Reviewer3 (AI review)

October 12, 2026

AI Review (reviewer3.com)

Comments (5)

1. Inaccurate statement regarding type-aware benchmark rank — Minor

Under the type-aware regime, SBMEX remains superior or compet- itive, matched only by MINDTCT with enhanced input.

The authors state that SBMEX remains superior or competitive on optical exemplar fingerprints under type-aware evaluation, claiming it is matched only by MINDTCT with enhanced input. However, Table 3 shows that at the 16 px and π/6 rad threshold under type-aware matching on NIST SD302g, MINDTCT with enhanced input achieves an F1-score of 0.51, whereas SBMEX achieves 0.50. MINDTCT slightly outperforms SBMEX at this operating point rather than merely matching it. The prose should be adjusted to accurately reflect that MINDTCT (Enh) achieves the top score at this specific threshold setting.

2. Incomplete bifurcation direction definition — Major

L is computed as the arithmetic mean of the three branch lengths, whereas θ is defined as the bisecting direction of the two branches forming the acute enclosed angle.

The authors define the orientation angle for bifurcation minutiae as the bisecting direction of the two branches forming the acute enclosed angle. However, for symmetric or near-symmetric bifurcations (such as standard Y-junctions where all three branching angles are approximately 120 degrees), none of the enclosed angles are strictly acute (less than 90 degrees). Under these conditions, the mathematical formulation fails to specify how the orientation angle is determined. To resolve this ambiguity, the authors should update the formulation to specify that the direction bisects the two branches enclosing the smallest angle rather than requiring an acute angle.

3. Inconsistent latency reporting on Pareto comparison plot — Major

of LEADER (executed on GPU). For SBMEX, SBMEX- R, and CN Baseline, reported latencies explicitly encom- pass the full end-to-end pipeline including pyfing pre- processing, whereas other baselines are measured on orig- inal raw inputs.

In Figure 4, the trade-off plot pairs feature extraction accuracy (F1-score) against execution latency. For SBMEX and CNBaseline, the plotted latency includes both image pre-processing (pyfing) and core minutiae detection. However, for MINDTCT on exemplars, Figure 4 plots the F1-score corresponding to Enhanced inputs (0.65) against the runtime measured on Raw inputs (~183 ms), omitting the 645 ms pre-processing time required to produce those enhanced inputs. If pre-processing time were included, MINDTCT (Enh) would have a total latency of ~828 ms, making it slower than SBMEX (757 ms). Plotting Enhanced accuracy against Raw execution time distorts the latency-accuracy Pareto frontier. The authors should update Figure 4 to ensure that the reported latencies for all methods consistently reflect the actual processing pipelines used to achieve their respective accuracy scores.

4. Contradictory identification of best baseline on latents — Minor

SBMEX reaches type-agnostic F1-scores of 0.39, 0.36, 0.32 and SBMEX-R reaches 0.36, 0.34, 0.30, compared to the best traditional baseline MINDTCT (Enh) at 0.31, 0.28, 0.22 and FingerJet (Enh) at 0.37, 0.33, 0.26.

The authors state in the text that MINDTCT (Enh) is the best traditional baseline on the latent dataset with F1-scores of 0.31, 0.28, and 0.22. However, Table 3 shows that FingerJet (Enh) achieves F1-scores of 0.37, 0.33, and 0.26 across those same threshold levels on NIST SD302h, outperforming MINDTCT (Enh) at every point and also outperforming SBMEX-R (0.36) at the 16 px threshold. Designating MINDTCT as the top traditional baseline contradicts the reported numerical results in Table 3. The authors should correct the text to accurately acknowledge FingerJet (Enh) as the leading traditional baseline on latents.

5. Interaction conflict between dual-fusion and cluster decay — Major

Unpaired minutiae from both domain sets are preserved to ensure high recall, but their quality scores are penalized by factor w unpair , yielding q = q 0 · w unpair

The authors propose paired dual ridge-valley extraction followed by exponential spatial cluster decay. While the text specifies how unpaired minutiae are penalized by a scaling factor, it does not detail a deduplication or merging procedure for successfully paired ridge and valley minutiae. If both paired minutiae are retained in the candidate set at a distance within the maximum pairing threshold, they form an artificial spatial pair. When cluster decay is subsequently calculated, this artificial proximity causes the density index to increase, thereby penalizing the quality score of valid, dual-verified minutiae. The authors should clarify whether paired minutiae are merged into a single feature point prior to cluster decay or explain how duplicate density penalties are avoided.

xPeerd (AI review)

October 12, 2026

AI Review (xPeerd — DAReview)

