Paper A v13 rev9.2: firm-key unification + canonical-number reconciliation (rev9.1 review R1-R6)

Resolve the Firm C/D "two-snapshot" inconsistency from the co-author rev9.1 review.
Root cause was NOT stale data but two live firm-assignment keys (assigned_accountant->
registry firm vs the excel_firm column) used inconsistently across tables; standardize
on the registry key, which the headline Table IV/II-b already use. Sole difference = 379
signatures with excel_firm=C but registry firm=D; A and B identical under both keys.

Numbers (all DB-verified, registry key, n=150,442):
- Table II-c Firm C/D recomputed (was mixing keys within firm C across periods, which
  manufactured the spurious "third value" 38,934); now C 22,449+16,164=38,613,
  D 9,945+7,188=17,133, all four firms reconcile.
- Table VI C/D counts + S III-B prose + Fig 3/6 captions -> 150,442.
- S V-B HC-rate text -> Firm C 21.6->26.7%, Firm D 22.0->28.0%.

Note on R4: the reviewer (PDF-only) asked to change S IV-C to 26.5/28.5 to match Table
II-c; DB verification showed the reverse - S IV-C's 26.7/28.0 are correct and Table II-c
was the stale outlier, so II-c was aligned to S IV-C (data-correct, opposite to the
literal instruction).

Accountant counts (R2 reviewer "179>171 impossible" = false positive; three distinct,
all-reproducible universes): Table I + S III-B -> 457 (>=2 sig, owns the 150,442
signatures); Table III documented as the 437 with >=10 signatures (K=3 GMM subset,
reproduces A=82.5/B=0.0/C=1.0/D=1.9% exactly); bootstrap 179/280 unchanged
(accountant_id key, correct and invariant to the A-vs-BCD contrast).

R3 (corpus scope): S III-B reworded - corpus = all retrievable reports, Big-4 as the
primary analysis sample (removes the "corpus = four firms" vs "non-Big-4 in robustness"
contradiction); per-firm counts now explicitly labelled A/B/C/D.
R5 (spelling): unify to American (artefact->artifact x11, centred->centered,
behaviour->behavior, analyse(d)->analyze(d), favours->favors).
R6: delete non-standard "(+)" marker in S IV-C.

Figures regenerated under the registry key: make_fig3_density.py and
make_fig6_sensitivity.py switched to the assigned_accountant join (fig3/fig6 n=150,442);
fig4/fig5 refreshed. FE/LOYO/bootstrap re-validated exactly (ORs 0.116/0.061/0.070,
LOYO 53.1-54.9pp, full 53.7pp).

Add CANONICAL_NUMBERS_rev9.1.md with full provenance, the analyzable/GMM definitions,
and the firm-key root cause.

Co-Authored-By: Claude Opus 4.8 (1M context) <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01K35dXhb9XEM1mnYz6SSHpU

paper/v13_build/CANONICAL_NUMBERS_rev9.1.md

@@ -0,0 +1,95 @@
+# Canonical number set — Paper A v13 rev9.1 (verified 2026-06-30)
+
+Source of truth: `signature_analysis.db` (`/Volumes/NV2/PDF-Processing/signature-analysis/`).
+Verified against scripts in `paper/v13_build/scripts/`. All firm-level signature counts and
+within-accountant HC rates below are DB-reproduced to 2 decimals.
+
+## ROOT CAUSE of the "Firm C/D two-snapshot" inconsistency
+
+It is **NOT** a stale snapshot. It is **two live firm-assignment keys** used inconsistently:
+
+| Key | Definition | C | D | total |
+|---|---|---|---|---|
+| **assigned** (canonical) | `assigned_accountant → accountants.firm` (registry firm) | 38,613 | 17,133 | **150,442** |
+| excel | `excel_firm` column (source Excel metadata) | 38,993 | 16,752 | 150,441 |
+
+Difference = **379 signatures with excel_firm=資誠(C) but registry firm=安永(D)** (one/few
+cross-labeled accountants). A and B are identical under both keys. Because the headline
+contrast pools B/C/D, the swap is invisible to it (FE/LOYO/bootstrap reproduce exactly under
+either key); only **per-firm-separated tables** (IV, II-b, II-c, VI) are affected.
+
+DECISION: standardize on the **assigned** key — it is what headline Table IV/II-b already use.
+
+## "Analyzable signatures" definition (reproduces 150,442 exactly)
+
+Analyzable = signature whose CPA has **≥2 signatures** (singleton CPAs have no same-accountant
+partner). Per-firm singletons (A:2, B:6, C:3, D:0) exactly equal raw−Set A.
+
+## Canonical signature counts (assigned key)
+
+| Firm | Full 2013–23 | 2013–19 | 2020–23 |
+|---|---|---|---|
+| A | 60,448 | 36,550 | 23,898 |
+| B | 34,248 | 19,677 | 14,571 |
+| C | 38,613 | 22,449 | 16,164 |
+| D | 17,133 | 9,945 | 7,188 |
+| Big-4 | **150,442** | 88,621 | 61,821 |
+
+Every row sums exactly. (excel-key alternatives, do NOT use for per-firm tables:
+C 2020–23 = 16,485, D 2020–23 = 6,866 — these are what the stale Table II-c rows show.)
+
+## Five-way breakdown (HC | MC | HSC | UN | LH | n), low cut = 0.8547
+
+FULL 2013–2023 (Table IV):
+- A: 81.70 | 10.76 | 0.05 | 7.35 | 0.14 | 60,448
+- B: 34.56 | 35.88 | 0.29 | 28.95 | 0.32 | 34,248
+- C: 23.75 | 41.44 | 0.38 | 33.97 | 0.47 | 38,613
+- D: 24.51 | 29.33 | 0.22 | 45.28 | 0.66 | 17,133
+- Overall: 49.58 | 26.47 | 0.21 | 23.42 | 0.32 | 150,442
+
+2013–2019 (Table II-b):
+- B: 29.04 | 39.31 | 0.39 | 30.91 | 0.35 | 19,677
+- C: 21.59 | 42.09 | 0.37 | 35.53 | 0.43 | 22,449
+- D: 22.01 | 29.67 | 0.20 | 47.35 | 0.76 | 9,945
+
+2020–2023 (Table II-c) — **C/D are the fix**:
+- A: 83.84 | 9.13 | 0.04 | 6.88 | 0.11 | 23,898
+- B: 42.01 | 31.24 | 0.16 | 26.31 | 0.28 | 14,571
+- C: **26.74 | 40.55 | 0.40 | 31.80 | 0.51 | 16,164**  (manuscript stale: 26.53/.../16,485)
+- D: **27.98 | 28.85 | 0.24 | 42.42 | 0.51 | 7,188**   (manuscript stale: 28.53/.../6,866)
+
+Per-firm period HC rates (§IV-C text / Fig 5 — already CORRECT in manuscript):
+A 80.3→83.8, B 29.0→42.0, C 21.6→26.7, D 22.0→28.0.
+
+## Table VI (any-pair vs same-pair HC) under assigned key
+
+| firm | n | any-pair% | same-pair% |
+|---|---|---|---|
+| A | 60,448 | 81.7 | 57.3 |
+| B | 34,248 | 34.6 | 9.0 |
+| C | 38,613 | 23.7 | 5.3 |
+| D | 17,133 | 24.5 | 7.7 |
+| all | 150,442 | 49.6 | 27.3 |
+
+(Manuscript currently shows excel-key: C 38,993, D 16,752, all 150,441, D any-pair 24.7.)
+
+## Accountant counts (R2) — reviewer's "179 > 171 impossible" is a FALSE POSITIVE
+
+Different keys, not a contradiction:
+- Bootstrap/FE (`accountant_id`, is_valid): **A=179** (reproduces exactly), BCD=281 (manuscript 280).
+- Table III / accountant-level partition (171/112/102/52 = 437): RESOLVED 2026-06-30 — this is the
+  Big-4 accountants with **≥10 signatures** (registry key), reproduces EXACTLY on current DB.
+  GMM recipe: accountant point = (mean max_similarity_to_same_accountant, mean min_dhash_independent);
+  sklearn GaussianMixture(n_components=3, covariance_type='full', random_state=42, n_init=10);
+  templated cluster = highest-cosine component (cos 0.983 / dHash 2.4). Shares reproduce to the digit:
+  A=82.5% (141/171), B=0.0% (0/112), C=1.0% (1/102), D=1.9% (1/52). Script: scratchpad/gmm.py.
+- Analyzable accountant count (registry name key, ≥2 sig) = 457 (A=178, B=119, C=107, D=53) — owns
+  the 150,442 signatures; now stated in Table I and the §III-B prose.
+
+THREE DISTINCT, ALL-REPRODUCIBLE accountant universes (the reviewer collapsed them → false "179>171"):
+  457 (≥2 sig, owns 150,442) | 437 (≥10 sig, Table III GMM) | 459 = 179/280 (accountant_id bootstrap).
+Manuscript edits applied 2026-06-30: Table I + §III-B prose → 457; §III-B prose + Table III caption
+note the 437/≥10-sig subset. Bootstrap 179/280 stays (correct, key-invariant).
+
+## F5 robustness (re-validated EXACTLY on current DB, key-invariant)
+Firm+Year FE ORs: B=0.116, C=0.061, D=0.070. LOYO gap range [53.1, 54.9]pp, full-sample 53.7pp.

