Bayesian inference offers a principled way to quantify uncertainty in gene expression studies, especially when biotechnology experiments have few biological replicates and noisy measurements. In practice, RNA-seq data often contain uneven library sizes, donor effects, low-count genes, outlier samples, and uncertain dispersion estimates. These problems are not minor technical details because they directly affect differential-expression calls. A realistic Bayesian analysis must therefore report both what the model estimates and where the model struggles. Many demonstrations of Bayesian transcriptomic methods are cleaner than the data encountered in small biotechnology experiments. Simulations are useful for understanding operating characteristics, but they cannot fully reproduce imperfect sample preparation, donor heterogeneity, hidden technical variation, or weakly expressed genes. Real datasets also force uncomfortable decisions about filtering, normalization, convergence failure, and prior sensitivity. These issues are often underreported even though they strongly influence downstream biological interpretation. This manuscript applies Bayesian hierarchical modeling to a real public RNA-seq dataset, GEO accession GSE52778, rather than to simulated data. The dataset contains human airway smooth muscle cells measured under untreated and dexamethasone-treated conditions, with four paired donor-derived cell lines and therefore only four replicates per condition. The goal is not to prove that Bayesian inference is superior, but to evaluate how it behaves when the data are small, noisy, and biologically heterogeneous. A standard frequentist analysis is used as a comparison rather than as a presumed gold standard. Raw gene-level counts were analyzed after low-count filtering, median-of-ratios normalization, and exploratory quality control. A negative-binomial Bayesian hierarchical model was specified with sample size factors, treatment effects, gene-specific dispersion, and donor blocking. Shrinkage priors were used for treatment effects to stabilize fold-change estimation under small n. DESeq2 and edgeR were fitted to the same filtered count matrix, and posterior diagnostics, prior sensitivity, and model failures were recorded rather than suppressed. The selected dataset was visibly imperfect: library sizes varied by approximately two-fold, more than half of the original gene rows were dominated by zeros or near-zero counts, and PCA showed strong donor structure in addition to treatment separation. After filtering, 24,159 genes were retained from the original 64,102 annotated gene rows, leaving a count matrix still affected by low expression and donor heterogeneity. MCMC convergence was adequate for most modeled genes, but a non-trivial subset of low-count or high-dispersion genes showed poor mixing, wide credible intervals, or unstable posterior treatment effects. Agreement between Bayesian posterior decision rules and DESeq2 was moderate rather than complete, especially for weakly expressed genes with large apparent fold changes. Bayesian inference helped make uncertainty visible, particularly for genes whose estimated treatment effects looked large but were poorly supported by sparse counts. It did not eliminate the consequences of small n, donor effects, low expression, or imperfect model fit. The analysis supports a cautious workflow in which Bayesian and frequentist results are compared, disagreements are reported, and convergence diagnostics are treated as substantive results. The main conclusion is that Bayesian methods are useful for real transcriptomic data only when uncertainty, failure, and prior dependence are made explicit.
Introduction
Bayesian analysis of gene expression data is attractive because it provides posterior uncertainty rather than only point estimates and adjusted p-values (Carita et al., 2025). This feature is valuable in biotechnology experiments, where cost, sample availability, and cell-line constraints often leave investigators with three to six replicates per condition (Torres-Cruz et al., 2025). Negative-binomial Bayesian models and empirical-Bayes shrinkage approaches have been developed to stabilize inference in precisely these settings, but their performance depends on assumptions about dispersion, exchangeability, and prior scale (Zhao et al., 2017; Landau et al., 2019; Zhu et al., 2019). In real RNA-seq data, those assumptions are stressed by low counts, heterogeneous samples, and technical artifacts rather than by clean textbook noise.
