PCOMPBIOL-D-26-00296

Uncertainty-aware quantitative analysis of high-throughput live cell migration data

PLOS Computational Biology

Dear Dr. Kitanovski,

Thank you for submitting your manuscript to PLOS Computational Biology. After careful consideration, we feel that it has merit but does not fully meet PLOS Computational Biology's publication criteria as it currently stands. Both reviewers find the method promising but request clearer articulation of the contribution, stronger benchmarking against appropriate methods, and improvements in presentation, modeling justification, and analysis. Therefore, we invite you to submit a revised version of the manuscript that addresses the points raised during the review process.

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PLOS Computational Biology

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Reviewers' comments:

Reviewer's Responses to Questions

Comments to the Authors:

Please note here if the review is uploaded as an attachment.

Reviewer #1: This manuscript presents cellmig, an R/Bioconductor package that uses a Bayesian hierarchical model to estimate treatment effects on single-cell migration velocity while accounting for nested experimental structure (cells within wells within plates) and plate/batch effects. The core idea is solid, practical for high-throughput migration experiments, and the software packaging is a meaningful contribution. The main issue is positioning: the manuscript frames its benchmarking as exhaustive and state-of-the-art, but the comparisons as presented do not yet support that level of claim. For a PLOS Computational Biology methods paper, the authors should either strengthen benchmarking against appropriate modern baselines or tone down the “SOTA” language and present the work as a rigorous, uncertainty-aware alternative to common practice. As written, I recommend major revision.

Strengths

* Addresses a common failure mode in migration analysis (pseudo-replication and batch effects) while carrying uncertainty through to effect estimates.

* Statistically coherent approach (hierarchical partial pooling; effect sizes with credible intervals; plate normalization using matched controls) implemented in Stan and distributed via Bioconductor.

* Outputs are practical and interpretable for experimental users (fold-changes with uncertainty and probability-style evidence summaries).

* Validation includes meaningful real datasets, including large-scale screens, showing plate-aware inference at scale.

* The simulation component for experimental design (biological vs technical replicates) is a genuinely valuable feature that many pipelines lack.

Key weaknesses (what currently blocks acceptance)

* Benchmarking and positioning do not match: the manuscript implies state-of-the-art performance but does not yet compare against the most relevant modern hierarchical alternatives.

* The manuscript uses “false positive/false negative” language in contexts where ground truth is not established, which overstates what can be concluded from method disagreement.

* Uncertainty is emphasized for velocity summaries, but upstream measurement uncertainty (segmentation/tracking/filtering choices) is treated lightly, leaving potential bias and sensitivity underexplored.

* Practical deployment guidance is still thin for a screening-oriented tool (runtime/scaling expectations, diagnostics conventions, thresholding guidance, and multiple-testing framing).

* Robustness to common data pathologies (heavy tails, mixtures, outliers, fragmented tracks) needs clearer stress testing and user-facing guidance.

Major concern 1: Benchmarking and “state-of-the-art” positioning are currently misaligned with the comparisons shown. If the authors want to retain an “exhaustive/SOTA” framing, the benchmark needs to include stronger, field-standard approaches for nested high-content data, ideally chosen from methods with stable, open implementations so the comparison is transparent and reproducible. At a minimum, that typically means testing against multilevel/hierarchical baselines (e.g., mixed-effects modeling, or Bayesian multilevel regression implemented in widely used frameworks such as Stan interfaces like brms), and also considering distribution-robust options that respect nesting (e.g., resampling approaches designed for clustered data). The high-throughput screening literature also provides relevant comparators and evaluation concepts that could strengthen the benchmarking story—plate QC metrics like Z′, spatial normalization approaches such as B-score/median polish, and established Bioconductor tooling for plate-based or image-based screens (e.g., cellHTS2, imageHTS). In parallel, there is now precedent for benchmarking batch-correction methods directly in image-based profiling (Cell Painting) using quantitative metrics for both batch removal and biological signal preservation; if the manuscript claims robustness to batch effects, this kind of framing can help define what “robust” means and how to measure it. Alternatively, if the authors’ real target is to improve on common practice in migration workflows (two-stage summaries plus conventional tests), they should say so clearly and consistently and retire the “state-of-the-art” benchmarking language. That reframing does not eliminate novelty: the defensible contribution is an end-to-end, migration-tailored hierarchical workflow that unifies biological effects and batch/plate effects in one generative model and pairs inference with simulation-based experimental planning.

