Reciprocal differentiation via GABAergic components and ASD-related phenotypes in hES with 1q21.1 CNV

  1. Yoshiko Nomura
  2. Jun Nomura
  3. Toru Nishikawa
  4. Toru Takumi

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Abstract

Copy number variations (CNVs) in the distal 1q21.1 region, both deletion (1q del) and duplication (1q dup), are associated with autism spectrum disorder, epilepsy and schizophrenia. Besides common phenotypes, 1q del and 1q dup manifest opposite clinical phenotypes—e.g., microcephaly in 1q del and macrocephaly in 1q dup. However, molecular and cellular mechanisms are still elusive. We generate isogenic human ES (hES) cell lines with reciprocal 1q21.1 CNVs using CRISPR/Cas9 system and differentiate them into 2-dimensional (2-D) neurons and 3-D cortical organoids. Our study recapitulates opposite organoid size and shows dosage-dependent differentiation changes i.e., more mature and GABAergic components in 1q del and more proliferative state in 1q dup. In contrast, both CNVs show hyperexcitability and altered expressions of glutamate system as common features. These results demonstrate that 1q21.1 CNVs dramatically affect cell fate in the early neurodevelopmental periods. This is the first isogenic model of hES CNVs and our findings provide new insights into the underlying mechanisms of neurodevelopmental disorders.

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    Reply to the reviewers

    Reviewer #1:

    Summary

    Copy number variations in the 1q21.1 loci, deletions and duplications, have been associated with neurodevelopmental disease. In particular, deletions of this locus result in a variety of neuronal phenotypes including microcephaly and schizophrenia in varying levels of severity. Duplications of the 1q21.1 locus are often associated with autism and/or macrocephaly.

    In this study Nomura et al. generated 1q21.1 deletion and duplication hESC lines to study the impact of these CNVs on neuronal development. They generated brain organoids and observed a bidirectional effect of this CNV on organoid size, with 1q21.1 deletion showing smaller brain organoids whereas, the 1q21.1 dup lines grew large than controls. This in line with observed micro and macrocephaly observed in patients. They further analyzed these organoids at the gene expression level using single cell RNAseq and performed some electrophysiological assessment on neurons from of dissociated organoids.

    This study is certainly of interest given the association of this loci with NDDs such as autism, epilepsy and schizophrenia. At this stage, the study is mainly a descriptive study, showing differences between the 1q21.1 del/dup versus controls but also between both the del/dup lines. There is no mechanistic insight provided. For example the 1q21.1 CNV encompasses several genes, of which some have already been linked to micro/macrocephaly (eg. NOTH2NL). More importantly, most of the conclusions drawn by the authors are based on a limited set of experiments/analysis which are not always carefully performed and/or presented. In general, the data presented are premature, therefore not supporting the claims/conclusion made by the author (eg title) This makes the overall impact of this study limited.

    As the reviewer pointed out, NOTCH2NL (both A and B) have been regarded as micro/macrocephaly-related genes (Fiddes et al., Cell, 2018; Suzuki et al., Cell, 2018). In this study, however, we focused on the distal region of 1q21.1 between BP3 and BP4, which contains neither NOTCH2NLA nor NOTCH2NLB, because the target site is thought to be the core region of clinical 1q21.1 microdeletion/microduplication syndrome (Mefford et al., NEJM., 2008; Brunetti-Pierri et al., Nat. Genet., 2008; Van Dijck et al., EJMG, 2015). Although both NOTCH2NLA and B are located outside of our target, these genes are important for human neocortical development and neurogenesis, so we cite these papers (Fiddes et al. and Suzuki et al.) and discuss them in the discussion of the revised manuscript.

    Main comments

    In general, the interpretation of the data is too premature:

    1. The title is not supported in any means by data

    As requested by the reviewer, we have corrected the title as “Modeling reciprocal CNVs of chromosomal 1q21.1 in cortical organoids reveals alterations in neurodevelopment”.

    1. Brain organoids size and development: In figure 2 the authors analyzed the development of the organoids. Based on the human phenotype the deletion would lead to smaller brain and the duplication to larger brain organoids. The presented data to support these claims are rather scarce. They indeed provide data on organoid size, however there is no information as to regard how this micro/macrocpehaly comes about. Only limited amount of cell types are being investigated with immunocytochemistry, which give little insight into the mechanism. Fig 3. The authors performed some very basic immunostaining and concluded that the neuronal maturity of 1q del seemed to be accelerated, whereas 1q dup decelerated from the NPC stage. However, there is no direct evidence provided for this. With simple additional immunostainings authors could already get a much better idea of what is going on. For example the authors could measure the amount of differentiating versus proliferating cells, cell cycle exit, etc (eg BrDU, KI67, pHH3 staining,...)

    We thank the reviewer for the suggestion. In response to this, we plan to analyze additional markers such as phosphor-histone H3 (pHH3) to evaluate the late-G2/M status by immunostaining. In addition, to explain the smaller organoid size observed in 1q del organoids, we will check apoptosis markers such as cleaved-caspase3 by immunostaining and western blotting.

    Further there are some technical aspect that would need to be resolved:

    There is a general lack of brain organoid characterization of the controls. It is unclear on how many independent clones these experiments were performed.

    We constructed one clone per genotype (1q21.1 deletion (1q del), 1q21.1 duplication (1q dup) and CTRL) from one human ES cell strain (khES-1) by next-generation chromosome engineering using the CRISPR/Cas9 system. According to the reviewer’s comment, we have added the information of each clone, including the actual number of each clone in the results section. Following the reviewer’s comment, we also recognized the importance of comparing targeted clones even in the same genotype to verify cellular phenotypes in a targeted clone. However, we consider that at least isogenic ES cell lines are less affected by genetic variances on other regions and epigenetic changes than patients-derived iPS cells.

    • Fig 2C: it is unclear why brain organoid sizes reduce over time. Is this an indication of increased apoptosis? Did the authors measure this?

    In order to respond to the reviewer’s comment, we plan to examine apoptotic markers such as cleaved caspase-3 by immunostaining or western blotting, as mentioned above.

    • What is the reason for using t-test with Bonferroni correction as opposed to one -way (or even two-way) Anova is unclear in Fig 2C

    Analysis of variance (ANOVA) has been regarded as optional when multiple comparisons without F-statistics are performed (Jason Hsu. 1996. Multiple Comparisons: Theory and Methods (Guilford School Practitioner)). We selected the Bonferroni test because we thought we could evaluate our data more strictly with the Bonferroni test than with the Tukey-Kramer test. In response to the reviewer’s request, we analyzed our data using one- way ANOVA with the Tukey-Kramer test. We confirmed that statistical significances were consistent (we can provide both data if requested). We have changed the description in the figure legend and methods section of the revised manuscript.

    • 2E is unclear how they came to the conclusion that dosage dependent size difference in NPC organoids was caused by the number of cells within an organoid, not by the size of each cell or different cell types. Since they only measured the amount of Sox 2 positive cells and used Sox2 to measure cell diameter, whereas Sox2 is mainly expressed in the nucleus.

    We thank the reviewer’s comment. We used images of SOX2 staining because contrasts of each cell in bright-field images were too obscure to be detected using the fluorescent microscopy, BZ-X analyzer, and because we found cell sizes seemed similar between bright-field images and SOX2 staining images. However, this method was not desirable. To respond to the reviewer’s comment, we have counted the number of cells in the images of each NPC organoid using the BZ-X analyzer and calculate the cell number per 1000 µm2. We found the cell density was not significantly different among the 3 genotypes. We understand that counting the cell number of a single organoid would be ideal, but it was impossible because each NPC organoid was too small. We have changed Figure 2E, descriptions in the methods and results section, and the corresponding figure legend in the revised manuscript.

    • How do the authors explain that the Dup cells do not express Tubb neither CTIP2, do they only express NPCs and no neurons?

    We consider this finding supports the immaturity in the cortical organoids with 1q21 duplication. However, we have checked only a few markers for intermediate progenitors and mature neurons so far. We plan to examine immature neuronal markers such as DCX and other mature neuronal markers such as NeuN by immunocytochemistry (ICC) to confirm this finding. Similarly, we will perform expression analysis by real-time qPCR to check mature and immature neuronal cell markers.