Differential-expression analysis in biotechnology is not only a statistical ranking exercise; it frequently guides target selection, pathway interpretation, and experimental validation. Methods such as DESeq2, edgeR, limma-style empirical Bayes, and fully Bayesian negative-binomial models often agree on high-signal genes but diverge for low-expression genes, genes with uncertain dispersion, and genes affected by outlying samples (Sun et al., 2019; Zhu et al., 2019; Li et al., 2022). Recent evaluations of RNA-seq differential-expression methods show that method choice can materially alter conclusions, especially when sample size is limited and normalization does not fully absorb unwanted variation (Costa-Silva et al., 2017; Li et al., 2022). For that reason, comparing Bayesian and frequentist outputs on the same imperfect dataset is more informative than presenting Bayesian results alone.
Batch effects and hidden confounders are particularly relevant because RNA-seq counts reflect both biology and processing history. Methods such as ComBat-seq, variance partitioning, surrogate-variable strategies, and unwanted-variation adjustment were motivated by real multi-sample studies in which library preparation, sequencing lane, donor, or study origin changed expression estimates (Zhang et al., 2020; Cote et al., 2022; Molania et al., 2023; Mostafavi et al., 2023; Yu et al., 2023). These corrections can reduce unwanted structure, but they can also remove biological signal or introduce new uncertainty when covariates are confounded. A Bayesian model can include nuisance effects explicitly, yet it cannot recover information that the design failed to identify.
This article therefore uses a real public dataset, GSE52778, consisting of human airway smooth muscle cells exposed to dexamethasone, with four paired donor-derived cell lines. The dataset is biotechnologically relevant because glucocorticoid response in airway smooth muscle is tied to therapeutic mechanisms and drug-response transcriptomics (Himes et al., 2014). It is also realistically imperfect: n is small, donor structure is strong, many genes are weakly detected, and library sizes are uneven. The aim is to show what a Bayesian workflow reveals under these constraints, including uncertainty, disagreement with DESeq2, prior sensitivity, and convergence problems (Zhao et al., 2017; Zhu et al., 2019; Li et al., 2022).
Figure 1 presents the full real-data workflow used in this manuscript, showing how GSE52778 moves from imperfect public RNA-seq counts through preprocessing, Bayesian hierarchical modeling, frequentist comparison, and explicit reporting of convergence, prior-sensitivity, and outlier-related uncertainty.
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Figure 1. Real-data Bayesian workflow for imperfect RNA-seq differential-expression analysis in GSE52778 |
Background
Real-World RNA-Seq in Biotechnology: Small N, Variable Quality
Small-n RNA-seq experiments remain common in biotechnology because biological material, sequencing budget, and validation capacity are limited. GSE52778 reflects this setting: it uses four human airway smooth muscle cell lines measured under control and drug-treated conditions, rather than dozens of exchangeable samples (Himes et al., 2014). In such designs, the donor or cell-line effect can be as important as treatment, so ignoring pairing inflates apparent information. Bayesian hierarchical modeling is useful here because it can share information across genes, but shrinkage cannot replace missing replication (Zhao et al., 2017; Landau et al., 2019; Ren & Kuan, 2020).
Known Imperfections: Batch Effects, Outliers, Missing Counts
Real transcriptomic data contain imperfections that are often only partly visible in metadata. Batch effects may arise from library preparation or sequencing, hidden unwanted variation may appear in principal components, and outliers may be sample-specific or gene-specific rather than globally obvious (Zhang et al., 2020; Molania et al., 2023; Yu et al., 2023). Missing values in count matrices are usually less common than zeros, but zeros themselves are a mixture of true absence, weak detection, and finite sequencing depth. Bayesian imputation and network methods can address missingness in some multi-omics settings, but count-based RNA-seq models should not automatically impute zeros as if they were ordinary missing values (Howey et al., 2021; Howey et al., 2025).
Bayesian Methods as a Solution for Small Samples — But Assumptions Matter
Bayesian and empirical-Bayes methods stabilize small-sample inference by borrowing strength across genes or imposing shrinkage on noisy effects. Heavy-tailed priors are especially useful because they shrink noisy small effects while preserving genuinely large fold changes better than overly narrow normal priors (Zhu et al., 2019). Negative-binomial Bayesian models can represent overdispersed counts, and covariate-dependent factor models can account for structured variation when sample information is available (Zhao et al., 2017; Zamani Dadaneh et al., 2018). These advantages depend on the prior and likelihood being plausible for the data, not merely mathematically convenient.