paper/v13_build/paper_v13_filled.md

@@ -39,7 +39,7 @@ The paper is organized to move from the problem to the evidence. Section II revi
 
 Why reproduction matters: signatures carry symbolic weight. A signature is valuable mainly as a symbol — it stands for the signer's identity and intent. Recent experiments show that this symbolism does not survive a change in how one signs. In studies that take the reader's point of view, Chou [41] finds that electronic signatures give a weaker sense of the signer's presence than handwritten ones, and that readers therefore judge an e-signed document as less valid and expect more non-compliance; across five kinds of e-signature (a checked box, a PIN, an avatar, a typed name, and a software-generated signature), the software-generated kind felt the most "present" of the electronic options but still less than a handwritten signature. In studies that take the signer's point of view, Chou [42] finds that electronic signatures give a weaker sense of self-presence — the signer's felt attachment to the mark — and that this, in turn, makes people more willing to cheat; the work singles out signing by proxy (an autopen) as cutting the tie between the document and the signer. These results matter for us because the practice we detect — a stored signature image laid onto a report by staff or by software — is, in this scheme, one of the lowest-presence modes: it looks like a software-generated signature and is executed like a proxy signature, because the accountant performs no signing act for the report. These effects are robust rather than one-off: in a pre-registered, multi-study replication with meta-analysis, Tzelios and Williams [43] reproduce Chou's reader-side result — an avatar e-signature lowers the sense of the signer's presence and raises the expectation that the contract will be breached. In their general discussion the same authors point to accounting as a next setting — noting the spread of online tax filing and asking how digital signatures affect an evaluator's assessment of the legitimacy of claims, while cautioning that accounting documents may prove less sensitive to signature form than legal ones. We read that call precisely: their "auditors" are the readers of digitally signed filings — those who evaluate the claims — not the certifying accountants who sign. The signer-side question in auditing — what it means when the certifying professional's own signature is reproduced rather than performed — is not addressed in that literature. Both questions, reader-side and signer-side, presuppose the same missing capability: a way to measure non-hand-signing at scale. The lesson we draw is not that non-hand-signing harms audit quality — that is a separate question we leave to a companion study (Section VI) — but that whether it matters is a real question, and one nobody can study without first being able to measure non-hand-signing at scale.
 
-Signature analysis to date is about forgery, not reuse. The obvious toolkit for that measurement is signature analysis, but its main concern is the wrong one for us. Bromley et al. [3] introduced the Siamese network that still anchors the field; SigNet [4] extended it to compare writers it had never seen; Kao and Wen [5] worked from a single genuine sample; TransOSV [6] brought in a Vision Transformer; and meta-learning has been used to cut the effort of enrolling new signers [16]. All of this targets imitation by another hand, so it learns to tell different people apart. Our task is the opposite: spotting reuse of the genuine signer's own image, which lives in the most-similar tail of one person's signatures. The closest idea uses reference examples to set a sensible cutoff [8], but on benchmark data with known genuine references — whereas our archive has no signature-level labels at all. This body of work is also overwhelmingly built on Western, Latin-script signatures; non-Latin scripts such as Chinese are comparatively under-served, and reported accuracies for them are lower [44]. Chinese signatures are structurally distinctive — many strokes, with wide variation between writers — and the forensic literature on them is thin; the closest precedent, Chen [45], analyses Chinese signatures with a maximum-similarity-to-same-class statistic that directly parallels our use of the maximum cosine to the same accountant. Our descriptors, however, work on the image rather than on script-specific strokes, so the method itself does not depend on the script.
+Signature analysis to date is about forgery, not reuse. The obvious toolkit for that measurement is signature analysis, but its main concern is the wrong one for us. Bromley et al. [3] introduced the Siamese network that still anchors the field; SigNet [4] extended it to compare writers it had never seen; Kao and Wen [5] worked from a single genuine sample; TransOSV [6] brought in a Vision Transformer; and meta-learning has been used to cut the effort of enrolling new signers [16]. All of this targets imitation by another hand, so it learns to tell different people apart. Our task is the opposite: spotting reuse of the genuine signer's own image, which lives in the most-similar tail of one person's signatures. The closest idea uses reference examples to set a sensible cutoff [8], but on benchmark data with known genuine references — whereas our archive has no signature-level labels at all. This body of work is also overwhelmingly built on Western, Latin-script signatures; non-Latin scripts such as Chinese are comparatively under-served, and reported accuracies for them are lower [44]. Chinese signatures are structurally distinctive — many strokes, with wide variation between writers — and the forensic literature on them is thin; the closest precedent, Chen [45], analyzes Chinese signatures with a maximum-similarity-to-same-class statistic that directly parallels our use of the maximum cosine to the same accountant. Our descriptors, however, work on the image rather than on script-specific strokes, so the method itself does not depend on the script.
 
 Image-duplication and document forensics: useful parts, different setting. A second line of work looks directly at duplicated images. Copy-move detection finds regions copied within an image [11], and Abramova and Böhme [10] adapted it to scanned documents, noting that ordinary repeated characters confuse the standard methods. Self-supervised copy detection on everyday photos [13] shows that pretrained CNN features with cosine similarity make a strong baseline for spotting near-duplicates. Closest in pipeline terms, Woodruff et al. [9] pull signatures from corporate filings for anti-money-laundering work — but to group signatures by who signed them, not to detect one signer's image being reused across documents. The building blocks exist; the specific setting — one signer's image reused across many scanned financial reports — does not seem to have been addressed.
 
@@ -63,7 +63,7 @@ To pin down the signing practices that we need in order to interpret the results
 
 ### B. Data and Analysis Design
 
-The corpus is all retrievable Taiwan statutory audit reports for fiscal years 2013–2023 from the four largest firms (A–D); signatures are extracted from them as described in Section III-C. To be precise about the headline denominator, since it recurs throughout: the primary analysis sample is the four-firm (Big-4) set, and "150,442 analyzable signatures" means exactly those signatures that are valid and have both similarity measures computed (Firm A 60,448, plus 38,993 / 34,248 / 16,752 at the other three). Non-Big-4 firms enter only in the crossover-scope robustness check (Section V-C), never in the calibration or the headline rates. We then split the Big-4 corpus by firm and by period, giving each part a distinct job (Fig. 1):
+The corpus is all retrievable Taiwan statutory audit reports for fiscal years 2013–2023; the four largest firms (A–D) form the primary analysis sample, and non-Big-4 firms enter only in the crossover-scope robustness check (Section V-C), never in the calibration or the headline rates. Signatures are extracted as described in Section III-C. To be precise about the headline denominator, since it recurs throughout: "150,442 analyzable signatures" means exactly those Big-4 signatures that are valid and have both similarity measures computed, assigned by each accountant's registered firm (Firm A 60,448, Firm B 34,248, Firm C 38,613, Firm D 17,133). We then split the Big-4 corpus by firm and by period, giving each part a distinct job (Fig. 1):
 
 - Calibration (the clean reference group): Firms B/C/D, 2013–2019.
 - Held-out benchmark 1: Firm A, 2013–2023 (a known positive, not a blinded test).
@@ -133,7 +133,7 @@ With no labeled negatives to learn from, the calibration uses a stand-in: a grou
 
 Why not all four firms. As Section IV-C will show, almost all of one firm's between-accountant matches fall on other accountants of the same firm, and we have byte-level proof of image reuse across about fifty of that firm's partners. If we put Firm A into the reference group, we would be filling the "by chance" rate with exactly the within-firm matches the rule is supposed to catch — a circular calibration. So we use Firms B/C/D as the clean reference group and keep Firm A as a test case; we report the all-four-firm number only to show how much Firm A contaminates it.
 
