Dear authors, as part of a group activity in our lab, we discussed your very interesting manuscript with the goal of reviewing it as well as improving our reviewing skills. The review below reflects thoughts and comments raised during this exercise. We hope these comments are helpful for strengthening the manuscript. Summary: This manuscript identifies the ER-resident MSP-domain protein MOSPD2 as a regulator of late endosome/lysosome (LE/Lys) homeostasis and proposes that MOSPD2 forms a functionally non-redundant complex with the LE/Lys cholesterol transporter STARD3 at ER-LE/Lys membrane contact sites. Loss of MOSPD2 or STARD3 increases LE/Lys number, shifts their distribution toward the cell periphery, causes cholesterol enrichment at LE/Lys, and impairs endolysosomal fusion. Structure-function and rescue experiments indicate that the FFAT-binding MSP domain of MOSPD2, the phospho-FFAT motif of STARD3, and the cholesterol-binding START domain of STARD3 are required for this function. The authors further show that STARD3 interacts preferentially with MOSPD2 over VAP-A/VAP-B and that STARD3 overexpression can overcome MOSPD2 deficiency, supporting a model in which partner affinity contributes to the functional specialization of ER-organelle contact sites. The study addresses an interesting question in membrane contact-site biology and combines genetic perturbation, imaging, biochemical interaction assays, and live-cell approaches. The comments below focus mainly on the interpretation of cholesterol redistribution, quantitative support for several imaging conclusions and the mechanistic connection between the observed LE/Lys phenotypes. Major comments: 1. Figure 2: the authors conclude that MOSPD2 is required for the normal distribution of free cholesterol based on increased filipin or D4-probe fluorescence within LE/Lys. However, these measurements alone do not distinguish redistribution of an unchanged cellular cholesterol pool from an overall increase in cellular cholesterol caused, for example, by altered uptake, synthesis, or degradation/esterification. Total cellular cholesterol should therefore be quantified biochemically or by lipidomics. 2. Figure 5&6: The authors see several correlated phenotypes after loss of MOSPD2/STARD3—cholesterol enrichment, impaired fusion, increased LE/Lys number, and more peripheral positioning—but the causal relationships between these phenotypes remain unclear. In particular, it is not established whether cholesterol accumulation causes the fusion defect and expansion of the LE/Lys compartment, or whether altered LE/Lys dynamics secondarily cause cholesterol accumulation. A cholesterol-manipulation experiment would help address causality. For example, reducing lysosomal cholesterol accumulation in MOSPD2/STARD3-deficient cells and testing whether fusion and LE/Lys number are rescued would directly connect the lipid phenotype to organelle dynamics. Conversely, an established perturbation that induces lysosomal cholesterol accumulation could be tested for phenocopy of the fusion defect. 3. Figure 1: The conclusion that MOSPD2 is enriched at discrete foci associated with LE/Lys appears to rely largely on representative images and line scans from only a few cells. The apparent overlap in the presented images is modest. This should be quantified across biological replicates and a substantially larger number of cells, using an appropriate contact-site or colocalization metric. 4. Figure 6: Given that contact sites frequently control fission events, it was unexpected that the LE/Ly phenotype in Fig. 6 (CD) represented a fusion defect rather than a fission defect. LE/Lys fusion as compared to fission. Fig. 6D's dual-color dextran pulse-chase test reveals t0 colocalization values that differ considerably between MOSPD2/STARD3 KO and WT, indicating variations in dextran internalization. Therefore, it would be difficult to attribute the LE/lys phenotype to a fusion defect. 5. Figure 9: In Fig. 9G, GFP-MOSPD2 expression is mostly endosomal, with no ER-like reticular morphology, whereas mClover3-MOSPD2 expression in Fig. 1D exhibits ER-like reticular morphology. Does this result from the coexpression of mCherry-STARD3? 6. Figure 10: Given MOSPD2 exhibited a binding affinity to ORP1L comparable to that of STARD3, as shown in supplementary Fig.S4A, so could ORP1L overexpression also override the phenotype caused by MOSPD2 loss. 7. Figure. 10: In Fig. 10F, it is unclear why the authors chose to rescue the MOSPD2 KO phenotype by overexpressing another MSP family member, VAPA. It would be more interesting and compelling to delete VAPA in the MOSPD2 KO background and co-express STARD3 to check if another MSP family member like VAPA can compensate for the loss of MOSPD2 in mediating STARD3 binding and rescue the LE/Ly phenotype.

