Author response:
The following is the authors’ response to the original reviews.
We thank the three reviewers for their encouraging and constructive comments. We have addressed them by increasing clarity of the writing and adding details to the methods section that were previously missing or not stated clearly enough. We have included additional experimental data. Specifically, we tested how the osmotic effect of lactulose depends on lactulose dosage and colonization state, added data on cecum sizes of mice with different microbiomes, and tested how lactulose treatment in the active phase affects feeding behavior.
Public Reviews:
Reviewer #1 (Public Review):
Greter et al. provide an interesting and creative use of lactulose as a "microbial metabolism" inducer, combined with tracking of H2 and other fermentation end products. The topic is timely and will likely be of broad interest to researchers studying nutrition, circadian rhythm, and gut microbiota. However, a couple of moderate to major concerns were noted that may impact the interpretation of the current data:
(1) Much of the data relies on housing gnotobiotic mice in metabolic cages, but I couldn't find any details of methods to assess contamination during multiple days of housing outside of gnotobiotic isolators/cages. Given the complexity of the metabolic cage system used, sterility would likely be incredibly challenging to achieve. More details needed to be included about how potential contamination of the mice was assessed, ideally with 16S rRNA gene sequencing data of the endpoint samples and/or qPCR for total colonization levels relative to the more targeted data shown.
We thank the reviewer for pointing out that we have not made the experimental setup clear in the text. One of the unique features of our metabolic cage setup is that the mice do not need to be housed outside gnotobiotic isolators, but that the whole system is placed inside an isolator. We have developed and published this system recently (Hoces et al, PLOS Biol 2022), including extensive testing for sterility/gnotobiosis. We have now adapted the main text to increase clarity on this issue (lines 76ff).
Given that 16S sequencing of germ-free mice will typically produce false-positive reads, we used Blautia pseudococcoides as an indicator strain for contamination. This strain is present in our SPF mouse colony, forms spores that are highly resilient to decontamination measures, and has been the most likely contaminant in our gnotobiotic system. We have checked for presence of this strain in the cecum content of all our animals at the end of each experiment, and only included experiments which had a B. pseudococcoides signal below threshold level. We have now added this information to the methods section (lines 389ff).
(2) The language could be softened to provide a more nuanced discussion of the results. While lactulose does seem to induce microbial metabolism it also could have direct effects on the host due to its osmotic activity or other off-target effects. Thus, it seems more precise to just refer to lactulose specifically in the figure titles and relevant text.
We have adapted all figure legends to not contain interpretations, but rather state what was done in the experiments shown in the figures. We have also adapted the text in multiple places to soften the language and avoid overinterpretation of our experimental results.
Additionally, the degree to which lactulose "disrupts the diurnal rhythm" isn't clear from the data shown, especially given that the markers of circadian rhythm rapidly recover from the perturbation. It is probably more precise to instead state that lactulose transiently induces fermentation during the light phase or something to that effect.
We tried to make the argument that what we call disruption of the diurnal rhythm is acute, meaning that it is not disrupting the rhythm "chronically" (i.e., for longer), but that it recovers rapidly from this transient disruption. Given the confusion this wording is causing we are introducing this conceptually in the new version of the manuscript (lines 56ff).
The discussion could also be expanded to address what methods are available or could be developed to build upon the concepts here; for example, the use of genetic inducers of metabolism which may avoid the more complex responses to lactulose.
We also appreciate the mention of concepts from our study that can be built on in future studies, and we added a paragraph on potential further research. (lines 301ff).
Despite these concerns, this was still an intriguing and valuable addition to the growing literature on the interface of the microbiome and circadian fields.
We thank the reviewer for all their encouraging and constructive remarks!
Reviewer #2 (Public Review):
Summary:
The authors aimed to investigate how microbial metabolites, such as hydrogen and short-chain fatty acids (SCFAs), influence feeding behavior and circadian gene expression in mice. Specifically, they sought to understand these effects in different microbial environments, including a reduced community model (EAM), germ-free mice, and SPF mice. The study was designed to explore the broader relationship between the gut microbiome and host circadian rhythms, an area that is not well understood. Through their experiments, the authors hoped to elucidate how microbial metabolism could impact circadian clock genes and feeding patterns, potentially revealing new mechanisms of gut microbiome-host interactions.
Strengths:
The manuscript presents a well-executed investigation into the complex relationship between microbial metabolites and circadian rhythms, with a particular focus on feeding behavior and gene expression in different mouse models. One of the major strengths of the work lies in its innovative use of a reduced community model (EAM) to isolate and examine the effects of specific microbial metabolites, which provides valuable insights into how these metabolites might influence host behavior and circadian regulation. The study also contributes to the broader understanding of the gut microbiome's role in circadian biology, an area that remains poorly understood. The experiments are thoughtfully designed, with a clear rationale that ties together the gut microbiome, metabolic products, and host physiological responses. The authors successfully highlight an intriguing paradox: the significant influence of microbial metabolites in the EAM model versus the lack of effect in germ-free and SPF mice, which adds depth to the ongoing exploration of microbial-host interactions. Despite some methodological concerns, the manuscript offers compelling data and opens up new avenues for research in the field of microbiome and circadian biology.
