A Configuration-Driven Python Pipeline for Reproducible Functional Brain Network Analysis: Internal Validation on a Public fMRI Dataset
Sara Pradhan Mountain View High School, Mountain View, California pradhan.sara@gmail.com
Background: Functional magnetic resonance imaging (fMRI) lets researchers estimate coordinated activity across brain regions, but turning raw scanner data into interpretable network metrics requires a chain of analysis decisions — confound regression, parcellation, connectivity estimation, statistical testing — each of which can change the result. This analytical flexibility is a particular obstacle for student investigators, who often assemble custom scripts with little guidance on which choices matter or how to document them.
Question: Can a modular, YAML-configured Python pipeline recover established features of large-scale brain organization and produce internally reproducible outputs when applied to a publicly available fMRI dataset?
Findings: I validated fmri-pipeline on a five-run subset of OpenNeuro ds007318 (3 participants, working-memory task fMRI treated as pseudo-resting-state). The pipeline recovered canonical network organization, confirmed by a permutation test (within-network r̄ = 0.43 vs. between-network r̄ = 0.21, gap = 0.22, p < 0.001) and a corroborating edge-level analysis using the same edges and network labels (Spearman rho = 0.32, 95% CI [0.31, 0.34]). Regional homogeneity profiles were highly stable within subjects across runs (within r̄ = 0.97 vs. between r̄ = 0.51, from 2 within-subject run pairs). Static functional connectivity showed a within-subject advantage (within r̄ = 0.71 vs. between r̄ = 0.43 across only 2 within-subject run pairs; bootstrap 95% CI on the gap [0.22, 0.35]). A parcellated temporal-ICA proxy was stable across random seeds (20/20 components, mean |r| = 0.88), though stability across leave-one-run-out subsets was substantially weaker (mean |r| = 0.411, descriptive only given n ≤ 3 subsets). In a sensitivity analysis, global signal regression (GSR) was the only tested parameter that substantially altered connectivity estimates (Spearman ρ = 0.862 vs. baseline); all other tested parameters produced near-identical outputs (ρ ≥ 0.99). All statistics above reflect the GSR-on baseline configuration.
Significance: This is an engineering and reproducibility validation, not a biological-discovery study. On a small public dataset, fmri-pipeline produced internally consistent, biologically plausible outputs with complete analytical transparency through a single plain-text configuration file and an automatic validation scorecard, lowering the barrier to reproducible fMRI analysis for student investigators.
My interest in brain networks began with watching a family member live with a serious neurological illness, and with how hard it was for the people around her to recognize what was happening until a crisis made it impossible to miss. I did not set out to study her condition, and this project does not: the dataset and sample size here cannot support clinical claims of any kind, and I make none. What stayed with me was a simpler question. When a brain-imaging analysis produces a number, how do we know that number reflects the brain and not just the choices we made along the way? That question is what led me to build and test a transparent, reproducible analysis pipeline rather than simply run an existing one.
Functional MRI allows researchers to estimate coordinated activity across brain regions, but the path from BOLD images to interpretable network results runs through many analysis choices. Reasonable teams can make different decisions about confound regression, motion scrubbing, spatial smoothing, atlas resolution, and statistical modeling, and the "many analysts" literature has shown that this flexibility can produce substantially different conclusions even when teams start from the same dataset [1]. For a student researcher the problem is sharper: a script can run cleanly while still producing outputs that are undocumented, sensitive to arbitrary parameter choices, or hard to reproduce. This raises a concrete, testable question — can a pipeline built around transparent parameterization and built-in internal-validity checks recover established features of large-scale brain organization and produce outputs that are stable across runs and analytical choices?
Several open-source tools already address parts of this workflow. fMRIPrep standardizes functional preprocessing [2], nilearn provides connectivity estimation in Python [3], and BrainIAK offers advanced methods such as intersubject correlation [4]. Integrated environments such as the CONN toolbox [5] and XCP-D [6] provide broader end-to-end processing. These tools are valuable, but they do not remove the need for a project-specific layer that records every parameter choice, links the analysis modules together, and checks whether outputs pass basic internal-validity tests before biological interpretation — and none provides a built-in scorecard designed for a student to confirm pipeline validity before drawing conclusions.
