PREreview del The fidelity of mRNA translation as a novel regulatory layer for brain development

Review coordinated via ASAPbio’s crowd preprint review

This review reflects comments and contributions by Debraj Manna, Rodolfo Aramayo, Shailee Rasania, Yuka Gliday, Patricia Garcez, Randa Salah Gomaa Mahmoud, Diptarup Mallick, Nitya Khetarpal, Emmanuel Odame, Reuben Opoku, Maria Beatriz Capitão, Timothy En Haw Chan, Joseph Biggane, Briana E. Pinales, and Yohana Amos. Review synthesised by Debraj Manna.

The current study was designed to uncover unexpected spatiotemporal dynamics of translation fidelity during organ development by generating a highly quantitative dual-luciferase reporter knock-in mouse model. The results revealed that stop codon readthrough occurs at substantially lower levels in intact organisms than in pluripotent stem cells and decreases progressively across development. The brain and muscle tissues exhibited the lowest error rates, indicating that mRNA translation fidelity is a developmentally programmed layer of gene regulation.

Crowd Review Comments:

Pertaining to the Abstract:

• In response to “vary across cell types”, the reviewers noticed that the authors use bulk data, organ-level tissue measurements, not sampling per brain region. Their organoid experiments are in vitro, so the authors may wish to temper their claims/goals regarding in vivo cell-type variation in mRNA translation integrity, unless they have or will have data to support them.

• In response to “experimentally increased translation errors”, the reviewers think specifying that the authors used a pharmacological block would help.

Pertaining to the Introduction:

• In response to “emerging evidence suggests that error-derived peptides can have beneficial effects in specific contexts”, the reviewers think that it would be useful to elaborate a bit here for the reader. Specifically, adding an example would help the reader understand the potential impact of this study.

Pertaining to the Results:

• The figures are generally clear and well-organised. The schematic in Fig. 1A effectively communicates the reporter design. However, Fig. 3 would benefit from an overlay or summary panel that directly compares the developmental trajectories across all organs on the same axes, making the organ-specific temporal dynamics easier to appreciate at a glance. The Ribo-seq metagene plots (Fig. 2D) are small and difficult to interpret—a quantified summary (e.g., bar graph of mean 3' UTR ribosome density across replicates) would complement the profiles.

• The study integrates multiple systems (mouse models, cerebral organoids, in vitro differentiation, and Ribo-seq analysis), thereby strengthening the validity and reproducibility of the findings.

• In response to “Halo-tag treated with a synthetic ligand conjugated with the Janelia Fluor 646 … Halo tag ligands has not succeeded with knock-in mouse tissue sections or derived cells due to the small number of error-containing products”, Fig. 1C shows levels of non-specific background autofluorescence.

• In Fig. 1B, the authors compare readthrough rates for UGA, UAG, and UAA. It would be helpful if the authors could clarify how these values were normalised and indicate which construct was used as the reference for calculating readthrough.

• In response to “Reporter mRNA was transcribed from the CAG promoter”, since promoters drive transcription of mRNAs, but do not directly transcribe them, it would be better to say "controlled by" or something similar.

• In response to “Each stop codon exhibited significantly different readthrough rates compared to the UGA stop codon”, normalization in Fig. 1B is unclear; UGA/UGA should be 1 based on this explanation. Is this a UAG vs UGA vs UAA (in which case UGA/UGA should be 1) or a 2 vs UGA as baseline?

• The authors should specify n in Fig. 1B.

• In Fig. 1C, the dotted connector is redundant given the panel layout. Scale bars are missing. And swapping the green for a white or yellow might be more visually striking, especially with such a small/low-res image.

• In response to Fig. 1F, the E9.5 homogeneity claim may be premature. The authors state that all tissues at E9.5 exhibit readthrough rates similar to those of mESCs (Fig. 1F). However, the box plots show substantial variability, and the comparison is made against a single mESC reference value (dashed line). A formal statistical test comparing each E9.5 tissue to mESCs, with appropriate multiple testing correction, should be performed to support this claim. The n of 10 is reasonable, but the whiskers in some groups are wide.