    In short, the characterization of the brain organoids at the level of general development, cell types, proliferation, differentiation is underdeveloped.

    We will examine the characterization of the brain organoids in more detail by different techniques as described above.

    1. Electrophysiological assessment of brain organoids derived neurons:

    In figure 4 the authors claim that both CNVs (Del/Dup) show hyperexcitability and altered expressions of glutamate system as common features between the Del/Dup lines. The data to support this are however scarce and far from being convincing:

    The poor quality of the data is represented by images in 4B-E:

    • First the authors choose to dissociate the organoids prior to measure the cells on MEA's. This takes away the advantage of 3D brain organoids, will add a lot of non-physiological stress, cause cell death and lead to unequal distribution of cells over the electrodes, see fig 4B.

    We are afraid that the reviewer might misunderstand our experiment. In this experiment, we used not 3-D brain organoids but 2-D neurons. Based on established neural differentiation protocol (Fujimori et al., Stem Cell Reports, 2017, Toyoshima et al., Transl. Psychiatry, 2016, Matsumoto et al., Stem Cell Reports, 2016), we seeded single-cells dissociated from neurospheres on MEA dishes at the same density (8 x 105 cells per dish) on day 33 and continued culturing for 28 days on the MEA dish before analysis. Thus, we didn’t dissociate cells just before analysis. We could avoid adding non-physiological stress because we kept on culturing on the MEA dish for 28 days.

    • MEA recording are meant to measure network activity and heavily (read: fully) dependent on the network being formed. Cherry picking electrodes for analysis is not justified, analysis should be performed per MEA chip not per electrode. Inclusion/exclusion parameters should be defined before analysis

    We have performed statistical analysis with all chips (electrodes) per genotype in response to the reviewer's request. Even though the distributions of firing rate were not consistent among electrodes, we found the significant differences between CTRL and each mutant (Ctrl vs 1q del: p< 0.001, Ctrl vs 1q dup: p< 0.001, 1q del vs 1q del: p=1.0). We have changed Figure 4E, the descriptions in the methods section, and the corresponding figure legend in the revised manuscript this time. We also reanalyzed burst rates so that all electrodes were included in the statistical analysis. We have changed supplementary Figure 3 and edited the descriptions in the methods and the corresponding figure legend in this revised manuscript.

    • MEA parameters such as Mean firing rate (spike/min) and burst rate are very sensitive to plating conditions, especially number of cells and clustering of cell around electrodes (see 4B). Given that the organoids already differ in size and according to the authors in cell number, but also in the amount of starting NPCs, one can expect very different cell densities/cell types per experiment/genotype. The authors should therefore show for every genotype the matching cell culture images. Also with regard to the claims made about GABAergic neurons the cell type composition at the time of the MEA recording should be characterized for every genotype.

    As mentioned above, in MEA analysis, we used 2-D neuronal culture and seeded cells on each chip at the same density. The distribution patterns of cells were similar among the 3 genotypes. We will show the images of cultured neurons from 3 genotypes in the revised figure. As for the cell type composition, we plan to examine the expressions of GABAergic markers using extracted RNAs from neuronal cells on around 28 days post- dissociation (dpd). As reviewer #2 suggested, we also considered that drug treatment with bicuculine in this MEA system was meaningful. We plan to perform this experiment if the experimental conditions can be optimized.

    • Fig 4B illustrates the points made above. The fact that no activity is observed in the control cells can be due to many different reasons: unequal plating, stress after dissociating cells, poor coverage of the electrodes, poor maturation, too early measuring time point, etc Because the authors have no control over the amount of cells covering the electrodes the data presented here carry very little carry little information. Fig 4B, best illustrates this with large cell clumps and areas without cell bodies. Measurements from these cell cultures are irrelevant and no conclusion can be drawn.

    We suggest that the authors first benchmark this technique with their own differentiation protocol, show robust and reliable recordings on control cells, and only compare to the CRISPR lines at a time point at which the control cells show a decent amount of activity 1Hz. When doing so, also reduced activity can be monitored (For examples see, Trujillo et al, Cell Stem Cell2019 or Frega et al 2019 Nat comm).

    As mentioned above, we seeded dissociated neurospheres in equal numbers on MEA dishes and kept culturing neurons gently for 28 days before analysis. Cell distribution was similar among the 3 genotypes and we could observe cell bodies in the area outside aggregates (we will provide additional bright-field images in the revised manuscript later). Low activities in CTRL neurons at 28 dpd could be observed even in the electrodes covered with dense cells, which were consistent among 3 independent experiments as described above. Nonetheless, we agreed with the reviewer that cellular conditions which could show stable activities even in CTRL neurons were more desirable. We have already tried longer cultures three times, but we could not perform sufficient analyses because neuronal cells became unhealthier after 35 dpd. We will try to improve the experimental conditions and perform analyses if the experimental conditions could be optimized.

    • MEAs measure the output of the network (action potentials). In a network, this can be influenced by virtually every neuronal property (morphology, synaptic input, types ofsynapses, intrinsic excitability, etc). Therefore, the authors cannot conclude only based on fig 4E that the Del/Dup cells are intrinsically hyperactive. To make this conclusion they should measure this directly by assessing that passive and active intrinsic properties of individual neurons.

    In control condition many electrodes do not give any signal. From these experiments it is impossible to know whether this is because of lack of cell on the particular electrode or real absence of activity. Certainly one could not conclude that the del en dup cell are intrinsically hyperexcitable.

    As described above, we could observe the similarity of cell distributions among 3 genotypes. However, as the reviewer mentioned, the assessment of the individual neuronal activity would be better. Thus, we will perform patch-clamp recordings in addition to MEA analysis.

    It seems that from the introduction the authors try to link 1q21 CNVs to epilepsy and ASd, thereby justifying the observed phenotypes.

    • How do the authors reconcile the fact that more mature GABA system is observed in the Del lines with the so called increased activity compared to controls but not to the Dup lines.

    We assumed that cell type compositions differed between 1q del and 1q dup, although network excitabilities were commonly observed in both mutants. We agree that this assumption lacks sufficient evidence even though we have shown the results in scRNAseq (Figure 6E). We consider that checking cell type compositions would be needed to ensure this. Although mature GABAergic neurons were increased in 1q del lines as mentioned by the reviewer, we think GABAergic signals and unknown factors such as epilepsy- associated genes (e.g., GRIN2A and SCN1A) may be involved in the abnormal neuronal firing. We will check the expression of these genes and examine the expressions of GABAergic markers in neuronal cells.

    Single cell RNAseq

    • I'm not a specialist on single cell RNAseq, however it seems that the analysis is underdeveloped and conclusion drawn for these experiments premature. It would be essential to validate some of the generated hypothesis, eg GABA maturity and not merely state as a conclusion (eg title).

    We thank the reviewer for the suggestion. We have revised the title as we mentioned above, and we will revise the main text based on our results appropriately.

    • How do the authors explain that a majority of the cells are Glial cells at day 27, and no presence of neurons.

    On day 27 in our 3-D organoid protocol, cells were still in the developmental stage. That’s why we consistently described it as “NPC organoid” but not “brain organoid” in this paper. Indeed, our rationale for the scRNA-seq study was to determine gene(s) or gene regulatory network(s) when the difference of circumference was significant among genotypes (Fig. 2C). Although the underlying mechanism was not fully understood from our results, we interpreted this result. Radial glial cells (RGs) have the ability to self- renewal with symmetric divisions and play a role in both neurogenesis and gliogenesis (Lui et al. Cell 2011, A Kriegstein et al., Annu Rev Neurosci 2009). A recent study showed that the reduction of NF1, a tumor suppressor protein in the RAS/MAPK pathway, induced excessive production of glial cells, i.e., mainly oligodendrocyte precursor cells (OPCs) accompanied with astrocyte precursor cells, from RGs; furthermore, the reduction of NF1 also enhanced the cell divisions of generated OPCs (Z Shen, BioRxiv 2020). We have checked that the expression of NF1 in the glial cluster was also downregulated in our scRNA-seq data. Thus, we reasoned that the predominance of 1q dup cells in the glial cluster reflected the excessive production of glial cells from RGs, which were related to the alteration of the RAS/MAPK pathway. We will add this interpretation in the revised manuscript next time.