I developed fmri-pipeline to fill that gap. All parameters live in a single YAML file, analysis modules run in dependency order, and a built-in reproducibility suite systematically tests whether outputs meet expected internal-consistency criteria. By "multi-scale" I mean analyses spanning the local (voxelwise regional homogeneity) and large-scale network (ROI-level functional connectivity) levels within one workflow. The design goal is not to replace mature neuroimaging packages but to make a complete, student-accessible workflow transparent and self-checking. I tested three hypotheses: (1) the pipeline recovers canonical network organization, measured as stronger within-network than between-network functional connectivity; (2) local and network-level outputs show higher within-subject than between-subject similarity across repeated runs; and (3) static FC estimates are mostly stable across common parameter changes, except for known high-impact choices such as global signal regression.
I used OpenNeuro dataset ds007318, a BIDS-formatted fMRI dataset for a working-memory "removal" task with encoding, maintenance, removal, and rest trial types, as defined in the dataset's task-removal_events.json file [7].
The dataset's own documentation is internally inconsistent about sample size: its README states "Subjects: 43," while the OpenNeuro landing-page metadata panel separately lists 42 participants. This manuscript follows the README and participants.tsv, which are the authoritative BIDS sources, and reports 43 as the repository size; this is a discrepancy in the source repository, not an error introduced by this analysis. This validation used the first three participants and a fixed set of five runs selected for usable coverage during preprocessing:
| Participant | Age | Sex | Group label (participants.tsv) | Runs analyzed |
|---|---|---|---|---|
| sub-01 | 23 | Female | patient | ses-1, ses-2 |
| sub-02 | 28 | Male | patient | ses-1 |
| sub-03 | 17 | Female | patient | ses-1, ses-2 |
The analyzed sample is therefore N = 3 participants and 5 BOLD runs (only a single run from sub-02 was included). This is adequate for a pipeline-validation exercise but not for population-level inference. All three analyzed participants are labeled as patients, so no diagnostic group comparison was performed. Because the validation focuses on within-subject reproducibility and canonical network structure — neither of which requires a control group — the absence of a healthy comparison group does not affect the conclusions reported here, but it does mean these results should not be assumed to generalize to healthy or true resting-state data.
The pipeline used fMRIPrep derivatives [2] as inputs (MNI152NLin2009cAsym space, 2 mm isotropic voxels). The functional data were acquired on a 3 T United Imaging (UIH) scanner using a 2D EPI sequence (TR = 2.0 s, TE = 30 ms, flip angle = 90°, 2 mm slice thickness, 75 slices, phase-encoding j−), with values read directly from the BIDS JSON sidecars. The task BOLD data were treated as pseudo-resting-state: no task-evoked regressors were modeled, and all connectivity analyses (FC, ReHo, ICA proxy) were applied as resting-state-style analyses. This is a reasonable choice for engineering validation but is not equivalent to analyzing true resting-state data. I treated this as a deliberate trade-off: these task runs were the data with usable coverage available to me, and the validation targets here — within- versus between-network separation and within-subject stability — do not depend on the rest-versus-task distinction, so I judged the substitution acceptable for an engineering validation while flagging it as a limit on generalization.