Prior Failures of Bayesian Models
Bayesian methods can fail in ways that are easy to overlook if only posterior means are reported. MCMC chains can mix slowly for low-count genes, dispersion and treatment effects can be highly correlated, and posterior intervals can become too wide for decisive biological claims (Papastamoulis & Rattray, 2018). Prior sensitivity is not a nuisance detail in small-n genomics because the prior may carry nearly as much influence as the observed counts for weakly expressed genes (Landau et al., 2019; Zhu et al., 2019). Honest Bayesian reporting therefore requires convergence diagnostics, effective sample sizes, divergent-transition counts, and sensitivity analyses, not just a list of significant genes.
Need for Honest Benchmarking on Real, Not Simulated, Data
Simulation studies remain important, but they cannot fully reproduce the messy relationship among donor effects, library size variation, low expression, and outlier behavior seen in real biotechnology datasets. Reviews and method comparisons have repeatedly shown that RNA-seq results depend on preprocessing, normalization, dispersion estimation, and statistical framework (Costa-Silva et al., 2017; Quinn et al., 2018; Quinn et al., 2019; Li et al., 2022). Real-data benchmarking is therefore necessary because it exposes disagreements that simulations may smooth over. In this manuscript, GSE52778 is used as a deliberately imperfect benchmark rather than as a polished demonstration dataset (Himes et al., 2014).
Description & Imperfections
Dataset Selection
The analysis uses GEO accession GSE52778, a human airway smooth muscle RNA-seq experiment measuring untreated control and dexamethasone-treated samples from four donor-derived cell lines. The working subset contains eight samples, with four paired biological replicates per condition, and the design is modeled as control versus dexamethasone while blocking on cell line. The original study is relevant to biotechnology because it examines transcriptomic response to asthma medications, including glucocorticoid exposure, in a disease-relevant primary cell type (Himes et al., 2014). The dataset does not provide a convenient explicit batch variable for the reduced two-condition subset, so donor identity, library size, and residual principal-component structure are treated as the main observed and hidden sources of unwanted variation (Zhang et al., 2020; Molania et al., 2023; Mostafavi et al., 2023).
Quantifiable Flaws
The count matrix used here contained 64,102 annotated gene rows across eight samples before filtering, with no literal missing count entries but many zero or near-zero observations. Library sizes based on assigned gene counts varied by roughly two-fold across samples, with the smallest library contributing substantially less information for lowly expressed genes than the largest library. PCA of variance-stabilized counts showed that donor/cell-line structure remained prominent after normalization, while treatment separation was clearer for a subset of high-response genes such as glucocorticoid-responsive transcripts (Himes et al., 2014). These flaws are typical of real RNA-seq data and are precisely why normalization, blocking, shrinkage, and diagnostic reporting are necessary rather than optional (Zhang et al., 2020; Cote et al., 2022; Li et al., 2022).
Table 1 clarifies how each documented imperfection in GSE52778 enters the inferential workflow, distinguishing data features that can be modeled, features that can only be diagnosed, and features that remain unavoidable limitations.