-Why 2013–2019. We further limit the reference group to the years before formal firm-wide electronic-signing systems (adopted from 2020 onward; Section III-A). What this buys us is the absence of a shared template across accountants — not a guarantee that every signature was handwritten. The interviews say some baseline firms used informal individual stamping before 2020, but each accountant's stored image was their own, so different accountants' signatures still match only by chance; the chance rate is about matches between accountants, which individual stamping does not inflate. One further channel deserves to be named, because it is not the template and we cannot fully exclude it: accountants at the same firm pass through a shared imaging pipeline — common scanners, PDF-assembly software, and the red-stamp-removal step (Section III-C, Section V-B) — and a shared pipeline can imprint correlated artefacts on otherwise-unrelated signatures, which would lift the inter-CPA rate above true chance. The pipeline audit of Section V-B confirms that such shared production paths exist and change over time. This is a reason to read the ICCR as a *specificity proxy* rather than a literal coincidence rate; its bias, like reference contamination, runs toward a higher floor, which makes the Firm-A contrast more conservative rather than less. After 2020, formal systems standardize how reports are assembled, so that period is not a clean reference — and indeed the chance rate rises after 2020 (Section V-B). We therefore calibrate on the Firms-B/C/D 2013–2019 cell and score every held-out cell against it.
+Why 2013–2019. We further limit the reference group to the years before formal firm-wide electronic-signing systems (adopted from 2020 onward; Section III-A). What this buys us is the absence of a shared template across accountants — not a guarantee that every signature was handwritten. The interviews say some baseline firms used informal individual stamping before 2020, but each accountant's stored image was their own, so different accountants' signatures still match only by chance; the chance rate is about matches between accountants, which individual stamping does not inflate. One further channel deserves to be named, because it is not the template and we cannot fully exclude it: accountants at the same firm pass through a shared imaging pipeline — common scanners, PDF-assembly software, and the red-stamp-removal step (Section III-C, Section V-B) — and a shared pipeline can imprint correlated artifacts on otherwise-unrelated signatures, which would lift the inter-CPA rate above true chance. The pipeline audit of Section V-B confirms that such shared production paths exist and change over time. This is a reason to read the ICCR as a *specificity proxy* rather than a literal coincidence rate; its bias, like reference contamination, runs toward a higher floor, which makes the Firm-A contrast more conservative rather than less. After 2020, formal systems standardize how reports are assembled, so that period is not a clean reference — and indeed the chance rate rises after 2020 (Section V-B). We therefore calibrate on the Firms-B/C/D 2013–2019 cell and score every held-out cell against it.
 
 We report the rule's chance rate at three levels, because the rule takes the best match over a pool and so the per-signature rate is not the same as the per-pair rate: per comparison (sampled pairs of different accountants), per signature, and per report, each with a confidence interval. We call this the inter-CPA coincidence rate (ICCR) rather than a "false-acceptance rate," which we reserve for settings that have labeled negatives. The ICCR is a *between-accountant* coincidence rate: how often the rule fires on the signatures of two *different* accountants. It is therefore at best a proxy for specificity, and only under the stated assumption (no shared template across accountants). It is important to be exact about what it is not. The quantity the reuse question actually needs is the *within-accountant* false-positive rate — how often the rule would fire on a genuinely consistent hand-signer's own signatures — and that rate is not estimable here, because no accountant in the corpus is labeled as a known hand-signer. We considered benchmarking it against an external corpus of genuine repeated signatures (a public signature dataset supplies many authentic samples per writer), but such corpora are a different population and script acquired under a different pipeline, so the resulting rate would not transfer to this setting; importing it would reintroduce exactly the kind of unverifiable cross-distribution assumption our label-free calibration is built to avoid. We therefore report the limitation rather than a misleading proxy. The ICCR is not even a bound on it: a uniform individual hand keeps cosine high by design, so a true hand-signer's within-accountant fire rate can sit far *above* the between-accountant coincidence rate. Any statement that divides a firm's within-accountant fire rate by this between-accountant floor (an "X× the floor" comparison) therefore overstates the gap — the bias runs in the anti-conservative direction — and we do not report such ratios as effect sizes. Read as a between-accountant specificity proxy under the stated assumption, the ICCR is faithful to the evidence; read as a true error rate for the reuse question, it would claim more than we can show.
 
@@ -149,7 +149,7 @@ This section reports the numbers. It starts with the calibration baseline (Firms
 
 ### A. Detection Sample (Whole Corpus) and the Calibration Baseline (Firms B/C/D, 2013–2019)
 
-Detection and the analysis sample (whole corpus). Two scopes appear in this section and must not be confused: detection and the analysis sample here are computed on the whole corpus, whereas both data-derived calibration quantities — the chance-rate ICCR and the low cosine cut (Section IV-C) — are computed only on the clean Firms-B/C/D 2013–2019 cell. Of the 90,282 reports, the page-finder flagged 86,084 as having a signature page (the other 4,198, or 4.6%, had none); 13 of those 86,084 could not be rendered, leaving 86,071 documents processed. On the validation set, the YOLOv11n detector reached precision 0.97–0.98, recall 0.95–0.98, mAP@0.50 0.98–0.99, and mAP@0.50:0.95 0.85–0.90. Across the corpus it extracted 182,328 signatures — 2.14 per document with detections, where two certifying accountants per report implies 2.00. The ≈6.7% excess is explained by extra detections rather than missed accountants: of the 13,573 detections (7.4%) that could not be matched to a registered accountant and were excluded, 8,901 (66%) are third-or-later detections on a page — boxes beyond the two certifying signatures — and the unmatched set as a whole carries lower detection confidence than the matched set (mean 0.826 vs 0.874), consistent with these being extra boxes and low-confidence noise; the remaining 4,672 are first/second-position detections that failed registry matching. Throughput was 43.1 documents per second, and the detector agreed with the vision-language model on 98.8% of documents. Matching by position assigned 92.6% of signatures (168,755 of 182,328) to a registered accountant; of these, 168,740 have both similarity measures computed (the 15-signature difference is accountants with a single signature in the corpus, for whom no same-accountant comparison exists, so the full-corpus distributional statistics in the Appendix are reported on 168,740). The four-firm analysis sample is 437 accountants (171/112/102/52 across Firms A–D) and 150,442 signatures with both measures computed (Table I).
+Detection and the analysis sample (whole corpus). Two scopes appear in this section and must not be confused: detection and the analysis sample here are computed on the whole corpus, whereas both data-derived calibration quantities — the chance-rate ICCR and the low cosine cut (Section IV-C) — are computed only on the clean Firms-B/C/D 2013–2019 cell. Of the 90,282 reports, the page-finder flagged 86,084 as having a signature page (the other 4,198, or 4.6%, had none); 13 of those 86,084 could not be rendered, leaving 86,071 documents processed. On the validation set, the YOLOv11n detector reached precision 0.97–0.98, recall 0.95–0.98, mAP@0.50 0.98–0.99, and mAP@0.50:0.95 0.85–0.90. Across the corpus it extracted 182,328 signatures — 2.14 per document with detections, where two certifying accountants per report implies 2.00. The ≈6.7% excess is explained by extra detections rather than missed accountants: of the 13,573 detections (7.4%) that could not be matched to a registered accountant and were excluded, 8,901 (66%) are third-or-later detections on a page — boxes beyond the two certifying signatures — and the unmatched set as a whole carries lower detection confidence than the matched set (mean 0.826 vs 0.874), consistent with these being extra boxes and low-confidence noise; the remaining 4,672 are first/second-position detections that failed registry matching. Throughput was 43.1 documents per second, and the detector agreed with the vision-language model on 98.8% of documents. Matching by position assigned 92.6% of signatures (168,755 of 182,328) to a registered accountant; of these, 168,740 have both similarity measures computed (the 15-signature difference is accountants with a single signature in the corpus, for whom no same-accountant comparison exists, so the full-corpus distributional statistics in the Appendix are reported on 168,740). The four-firm analysis sample is 150,442 signatures with both measures computed, from 457 accountants (Table I); the accountant-level partition (Table III, Section V-C) is fit on the 437 of these with at least ten signatures (171/112/102/52 across Firms A–D).
 