All data were obtained from the public OpenNeuro repository (OpenNeuro ds007318, snapshot v1.0.0, downloaded February 2026; https://openneuro.org/datasets/ds007318/versions/1.0.0), distributed under a CC0 license. This work is a secondary analysis of a publicly available, fully de-identified dataset and involved no new data collection or contact with participants; secondary use of openly licensed, de-identified data of this kind does not constitute human-subjects research requiring new ethical approval.
fmri-pipeline accepts fMRIPrep derivatives in BIDS format and is controlled entirely by a single YAML configuration file. The modules exercised in this validation were: (1) preprocessing quality-control checks and confound regression; (2) regional homogeneity (ReHo), computed voxelwise as Kendall's coefficient of concordance over each voxel's 26-neighbor cluster and summarized to ROI level using the atlas parcellation [10]; (3) static functional connectivity (FC), estimated as pairwise Pearson correlations followed by Fisher-z transformation across the Schaefer-200 atlas (200 ROIs, 7-network assignment, 2018 release, applied in MNI152NLin2009cAsym space) [8,9]; (4) exploratory dynamic FC using a sliding-window approach across multiple window lengths [11]; (5) a parcellated temporal-ICA stability check [12,13]; (6) graph-metric summaries of thresholded FC matrices [14]; and (7) a sensitivity-analysis module that systematically varies parameters and computes pairwise Spearman correlations between the resulting connectivity vectors. The pipeline additionally implements intersubject correlation [4] and group-level mass-univariate OLS with Benjamini-Hochberg FDR correction [17]; these modules were not exercised in this single-dataset, single-group validation and are therefore not reported in the Results.
Following fMRIPrep preprocessing, confound regression used six rigid-body motion parameters (three translations, three rotations) and their temporal derivatives (12 motion regressors), mean white-matter signal, and mean CSF signal. Volumes with framewise displacement (FD) exceeding 0.5 mm were flagged and excluded from downstream statistical operations via NaN masking. Cleaned BOLD timeseries were bandpass-filtered at 0.01–0.10 Hz with a zero-phase Butterworth filter and spatially smoothed with a 6 mm FWHM Gaussian kernel before connectivity estimation (baseline condition). For the global signal regression (GSR) sensitivity condition, a whole-brain mean BOLD regressor was additionally appended to the confound matrix. GSR was treated as a high-impact parameter because prior work shows it can substantially change FC estimates and network topology [15,16].
Baseline note: all within- versus between-network and reproducibility statistics reported in the Results (Table 2) were computed under this GSR-on baseline configuration. Because the sensitivity analysis below shows GSR is the single parameter that substantially alters connectivity estimates (ρ = 0.862 relative to GSR-off), the specific gap magnitudes reported here should not be assumed to hold under GSR-off preprocessing; GSR status should be matched whenever these results are compared against other pipelines or datasets.
For each run the pipeline extracted Schaefer-200 ROI timeseries and computed a 200 × 200 FC matrix; the upper triangle contained 19,900 unique ROI-pair values before masking invalid edges. One ROI in sub-03 ses-2 had a zero-variance timeseries from incomplete brain coverage and was excluded via NaN masking; all statistics used only jointly valid edges. To test canonical organization, edges were divided into within-network (both ROIs in the same Yeo/Schaefer network) and between-network pairs, and mean within- vs. between-network FC was compared with a permutation test (1,000 shuffles of the network-label vector, two-tailed; p lower-bounded at 1/1,000). As a complementary, effect-size-oriented view of the same contrast — not an independent check, since it uses the identical edges and network labels — I also computed the Spearman correlation between Fisher-z edge values and a same-network membership indicator (3,093 within-network and 16,807 between-network edges).
FC reproducibility. For each subject I computed the upper-triangle FC vector per run, then within-subject run-pair correlations and between-subject cross-run correlations (Pearson r on valid edges, pairwise NaN masking). I compared within- to between-subject similarity with a one-sided Wilcoxon rank-sum test and a bootstrap 95% CI (B = 1,000 run-level resamples) on the within-minus-between gap. Because only sub-01 and sub-03 contributed repeated runs, this run-pair comparison was restricted to those two subjects, yielding 2 within-subject and 4 between-subject run pairs (sub-02's single run cannot form a within-subject pair and is excluded from this test, though it does enter the three-subject ReHo comparison below). With only 2 within-subject and 4 between-subject pairs, this test has theoretical power below 17% even for large true effects, so the bootstrap CI is treated as suggestive, not confirmatory, evidence throughout this manuscript.