We thank the reviewer for their encouraging remarks, specifically on the surprising findings that microbial metabolism seems to affect circadian clock gene expression and behavior differently in EAM and SPF mice.
Weaknesses:
The manuscript, while providing valuable insights, has several methodological weaknesses that impact the overall strength of the findings. First, the process for stool collection lacks clarity, raising concerns about potential biases, such as the risk of coprophagia, which could affect the dry-to-wet weight ratio analysis and compromise the validity of these measurements.
We thank the reviewer for pointing out that our description of the specific methods used for collecting feces were presented in a somewhat confusing manner. In short, dry and wet faecal weights were determined based on fecal pellets that were freshly produced and directly collected from restrained mice. To determine total fecal output over time, we collected all fecal pellets produced in a 5-hour window in a cage, determined their dry weight, and then used the water content determined for fresh faeces to calculate wet weight. Using this method, we cannot account for potential differences in coprophagia between the groups. However, this is not likely to affect the dry-to-wet ratio of faecal output in our results. We have now adapted the section in the methods to increase clarity (lines 440ff), and changed the quantity shown in Figure S2C and E to "water content", which is a more intuitive measure for the same thing.
Additionally, the use of the term "circadian" in some contexts appears inaccurate, as "diurnal" might be more appropriate, especially given the uncertainty regarding whether the observed microbiome fluctuations are truly circadian.
Similarly to our answer to reviewer 1 above, we appreciate this remark about imprecise language and have addressed this issue in the text and the figure legends. Indeed, we do not think the fluctuations in microbiota activity are truly circadian, but likely a result of the entrainment through the host's food intake.
Another significant issue is the unexpected absence of an osmotic effect of lactulose in EAM mice, which contradicts the known properties of lactulose as an osmotic laxative. This finding requires further verification, including the use of a positive control, to ensure it is not artifactual.
This is a good point. We have used this lactulose dosage specifically to induce microbial metabolism without causing osmotic diarrhoea and went to some lengths do demonstrate this (FigureS2C-E). In response to this comment (and one by reviewer 3 below about transit time), we have now performed additional experiments using higher lactulose dosage (new FigureS3). Our results indicate that the effect of lactulose on water content and transit time depends on microbiota complexity, with no change in fecal water content in 3MM mice even when treated with higher lactulose doses, and a stronger change in SPF mice. We now address this in the main text (lines 127ff).
The presentation of qRT-PCR data as log2-fold changes, with a mean denominator, could introduce bias by artificially reducing variability, potentially leading to spurious findings or increased risk of Type I error. This approach may explain the unexpected activation of both the positive and negative limbs of the circadian clock.
While we agree that our description of the qPCR method used for measuring circadian clock gene expression was lacking detail, we do not see how our analysis would lead to an increased risk of Type 1 error.
Briefly, we use the standard ΔΔCt method to analyze our RT-PCR results. We first normalize gene expression values for each gene of interest to an internal housekeeping gene. Then, we use these normalized values to compare gene expression values in treatment vs control groups (or to the control group at time point 0 in the case of Figure 3C). We then use a log2 transformation to convert the logarithmic RT-PCR values to fold changes. We apologize for the confusing labeling in the figures, where we called the values "log2(fold changes)", which we have now changed to "log2(ΔΔCt) of expression" in Figures 3B, C and S4.
The simultaneous activation of both limbs of the circadian clock is indeed a surprising result and somewhat complicates interpreting the effect of lactulose treatment on clock gene expression. We take it as evidence that it generally interferes with clock gene expression, while a clearer understanding of the effects would require further research.
Moreover, the lack of detailed information on the primers and housekeeping genes used in the experiments is concerning, particularly given the importance of using non-circadian housekeeping genes for accurate normalization.
It seems like the resource table describing these important experimental details was omitted in the original submission. We have now included it in the revised version (Table S1).
The methods for measuring metabolic hormones, such as GLP-1 and GIP, are also not adequately described. If DPP-IV/protease inhibitor tubes were not used, the data could be unreliable due to the rapid degradation of these hormones by circulating proteases.
We thank the reviewer for pointing out this omission. We have now added details of how we measured the metabolic hormones to the methods section, including the fact that we have added a DPP-IV inhibitor to the tubes at sampling (lines 469ff).
Finally, the manuscript does not address the collection of hormone levels during both fasting and fed phases, a critical aspect for interpreting the metabolic impact of microbial metabolites.
While we agree that it would be interesting to measure hormone levels also in the fed phase, a more thorough examination of hormone levels over the diurnal cycle, as suggested by reviewer 3, would be relevant for a full-scale follow-up. Given our data, we of course cannot exclude that there may be time-point-specific differences and therefore have softened the language around this conclusion to state that hormone levels are not acutely changed after a lactulose intervention at the time-points examined. (lines 318ff).
