Author response:
Public Reviews:
Reviewer #1 (Public Review):
Summary:
In this study, Kroll et al. conduct an in-depth behavioral analysis of F0 knockouts of 4 genes associated with late-onset Alzheimer's Disease (AD), together with 3 genes associated with early- onset AD. Kroll and colleagues developed a web application (ZOLTAR) to compare sleep-associated traits between genetic mutants with those obtained from a panel of small molecules to promote the identification of affected pathways and potential therapeutic interventions. The authors make a set of potentially important findings vis-à-vis the relationship between AD-associated genes and sleep. First, they find that loss-of-function in late-onset AD genes universally results in nighttime sleep loss, consistent with the well-supported hypothesis that sleep disruption contributes to Alzheimer's-related pathologies. psen-1, an early-onset associated AD gene, which the authors find is principally responsible for the generation of AB40 and AB42 in zebrafish, also shows a slight increase in activity at night and slight decreases in nighttime sleep. Conversely, psen-2 mutations increase daytime sleep, while appa/appb mutations have no impact on sleep. Finally, using ZOLTAR, the authors identify serotonin receptor activity as potentially disrupted in sorl1 mutants, while betamethasone is identified as a potential therapeutic to promote reversal of psen2 knockout-associated phenotypes.
This is a highly innovative and thorough study, yet a handful of key questions remain. First, are nighttime sleep loss phenotypes observed in all knockouts for late-onset AD genes in the larval zebrafish a valid proxy for AD risk?
We cannot say, but it is an interesting question. We selected the four late-onset Alzheimer’s risk genes (APOE, CD2AP, CLU, SORL1) based on human genetics data and brain expression in zebrafish larvae, not based on their likelihood to modify sleep behaviour, which we could have tried by searching for overlaps with GWAS of sleep phenotypes, for example. Consequently, we find it remarkable that all four of these genes caused a night-time sleep phenotype when mutated. We also find it reassuring that knockout of appa/appb and psen2 did not cause a night-time sleep phenotype, which largely excludes the possibility that the phenotype is a technical artefact (e.g. caused by the F0 knockout method) or a property of every gene expressed in the larval brain.
Having said that, it could still be a coincidence, rather than a special property of genes associated with late-onset AD. In addition to testing additional late-onset Alzheimer’s risk genes, the ideal way to answer this question would be to test in parallel a random set of genes expressed in the brain at this stage of development. From this random set, one could estimate the proportion of genes that cause a night-time sleep phenotype when mutated. One could then use that information to test whether late-onset Alzheimer’s risk genes are indeed enriched for genes that cause a night-time sleep phenotype when mutated.
For those mutants that cause nighttime sleep disturbances, do these phenotypes share a common underlying pathway? e.g. Do 5-HT reuptake inhibitors promote sleep across all 4 late-onset genes in addition to psen1? Can 5-HT reuptake inhibitors reverse other AD-related pathologies in zebrafish? Can compounds be identified that have a common behavioral fingerprint across all or multiple AD risk genes? Do these modify sleep phenotypes?
To attempt to answer these questions, we used ZOLTAR to generate predictions for all the knockout behavioural fingerprints presented in the study, in the same way as for sorl1 in Fig. 5 and Fig. 5–suppl. 1. Here are the indications, targets, and KEGG pathways which are shared by the largest number of knockouts:
– Four indications are shared by 4/7 knockouts: “mydriasis” (dilated pupils, significant for psen1, apoea/apoeb, cd2ap, clu); “fragile X syndrome” (psen1, apoea/apoeb, cd2ap, sorl1), “insomnia” (psen2, apoea/apoeb, cd2ap, sorl1); “malignant essential hypertension” (appa/appb, psen1, apoea/apoeb, cd2ap).
– Two targets are shared by 5/7 knockouts: “glycogen synthase kinase−3 alpha” (psen1, apoeab, cd2ap, clu, sorl1) and “neuronal acetylcholine receptor beta−2” (appa/appb, psen1, apoeab, cd2ap, clu).
– Two KEGG pathways are shared by 5/7 knockouts: “cholinergic synapse” (psen1, apoea/apoeb, cd2ap, clu, sorl1) and “nitrogen metabolism” (appa/appb, psen1, psen2, cd2ap, clu).
