposure were just too short.

    The reviewer raises this relevant point which we considered during the study design period. Given that we had previously reported significant modulation of AHN with a relatively short period of 30% CR (14 days followed by 14 days AL refeeding (Hornsby et al.2016)), we predicted that a 6 week course on the 5:2 paradigm (totalling 12 days of complete food restriction over the 6 week period) would provide a similar dietary challenge. The fact that we did not observe similar changes in AHN with this 5:2 paradigm is notable.

    The graphical representation of the data could also be improved. Below are a few

    examples listed:

    1.) Figure 1 B and C, the same symbol and colours are used for the adolescent and adult animals, which makes the graphs hard to read. One colour and symbol per group throughout the manuscript would be better.

    We thank the reviewer for this comment. We will amend the presentation of the graphs throughout the manuscript to ensure that they are easier to interpret.

    2.) The authors found no differences in the total number of Ki67 positive cells in the DG. However, Ki67 staining does not allow to conclude the type of cell which is proliferating. It would thus strengthen the findings if this analysis was combined with different markers, such as Sox2, GFAP and DCX.

    Double labelling of Ki67 positive cells would allow for further insight into the identity of distinct proliferating cell populations. However, quantifying Ki67 immunopositive cells within the sub-granular zone of the GCL, as a single marker, is commonly used in studies of AHN. Given that studies of intermittent fasting, calorie restriction and treatment with exogenous acyl-ghrelin report no effect on NPC cell division, we decided not to pursue this line of inquiry.

    3.) In Figure 3, the authors say that the diet increases the number of DCX in adolescent and adult mice, which is not clear when looking at the graph in 3B. Are there any significant differences when directly comparing the corresponding groups, for instance the WT AL vs the WT 5:2? It is further not clear how the authors distinguished the different types of DCX morphology-wise. The quantification in C and D would need to be illustrated by example images. Furthermore, the colour-code used in these graphs is not explained and remains unclear

    While the 3 way ANOVA does yield a significant overall effect for diet, we agree that it is indeed difficult to see a difference on the graph, although the mean values of the adolescent 5:2 animals are more prominent than the AL counterparts. Mean +/- SEM will be provided in the supplementary section of the revised manuscript. Furthermore, we will clarify the method used to identify distinct DCX+ morphologies, include representative high-resolution images of each DCX+ cell category, and amend the colour coding to avoid misinterpretation.

    1. In Figure 5, the authors show that the number of new NSCs is significantly increased in the adolescent GHS-R-/- mice, independent of the diet, but this increase does not persist in the adult mice. They conclude that "the removal of GHS-R has a detrimental effect on the regulation of new NSC number..." this claim is not substantiated and needs to be reformulated. As the GHS-R-/- mice have a transcriptional blockage of Ghrs since start of its expression, would such an effect on NSC regulation not result in an overall difference in brain development, as ghrelin is also important during embryonic development?

    This is an interesting point. However, we disagree that the statement "the removal of GHS-R has a detrimental effect on the regulation of new NSC number..." is unsubstantiated, since it does not exclude any developmental deficits in these mice that may account for the differences observed. Nonetheless, we will rephrase the sentence to clarify our intended point and remove any ambiguity.

    5.) In Figure 6, the authors asses spatial memory performance with a single behavioral test, the OIP. As these kind of tests are influenced by the animal's motivation to explore, it's anxiety levels, physical parameters (movement) etc., the interpretation of such a test without any additional measured parameters can be problematic. The authors claim that the loss of GHS-R expression impairs spatial memory performance. As the discrimination ratio was calculated, it is not possible to see if there is an overall difference in exploration time between genotypes. This would be a good additional information to display.

    We thank the reviewer for this insight. We have open-field recordings that will now be analysed to assess general locomotor activity, anxiety and exploration behaviour. These data, alongside exploratory time of the mice during the OIP task will be incorporated into the revised manuscript.

    Besides these points listed above, the methods are presented in such a way that they can be reproduced. The experiments contained 10-15 mice per group, which is a large enough group to perform statistical analyses. As mentioned above, the statistical analysis over all 4 groups with p-values for the main effects should be followed by post hoc multiple comparison tests to allow the direct comparison of the corresponding groups.