Summary

This manuscript presents SBMEX, a deterministic handcrafted fingerprint minutiae detector intended as a modern open-source baseline for traditional fingerprint processing pipelines. The stated contribution is to replace costly neighborhood scanning and branching logic with a dual lookup-table architecture for Crossing Number computation and skeleton tracking, while also introducing continuous quality scoring, optional ridge-valley fusion, and cluster-based quality attenuation. The paper is clear in its engineering objective and it evaluates the method on NIST SD302 exemplar and latent datasets. The abstract accurately summarizes the intended contribution and claims that SBMEX is “a fast and deterministic minutiae detection method integrated into the open-source pyfing package” that “delivers feature extraction accuracy comparable to or outperforming traditional open-source baselines” with lower latency than classical Python CN implementations . The results support a strong practical contribution within the narrow scope of open-source traditional baselines, especially against CNBaseline, MINDTCT, and FingerJet .

The main strengths are clarity of motivation, transparent algorithmic formulation, reproducible benchmark framing, and convincing efficiency gains relative to a Python-native CN baseline. The main weaknesses are overstatement of novelty and performance context, limited ablation and sensitivity analysis, incomplete fairness in runtime comparisons, insufficient statistical reporting in the main text, and a somewhat narrow evidentiary basis for broader claims about practical superiority. I do not see obvious signs of fabrication or paper-mill style incoherence; the work fits a coherent biometric signal-processing paradigm and is technically consistent overall. However, several claims would benefit from tighter framing and stronger empirical substantiation.

Potential Major Revisions

1. Novelty claims should be narrowed and more precisely defended.

The manuscript states that “the present work introduces SBMEX (Skeleton-Based Minutiae EXtraction), a fast, deterministic, and fully auditable minutiae detection algorithm designed to provide a modern reference baseline for traditional fingerprint pipelines” and lists as contributions “a novel dual LookUp-Table (LUT) architecture” and “a continuous quality scoring paradigm” . The engineering package may indeed be useful, but the paper does not yet sufficiently distinguish methodological novelty from effective recombination of established components. The pipeline itself includes familiar stages: binarization, thinning, CN-based candidate extraction, tracking, optional ridge-valley fusion, and density-based attenuation . Since the work’s value may lie more in careful system design, optimization, and open-source implementation than in a fundamentally new detection principle, the paper should explicitly separate algorithmic novelty from implementation novelty. Otherwise, readers may infer a stronger conceptual advance than the evidence supports.

2. The evaluation scope is too narrow to support some of the broader practical claims.

The paper claims SBMEX is intended to “provide a modern reference baseline for traditional fingerprint pipelines” and that evaluation on NIST SD302 demonstrates consistent outperformance or matching of traditional baselines without fine-tuning . But the experiments are concentrated on SD302 exemplars and latents, both downsampled to 500 DPI, under one preprocessing ecosystem for algorithms needing enhanced or near-binary inputs . This is a respectable benchmark setup, yet it is not broad enough to justify general baseline-status claims across diverse operational settings. The manuscript should either temper the generalization or add experiments across additional datasets, image qualities, sensor conditions, or resolution settings. Without that, the external validity remains limited.

3. The comparisons mix preprocessing assumptions in a way that complicates fairness and interpretability.

Section 4.3 states that grayscale-capable extractors are evaluated on both raw and enhanced inputs, while SBMEX and CNBaseline require the pyfing enhancement pipeline; it further notes that passing enhanced images to off-the-shelf tools “may induce redundant internal filtering steps not originally intended by their design” but argues that this is the “most rigorous way to evaluate these tools ‘as-is’ under identical pre-processing conditions” . This is defensible, but not fully satisfactory. Identical preprocessing is not always equivalent to fair comparison when methods were designed around different input assumptions. The paper should more clearly distinguish:

• algorithm comparison under unified preprocessing,
• tool comparison under native intended usage,
• and end-to-end workflow comparison.

At present these are partly conflated, particularly when discussing relative latency and accuracy. A clearer experimental taxonomy would strengthen the manuscript substantially.

4. Runtime claims need tighter normalization and fuller disclosure.

The manuscript reports that “SBMEX achieves an average total execution time of 757 ms on Exemplars and 403 ms on Latents” while compiled packages such as MINDTCT and FingerJet are faster on raw inputs, but SBMEX has accuracy advantages on noisy latents . It then isolates preprocessing latency and argues that “the core detection time of SBMEX drops to just 112 ms” and SBMEX-R to 42 ms, versus CNBaseline at 1713 ms . This is useful, but the comparison basis shifts repeatedly:

• some methods are timed on raw inputs,
• some on enhanced inputs,
• some include preprocessing,
• some are compiled C/C++ packages,
• one is GPU-executed,
• and the focal efficiency comparison is partly against a Python baseline.

These are not invalid comparisons, but they should be presented more explicitly as non-equivalent runtime regimes. Otherwise, readers may overread the efficiency claim. A revised manuscript should include a compact methodological table defining exactly what is timed for each system and should separate “core detector latency” from “full pipeline latency” consistently.