ReHo stability. Per run, the ReHo map was computed from cleaned BOLD and summarized to ROI level using the Schaefer-200 atlas; I compared within- to between-subject run-to-run Pearson r using the same bootstrap procedure (2 within-subject pairs: sub-01 ses-1×ses-2 and sub-03 ses-1×ses-2; 8 between-subject pairs across all three subjects). An early pipeline run wrote empty NIfTI stubs rather than valid ReHo maps because of a bug in the output-writing module (corrected before the archived release, v1.0.1); I recomputed ReHo from cleaned BOLD using a brain mask derived from temporal variance, which is methodologically equivalent to a gray-matter mask for ROI-level extraction.
ICA stability. I ran temporal FastICA [12] on the group-averaged Schaefer-200 ROI timeseries using 5 random seeds (k = 20) and matched components across seeds with the Hungarian algorithm [13] on the absolute-correlation matrix; a component was robust if |r| ≥ 0.70 against all counterparts. This is a parcellated temporal-ICA proxy and does not directly validate the pipeline's spatial-ICA module. A leave-one-run-out cross-validation yielded only 3 run subsets and is reported descriptively only.
Graph metric stability. From the group-average FC matrix I computed modularity (Louvain), global efficiency, and clustering coefficient at density thresholds 0.10, 0.15, and 0.20, with bootstrap resampling (B = 500) for 95% CIs and the coefficient of variation.
Dynamic FC sensitivity. I computed sliding-window FC variability (SD of the upper-triangle vector over time) at window lengths 20, 30, and 40 TRs, used k-means (k = 4, k-means++, 10 restarts) to assign states within each condition, and computed the Adjusted Rand Index (ARI) between conditions.
I tested output stability across 11 conditions spanning 5 dimensions: GSR (on/off), atlas resolution (Schaefer-100/200/400), dynamic-FC window length (20/30/45/60 TRs; this sweep uses a wider window grid than the 20/30/40-TR reproducibility analysis above), motion scrubbing threshold (FD 0.3/0.5/0.9 mm), and smoothing kernel (4/6/8 mm FWHM). Baseline was Schaefer-200, GSR on, FD 0.5 mm, 6 mm smoothing, 30-TR window. For each condition I compared the static FC upper-triangle vector to baseline with Spearman correlation. Note that static FC does not depend on the dynamic-FC window length, so the window-length conditions are identical to baseline (ρ = 1.00) by construction and are reported only for completeness; the atlas-resolution conditions produce FC vectors of a different length (Schaefer-100/400 have different ROI counts than the Schaefer-200 baseline) and are therefore not directly edge-comparable to baseline — no Spearman ρ was computed for these conditions, and Figure 2 marks them "N/T" (not tested) rather than showing a numeric value. The smoothing conditions apply the kernel to the cleaned BOLD before ROI extraction. The figure reports the 9 conditions with atlas resolution held constant (so edges are directly comparable); all 11 are discussed in the text, with the per-condition similarity table (recommended_defaults.csv) and the full pairwise similarity matrix (stability_matrix_static_fc.npy with stability_labels.csv) provided in the archived repository.
fmri-pipeline is implemented in Python (≥ 3.8) and depends on numpy, scipy, pandas, nilearn, nibabel, statsmodels, scikit-learn, and pyyaml. Group-level testing uses mass-univariate OLS with Benjamini-Hochberg FDR correction [17]. All stochastic operations used deterministic seeds set in the configuration file. The test suite validates core computations on synthetic data and requires no neuroimaging files to run.
All five runs passed the predefined motion-quality criteria (mean FD < 0.5 mm, percent scrubbed < 20%). Mean FD ranged from 0.101 to 0.150 mm, and only sub-02 ses-1 had any scrubbed volumes (≈1.2%) at the FD > 0.5 mm threshold (Table 1). DVARS ranged from 3.68 to 4.41 across runs. One ROI in sub-03 ses-2 had a zero-variance timeseries and was excluded via NaN masking.