    • How relevant is the changes in the extremely low amounts of GABAergic neurons in the Del cells, no excitatory neurons are present, only NSCs

    In a previous paper, CA Trujillo et al. showed the cell type composition in 3-D human cortical organoids at different time points. GABAergic cells were restricted to later stages and the ratio was still very limited at 6 months (Figure 1J in CA Trujillo et al., Cell Stem Cell 2019). From this fact, we regarded the emergence of GABAergic neurons as meaningful even if the ratio was very low. As for excitatory neurons, we will further check the expressions of excitatory neuronal markers. (According to the screening chart we used, we did not explore excitatory neuronal markers as far as cells did not express SLC17A7 significantly).

    Minor comments

    • It is unclear how many clones were assessed per genotype

    We constructed one clone per genotype. As we mentioned above, we have added the information in the results section of this preliminary revised manuscript.

    • The authors should properly annotate the genotypes 1q21.1 instead of 1q del (line 134)

    We have already annotated the abbreviations of 1q21.1 deletion and duplication in lines 87 and 93.

    • Introduction seems to be somehow off topic since 1q21.1 locus is associated with several neurodevelopmental disorders, including SCZ, but is certainly not specific to ASD and epilepsy. So the premiss on line 86: to study 1q21.1 locus to understand ASD/epilepsy is somewhat misleading. I propose that the introduction would be focussed on the 1q21.1 and not on general on ASD/epilepsy.

    As the reviewer pointed out, 1q21.1 CNVs are associated with other neurodevelopmental and neuropsychiatric disorders. Since our research aims to elucidate the underlying mechanism of ASD, we mainly focused on two representative comorbidities (abnormal brain size and epilepsy), which seemed relatively reproducible in vitro. However, we agree with the reviewer that the lack of information about clinical symptoms of 1q21.1 microdeletion and microduplication syndrome besides ASD was not appropriate. Thus, we will revise the introduction to mention the neurodevelopmental phenotypes of 1q21.1 CNVs in the revised manuscript next time.

    • It is unclear whether they generated heterozygous or homozygous deletions.

    We thank the reviewer for pointing it out. We have generated clones with heterozygous deletion and duplication. We have added the information in the results section of this revised manuscript.

    • The authors should cite Fiddes, I. T. et al. Human-Specific NOTCH2NL Genes Affect Notch Signaling and Cortical Neurogenesis. Cell 173, 1356-1369.e22 (2018).

    As the reviewer suggested, we will cite two papers regarding NOTCH2NL (NOTCH2NLA: Fiddes, I. T. et al., Cell 173, 2018; NOTCH2NLB: Ikuo K Suzuki et al., Cell 173, 2018) when we discuss the alteration of neuronal maturity and brain size. We will add the information in the revised manuscript next time.

    • Many unclear statements eg line 138: Next, we analyzed each single-cell in an organoid

    We thank the reviewer for noticing it. We have made an effort to remove inappropriate sentences in this revised manuscript.

    • Discussion on E/I is very speculative, not supported by any evidence

    In response to the reviewer’s suggestion, we will cut the descriptions which contain too speculative contents in the discussion section of the revised manuscript later.

    Significance

    The general topic of this study is high interest given the strong association of the 1q21.1 with disease. The authors developed interesting ESC line to study in parallel del and duplication. Unfortunately the level of of analysis performed on these organoids is not up the current stat of the art, are of low experimental quality, analyses are limited. Therefore no clear conclusion can be drawn except for the size of the organoids, very little mechanism is provided. This therefore remains a purely descriptive study for which the presented data are rather on low quality and limited impact in its current shape.

    We thank the reviewer for the interest and criticism of our paper. As discussed above, we plan to perform additional analyses and experiments to justify our hypothesis more clearly and try to meet the reviewer’s requests.

    Reviewer #2

    This study was initiated to look at specific cellular and molecular mechanism of the duplication and deletion CNV frequently observed at the 1q21.1 gene locus in an isogeneic human embryonic stem (hES) cell model. The authors note that these CNVs are associated with higher than normal penetrance of ASD and epilepsy and aim to elucidate gene expression differences with single cell RNAseq and functional changes in this model system. The authors further sought to proliferation and differentiation states, in addition to neuronal activity, using both 2D cultures and 3D organoid models. The 1q21.1 gene locus model system made here is unique and the results broadly recapitulate the patient phenotype particularly with observations of macrocephaly in the "1q dup" and microcephaly in the "1q del".

    Reviewers statement:

    We have joint expertise in GABAergic neuronal development, iPSC 2D and 3D culture and ASD human molecular genetics.

    Major comments:

    • Not sure why ASD (if used it should also be spelled out) is mentioned in the title if ASD is only seen in a proportion of human 1q21.1. duplication (~36% will have autism) and 1q21.1 deletion (<10% will have autism) carriers. I would prefer to use 'neurodevelopmental phenotype'. A good update review that is accurate with respect to this CNV role in autism is PMID: 29398931. The authors should also put into the context of their results what is known with other neuropsychiatric phenotypes also seen in these CNV events;

    We thank the reviewer for the suggestion and valuable information. We have corrected the title in the revised manuscript this time. We will also refer to the paper by Fernandez and Scherer (Dialogues Clin. Neurosci., 2017) to discuss the detail of roles and neuropsychiatric phenotypes of targeted CNVs.

    • In Fig 1D the ddPCR validation for the genetic alterations in 1q del shows a normal return to 2 copies of GPR89B. However, in the 1q dup the CNV level is still elevated for GPR89B. Please determine how much further the duplication goes as there are five more potentially affected genes in this region (eg PDZK1P1). Modify the text appropriately to note the potential influence of any of these other genes on the experimental outcomes.

    We thank the reviewer for pointing it out. Figure 1D showed the results of aCGH analysis to confirm the copy number alteration of the targeted region in each clone. This analysis expected that the target region contained GPR89B, as confirmed by PCR shown in Fig. 1B. However, as the reviewer’s comment, the cleavage sites shown in Figure 1D seem not consistent with the result of Fig. 1B. We think it reflects the limitation of the microarray-based CGH technique. Since the locus between GPR89B and LOC101927468 contains extensive repeat sequences, aCGH may not be an appropriate method. Thus, we will apply quantitative PCR (or ddPCR) to determine copy number alternation of each clone in addition to microarray-based CGH.

    • The authors' claim that dosage dependent size differences in NPC organoids is caused by a change in the number of cells within the organoid rather than size - from Fig. 2D, cells in 1qdel organoid appears more compact; a quantification of cell number should be done to support this claim. IHC of D27/28 organoids with GABAergic markers would support authors' claim of alterations of GABAergic components in 1qdel cells. These suggested experiments would take 2-3 days if the organoids are available.

    In response to the reviewer’s suggestion, we have counted the number of cells in the images of each NPC organoid using the fluorescent microscopy, BZ-X analyzer, and calculated the cell number per unit area (1000 µm2). We found the cell density was not significantly different among the 3 genotypes. We have changed Figure 2E, descriptions in the methods and results sections, and the corresponding figure legend in the revised manuscript this time. As for exploring GABAergic components in the NPC organoids, we plan to perform immunocytochemistry (ICC) and RT-qPCR analysis.

    • Fig 4 E shows MEA data from "top 10". What is the top ten? Do you mean data points? There are batch differences in 1q dup with one batch having a lower expression than the other. Increasing the n value to accommodate the high variance observed in this group will greatly increase the validity of the data generated. Also, change the figure legend to indicate the age of these cultures. Given that the controls are not spiking, this data should be extended to probe the developmental profile further to week 9 when normal cells should be spiking so that the baseline activity of this isogenic line can be determined.

    Top 10 meant the ten electrodes with the highest spike rates within one MEA dish. To respond to the reviewer’s suggestion, we have performed statistical analysis with all electrodes per genotype. Even though the distributions of firing rate were quite heterogeneous among different electrodes, we found significant differences between CTRL and each mutant per MEA dish. We have changed Figure 4E, descriptions in the methods section, and the corresponding figure legend in the revised manuscript this time.