Table 1. Analytical role of real-data imperfections in Bayesian RNA-seq inference
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Real-data imperfection |
Manifestation in GSE52778 analysis |
Statistical consequence |
Bayesian treatment |
Residual risk after modeling |
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Small biological replication |
Four paired donor-derived cell lines per condition |
Limited information for gene-specific treatment effects and dispersion |
Hierarchical shrinkage stabilizes weakly estimated effects |
Subtle effects may remain indistinguishable from noise |
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Donor / cell-line heterogeneity |
Strong paired donor structure visible in exploratory diagnostics |
Treatment effects may be confounded with baseline donor differences |
Donor blocking included in the linear predictor |
Donor-specific treatment responses cannot be fully resolved |
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Uneven library sizes |
Approximately two-fold variation in assigned gene-count totals |
Low-depth samples contribute less information, especially for weak genes |
Size-factor offset included in the negative-binomial model |
Normalization cannot recover counts that were never observed |
|
Low-count genes |
Large number of genes removed during filtering; sparse counts remain after filtering |
Inflated uncertainty, unstable dispersion, and poor MCMC mixing |
Low-count filtering plus shrinkage priors |
Some retained genes still yield unreliable posterior summaries |
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Zero-heavy observations |
Many gene-sample entries are zero or near zero |
Large apparent fold changes may reflect weak detection rather than biology |
Negative-binomial likelihood applied directly to counts |
Zero-heavy genes can remain prior-sensitive |
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Hidden unwanted variation |
Residual structure after normalization and donor blocking |
Posterior treatment effects may absorb unmodeled technical variation |
PCA and residual diagnostics used; nuisance structure considered cautiously |
Unidentified batch-like effects may persist |
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Gene-specific outliers |
Individual donor spikes or Cook’s-distance flags for selected genes |
Differential-expression calls may depend on one biological replicate |
Leave-one-donor sensitivity analysis |
Outlier-sensitive genes cannot support strong claims |
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Model-computation instability |
Elevated R̂ or low effective sample size for some genes |
Posterior summaries may be unreliable despite formal model specification |
Convergence diagnostics used as exclusion and warning criteria |
Failed genes reduce transcriptome-wide interpretability |
Why This Dataset Is Realistic for Biotechnology
GSE52778 is realistic because it was generated for a biological drug-response question, not for a statistical benchmarking contest. The small number of paired donor-derived cell lines makes it representative of expensive cell-based biotechnology experiments where replication is limited by biological material and laboratory cost (Himes et al., 2014). The dataset also contains a large proportion of genes with little or no usable information, so filtering decisions materially shape the inference space. This is a more honest setting for Bayesian inference than a simulated count matrix with known truth and perfectly balanced noise (Costa-Silva et al., 2017; Zhao et al., 2017; Li et al., 2022).
Preprocessing and Quality Control (Real Issues)
Count Filtering
Low-count filtering was performed before model fitting because thousands of annotated gene rows carried essentially no information about dexamethasone response. Genes were retained if they had at least 10 total counts across the eight samples and at least 1 count per million in four or more samples, leaving 24,159 genes from the original 64,102 rows and removing 39,943 low-information rows. This filtering step reduced the extreme zero burden but did not make the data clean, because many retained genes still had weak counts in one condition or one donor. The decision is consistent with count-based RNA-seq practice, where retaining uninformative rows can worsen multiple testing and destabilize dispersion estimation (Costa-Silva et al., 2017; Quinn et al., 2018; Li et al., 2022).
Normalization Choices
The primary normalization used DESeq2 median-of-ratios size factors, while TMM normalization was used as a sensitivity check because compositional effects can distort RNA-seq comparisons. Neither method can fully correct donor heterogeneity or hidden unwanted variation, because normalization rescales libraries but does not identify all biological and technical sources of structure (Quinn et al., 2018; Quinn et al., 2019). For quality control, variance-stabilized counts were used for PCA and sample-distance plots, but the inferential models used raw counts with size-factor offsets. This distinction matters because visual transformations can help detect problems without replacing the negative-binomial likelihood used for differential-expression modeling (Zhao et al., 2017; Ren & Kuan, 2020; Li et al., 2022).
Outlier Detection and Handling
No sample was removed from the primary analysis because the design already had only four paired replicates per condition, and deleting one donor pair would have caused a severe loss of information. However, one lower-depth sample and several gene-specific Cook’s-distance flags were treated as warning signs rather than ignored. PCA did not justify global sample exclusion, but it did show that donor structure was strong enough to require explicit blocking in both Bayesian and DESeq2 models (Himes et al., 2014; Cote et al., 2022; Mostafavi et al., 2023). A leave-one-donor sensitivity analysis was therefore planned to quantify how many differential-expression calls depended on any single donor rather than on the full paired pattern (Li et al., 2022; Molania et al., 2023).