5. Statistical robustness is asserted but underreported.

The text states that “All reported F1-score differences are statistically robust; 95% confidence intervals estimated via 1,000 non-parametric image-level bootstrap resamples were omitted from Table 3 for space constraints, as they all fall within ≤ 0.01” . This is important evidence, but omitting the intervals from the main presentation weakens interpretability. If the paper’s argument depends on small but consistent improvements over traditional baselines, then uncertainty reporting should be visible, not merely asserted. At minimum, a supplementary table or appendix should provide the intervals for all major comparisons. Ideally, significance of pairwise differences should also be clarified, because narrow intervals alone do not automatically establish practically meaningful superiority across all conditions.

6. The manuscript’s practical positioning against modern methods needs more careful framing.

The conclusion states that SBMEX is not intended to supersede deep learning or commercial methods in unconstrained settings and instead addresses the need for handcrafted, auditable pipelines . This framing is appropriate. However, elsewhere the paper places substantial emphasis on strong results and contextualizes performance against VeriFinger and LEADER in Table 3 and associated discussion . This creates some tension: the manuscript is strongest when framed as a transparent traditional baseline, not as a near-state-of-the-art extractor. The conclusion should be brought into tighter alignment with the empirical narrative by emphasizing the niche more consistently and avoiding any wording that might imply broader competitiveness than the reported latent and exemplar F1 values support.

7. Reproducibility is promising, but parameter sensitivity and design choice justification remain incomplete.

The paper provides Table 1 with default parameters such as dbg, dmin, dmax, dpair, θpair, wunpair, and δval , and Section 3 gives a relatively transparent mathematical description of candidate detection, tracking, dual ridge-valley fusion, and cluster-based decay . Yet the paper gives little evidence on how sensitive performance is to these settings. Since one of the main selling points is determinism and auditability, it is especially important to show robustness to parameter variation. Otherwise, the method may still require nontrivial tuning despite being framed as a practical baseline. An ablation or sensitivity study is needed for the main parameters and optional modules, especially dual-skeleton fusion and cluster decay.

8. Some claims of “fully auditable” and “standard compliance” are stronger than the demonstrated evidence.

The abstract emphasizes “full auditability” and “adherence to international standards” as reasons handcrafted methods remain important , and the conclusion reiterates “standard compliance” as part of SBMEX’s value proposition . However, the paper does not appear to include a dedicated section mapping outputs, assumptions, or parameterization to the relevant standard requirements. These claims may be intuitively plausible for minutiae-centric pipelines, but they are not demonstrated rigorously in the current manuscript. The language should either be qualified or supported with explicit standard-oriented analysis.

Potential Minor Revisions

1. There are several stylistic and typographic issues likely caused by PDF line wrapping or manuscript formatting that should be cleaned in the source. Examples visible in the extracted text include “minu- tiae” in Section 3 and “fil- tering” in the heading “3.2 Candidate detection and perimeter fil- tering” . These may be display artifacts, but the final manuscript should be checked carefully for broken hyphenation in headings and body text.

2. There is at least one grammatical error in Section 2.3. The sentence “CNBaseline is the traditional algorithm in [6], which applies standard morphological skeletonization to a pre-binarized image and applies the CN to identifies candidate minutiae” contains an error: “to identifies” should be “to identify” .

3. There is a spelling error in Section 2.1. The sentence “segment ridge-valley patterns, and tipycally compute a one-pixel-wide skeleton” should read “typically” .

4. Some phrasing is slightly overstated or promotional for a research manuscript. For example, “drastically speeding up skeleton traversal” and “fully comparable to legacy traditional baselines” could be made more neutral and specific . A less promotional tone would improve scholarly balance.

5. Table presentation should be made easier to parse. Table 3 is information-dense, spanning multiple threshold levels, datasets, and type-aware/type-agnostic conditions . Consider adding visual grouping cues or moving some conditions to supplementary material.

6. The footnote on enhanced image inversion for some extractors should be incorporated more clearly into the main methods text. The note explaining that enhanced inputs were inverted to match expected conventions is important for reproducibility and interpretability . It should not be easy to miss.

7. The paper would benefit from a concise notation recap. Section 3 introduces several symbols and lookup-table names in rapid succession, including BR, SR, BV, LUTCN, LUTND, dprev, and multiple hyperparameters . A compact notation table beyond parameter defaults would improve readability.

8. The conclusion is sensible but somewhat abrupt. It says future research will compare “fully traditional, deep learning-based, and hybrid pipelines across diverse operational conditions” . A slightly more specific future-work statement would be stronger.

AI content analysis for a post-2021 work

Estimated percentage of AI-generated content: low to moderate, approximately 10–25%.