As reminder, we hypothesised that loss of Sorl1 affected serotonin signalling based on the following annotations being significant: indication “depression”, target “serotonin transporter”, and KEGG pathway “serotonergic synapse”. All three are also significant for psen2 knockouts, but none others. ZOLTAR therefore does not predict serotonin signalling to be a major theme common to all mutants with a night-time sleep loss phenotype.
While perhaps not surprising, we find reassuring that insomnia appears in the indications shared by the largest number of knockouts. apoea/apoeb, cd2ap, sorl1 also happen to be the knockouts with the largest loss in night-time sleep.
Particularly interesting is cholinergic signalling appearing in the most common targets and KEGG pathways. Acetylcholine signalling is a major theme in research on Alzheimer’s disease. For example, the first four drugs ever approved by the FDA to treat Alzheimer’s disease were acetylcholinesterase inhibitors, which increase acetylcholine signalling by preventing its breakdown by acetylcholinesterase. These drugs are generally considered only to treat symptoms and not modify disease course, but this view has been called into question (Munoz-Torrero, 2008; Relkin, 2007). If, as ZOLTAR suggests, mutations in several Alzheimer’s risk genes affect cholinergic signalling early in development, this would point to a potential causal role of cholinergic disruption in Alzheimer’s disease.
We see that literature also exists on the involvement of glycogen synthase kinase-3 in AD (Lauretti et al., 2020). We plan to explore further these predictions in a future study.
Finally, the web- based platform presented could be expanded to facilitate comparison of other behavioral phenotypes, including stimulus-evoked behaviors.
Yes, absolutely. The behavioural dataset we used (Rihel et al., 2010) did not measure other stimuli than day/night light transitions, but the “SauronX” platform and dataset (Myers-Turnbull et al., 2022) seems particularly well suited for this. To provide some context, we and collaborators have occasionally used the dataset by Rihel et al. (2010) to generate hypotheses or find candidate drugs that reverse a behavioural phenotype measured in the sleep/wake assay (Ashlin et al., 2018; Hoffman et al., 2016). The present work was the occasion to enable a wider and more intuitive use of this dataset through the ZOLTAR app, which has already proven successful. Future versions of ZOLTAR will seek to incorporate larger drug datasets using more types of measurements.
Finally, the authors propose but do not test the hypothesis that sorl1 might regulate localization/surface expression of 5-HT2 receptors. This could provide exciting / more convincing mechanistic support for the assertion that serotonin signaling is disrupted upon loss of AD-associated genes.
5-HT receptor type 4a is another candidate as it was shown to interact with sorting nexin 27, a subunit of retromer (Joubert et al., 2004). We see that antibodies against human 5-HT receptor type 2 and 4a exist; whether they would work in zebrafish remains to be tested, and in our experience, the availability of antibodies suitable for immunohistochemistry in the zebrafish is a serious experimental roadblock.
Despite these important considerations, this study provides a valuable platform for high-throughput analysis of sleep phenotypes and correlation with small-molecule-induced sleep phenotypes.
Strengths:
- Provides a useful platform for comparison of sleep phenotypes across genotypes/drug manipulations.
- Presents convincing evidence that nighttime sleep is disrupted in mutants for multiple late-onset AD-related genes.
- Provides potential mechanistic insights for how AD-related genes might impact sleep and identifies a few drugs that modify their identified phenotypes
Weaknesses:
- Exploration of potential mechanisms for serotonin disruption in sorl1 mutants is limited.
- The pipeline developed can only be used to examine sleep-related / spontaneous movement phenotypes and stimulus-evoked behaviors are not examined.
- Comparisons between mutants/exploration of commonly affected pathways are limited.
Thank you for these excellent suggestions, please see our answers above.
Reviewer #2 (Public Review):
Summary:
This work delineates the larval zebrafish behavioral phenotypes caused by the F0 knockout of several important genes that increase the risk for Alzheimer's disease. Using behavioral pharmacology, comparing the behavioral fingerprint of previously assayed molecules to the newly generated knockout data, compounds were discovered that impacted larval movement in ways that suggest interaction with or recovery of disrupted mechanisms.