Minor comments: 1. Figure 1: The electron microscopy provides potentially valuable ultrastructural information, but the apparent increase in multivesicular/endolysosomal structures is not quantified. Quantification of organelle number, size, and morphology would make better use of these data. 2. Figure 1: LE/Lys positioning analysis: The definition of 0–0.5 of the normalized nucleus-to-cell-edge distance as 'perinuclear' encompasses a large fraction of the cytoplasm. Please justify this threshold and ideally show the full continuous distribution of normalized organelle distances in addition to the binary perinuclear/peripheral classification. 3. Figure S2: Please provide the rationale for selecting MRC5 cells as the second cell type. Statistical comparisons should primarily be made between the siRNA-treated control and target siRNA conditions rather than between target siRNA and non-transfected cells. 4. Figure 2: Cholesterol-probe enrichment within LE/Lys would be more interpretable if normalized to lysosomal area or membrane area, particularly because MOSPD2 loss changes LE/Lys number and potentially morphology. Colocalization/contact between the cholesterol probes and LE/Lys markers should also be quantified. 5. Figure 2: Inclusion of a positive control known to produce lysosomal cholesterol accumulation, such as an NPC-pathway perturbation, would help benchmark the magnitude and appearance of the cholesterol phenotype. 6. Figure 3: Please show that the MOSPD2 deletion and point mutants used for rescue retain the expected subcellular localization, particularly ER localization. 7. Figure 5: The relationship between LAMP1/LAMP2 abundance on Western blot and the imaging-based LE/Lys-number phenotype differs between the two STARD3 KO clones. Quantification of the Western blots and discussion of this clone-to-clone variability would be helpful. 8. Figure 5: A direct rescue of STARD3 KO cells with WT STARD3 for LE/Lys number and positioning would strengthen the initial phenocopy experiments. Although later structure-function experiments provide rescue data for LE/Lys number and cholesterol, the positioning phenotype is not equivalently rescued. 14. Figure 5: The apparent redistribution of the D4 cholesterol probe from the plasma membrane toward intracellular/LysoTracker-positive structures is potentially important and should be quantified directly, for example by comparing plasma-membrane and LE/Lys-associated probe fractions.

1. Figure 6: The dextran pulse–chase assay suggests impaired convergence/fusion of endocytic compartments in MOSPD2- and STARD3-deficient cells. However, a difference between WT and KO cells is already apparent at t = 0, before the chase period. Please clarify the origin of this initial difference and whether differences in dextran uptake, endocytic trafficking, or the pre-existing LE/Lys compartment could contribute to the subsequent differences in colocalization.

Dear authors, as a part of a group activity in our lab we discussed your very interesting manuscript with the goal of reviewing it as well as improving our reviewing skills. The below review is the result of this exercise and reflects thoughts and comments of several people. We hope this helps you with your way forward to publish the paper in a good journal.

Summary: This manuscript uses spatiotemporal proteomics (POTATOMap), live-cell imaging, biochemical perturbation, endogenous knock-in labeling, and organotypic slice culture to characterize the biosynthetic trafficking of Neuroligin 1 and Neuroligin 2 to the axon initial segment (AIS). The authors propose that both paralogs are co-delivered to the AIS via kinesin-1 in a largely non-selective manner, with NLGN2 subsequently retained at axo-axonic inhibitory synapses in an ectodomain-dependent manner, while NLGN1 is cleared by endocytosis. This is a well-designed and technically demanding study addressing an important question in neuronal cell biology. Our comments below focus on aspects of quantification, experimental design, physiological interpretation, and reporting that we believe warrant clarification or additional data before the model can be considered fully established.