Major concern 2: The manuscript sometimes labels disagreements with the baseline analysis as “false positives” and “false negatives” without an independent truth standard. On real datasets, this is stronger than the evidence supports and reads as if the authors are declaring their own method the ground truth. A cleaner approach is to describe these as discordant calls and then argue, mechanistically and statistically, why one approach is more appropriate for the experimental structure at hand. If the authors want to make error-rate statements, they should confine those to settings where truth is known (e.g., simulations that include realistic plate/well/cell nesting and batch effects) or to external validation. More broadly, the screening literature already offers a vocabulary for decision-making that can be more informative than “false positive/false negative versus my method,” including effect-size and ranking metrics used for hit selection such as SSMD; positioning the decision layer in that ecosystem would strengthen the paper and make it more familiar to screening practitioners.

Major concern 3: The paper emphasizes uncertainty and probability-style evidence summaries, but it does not yet make a convincing case that these quantities are calibrated or how they should be used to make screening decisions at scale. The Bayesian workflow literature is blunt on this point: uncertainty intervals are only as good as the model and need to be interrogated with posterior predictive checks and sensitivity analysis, especially when the data-generating process is plausibly misspecified. This matters here because velocity distributions can be skewed and heavy-tailed, and can also be “structurally weird” due to tracking dropouts and filtering rules. The paper would be much stronger if it demonstrated that its uncertainty statements behave sensibly under realistic conditions and then explained, in practical terms, how an analyst should use those quantities to prioritize treatments in large screens (including how the approach interacts with multiple testing or multi-condition ranking).

Major concern 4: Robustness to model misspecification and common migration-data artifacts needs more emphasis. Migration velocity estimates can be sensitive to outliers, track fragmentation, and heterogeneity that looks more like mixtures than a single clean distribution. The manuscript would benefit from explicitly acknowledging these failure modes and showing that conclusions are either stable to them or that the tool provides clear indicators when they are not. This is also where the existing ecosystem provides useful context: in many migration settings, investigators rely on mature tracking and analysis toolchains (e.g., TrackMate, u-track, CellProfiler) and the broader community has developed benchmark standards for tracking performance (e.g., the Cell Tracking Challenge). If the paper’s downstream inference depends heavily on tracking-derived velocities, it should engage with that reality and help users understand when measurement artifacts could dominate the inference.

Major concern 5: The manuscript should more clearly delimit what is modeled and what is not with respect to upstream image analysis. Right now, the inference layer risks being read as more “uncertainty-aware” than it truly is, because segmentation/tracking uncertainty is not explicitly modeled and filtering choices can change the effective population being analyzed. The most convincing way to handle this is straightforward: state the scope clearly, then show sensitivity analyses that demonstrate how robust the reported treatment effects are to plausible variations in preprocessing and QC. The paper would also benefit from stronger evidence of measurement fidelity (clearer overlays of raw images with segmentation and tracks, and reporting of basic QC summaries such as track-length distributions and exclusion rates), so that readers can judge whether the velocity measurements are trustworthy inputs to a hierarchical inference engine.

Minor concern 1: Figure clarity, especially for segmentation/tracking examples, should be improved so readers can actually evaluate measurement fidelity. If space is tight in the main text, the supplement is fine, but the examples need to be legible and representative.

Minor concern 2: The manuscript should ensure consistent handling of fold-change null references. If the null is 1 on the natural scale and 0 on the log scale, that needs to be stated and used consistently across axes, captions, and legends to avoid confusion.