Bayesian Model Specification
Likelihood
The primary Bayesian likelihood was negative binomial because the data are integer counts with overdispersion beyond a Poisson model. For gene g in sample i, the observed count was modeled using a mean linked to the treatment, donor blocking, and sample-specific size factor, with a gene-specific dispersion parameter (Agrawal et al., 2024; Bona & Lozano, 2024; Khan et al., 2024; Qiao et al., 2024; Ha et al., 2025; Yilmaz & Erkol, 2025). This choice follows the logic of Bayesian and frequentist RNA-seq models that treat biological variability as larger than simple sampling noise (Zhao et al., 2017; Landau et al., 2019; Ren & Kuan, 2020). A log-normal model was reserved for sensitivity analysis on transformed counts, not as the main model, because it handles continuous transformed expression less directly than the negative-binomial count likelihood (Zamani Dadaneh et al., 2018; Osabe et al., 2019).
Priors
Treatment log fold changes were assigned heavy-tailed shrinkage priors centered at zero so that noisy weak effects were pulled toward zero while large drug-response signals could remain large when supported by the data. The main prior used a Student-t distribution with moderate scale, and sensitivity analyses compared stronger and weaker scales to identify prior-sensitive genes. This choice was motivated by evidence that heavy-tailed priors can reduce noise without erasing large effects in sequence count data (Zhu et al., 2019). Dispersion parameters received weakly informative positive priors, but the model did not assume that the prior could overcome the limited information available for very low-count genes (Zhao et al., 2017; Papastamoulis & Rattray, 2018).
Model Equation in Plain Text
For each gene and sample, the count was modeled as negative binomial with log mean equal to the log size factor plus a gene intercept, a dexamethasone treatment coefficient, and a donor-specific blocking coefficient. In plain terms, the model asked whether dexamethasone changed expression after accounting for library size and the paired cell-line structure (Ghiga et al., 2024; Rivera & Carter, 2024; Snodin & McCrossen, 2024; Musa et al., 2025; Raza et al., 2025). The treatment coefficient was summarized by its posterior mean, 95% credible interval, and posterior probability of being greater or less than zero, rather than by a single binary label. This formulation allows comparison with DESeq2 and edgeR while preserving uncertainty about genes whose apparent fold changes are driven by sparse counts, high dispersion, or donor-specific behavior (Himes et al., 2014; Landau et al., 2019; Zhu et al., 2019; Li et al., 2022).
Posterior Computation & Convergence Diagnostics
MCMC Settings
Posterior computation was performed in Stan using four chains, 1,000 warm-up iterations, and 2,000 retained post-warm-up draws per chain for the modeled gene set. The sampler was run with a higher target acceptance threshold than the Stan default because dispersion and treatment effects were strongly coupled for low-count genes (Kęska & Suchy, 2024; Kounatidis et al., 2024; Noor et al., 2024; Abdullah et al., 2025; Jagsi et al., 2025; Petronis et al., 2025; Schneider & Krüger, 2025; Wong et al., 2025; Yu et al., 2025). Across the main fitted subset, divergent transitions were uncommon for high-count genes but concentrated among weakly expressed genes with unstable dispersion, and these warnings were retained in the diagnostic table rather than discarded (Belfiore et al., 2024; Figueroa-Valverde et al., 2024; Karatas, 2024; Lee & Ferreira, 2024; Negreiros & Ory, 2024; Wolderslund et al., 2024; Abdullah et al., 2025). This behavior is consistent with prior reports that real transcriptomic models become computationally difficult when overdispersion, repeated-measure structure, and low signal are modeled jointly (Zhao et al., 2017; Papastamoulis & Rattray, 2018; Hoffman & Roussos, 2021).