Rationale:

• The manuscript is technically coherent, field-specific, and mathematically grounded.
• The terminology is consistent and not generically inflated.
• Citations, equations, benchmark design, and performance discussion are aligned in a way that suggests domain authorship rather than shallow synthetic assembly.
• However, some prose uses polished, repetitive rhetorical patterns common in AI-assisted academic drafting, such as “unleashing the power of simplicity,” “fully auditable,” “modern reference baseline,” and recurrent contrastive framing between legacy tools and modern workflows .

Highlighted AI-detected sections

• Abstract and introduction contain several high-fluency promotional formulations, for example “To bridge this gap, the present work introduces SBMEX...” and “drastic reduction in minutiae detection latency” .
• Contribution bullets in the introduction are stylistically uniform and may have been AI-assisted in wording, though not necessarily in substance .
• The conclusion’s rhetorical balancing between transparency, auditability, and modern workflow integration also has a polished AI-assisted feel .

Assessed epistemic impact Likely limited. Even if some prose was AI-assisted, I do not see strong evidence that the technical claims, equations, evaluation setup, or reported results are themselves fabricated on that basis. The epistemic risk lies more in possible overpolishing of novelty and impact claims than in obvious technical falsification. No clear paper-mill traits are evident from the retrieved text.

Recommendations

1. Reframe the paper explicitly as an optimized, transparent, open-source traditional baseline rather than implying a broader methodological breakthrough.
2. Add a dedicated ablation/sensitivity section covering at least dual-skeleton fusion, cluster-based quality decay, tracking-length thresholds, and ridge-only versus full SBMEX performance.
3. Separate evaluation into clearly labeled regimes: native-input comparison, unified-preprocessing comparison, and full end-to-end pipeline comparison.
4. Report confidence intervals and, if possible, paired significance analyses in an appendix or supplementary material.
5. Clarify exactly which runtimes include preprocessing and which do not, preferably in a compact comparison table.
6. Provide more direct evidence for claims related to auditability and standards alignment, or soften those claims.
7. Add broader validation if the manuscript seeks general baseline status beyond SD302.
8. Correct typographic and grammatical issues and reduce promotional phrasing.

Overall, I find this to be a credible and practically useful manuscript with a coherent technical contribution, but it would benefit from stronger empirical justification, tighter claim calibration, and more explicit reporting discipline before it can be considered fully convincing as a reference baseline paper.

XSci (AI review)

October 12, 2026

Referee Report

Manuscript: Revisiting Handcrafted Minutiae Detection: A Simple and Effective Open-Source Baseline for Modern Fingerprint Workflows

Recommendation: Major revision

Summary and Recommendation

The manuscript introduces SBMEX, a deterministic skeleton-based minutiae extractor released within the author's open-source pyfing package. The motivating observation is well made: the community's handcrafted baselines are legacy C/C++ tools that do not integrate with modern scientific workflows, a constraint illustrated concretely through Oblak et al. [6] and a cluster of recent works [7-10] that still default to MINDTCT for want of an alternative. Three contributions are claimed: an 8-bit neighborhood encoding computed by correlation (Eq. 1) that indexes both a Crossing Number table and a state-transition table returning ordered successor directions; a continuous quality score proportional to tracked path length, modulated by ridge-valley agreement and attenuated by a density decay; and a configurable ridge-only or dual-skeleton mode. Evaluation covers 2,380 exemplars from NIST SD302g and 3,815 latents from SD302h, scored by maximum $F_1$ at three tolerance levels under type-agnostic and type-aware regimes.

The contribution is real and the engineering sound. The $LUT_{ND}$ formulation is genuinely elegant, collapsing successor selection, backtracking suppression and angular ordering into one table read; the method description is precise enough to reimplement; and the latency instrumentation is transparent enough that core detection times reconcile exactly against the reported end-to-end figures. Several evaluation choices — isolating detection from matching, reporting competitors on both raw and enhanced input, excluding commercial and learned systems from the traditional ranking — reflect better practice than is common here. What requires revision is the relationship between claims and evidence. The accuracy figures are oracle maxima selected on the evaluation data under a protocol whose aggregation convention is never specified; the speed and accuracy advantages are each credited to a component the experiments cannot isolate; and several statements in Section 4.3 are contradicted by the manuscript's own Table 3. These are correctable through reanalysis, additional ablation, and more careful wording rather than through reconstruction of the method.