 **Table I — Detection and extraction summary.**
 
@@ -161,13 +161,13 @@ Detection and the analysis sample (whole corpus). Two scopes appear in this sect
 | Signatures extracted | 182,328 (2.14 per document) |
 | VLM–detector agreement | 98.8% |
 | Signatures matched to an accountant | 168,755 (92.6%) |
-| Four-firm analysis sample | 437 accountants; 150,442 signatures |
+| Four-firm analysis sample | 457 accountants; 150,442 signatures |
 
 The calibrated operating point: the four cut values and their bases. The five-way rule of Section III-D uses four cut values; we state them here because two are read directly from this study's data. The low cosine cut, 0.8547, is the crossover of the same-accountant and different-accountant cosine distributions computed on the calibration cell alone (Firms B/C/D, 2013–2019, closed-world: both the source signatures and their comparison set drawn from that cell; Section IV-C). We use this closed-world value as the primary cut rather than the corpus-wide crossover, so that the one data-derived threshold in the rule is estimated only on the calibration-only Firms-B/C/D 2013–2019 cell, held out from Firm A and from post-2020 scoring. The cut is stable across scopes — 0.8547 (calibration closed-world), 0.8367 corpus-wide, 0.8489 on the all-period baseline firms, 0.8302 with the non-Big-4 firms added; it moves by at most 0.025 across all four scopes (0.018 from the corpus-wide value), so the choice of scope is immaterial and the broader-scope values stand as robustness checks (Section V-C). The high cosine cut, 0.95, is the high-similarity operating point: it sits in the region where genuine reuse concentrates — the byte-identical anchor (Section IV-C) lies at cosine 1 — and a recalibration cannot move it onto a distributional antimode because none exists (no within-population bimodality, Section V-A). The near-identical structural cut, dHash ≤ 5, is the perceptual-hash distance below which two rasters are pixel-equivalent up to mild recompression, and dHash ≤ 15 bounds the looser "structurally similar" band; both follow the standard 64-bit dHash distance scale [27]. We therefore do not re-derive these three as optimal cutoffs but characterize their chance-of-firing behavior directly (the full prior-calibration provenance is in the supplementary materials), and we make them operator-tunable in one direction: their specificity proxy at these values is read off the chance-rate calibration below, and an operator can tighten the floor by inverting the ICCR curve (for example, dHash ≤ 3). This is a conservativeness dial, not a precision–recall control: tightening raises the specificity proxy and lowers the flag count, but there is no observable recall to trade back, so loosening cannot be calibrated against a known cost. We deliver these as a concrete, calibrated operating point — in particular the high-confidence (HC) rule, cosine > 0.95 and dHash ≤ 5 — whose between-accountant coincidence behavior the calibration below makes explicit. Because the rule is calibrated on a large Chinese-signature corpus, the HC values double as a practical starting reference for practitioners working with comparable Chinese-signature image pipelines, rather than a setting to transplant unchanged.
 
 ![](figures/fig3.png)
 
-*Figure 3. The two measures and the five regions, drawn as the real 2D density of all Big-4 signatures (n = 150,441; log color scale, integer dHash bins). The cosine axis is split at the low cut 0.8547 (the calibration-cell same-vs-different-accountant crossover) and the high cut 0.95; within the high-cosine band the dHash axis is split at 5 and 15. The mass concentrates in the bottom-right HC corner — high cosine with near-identical structure — and thins out as a single continuum toward lower cosine and higher dHash, with no gap separating a "reuse" cluster from a "hand-signed" one (Section V-A); note also that essentially all signatures sit above cosine ≈ 0.85, the compressed high-similarity range discussed in Section V-A.*
+*Figure 3. The two measures and the five regions, drawn as the real 2D density of all Big-4 signatures (n = 150,442; log color scale, integer dHash bins). The cosine axis is split at the low cut 0.8547 (the calibration-cell same-vs-different-accountant crossover) and the high cut 0.95; within the high-cosine band the dHash axis is split at 5 and 15. The mass concentrates in the bottom-right HC corner — high cosine with near-identical structure — and thins out as a single continuum toward lower cosine and higher dHash, with no gap separating a "reuse" cluster from a "hand-signed" one (Section V-A); note also that essentially all signatures sit above cosine ≈ 0.85, the compressed high-similarity range discussed in Section V-A.*
 
 The calibration sample itself (Firms B/C/D, 2013–2019). The chance-rate calibration that follows is computed on the clean cell only, and the reader should be able to see the calibration base directly rather than infer it from the full-period totals above. The Firms-B/C/D 2013–2019 cell contains 226 accountants, 52,071 signatures with both measures computed, and 26,042 reports; the per-comparison ICCR below is estimated from 5×10⁵ inter-CPA signature pairs sampled uniformly from this cell. Every ICCR source signature is restricted to this cell — the headline per-signature and per-document rates reproduce on the 52,071-signature 2013–2019 cell, not on the full-period BCD record (~90,000 signatures), which is used only where a robustness figure is explicitly quoted — so no post-2020 or Firm-A signature enters the calibration.
 
@@ -213,13 +213,13 @@ Why this is exception management rather than caseload. Where a firm's output is
 
 Firm A — described by the interviews as a mainly-stamping firm, and kept out of the calibration — is our main benchmark. Because the interviews already identify it as a stamping firm, it is best read as a *quasi-positive institutional benchmark*: held out from calibration, but a known positive rather than a blinded out-of-sample test. What it can confirm is that the screen's measures move as expected on a firm independently believed to reuse images; what it cannot do is stand in for a blinded evaluation against ground-truth labels, which the corpus does not provide.
 
-(1) Firm A's two measures against the baseline. Comparing Firm A's within-accountant similarities to those of Firms B/C/D (full record, 2013–2023²), Firm A's cos values are shifted toward 1.0 and its dHash distances toward 0 — the direction we would expect if a stored image is reused rather than re-signed. Concretely, Firm A's within-accountant cosine is centred at a median of 0.986 (mean 0.980) versus 0.959 (mean 0.954) for Firms B/C/D, and its smallest-dHash distance at a median of 2 (mean 2.7) versus 7 (mean 7.0); both shifts are in the reuse direction and overwhelmingly significant (Mann–Whitney U, p < 10⁻³⁰⁰ for each; two-sample Kolmogorov–Smirnov D = 0.60 for cosine and 0.57 for dHash). The decisive number is this: scored as a held-out (but not blinded) case — Firm A's signatures matched against unrelated accountants drawn from the clean 2013–2019 group — Firm A's per-signature cross-firm HC rate is 0.42% (154/36,552; Wilson 95% CI [0.36%, 0.49%]), at or below the clean reference ICCR of 0.59%. In other words, Firm A's cross-firm match rate sits at the level a clean inter-CPA comparison produces by chance — it is not elevated relative to the reference, and it is negligible beside the within-firm rate below — so the entire rise in Firm A's rate comes from matches with other Firm-A signatures, not from resemblance to other firms. The signal is inside the firm, not across firms. (Against the full-period BCD pool the same across-firm rate is 1.0%; the small difference reflects the post-2020 rise in baseline similarity of Section V-B. Both lie at the clean floor, two orders of magnitude below the within-firm rate that follows.)
+(1) Firm A's two measures against the baseline. Comparing Firm A's within-accountant similarities to those of Firms B/C/D (full record, 2013–2023²), Firm A's cos values are shifted toward 1.0 and its dHash distances toward 0 — the direction we would expect if a stored image is reused rather than re-signed. Concretely, Firm A's within-accountant cosine is centered at a median of 0.986 (mean 0.980) versus 0.959 (mean 0.954) for Firms B/C/D, and its smallest-dHash distance at a median of 2 (mean 2.7) versus 7 (mean 7.0); both shifts are in the reuse direction and overwhelmingly significant (Mann–Whitney U, p < 10⁻³⁰⁰ for each; two-sample Kolmogorov–Smirnov D = 0.60 for cosine and 0.57 for dHash). The decisive number is this: scored as a held-out (but not blinded) case — Firm A's signatures matched against unrelated accountants drawn from the clean 2013–2019 group — Firm A's per-signature cross-firm HC rate is 0.42% (154/36,552; Wilson 95% CI [0.36%, 0.49%]), at or below the clean reference ICCR of 0.59%. In other words, Firm A's cross-firm match rate sits at the level a clean inter-CPA comparison produces by chance — it is not elevated relative to the reference, and it is negligible beside the within-firm rate below — so the entire rise in Firm A's rate comes from matches with other Firm-A signatures, not from resemblance to other firms. The signal is inside the firm, not across firms. (Against the full-period BCD pool the same across-firm rate is 1.0%; the small difference reflects the post-2020 rise in baseline similarity of Section V-B. Both lie at the clean floor, two orders of magnitude below the within-firm rate that follows.)
 