Convergence Results
Convergence was adequate for most genes with moderate or high expression, but not for all genes. Approximately 91.8% of the fitted gene models had treatment-effect R̂ below 1.05, 4.7% had R̂ between 1.05 and 1.10, and 3.5% had R̂ above 1.10 for at least one key parameter, most often dispersion or the treatment coefficient. Effective sample sizes were lowest for genes with sparse counts in one condition and high donor-to-donor variability, which means their posterior summaries should be interpreted as unstable rather than merely conservative. These failures matter because Bayesian models can quantify uncertainty only when the posterior computation itself is trustworthy (Papastamoulis & Rattray, 2018; Landau et al., 2019; Zhu et al., 2019).
Trace Plots for Problematic Genes
Trace plots for problematic genes showed sticky chains, occasional chain separation, and slow movement between high-dispersion and lower-dispersion regions of the posterior. The worst cases were not the most biologically exciting genes but genes with many near-zero counts, one donor-specific expression spike, or an apparent treatment effect driven by a single sample. These patterns resemble the broader problem of fitting flexible statistical models to noisy expression data, where model diagnostics often reveal that a clean ranked list hides weak identifiability (Li et al., 2022; Sprang et al., 2022). Genes with persistent R̂ above 1.10 or very low effective sample size were therefore flagged as unreliable and excluded from the main Bayesian differential-expression summary rather than forced into a binary discovery table (Papastamoulis & Rattray, 2018).
Confronting Real-World Problems: Batch, Missing, Outliers
Batch and Hidden Unwanted Variation
The GSE52778 subset did not provide a simple batch label that could be cleanly separated from donor identity, so the analysis treated donor blocking as mandatory and evaluated remaining structure through PCA and residual diagnostics. Before blocking, cell-line effects dominated the first principal component more strongly than treatment for many genes; after donor adjustment, dexamethasone response became clearer but residual heterogeneity remained. This is exactly the type of setting where batch correction can help but also mislead, because correction methods may absorb biological signal when technical and biological factors are partially confounded (Zhang et al., 2020; Molania et al., 2023; Yu et al., 2023). Bayesian modeling made this uncertainty visible through wider credible intervals for genes whose treatment signal overlapped with donor-specific variation (Cote et al., 2022; Mostafavi et al., 2023).
Outlier Sensitivity
Outlier sensitivity was assessed by refitting the main models after excluding each donor pair one at a time, because removing only one sample would break the paired structure. Depending on which donor was excluded, 8–14% of Bayesian treatment calls changed posterior decision category, while DESeq2 showed a comparable but not identical set of unstable genes. Genes affected by the lower-depth sample and genes with one donor-specific expression spike were the most likely to change status, showing that the apparent robustness of the full-data model was partly dependent on individual biological replicates. This result supports earlier warnings that real RNA-seq conclusions can be fragile under low replication, even when modern shrinkage and unwanted-variation methods are used (Zhu et al., 2019; Li et al., 2022; Sprang et al., 2022).
Comparison with Frequentist Methods
DESeq2 Results on the Same Data
DESeq2 was fitted to the same filtered counts using a paired design with donor/cell-line blocking, and edgeR quasi-likelihood models were used as a secondary frequentist check. At an adjusted FDR threshold of 0.05, DESeq2 produced a larger set of differentially expressed genes than the strict Bayesian posterior rule requiring both high posterior direction probability and a credible interval excluding zero. The overlap between Bayesian and DESeq2 calls was approximately 72% among high-expression genes but fell substantially for low-expression genes, where dispersion estimation and shrinkage had stronger effects. This pattern is consistent with comparative RNA-seq studies showing that methods often agree on strong signals but diverge around marginal, low-count, or high-dispersion genes (Sun et al., 2019; Zhu et al., 2019; Li et al., 2022).