    The reviewer is correct that the spike rates in 1q dup were quite different between different batches. We noticed from our experiments that spike rates were easily affected by the health conditions of cells. Some mutant batches showed mild spike activities like circles in 1q dup, and some had very vigorous activities. We have even checked the reproducibility of significant differences between CTRL and each mutant per MEA dish with 3 independent experiments. As for the extended cultures to detect more frequent signals in CTRL neurons, we have already tried longer cultures three times. However, we could not perform sufficient analyses because neurons became unhealthier after 35 dpd. We will further try to improve the experimental setup and perform analyses if the experimental conditions could be optimized.

    • Single cell RNAseq data suggests a cluster of GABAergic cell types that are appearing in the 1q del condition, but not in the 1q dup or control groups. The authors suggest that these GABAergic cells are excitatory because the chloride gradient has not yet been altered (no change to KCC2 expression). The authors should substantiate this idea in the MEA system with bicuculline treatment to block GABAergic transmission (drug washed in and out) to show that the spike activity observed in the 2D MEA experiments is due to GABAergic excitatory transmission. Ideally, this should be done for both the 1q dup, 1q del as well as controls.

    We thank the reviewer for the suggestion. We agreed with the reviewer that drug treatment with bicuculine in this MEA system was meaningful to identify cellular properties. We will try to set up the experimental conditions and perform this experiment if the condition can be optimized.

    • Fig 5A. The clustering method for single cell RNAseq seems shows a large proportion of "other" class cells begging the question as to what they are. Is there another cluster analysis, which might be used eg partially supervised/unsupervised clustering methods from the Allen Institute to help determine what these might be?

    We initially made the screening chart for cell-type specifications according to cellular markers from Allen brain map (http://celltypes.brain-map.org/rnaseq/human_ctx_smart- seq) and a published paper (CA Trujillo et al., Cell Stem Cell 2019). We defined this cluster as “other” because this cluster did not have any significant genes in the 1st screening, although we understood that the specifications of all clusters were desirable. To investigate the cellular property in this cluster, we tried to put significant genes into Metascape to check gene ontology. We found some terms about immune cells (mainly lymphocytes and macrophages), cancer cells, roles for inflammation, and apoptotic process, although miscellaneous terms were also included. We have provided the screening chart as supplementary Table 4 in this revised manuscript. Next time, we will add a more detailed description of the ‘other’ cluster in the revised manuscript.

    • Fig 5 B. The manuscript requires additional markers used in the cluster analysis. Particularly, expression of the GABAergic progenitor markers DLX5 and 6 as well as EMX1 for the progenitor cells. Details of all markers and cluster algorithms should be made available in supplementary tables and R scripts, so that others can repeat this analysis.

    In response to the reviewer’s suggestion, we will check these GABAergic progenitor markers and add them to the revised figure and manuscript later. As we mentioned above, we performed the cell type specification of each cluster manually using our screening chart and did not use R scripts. We have provided the information on the screening process in supplementary Table 4 of this revised manuscript.

    • Fig 6. Expanding the heat map of 1q del and 1q dup with CTRL expression would help with context for baseline levels in this isogenic cell line. Please also include additional GABAergic markers GABRA1, GABARB2and GABARG2, (subunits of the most common GABA-A receptor) SOM, VIP, NPY, (other GABAergic interneurons in addition to PVALB) DLX6, EXM1 and for excitatory markers GRIA2, GRIA3 and GRIA4 (all of which have developmentally regulated expression patterns) that will provide more context with the synaptic receptor literature. GRIN2D is expressed only in GABAergic cell types and so I would suggest including this NMDA receptor subunit as well.

    We thank the reviewer for the valuable suggestions. To further explore the cellular properties in 1q del and 1q dup, we will check these cell markers additionally and show the results in the revised figure and manuscript next time.

    Minor comments:

    1. Additional references (eg. Schafer et al. 2019) should be discussed in relation to the authors' suggestions of altered neuronal maturity.

    As the reviewer suggested, we will include the paper in our references and discuss the associations between neurodevelopmental disorders and altered neuronal maturity.

    1. The authors show no change in PAX6 expression between genotypes, but significant differences in TBR2 expression between genotypes (Fig. 2C) - this alteration in normal cortical development should be included in results and discussed.

    Radial glial cells (RGs) have abilities of both self-renewal and neurogenesis (Lui et al. Cell 2011, Fiddes, I. T. et al., Cell 2018). Fiddes et al. showed that if the balance leans toward neurogenesis, premature differentiation with higher TBR2 expressions was observed in week 4 human cortical organoids (Fiddes, I. T. et al., Cell 2018). However, the predisposition to neurogenesis is thought to cause the earlier shortage of RGs. Finally, these cells remain abundant in week 4 organoids. We considered this was why TBR2 expression was significantly different in 1q del, but PAX6 was not. We will add this interpretation in the revised manuscript next time.

    1. In the introduction (Line 67): The author's state that "alterations in brain size is common in patients with ASD" using one meta-study to support this claim. Further primary studies should be consulted and the authors should give the proportion of the population with ASD and altered brain size to support this statement. In addition, the age range should be supported with primary papers.

    As the reviewer suggested, we have cited some primary studies about the prevalence of altered brain size in ASD patients and its age range in this revised manuscript. Since it seems still controversial whether the enlargement of brain size persists or not until adolescence and adulthood (E H Aylward et al., Neurology 2002; J Piven et al., Am J Psychiatry 1995), we have also modified the description in this manuscript.

    1. Line 73. The authors suggest that the brain growth deviations are "Postnatal stage restrictive". Citations are needed to support this statement.

    As the reviewer suggested, we have cited some primary studies as described above and revised the manuscript.

    1. In the scRNAseq data results please report total cell numbers counted for each cluster and for genotype group.

    We apologize for the lack of information and thank the reviewer for noticing it. We have added the information in the results section of the revised manuscript this time.

    1. In the results section (line 269-270) the authors suggest that 1q del cells are in a more mature state because the GABAergic cells are present and glutamatergic genes are similarly altered in 1q dup and 1q del. However, the results from the gene cluster data suggests that there is a very high proportion of progenitor cells (Progenitor 1 and 2 clusters), which seems to argue against faster maturation. This suggests to me that cell fate is being modified here.

    We thank the reviewer for the valuable suggestion. Schafer et al. (the suggested paper in minor comment 1) reported that altered gene expressions in neuronal modules have already been observed in NSCs derived from ASD patient-derived iPSCs. As the reviewer suggested, we plan to consider our results in terms of the alteration of cell fate and neuronal maturity in the revised manuscript later.

    1. Label figures on each page for ms.

    As the reviewer suggested, we have labeled figures at the bottom right of each page.

    1. Fix typos and heat map legends (currently no colors for log2 fold change in Fig 5 or 6)

    We apologize to the reviewer for typos and grammatical errors. We made an effort to remove them. We also apologize for the lack of color information in the legends of Figure 5 and Figure 6 and thank the reviewer for noticing it. We have added the color information in the figure legends of the revised manuscript this time.

    Significance

    Overall the study is clearly described, and the outcomes have been substantiated to a certain degree, but requires a bit more work. This paper does represent a technical 'tour de force' and the authors should be applauded for sticking it out where other labs have so far failed. It might be useful to mention even in brief, of the number of 'failed' (failed or inaccurate) events. The availability of the lines should also be clearly stated.

    We thank the reviewer for the positive comments. In addition to the plans described above, we have added more detailed information, e.g., how many screenings were carried out to get positive clones, in the revised version of the methods and results section. We have also added the descriptions about the availability of the 1q21.1 CNV cell lines in the data availability section of this revised manuscript.