Table 1. Run-level motion quality-control summary at the FD 0.5 mm scrubbing threshold. All runs passed pipeline exclusion criteria.
| Run | Mean FD (mm) | Median FD (mm) | Scrubbed (%) | DVARS |
|---|---|---|---|---|
| sub-01, ses-1 | 0.105 | 0.096 | 0.00 | 3.73 |
| sub-01, ses-2 | 0.101 | 0.095 | 0.00 | 3.68 |
| sub-02, ses-1 | 0.144 | 0.119 | 1.18 | 4.41 |
| sub-03, ses-1 | 0.122 | 0.103 | 0.00 | 3.85 |
| sub-03, ses-2 | 0.150 | 0.121 | 0.00 | 3.95 |
The strongest validation result was the recovery of canonical large-scale network organization. Mean within-network FC (r̄ = 0.43) substantially exceeded mean between-network FC (r̄ = 0.21) across all seven canonical Yeo networks, a gap of 0.22 (p < 0.001, permutation test, 1,000 shuffles; p at the minimum resolvable value of 1/1,000).
Spatial autocorrelation caveat: the Schaefer-200 parcellation assigns ROIs by functional similarity, but Yeo-network labels remain spatially contiguous to a meaningful degree, and the label-shuffling permutation test used here does not preserve or destroy spatial structure. It therefore cannot, by itself, rule out a contribution from spatial autocorrelation (e.g., smoothing-induced proximity correlations) to the observed within-network effect. A spatially-constrained ("spin test") permutation, which preserves the geometry of the cortical surface while shuffling network identity, would be needed to more rigorously isolate the network-driven component of this effect; that test was not run for this validation and is flagged as a priority follow-up rather than a settled conclusion.
As an effect-size restatement of the same within- versus between-network contrast — using the identical edges and network labels, not an independent check — the Spearman correlation between Fisher-z edge values and same-network membership was rho = 0.32 (95% CI [0.31, 0.34]), confirming that same-network ROI pairs are systematically more connected than cross-network pairs across the full edge distribution.
Within-network FC was highest for the Visual (Fisher-z M = 0.72) and Dorsal Attention (M = 0.49) networks, consistent with strong local synchrony commonly reported in unimodal sensory and attention systems, followed by Somatomotor (M = 0.45), Salience/Ventral Attention (M = 0.39), Default Mode (M = 0.35), and Frontoparietal (M = 0.33); the Limbic network was weakest (M = 0.17), consistent with the lower BOLD signal-to-noise ratio typically reported in limbic regions. No specific canonical rank ordering was pre-registered for this comparison, so this ordering is reported descriptively rather than as a validated match to an external benchmark. Because the data are task fMRI treated as pseudo-resting-state, this is best read as evidence of biologically plausible network structure rather than proof that task-state FC matches resting-state architecture (Figure 1).
![Figure 1. Group-average functional connectivity matrix (N = 3 subjects, 5 runs, ds007318). Panel A: 200×200 FC heatmap ordered by Yeo-7 network membership (Schaefer-200 parcellation, Fisher-z scale, clipped to [−0.5, 1.5]); axis colour bars denote network identity. The block-diagonal structure reflects canonical large-scale network organization. Panel B: Mean within-network FC per canonical network; error bars show standard deviation across the 5 runs. All networks exceed the between-network mean (dashed line; M = 0.21). Vis = Visual; SomMot = Somatomotor; DorsAttn = Dorsal Attention; SalVentAttn = Salience/Ventral Attention; Cont = Frontoparietal/Control; Limbic = Limbic; DMN = Default Mode.](/sarapradhan/biomed-research/blob/main/figures/fc_matrix_canonical.png)
Table 2 summarizes the reproducibility analyses, described below in order of evidential strength.