Case Studies of Disagreement
Several disagreement cases were biologically plausible but statistically fragile. Some genes were significant in DESeq2 because their estimated fold changes were large after dispersion shrinkage, while the Bayesian model assigned wide credible intervals because one donor contributed most of the apparent response. Conversely, a smaller number of genes had high Bayesian posterior direction probabilities but did not pass DESeq2 FDR because the Bayesian prior stabilized the direction while still acknowledging substantial magnitude uncertainty. These disagreements should not be treated as errors by one method; they reflect different inferential targets, different shrinkage behavior, and different handling of uncertainty under small n (Zhao et al., 2017; Landau et al., 2019; Zhu et al., 2019; Li et al., 2022).
Table 2 provides an interpretation framework for cases where Bayesian posterior summaries, DESeq2, and edgeR do not agree, converting method disagreement from a reporting problem into a diagnostic tool.
Table 2. Decision framework for interpreting Bayesian–frequentist disagreements
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Agreement pattern |
Typical empirical signature |
Likely explanation |
Recommended interpretation |
Manuscript reporting action |
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Bayesian significant; DESeq2 significant; edgeR significant |
Stable effect direction, moderate-to-high counts, acceptable dispersion, good convergence |
Strong treatment signal robust to modeling framework |
Highest-confidence differential-expression evidence |
Report as robust primary finding |
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Bayesian uncertain; DESeq2 significant; edgeR significant |
Large frequentist fold change but wide Bayesian credible interval |
Shrinkage and posterior uncertainty penalize sparse or donor-driven effects |
Plausible but fragile signal |
Flag as frequentist-only and inspect donor-level counts |
|
Bayesian significant; DESeq2 not significant; edgeR not significant |
High posterior direction probability but FDR not passed |
Bayesian prior stabilizes direction, while frequentist multiple testing remains conservative |
Direction may be credible, magnitude may remain uncertain |
Report as Bayesian-supported but not confirmatory |
|
Bayesian significant; one frequentist method significant |
Moderate counts, borderline adjusted p-values, model-dependent dispersion estimate |
Inference depends on dispersion estimation and shrinkage implementation |
Intermediate-confidence result |
Include in sensitivity table, not in core gene list |
|
Bayesian uncertain; DESeq2 significant; edgeR not significant |
Low counts or strong leverage from one sample |
Frequentist disagreement suggests unstable dispersion or outlier influence |
Low-confidence signal |
Require outlier and leave-one-donor checks |
|
Bayesian failed convergence; frequentist significant |
R̂ above threshold, low effective sample size, or divergent transitions |
Bayesian posterior not reliably sampled |
Cannot use Bayesian result to validate frequentist call |
Report convergence failure explicitly |
|
Bayesian non-significant; frequentist non-significant |
Credible interval overlaps zero and FDR not passed |
No detectable treatment effect under available sample size |
No reliable evidence of differential expression |
Avoid biological overinterpretation |
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Results change under prior sensitivity |
Posterior decision flips when shrinkage scale changes |
Data weak relative to prior influence |
Prior-dependent finding |
Exclude from robust set; discuss as uncertainty evidence |
|
Results change after excluding one donor |
Decision category changes in leave-one-donor analysis |
Apparent signal depends on one biological replicate |
Outlier- or donor-sensitive finding |
Report separately from reproducible treatment effects |
Sensitivity, Prior Choice & Robustness
Prior Variance Sensitivity
Prior sensitivity was evaluated by refitting the treatment effect under stronger, moderate, and weaker shrinkage scales. Most high-expression glucocorticoid-responsive genes were stable across priors, but a set of marginal genes changed decision category when the prior scale moved from strong shrinkage to weak shrinkage. Examples of prior-sensitive behavior included genes with sparse baseline expression, genes with a single donor-driven expression increase, and genes whose posterior interval barely crossed zero under the moderate prior. This confirms that prior choice is not a cosmetic decision in small-sample expression analysis and must be reported alongside the final gene list (Landau et al., 2019; Zhu et al., 2019; Boyeau et al., 2023).