• Also, unclear which test they used here (they state "Mann-Whitney/Kruskal-Wallis," but these differ); if both, it merits an explanation of why. Interestingly, if they have all tissue bits from the same embryo, it would be cool to do a paired test for significance! Also, "n≥10 harvested from more than 2 litters" could be more specific, e.g., n = a specific number, for clarity.

• In reference to “To achieve systemic and high-level expression, we integrated the reporter transgene with the CAG promoter … both male and female without any notable maturation defects or abnormalities (Fig. S2A)”, the reviewers appreciate the use of good controls.

• In response to “Hence, we hypothesised that cells and tissues establish specialised fidelity across differentiation, either maintaining fidelity or increasing translation errors”, the reviewers believe that the in vivo–to–in vitro comparison conflates many variables. A core claim is that translation fidelity is higher in vivo than in cultured cells (Fig. 2A–B). However, comparing intact organs with mESCs or MEFs conflates numerous variables: cell type, proliferative state, oxygen tension, metabolic environment, passage number, and media conditions. The observation that MEFs rapidly increase error rates upon derivation (Fig. 2B) is interesting but could reflect adaptation to culture conditions, oxidative stress, or changes in protein quality control rather than a specific "in vivo fidelity program." The authors should discuss these confounds more carefully and temper claims about in vivo regulation of fidelity per se. A more controlled comparison might involve freshly isolated primary cells versus cultured cells of the same type.

• In reference to “suggest that in vivo organisms display higher translation fidelity than cultured cells”, the reviewers think that this claim needs more data than a single MEF passage.

• In reference to “Consistent with the higher stop codon readthrough observed in the lung compared to the brain, the lung exhibited more stop codon readthrough products than the brain, relative to the accurate products, which were used as a loading control (Figs. 2C, and S3A)”, the reviewers think that the authors might consider doing westerns for all of the organ samples. There are potential issues with using the double reporter ratio to quantify fluorescence differences, such as quantum yield discrepancies that can result in non-linear comparison ratios.

• In reference to “The brain has low stop codon readthrough genome-wide”, the reviewers believe that the Ribo-seq analysis of endogenous readthrough (Fig. 2D) is insufficiently rigorous. The authors re-analysed a published Ribo-seq dataset to examine ribosome occupancy in 3' UTRs as evidence of endogenous stop codon readthrough. However, the analysis as presented has several limitations. First, 3' UTR ribosome footprints can arise from multiple sources besides stop codon readthrough, including internal ribosome entry, re-initiation, or even RNA-binding protein footprints that co-sediment during ribosome profiling. The authors do not perform any filtering or statistical framework to distinguish genuine readthrough from these confounders. Second, the metagene plots show only two biological replicates per tissue with notable variability between them (e.g., kidney and lung), and no statistical test is applied to compare tissues. Third, while three-nucleotide periodicity in 3' UTR reads is mentioned for some tissues, this critical evidence is not quantified—the authors should compute periodicity scores and demonstrate frame bias to confirm translational origin. Finally, the absence of a matched total RNA-seq normalisation makes it difficult to exclude that differences in 3' UTR ribosome density simply reflect tissue-specific differences in mRNA abundance or 3' UTR length distributions.

• In response to “extend our results from our reporter construct to endogenous mRNA transcripts”, the knock-in reporter uses a CAG promoter driving the construct from the Hipp11 locus, meaning it does not reflect endogenous gene regulation. Tissue-specific differences in CAG promoter activity, mRNA stability, or protein turnover could confound interpretation of the Fluc/Rluc ratio. The authors address mRNA levels (Fig. S3B) showing similar Halo/SNAP and Fluc/Rluc RNA ratios across organs, which is reassuring. However, differential protein stability or proteasomal degradation rates between tissues—which could preferentially degrade the readthrough product in some organs—are not addressed. If the brain has higher proteasome activity for misfolded proteins, the lower Fluc/Rluc ratio could partly reflect enhanced clearance of the readthrough product rather than fewer readthrough events.