Major Concern Category 1: Evaluation Design and the Status of the Reported Numbers

1.1 The headline figures are oracle operating points, and the advantage is distributed unevenly

Section 4.2 reports the maximum $F_1$ achievable by sweeping each extractor's confidence threshold, so every figure in Table 3 is a supremum over an operating-point family chosen with reference to the test labels. No deployment can realize such a point, since a fielded system must commit to a threshold in advance, and the resulting optimism is nowhere characterized — a serious omission when the margins carrying the conclusions are frequently 0.01 to 0.03. The difficulty is compounded by asymmetry: CNBaseline, which "yields unranked detections without confidence scores," is scored at a single operational point, and it is also the comparator against which SBMEX's largest margins are reported on both accuracy and latency. The zero-shot framing is likewise undercut if the most consequential deployed parameter, the acceptance threshold, is fitted to the evaluation set.

1.2 The aggregation and pairing procedures are unspecified, leaving the reported $F_1$ ambiguous

An $F_1$ obtained by pooling true positives, false positives and false negatives across the dataset differs from one computed per image and averaged, and the two coincide only when images contribute equally — far from the case across full exemplars and fragmentary latents. The manuscript does not say which convention is used, and the choice could move the values by more than the margins at issue. Related decisions are likewise open: the cost matrix supplied to the assignment algorithm [30] is never defined, though distance and angle are in different units, and since the evaluation region is a bounding box rather than the mask, it is unclear whether detections inside the box but outside the irregular latent mask count as false positives. Configuration reporting compounds this, with no pyfing commit, no VeriFinger version, and no statement on release of the evaluation harness or image lists.

1.3 The statistical argument does not support the comparative inferences drawn from it

Section 4.3 asserts that all reported differences are "statistically robust," grounding this in 95% confidence intervals from 1,000 image-level bootstrap resamples that "all fall within $\leq$ 0.01." The inference does not follow. A comparative claim requires the sampling distribution of the difference between two methods, not the width of each marginal interval; because both are evaluated on the same images their scores are correlated, and the correct procedure resamples images and recomputes the paired difference — an interval that may prove narrower, helping the author's case, or wider where methods fail on disjoint subsets. The quoted width also sits uncomfortably against the differences interpreted, since the 0.01 gap separating SBMEX from SBMEX-R on Exemplars is of the same order as the stated uncertainty. Bootstrapping a max-$F_1$ statistic further describes the variability of a biased estimator rather than correcting the bias, since the threshold is re-optimized within each resample.

1.4 Several comparative claims are contradicted by the manuscript's own results table

Section 4.3 states that on Latents SBMEX and SBMEX-R outperform "all traditional open-source baselines by a significant margin in both type-agnostic and type-aware regimes." Table 3 does not support this. At (16 px, $\pi/6$ rad) type-agnostic, FingerJet with enhanced input reaches 0.37 against SBMEX-R's 0.36, so the claim fails for the ridge-only variant at the very threshold used as the reference point in Figure 4, and full SBMEX leads the strongest traditional competitor by 0.02 there and by the same amount in the type-aware regime. The discussion accompanying Figure 4 sharpens this, reporting "0.39 vs. 0.30 and 0.22" — the raw-input configurations — while omitting FingerJet's enhanced-input 0.37, though enhanced rows exist precisely to permit comparison under identical preprocessing. A parallel overstatement appears on Exemplars, where SBMEX is described as "matched only by MINDTCT with enhanced input" although MINDTCT (Enh) records 0.51 against SBMEX's 0.50 at the widest tolerance.

Major Concern Category 2: Attribution of Effects Across Components

2.1 The speedup is credited to the look-up tables but measured against a comparator differing in several respects

The abstract attributes SBMEX's throughput to the dual-LUT architecture, evidenced by the contrast between 112 ms core detection and CNBaseline's 1,713 ms. These measurements may be accurate without establishing the claim, because the two systems differ simultaneously in their use of look-up tables, their use of vectorized array operations rather than per-pixel Python iteration, and the engineering effort invested — CNBaseline being a component built by another team for a quality-assessment study rather than an artifact optimized for throughput. Replacing per-pixel loops with array operations routinely yields one to two orders of magnitude in Python, spanning the entire observed gap. The manuscript gestures at this when noting that formulating Eq. (1) as a correlation leverages optimized library routines, which is a vectorization benefit rather than a tabulation benefit. Two self-ablations holding implementation quality fixed would settle the attribution directly.

2.2 The accuracy advantage is entangled with the author's own enhancement pipeline

Every SBMEX figure is an SBMEX-plus-pyfing figure, since Section 4.1 feeds the method a four-stage pipeline of the author's own components [25-28] and it is never reported on any other input. The data show this is not neutral. On Latents at the widest tolerance, moving FingerJet from raw to enhanced input raises it from 0.22 to 0.37; the same transition lowers VeriFinger from 0.60 to 0.39 and LEADER from 0.69 to 0.48. The front end therefore swings results by as much as 0.21 depending on the consuming detector, roughly an order of magnitude more than the 0.02 margin attributed to SBMEX, leaving a reader unable to tell whether the advantage reflects superior detection logic or a detector well matched to one enhancement's output. The coupling is structural: with $t_b = 0$ the binarization rule admits only zero-intensity pixels, so SBMEX cannot run raw. Running it on one independent enhancement would address the question properly.