Table 2. Validation scorecard for fmri-pipeline on OpenNeuro ds007318 (N = 3 subjects, 5 runs). Seed stability and cross-run stability of the temporal-ICA proxy are reported as separate rows so a strong seed result cannot mask a weaker cross-run result. Rows marked "suggestive" rest on bootstrap CIs built from only 2 within-subject pairs and should not be read as precise interval estimates. The FC fingerprint result (rho = 0.32 [0.31, 0.34]) is reported in the text above. CI = bootstrap 95% confidence interval (B = 1,000 run-level resamples). n/a = not assessable at this sample size.
| Validation dimension | Metric | Result | CI (gap) | Status |
|---|---|---|---|---|
| Static FC plausibility | Canonical network organization | within r̄ = 0.43, between r̄ = 0.21, gap = 0.22, p < 0.001 | — | ✓ |
| ReHo stability | Cross-run spatial similarity (2 within / 8 between pairs) | within r̄ = 0.97, between r̄ = 0.51 | [0.436, 0.480] | ✓ (suggestive, n=2) |
| ICA seed stability (temporal proxy) | Component recovery across seeds | 20/20 robust, mean |r| = 0.88 | — | ✓ (seed only) |
| ICA cross-run stability (LORO-CV) | Component recovery across run subsets | mean |r| = 0.411 (3 subsets) | — | ✗ Fails |r| ≥ 0.70 |
| FC reproducibility | Within- vs. between-subject (2 within / 4 between pairs) | within r̄ = 0.71, between r̄ = 0.43, p = 0.067 | [0.217, 0.348] | ✓ (suggestive, n=2) |
| Graph metric stability | Bootstrap CI on modularity | Q = 0.447, 95% CI [0.391, 0.503], CV = 17% | — | ✓ |
| Dynamic FC robustness | Multi-window ARI | ARI 0.42–0.57 | — | n/a (exploratory) |
ReHo stability was the strongest reproducibility result. Within-subject run-to-run Pearson r for ROI ReHo profiles was 0.97 versus 0.51 between subjects (2 within-subject pairs vs. 8 between-subject pairs; gap = 0.455, 95% CI [0.436, 0.480]). The near-perfect within-subject similarity indicates the ReHo spatial pattern is highly consistent across runs, and the large gap shows individual differences are preserved. Standardizing this gap yields a numerically enormous Cohen's d (≈31), but at N = 3 that value is an artifact of near-ceiling within-subject similarity rather than a meaningful reliability estimate, so I report the raw within- and between-subject means, the pair counts, and the bootstrap CI as the interpretable quantities — read as suggestive given the very small number of within-subject pairs, not as a precise population estimate.
ICA stability across random seeds was strong: all 20 components were robustly recovered (|r| ≥ 0.70) across all 5 seeds, mean |r| = 0.88, indicating the temporal decomposition is not sensitive to initialization. This validates seed stability of the parcellated temporal-ICA proxy only, not the spatial-ICA module. The LORO-CV (3 run subsets) told a different story: mean |r| = 0.411, well below the 0.70 robustness threshold used for seed stability, consistent with the known instability of temporal ICA on very small datasets. Because these two tests probe different kinds of robustness, Table 2 reports them as separate scorecard rows — seed stability passes, cross-run (LORO-CV) stability does not — so the strong seed result does not mask the weaker cross-run result.
FC reproducibility showed a consistent within-subject advantage: within-subject run-pair FC correlation r̄ = 0.71 (n = 2 pairs) versus between-subject r̄ = 0.43 (n = 4 pairs), a gap of 0.28. The bootstrap 95% CI on the gap [0.217, 0.348] excludes zero. The Wilcoxon rank-sum test did not reach significance (p = 0.067), but with only 2 within-subject pairs it is severely underpowered. Given that the bootstrap CI itself rests on only 2 within-subject pairs, it is offered here as supporting, not definitive, evidence of a within-subject advantage.
Graph metric stability was adequate. Bootstrap resampling (B = 500) of modularity at density 0.15 gave Q = 0.447 (95% CI [0.391, 0.503], CV = 17%). No published consensus CV threshold exists for this context; 17% is reported descriptively. The observed Q falls within the range commonly reported for resting-state networks at comparable atlas resolutions [14], providing an external anchor for the observed network separation.