Strengths:
This is a well-written manuscript that uses newly developed analysis methods to present the findings in a clear, high-quality way. The addition of an extensive behavioral analysis pipeline is of value to the field of zebrafish neuroscience and will be particularly helpful for researchers who prefer the R programming language. Even the behavioral profiling of these AD risk genes, regardless of the pharmacology aspect, is an important contribution. The recovery of most behavioral parameters in the psen2 knockout with betamethasone, predicted by comparing fingerprints, is an exciting demonstration of the approach. The hypotheses generated by this work are important stepping stones to future studies uncovering the molecular basis of the proposed gene-drug interactions and discovering novel therapeutics to treat AD or co-occurring conditions such as sleep disturbance.
Weaknesses:
- The overarching concept of the work is that comparing behavioral fingerprints can align genes and molecules with similarly disrupted molecular pathways. While the recovery of the psen2 phenotypes by one molecule with the opposite phenotype is interesting, as are previous studies that show similar behaviorally-based recoveries, the underlying assumption that normalizing the larval movement normalizes the mechanism still lacks substantial support. There are many ways that a reduction in movement bouts could be returned to baseline that are unrelated to the root cause of the genetically driven phenotype. An ideal experiment would be to thoroughly characterize a mutant, such as by identifying a missing population of neurons, and use this approach to find a small molecule that rescues both behavior and the cellular phenotype. If the connection to serotonin in the sorl1 was more complete, for example, the overarching idea would be more compelling.
Thank you for this cogent criticism.
On the first point, we were careful not to claim that betamethasone normalises the molecular/cellular mechanism that causes the psen2 behavioural phenotype. Having said that, yes, to a certain extent that would be the hope of the approach. As you say, every compound which normalises the behavioural fingerprint will not normalise the underlying mechanism, but the opposite seems true: every compound that normalises the underlying mechanism should also normalise the behavioural fingerprint. We think this logic makes the “behaviour-first” approach innovative and interesting. The logic is to discover compounds that normalise the behavioural phenotype first, only subsequently test whether they also normalise the molecular mechanism, akin to testing first whether a drug resolves the symptoms before testing whether it actually modifies disease course. While in practice testing thousands of drugs in sufficient sample sizes and replicates on a mutant line is challenging, the dataset queried through ZOLTAR provides a potential shortcut by shortlisting in silico compounds that have the opposite effect on behaviour.
You mention a “reduction in movement bouts” but note here that the number of behavioural parameters tested is key to our argument. To take the two extremes, say the only behavioural parameter we measured in psen2 knockout larvae was time active during the day, then, yes, any stimulant used at the right concentration could probably normalise the phenotype. In this situation, claiming that the stimulant is likely to also normalise the underlying mechanism, or even that it is a genuine “phenotypic rescue”, would not be convincing. Conversely, say we were measuring thousands of behavioural parameters under various stimuli, such as swimming speed, position in the well, bout usage, tail movements, and eye angles, it seems almost impossible for a compound to rescue most parameters without also normalising the underlying mechanism. The present approach is somewhere in-between: ZOLTAR uses six behavioural parameters for prediction (e.g. Fig 6a), but all 17 parameters calculated by FramebyFrame can be used to assess rescue during a subsequent experiment (Fig. 6c). For both, splitting each parameter in day and night increases the resolution of the approach, which partly answers your criticism. For example, betamethasone rescued the day-time hypoactivity without causing night-time hyperactivity, so we are not making the “straw man argument” explained above of using any broad stimulant to rescue the hypoactivity phenotype.
Furthermore, for diseases where the behavioural defect is the primary concern, such as autism or bipolar disorder, perhaps this behaviour-first approach is all that is needed, and whether or not the compound precisely rescues the underlying mechanism is somewhat secondary. The use of lithium to prevent manic episodes in bipolar disorder is a good example. It was initially tested because mania was thought to be caused by excess uric acid and lithium can dissolve uric acid (Mitchell and Hadzi-Pavlovic, 2000). The theory is now discredited, but lithium continues to be used without a precise understanding of its mode of action. In this example, behavioural rescue alone, with tolerable secondary effects, is sufficient to be beneficial to patients, and whether it modulates the correct causal pathway is secondary.