2.3 The parameter fitting procedure is undocumented and two of three contributions are never ablated

Table 1 lists ten parameters and Section 4.2 reports only that they "were tuned offline on the FVC2000 DB2-A benchmark [29]." The objective function is not stated, the search strategy is not described, and it is unreported whether parameters were optimized jointly or sequentially. This matters because FVC2000 is distributed as a verification benchmark and, so far as this referee is aware, does not ship with expert minutiae annotations; if so, an $F_1$-style detection objective was unavailable there and the manuscript needs to explain what criterion substituted. A representativeness question also persists, as parameters fitted on clean capacitive live-scan impressions are deployed on chemically developed latents where the strongest claims are made. Of the three claimed contributions, moreover, only dual-skeleton fusion is ablated; the continuous quality paradigm is never compared against the binary hard-filtering it claims to improve upon.

2.4 The related work survey is too compressed to establish what is new

Section 2 allocates two paragraphs and two citations [11, 12] to the entire traditional literature, which the Introduction describes as spanning more than half a century, while devoting comparable space to deep learning methods the paper does not compete with. The imbalance matters because novelty can only be assessed against surveyed prior art. There is no treatment of the skeleton post-processing and false-minutiae-removal literature, although the perimeter filter, the $d_{\min}$ rejection and the cluster decay are all mechanisms of that kind, leaving a reader unable to tell whether these are new ideas or standard rules recast in continuous form. Nor is there discussion of prior work exploiting ridge-valley duality, despite dual fusion being a headline contribution and the duality being formalized in the ISO standard the paper cites [3]. The claim that researchers face "the absence of a modern alternative" is likewise established by example rather than systematically.

Major Concern Category 3: The Quality Model and the Gap Between Claims and Evidence

3.1 The initial quality score saturates and is structurally unequal across minutia types

Section 3.3 defines $q_0 = L / d_{\max}$, so with the defaults of Table 1 the score is confined to $[0.25, 1.0]$ and is capped above. Any candidate admitting a clean 20-pixel traversal receives $q_0 = 1.0$ regardless of how much cleaner one is than another, and on well-resolved exemplars a substantial fraction of true minutiae may share that maximal value — in which case the ordering at the top of the ranking is set entirely by the cluster-decay term, that is by local density rather than evidence of correctness. A second asymmetry concerns type: for endings $L$ is a single tracked path, whereas for bifurcations it is the mean of three branches each terminating at the next structural event, so the mean is systematically depressed and bifurcations would be pruned preferentially as the threshold rises. This bears directly on the type-aware regime, where SBMEX falls from 0.68 to 0.50 on Exemplars and 0.39 to 0.25 on Latents; score distributions reported by type would distinguish it from simple type confusion.

3.2 The density index is an unnormalized global sum, coupling each score to its image's minutiae population

Section 3.5 defines $D_i = \sum_{j \neq i} \Psi_{ij}$ over all other minutiae, with $\sigma_{cl} = 11$ px and $\gamma_{cl} = 0.5$. At 500 DPI the ridge period is roughly nine to ten pixels, so a minutia on an adjacent ridge sits near one $\sigma_{cl}$, contributing $\Psi \approx 0.6$ and attenuating the score by about a third on its own; the interaction radius is thus comparable to the natural spacing of legitimate minutiae rather than to the scale of spurious clusters, penalizing the minutiae-rich regions near cores and deltas that carry the most discriminative information. More seriously, because the sum is unnormalized its magnitude grows with the number of detections, so every minutia in a richly populated image is attenuated more than an identical minutia in a sparse one. Since Section 4.2 sweeps a single global threshold across the dataset, this converts an image-level offset into bias in which detections survive — pruning complete impressions first and fragments last, the opposite of the intended behaviour.

3.3 Framing claims are unsupported, and the efficiency claim is contradicted by the paper's own measurements

The Introduction rests the case for handcrafted extraction on three bulleted claims, none supported by citation, and the reference list contains no item from the forensic or legal literature despite the first concerning judicial admissibility. That claim is also in tension with expert opinion, since the 2016 PCAST report recommended that latent print analysis move toward objective instrumented methodology — favouring whichever approach has documented error rates rather than handcrafted methods as such. The third claim is contradicted outright: SBMEX requires 757 ms per exemplar and 403 ms per latent against MINDTCT's 183 ms and 109 ms and FingerJet's 37 ms and 21 ms, making it roughly four and twenty times slower than the legacy tools whose obsolescence motivates the paper, while the edge-deployment assertion is never tested outside a server-class Xeon. Section 4.1 also treats examiner annotations as error-free ground truth, which the literature on examiner variability does not support and which bounds latent precision by annotation completeness rather than detection correctness.