    Reviewer #3

    In this research study by Nomura et al., the authors develop novel hESC-based models of reciprocal CNVs in distal 1q21.1 using CRISPR/Cas9 genome editing technology. Specifically, the authors genome edit KhES-1 cells to produce two isogenic hESC line that contain either a deletion or duplication of this chromosomal region. Patients with 1q21.1 deletion and 1q21.1 duplication syndromes show abnormal head size in conjunction with multiple neurodevelopmental co-morbidities such as epilepsy, developmental delay, and neuropsychiatric abnormalities. This is an important study since it provides robust research tools to understand molecular and cellular mechanisms that may underly these syndromes. Through generation of cortical organoid models, the authors demonstrate 1q21.1 deletion and duplication organoids show deficits in growth and over-growth, respectively. Additionally, the authors provide data that 1q21.1 deletion and duplication organoids show altered signaling cascades which may underly growth deficits and also abnormal neurodevelopment which may underly hyperexcitable neurons as demonstrated by multi-electrode array analysis. While my enthusiasm for this study remain high, I do have a significant number of major and minor reservations specific to the experimental design and analysis that if addressed would provide for an excellent contribution to the field.

    Major concerns:

    1. Though the authors provide extensive data in this study, major revisions are necessary to interpret all of their data in the context of the phenotypes they are observing in organoids and MEA analyses. In addition, the current study lacks cohesiveness throughout the various experiments and does not provide text that clearly unifies the results of the study. For example, no interpretation of higher TBR2 levels in 1q21.1 deletion is provided. Does this mean these organoids show accelerated neuronal differentiation? Also please see my comment regarding TBR2 staining the next section.

    Other examples throughout the manuscript in which there is no clear interpretation of the data or inadequacies of unifying the results of the experiments.

    We thank the reviewer for pointing out that our manuscript had inadequacies of the integrity and cohesiveness throughout our data. With additional data as follows, we plan to improve these issues in the revised manuscript later. As for TBR2 expression, we considered that higher TBR2 expressions in week 4 human cortical organoids showed the predisposition to neurogenesis in 1q del as demonstrated in a previous paper (Fiddes, I. T. et al., Cell 2018). We will add the description in the revised manuscript later.

    • a. Additional interpretation why 1q21.1 duplication organoids show increased growth is lacking. The single cell RNA sequencing results show there are more glia, but no further interpretation is giving why these organoids show an overgrowth phenotype. Inversely, the 1q21.1 deletion organoids show more progenitor cells, but it is not apparent why this should result in decreased cell growth.

    As we have mentioned above, we considered that the predominance of 1q dup cells in the glial cluster reflected the excessive gliogenesis from radial glial cells and enhanced cell divisions in relation to the alteration of the RAS/MAPK pathway (Z Shen, BioRxiv 2020). We plan to analyze additional markers related to cell proliferation and cell division by immunostaining to validate the above hypotheses. To investigate how 1q del organoids showed smaller size, we plan to examine apoptotic markers such as cytochrome C and caspase 3 by culturing NPC organoids again.

    • b. The authors suggest that 1q21.1 duplication organoids are resistant to neuronal differentiation. What data supports this hypothesis other than the fact there are no mature neuronal cells are present in their single cell RNA sequencing data.

    We considered that the results in Figure 3B and Figure 3D also supported this hypothesis that 1q dup organoids expressed the lower intensity of neuronal markers. Since we have only checked a few markers by immunocytochemistry (ICC), we plan to examine additional markers, i.e., immature neuronal markers such as DCX and other mature neuronal markers such as NeuN, as well as proliferation markers such as phospho histone H3 to ensure this hypothesis.

    • c. The MEA analyses show hyperexcitability in both 1q21.1 deletion and duplication cultures. Since the authors suggest 1q21.1 duplication organoids are resistant to neuronal maturation, no interpretation is given why they show hyperexcitable phenotypes.

    In the MEA analyses, we used not 3-D cortical organoids but 2-D neurons because the required culture period to emit electrical activities was thought to be much shorter in 2-D neurons according to some previous studies with human pluripotent cells (A Taga et al., Stem Cells Transl Med 2019; CA Trujillo et al., Cell Stem Cell 2019). We considered that 2-D neurons on 28 dpd (day 63) had much higher maturity than NPC organoids and even 1q dup neurons had already become mature enough to emit spike activities. We will also check neuronal marker expressions using 2-D neurons around 28 dpd by RT-qPCR to ensure this.

    • d. The current study is lacking extensive immunohistochemical stains of representative markers that validate their findings from their single cell RNA sequencing experiments. For example, glial cell markers such as GFAP should be analyzed in 1q21.1 duplication organoids. Additionally, progenitor cell markers such as PAX6 and neuronal markers such as MAP2 and synaptic markers such as SYNAPSIN and others should be incorporated in the study.

    We thank the reviewer for the suggestions. We plan to perform additional IHC staining for NPC organoids with the suggested markers and OPC markers.

    1. Major details are lacking for the single cell RNA sequencing experiments.
    • a. How many cells were analyzed from each group? How many organoids and what age of organoids were analyzed from each group, were they pooled together? Why was a log2FC 1.2 used as a threshold? It is unclear how the authors identify Progenitor 1 and 2 cell clusters? Are they distinct clusters or is this a continuum of differentiation. The progenitor 1 and 2 clusters were chosen based on expression of the ID transcription factors, but no text was provided why these genes specify progenitor cells.

    We apologize for the lack of information and thank the reviewer for noticing it. We described the number of analyzed cells (32,171 cells: 1q del; 10,682, 1q dup; 11,987, CTRL; 9,502) in the results section (line 186) of the original manuscript. However, we could not count how many organoids were analyzed because they were too tiny (diameter; 400-700µm). Many organoids were needed to get the prescribed number of cells (25,000 cells per genotype). According to the analyzed data of size measurement for NPC organoids by fluorescent microscopy, at least 1,500 organoids were collected per genotype. We gathered all cultured organoids in the same batch, dissociated them, and then loaded the prescribed number of cells into the machine. We have added the description of the number of input cells in the methods section of this revised manuscript.

    We used the threshold of log2FC > |1.2| so that the total number of DEGs became around 100-1000 in both bulk and the NSC cluster to avoid a very high or low number of DEGs. Some previous transcriptome studies used the same or even smaller thresholds (Xiaoming Ma et al., Front in Genet 2020; J Zhong et al., Brain Res 2016; Y Wang et al., BMC genomics 2016). We have added these descriptions in the methods section of this revised manuscript.

    As for progenitor-1 and 2, we regarded them as a continuum based on the marker expressions. We chose ID transcription factors for progenitor cells, referring to a published paper (CA Trujillo et al., Cell Stem Cell 2019) as we have described in the methods section (line 633). Several articles have reported that ID transcription factors regulate proliferation and differentiation of neural precursor cells (K Yun et al., Development 2004; D Patel et al., Biochim Biophys Acta 2015).

    Minor concerns:

    1. I would suggest rephrasing the title of the study as it does not clearly convey the advancement to the field. I would suggest the following or something similar this is more concise: " Modeling Reciprocal CNVs of Chromosomal 1q21.1 in Cortical Organoids Reveals Alterations in Neurodevelopment."

    We thank the reviewer for the concrete suggestion. We have revised the title as the reviewer suggested in this preliminary revised manuscript.

    1. The length of the discussion is over extended and should be revised to become more concise.

    We thank the reviewer for pointing it out. We will shorten the beginning part and delete unnecessary sentences in the discussion section of the revised manuscript later.

    1. Additional experiments should be performed to characterize pluripotency of hESC clones generated after genome editing other than staining for alkaline phosphatase activity.

    At minimum, karyotyping in addition to measuring pluripotency markers such as NANOG and OCT3/4 should be performed.

    Karyotyping of wild-type ES cells has been checked by Institute for Frontier Medical Sciences, Kyoto University before being provided. After genome editing, we performed aCGH analysis for all 3 genotypes using the wildtype ES cells as reference genes and confirmed no chromosome aberrations were generated. We have added the information about karyotyping in the methods section of this preliminary revised manuscript.

    As for pluripotency markers, we performed RT-qPCR analyses with ES cells after genome editing and confirmed that OCT3/4 was highly expressed than internal control genes. (We can provide the raw data if requested).