On the second point, we agree that testing first ZOLTAR on a mutant for which we have a fairly good understanding of the mechanism causing the behavioural phenotype could have been a productive approach. Note, however, that examples already exist in the literature. First, Hoffman et al. (2016) found that drugs generating behavioural fingerprints that positively correlate with the cntnap2a/cntnap2b double knockout fingerprint are enriched with NMDA and GABA receptor antagonists. In experiments analogous to our citalopram treatment (Fig. 5c,d), cntnap2a/cntnap2b knockout larvae were found to be overly sensitive to the NMDA receptor antagonist MK-801 and the GABAA receptor antagonist pentylenetetrazol (PTZ). Among other drugs tested, zolpidem, a GABAA receptor agonist, caused opposite effects on wild-type and cntnap2a/cntnap2b knockout larvae. Knockout larvae also had fewer GABAergic neurons in the forebrain. Second, Ashlin et al. (2018) found that the fingerprint of pitpnc1a knockout larvae clustered with anti-inflammatory compounds. Flumethasone, an anti-inflammatory corticosteroid, caused a lower increase in activity when added to knockout larvae compared to wild-type larvae. While these studies did not use precisely the same analysis that ZOLTAR runs, they used the same rationale and behavioural dataset to make these predictions (Rihel et al., 2010), which shows that approaches like ZOLTAR can point to causal processes.
Related to your next point, we may reduce the discussion on sorl1 and serotonin and add some of the present arguments instead, depending on the results from testing a second SSRI (see next point).
- The behavioral difference between the sorl1 KO and scrambled at the higher dose of the citalopram is based on a small number of animals. The KO Euclidean distance measure is also more spread out than for the other datasets, and it looks like only five or so fish are driving the group difference. It also appears as though the numbers were also from two injection series. While there is nothing obviously wrong with the data, I would feel more comfortable if such a strong statement of a result from a relatively subtle phenotype were backed up by a higher N or a stable line. It is not impossible that the observed difference is an experimental fluke. If something obvious had emerged through the HCR, that would have also supported the conclusions. As it stands, if no more experiments are done to bolster the claim, the confidence in the strength of the link to serotonin should be reduced (possibly putting the entire section in the supplement and modifying the discussion). The discussion section about serotonin and AD is interesting, but I think that it is excessive without additional evidence.
We mostly agree with this criticism. One could interpret the larger spread of the data for sorl1 larvae treated with 10 µM citalopram as evidence that the knockout larvae do indeed react differently to the drug at this dose. However, the result indeed does not survive removing the top 5 (p = 0.87) or top 3 (p = 0.18) sorl1 larvae.
Given that the HCR did not reveal anything striking, we agree with you that too much of our argument relies on this result being robust. As you and reviewer #3 suggest, we plan on repeating this experiment with a different serotonin reuptake inhibitor (SSRI). If the other SSRI also shows a differential effect, this should strengthen the claim that ZOLTAR correctly predicted serotonin signalling as being affected by the loss of Sorl1, even if we did not discover the molecular mechanism.
- The authors suggest two hypotheses for the behavioral difference between the sorl1 KO and scrambled at the higher dose of the citalopram. While the first is tested, and found to not be supported, the second is not tested at all ("Ruling out the first hypothesis, sorl1 knockouts may react excessively to a given spike in serotonin." and "Second, sorl1 knockouts may be overly sensitive to serotonin itself because post-synaptic neurons have higher levels of serotonin receptors."). Assuming that the finding is robust, there are probably other reasons why the mutants could have a different sensitivity to this molecule. However, if this particular one is going to be mentioned, it is surprising that it was not tested alongside the first hypothesis. This work could proceed without a complete explanation, but additional discussion of the possibilities would be helpful or why the second hypothesis was not tested.
There are no strong scientific reasons why this hypothesis was not tested. The lead author (F Kroll) moved to a different lab and country so the project was finalised at that time. We do not plan on testing this hypothesis at this stage. However, we will adapt the wording to make it clear this is one possible alternative hypothesis which could be tested in the future, rather than the only alternative.
- The authors claim that "all four genes produced a fairly consistent phenotype at night". While it is interesting that this result arose in the different lines, the second clutch for some genes did not replicate as well as others. I think the findings are compelling, regardless, but the sometimes missing replicability should be discussed. I wonder if the F0 strategy adds noise to the results and if clean null lines would yield stronger phenotypes. Please discuss this possibility, or others, in regard to the variability in some phenotypes.