These methodological concerns collectively weaken the robustness of the study's results and warrant careful reconsideration and clarification by the authors.
Because of these weaknesses, the authors have partially achieved their aims by providing novel insights into the relationship between microbial metabolites and host circadian rhythms. The data do suggest that microbial metabolites can significantly influence feeding behavior and circadian gene expression in specific contexts. However, the unexpected absence of an osmotic effect of lactulose, the potential biases introduced by the log2-fold change normalization in qRT-PCR data, and the lack of clarity in critical methodological details weaken the overall conclusions. While the study provides valuable contributions to understanding the gut microbiome's role in circadian biology, the methodological weaknesses prevent a full endorsement of the authors' conclusions. Addressing these issues would be necessary to strengthen the support for their findings and fully achieve the study's aims.
We thank the reviewer again for their careful and critical reading of our work, and for their constructive input. In the revised version of our manuscript, we address the reviewer's concerns by providing more methodological detail and additional experimental data.
Despite the methodological concerns raised, this work has the potential to make a significant impact on the field of circadian biology and microbiome research. The study's exploration of the interaction between microbial metabolites and host circadian rhythms in different microbial environments opens new avenues for understanding the complex interplay between the gut microbiome and host physiology. This research contributes to the growing body of evidence that microbial metabolites play a crucial role in regulating host behaviors and physiological processes, including feeding and circadian gene expression.
We thank the reviewer for their encouraging remarks!
Reviewer #3 (Public Review):
Summary:
In the manuscript by Greter, et al., entitled "Acute targeted induction of gut-microbial metabolism affects host clock genes and nocturnal feeding" the authors are attempting to demonstrate that an acute exposure to a non-nutritive disaccharide (lactulose) promotes microbial metabolism that feeds back onto the host to impact circadian networks. The premise of the study is interesting and the authors have performed several thoughtful experiments to dissect these relationships, providing valuable insights for the field. However, the work presented does not necessarily support some of the conclusions that are drawn. For instance, lactulose is administered during the fasting period to mimic the impact of a feeding bout on the gut microbiota, but it would be important to perform this treatment during the fed state as well to show that the effects on food intake, etc. do not occur.
We thank the reviewer for this important point. In the revised version, we include an experiment where we administer lactulose during the fed state and do not observe a significant change in food intake. We describe this in the text (lines 189ff) and in the new Figure S5C and D.
To truly draw the conclusion that the current outcomes are directly connected to and mediated via an impact on the host circadian clock, it would be ideal to perform these studies in a circadian gene knock-out animal (i.e., Cry1 or Cry2 KO mice, or perhaps Bmal-VilCre tissue-specific KO mice). If the effects are lost in these animals, this would more concretely connect the current findings to the circadian clock gene network.
We agree that these would be interesting experiments to follow up on the question how the observed effects are actuated by host functions. However, they would require a large amount of preparatory work (including rederiving the KO mice to get them germ-free in our gnotobiotic facility), we argue that they are beyond the scope of this study.
Despite these reservations, the work is promising.
We thank the reviewer for their encouraging assessment.
Strengths:
Attempting to disentangle nutrient acquisition from microbial fermentation and its impact on diurnal dynamics of gut microbes on host circadian rhythms is an important step for providing insights into these host-microbe interactions.
The authors utilize a novel approach in leveraging lactulose coupled with germ-free animals and metabolic cages fitted with detectors that can measure microbial byproducts of fermentation, particularly hydrogen, in real-time.
The authors consider several interesting aspects of lactulose delivery, including how it shifts osmotic balance as well as provides calculations that attempt to explain the caloric contribution of fermentation to the animal in the context of reduced food intake. This provides interesting fundamental insights into the role of microbial outputs on host metabolism.
Thank you!
Weaknesses:
While the authors have done a large amount of work to examine the osmotic vs. metabolic influence of lactulose delivery, the authors have not accounted for the enlarged cecum and increased cecal surface area in germ-free mice. The authors could consider an additional control of cecectomy in germ-free mice.
We thank the reviewer for pointing out the potential effect of the anatomical differences of germ-free and conventionally colonized mice. We agree that when comparing germ-free mice to SPF mice, the enlarged cecum area in germ-free animals could lead to differences in water release or uptake. However, this difference is smaller in gnotobiotic mice colonized with our minimal microbiota, even though their ceca are still slightly smaller than those of germ-free mice (new Figure S2F). While we agree that including control of cecectomy in germ-free mice could be interesting, we do not have the option of doing surgery on germ-free mice given our current experimental setup. We have now added information on cecum weight, a good proxy for cecum size, in the new Figure S2F done.
The authors have examined GI hormones as one possible mechanism for how food intake is altered by microbial fermentation of lactulose. However, the authors measure PYY and GLP-1 only at a single time point, stating that there are no differences between groups. Given the goal of the studies is to tie these findings back into circadian rhythms, it would be important to show if the diurnal patterns of these GI hormones are altered.
We fully agree that a deeper investigation of the diurnal fluctuations of hormone levels would be an interesting next step in studying whether perturbations in food intake can disturb these rhythms. Doing this for the whole rhythm would really require a full second study.