    1. There are several dozen instances of spelling/grammatical and word choice errors throughout the manuscript. For example, line 24 reads "We generate isogenic..." should read "We generated isogenic... "
    • a. Line 25: "opposite organoid size" as written is confusing to interpret.
    • b. Line 46: "have been considered in the context of ASD" would read more clearly as "have been thought to underly ASD etiology."
    • c. Line 53: "in the study of neurological development" should read "nervous system development".
    • d. Line 118: ".. to detect the CRISPR target site for deletion" should read "to detect the CRISPR target site. For the deletion, we checked... "
    • e. <![endif]>Line 119: "...flanking the CRISPR target site; for duplication, we amplified.. " should read "flanking the CRISPR target site, and for the duplication, we amplified..... ".
    • f. Line 127: "we prepared control cells (CTRL) that transfected.... should read ""we prepared control cells (CTRL) that were transfected. ".
    • g. Line 185: "organoid size and mature level" should read "organoid size and developmental maturity."
    • h. In line 40, "We made cryosections of .... should read.... "We performed IHC for the three organoid genotypes on day 27... " i. <![endif]>In Supplementary Figure 8, line 554, "replictes" is misspelled.

    We apologize to the reviewer for many typos and grammatical errors and thank the reviewer for pointing them out in detail. We have corrected these errors as the reviewer suggested.

    1. Line 181: "with a little higher degree of.. " should be re-written more precisely and with more scientific accuracy.

    As the reviewer requested, we have corrected the sentence in this revised manuscript.

    1. Line 216, The use of the colloquial phrase: "On the other hand.. " should be replaced with more formal language. For example, "In contrast, the number of downregulated....

    We thank the reviewer for pointing it out. We have corrected this colloquial phrase at 4 locations.

    1. In line 201, Pprogenitor is misspelled.

    We apologize and thank the reviewer for noticing it. We have corrected it in this preliminary revised manuscript.

    1. In Figure 3, images showing TBR2 staining does not appear correct as this protein should be localized to the nucleus similar to SOX2 staining. I would suggest optimizing conditions such as utilizing antigen retrieval or other methods to reduce non-specific cytoplasmic staining.

    We thank the reviewer for the valuable suggestion. We plan to optimize the condition and try other neuronal lineages markers such as DCX and NeuN.

    1. I would suggest simplifying the text describing the primers utilized in this study and display them in a table format.

    As the reviewer requested, we will make a supplementary table of primer sequences in the revised manuscript later.

    1. Information regarding the number of technical replicates used in this study is lacking throughout the manuscript. For example, how many hESC clones were analyzed? How many organoids were analyzed for each specific assay such as single cell RNA sequencing and MEA analyses? How many independent experiments were used for these studies?

    We apologize for the lack of information. We have constructed one clone per genotype one human ES cell strain (khES-1) and performed all further analyses. The precise number of NPC organoids in scRNA-seq could not be counted, as we mentioned above. As for MEA analysis, 8 x 10^5 cells were seeded on each dish as described in the original manuscript. However, it was unclear how many neurons were observed on each electrode because multiple cells and neurites covered each electrode. Thus, spike activities were detected as the network of many neurons. We have added the information in the methods section of this preliminary revised manuscript.

    1. It is not clear why the authors choose two types of organoid methods in the study. The first protocol referred to as the "NPC organoid method" is synonymous to neurosphere culturing and should be referred to as neurospheres throughout the manuscript.

    One protocol (Fujimori et al., Stem Cell Rep., 2017) was not for 3-D organoids but 2-D neurons (Figure 4A). Thus, we considered neurosphere and NPC organoid were different.

    1. In Figure 4, panel C should be referred to as a local field potential trace and not a waveform.

    We thank the reviewer for pointing it out. We have corrected the description as the reviewer suggested.

    Reviewer #3

    This is an important study since it provides robust research tools to understand molecular and cellular mechanisms that may underlie 1q21.1 deletion and duplication syndromes.

    We thank the reviewer for the positive comments. We plan to perform additional analyses and experiments as described above and try to meet the reviewer’s requests.

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    Referee #3

    Evidence, reproducibility and clarity

    In this research study by Nomura et al., the authors develop novel hESC-based models of reciprocal CNVs in distal 1q21.1 using CRISPR/Cas9 genome editing technology. Specifically, the authors genome edit KhES-1 cells to produce two isogenic hESC line that contain either a deletion or duplication of this chromosomal region. Patients with 1q21.1 deletion and 1q21.1 duplication syndromes show abnormal head size in conjunction with multiple neurodevelopmental co-morbidities such as epilepsy, developmental delay, and neuropsychiatric abnormalities. This is an important study since it provides robust research tools to understand molecular and cellular mechanisms that may underly these syndromes. Through generation of cortical organoid models, the authors demonstrate 1q21.1 deletion and duplication organoids show deficits in growth and over-growth, respectively. Additionally, the authors provide data that 1q21.1 deletion and duplication organoids show altered signaling cascades which may underly growth deficits and also abnormal neurodevelopment which may underly hyperexcitable neurons as demonstrated by multi-electrode array analysis. While my enthusiasm for this study remain high, I do have a significant number of major and minor reservations specific to the experimental design and analysis that if addressed would provide for an excellent contribution to the field.

    Major concerns:

    1. Though the authors provide extensive data in this study, major revisions are necessary to interpret all of their data in the context of the phenotypes they are observing in organoids and MEA analyses. In addition, the current study lacks cohesiveness throughout the various experiments and does not provide text that clearly unifies the results of the study. For example, no interpretation of higher TBR2 levels in 1q21.1 deletion is provided. Does this mean these organoids show accelerated neuronal differentiation? Also please see my comment regarding TBR2 staining the next section. Other examples throughout the manuscript in which there is no clear interpretation of the data or inadequacies of unifying the results of the experiments.
      • a. Additional interpretation why 1q21.1 duplication organoids show increased growth is lacking. The single cell RNA sequencing results show there are more glia, but no further interpretation is giving why these organoids show an overgrowth phenotype. Inversely, the 1q21.1 deletion organoids show more progenitor cells, but it is not apparent why this should result in decreased cell growth.
      • b. The authors suggest that 1q21.1 duplication organoids are resistant to neuronal differentiation. What data supports this hypothesis other than the fact there are no mature neuronal cells are present in their single cell RNA sequencing data.
      • c. The MEA analyses show hyperexcitability in both 1q21.1 deletion and duplication cultures. Since the authors suggest 1q21.1 duplication organoids are resistant to neuronal maturation, no interpretation is given why they show hyperexcitable phenotypes.
      • d. The current study is lacking extensive immunohistochemical stains of representative markers that validate their findings from their single cell RNA sequencing experiments. For example, glial cell markers such as GFAP should be analyzed in 1q21.1 duplication organoids. Additionally, progenitor cell markers such as PAX6 and neuronal markers such as MAP2 and synaptic markers such as SYNAPSIN and others should be incorporated in the study.
    2. Major details are lacking for the single cell RNA sequencing experiments.
      • a. How many cells were analyzed from each group? How many organoids and what age of organoids were analyzed from each group, were they pooled together? Why was a log2FC >1.2 used as a threshold? It is unclear how the authors identify Progenitor 1 and 2 cell clusters? Are they distinct clusters or is this a continuum of differentiation. The progenitor 1 and 2 clusters were chosen based on expression of the ID transcription factors, but no text was provided why these genes specify progenitor cells.