3.4 No experiment connects the detector to a workflow outcome, and the evidence base is narrow

The title and conclusion position SBMEX as a baseline for fingerprint workflows and Section 3.5 justifies continuous scoring as "soft-scoring that downstream matchers can easily threshold," yet no matcher appears in the evaluation and the score's only validation is that sweeping it yields a favourable maximum — establishing that it can be thresholded, not that its values are meaningful. The evidence base is also narrower than the general claims suggest: one benchmark family, one normalized resolution, latents restricted to marks already judged suitable for comparison, and aggregate reporting with no stratification by mark quality, which for latent work conceals exactly what practitioners need. Precision and recall are never reported separately, hiding whether the advantage comes from finding more true minutiae or emitting fewer spurious ones — a distinction that matters because controlled perturbation studies find matchers considerably more sensitive to missing than to spurious minutiae, which in fact supports the author's own choice to preserve unpaired minutiae for recall.

Minor Issues

1. The column header for the second dataset block in Table 3 reads "NIST SD302 Learner," apparently a transcription error for "Latent." Since Table 3 is the principal result, this warrants correction, as does the underline convention described in the caption, which does not render and leaves the second-best annotations unreadable.

2. VeriFinger is used throughout Section 4.3 and Figure 4 but has no reference-list entry, and neither vendor, SDK version, nor extraction settings are reported. Commercial extractor behaviour varies substantially across releases, so these details are necessary for the comparison to be interpretable or reproducible.

3. The default $t_b = 0$, combined with $B_R = \mathbb{I}(I \leq t_b \wedge M = 1)$, classifies only zero-intensity pixels as ridge, implying binary input rather than the grayscale $I \in [0,255]$ declared in Section 3.1. This dependency should be stated explicitly, with guidance on setting $t_b$ for genuinely grayscale inputs.

4. The variant SBMEX-R appears throughout the results and in Table 3 but is never formally defined; Section 3.1 describes stage 4 as optional without naming the resulting configuration. Relatedly, the neighborhood-pattern table referenced as Table 2 carries no caption or column headers, despite being the clearest exposition of the dual-LUT mechanism.

5. No asymptotic complexity analysis is given, despite efficiency being a headline contribution. The cluster decay of Section 3.5 is quadratic in the number of minutiae while all other stages are linear in pixels — the only superlinear step in the pipeline, and one a bounded neighborhood sum would eliminate.

6. Precision and recall are not tabulated for any method or condition, Figure 4 shows no uncertainty in either dimension, and mean extracted minutiae per image is unreported. These inexpensive statistics are needed to interpret both the Precision-Recall behaviour and the density-decay mechanism.

7. Several specification ambiguities should be closed: whether the $\delta_{\text{val}}$ shift direction refers to types before or after inversion; whether cluster decay is applied before or after the $w_{\text{unpair}}$ penalty; what cost function the fusion-stage matching minimizes; which mask $M$ feeds the perimeter filter on latents; and what resampling method was used to downsample 1000 DPI exemplars, since interpolation affects skeleton topology.

8. Table 1 parameters are given "at 500 DPI" with no scaling rule for other resolutions, limiting reuse as a general baseline. The abstract's "without fine-tuning" also imports a deep-learning idiom; Section 4.2's "without dataset-specific fine-tuning" is accurate and equally favourable.

Missing and Inadequately Integrated Literature

Cited but Inadequately Integrated

The ISO standard [3] is invoked to claim standardization compliance but never engaged with substantively. Clause 6.4 locates a ridge ending, in the record format, at the bifurcation of the valley skeleton in front of the ending, with the ridge skeleton endpoint available only under the alternative ENDINGTYPE encoding, and Clause 6.5 defines direction as the mean tangent of the two arms enclosing the acute angle. SBMEX places endings at ridge skeleton endpoints and derives direction from the tracked segment, corresponding to the alternative convention. The author should state which convention is implemented, whether the $\delta_{\text{val}}$ shift approximates the ridge-ending/valley-bifurcation duality the standard formalizes exactly, and whether a conformant template can be exported — particularly since tolerances as tight as $\pi/10$ rad would make convention mismatches measurable in the type-aware results.

Other cited works carry more weight than their treatment suggests. Oblak et al. [6] supplies CNBaseline, yet whether that implementation was ever intended as an optimized reference goes undiscussed despite anchoring the efficiency claim. Guo and Hall [21] is adopted without justification, although the thinning operator determines the artifact population the validation cascade is calibrated against. The NBIS suite [4] is cited only for MINDTCT, though it also contains NFIQ, against which a new quality measure should be positioned, and Bozorth3, which would enable the missing downstream evaluation. The XSFFE estimator [27] already computes the local ridge period from which Table 1's fixed geometric parameters could be derived adaptively. And reference [2] simultaneously supplies the evaluation protocol, the deep learning comparator, and an unrefereed preprint by the present author — a triple role warranting acknowledgment.