In response to the reviewer's comments, we have changed the statements made around these data to point out just that hormone level fluctuations could not be detected during specific time points after lactulose treatment and therefore do not seem to explain the imminent behavioral changes (lines 318ff).
Considerations of other factors, such as conjugated vs. deconjugated bile acids, microbial bile salt hydrolase activity, and bile acid resorption, might be an important consideration for how lactulose elicits more influence on ileal circadian clock genes relative to cecum and colon.
We absolutely agree that investigation of microbial bile acid modification and their metabolism by the host would be an interesting topic for a follow-up study.
Measurements of GI transit time (both whole gut and regional) would be an important for consideration for how lactulose might be impacting the ileum vs. cecum vs. colon.
This is also an interesting point. While we did not add an experiment in which we specifically measure transit time to the revised version, we now measure total faecal output in a 5 h time period after PBS or lactulose treatment (Figure S3C). Faecal output is known to be a good proxy for transit time, and we see no significant difference between lactulose treatment (even with a two-fold higher dose than used before, new Figure S3) and PBS treatment.
Recommendations for the authors:
Reviewer #1 (Recommendations For The Authors):
(1) Line 126 - see the point in the public review, this data argues against disrupting the rhythm.
See our response above
(2) Line 156 - the metric used for water content is confusing. Why not just subtract dry weight from wet weight to get water content? The ratio is much harder to think about for me. Perhaps more importantly, this data is very confusing given that colonization seems to impact the activity of lactulose, which complicates the interpretation. Could be an interesting area for future study that you might highlight more in the discussion.
We thank the reviewer for pointing out that our presentation of water content could be clearer. We have changed the dry/wet ratio we have used in the previous version to the "water fraction" (new Figure S2C, E; new Figure S3A,B), i.e., the per cent of weight of the wet sample that is made up by water. We would argue that this is a measurement that is easier to interpret than the difference suggested by the reviewer, because it is independent of the absolute sample weight.
We also agree that it is surprising that colonization state changes the osmotic state of the gut environment and have now added text discussing that (lines 127ff).
(3) Line 188 - the lack of expression changes in the distal gut (cecum/colon) potentially conflicts with the model, warranting additional discussion/qualifications. Is lactulose getting metabolized in the small intestine? Alternatively, does lactulose have a direct effect on the host? The current text seems to imply that lactulose is fermented in the colon, the fermentation products are absorbed, and then they only impact the ileum through circulation, which doesn't seem physiologically possible.
It is possible that lactulose affects small intestinal tissue directly, but we show that the effect depends on microbial activity. Microbial activity is much larger in the large intestine than in the small intestine, which is why we hypothesize that it acts through systemic signals rather than locally. These systemic signals might be fermentation products impacting the ileum through circulation. We would argue that this is not implausible, given that there are well-documented systemic effects of fermentation products in circulation (e.g., den Besten et al, 2013). It is, however, also possible that, e.g., metabolism of fermentation products in the liver triggers a secondary signal that acts systemically.
(4) Line 241 - need to weaken this sub-heading. The experimental design shows that fermentation products impact feeding behavior, but this does not necessarily imply that fermentation products are responsible for the lactulose effect.
Done.
(5) Line 256 - The lack of an effect in SPF mice is surprising and potentially conflicts with the model proposed. Given this and other confusing results (gene expression site specificity, osmolarity effects, etc) it seems prudent to be more cautious as to the potential mechanisms through which lactulose supplementation impacts host gene expression and feeding behavior, which would likely require a lot more experiments to provide a definitive answer.
While the lack of an effect in SPF mice is surprising, we would argue that this is rather points towards the need for a better understanding of host-microbiota-diet interactions than a conflict with our interpretation. We do agree with the reviewer that more work is necessary for providing definitive proof of the underlying mechanisms of the observed effects and have adapted the language throughout the text.
(6) Line 260 - A lot of text is devoted to the potential caloric effects of the fermentation products and the lactulose itself. Was this in response to a prior reviewer? Either way, it seems too speculative to me and I would recommend trimming it down and moving it to the discussion.
We have rewritten this section to make it more concise and increase readability (lines 224ff).
(7) Line 305 - Not fasting, just lower caloric intake, as shown by Figure 1c.
We have changed the text to reflect that.
(8) Line 371 - Too definitive given the current data. Need to qualify the interpretation here.
We have adapted the text and qualified the interpretation.
(9) Figure 2 - Need to revise the title, no data showing that the rhythm is disrupted.
Done.
(10) Figure 3b - Clarify what timepoint is shown in the legend.
Done.
(11) Figure 3c - label when the treatment started. Consider changing to 2-way ANOVA which is probably more appropriate than t-tests.
We have added information on treatment start to the figure legend and have changed the statistical analysis to a two-way ANOVA (time, treatment).
(12) Figure 4c - move to supplement as this negative data isn't sufficient to rule out an impact on the hypothalamus or liver. Even when only considering transcript levels it's possible that the timepoint is just not ideal.