Major comments: 1. For most quantifications, plotted data points represent individual neurons pooled across three biological replicates (as indicated in the Methods), and statistical comparisons are performed on this pooled neuron-level data. The appropriate approach is to first calculate the mean value per biological replicate, then plot and statistically compare these replicate means ± SD; individual neurons can still be displayed for transparency using a superplot format. 2. Overexpression and dose-dependency. All RUSH-based trafficking experiments rely on lentiviral or plasmid-based overexpression of tagged NLGN1/NLGN2 constructs. Overexpressed cargo can saturate finite sorting machinery and thereby appear to access non-physiological routes, or conversely mask genuine sorting selectivity. The authors should report expression level relative to endogenous NLGN1/NLGN2. 3. The specificity of the knockdown effect (shKIF1A、shNSG2、shAFTPH、shMAGI3、shAPBB1) on NLGN1 should be tested by examining transport of other cargoes (negative controls). Additionally, rescue experiments using RNAi-resistant constructs of the knocked-down targets would strengthen the specificity of the findings. 4. A negative control (e.g., a cargo known to take a different trafficking route) would help validate the relocalization assay. 5. Please specify which region(s) of the axon and dendrite were used for Polarity Index quantification across all measurements. A specified distance criterion should be reported, as the region selected could influence the apparent magnitude of the effect. 6. Is a dedicated AIS marker used to define the region of interest, rather than relying on whole-neuron staining? Since quantification is restricted to the AIS, please clarify how the authors ensure that the region analyzed accurately corresponds to the AIS. Minor comments: 1. Control Western blots confirming knockdown efficiency at the protein level (in addition to qPCR) would be nice to include. 2. Figure 2C: Please clarify the selection criteria used to choose these six proteins. 3. Figure 2H: The evidence (Fig. 2H and S2D) for “NLGN1 can exit the Golgi in different vesicle subpopulations” is weak. A systematic quantification across a larger vesicle population is needed to assess how common each vesicle population actually is. 4. Figure 3F: If a Soma vs. Dendrite comparison was performed for this knockdown, it would be useful to include the same analysis for other Polarity Index experiments. 5. Figure 3D–F: The effect of KIF1A knockdown on axonal trafficking was not analyzed; an Axon/Soma intensity ratio (analogous to Fig. 2F) could be included, complementing the AIS intensity analysis, which showed no change. 6. Figure 4D: The operational definitions of “vesicles moving into the axon” and “stop & return events” are not provided. It is also unclear how vesicles moving past the AIS are selected for this analysis — based on the data shown, these may correspond to antero-/retrograde traces reaching the edge of the kymograph, but this is not explicitly stated. 7. The evidence for APBB1- and MAGI3-dependent removal of NLGN1 from the AIS is also weak. A direct physical interaction between NLGN1 and APBB1/MAGI3 via the WW-binding domain has not been demonstrated and should be tested experimentally. Is the APBB1/MAGI3-mediated internalization specific to NLGN1? NLGN2 levels should be examined upon APBB1/MAGI3 knockdown to test this specificity. 8. A control experiment is needed to confirm that the NLGN1 truncation mutants are expressed at comparable levels. Increased AIS signal in the truncation mutants could otherwise reflect higher overall expression rather than a genuine trafficking defect. 9. Is there an additive effect when both the WW and PDZ motifs are truncated simultaneously? 10. A validation of the HaloTag (NLGN1) and 3xalfa (NLGN2) knock-in lines is needed. 11. In Figure 6A–D, the higher number of NLGN2 puncta at the AIS could reflect differences in total cellular expression of NLGN1 versus NLGN2 rather than differences in AIS membrane stability. Please clarify whether total protein abundance was quantified and whether AIS puncta density was normalized to overall expression level. 12. In Figure 6E–J, NLGN1/NLGN2 puncta at the AIS and their colocalization with VGAT are quantified, but two aspects of the labeling strategy limit interpretation. First, no cell-type marker is included, even though axo-axonic innervation density depends strongly on postsynaptic neuron identity; co-labeling with CaMKIIα or GAD67 would allow stratification by cell type. Second, VGAT is the only presynaptic marker used, leaving the ~75% of NLGN1 puncta that do not colocalize with VGAT unassigned; adding VGluT1 would clarify whether these correspond to excitatory contacts, particularly given the unquantified NLGN1–Homer1 colocalization noted at the proximal AIS (Fig. S6A). 13. The authors state that imaging was performed in cortical layers 2/3 and 5, but no overview image of the slice or the identified layer boundaries is shown — only cropped AIS images. The rationale for comparing these two layers, and the interpretation of the reported length/puncta correlations, are not explained. 14. Is the antibody specificity for the endogenous immunostaining used in Fig. 7 (commercial anti-NLGN1/anti-NLGN2 antibodies applied to organotypic slices) well validated?