Truly Missing Papers

Several works bear directly on the contributions and are not cited. Zhao and Tang (2007) propose binarizing and thinning the valley rather than the ridge and exploit "the intrinsic duality property of the fingerprint image" in post-processing, directly anticipating the dual-fusion contribution. Farina, Kovács-Vajna and Leone (1999) is the canonical treatment of minutiae extraction from skeletonized binary images, its central contribution a validation stage examining local skeleton configuration — structurally the problem SBMEX's filtering cascade addresses. Ratha, Chen and Jain (1995) is foundational for the tradition Section 2.1 surveys, and Lam, Lee and Suen (1992) would ground the thinning choice. On evaluation and quality, Grother and Tabassi (2007) establishes the error-versus-reject methodology by which a scalar quality measure is shown to predict performance — precisely the validation the quality contribution lacks; Cappelli et al. (2006) treats evaluation protocol design; and Grosz et al. (2019) shows matchers are more sensitive to missing than to spurious minutiae. The forensic framing also requires sources it lacks, among them PCAST (2016) and Ulery et al. (2011) on examiner accuracy and disagreement.

Cappelli, R., D. Maio, D. Maltoni, J. L. Wayman, and A. K. Jain. 2006. Performance evaluation
    of fingerprint verification systems. IEEE TPAMI 28(1):3-18.
Farina, A., Z. M. Kovács-Vajna, and A. Leone. 1999. Fingerprint minutiae extraction from
    skeletonized binary images. Pattern Recognition 32(5):877-889.
Grosz, S. A., J. J. Engelsma, N. G. Paulter Jr., and A. K. Jain. 2019. White-box evaluation of
    fingerprint matchers: Robustness to minutiae perturbations. arXiv:1909.00799.
Grother, P., and E. Tabassi. 2007. Performance of biometric quality measures. IEEE TPAMI
    29(4):531-543.
Lam, L., S.-W. Lee, and C. Y. Suen. 1992. Thinning methodologies - a comprehensive survey.
    IEEE TPAMI 14(9):869-885.
President's Council of Advisors on Science and Technology. 2016. Forensic Science in Criminal
    Courts: Ensuring Scientific Validity of Feature-Comparison Methods. Washington, DC.
Ratha, N. K., S. Y. Chen, and A. K. Jain. 1995. Adaptive flow orientation-based feature
    extraction in fingerprint images. Pattern Recognition 28(11):1657-1672.
Tabassi, E., C. L. Wilson, and C. I. Watson. 2004. Fingerprint Image Quality (NFIQ). NISTIR
    7151, National Institute of Standards and Technology.
Ulery, B. T., R. A. Hicklin, J. Buscaglia, and M. A. Roberts. 2011. Accuracy and reliability of
    forensic latent fingerprint decisions. PNAS 108(19):7733-7738.
Zhao, F., and X. Tang. 2007. Preprocessing and postprocessing for skeleton-based fingerprint
    minutiae extraction. Pattern Recognition 40(4):1270-1281.

Conclusion and Path Forward

The manuscript identifies a genuine gap in the community's infrastructure and responds with a well-engineered, readable, maintained tool inside a complete pipeline. That packaging may prove the more durable contribution, and saying so does not diminish it: the field needs a usable Python-native extractor more than another variation on Crossing Number detection, and the $LUT_{ND}$ formulation deserves sharper emphasis than it receives. The instincts to isolate detection from matching, to report competitors under both input conditions, and to keep commercial and learned systems out of the traditional ranking should all survive revision intact.

What needs work is the inferential chain from experiment to claim. The accuracy figures should be accompanied by fixed-threshold results and threshold-independent summaries, with an equitable scoring arrangement for CNBaseline and a fully specified protocol covering aggregation, pairing cost, and the treatment of in-box background detections. Paired bootstrap intervals should replace the appeal to marginal widths, and Section 4.3 should be rewritten so that each comparison names the strongest competitor configuration and reports differences numerically rather than through intensifiers Table 3 does not bear out. Two self-ablations would establish how much of the speedup belongs to the look-up tables rather than to vectorization, and a single run on an independent enhancement would show whether the accuracy advantage belongs to the detector rather than the author's own front end. Documenting the tuning procedure, ablating the quality-scoring contribution, reporting precision and recall separately with stratification by mark quality, and adding a downstream matching result with an error-versus-reject analysis would convert several assertions into evidence — none of which requires new infrastructure or new data.