    Minor concerns:

    1. I would suggest rephrasing the title of the study as it does not clearly convey the advancement to the field. I would suggest the following or something similar this is more concise: " Modeling Reciprocal CNVs of Chromosomal 1q21.1 in Cortical Organoids Reveals Alterations in Neurodevelopment."
    2. The length of the discussion is over extended and should be revised to become more concise.
    3. Additional experiments should be performed to characterize pluripotency of hESC clones generated after genome editing other than staining for alkaline phosphatase activity. At minimum, karyotyping in addition to measuring pluripotency markers such as NANOG and OCT3/4 should be performed.
    4. There are several dozen instances of spelling/grammatical and word choice errors throughout the manuscript. For example, line 24 reads "We generate isogenic...." should read "We generated isogenic...."
      • a. Line 25: "opposite organoid size" as written is confusing to interpret.
      • b. Line 46: "have been considered in the context of ASD" would read more clearly as "have been thought to underly ASD etiology."
      • c. Line 53: "in the study of neurological development" should read "nervous system development".
      • d. Line 118: "...to detect the CRISPR target site for deletion" should read "to detect the CRISPR target site. For the deletion, we checked....".
      • e. Line 119: "...flanking the CRISPR target site; for duplication, we amplified..." should read "flanking the CRISPR target site, and for the duplication, we amplified......".
      • f. Line 127: "we prepared control cells (CTRL) that transfected.... should read ""we prepared control cells (CTRL) that were transfected...."
      • g. Line 185: "organoid size and mature level" should read "organoid size and developmental maturity."
      • h. In line 40, "We made cryosections of .... should read.... "We performed IHC for the three organoid genotypes on day 27...."
      • i. In Supplementary Figure 8, line 554, "replictes" is misspelled.
    5. Line 181: "with a little higher degree of..." should be re-written more precisely and with more scientific accuracy.
    6. Line 216, The use of the colloquial phrase: "On the other hand..." should be replaced with more formal language. For example, "In contrast, the number of downregulated....
    7. In line 201, Pprogenitor is misspelled.
    8. In Figure 3, images showing TBR2 staining does not appear correct as this protein should be localized to the nucleus similar to SOX2 staining. I would suggest optimizing conditions such as utilizing antigen retrieval or other methods to reduce non-specific cytoplasmic staining.
    9. I would suggest simplifying the text describing the primers utilized in this study and display them in a table format.
    10. Information regarding the number of technical replicates used in this study is lacking throughout the manuscript. For example, how many hESC clones were analyzed? How many organoids were analyzed for each specific assay such as single cell RNA sequencing and MEA analyses? How many independent experiments were used for these studies?
    11. It is not clear why the authors choose two types of organoid methods in the study. The first protocol referred to as the "NPC organoid method" is synonymous to neurosphere culturing and should be referred to as neurospheres throughout the manuscript.
    12. In Figure 4, panel C should be referred to as a local field potential trace and not a waveform.

    Significance

    This is an important study since it provides robust research tools to understand molecular and cellular mechanisms that may underlie 1q21.1 deletion and duplication syndromes.

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    Referee #2

    Evidence, reproducibility and clarity

    This study was initiated to look at specific cellular and molecular mechanism of the duplication and deletion CNV frequently observed at the 1q21.1 gene locus in an isogeneic human embryonic stem (hES) cell model. The authors note that these CNVs are associated with higher than normal penetrance of ASD and epilepsy and aim to elucidate gene expression differences with single cell RNAseq and functional changes in this model system. The authors further sought to proliferation and differentiation states, in addition to neuronal activity, using both 2D cultures and 3D organoid models. The 1q21.1 gene locus model system made here is unique and the results broadly recapitulate the patient phenotype particularly with observations of macrocephaly in the "1q dup" and microcephaly in the "1q del".

    Reviewers statement: We have joint expertise in GABAergic neuronal development, iPSC 2D and 3D culture and ASD human molecular genetics.

    Major comments:

    • Not sure why ASD (if used it should also be spelled out) is mentioned in the title if ASD is only seen in a proportion of human 1q21.1. duplication (~36% will have autism) and 1q21.1 deletion (<10% will have autism) carriers. I would prefer to use 'neurodevelopmental phenotype'. A good update review that is accurate with respect to this CNV role in autism is PMID: 29398931. The authors should also put into the context of their results what is known with other neuropsychiatric phenotypes also seen in these CNV events;
    • In Fig 1D the ddPCR validation for the genetic alterations in 1q del shows a normal return to 2 copies of GPR89B. However, in the 1q dup the CNV level is still elevated for GPR89B. Please determine how much further the duplication goes as there are five more potentially affected genes in this region (eg PDZK1P1). Modify the text appropriately to note the potential influence of any of these other genes on the experimental outcomes.
    • The authors' claim that dosage dependent size differences in NPC organoids is caused by a change in the number of cells within the organoid rather than size - from Fig. 2D, cells in 1qdel organoid appears more compact; a quantification of cell number should be done to support this claim. IHC of D27/28 organoids with GABAergic markers would support authors' claim of alterations of GABAergic components in 1qdel cells. These suggested experiments would take 2-3 days if the organoids are available.
    • Fig 4 E shows MEA data from "top 10". What is the top ten? Do you mean data points? There are batch differences in 1q dup with one batch having a lower expression than the other. Increasing the n value to accommodate the high variance observed in this group will greatly increase the validity of the data generated. Also, change the figure legend to indicate the age of these cultures. Given that the controls are not spiking, this data should be extended to probe the developmental profile further to week 9 when normal cells should be spiking so that the baseline activity of this isogenic line can be determined.
    • Single cell RNAseq data suggests a cluster of GABAergic cell types that are appearing in the 1q del condition, but not in the 1q dup or control groups. The authors suggest that these GABAergic cells are excitatory because the chloride gradient has not yet been altered (no change to KCC2 expression). The authors should substantiate this idea in the MEA system with bicuculline treatment to block GABAergic transmission (drug washed in and out) to show that the spike activity observed in the 2D MEA experiments is due to GABAergic excitatory transmission. Ideally, this should be done for both the 1q dup, 1q del as well as controls.
    • Fig 5A. The clustering method for single cell RNAseq seems shows a large proportion of "other" class cells begging the question as to what they are. Is there another cluster analysis, which might be used eg partially supervised/unsupervised clustering methods from the Allen Institute to help determine what these might be?
    • Fig 5 B. The manuscript requires additional markers used in the cluster analysis. Particularly, expression of the GABAergic progenitor markers DLX5 and 6 as well as EMX1 for the progenitor cells. Details of all markers and cluster algorithms should be made available in supplementary tables and R scripts, so that others can repeat this analysis.
    • Fig 6. Expanding the heat map of 1q del and 1q dup with CTRL expression would help with context for baseline levels in this isogenic cell line. Please also include additional GABAergic markers GABRA1, GABARB2and GABARG2, (subunits of the most common GABA-A receptor) SOM, VIP, NPY, (other GABAergic interneurons in addition to PVALB) DLX6, EXM1 and for excitatory markers GRIA2, GRIA3 and GRIA4 (all of which have developmentally regulated expression patterns) that will provide more context with the synaptic receptor literature. GRIN2D is expressed only in GABAergic cell types and so I would suggest including this NMDA receptor subunit as well.

    Minor comments:

    1. Additional references (eg. Schaefer et al. 2019) should be discussed in relation to the authors' suggestions of altered neuronal maturity.
    2. The authors show no change in PAX6 expression between genotypes, but significant differences in TBR2 expression between genotypes (Fig. 2C) - this alteration in normal cortical development should be included in results and discussed.
    3. In the introduction (Line 67): The author's state that "alterations in brain size is common in patients with ASD" using one meta-study to support this claim. Further primary studies should be consulted and the authors should give the proportion of the population with ASD and altered brain size to support this statement. In addition, the age range should be supported with primary papers.
    4. Line 73. The authors suggest that the brain growth deviations are "Postnatal stage restrictive". Citations are needed to support this statement.
    5. In the scRNAseq data results please report total cell numbers counted for each cluster and for genotype group.
    6. In the results section (line 269-270) the authors suggest that 1q del cells are in a more mature state because the GABAergic cells are present and glutamatergic genes are similarly altered in 1q dup and 1q del. However, the results from the gene cluster data suggests that there is a very high proportion of progenitor cells (Progenitor 1 and 2 clusters), which seems to argue against faster maturation. This suggests to me that cell fate is being modified here.
    7. Label figures on each page for ms.
    8. Fix typos and heat map legends (currently no colors for log2 fold change in Fig 5 or 6)

    Significance

    Overall the study is clearly described, and the outcomes have been substantiated to a certain degree, but requires a bit more work. This paper does represent a technical 'tour de force' and the authors should be applauded for sticking it out where other labs have so far failed. It might be useful to mention even in brief, of the number of 'failed' (failed or inaccurate) events. The availability of the lines should also be clearly stated.