We agree that this data only represents a snapshot of gene expression at one timepoint after treatment and does not rule out involvement of hypothalamus or liver in this process. We have now moved the previous Figure 4C to the supplementary information (new Figure S6A).
(13) Figure 5 - defined the "fermentation products" and their concentrations in the legend. Consider moving panels d, and e to the supplement - negative results with unclear interpretation. Clarify in the legend how many calories/g were assumed for the fermentation products and provide a scientific rationale for this decision. Modify the title to be more cautious - as discussed above.
We thank the reviewer for pointing out that this was not clear. We have now added the formulation of the fermentation products to the figure legend and moved panels D and E to the supplement. We have also combined the former Figures 4AB and 5ABC into the new Figure 4.
(14) Figure S1 - The patterns in panel a are really intriguing and could be discussed more. For example, what do you think is driving the rapid oscillations in E. rectale?
We agree that the patterns are potentially interesting, but the fact that the patterns we observe do not replicate well between the two light-dark cycles we monitor suggest a large contribution of experimental noise. We therefore refrain from interpreting too much into this dataset.
(15) Figure S2 - Could changing the metric for water content be more easily interpretable? Modify the title to better match the data shown.
We thank the reviewer for pointing that out. We have now changed the metric in Figure S2 (and the new Figure S3) to % water in feces/cecum content, which is easier to interpret.
(16) Figure S3 - need to specify the multiple testing correction used.
Done.
(17) Figure S4 title - replace "inducing microbial metabolism" with "lactulose".
Done.
(18) Figure S5 title - modify to weaken the causal claim.
We have adapted all figure titles to conform to this comment.
Reviewer #2 (Recommendations For The Authors):
Greter and colleagues present an insightful manuscript investigating the effects of microbial metabolites, such as hydrogen and SCFAs, on feeding behavior and circadian gene expression at a single time point. Notably, they observed that these metabolites exert a significant influence on behavior in a reduced community model (EAM). However, this effect was not evident in germ-free or SPF mice, highlighting an intriguing paradox. The manuscript is well-written, with experiments that are thoughtfully designed and clearly rationalized. The study contributes valuable data to the poorly understood relationship between the gut microbiome and host circadian rhythms. While I find the manuscript compelling, I believe that providing additional experimental and analytical details would enhance clarity and rigor.
Major Comments:
(1) Additional clarity is needed regarding the stool collection process. Were the samples collected as fresh specimens, or was there a possibility of coprophagia before collection? Clarification on this point is important, as it could impact the results, particularly the dry-to-wet weight ratio analysis. Ensuring the collection process did not introduce this bias is crucial for the validity of these measurements.
Thank you for pointing out that this was not stated clearly. Wherever we assessed water content in faeces, we used fresh samples that were directly collected from a live animal and immediately frozen in a closed container or analyzed. When we assessed total faecal output, we collected the total bedding from a cage, sorted out the faecal pellets, and only measured dry weight. Total wet weight output was then assessed by using the water content of fresh faeces of animals with the same microbiota and the same treatment as a correction factor. We have now made this clear in the methods section (lines 435ff).
In cases where we performed total output measurements by collecting bedding, there was the possibility for coprophagia. We did not control for this but assumed that coprophagia will have a small effect that is likely similar between groups and should thus not affect the comparison.
(2) Caution is advised in the use of the term 'circadian,' which is sometimes used when 'diurnal' might be more appropriate. For example, the title of the first results section could be revised to 'Host Feeding [or Diurnal] Rhythms Influence Microbial Metabolic Fluctuations.' Additionally, line 357 should likely use 'diurnal' instead of 'circadian.' It's important to note that 'circadian' implies that cyclical fluctuations would persist without environmental cues (e.g., feeding). Since it's not clear whether most microbiome compositional or functional fluctuations are truly circadian, 'diurnal' is likely the more accurate term.
We thank the reviewer for pointing out our imprecise use of the term circadian. We have now adapted this throughout the manuscript.
(3) The lack of an osmotic effect of lactulose in EAM mice is quite surprising, given that lactulose is known to be an osmotic laxative. Was this finding specific to EAM mice, or was a similar lack of osmotic effect observed in SPF mice? A positive control is necessary to verify that this unexpected result is not artifactual. If there is no osmotic laxative effect in SPF mice, an explanation is needed as to why this medication is not functioning as expected in these mice.
This is a good point. While we initially thought that the lack of an osmotic effect was due to the specific lactulose dose we were using, we also did not observe an osmotic effect (measured by the water content of fresh faecal pellets produced after treatment) when we used twice the amount of lactulose in EAM mice (new Figure S3). However, in SPF mice, we did see an increase in faecal water content after treatment. This intriguing result suggests that the effect of lactulose as an osmotic laxative depends on the presence of a complex microbiota. We now show this data in the new Figure S3A and discuss it in the text (lines 127ff).