• In response to “Stop codon readthrough errors are reduced across development”, the reviewers suggest that potential confound of cell-type composition changes during development. The developmental time course (Fig. 3) measures bulk tissue readthrough at E11.5, E13.5, E18.5, and 2 months. However, the cellular composition of each organ changes dramatically across these stages. For instance, the embryonic brain at E11.5 is predominantly composed of neural progenitors, whereas by 2 months it is dominated by post-mitotic neurons and glia. The observed decline in readthrough could partly reflect shifting proportions of cell types with inherently different fidelity levels, rather than a cell-autonomous developmental program. Single-cell or cell-type-specific measurements at multiple developmental stages would be needed to disentangle compositional effects from genuine within-cell fidelity changes. The authors should acknowledge this confound explicitly in the discussion.

• In response to “This data indicates that organ-specific translation”, the reviewers think that this part would benefit from single-cell or cell-type-specific trajectories; this is an over-conclusion from the current data (bulk tissue across broad time points).

• In response to “the brain needs to express exceptionally long proteins”, the reviewers suggest that the brain usually expresses different mRNA isoforms. It could be discussed here or in the discussion.

• In response to Fig. 3, the reviewers suggest statistical considerations: For the developmental time course (Fig. 3), all comparisons are made relative to mESCs. However, the biologically more relevant comparisons are between consecutive developmental stages within each organ (e.g., E11.5 vs. E13.5 vs. E18.5). These pairwise comparisons would better support the claim of "gradual" reduction. Additionally, the choice of the Mann-Whitney U test versus the Student's t-test varies across experiments without a clear justification for when each is used. With the relatively small sample sizes (n ≥ 3), the power to detect modest differences is limited, and effect sizes should be reported alongside p-values.

• In response to “Translation errors impair cerebral organoid formation”, the reviewers think that the authors have put heavy reliance on paromomycin as the sole means of inducing translation errors. The functional experiments (cerebral organoids, Figs. 4; iPSC-derived neurons, Fig. 5F) rely exclusively on paromomycin to increase translation errors. Aminoglycosides have well-documented pleiotropic effects beyond ribosomal decoding, including induction of ER stress, oxidative stress, mitochondrial dysfunction, and direct cytotoxicity—particularly relevant in neural cells (the authors themselves cite ref. 50 on aminoglycoside-induced ER stress). While the authors show that PAX6+ progenitors are unaffected, this does not rule out the possibility that the reduction in TUBB3+ neurons reflects generalised toxicity to differentiating cells rather than a specific consequence of increased translation errors. A genetic approach to increasing mistranslation (e.g., expression of an error-prone ribosomal protein mutant, or an editing-defective tRNA synthetase) would greatly strengthen the causal claims. At minimum, the authors should test a second, mechanistically distinct error-inducing perturbation, or include dose-response and cell viability data to argue against non-specific toxicity.

• In reference to “organoid size reduction “, the reviewers ask if the top and bottom of 4F are on the same scale.

• In reference to Fig. 4F, the authors may please include scale bars. This is particularly relevant, as they are comparing organoid size.

• In response to “Given that the PAX6-positive progenitors remained unchanged, our results indicate that increasing translation errors induces a loss of differentiation from NPCs to neuronal cells”, the reviewers believe that the fact that PAX6+ progenitors are unchanged in numbers does not necessarily mean that the reduction of Tuj1+ cells is related to a loss of differentiation. The authors should clarify whether there is an increase in cell death and whether there are alterations in the other progenitor population, the TBR2+ progenitors.

• In response to “reduced organoid size”, the reviewers suggest that the cerebral organoid size reduction could have multiple explanations. While consistent with microcephaly seen in ribosomopathy patients, reduced organoid size under paromomycin treatment could also reflect reduced proliferation, increased apoptosis, or metabolic impairment. The authors dismiss radial glia expansion as an explanation but do not show proliferation markers (Ki67, EdU), apoptosis markers (cleaved caspase-3, TUNEL), or cell cycle analysis. These data would distinguish between impaired differentiation and reduced cell survival.