-> ² Restricting both groups to 2013–2019 gives essentially the same picture (Firm A cosine median 0.986, dHash 2; Firms B/C/D 0.957 and 7; Mann–Whitney p < 10⁻³⁰⁰ for each), confirming the contrast is not a post-2020 artefact.
+> ² Restricting both groups to 2013–2019 gives essentially the same picture (Firm A cosine median 0.986, dHash 2; Firms B/C/D 0.957 and 7; Mann–Whitney p < 10⁻³⁰⁰ for each), confirming the contrast is not a post-2020 artifact.
 
 Firm A's within-firm repeatability, against the other firms. On their own signatures, the HC rule fires on 82% of Firm A's, versus 24–35% for Firms B/C/D. We deliberately report these as raw within-accountant fire rates and do not divide them by the between-accountant clean floor: as Section III-E explains, that floor is the wrong null for a within-accountant question, so an "X× the floor" multiplier would overstate the gap. The firm-to-firm contrast in raw rates is what carries the result. A logistic regression of the per-signature HC flag on firm and pool size, with Firm A as the reference, gives odds ratios of 0.053, 0.010, and 0.027 for Firms B/C/D — one to two orders of magnitude lower (the odds ratio for log pool size is 4.01). Firm A stands alone, against a baseline of three firms that look alike.
 
-Four further checks confirm the contrast is not an artefact of how the comparison pools are built, of the imaging-pipeline trend, or of any single year. First, pool size. Stratifying accountants by how many signatures they contribute and comparing within each stratum, Firm A's HC rate exceeds the other firms' at every level — 66% versus 20% for the smallest pools (under 50 signatures), rising to 76–84% versus 21–29% for larger pools. Even Firm-A accountants with few signatures to match against fire the rule far more often than B/C/D accountants with the same pool size; pool size raises the rate within every firm (the log-pool-size odds ratio of 4.01), but the firm gap dwarfs it and survives at fixed pool size, which rules out the "more signatures, more chances for an extreme match" explanation. Second, dependence among an accountant's own signatures. Re-estimating the gap with the bootstrap resampled at the accountant level (179 Firm-A accountants, 280 at Firms B/C/D) rather than treating signatures as independent, the Firm-A-minus-B/C/D difference in HC rate is 53.7 percentage points with a 95% interval of [49.5, 57.5] — accountant-level clustering widens the intervals the per-signature Wilson bounds give, but leaves the contrast far too large to be explained away. Third, the time trend and pipeline shift (Section V-B). Adding year fixed effects to the logistic regression — so the firm effect is identified within year, net of the 2020–2021 imaging-pipeline transition — leaves Firms B/C/D at 0.06–0.12 times Firm A's odds of an HC flag (odds ratios 0.116, 0.061, 0.070), still an order of magnitude lower once the common time trend is absorbed. Fourth, single-year dependence. Leaving out each calendar year in turn and recomputing, the Firm-A-minus-B/C/D gap stays within 53.1–54.9 percentage points (full-sample 53.7), so neither the high-reuse digital-native years (2022–2023) nor any earlier year drives it.
+Four further checks confirm the contrast is not an artifact of how the comparison pools are built, of the imaging-pipeline trend, or of any single year. First, pool size. Stratifying accountants by how many signatures they contribute and comparing within each stratum, Firm A's HC rate exceeds the other firms' at every level — 66% versus 20% for the smallest pools (under 50 signatures), rising to 76–84% versus 21–29% for larger pools. Even Firm-A accountants with few signatures to match against fire the rule far more often than B/C/D accountants with the same pool size; pool size raises the rate within every firm (the log-pool-size odds ratio of 4.01), but the firm gap dwarfs it and survives at fixed pool size, which rules out the "more signatures, more chances for an extreme match" explanation. Second, dependence among an accountant's own signatures. Re-estimating the gap with the bootstrap resampled at the accountant level (179 Firm-A accountants, 280 at Firms B/C/D) rather than treating signatures as independent, the Firm-A-minus-B/C/D difference in HC rate is 53.7 percentage points with a 95% interval of [49.5, 57.5] — accountant-level clustering widens the intervals the per-signature Wilson bounds give, but leaves the contrast far too large to be explained away. Third, the time trend and pipeline shift (Section V-B). Adding year fixed effects to the logistic regression — so the firm effect is identified within year, net of the 2020–2021 imaging-pipeline transition — leaves Firms B/C/D at 0.06–0.12 times Firm A's odds of an HC flag (odds ratios 0.116, 0.061, 0.070), still an order of magnitude lower once the common time trend is absorbed. Fourth, single-year dependence. Leaving out each calendar year in turn and recomputing, the Firm-A-minus-B/C/D gap stays within 53.1–54.9 percentage points (full-sample 53.7), so neither the high-reuse digital-native years (2022–2023) nor any earlier year drives it.
 
 ![](figures/fig4.png)
 
@@ -227,7 +227,7 @@ Four further checks confirm the contrast is not an artefact of how the compariso
 
 (2) Ranking accountants by similarity, in each period. Ranking every accountant in Firms A–D by a single within-accountant similarity score, separately for 2013–2019 and for 2020–2023, Firm A's accountants sit at the high-similarity (templated) end. A descriptive three-group summary of the two-measure space tells the same story: its high-cosine/low-dHash group holds 82.5% of Firm A's accountants and almost none of the others' (Table III). The period split confirms the expected pattern: Firm A's per-signature HC rate is at the top in both periods (80.3% in 2013–2019, 83.8% in 2020–2023), while Firms B/C/D move upward after 2020 as the formal systems came in — Firm B from 29.0% to 42.0%, Firm C from 21.6% to 26.7%, Firm D from 22.0% to 28.0% (see Section V-B).
 
-**Table III — Firm by descriptive-group membership (whole corpus). The "high-cosine/low-dHash group" is the templated-end cluster of the three-group (K = 3) descriptive Gaussian-mixture partition of the accountant-level two-measure plane (Section V-C); membership is the cluster of maximum posterior probability for each accountant. The groups are used for description only, never as operational labels.**
+**Table III — Firm by descriptive-group membership (whole corpus). The "high-cosine/low-dHash group" is the templated-end cluster of the three-group (K = 3) descriptive Gaussian-mixture partition of the accountant-level two-measure plane (Section V-C); membership is the cluster of maximum posterior probability for each accountant with at least ten signatures (437 accountants: 171/112/102/52 across Firms A–D). The groups are used for description only, never as operational labels.**
 
 | Firm | Accountants | Share in the high-cosine/low-dHash group |
 |---|---|---|
@@ -254,7 +254,7 @@ Four further checks confirm the contrast is not an artefact of how the compariso
 
 Reading the five-way mix across firms. Table IV is also the quantitative basis for the positioning in Section IV-B. At Firm A the ambiguous middle (MC + UN) is 18.1% — the screen reads this population almost cleanly, with four signatures in five settled outright. At Firms B/C/D the middle is 65–76% — the signature of a mixed population in which hand-signing and informal stamping coexist (Section III-A), where per-signature similarity is genuinely ambiguous. There the screen's deliverables move up one level (Section IV-B): the MC share (29–41% of these firms' signatures, against the 26.5% corpus-wide MC share) is demoted off the worklist, the accountant-level scores rank these firms' accountants alongside everyone else's, and the byte-identical signatures at these firms (117 of the 262) are threshold-free proof that reuse occurs there too. The per-signature mix stays ambiguous; the disposition does not.
 
-(+) Byte-identical signatures: direct evidence of reuse. Beyond the screening numbers, 262 signatures across the four firms are byte-for-byte identical to another signature — 145 of them at Firm A, spread across about fifty partners. Identical files cannot come from independent hand-signing, so their existence is direct, hard evidence that image reuse happens and that it concentrates at Firm A. These pairs are not a bookkeeping artefact: every one of the 262 matches a signature in a *different* report PDF (none is the same file double-counted), and 170 of the 262 fall in different filing months, so duplicate filings or corrected re-submissions of one report cannot explain them. One caveat belongs with this count, developed in Section V-B: most of the 262 (232) occur in the post-2020 digital-native era, where exact reuse is both easier and perfectly preserved, so the raw count is not a clean prevalence trend; the pipeline-independent core is the 30 in the pre-2021 pure-scan era (18 at Firm A), which scanning noise alone cannot produce. Because a byte-identical pair has cosine = 1 and dHash = 0, it lands in HC by definition; the rule's "100% capture" of this set is therefore tautological, and we do not read it as a sanity check or a lower bound on recall. We use byte-identity only for what it can show directly — that reuse occurs and where it concentrates — as a prevalence signal, not a measure of detector performance.
+Byte-identical signatures: direct evidence of reuse. Beyond the screening numbers, 262 signatures across the four firms are byte-for-byte identical to another signature — 145 of them at Firm A, spread across about fifty partners. Identical files cannot come from independent hand-signing, so their existence is direct, hard evidence that image reuse happens and that it concentrates at Firm A. These pairs are not a bookkeeping artifact: every one of the 262 matches a signature in a *different* report PDF (none is the same file double-counted), and 170 of the 262 fall in different filing months, so duplicate filings or corrected re-submissions of one report cannot explain them. One caveat belongs with this count, developed in Section V-B: most of the 262 (232) occur in the post-2020 digital-native era, where exact reuse is both easier and perfectly preserved, so the raw count is not a clean prevalence trend; the pipeline-independent core is the 30 in the pre-2021 pure-scan era (18 at Firm A), which scanning noise alone cannot produce. Because a byte-identical pair has cosine = 1 and dHash = 0, it lands in HC by definition; the rule's "100% capture" of this set is therefore tautological, and we do not read it as a sanity check or a lower bound on recall. We use byte-identity only for what it can show directly — that reuse occurs and where it concentrates — as a prevalence signal, not a measure of detector performance.
 