Minor concern 3: A short scope statement would help. Readers should know exactly which migration paradigms the method targets (single-cell velocity summaries in high-throughput, plate-based assays) and which common paradigms it is not aiming to replace (e.g., scratch/wound-closure analysis pipelines such as TScratch, broader end-to-end migration environments like CellMissy, or collective-migration workflows that use optical-flow/PIV rather than single-cell tracking). This also helps prevent overgeneralization of “velocity” across biological regimes.

Minor concern 4: Reproducibility and deployment details should be tightened. Readers will expect basic guidance on versions, typical compute requirements, and a minimal end-to-end script or vignette that reproduces a primary analysis.

Minor concern 5: Copyediting would improve readability. Tightening informal phrasing and standardizing terminology throughout would make the manuscript feel more careful and reduce opportunities for misinterpretation.

Closing

I view cellmig as promising and potentially impactful because it brings replicate-aware inference and uncertainty reporting to a workflow that is often analyzed with overconfident pooled statistics. If the authors either (a) broaden benchmarking to match the strength of their claims—using appropriate hierarchical baselines and established screening/batch-effect evaluation concepts—or (b) adjust the claims to match the evidence while keeping the methodological contribution front and center, and they strengthen calibration/robustness/QC guidance, I would be supportive of publication.

Reviewer #2: The authors present a Bayesian hierarchical approach to analysis high throughput data related to cell migration. An important component to their approach is the explicit modelling of biological and technical heterogeneity, which is often overlooked in many studies due to pooling of data across technical replicates/batches. They also provide a R package called ``cellmig'' to provide their tools to the research community.

I think this work is timely and valuable contribution to the literature, however, there are a number of concerns I have in relation general presentation of the work and with respect to some claims and results. If the authors are able to satisfactorily address my concerns, then I think it would be suitable for publication in PLOS Computational Biology.

Major Comments:

1. General presentation: I find the manuscript which confusing to read its current layout. It actually feels like the work was originally written for a Journal with section orders of Introduction -> Results -> Discussion -> Materials and Methods (e.g., like many general science journals). I found the transition from Introduction to Materials and Method to be incredibly jarring with the Materials and Methods being full of undefined acronyms and jargon, most of which was not at all properly defined until the Results section.

2. Contribution: It is difficult for me to identify what the main contribution to paper is presenting. Is it the cellmig package itself? or is it the modelling and the demonstration of the importance of dealing with technical/biological heterogeneity in a hierarchical sense? A clear contribution statement in the introduction would benefit the paper substantially. There also needs to be more clarity in exactly what the cellmig R package is providing. For example, if the cellmig restricted to the hierarchical model presented? What does it provide that other Bayesian tools for say Generalised linear/non-linear mixed-effects models would provide (like BRMS). The model that is presented in Equations (1)--(11) is not novel in of itself, so this all needs more clarity for me. Finally, the claim about the generative features within cellmig is not a contribution really, as this is an automatic feature of any parametric model (Bayesian or not), and the authors concepts of fully generative and partially generative is effectively equivalent to prior and posterior predictive sampling which is standard practice. To be clear, I am not saying that this is not a valid thing to do, but the claims of novelty here are tool strong.

3. Modelling: I am generally comfortable with the modelling itself, but I think the choices around priors are not clear at all. The section titled ``Model priors'' on page 10 state ``Wherever possible, we used priors informed by the literature, otherwise employing weakly informative priors ... ' ' however, there is not a single reference to the literature in this section, nor would I consider a normal prior with variance of 1 to be weakly informative, especially for a scale parameter. The Supplementary figures referred to are useful, but they are not justification for the prior choice alone. The priors obtained form the literature should be justified by clear reference to the relevant literature and the claim of weakly informative priors should also be justified (e.g., Gelman text book cited elsewhere discusses this quite a bit in the context of the schools example).

