Peer review process
Not revised: This Reviewed Preprint includes the authors’ original preprint (without revision), an eLife assessment, public reviews, and a provisional response from the authors.
Read more about eLife’s peer review process.Editors
- Reviewing EditorChristopher HuangUniversity of Cambridge, Cambridge, United Kingdom
- Senior EditorChristopher HuangUniversity of Cambridge, Cambridge, United Kingdom
Reviewer #1 (Public Review):
Summary:
The authors propose an improved neuro-muscle co-culture system to study ALS-related functional differences in human pluripotent stem cell lines.
Strengths:
A simple co-culture system with functional readout.
Weaknesses:
There are concerns about the lack of novelty, rigor, and clarity in the approach. The strength of the study is undermined by its reliance on transcription factors used more than a decade ago, low myocyte activity, and inadequate validation methods, such as the lack of single-cell transcriptome analysis and detailed neuromuscular synapse characterization. The evidence presented requires substantial validation through rigorous experimental approaches and resolution of the identified concerns for the study's findings to be considered significant and reliable.
Reviewer #2 (Public Review):
The manuscript by Chen et al from the group of Helen Miranda aims to describe an improved neuromuscular junction (NMJ) model to study synaptic dysfunction in several cases of familial ALS. Overall, the system described in the paper appears as a valid platform to study disease phenotypes with exciting results showing specific effects of GDNF on non-SOD1 ALS patient lines. The strength of the paper lies in the use of myotubes, and motor neurons derived from the same donor. However, the current study: (1) lacks a clear comparison of the current system with numerous previously described systems; (2) is limited by the number of repeat experiments in the study and (3) has no description of the synaptic phenotype observed in the study. These major points are discussed in more detail below.
Major points:
(1) In the introduction the authors state (p. 4): "Finally, recent human NMJ models have been established from PSCs by differentiating these cells into both skeletal muscles and motor neurons in 2D and 3D formats. These previous systems present a remarkable advancement to the studies of human NMJs, however, they require long NMJ formation and maturation time (40 to 60 days), which, restricts their sensitivity and scalability [42]"
In fact, a number of studies have described various in-vitro NMJ systems, with the same timeframes for NMJ formation. For example, in studies by Osaki et al, 2018, Sci Adv; Bellmann et al, 2019, Biomat; Demestre et al, 2015, Stem Cell Res; Badu-Mensah et al, 2022, Biomat (this is just an exemplar selection of the papers); NMJ formation was observed as early as 14 d in culture, in line with or at least slightly longer than reported by Chen et al. With the exception of the study by Osaki et al, all co-culture systems cited above are 2D-based. The authors need to expand on this further or provide a quantitative assessment of why their system is better compared to previously published models.
(2) Further, when comparing their results with other work it is hard to claim how the current system is (p. 5) "more reproducible, and offers a 6-fold increase in scalability compared to previous models [40-43]". The authors need to expand on this further.
(3) Although mentioned, there were no examples of the modularity of the system, which of course would strengthen the paper and help to uncover ALS mechanisms of synaptic formation, for example by combining WT myotubes and fALS motor neurons (see point 4 below). The authors should show how they would adapt to 96 well plate format to showcase the scalability of the system. Based on their data on the efficacy of synaptic formation (60 per 0.7 cm2 area), is further miniaturization allowed?
(4) A lot of a-bungarotoxin staining corresponds to AChR clusters that do not seem to be associated with muscle and do not form normal rings of clustering (pretzel-like) associated with the NMJ in vivo. This is seen clearly in Figure 3B and Figure 5B. Figures 3B and 5B only show low-magnification images which makes it difficult to assess the specificity of localization of the pre-/post-synaptic markers. The authors should clearly show the morphologies of the NMJs formed in WT and fALS lines at high magnification. In addition, the authors should show co-localization images for a-bungarotoxin and myosin-heavy chains to confirm the localization of the bungarotoxin signal on the myotubes.
In addition to that, the authors report that the number of functional synapses formed on a plate varies from 30 (fASL) to 60 (Ctrl) per 10,000 neurons spread over the 0.7 cm2 area (0.6%). How do the authors explain an extensive loss of a-bungarotoxin signal in Figure 5B the majority of which likely corresponds to AChR clusters that are formed outside of neuronal connections? Such clustering can be usually observed in immature co-cultures and in vivo prior to the innervation of myotubes. One explanation could be that myotubes derived from fALS PSC are less capable of synaptic formation. Noteworthy, a study of PSC-derived myotubes and motor neurons from PSC lines with various SOD1 mutations has already been published, but not cited by Chen et al (Badu-Mensah et al). Given the importance of those confounding factors, the authors should test cell-intrinsic (motor neuron-related) vs non-cell-intrinsic mechanisms by co-culturing healthy myotubes with fALS-derived motor neurons followed by NMJ quantification.
(5) The authors present the advantage of optogenetic stimulation, but they only show the proof-of-principle and never really apply it to their studies. Specifically, with regard to Figure 6, are motor units derived from fALS PSCs incapable of being ontogenetically activated to the same extent as control motor units? Does the dysfunction stem from fALS motor neurons or fALS myotubes?
(6) Figures 6 B and C appear to be identical except for the addition of the GDNF effect on the fALS lines. This should all be put in one figure. The authors should also show whether GDNF-induced functional recovery is associated with recovery in the number of motor units or with merely synaptic function by quantifying the NMJ number in the presence of GDNF.
(7) Figure 5 and Figure 6. The authors only use one line per fALS mutation and their corresponding isogenic controls. They state that the n=6 for these experiments represents the technical replication of the experiment. These experiments should be performed at least n=3 times starting from neuronal differentiation, and not by seeding replicate wells representing a true replication of each experiment. This would significantly strengthen their argument that their method is robust and the results are easily reproducible.
(8) In the discussion the authors may want to mention that the lack of function of GDNF on the SOD1 lines may relate to the fact that SOD1 mutations do not lead to TDP43 pathology. Although speculative this suggests that in cases with TDP43 mutations (their data) or sporadic disease GDNF may be effective.
(9) Although beyond the scope of this paper, it would of course be interesting to see if sporadic forms of ALS had this same phenotype.