    Reviewer #3 (Significance (Required)):

    In the last years, growing evidences suggested that IF might have positive effect on health in general and also for neurogenesis. However, a few recent studies report no effects on neurogenesis, using different IF paradigms. This study adds another proof that not all IF paradigms influence neurogenesis and shows that more work needs to be done to better understand when and how IF can have beneficial effects. This is an important finding for the neurogenesis field, but the results are only valid for this specific paradigm used here, which limits its significance. The reporting of such negative findings is however still important, as it shows that IF is not just a universal way to increase neurogenesis. In the end, such findings might have the potential to bring the field together to come up with a more standardized dietary intervention paradigm, which would be robust enough to give similar results across laboratories and mouse strains, and would allow to test the effect of genetic mutations on dietary influences of neurogenesis.

    We thank the reviewer for their insightful and thorough feedback.

    1. Description of the revisions that have already been incorporated in the transferred manuscript

    Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

    The manuscript has not been revised at this stage.

    2. Description of analyses that authors prefer not to carry out

    Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

    We have included in our replies to the reviewers a description of the amendments that we will make to our manuscript. Two requested revisions stand out as being unnecessary or cannot be provided within the scope of a revision.

    The first was the request to perform the 5:2 study in older mice. This an interesting suggestion, however, the expense and time needed to maintain mice into old age (e.g >18 months) cannot be provided within the scope of our revision. In addition, given that we report no effect of the 5:2 paradigm on AHN in adolescent (7 week old) and adult (7 month old) mice, there is less justification for such a study in older mice.

    The second request, that we disagree with, was to remove data relating to the GHS-R null mice (see reviewer 2, point 2). The role of ghrelin signalling via its receptor, GHS-R, is a central tenet of our hypothesis. Whilst our findings do not support a role for ghrelin signalling in the context of the 5:2 diet studied, we followed the scientific method to empirically test the stated hypothesis. While critiques of experimental design are welcome, the removal of such data may perpetuate publication bias in favour of positive outcomes and is something we wish to avoid.

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    Referee #3

    Evidence, reproducibility and clarity

    In this study, Roberts and colleagues used a specific paradigm of intermitted fasting, the 5:2 diet, meaning 5 days ad libitum food and 2 non-consecutive days of fasting. They exposed adolescent and adult wildtype mice and ghrelin receptor knockout mice (GHS-R-/-) for 6 weeks to this paradigm, followed by 1 week ad libitum food. They further used the "object in place task" (OIP) to assess spatial memory performance. At the end of the dietary regime, the authors quantified newborn neurons and neural stem cells (NSCs) by immunohistochemistry. Roberts et al. show that the 5:2 diet does not change the proliferation of cells in the hippocampus, but report an increased number of immature neurons (based on DCX) in all the mice exposed to the 5:2 diet. This change however did not result in an increased number of mature adult-born neurons, as assessed by a BrdU-birthdating paradigm. The authors further show diet-independent effects of the ghrelin receptor knockout, leading to less adult born neurons, but more NSCs in the adolescent mice and a lower performance in the OIP task.

    Major comments:

    The main conclusion of this study is that a specific type of intermitted fasting (5:2 diet) has no effects on NSC proliferation and neurogenesis. As there are several studies showing beneficial effects of intermitted fasting on adult neurogenesis, while other studies found no effects, it is important to better understand the effects of such a dietary paradigm.

    The experimental approaches used in this manuscript are mostly well explained, but it is overall rather difficult to follow the results part, as the authors always show the 4 experimental groups together (adolescent vs adult and wt vs GHS-R-/-). They highlight the main effects comparing all the groups, which most of the time is the factor "age". Age is a well-known and thus not surprising negative influencer of adult neurogenesis. Instead of focusing on the main tested factor, namely the difference in diet, the authors show example images of the two age classes (adolescent vs adult), which does not underly the major point they are making. Most of the time, they do not provide a post hoc analysis, so it is difficult to judge if the results with a significant main effect would be significant in a direct 1 to 1 comparison of the corresponding groups. The authors point out themselves that previous rodent studies did not use such a 5:2 feeding pattern, so having diet, age and genotype as factors at the same time makes the assessment of the diet effect more difficult. The manuscript would improve if the authors restructure their data to compare first the diet groups (adolescent wt AL vs 5:2 and in a separate comparison adult wt AL vs 5:2) and only in a later part of the results check if the Ghrelin receptor plays a role or not in this paradigm.