• In response to “Our knock-in mice revealed that the brain possesses”, the reviewers suggest that, to be comprehensive, the authors should consider all brain cell populations, e.g., using snRNAseq.

• In response to “...translation fidelity more generally”, the reviewers mention that the brain contains cells other than neurons, including astrocytes, microglia, and endothelial cells, each with different metabolic rates. The authors should clarify whether this high fidelity is a property of all brain cells or specifically of post-mitotic neurons.

• In response to “These two cell populations were fractionated based on their differences in cell adhesion properties”, could the authors perform FACS or a bead-based separation after detaching cells?

• In reference to Fig. 5:

  1. A suggestion is made to include scale bars in the microscopy images.

  2. The neuron versus non-neuron comparison uses a crude fractionation approach. The in vitro neuron differentiation experiments (Fig. 5) separate neurons from non-neuronal cells based on differential trypsin sensitivity (2 min vs. 5 min). This is a coarse method that is likely to yield impure populations. The purity of each fraction is not rigorously assessed—only Tuj1 western blots are shown. Residual neurons in the "non-neuron" fraction or contaminating progenitors in the "neuron" fraction could artifactually reduce or increase measured error rates, respectively. FACS-based purification using a neuronal surface marker would provide cleaner populations and more convincing data.

  3. The green arrows are not visible in Fig. 5A.

  4. The ageing data (Fig. 5G) are tangential and underdeveloped. The ageing time course (2, 10, 18 months) is shown for the brain only, with no other organs presented for comparison. This single-organ observation, while consistent with a recent publication (ref. 34), adds little to the developmental story and might distract from the main narrative. It could be moved to the supplementary data or expanded to include additional organs.

• In response to “Although −1 frameshift was not significant, it also indicated a trend in the same direction (p=0.0501)”, the reviewers suggest that the −1 frameshift result is borderline (p = 0.0501) and should not be grouped with the significant findings. The text states that neurons exhibited fewer errors for amino acid misincorporation and +1 frameshifting, but then adds that −1 frameshifting "also indicated a trend in the same direction." This should be clearly stated as non-significant, and the authors should avoid implying it supports the same conclusion.

• In response to “we observed fewer MAP2 positive mature neurons”, the reviewers mention that in in vitro experiments, the authors have observed a reduction of MAP2+ cells. If there is a differentiation defect or a maturation impairment, the authors would expect fewer MAP2+ cells and more indifferentiated cells (SOX2+?). However, it seems (at least from the representative image), that there is an overall reduction of the number of cells in this culture. Could the authors clarify?

• In response to “iPSC lines produced from different individuals”, the reviewers believe that controls are missing in the iPSC experiment. The iPSC-derived NPC to neuron maturation experiment (Fig. 5F) shows fewer MAP2+ neurons under paromomycin. The reviewers ask about the number of iPSC lines and the number of independent differentiations performed. The text mentions "iPSC lines produced from different individuals", but the figure legend should specify the exact number of biological replicates and whether the data were replicated across independent differentiation batches.

Pertaining to Discussion:

• The reviewers suggest that since fidelity drops almost immediately once cells are moved to a dish, the authors should discuss whether the low fidelity seen in mESCs is a biological trait of stemness or simply an artifact of cell culture stress.

• The discussion could better integrate the emerging literature on beneficial roles of translation errors. The authors briefly mention that error-derived peptides can have beneficial effects (refs. 35–39, covering the cancer immunopeptidome literature). This is an exciting conceptual counterpoint to the "errors are always bad" framework. If tissues like liver and lung tolerate higher error rates, might this reflect a functional advantage—for instance, in generating peptides for MHC-I presentation in immune surveillance? The authors raise this possibility but could develop it further, as it could explain why not all tissues evolve toward maximal fidelity.

• The manuscript convincingly documents that translation error rates vary across tissues and development but provides no mechanistic data on how this regulation is achieved. Are there tissue-specific differences in tRNA pools, aminoacyl-tRNA synthetase fidelity, ribosome composition, or protein quality control (proteasome/autophagy) that could explain the observed patterns? The authors speculate briefly about proteasome activity in stem cells (citing ref. 69) but do not test this. Even correlative data—such as expression profiling of tRNA genes, ribosomal protein paralogs, or quality control factors across the tissues and timepoints studied—would add substantial value. Without any mechanistic entry point, the study remains largely descriptive.