For the first part of this point, please see below our answer to Reviewer #3, point (2) c.
Regarding the F0 strategy potentially adding variability, it is an interesting question which we tested in a larger dataset of behavioural recordings from F0 and stable knockouts for the same genes (unpublished). In summary, the F0 knockout method does not increase clutch-to-clutch or larva-to-larva variability in the assay. F0 knockout experiments found many more significant parameters and larger effect sizes than stable knockout experiments, but this difference could largely be explained by the larger sample sizes of F0 knockout experiments. In fact, larger sample sizes within individual clutches appears to be a major advantage of the F0 knockout approach over in-cross of heterozygous knockout animals as it increases sensitivity of the assay without causing substantial variability. We plan to report in more details on this analysis in a separate paper as we think it would dilute the focus of the present work.
- In this work, the knockout of appa/appb is included. While APP is a well-known risk gene, there is no clear justification for making a knockout model. It is well known that the upregulation of app is the driver of Alzheimer's, not downregulation. The authors even indicate an expectation that it could be similar to the other knockouts ("Moreover, the behavioural phenotypes of appa/appb and psen1 knockout larvae had little overlap while they presumably both resulted in the loss of Aβ." and "Comparing with early-onset genes, psen1 knockouts had similar night-time phenotypes, but loss of psen2 or appa/appb had no effect on night-time sleep."). There is no reason to expect similarity between appa/appb and psen1/2. I understand that the app knockouts could unveil interesting early neurodevelopmental roles, but the manuscript needs to be clarified that any findings could be the opposite of expectation in AD.
On “there is no reason to expect similarity […]”, we disagree. Knockout of appa/appb and knockout psen1 will both result in loss of Aβ (appa/appb encode Aβ and psen1 cleaves Appa/Appb to release Aβ, cf. Fig. 3e). Consequently, a phenotype caused by the loss of Aβ, or possibly other Appa/Appb cleavage products, should logically be found in both appa/appb and psen1 knockouts.
On “it is well known that the upregulation of APP is the driver of Alzheimer’s, not downregulation”; we of course agree. Among others, the examples of Down syndrome, APP duplication (Sleegers et al., 2006), or mouse models overexpressing human APP show definitely that overexpression of APP is sufficient to cause AD. Having said that, we would not be so quick in dismissing APP knockout as potentially relevant to understanding of Alzheimer’s disease. Loss of soluble Aβ due to aggregation could contribute to pathology (Espay et al., 2023). Without getting too much into this intricate debate, links between levels of Aβ and risk of disease are often counter-intuitive too. For example, out of 138 PSEN1 mutations screened in vitro, 104 reduced total Aβ production and 11 even seemingly abolished the production of both Aβ40 and Aβ42 (Sun et al., 2017). In short, loss of soluble Aβ occurs in both AD and in our appa/appb knockout larvae, but the ideal approach would be to study zebrafish larvae with an in-frame deletion in the Aβ sequence within appa/appb.
We will adapt the language to address your point. We would not want to imply, for example, that the absence of a night-time sleep phenotype for appa/appb is contradictory to the body of literature showing links between Aβ and sleep, including in zebrafish (Özcan et al., 2020). As you say, our experiment tested loss of App, including Aβ, while the literature typically reports on overexpression of APP, as in APP/PSEN1-overexpressing mice (Jagirdar et al., 2021).
Reviewer #3 (Public Review):
In this manuscript by Kroll and colleagues, the authors describe combining behavioral pharmacology with sleep profiling to predict disease and potential treatment pathways at play in AD. AD is used here as a case study, but the approaches detailed can be used for other genetic screens related to normal or pathological states for which sleep/arousal is relevant. The data are for the most part convincing, although generally the phenotypes are relatively small and there are no major new mechanistic insights. Nonetheless, the approaches are certainly of broad interest and the data are comprehensive and detailed.
A notable weakness is the introduction, which overly generalizes numerous concepts and fails to provide the necessary background to set the stage for the data.
Major points
(1) The authors should spend more time explaining what they see as the meaning of the large number of behavioral parameters assayed and specifically what they tell readers about the biology of the animal. Many are hard to understand--e.g. a "slope" parameter.