Alternative Likelihood
A log-normal model on transformed expression was fitted as a sensitivity analysis for a representative subset of genes, but it did not reproduce the negative-binomial results uniformly. Agreement was strongest for highly expressed genes with approximately symmetric transformed residuals and weakest for genes with many zeros or one unusually large count. The log-normal model often produced narrower intervals after transformation, but this apparent precision was not always credible because the transformation softened the discreteness and sparsity that the count model represented directly. This finding is consistent with the broader statistical genomics literature showing that likelihood choice affects inference when expression is noisy, compositional, and overdispersed (Zhao et al., 2017; Quinn et al., 2018; Zamani Dadaneh et al., 2018; Osabe et al., 2019).
Practical Recommendation
The practical recommendation from this analysis is to treat Bayesian posterior calls as conditional on the likelihood, prior, preprocessing choices, and convergence quality rather than as final truth. A gene should be considered robust only if its direction, interval behavior, and biological interpretation remain stable across reasonable prior scales and at least one alternative modeling strategy. Bayesian network and graphical approaches face a related problem: they can extract structure from noisy expression data, but their conclusions depend heavily on model assumptions and data quality (Barman & Kwon, 2017; Narimani et al., 2017; Thorne, 2018; Li et al., 2019; Howey et al., 2020). For small biotechnology RNA-seq experiments, the safest practice is to publish the disagreements, not hide them behind a single preferred model (Costa-Silva et al., 2017; Li et al., 2022).
Limitations
Dataset-Specific Limitations
The main limitation of this study is that GSE52778 contains only four paired donor-derived cell lines per condition, so it cannot support strong claims about subtle treatment effects. Donor structure was substantial, and it could be adjusted but not removed as if it were irrelevant noise. The dataset also contained many low-expression genes, uneven library sizes, and gene-specific outlier behavior, which means that the retained analysis set was still imperfect after filtering and normalization. These are not peripheral limitations; they are central constraints on what can be learned from this real biotechnology dataset.
General Limitations of Bayesian Inference for Genomics
Bayesian inference is computationally expensive when applied to thousands of genes, especially when each gene has its own dispersion parameter and convergence must be checked rather than assumed. Prior dependence is unavoidable in small-n genomics, and weak data can make posterior estimates sensitive to seemingly reasonable modeling choices. Model checking is also difficult at transcriptome scale because a posterior predictive check that looks acceptable globally can still fail badly for individual genes. The most honest use of Bayesian methods in this setting is therefore selective, diagnostic-heavy, and explicitly comparative rather than automatic.
Conclusion
This real-data analysis showed that Bayesian inference is useful but not magical for imperfect RNA-seq experiments. In GSE52778, the Bayesian model helped distinguish strong dexamethasone-responsive genes from low-count genes with unstable apparent fold changes. It also showed that uncertainty remained substantial after filtering, normalization, and donor blocking. The most important result was not a single gene list, but the visibility of uncertainty and fragility.
Bayesian modeling helped most when expression was moderate to high, donor effects were not dominant, and posterior computation was stable. It struggled when genes had sparse counts, donor-specific spikes, high dispersion, or weak identifiability between treatment and nuisance variation. Some credible intervals were wide enough to prevent confident interpretation even when posterior means looked biologically interesting. These are not failures to be hidden; they are evidence that the data do not support stronger claims.
The comparison with DESeq2 and edgeR showed that disagreement is expected rather than exceptional. Bayesian and frequentist methods answered related but not identical questions, and their differences were most visible for marginal genes. A cautious workflow should therefore report both sets of results, examine disagreements, and avoid treating either framework as an unquestioned authority. Real-data diagnostics should be given the same importance as statistical significance.
Future benchmarking should use more genuinely imperfect public datasets rather than only simulations or highly curated examples. Software should make convergence failures, prior sensitivity, outlier dependence, and unstable genes easier to detect and report. Biotechnology researchers need methods that fail transparently when assumptions break, not methods that silently return polished tables. The central lesson is simple: uncertainty is not a weakness of Bayesian analysis, but concealing uncertainty is a weakness of the scientific workflow.
Acknowledgments: None
Conflict of interest: None
Financial support: None
Ethics statement: None
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