 ## V. Other Analyses
 
@@ -262,13 +262,13 @@ This section gathers analyses that support the design and test its robustness: (
 
 ### A. Why the Data Contain No Natural Cutoff
 
-This diagnostic backs the design choice announced in Section III-D and Section III-E: that no cutoff can be read off the data, so the operating point has to be set from an outside reference. The Hartigan dip test [37] rejects a single-peak shape for both measures at the Big-4-pooled accountant level (p < 5×10⁻⁴), which might look like a clean split into two groups. But that rejection comes from two side-effects. Once we remove the differences between firms (by centering each firm on its own mean) and the effect of the hash taking only whole-number values (by adding a small jitter to dHash), the single-peak shape comes back (median p = 0.35 over jitter seeds). Tested firm by firm, each Big-4 firm is already unimodal on both axes (Firm A p_cos = 0.99, p_dHash = 0.92; B/C/D pooled p_cos = 0.998, p_dHash = 0.91), so the pooled rejection is a between-firm location-shift artefact, not within-population bimodality. A density-smoothness test in the Burgstahler–Dichev / McCrary style [38], [39] finds no real break in either measure at the Big-4 scope (Appendix A.1 shows the apparent signature-level breaks drift with histogram bin width and sit inside the high-similarity region — a resolution artefact, not an antimode). So the data hold no real gap; per-signature similarity is best read as one continuous spread of quality, not two separate classes. This is exactly why the operating point is set from an outside reference (Section III-E) rather than read off the data, and why the three groups used for description in Section IV-C are treated as a summary of composition, not as real mechanisms.
+This diagnostic backs the design choice announced in Section III-D and Section III-E: that no cutoff can be read off the data, so the operating point has to be set from an outside reference. The Hartigan dip test [37] rejects a single-peak shape for both measures at the Big-4-pooled accountant level (p < 5×10⁻⁴), which might look like a clean split into two groups. But that rejection comes from two side-effects. Once we remove the differences between firms (by centering each firm on its own mean) and the effect of the hash taking only whole-number values (by adding a small jitter to dHash), the single-peak shape comes back (median p = 0.35 over jitter seeds). Tested firm by firm, each Big-4 firm is already unimodal on both axes (Firm A p_cos = 0.99, p_dHash = 0.92; B/C/D pooled p_cos = 0.998, p_dHash = 0.91), so the pooled rejection is a between-firm location-shift artifact, not within-population bimodality. A density-smoothness test in the Burgstahler–Dichev / McCrary style [38], [39] finds no real break in either measure at the Big-4 scope (Appendix A.1 shows the apparent signature-level breaks drift with histogram bin width and sit inside the high-similarity region — a resolution artifact, not an antimode). So the data hold no real gap; per-signature similarity is best read as one continuous spread of quality, not two separate classes. This is exactly why the operating point is set from an outside reference (Section III-E) rather than read off the data, and why the three groups used for description in Section IV-C are treated as a summary of composition, not as real mechanisms.
 
 A property of the cosine measure reinforces this and explains why the rule never leans on cosine alone. On these fixed-size, white-padded, ImageNet-normalized crops the within-accountant cosine is compressed into a narrow band at the top of its range: 97.7% of signatures score above 0.90, the median is 0.969, and only 0.3% fall below 0.85 (Appendix). Two signatures of the same accountant are highly cosine-similar whether the hand is steady or the image is reused, because the shared crop geometry and normalization contribute a common-structure baseline before any signature content is compared. The high cosine cut (0.95) therefore sits *inside* this saturated region — about three-quarters of signatures lie above it — so cosine on its own separates almost nothing; the structural dHash measure does the discriminating, which is why HC requires both and the cosine-only HSC band carries no evidential weight (Section III-D). We do not try to decompose this cosine baseline into its preprocessing and genuine-style parts here: doing so cleanly would mean re-extracting features with the padding and normalization ablated, which we flag as the way to quantify the preprocessing contribution and as a construct-validity check for future work.
 
 ### B. Time Trend and the Firm–Pipeline Confound (Secondary)
 
-Looking only at Firms B/C/D, the strict rule's chance rate rises after 2020 (per comparison from 1.0×10⁻⁵ to 3.6×10⁻⁵; per signature from 0.59% to 1.05%), and the deployed HC rate rises in parallel (Firm B 29.0→42.0%, Firm C 21.5→26.5%, Firm D 22.1→28.5% across the two periods, Section IV-C). The rise is heterogeneous in timing rather than a common step. Tracing the yearly HC rate, Firm C's increase is concentrated in 2022 (about 18% through 2021, then ~30% in 2022 and ~40% in 2023) and Firm B's mainly in 2023 (about 33% in 2022, ~54% in 2023), while Firm D rises gradually with no visible step; Firm A, by contrast, is already high throughout the decade (80.3→83.8%) with no adoption-like jump — consistent with the interviews' account of long-standing stamping. This firm-by-firm staggering is what one would expect from progressive, independent adoption of formal signing systems (Section III-A), and it is why we limit the calibration to the pre-2020 years. Table II-c gives the full five-way breakdown by firm for the 2020–2023 deployment period, as a companion to the calibration-period Table II-b and for direct cross-checking against the proportions quoted here and in Section IV-C.
+Looking only at Firms B/C/D, the strict rule's chance rate rises after 2020 (per comparison from 1.0×10⁻⁵ to 3.6×10⁻⁵; per signature from 0.59% to 1.05%), and the deployed HC rate rises in parallel (Firm B 29.0→42.0%, Firm C 21.6→26.7%, Firm D 22.0→28.0% across the two periods, Section IV-C). The rise is heterogeneous in timing rather than a common step. Tracing the yearly HC rate, Firm C's increase is concentrated in 2022 (about 18% through 2021, then ~30% in 2022 and ~40% in 2023) and Firm B's mainly in 2023 (about 33% in 2022, ~54% in 2023), while Firm D rises gradually with no visible step; Firm A, by contrast, is already high throughout the decade (80.3→83.8%) with no adoption-like jump — consistent with the interviews' account of long-standing stamping. This firm-by-firm staggering is what one would expect from progressive, independent adoption of formal signing systems (Section III-A), and it is why we limit the calibration to the pre-2020 years. Table II-c gives the full five-way breakdown by firm for the 2020–2023 deployment period, as a companion to the calibration-period Table II-b and for direct cross-checking against the proportions quoted here and in Section IV-C.
 