    As this 5:2 is a very specific paradigm, it is furthermore difficult to compare these results to other studies and the conclusions are only valid for this specific pattern and timing of the intervention (6 weeks). It remains unclear why the authors have not first tried to establish a study with wildtype mice and a similar duration as in previous studies observing beneficial effects of intermitted fasting on neurogenesis. Like this, it would have been possible to make a statement if the 5:2 per se does not increase neurogenesis or if the 6 weeks exposure were just too short.

    The graphical representation of the data could also be improved. Below are a few examples listed:

    1. Figure 1 B and C, the same symbol and colours are used for the adolescent and adult animals, which makes the graphs hard to read. One colour and symbol per group throughout the manuscript would be better.
    2. The authors found no differences in the total number of Ki67 positive cells in the DG. However, Ki67 staining does not allow to conclude the type of cell which is proliferating. It would thus strengthen the findings if this analysis was combined with different markers, such as Sox2, GFAP and DCX.
    3. In Figure 3, the authors say that the diet increases the number of DCX in adolescent and adult mice, which is not clear when looking at the graph in 3B. Are there any significant differences when directly comparing the corresponding groups, for instance the WT AL vs the WT 5:2? It is further not clear how the authors distinguished the different types of DCX morphology-wise. The quantification in C and D would need to be illustrated by example images. Furthermore, the colour-code used in these graphs is not explained and remains unclear.
    4. In Figure 5, the authors show that the number of new NSCs is significantly increased in the adolescent GHS-R-/- mice, independent of the diet, but this increase does not persist in the adult mice. They conclude that "the removal of GHS-R has a detrimental effect on the regulation of new NSC number..." this claim is not substantiated and needs to be reformulated. As the GHS-R-/- mice have a transcriptional blockage of Ghrs since start of its expression, would such an effect on NSC regulation not result in an overall difference in brain development, as ghrelin is also important during embryonic development?
    5. In Figure 6, the authors asses spatial memory performance with a single behavioral test, the OIP. As these kind of tests are influenced by the animal's motivation to explore, it's anxiety levels, physical parameters (movement) etc., the interpretation of such a test without any additional measured parameters can be problematic. The authors claim that the loss of GHS-R expression impairs spatial memory performance. As the discrimination ratio was calculated, it is not possible to see if there is an overall difference in exploration time between genotypes. This would be a good additional information to display.

    Besides these points listed above, the methods are presented in such a way that they can be reproduced. The experiments contained 10-15 mice per group, which is a large enough group to perform statistical analyses. As mentioned above, the statistical analysis over all 4 groups with p-values for the main effects should be followed by post hoc multiple comparison tests to allow the direct comparison of the corresponding groups.

    Minor comments:

    The authors should provide more information in the figure legends and always show representative images of the parameters analyzed. Some of the images are also of low resolution and should be replaced with higher resolution images (for instance Fig. 5A). The significant P values of the multiple comparison between groups should be added into the figures.

    Significance

    In the last years, growing evidences suggested that IF might have positive effect on health in general and also for neurogenesis. However, a few recent studies report no effects on neurogenesis, using different IF paradigms. This study adds another proof that not all IF paradigms influence neurogenesis and shows that more work needs to be done to better understand when and how IF can have beneficial effects. This is an important finding for the neurogenesis field, but the results are only valid for this specific paradigm used here, which limits its significance. The reporting of such negative findings is however still important, as it shows that IF is not just a universal way to increase neurogenesis. In the end, such findings might have the potential to bring the field together to come up with a more standardized dietary intervention paradigm, which would be robust enough to give similar results across laboratories and mouse strains, and would allow to test the effect of genetic mutations on dietary influences of neurogenesis.