4. Results: There are two main concerns about the results:

4.1 The comparison between the probability of differential effect on migration $\pi$ given in Equation (8) and the

outcome of a frequentist hyponthesis test using a non-parametric test. This is statistically invalid from my

perspective as Bayesian methods do not have statistical converage guarentees at all and the definition of $\pi$ is

simply not comparable to a p-value. Furthermore, a comparison of non-parametric methods with a parametric

model is also not valid. To properly evaluate the improvements of cellmig, an equivalent Bayesian model that

ignores the hierarchical structure would be needed. Such a comparison would ideally include prior sensitivity

analysis.

4.2 The experimental design results and associated claims are potentially extremely biased as the simulations are

effectively posterior predictive samples. So it is unclear how generalisable these results are. I wonder if a prior

predictive approach would be better to highlight the value of the cellmig tools.

5. Software: I was a bit surprised given the emphasis on the cellmig package that there was not clear description of it anywhere. I think the paper would benefit from a short appendix/supplementary description with example code demonstrating the main features of the software.

Minor comments:

1. The next revision should include line numbers, it is quite difficult to provide minor feedback without line numbers.

2. throughout, can Curiour New font be used for the cellmig software name.

3. The abstracts reference to the detail of the experiments are too vague. just remove them, that is the number of cells and conditions.

4. Page 3, can you provide references for the ``Diverse experimental methods...''

5. Page 3, what you you mean by high-throughput?

6. Page 4, I dont understand the point of the ``simple plots'' as being a methodological issue, this is a communication issue.

7. Generally I find the methods section to be too vague. (e.g., what is the difference between A & B in dataset 1) especially page 4 to 7.

8. Page 10 remove the $\rho = $ in the integral lower bounds in equation (8).

9. Page 15, a Wilcoxon rank-sum test and Kruskal-Wallis text etc are not state-of-the-art, they are classical and standard methods, but not state-of-the-art.

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Have the authors made all data and (if applicable) computational code underlying the findings in their manuscript fully available?

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Reviewer #1: Yes

Reviewer #2: No: The software is provided but not sufficient to reproduce the analysis.

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Reviewer #1: Yes: Francesco Pasqualini

Reviewer #2: No

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Dear Mr. Kitanovski,

We are pleased to inform you that your manuscript 'Uncertainty-aware quantitative analysis of high-throughput live cell migration data' has been provisionally accepted for publication in PLOS Computational Biology.

Before your manuscript can be formally accepted you will need to complete some formatting changes, which you will receive in a follow up email. A member of our team will be in touch with a set of requests.

Please note the reviewer's remark regarding providing a reference to the data used in the software.

Please note that your manuscript will not be scheduled for publication until you have made the required changes, so a swift response is appreciated.

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Thank you again for supporting Open Access publishing; we are looking forward to publishing your work in PLOS Computational Biology.

Best regards,

Dimitrios Vavylonis

Section Editor

PLOS Computational Biology

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Reviewer's Responses to Questions

Comments to the Authors:

Please note here if the review is uploaded as an attachment.

Reviewer #1: The authors addressed all my concerns.

Reviewer #2: I thank the authors for their careful consideration of my comment. I am pleased with the revision. The paper is now much clearer in its flow, presents a better case of novelty (focusing on the computational tools, rather than the modelling contribution), presents more principled analysis, and make more appropriate statistical claims while avoiding possible miss -understandings in interpretation.

I have not additional comments to make, I think the article is now appropriate for publication.

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Have the authors made all data and (if applicable) computational code underlying the findings in their manuscript fully available?

The PLOS Data policy requires authors to make all data and code underlying the findings described in their manuscript fully available without restriction, with rare exception (please refer to the Data Availability Statement in the manuscript PDF file). The data and code should be provided as part of the manuscript or its supporting information, or deposited to a public repository. For example, in addition to summary statistics, the data points behind means, medians and variance measures should be available. If there are restrictions on publicly sharing data or code —e.g. participant privacy or use of data from a third party—those must be specified.

Reviewer #1: Yes

Reviewer #2: No: Software seems to be available, but I could not find any reference to the data used.

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Reviewer #1: Yes: Francesco Pasqualini

Reviewer #2: No