We agree that some parameters do not tell something intuitive about the biology of the animal. It would be easy to speculate. For example, the “activity slope” parameter may indicate how quickly the animal becomes tired over the course of the day. On the other hand, fractal dimension describes the “roughness/smoothness” of the larva’s activity trace (Fig. 2–suppl. 1a); but it is not obvious how to translate this into information about the physiology of the animal. We do not see this as an issue though. While some parameters do provide intuitive information about the animal’s behaviour (e.g. sleep duration or sunset startle as a measure of startle response), the benefit of having a large number of behavioural parameters is to compare behavioural fingerprints and assess rescue of the behavioural phenotype by small molecules (Fig. 6c). For this purpose, the more parameters the better. The “MoSeq” approach from Wiltschko et al., 2020 is a good example from literature that inspired our own Fig. 6c. While some of the “behavioural syllables” may be intuitive (e.g. running or grooming), it is probably pointless to try to explain the ‘meaning’ of the “small left turn in place with head motion” syllable (Wiltschko et al., 2020). Nonetheless, this syllable was useful to assess whether a drug specifically treats the behavioural phenotype under study without causing too many side effects. Unfortunately, ZOLTAR has to reduce the FramebyFrame fingerprint (17 parameters) to just six parameters to compare it to the behavioural dataset from Rihel et al., 2010, but here, more parameters would almost certainly translate into better predictions too, regardless of their intuitiveness.
It is true however that we do not give much information on how some of the less intuitive parameters, such as activity slope or fractal dimension, are calculated or what they describe about the dataset (e.g. roughness/smoothness for fractal dimension). We will improve this in our revised version.
(2) Because in the end the authors did not screen that many lines, it would increase confidence in the phenotypes to provide more validation of KO specificity. Some suggestions include:
a. The authors cite a psen1 and psen2 germline mutant lines. Can these be tested in the FramebyFrame R analysis? Do they phenocopy F0 KO larvae?
We unfortunately do not have those lines. We investigated the availability of importing a psen2 knockout line from abroad, but the process of shipping live animals is becoming more and more cost and time prohibitive. However, we observed the same pigmentation phenotype for psen2 knockouts as reported by Jiang et al., 2018, which is at least a partial confirmation of phenocopying a loss of function stable mutant.
b. psen2KO is one of the larger centerpieces of the paper. The authors should present more compelling evidence that animals are truly functionally null. Without this, how do we interpret their phenotypes?
We disagree that there should be significant doubt about these mutants being truly functionally null, given the high mutation rate and presence of the expected pigmentation phenotype (Jiang et al., 2018, Fig. 3f and Fig. 3–suppl. 2). The psen2 F0 knockouts were virtually 100% mutated at three exons across the gene (mutation rates were locus 1: 100 ± 0%; locus 2: 99.99 ± 0.06%; locus 3: 99.85 ± 0.24%). Additionally, two of the three mutated exons had particularly high rates of frameshift mutations (locus 1: 97 ± 5%; locus 2: 88 ± 17% frameshift mutation rate). It is virtually impossible that a functional protein is translated given this burden of frameshift mutations. Phenotypically, in addition to the pigmentation defect, double psen1/psen2 F0 knockout larvae had curved tails, the same phenotype as caused by a high dose of the γ-secretase inhibitor DAPT (Yang et al., 2008). These double F0 knockouts were lethal, while knockout of psen1 or psen2 alone did not cause obvious morphological defects. Evidently, most larvae must have been psen2 null mutants in this experiment, otherwise functional Psen2 would have prevented early lethality.
Translation of zebrafish psen2 can start at downstream start codons if the first exon has a frameshift mutation, generating a seemingly functional Psen2 missing the N-terminus (Jiang et al., 2020). Zebrafish homozygous for this early frameshift mutation had normal pigmentation, showing it is a reliable marker of Psen2 function even when it is mutated. This mechanism is not a concern here as the alternative start codons are still upstream of two of the three mutated exons (the alternative start codons discovered by Jiang et al., 2020 are in exon 2 and 3, but we targeted exon 3, exon 4, and exon 6).