(4) The authors state that 'To account for faulty measurements due to disruptive events and for measurement noise, some datapoints were excluded from the raw datasets.' It would be important for the authors to confirm that this data exclusion was unbiased, meaning it did not disproportionately affect one group over another, and that any exclusions affected groups randomly.
This is a good point, and we analyzed this for the experiments we show in Figs 4A/S5A, 4B/S5E, 4C, and S5F, and discuss this in the methods part (lines 493ff). The resulting statistics is not fully conclusive: using a Chi-square test to check whether the probability of excluding values differs between experiments, we get significant differences (p=3.9 x 10-18). We would, however, argue that this is not surprising, as different experiments sometimes different in the number of times we needed to do maintenance work on the isolators, which could lead to actuation of the scales measuring feed values, and thus faulty measurements.
We face the same problem within experiments: we found a significant difference in the probability to exclude values between treatment and control in the experiment shown in Figs 4A/S5A (p=1.7 x 10-6), but no significant differences in the experiments in Figs 4B/S5E and S5F (p=0.71, and p=0.10, respectively). While it is hard to strictly exclude an influence of our data exclusion strategy, these findings speak against a systematic effect of treatment.
(5) The authors should provide details on the primers and housekeeping genes used in their experiments. It's crucial that the housekeeping gene is not circadian and is stable at all time points (PMID 17878933).
In the previous submission, the main resources table was omitted by accident. We have now added it (Table S1), including details on the primers and reagents used for all experimental work.
(6) The presentation of qRT-PCR data as log2-fold change is confusing. It's unclear what the numerator and denominator represent for this ratio or why such normalization was deemed necessary. Ideally, transcripts should be normalized to a housekeeping gene (as noted in a previous comment), not to a baseline measure of other same genes acquired from other mice. Log2-fold change is typically appropriate when comparing two measures from the same mice; however, in this study, the mice were euthanized, and the denominator is a mean of genes measured from other samples. This approach could introduce bias and might explain why both the positive and negative limbs appear to be activated by the microbial metabolites. It would be more rigorous to present these values as absolute gene expression levels.
We thank the reviewer for pointing out that this was not described clearly in the previous version of our manuscript. We have now adapted the methods part to explain that all data showing RT-PCR data is normalized to a housekeeping gene. Only after that, we compare the gene expression levels of the treatment group to the control group (or to gene expression of the control group at timepoint 0 in the case of Figure 3C).
(7) The use of log-ratios, with a mean as the denominator, could artificially reduce the variability in the data, potentially leading to spurious findings or an increased risk of Type I error.
As pointed out above, we have used internal normalization to a housekeeping gene before comparing the resulting values of the treatment and control groups. This method (commonly known as ΔΔCt method) is a standard way of comparing gene expression values obtained by RT-PCR. The use of a log2 transformation is commonly used to convert the logarithmic data resulting from the RT-PCR measurement to a linear fold-change measurement. We do not see that this data analysis strategy should lead to an increased risk for producing false positives. We now explain this better in the methods section of the manuscript (lines 541ff), and have adapted the labels in Figures 3B, C and S4 to avoid confusion.
(8) It is unusual that both the positive and negative limbs of the circadian clock are overexpressed following lactulose administration. The authors should provide data confirming that these genes are in counter phase to each other at baseline. This clarification would help readers better understand the effects of the experimental interventions. As it stands, this critical part of the results is quite confusing.
We agree that this result does not allow a clear interpretation of the effect of lactulose on the diurnal rhythm of the host. While we agree that this would be interesting to understand in detail, we are merely taking this as a first indication that actuation of microbial metabolism during the inactive phase of the diurnal rhythm can lead to changes in clock genes. This claim is supported by our data.
(9) Could the effects of the microbial metabolites be mediated by AMPK, a known nutrient sensor that can influence the post-translational modification of Cry proteins? It would be beneficial for the authors to explore whether these metabolites have a more direct, previously unknown mechanism of affecting the circadian clock, or if their effects are mediated through known signaling pathways such as AMPK.
We agree that this would be a valuable path to continue investigating the effect of microbial metabolism on clock gene activity.
(10) The methods section does not specify how the metabolic hormones (e.g., GLP-1, GIP, leptin, ghrelin) were measured in the experiments. It is important for the authors to confirm that DPP-IV/protease inhibitor tubes were used for hormone measurement, as these proteins can be rapidly degraded by circulating proteases. Without the use of appropriate tubes, this data cannot be reliably interpreted. Additionally, it would have been ideal to collect these hormone levels during both the fasting and fed phases, but it appears this was not done. This represents a significant limitation of the study and should be addressed in the discussion.
We thank the reviewer for pointing out this omission, we have now added a description of our protocol to measure metabolic hormones to the methods section (lines 469ff).
(11) If the samples were appropriately collected in DPP-IV/protease inhibitor tubes, the authors should consider measuring active GLP-1, as this would likely provide a more accurate assessment of GLP-1 activity.
We agree that this would be a valuable next step, in addition to testing the effect of changes in microbial metabolism on the time traces of hormone levels.