• In response to “this observation is consistent with the traditional dogma that translation errors impose a burden on cellular homeostasis”, consistent observations across independent methods (reporter assays and ribosome profiling) support the reliability of conclusions regarding tissue-specific translation fidelity.

• In response to “uncovered pronounced organ-specific differences in translation fidelity in young … multiple lines of evidence strongly support a translational origin of the observed signals”, the reviewers mention that the study relies heavily on reporter constructs, which may not fully capture endogenous translation error complexity, and some mechanistic insights into how fidelity is regulated remain unclear.

• In response to “foundation to further explore the dynamics of mRNA translation fidelity in health and disease”, the authors should investigate the molecular mechanisms regulating translation fidelity across tissues and development; explore the role of translation fidelity in human neurological disorders and aging-related diseases; extend analysis to additional cell types and environmental conditions to assess broader biological relevance; use complementary techniques (e.g., proteomics, single-cell analysis) to validate findings at higher resolution; examine therapeutic strategies targeting translation fidelity to improve neuronal health or treat disease.

Pertaining to Methods:

• In response to “Generation of knock-in reporter mice”, the reviewers mention that the use of a dual-luciferase knock-in reporter mouse model is a strong and innovative approach, allowing in vivo quantification of translation errors with high sensitivity and specificity.

• In response to “reviewed and approved by the University of Florida Animal Care Services (ACS)”, the reviewers suggest the addition of the approval code.

• In response to “Age-matched, litter-matched cohorts of transgenic and wild-type were regularly weighed in grams from birth to 22-weeks”, the reviewers mention that litter‑matched means that transgenic and wild‑type animals are siblings from the same litter, ensuring that differences observed are attributable to genotype rather than maternal or environmental variation; however, the results of litter‑based analysis were not illustrated.

• Please expand the abbreviations like DMEM, ESC, FBS, mLIF, SNAP, Halo, JF646, PBS, IP, PVDF, DMEM/F-12, MEM-NEAA, 2-ME, iPSC, IF, MAP-2, etc.

• Please identify the cell types of C3H/10T/1/2, NIH3T3, and HAP1 cells.

• In response to “(DMEM supplemented with 2 mM L-glutamine, 10% FBS, and penicillin–streptomycin)”, the reviewers note that this medium differs from that mentioned in the 1st paragraph of the cell line section; (2 mM L-glutamine was not added).

• In response to “...Rluc and Fluc or Fluc and Nluc were used…”, the reviewers suggest that the authors please elaborate on firefly luciferase (Fluc) as an experimental reporter (responsive element), Renilla luciferase (Rluc) as an internal control (normalisation), and NanoLuc luciferase (Nluc) as an internal control or secondary normalisation reporter.

• In response to “Ribosome profiling data analysis”, the reviewers think that the statistical analyses (Student’s t-test and Mann–Whitney U test) are appropriate, but details such as effect sizes and confidence intervals are not consistently reported. The number of biological replicates is generally adequate (minimum n=3), though larger sample sizes would improve statistical power. Data availability is clearly stated, with all data included in the manuscript and supplementary materials. Some experimental details (e.g., normalisation methods in luciferase assays) could be described more transparently.

Pertaining to Statistical analysis:

• The descriptive statistics and the program used to assess the statistical analysis should be mentioned.

• The authors could please identify the basis for using each test like the choice between the Mann–Whitney U test and the Student’s t test.

Pertaining to Data and materials availability:

• The authors state, "All data are available in the main text or the supplementary materials," but no raw data accession numbers are provided. The Ribo-seq reanalysis should cite the specific GEO/SRA accession used, and ideally, the analysis code should be deposited on GitHub or a similar platform to enable reproducibility.

Competing interests

The authors declare that they have no competing interests.

Use of Artificial Intelligence (AI)

The authors declare that they did not use generative AI to come up with new ideas for their review.