We understand that the zebrafish community may be cautious about F0 phenotyping compared to stably generated mutants. As mentioned to Reviewer 2, we are planning to assemble a paper that expressly examines F0s vs. stable mutants to allay some of these concerns. We would also suggest that our current manuscript, which combines CRISPR-F0 rapid screening with in silico pharmacological predictions, ultimately represents a first step in characterizing the functions of genes.
c. Related to the above, for cd2AP and sorl1 KO, some of the effect sizes seem to be driven by one clutch and not the other. In other words, great clutch-to-clutch variability. Should the authors increase the number of clutches assayed?
Correct, there is great clutch-to-clutch variability in this behavioural assay. This is not specific to our experiments. Even within the same strain, wild-type larvae from different clutches (i.e. non-siblings) behave differently (Joo et al., 2021). This is why it is essential to compare behavioural phenotypes within individual clutches (i.e., from a single pair of parents, one male and one female), as we explain in Methods (section Behavioural video-tracking) and in the documentation of the FramebyFrame package. We often see two different experimental designs in literature: comparing non-sibling wild-type and mutant larvae, or pooling different clutches which include all genotypes (e.g., pooling multiple clutches from heterozygous in-crosses or pooling wild-type clutches before injecting them). The first experimental design causes false positive findings, as the clutch-to-clutch variability we and others (Joo et al., 2021) observe gets interpreted as a behavioural phenotype. The second experimental design should not cause false positives but will decrease the sensitivity of the assay by increasing the spread within genotypes. In both cases, the clutch-to-clutch variability is hidden, either by interpreting it as a phenotype (first case) or by adding it to animal-to-animal variability (second case). Our experimental design is technically more challenging as it requires obtaining large clutches from unique pairs of parents. However, this approach is better as it clearly separates the different sources of variability (clutch-to-clutch or animal-to-animal). As for every experiment, yes, a larger number of replicates would be better, but we do not plan to assay additional clutches at this time. Our work heavily focuses on the sorl1 and psen2 knockout behavioural phenotypes. The key aspects of these phenotypes were effectively tested in four clutches as sorl1 were also tested in the citalopram experiment (Fig. 5), and psen2 was also tested in the small molecule rescue experiment (Fig. 6 and Fig. 6–suppl. 1). In the citalopram experiment, one H2O-treated sorl1 knockout clutch (n = 10) replicates fairly well the baseline recordings in Fig. 4–suppl. 5, the other does not but had especially low sample size (n = 6).
We also plan to test another SSRI on sorl1 knockouts, so this point will be addressed.
(3) The authors make the point that most of the AD risk genes are expressed in fish during development. Is there public data to comment on whether the genes of interest are expressed in mature/old fish as well? Just because the genes are expressed early does not at all mean that early- life dysfunction is related to future AD (though this could be the case, of course). Genes with exclusive developmental expression would be strong candidates for such an early-life role, however. I presume the case is made because sleep studies are mainly done in juvenile fish, but I think it is really a pretty minor point and such a strong claim does not even need to be made.
This is a fair criticism but we do not make this claim, at least not from expression. The reviewer is probably referring to the following quote:
“[…] most of these were expressed in the brain of 5–6-dpf zebrafish larvae, suggesting they play a role in early brain development or function,”
which does not mention future risk of Alzheimer’s disease. We do suggest that these genes have a function in development. After all, every gene that plays a role in brain development must be expressed during development, so this wording seems reasonable. As noted, the primary goal was to check that the genes we selected were indeed expressed in zebrafish larvae before performing knockout experiments. Our discussion does raise the hypothesis that mutations in Alzheimer’s risk genes impact brain development and sleep early in life, but this argument primarily relies on our observation that knockout of late-onset Alzheimer’s risk genes causes sleep phenotypes in 7-day old zebrafish larvae and from previous work showing brain structural differences in infants and children at high genetic risk of Alzheimer’s disease (Dean et al., 2014; Quiroz et al., 2015), not solely on gene expression early in life.
(4) A common quandary with defining sleep behaviorally is how to rectify sleep and activity changes that influence one another. With psen2 KOs, the authors describe reduced activity and increased sleep during the day. But how do we know if the reduced activity drives increased behavioral quiescence that is incorrectly defined as sleep? In instances where sleep is increased but activity during periods during wake are normal or elevated, this is not an issue. But here, the animals might very well be unhealthy, and less active, so naturally they stop moving more for prolonged periods, but the main conclusion is not sleep per se. This is an area where more experiments should be added if the authors do not wish to change/temper the conclusions they draw. Are psen2 KOs responsive to startling stimuli like controls when awake? Do they respond normally when quiescent? Great care must be taken in all models using inactivity as a proxy for sleep, and it can harm the field when there is no acknowledgment that overall health/activity changes could be a confound. Particularly worrisome is the betamethasone data in Figure 6, where activity and sleep are once again coordinately modified by the drug.