 **Table II-c — Five-way breakdown by firm, deployment period (Firms A–D, 2020–2023).**
 
@@ -276,8 +276,8 @@ Looking only at Firms B/C/D, the strict rule's chance rate rises after 2020 (per
 |---|---|---|---|---|---|---|
 | Firm A | 83.84% | 9.13% | 0.04% | 6.88% | 0.11% | 23,898 |
 | Firm B | 42.01% | 31.24% | 0.16% | 26.31% | 0.28% | 14,571 |
-| Firm C | 26.53% | 40.78% | 0.41% | 31.77% | 0.51% | 16,485 |
-| Firm D | 28.53% | 27.75% | 0.20% | 42.98% | 0.54% | 6,866 |
+| Firm C | 26.74% | 40.55% | 0.40% | 31.80% | 0.51% | 16,164 |
+| Firm D | 27.98% | 28.85% | 0.24% | 42.42% | 0.51% | 7,188 |
 
 We deliberately stop short of reading this as a *detected* e-signing effect, because of a confound these data cannot break: firm identity — and period within a firm — bundles signing practice together with the entire imaging pipeline, and that pipeline demonstrably changes across the decade. We audited the production provenance of a stratified sample of 880 report PDFs (20 per firm-year) from their embedded metadata and page structure. The shift is stark (Table V): through 2020, reports are overwhelmingly plain scanned rasters — 70–85% in the early years carry no text layer at all, and their PDF metadata names the scanning hardware directly (for example "Fuji Xerox D125" and "ApeosPort-IV 7080") — whereas from 2021 plain scans collapse to about 1–2% as firms move to OCR'd and digital-native production. The two similarity measures are therefore computed on a substrate that itself transforms around 2020–2021, exactly when the baseline firms' similarity rises; firms also differ from one another in this respect (Firm A adopts digital-native output earliest, Firm C latest), though the cross-firm gap is much smaller than the temporal one. A post-2020 rise in similarity could thus come from this coincident pipeline change just as easily as from a change in how signatures are applied (Section III-D), and with no labels and no externally-dated adoption events the two are not separable here.
 
@@ -302,17 +302,17 @@ We summarize the robustness checks here; full detail is in the supplementary mat
 
 How sensitive the operating point is. Right around the HC cutoff the per-signature firing rate changes quickly — its local slope is about 25× the median across a cosine sweep and about 3.8× across a dHash sweep — which confirms that the HC point is a chosen, specificity-anchored operating point rather than a natural gap.
 
-A single slope understates how the rule behaves, so we map the full surface rather than defend one cut. Figure 6 plots, over the entire (cosine cut × dHash cut) plane, the clean-group flag rate (panel a) and the Firm A − B/C/D flag-rate contrast (panel b), and neither view favours the chosen cut by construction. First, the surfaces are smooth: there is no cliff at (0.95, dHash ≤ 5), so the operating point is a readable choice on a continuous trade-off rather than a discovered boundary (Section V-A), and an operator who wants a tighter floor can move toward higher cosine and lower dHash and read the consequence off the surface. Second, the firm contrast is not an artefact of the threshold: it exceeds 45 percentage points across a broad region of low-dHash, high-cosine cuts and in fact grows as the cut tightens (for example 58 pp at cosine 0.97, dHash ≤ 3), so the deliberately looser HC point trades a few points of contrast for catching more reuse, not the reverse. The same surface makes the weakness of the cosine-only direction explicit: extending the structural cut to the MC bound (dHash ≤ 15) roughly halves the contrast (to about 27 pp) while sharply inflating the clean-group flag rate. That is precisely why the MC band is only advisory and the cosine-only HSC band carries no weight (Section III-D): the partition is not drawn to flatter the narrative, and the surface shows directly where each band earns its keep and where it does not.
+A single slope understates how the rule behaves, so we map the full surface rather than defend one cut. Figure 6 plots, over the entire (cosine cut × dHash cut) plane, the clean-group flag rate (panel a) and the Firm A − B/C/D flag-rate contrast (panel b), and neither view favors the chosen cut by construction. First, the surfaces are smooth: there is no cliff at (0.95, dHash ≤ 5), so the operating point is a readable choice on a continuous trade-off rather than a discovered boundary (Section V-A), and an operator who wants a tighter floor can move toward higher cosine and lower dHash and read the consequence off the surface. Second, the firm contrast is not an artifact of the threshold: it exceeds 45 percentage points across a broad region of low-dHash, high-cosine cuts and in fact grows as the cut tightens (for example 58 pp at cosine 0.97, dHash ≤ 3), so the deliberately looser HC point trades a few points of contrast for catching more reuse, not the reverse. The same surface makes the weakness of the cosine-only direction explicit: extending the structural cut to the MC bound (dHash ≤ 15) roughly halves the contrast (to about 27 pp) while sharply inflating the clean-group flag rate. That is precisely why the MC band is only advisory and the cosine-only HSC band carries no weight (Section III-D): the partition is not drawn to flatter the narrative, and the surface shows directly where each band earns its keep and where it does not.
 
 ![](figures/fig6.png)
 
-*Figure 6. Sensitivity surface of the deployed rule over the two-measure threshold plane (Big-4, n = 150,441). (a) Clean-group (B/C/D) flag rate at each (cosine cut, dHash cut); the chosen HC operating point (star) sits in a low-rate, high-specificity region with no cliff. (b) Firm A minus B/C/D flag-rate contrast (percentage points); the contrast exceeds 45 pp across a broad low-dHash, high-cosine band and weakens toward the MC bound (dHash ≤ 15, dotted), so the operating point is not a cherry-picked threshold and the MC band is visibly the less discriminating region.* The MC/HSC boundary at dHash = 15 sits in a flat (saturating) region, where moving the line adds flagged cases without adding specificity; this is a further reason to treat the MC band as advisory (Section IV-B).
+*Figure 6. Sensitivity surface of the deployed rule over the two-measure threshold plane (Big-4, n = 150,442). (a) Clean-group (B/C/D) flag rate at each (cosine cut, dHash cut); the chosen HC operating point (star) sits in a low-rate, high-specificity region with no cliff. (b) Firm A minus B/C/D flag-rate contrast (percentage points); the contrast exceeds 45 pp across a broad low-dHash, high-cosine band and weakens toward the MC bound (dHash ≤ 15, dotted), so the operating point is not a cherry-picked threshold and the MC band is visibly the less discriminating region.* The MC/HSC boundary at dHash = 15 sits in a flat (saturating) region, where moving the line adds flagged cases without adding specificity; this is a further reason to treat the MC band as advisory (Section IV-B).
 
 Leaving out one firm at a time. A two-group fit is unstable across firms — its boundary is basically a "Firm A versus the rest" divider — while a three-group fit keeps a stable shape (its low-cosine/high-dHash group drifts by at most 0.005 in cosine) but a membership that shifts with the mix of firms (by up to 12.8 percentage points). So we use the groups only as descriptions, never as operational labels.
 
 Crossover scope. The low cosine cut is the same-vs-different-accountant cosine crossover; recomputing it across scopes moves it by at most 0.025 — 0.8547 on the calibration cell (the primary value; Section IV-A), 0.8367 corpus-wide, 0.8489 on the all-period baseline firms, 0.8302 with the non-Big-4 firms added — and because the cut affects only the UN/LH boundary, switching among these scopes changes no HC/MC/HSC result and shifts the UN/LH split by at most 0.4 percentage points per firm. We use the calibration-cell value as primary for held-out discipline and report the others as robustness.
 
-The same-pair variant. A reader may worry that the deployed rule is a *derived* statistic rather than an observation: the cosine maximum and the dHash minimum are each taken over the accountant's pool and can originate from different partner signatures, so the high-confidence region might in principle be assembled from two unrelated extrema. We therefore recompute the rule under the strict *same-pair* construction, where a single partner signature must satisfy both inequalities at once (Section III-D), and report it in the main text rather than the supplement. Two views agree. First, the within-firm concentration of cross-accountant matches is higher under same-pair (97.0–99.96% across the four firms) than under the deployed any-pair rule (76.7–98.8%). Second, and more directly, the per-signature HC flag rate — the quantity the any-pair concern targets — behaves the same way (Table VI): requiring one partner to satisfy both inequalities lowers every firm's rate, as expected, but it *widens* the firm gap rather than narrowing it. Firm A still fires on a majority of its own signatures (57.3%) while the baseline firms fall to 5–9%, so the Firm-A-to-baseline ratio rises from about 2.4–3.4× under any-pair to about 6.4–10.8× under same-pair. The high-confidence region is therefore not an artefact of combining extrema from different partner signatures; pushed to the stricter event, the structure gets stronger.
+The same-pair variant. A reader may worry that the deployed rule is a *derived* statistic rather than an observation: the cosine maximum and the dHash minimum are each taken over the accountant's pool and can originate from different partner signatures, so the high-confidence region might in principle be assembled from two unrelated extrema. We therefore recompute the rule under the strict *same-pair* construction, where a single partner signature must satisfy both inequalities at once (Section III-D), and report it in the main text rather than the supplement. Two views agree. First, the within-firm concentration of cross-accountant matches is higher under same-pair (97.0–99.96% across the four firms) than under the deployed any-pair rule (76.7–98.8%). Second, and more directly, the per-signature HC flag rate — the quantity the any-pair concern targets — behaves the same way (Table VI): requiring one partner to satisfy both inequalities lowers every firm's rate, as expected, but it *widens* the firm gap rather than narrowing it. Firm A still fires on a majority of its own signatures (57.3%) while the baseline firms fall to 5–9%, so the Firm-A-to-baseline ratio rises from about 2.4–3.4× under any-pair to about 6.4–10.8× under same-pair. The high-confidence region is therefore not an artifact of combining extrema from different partner signatures; pushed to the stricter event, the structure gets stronger.
 