  4. Review Commons

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    Referee #2

    Evidence, reproducibility and clarity

    In this manuscript, Roberts et al. investigate the effect of the 5:2 diet on adult hippocampal neurogenesis (AHN) in mice via the ghrelin receptor. Many studies have reported benefits of dietary restriction (DR) on the brain that include increasing neurogenesis and enhancing cognitive function. However, neither the mechanisms underlying the effects of the 5:2 diet, nor potential benefits on the brain, are well understood. The authors hypothesize that the 5:2 diet enhances AHN and cognitive function via ghrelin-receptor signaling. To test this, they placed adolescent and adult ghrelin receptor knockout or wild type mice on either the 5:2 or ad libitum (AL) diet for 6 weeks, followed by spatial memory testing using an object in place (OIP) task. The authors also assessed changes in AHN via IHC using multiple markers for cell proliferation and neural stem cells. The authors observed a decrease in AHN due to age (from adolescent to adult), but not due to diet or ghrelin-receptor signaling. While loss of the ghrelin-receptor impaired spatial memory, the 5:2 diet did not affect cognitive function. The authors conclude that the 5:2 diet does not enhance AHN or spatial memory.

    Major Points

    1. The authors use a 5:2 diet but fail to provide a basic characterization of this dietary intervention. For example, was the food intake assessed? In addition to the time restriction of the feeding, does this intervention also represent an overall caloric restriction or not? According to the provided results, the 5:2 diet does not appear to regulate adult hippocampal neurogenesis contrary to the authors' original hypothesis. Did the authors measure the effects of the 5:2 diet on any other organ system? Do they have any evidence that the intervention itself resulted in any well documented benefits in other cell types? Such data would provide a critical positive control for their intervention.
    2. Based on the effects of grehlin in other dietary interventions, the authors speculate that the effect of the 5:2 diet is similarly mediated through grehlin. However, the authors do not provide any basic characterization of grehlin signaling to warrant this strong focus on the GSH-R mice. While the GSH-R mice display changes in NSC homeostasis and neurogenesis, none of these effects appear to be modified by the 5:2 diet. Thus, the inclusion of the GSH-R mice does not seem warranted and detracts from the main 5:2 diet focus of the manuscript.
    3. Neurogenesis is highly sensitive to stress. The 5:2 diet may be associated with stress which could counteract any benefits on neurogenesis in this experimental paradigm. Did the authors assess any measures of stress in their cohorts? Were the mice group housed or single housed?
    4. The authors state that the 5:2 diet led to a greater reduction in body weight (31%) in adolescent males compared to other groups. However, it appears that the cohorts were not evenly balanced and the adolescent 5:2 male mice started out with a significantly higher starting weight (Supplementary Figure 1). The difference in starting weight at such a young age is significantly confounding the conclusion that the 5:2 diet is more effective at limiting weight gain specifically in this group.
    5. The authors count NSCs as Sox2+S100b- cells. However, the representative S100b staining does not look very convincing. Instead, it would be more appropriate to count Sox2+GFAP+ cells with a single vertical GFAP+ projection. Alternatively, the authors could also count Nestin-positive cells. Additionally, the authors label BrdU+ Sox2+ S100B- cells as "new NSCs". However, it appears that the BrdU labeling was performed approximately 6 weeks before the tissue was collected (Figure 1A). Thus, these BrdU-positive NSCs most likely represent label-retaining/quiescent NSCs that divided during the labeling 6 weeks prior but have not proliferated since. As such, the term "new NSC" is misleading and would suggest an NSC that was actively dividing at the time of tissue collection.
    6. Overall, this manuscript lacks a clear focus and narrative. Due to a lack of an affect by the 5:2 diet on hippocampal neurogenesis, the authors mostly highlight already well-known effects of aging and Grehlin/GSH-R on neurogenesis. Moreover, the authors repeatedly use age-related decline and morbidities as a rational for their study. However, they assess the effects of the 5:2 diet on neurogenesis only in adolescent and young mature but not aged mice.

    Minor Points

    1. The authors combine the data from both male and female mice for most bar graphs. While this does not appear to matter for neurogenesis or behavioral read-outs, there are very significant sexually dimorphic differences with respect to body size and weight. As such, male and female mice in Figure 1D,F should not be plotted in the same bar graph.
    2. The Figure legends are very brief and should be expanded to include basic information of the experimental design, statistical analyses etc.
    3. Many figures include a representative image. However, it is often unclear if that is a representative image of a WT or mutant mouse, or a 5:2 or control group (Figure 2A, 3A, 4A, 5A).
    4. It would be helpful to provide representative images of DCX-positive cells in Figure 3A-F. Additionally, the authors should include a more extensive description of how this quantification was performed in the method section.
    5. The authors state "the hippocampal rostro-caudal axis (also known as the dorso-ventral [] axis". However, the rostral-caudal and dorsal-central axis are usually considered perpendicular to one another.