This is a fair criticism. We agree it is a concern, especially in the case of psen2 as we claim that day-time sleep is increased while zebrafish are diurnal. We do not rely heavily on the day-time inactivity being sleep (the ZOLTAR predictions or the small molecule rescue do not change whether the parameter is called sleep or inactivity), but our choice of labelling may be misleading. We will try to test this claim by plotting the distribution of the inactive period durations. If psen2 knockout larvae indeed sleep more during the day compared to controls, we might predict that inactive periods longer than 1 minute to increase disproportionately compared to the increase in shorter inactive periods.
To address, “are psen2 KO responsive to startling stimuli like controls when awake/when quiescent”, we can try to look at the behaviour of psen2 knockout larvae that were awake (i.e., moved in the preceding one minute) or ‘asleep’ (i.e., did not move in the preceding one minute) at the light transitions and count the proportion of psen2 knockout or control larvae which displayed a startle response. If most psen2 knockouts react to the light transition, it should at least exclude the concern that they are very unhealthy, as the reviewer suggests. This criticism seems challenging to definitely address experimentally though. A possible approach could be to use a closed-loop system which, after one minute of inactivity, triggers a stimulus which is sufficient to startle an awake larva but not an asleep larva. If psen2 knockout larvae indeed sleep more during the day, the stimulus should usually not be sufficient to startle them. Note, how to calibrate this stimulus is also not straightforward. We do not plan to test this, but our analysis of the light transitions may provide a decent proxy.
(5) The conclusions for the serotonin section are overstated. Behavioural pharmacology purports to predict a signaling pathway disrupted with sorl1 KO. But is it not just possible that the drug acts in parallel to the true disrupted pathway in these fish? There is no direct evidence for serotonin dysfunction - that conclusion is based on response to the drug. Moreover, it is just 1 drug - is the same phenotype present with another SSRI? Likewise, language should be toned down in the discussion, as this hypothesis is not "confirmed" by the results (consider "supported"). The lack of measured serotonin differences further raises concern that this is not the true pathway. This is another major point that deserves further experimental evidence, because without it, the entire approach (behavioral pharm screen) seems more shaky as a way to identify mechanisms. There are any number of testable hypotheses to pursue such as a) Using transient transgenesis to visualize 5HT neuron morphology (is development perturbed: cell number, neurite morphology, synapse formation); b) Using transgenic Ca reporters to assay 5HT neuron activity.
Regarding the comment, “is it not just possible that the drug acts in parallel to the true disrupted pathway”, we think no, assuming we understand correctly your question. Key to our argument is the fact that sorl1 knockout larvae react differently to the drug than control larvae. As an example, take night-time sleep bout length, which was not affected by knockout of sorl1 (Fig. 4–suppl. 5). For the sake of the argument, say only dopamine signalling (the “true disrupted pathway”) was affected in sorl1 knockouts but that serotonin signalling was intact. Assuming that citalopram specifically alters serotonin signalling, then treatment should cause the same increase in sleep bout length in both knockouts and controls as serotonin signalling is intact in both. This is not what we see, however. Citalopram caused a greater increase in sleep bout length in sorl1 knockouts than in scrambled-injected larvae. In other words, the effect is non-additive, in the sense that citalopram did not add the same number of Z-scores to sorl1 knockouts or controls. We think this shows that serotonin signalling is somehow different in sorl1 knockouts. Nonetheless, we would concede that the experiment does not necessarily says much about the importance of the serotonin disruption caused by loss of Sorl1. It could be, for example, that the most salient consequence of loss of Sorl1 is cholinergic disruption (see reply to Reviewer #1 above) and that serotonin signalling is a minor theme.
Furthermore, we agree with you and Reviewer #2 that the conclusions are overly confident. We will repeat this experiment with another SSRI as you suggest. Your suggestions to further test the serotonin system in the sorl1 knockouts are excellent as well, however we do not plan to pursue them at this stage.
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