Minor Comments:
(12) Line 350 appears to have an incomplete sentence, as it seems part of the first sentence in the paragraph has been inadvertently deleted. This should be reviewed and corrected for clarity.
Done.
Reviewer #3 (Recommendations For The Authors):
Major comments:
(1) Could the authors provide a deeper description about what they are referring to in the following statement? "...higher order interactions and microbial metabolism are variable..." it is difficult to interpret as written. Do the authors mean cross-feeding interactions?
We have changed this sentence to clarify the meaning.
(2) Could the authors explicitly state their hypothesis in the introduction and provide a brief, but deeper explanation of the intervention prior to the results section?
This is a good point, we have adapted the text accordingly (lines 53ff).
(3) Could the authors include a bit more information regarding the diet provided to the mice? If grain-based chow, please provide insights into the fiber source, etc.
While we agree that it would be interesting to know what part of the mouse diet is available to the microbes, this is hard for the standard mouse chow that we (and most others doing experiments with mice) feed the experimental animals. We have now added more detailed information on the specific type of chow the mice were fed (lines 347f). We would argue that, because the control and treatment groups were always fed the same chow, the effect of the fiber source and other specifics are controlled for, even if we do not know them.
(4) In figure 1A - cells/g does not seem to be the correct unit - # of copies/g feces perhaps?
Cells/g is the appropriate unit, but it seems like we have not explained the way we arrive at this unit in sufficient detail. In short, we use a qPCR run on a known standard curve of bacterial counts (known cells/g values) to estimate these numbers from qPCR results from faeces. We have now explained this better in the methods section (lines 385f).
(5) Figure 1B/C and Figure S1B/C are confusing - the legend states these measurements were taken over two days, however, the plot shows a single 12:12 LD period. Was the data averaged? It might be best to show each day separately (i.e., over a 48-hour period) rather than in one 24-hour plot. Then, the authors could also show the averages in the light period vs. the dark period in a separate, complementary graph.
We thank the reviewer for pointing this out. The previous figures were indeed averaged over the two days of measurement and projected onto one 24h period for plotting. We have now changed Figures 1B,C and S1B,C to show the full 48h time windows.
(6) Line 109 - The reviewer concurs that lactulose is a non-nutritive, synthetic disaccharide, however, in theory, lactulose may have a high heat increment, which could cause the animal to undergo metabolic responses to defend core body temperature (which also exhibits diurnal rhythmicity). Have the authors considered core body temperature rhythms, their connection to microbial metabolism, and the core circadian clock gene network in their model?
This is an interesting thought. We have not measured body temperature in our experiments. As the heat increment from food is typically associated with metabolic activity, and lactulose is not metabolized, we do not expect its heat increment to be high, at least in GF mice. In mice with a microbiota, we agree that metabolic heat will be produced upon lactulose metabolism by the microbes, which could be a contributor the observed effect.
(7) Figure 2A and corresponding text in lines 121 - 123 - indicate at what time the bar and whisker plots were taken (assuming at ZT8, but please be explicit in the figure and corresponding text). Could the authors also include statistics for these waveforms?
Done.
(8) In Figure 2B, the authors state that microbial metabolism had been restored to normal levels by ZT15, however, did this persist into the next light phase? It would be ideal if the authors could present these data in a similar manner to that shown in Figure S2A for SPF mice. Further, what are the statistical considerations here to describe changes in phase, amplitude, periodicity, etc.
This is a good point. Unfortunately, we do not have H2 measurements for EAM and GF mice over comparable time periods as shown for SPF mice in Figure S2A. However, the food intake data shown in Figure S5BCD is a indicates that the food intake normalized in the second dark phase after treatment.
(9) In lines 147 - 149 and in Figure S2B figure legend - assuming these measurements are from individual bacteria? Could this be stated clearly in the text or legend? Also, what are the statistical considerations? Were there significant differences in SCFA production between bacteria?
We thank the reviewer for pointing out that this was unclear. We have now adapted the legend to explain the way these data were collected and added a statistical analysis.
(10) The authors have done a large amount of work to examine the osmotic vs. metabolic influence of lactulose delivery - however, have the authors accounted for the enlarged cecum and increased cecal surface area in germ-free mice? Would an additional control be cecectomy in germ-free mice to be more in-line w/ SPF animals? Further, could the authors tie in these findings more explicitly and state how they pertain to the overall goal of the study? Is this simply to draw the conclusion that microbial biomass is increased w/ lactulose?
We wanted to make sure that the effect we see with lactulose is due to microbial metabolism and not due to the induction of osmotic diarrhoea or other host-dependent effects, and we have added a statement to that effect (lines 127ff). We have not corrected for the change in cecum size between GF and EAM mice, as EAM size (and many other gnotobiotic mouse models) also have enlarged ceca relative to conventionally colonized mice, but have added a dataset showing how cecum size of EAM and GF mice compare and discuss this in the text (new Figure S2F, lines 135ff).
(11) Is Figure 3A necessary?
It might not be strictly necessary, but it can help with understanding the relation of the genes tested in B and C, and we would therefore like to keep it in.