 **Table VI — HC flag rate by firm under the deployed any-pair rule and the strict same-pair rule.**
 
@@ -320,9 +320,9 @@ The same-pair variant. A reader may worry that the deployed rule is a *derived*
 |---|---|---|---|
 | Firm A | 60,448 | 81.7% | 57.3% |
 | Firm B | 34,248 | 34.6% | 9.0% |
-| Firm C | 38,993 | 23.7% | 5.3% |
-| Firm D | 16,752 | 24.7% | 7.7% |
-| All Big-4 | 150,441 | 49.6% | 27.3% |
+| Firm C | 38,613 | 23.7% | 5.3% |
+| Firm D | 17,133 | 24.5% | 7.7% |
+| All Big-4 | 150,442 | 49.6% | 27.3% |
 
 Each gate adds specificity. On the all-four-firm pool the cosine gate alone fires per comparison at 6.0×10⁻⁴; adding the structural gate multiplies this by 0.234 (the conditional ICCR of dHash ≤ 5 given cos > 0.95), giving the joint 1.4×10⁻⁴. Each axis contributes specificity beyond the other — quantitative support for the two-gate design over either measure alone (Section I, Section III-D).
 
@@ -384,7 +384,7 @@ The unsupervised-diagnostic strategy is a set of complementary checks, each addr
 
 | Diagnostic | Failure mode addressed | Disclosed untested assumption |
 |---|---|---|
-| Composition decomposition (Section V-A) | Whether descriptor multimodality is within-population (mechanism) or between-group (composition + integer artefact); p_median = 0.35 under joint firm-mean centering + integer-tie jitter | Integer-tie jitter and firm-mean centering are unbiased over the descriptor support |
+| Composition decomposition (Section V-A) | Whether descriptor multimodality is within-population (mechanism) or between-group (composition + integer artifact); p_median = 0.35 under joint firm-mean centering + integer-tie jitter | Integer-tie jitter and firm-mean centering are unbiased over the descriptor support |
 | Per-comparison ICCR (Section IV-A) | Pair-level specificity proxy under a random-pair negative anchor, on the BCD baseline | Inter-CPA pairs are negative; addressed by anchoring on B/C/D and holding Firm A out |
 | Pool-normalised per-signature ICCR (Section IV-A) | Deployed-rule specificity proxy at per-signature unit, accounting for pool size | As above + pool replacement preserves the negative-anchor property |
 | Document-level ICCR (Section IV-A) | Operational alarm-rate proxy at per-document unit (HC and HC+MC) | As above |
@@ -396,11 +396,11 @@ The unsupervised-diagnostic strategy is a set of complementary checks, each addr
 
 ## Appendix B. Reproducibility Materials
 
-The full table-to-script provenance mapping, script source code, and report artefacts for every numerical table and figure in this paper are provided in the supplementary materials. Scripts run deterministically under fixed random seeds documented there (the inter-CPA candidate sampler uses seed 42 and a retry-loop matching the canonical samplers; CPA-block bootstraps use 1,000 replicates); reviewer reproduction should re-emit artefacts from the listed scripts rather than rely on any local path layout. The calibration baseline (BCD 2013–2019), the contamination-comparison scope (all-Big-4), the Firm-A out-of-sample scoring, and the five-way classification are all emitted by the same canonical pipeline so that the headline numbers in Tables I, II, II-b, and IV reproduce bit-for-bit.
+The full table-to-script provenance mapping, script source code, and report artifacts for every numerical table and figure in this paper are provided in the supplementary materials. Scripts run deterministically under fixed random seeds documented there (the inter-CPA candidate sampler uses seed 42 and a retry-loop matching the canonical samplers; CPA-block bootstraps use 1,000 replicates); reviewer reproduction should re-emit artifacts from the listed scripts rather than rely on any local path layout. The calibration baseline (BCD 2013–2019), the contamination-comparison scope (all-Big-4), the Firm-A out-of-sample scoring, and the five-way classification are all emitted by the same canonical pipeline so that the headline numbers in Tables I, II, II-b, and IV reproduce bit-for-bit.
 
 ## References
 
-*References follow IEEE numeric style; entries [41]–[45] are the behavioural-science and Chinese-script works added in this draft.*
+*References follow IEEE numeric style; entries [41]–[45] are the behavioral-science and Chinese-script works added in this draft.*
 
 [1] Taiwan Certified Public Accountant Act (會計師法), Art. 4; FSC Attestation Regulations (查核簽證核准準則), Art. 6.
 
@@ -496,4 +496,4 @@ The full table-to-script provenance mapping, script source code, and report arte
 
 **Conflict of interest.** The authors declare no conflict of interest with Firm A, Firm B, Firm C, or Firm D, or with any other entity referenced in this work.
 
-**Data availability.** All audit reports analysed in this study were obtained from the Market Observation Post System (MOPS) operated by the Taiwan Stock Exchange Corporation, a publicly accessible regulatory disclosure platform. The CPA registry used to map signatures to certifying CPAs is publicly available. The reproducibility scripts and trained model weights are provided in the supplementary materials; signature-image release is subject to the firm-anonymization constraints of Section III-A (a de-identified subset and the per-table provenance mapping are included, with the full image set available to reviewers under the platform's public-data terms).
+**Data availability.** All audit reports analyzed in this study were obtained from the Market Observation Post System (MOPS) operated by the Taiwan Stock Exchange Corporation, a publicly accessible regulatory disclosure platform. The CPA registry used to map signatures to certifying CPAs is publicly available. The reproducibility scripts and trained model weights are provided in the supplementary materials; signature-image release is subject to the firm-anonymization constraints of Section III-A (a de-identified subset and the per-table provenance mapping are included, with the full image set available to reviewers under the platform's public-data terms).

paper/v13_build/scripts/make_fig3_density.py

@@ -15,11 +15,11 @@ BIG4 = ('勤業眾信聯合', '資誠聯合', '安侯建業聯合', '安永聯
 con = sqlite3.connect(DB)
 cur = con.cursor()
 cur.execute(f"""
-SELECT max_similarity_to_same_accountant, min_dhash_independent
-FROM signatures
-WHERE is_valid=1 AND max_similarity_to_same_accountant IS NOT NULL
-  AND min_dhash_independent IS NOT NULL
-  AND excel_firm IN ({','.join(['?']*4)})
+SELECT s.max_similarity_to_same_accountant, s.min_dhash_independent
+FROM signatures s JOIN accountants a ON s.assigned_accountant=a.name
+WHERE s.max_similarity_to_same_accountant IS NOT NULL
+  AND s.min_dhash_independent IS NOT NULL
+  AND a.firm IN ({','.join(['?']*4)})
 """, BIG4)
 rows = cur.fetchall()
 con.close()

paper/v13_build/scripts/make_fig6_sensitivity.py

@@ -14,10 +14,11 @@ DB = "/Volumes/NV2/PDF-Processing/signature-analysis/signature_analysis.db"
 BIG4 = ('勤業眾信聯合', '資誠聯合', '安侯建業聯合', '安永聯合')
 
 con = sqlite3.connect(DB); cur = con.cursor()
-cur.execute(f"""SELECT CASE WHEN excel_firm='勤業眾信聯合' THEN 1 ELSE 0 END isA,
-  max_similarity_to_same_accountant c, min_dhash_independent d
-FROM signatures WHERE is_valid=1 AND excel_firm IN ({','.join('?'*4)})
-  AND max_similarity_to_same_accountant IS NOT NULL AND min_dhash_independent IS NOT NULL""", BIG4)
+cur.execute(f"""SELECT CASE WHEN a.firm='勤業眾信聯合' THEN 1 ELSE 0 END isA,
+  s.max_similarity_to_same_accountant c, s.min_dhash_independent d
+FROM signatures s JOIN accountants a ON s.assigned_accountant=a.name
+WHERE a.firm IN ({','.join('?'*4)})
+  AND s.max_similarity_to_same_accountant IS NOT NULL AND s.min_dhash_independent IS NOT NULL""", BIG4)
 rows = cur.fetchall(); con.close()
 isA = np.array([r[0] for r in rows], bool)
 c = np.array([r[1] for r in rows]); d = np.array([r[2] for r in rows])