Global signal regression was the only parameter that substantially altered connectivity estimates (Spearman ρ = 0.862 relative to baseline), consistent with the established literature on GSR's effect on FC topology [15,16]. Of the parameters actually tested against a comparable baseline, all others produced near-identical static FC outputs when atlas resolution was held constant: smoothing-kernel variations were very close to baseline (4 mm: ρ = 0.997; 8 mm: ρ = 0.997), and scrubbing-threshold variations remained very high (FD 0.3 mm: ρ = 0.991; FD 0.9 mm: ρ = 0.997). Window-length variations are identical to baseline by construction (ρ = 1.00, since static FC does not depend on the dynamic-FC window) and atlas-resolution conditions were not edge-comparable to baseline, so neither is treated as a genuine robustness test (see Figure 2 caption). With the exception of GSR, the pipeline's static FC outputs were robust (ρ ≥ 0.99) across the preprocessing parameters that could be directly tested against baseline in this low-motion subset (Figure 2).
Dynamic FC variability (upper-triangle SD over time) decreased monotonically with window size (W = 20 TR: 0.409; 30 TR: 0.308; 40 TR: 0.253), as expected from the averaging properties of longer windows. State-assignment consistency across window lengths was moderate (ARI 0.42–0.57), reflecting the dependence of sliding-window clustering on temporal resolution. Dynamic FC outputs are included for exploratory characterization only and are not the basis for state-based inference at this sample size.
fmri-pipeline produced coherent, internally reproducible functional-network outputs from a small public fMRI dataset without modification of source code — only the YAML configuration was changed to point at the new data. The strongest result — recovery of canonical network organization confirmed by a permutation test (p < 0.001) and corroborated by an effect-size restatement of the same contrast (rho = 0.32) — establishes that the pipeline's FC matrices are biologically plausible: within-network connections are systematically stronger than between-network connections across all seven Yeo networks, though spatial autocorrelation has not been formally ruled out as a partial contributor (see Results). This is the expected signature of large-scale brain modularity [14], and its recovery is consistent with correct functioning of the atlas-parcellation and connectivity-estimation steps.
The reproducibility analyses collectively indicate the outputs are not arbitrary, though the within-subject sample size (2 repeated-run pairs) limits how strongly this can be stated. ReHo profiles were nearly perfectly reproduced within subjects across runs; static FC showed a within-subject advantage with a bootstrap CI that excludes zero, treated here as suggestive rather than confirmatory; and the parcellated temporal-ICA proxy was stable across seeds but not across leave-one-run-out subsets. The paper's strongest defensible claim is that the pipeline produced biologically plausible and internally reproducible outputs on a small public subset, supporting its use as a transparent validation workflow for future, larger analyses. The current data do not support claims of disease-biomarker discovery, schizophrenia-related dysconnectivity, or general test-retest reliability, and I do not make them.
The network-anchor test functions like a diagnostic check on the whole FC workflow. If the atlas labels, timeseries extraction, confound regression, or FC computation were seriously misconfigured, the matrix would be unlikely to show stronger within- than between-network connectivity. Recovering the expected pattern does not prove every module is correct, but it provides meaningful evidence that the core workflow is functioning sensibly — much as checking that a new thermometer reads a plausible room temperature before an experiment does not answer the scientific question but does rule out using a broken instrument.
The sensitivity analysis directly addresses hypothesis 3 and supports it for every parameter except GSR. Crucially, the pipeline does not eliminate analytical variability — it documents it. The GSR result (ρ = 0.86) shows that a single parameter can substantially change connectivity topology; the pipeline's contribution is to make that choice explicit, version-controlled, and reproducible in a plain-text file rather than buried in custom scripts. Practically, minor differences in scrubbing threshold or smoothing kernel are unlikely to alter static FC conclusions in low-motion data, whereas GSR usage should be matched whenever cross-study comparisons are made and treated as a pre-specified decision rather than a casual toggle — and, as noted in Methods, every gap statistic reported in this paper is itself a GSR-on number.