(12) Line 155 - 157 - the authors make the statement that dry/wet feces weight ratio is decreased in GF mice, but this does not appear to be statistically significant. Please adjust to state numerical differences were observed or provide statistics.
We have changed the statement in the text.
(13) Could Figure S3A be moved to the main Figure 3 as this may provide a more logical flow? qRT-PCR data is expressed as - log2 (fold expression), but relative to what? Could the authors provide further info about the control?
The former Figure S3A (new S4A) and Figure 3B show the same data in slightly different ways. We therefore opted to keep only one of those illustrations in a main figure. The fold changes are always relative to the average of the PBS control group, which we now state explicitly in the figure legend.
(14) The authors state that the qRT-PCR data shows that microbial metabolism of lactulose impacts peripheral circadian gene expression, but this conclusion seems simplified. Lactulose treatment only impacted the ileum circadian gene expression. Additional peripheral tissues (liver, adipose tissue, etc.) could be moved to this figure, i.e., move Figure 4C data. Why do the authors think the ileum was most impacted beyond GI hormones as discussed later in the manuscript? Could changes in bile acid deconjugation (i.e., BSH activity?) and/or bile acid resorption by the host in the distal ileum due to lactulose delivery be involved? Or is it simply due to differences in GI transit time (which was not measured in the current study)? Further, lactulose had minimal impact in SPF ileum, and in fact, shifted Cry1 in the opposite direction relative to EAM mice. Could the authors provide more insight into these disparate observations (line 196 - 200)?
We agree that the statement "lactulose impacts peripheral gene expression" is oversimplified, and we have now adapted the text to avoid the impression that this is our conclusion. No tested tissues other than the ileum showed significant differences in gene expression at the time point tested, which does not rule out that other tissues would react to the treatment at that time point, or the tested tissues would do so at the tested time point. As we don't have a good enough understanding of what mechanism causes the gene expression changes in the ileum, we refrain from speculating in the text, even though we agree that this is an intriguing question.
(15) Could the authors provide more insight into the statistical approaches used to assess amplitude, peak, nadir, etc. in Figure 3C? Was the co-sinor waveform tested?
This is a good question. Even though this was a highly work-intensive experiment using many animals, we would argue that the noise level is too high and the coverage of the time analyzed too sparse to infer meaningful statistics on the fluctuations of gene expression over time. In the new version, we have changed our statistical analysis of this dataset to a two-way ANOVA (treatment, time) to better analyze this dataset.
(16) The food intake decrease and interpretation following treatment (Figure 4A and S4A) is curious - all animals were gavaged and in EAM mice, many animals, regardless of PBS or lactulose are trending down in food intake rate/total intake. It seems to be more of an impact of gavage and not of treatment, which the authors somewhat acknowledge in Lines 228 - 230.
We agree that gavage is a possible factor in future food intake of experimental animals, which is precisely why we used the PBS gavage as a control. Even though the difference is not large, we see a significant change in food intake when lactulose is given, but not when PBS is given (Figure 4A, S4A).
(17) Could the authors provide a deeper rationale for their line of thinking for lines 234 - 240? What is the evidence that systemic effects are likely to occur 3 hours after lactulose delivery? Further, as stated in comment 13, could brain and liver data be moved to Figure 3/Figure S3 as an additional example of peripheral tissue clocks?
We have added an explanation for the rationale we use to justify the 8h time point (it is 3h after the peak of H2 production, as shown in Fig2AB, which happens 5h after lactulose delivery). While we agree that the brain and liver data would also fit into the Figure 3, we have now moved all negative data to the supplementary information (in response to a comment by reviewer 1, and in a general effort to clean up the data in the manuscript).
(18) The authors measure PYY and GLP-1 at a single time point and state there are no differences, yet, the goal of the studies is to tie this back to circadian networks. Would it be possible to measure these GI hormones over a 24-hour period to show that the diurnal patterns are altered?
We fully agree that measuring the metabolic hormones over time would be very interesting. It is possible but would represent a major effort using many animals and a large amount of work. We would therefore argue that it is beyond the scope of this revision, but a good starting point for a follow-up study.
(19) The authors state that the administration of fermentation products acutely altered circadian food intake, but the studies do not support that this change is connected to the circadian network. Suggest softening the interpretation of the findings.
We have changed the language there to soften the interpretation.
Minor comments:
(1) The authors should consider when it is appropriate to refer to rhythms as diurnal vs. circadian, as each has a distinct meaning. Diurnal follows entrainment cues while circadian is endogenously driven (i.e., line 39, line 58).
We thank the reviewer for pointing out this important difference, we have adapted this in the whole text accordingly.
(2) Circadian rhythm should be plural throughout the manuscript (circadian rhythms).
Thank you, we have changed that where we refer to host circadian rhythms generally.
(3) Lines 54 - 63. Fermentation should be capitalized when used at the beginning of a sentence.
Done.
(4) Line 289 - This should be Figure 5D and 5E.
Done.
(5) Line 290 - heart should be cardiac.
Done.