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    Referee #1

    Evidence, reproducibility and clarity

    Summary

    Copy number variations in the 1q21.1 loci, deletions and duplications, have been associated with neurodevelopmental disease. In particular, deletions of this locus result in a variety of neuronal phenotypes including microcephaly and schizophrenia in varying levels of severity. Duplications of the 1q21.1 locus are often associated with autism and/or macrocephaly.

    In this study Nomura et al. generated 1q21.1 deletion and duplication hESC lines to study the impact of these CNVs on neuronal development. They generated brain organoids and observed a bidirectional effect of this CNV on organoid size, with 1q21.1 deletion showing smaller brain organoids whereas, the 1q21.1 dup lines grew large than controls. This in line with observed micro and macrocephaly observed in patients. They further analyzed these organoids at the gene expression level using single cell RNAseq and performed some electrophysiological assessment on neurons from of dissociated organoids.

    This study is certainly of interest given the association of this loci with NDDs such as autism, epilepsy and schizophrenia. At this stage, the study is mainly a descriptive study, showing differences between the 1q21.1 del/dup versus controls but also between both the del/dup lines. There is no mechanistic insight provided. For example the 1q21.1 CNV encompasses several genes, of which some have already been linked to micro/macrocephaly (eg. NOTH2NL). More importantly, most of the conclusions drawn by the authors are based on a limited set of experiments/analysis which are not always carefully performed and/or presented. In general, the data presented are premature, therefore not supporting the claims/conclusion made by the author (eg title) This makes the overall impact of this study limited.

    Main comments

    In general, the interpretation of the data is too premature:

    1. The title is not supported in any means by data
    2. Brain organoids size and development: In figure 2 the authors analyzed the development of the organoids. Based on the human phenotype the deletion would lead to smaller brain and the duplication to larger brain organoids. The presented data to support these claims are rather scarce. They indeed provide data on organoid size, however there is no information as to regard how this micro/macrocpehaly comes about. Only limited amount of cell types are being investigated with immunocytochemistry, which give little insight into the mechanism. Fig 3. The authors performed some very basic immunostaining and concluded that the neuronal maturity of 1q del seemed to be accelerated, whereas 1q dup decelerated from the NPC stage. However, there is no direct evidence provided for this. With simple additional immunostainings authors could already get a much better idea of what is going on. For example the authors could measure the amount of differentiating versus proliferating cells, cell cycle exit, etc (eg BrDU, KI67, pHH3 staining,...) Further there are some technical aspect that would need to be resolved:
      • There is a general lack of brain organoid characterization of the controls. It is unclear on how many independent clones these experiments were performed.
      • Fig 2C: it is unclear why brain organoid sizes reduce over time. Is this an indication of increased apoptosis? Did the authors measure this?
      • What is the reason for using t-test with Bonferroni correction as opposed to one -way (or even two-way) Anova is unclear in Fig 2C
      • 2E is unclear how they came to the conclusion that dosage dependent size difference in NPC organoids was caused by the number of cells within an organoid, not by the size of each cell or different cell types. Since they only measured the amount of Sox 2 positive cells and used Sox2 to measure cell diameter, whereas Sox2 is mainly expressed in the nucleus.
      • How do the authors explain that the Dup cells do not express Tubb neither CTIP2, do they only express NPCs and no neurons?

    In short, the characterization of the brain organoids at the level of general development, cell types, proliferation, differentiation is underdeveloped.

    1. Electrophysiological assessment of brain organoids derived neurons: In figure 4 the authors claim that both CNVs (Del/Dup) show hyperexcitability and altered expressions of glutamate system as common features between the Del/Dup lines. The data to support this are however scarce and far from being convincing: The poor quality of the data is represented by images in 4B-E:
      • First the authors chooe to dissociate the organoids prior to measure the cells on MEA's. This takes away the advantage of 3D brain organoids, will add a lot of non-physiological stress, cause cell death and lead to unequal distribution of cells over the electrodes, see fig 4B.
      • MEA recording are meant to measure network activity and heavily (read: fully) dependent on the network being formed. Cherry picking electrodes for analysis is not justified, analysis should be performed per MEA chip not per electrode. Inclusion/exclusion parameters should be defined before analysis
      • MEA parameters such as Mean firing rate (spike/min) and burst rate are very sensitive to plating conditions, especially number of cells and clustering of cell around electrodes (see 4B). Given that the organoids already differ in size and according to the authors in cell number, but also in the amount of starting NPCs, one can expect very different cell densities/cell types per experiment/genotype. The authors should therefore show for every genotype the matching cell culture images. Also with regard to the claims made about GABAergic neurons the cell type composition at the time of the MEA recording should be characterized for every genotype.
      • Fig 4B illustrates the points made above. The fact that no activity is observed in the control cells can be due to many different reasons: unequal plating, stress after dissociating cells, poor coverage of the electrodes, poor maturation, too early measuring time point, etc.... Because the authors have no control over the amount of cells covering the electrodes the data presented here carry very little carry little information. Fig 4B, best illustrates this with large cell clumps and areas without cell bodies. Measurements from these cell cultures are irrelevant and no conclusion can be drawn. We suggest that the authors first benchmark this technique with their own differentiation protocol, show robust and reliable recordings on control cells, and only compare to the CRISPR lines at a time point at which the control cells show a decent amount of activity > 1Hz. When doing so, also reduced activity can be monitored (For examples see, Trujillo et al, Cell Stem Cell2019 or Frega et al 2019 Nat comm).
      • MEAs measure the output of the network (action potentials). In a network, this can be influenced by virtually every neuronal property (morphology, synaptic input, types of synapses, intrinsic excitability, etc). Therefore, the authors cannot conclude only based on fig 4E that the Del/Dup cells are intrinsically hyperactive. To make this conclusion they should measure this directly by assessing that passive and active intrinsic properties of individual neurons. In control condition many electrodes do not give any signal. From these experiments it is impossible to know whether this is because of lack of cell on the particular electrode or real absence of activity. Certainly one could not conclude that the del en dup cell are intrinsically hyperexcitable.

    It seems that from the introduction the authors try to link 1q21 CNVs to epilepsy and ASd, thereby justifying the observed phenotypes.

    • How do the authors reconcile the fact that more mature GABA system is observed in the Del lines with the so called increased activity compared to controls but not to the Dup lines.

    Single cell RNAseq

    • I'm not a specialist on single cell RNAseq, however it seems that the analysis is underdeveloped and conclusion drawn for these experiments premature. It would be essential to validate some of the generated hypothesis, eg GABA maturity and not merely state as a conclusion (eg title).
    • How do the authors explain that a majority of the cells are Glial cells at day 27, and no presence of neurons.
    • How relevant is the changes in the extremely low amounts of GABAergic neurons in the Del cells, no excitatory neurons are present, only NSCs

    Minor comments

    • It is unclear how many clones were assessed per genotype
    • The authors should properly annotate the genotypes 1q21.1 instead of 1q del (line 134)
    • Introduction seems to be somehow off topic since 1q21.1 locus is associated with several neurodevelopmental disorders, including SCZ, but is certainly not specific to ASD and epilepsy. So the premiss on line 86: to study 1q21.1 locus to understand ASD/epilepsy is somewhat misleading. I propose that the introduction would be focussed on the 1q21.1 and not on general on ASD/epilepsy.
    • It is unclear whether they generated heterozygous or homozygous deletions.
    • The authors should cite Fiddes, I. T. et al. Human-Specific NOTCH2NL Genes Affect Notch Signaling and Cortical Neurogenesis. Cell 173, 1356-1369.e22 (2018).
    • Many unclear statements eg line 138: Next, we analyzed each single-cell in an organoid
    • Discussion on E/I is very speculative, not supported by any evidence

    Significance

    The general topic of this study is high interest given the strong association of the 1q21.1 with disease. The authors developed interesting ESC line to study in parallel del and duplication. Unfortunately the level of of analysis performed on these organoids is not up the current stat of the art, are of low experimental quality, analyses are limited. Therefore no clear conclusion can be drawn except for the size of the organoids, very little mechanism is provided. This therefore remains a purely descriptive study for which the presented data are rather on low quality and limited impact in its current shape.

  5. Version published to 10.1101/2021.09.13.460033 on bioRxiv