    Significance

    Understanding the mechanisms of a popular form of intermittent fasting (5:2 diet) that is not well understood is an interesting topic. Moreover, examining the effect of this form of intermittent fasting on the brain is timely. Notwithstanding, while the authors use multiple markers to validate the effect of the 5:2 diet on adult hippocampal neurogenesis, concerns regarding experimental design, validation, and data analysis weaken the conclusions being drawn.

  5. Review Commons

    Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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    Referee #1

    Evidence, reproducibility and clarity

    In this manuscript, Roberts et al. hypothesised that the 5:2 diet (a popular form of IF, a dietary strategy within the Intermittent fasting that is thought to increase adult hippocampal neurogenesis - AHN) would enhance AHN in a ghrelin-dependent manner. To do this, the Authors used immunohistochemistry to quantify new adult-born neurons and new neural stem cells in the hippocampal dentate gyrus of adolescent and adult wild-type mice and mice lacking the ghrelin receptor, following six weeks on a 5:2 diet. They report an age-related decline in neurogenic processes and identify a novel role for ghrelin-receptor in regulating the formation of new adult born neural stem cells in an age-dependent manner. However, the 5:2 diet did not affect new neuron or neural stem cell formation in the dentate gyrus, nor did alter performance on a spatial learning and memory task. They conclude that the 5:2 diet used in their study does not increase AHN or improve associated spatial memory function.

    Major comments:

    I think that the key conclusions are convincing and no further experiments are required. Maybe some parts of the text should be rewritten (see below). The methods are presented in such a way that they can be reproduced, and the experiments adequately replicated with proper statistical analysis.

    • One criticism might be the fact that many aspects are addressed at the same time. For instance it is not fully clear the role of ghrelin with respect to testing the DR effects on AHN. Although the link between ghrelin, CR and AHN is explained by citing several previous studies, it is difficult to identify the main focus of the study. Maybe this is due to the fact that the Authors analyse and comment throughout the paper the different experimental approaches used by different Authors to study effect of DR to AHN. This is not bad in principle, since I think the Authors have a deep knowledge of this complex matter, but all this results in a difficulty to follow the flow of the rationale in the manuscript.
    • Another major point: the Discussioni is too long. The Authors analyse all the possible reasons why different studies obtained different results concerning the effectiveness of DR in stimulating adult neurogenesis. Thus, the Discussion seems more as a review article dealing with different methods/experimental approaches to evaluate DR effects. We know that sometimes different results are due to different experimental approaches, yet, when an effect is strong and clear, it occurs in different situations. Thus, I think that the Authors must be less shy in expressing their conclusions, also reducing the methodological considerations. It is also well known that sometimes different results can be due to a study not well performed, or to biases from the Authors.

    Minor comments:

    • This sentence: "There is an age-related decline in adult hippocampal neurogenesis" cannot be put in the HIGHLIGHTS, since is a well known aspect of adult hippocampal neurogenesis
    • Images in Figure 5 are not good quality.
    • In general, there are not a lot of images refferring to microscopic/confocal photographs across the entire manuscript.
    • The last sentence of the Discussion "These findings suggest that distinct DR regimens differentially regulate neurogenesis in the adult hippocampus and that further studies are required to identify optimal protocols to support cognition during ageing" is meaningless in the context of the study, and in contrast with the main results.

    Honestly, my impression is that the Authors do not want to disappoint the conclusions of the previous studies; an alternative is that other Reviewers asked for this previously.

    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.

    The Author cite in the Discussion the work by Gabarro-Solanas et al. (preprint), which share the same conclusion although analysing different aspect of neurogenesis. Both seems sound studies, substantially balanced in their conclusions.

  6. Version published to 10.1101/2022.10.03.510613v1 on bioRxiv