Several limitations constrain these conclusions. First, the validation sample was very small — three participants and five runs, with only two participants contributing repeated runs — which severely limits power for between-subject comparisons and means the bootstrap CIs on reproducibility gaps rest on as few as 2 within-subject pairs. Second, all analyzed participants were labeled as patients, so no healthy-control comparison was possible. Third, the data were acquired during a working-memory task and treated as pseudo-resting-state; this is useful for engineering validation but is not equivalent to true resting-state data. Fourth, the ICA stability analysis used a parcellated temporal-ICA proxy that was stable across random seeds but not across leave-one-run-out subsets, and does not validate the spatial-ICA module. Fifth, dynamic FC analyses are exploratory at this sample size. Sixth, the ReHo recomputation used a temporal-variance brain mask rather than a gray-matter segmentation mask; for ROI-level extraction this distinction is negligible but is noted for completeness. Seventh, the permutation test used to establish canonical network organization does not control for spatial autocorrelation and cannot, on its own, rule out a contribution from spatial proximity to the within-network effect.
fmri-pipeline is designed to lower the barrier to reproducible fMRI analysis for student investigators. Because all analytical decisions live in a version-controlled plain-text file, the methodology can be shared alongside results, and the automatic reproducibility scorecard lets a student check internal consistency before drawing biological conclusions. The clear next step is to run the same validation framework on a larger dataset with more repeated sessions — ideally ≥ 20 participants, ≥ 2 usable runs each, a true resting-state or naturalistic-viewing design, direct validation of the spatial-ICA module, a spatially-constrained (spin-test) permutation for the network-anchor result, and pre-registered settings for GSR, scrubbing, smoothing, and atlas resolution. A configuration for a naturalistic-viewing dataset has been prepared, and running it is the highest-impact way to move this work from an engineering-validation paper toward a stronger reproducibility methods paper.
On this small public subset, fmri-pipeline recovered the canonical within- versus between-network connectivity gap (permutation p < 0.001, with spatial autocorrelation not yet ruled out), reproduced ROI-level ReHo profiles within subjects (r̄ = 0.97, from 2 within-subject pairs), showed a within-subject FC advantage whose bootstrap CI excluded zero (also from 2 within-subject pairs), and isolated global signal regression as the single high-impact preprocessing parameter among those tested. The manuscript should be read as a reproducible pipeline-validation study rather than a biological-discovery study. With larger repeated-session validation and public archiving of all code and result files, this work could provide a useful, student-accessible framework for transparent fMRI network analysis.
The input fMRI dataset is publicly available as OpenNeuro ds007318 (https://openneuro.org/datasets/ds007318) [7], distributed under a CC0 license. The source code for fmri-pipeline is openly available at https://github.com/sarapradhan/biomed-research (release v1.0.1, MIT License) and is archived at https://doi.org/10.5281/zenodo.20280072. The pipeline configuration files (config/), the per-module reproducibility outputs and validation scorecard (reports/reproducibility/, including scorecard.csv, reho_summary.csv, fc_within_vs_between.csv, network_anchor_summary.csv, and graph_metrics_bootstrap.csv), and the combined sensitivity figure (updated per the Figure 2 revision described above) used to generate the reported results are included in the archived repository.
This work was made possible by the open-source neuroimaging community. The author thanks the developers of fMRIPrep, nilearn, nibabel, scipy, scikit-learn, statsmodels, and the Schaefer-200 atlas, whose freely available tools form the foundation of fmri-pipeline. The author also thanks the creators of OpenNeuro and the team that collected and shared dataset ds007318, as well as the study participants whose data made this validation possible.
The author thanks Arefeh Sherafati, Research Scientist at St. Jude Children's Research Hospital, for guidance and feedback throughout this project.
The author used generative AI (Anthropic's Claude) as a writing and coding assistant during manuscript preparation and software development. All scientific content, analyses, interpretations, and final code were designed, reviewed, and verified by the author, who takes full responsibility for the work.
The author declares no competing interests.
This research received no external funding.
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