Decomposition-Induced Context-Memory Conflict: When Fact-Checking Pipelines Contradict Their Own Source Text

# Decomposition-Induced Context-Memory Conflict
Source: [https://arxiv.org/html/2608.10627](https://arxiv.org/html/2608.10627)
## 1Decomposition\-Induced Context\-Memory Conflict: When Fact\-Checking Pipelines Contradict Their Own Source Text

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### 1\.1Abstract

Decompose\-then\-verify pipelines, including FActScore\-style fact\-checkers, hallucination detectors, and long\-form factuality evaluators, first split a passage into atomic claims before checking each one\. Decomposition itself is treated as a neutral preprocessing step\. We show it is not\. When a language model decomposes a passage, it can be induced to substitute its own parametric belief for what the passage actually says, producing a claim that contradicts the source text it was supposed to summarize faithfully\. We call thisDecomposition\-Induced Context\-Memory Conflict \(DI\-CC\)and show it is mechanistically the same phenomenon as classical context\-memory conflict, occurring inside a different pipeline stage than prior work has examined\. A linear probe trained only on classical context\-memory conflict data \(NQ\-Swap\), never exposed to any decomposition output, significantly separates decomposition positions that produce DI\-CC from faithful decompositions, and, under most but not all tested configurations, from non\-contradictory elaborations as well, at n=64 DI\-CC positives \(AUC = 0\.86–0\.88, 95% CI excludes chance, permutation p < 0\.0005, the resolution limit of a 2000\-permutation test\)\. This result holds under both a variance\-ratio and, without any post\-hoc adjustment, a standard held\-out\-accuracy layer\-selection criterion, and it reproduces the original n=14 pilot’s effect size at a larger, same\-construction sample \(not an independently\-constructed replication\), with every positive case independently human\-verified\. On this same dataset, an existing reference\-free baseline, SelfCheckGPT\-style self\-consistency sampling, fails to detect DI\-CC at all \(AUC 0\.51, chance\-level\)\. This failure is mechanistically predictable: DI\-CC’s defining stability \(recoverable, reproducible parametric content\) makes it recur consistently across resamples rather than vary, the opposite of the signal self\-consistency methods rely on\. Building on the mechanistic finding, we show that context\-aware decoding \(CAD\), a training\-free mitigation from the classical conflict setting, transfers to the decomposition setting and significantly suppresses DI\-CC \(4\.16% to 2\.57%, McNemar’s p = 0\.000041\)\. This comes at a severe cost: 19\.4% of decompositions under coreference\-heavy conditions fail to parse at all, and 84% of those failures involve the decomposer fabricating a different person’s identity rather than merely omitting detail\. This is a faithfulness\-completeness trade\-off the original CAD paper did not report, and we do not consider it deployment\-ready as implemented\. Furthermore, we characterize the mechanism’s boundaries\. Its natural occurrence rate is too sparse to regress reliably \(0\.2–0\.4% of atomic claims\), it does not manifest on naturally\-occurring hallucinated text under FActScore’s external support criterion, and it requires a minimum model scale to detect: 3B fails to show the signal under both a standard accuracy\-based and a generalization\-oriented \(variance\-ratio\) layer\-selection criterion, a floor pattern that does not depend on which criterion is used, while 7B succeeds under both\. 14B succeeds under variance\-ratio selection but not accuracy\-based selection; that criterion was adopted only after seeing accuracy\-based selection fail at 14B \(Section 7\), so we do not treat this magnitude as confirmed evidence the signal increases with scale, and we omit it from this summary\. Together these results establish DI\-CC as a real, mechanistically grounded, and partially treatable failure mode of decompose\-then\-verify pipelines, with a scope we characterize precisely rather than overstate\.

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### 1\.21\. Introduction

Long\-form factuality evaluation and hallucination detection increasingly follow adecompose\-then\-verifyrecipe: split a generated passage into short, self\-contained atomic claims, then check each claim independently against a reference \(Min et al\., 2023; \[DnDScore, 2024\]\)\. This decomposition step is treated as bookkeeping, a way to get finer\-grained verification rather than a place where new errors originate\. The decomposer is itself a language model, however, and language models are well known to substitute their own parametric knowledge for the knowledge given in context when the two disagree, a phenomenon extensively studied under the namecontext\-memory conflict\(Longpre et al\., 2021\)\. No prior work has asked whether this same failure mode occursinside the decomposition step itself: whether, in the course of restating a passage as atomic claims, a decomposer can quietly replace what the passage says with what the model believes, producing a claim that then gets independently "verified" against the very source text it contradicts\.

We call thisDecomposition\-Induced Context\-Memory Conflict \(DI\-CC\): a decomposer, asked to atomize a source passageRR, produces an atomic claimcic\_\{i\}that \(a\) is not entailed byRR, \(b\) contains content traceable to the decomposer’s own closed\-book knowledge \(i\.e\., recoverable by probing the same model with no access toRR\), and \(c\) directly contradicts whatRRstates\. We distinguish this from a weaker, non\-contradictory sibling phenomenon,Decomposition\-Induced Unsupported Elaboration \(DI\-UE\), where the injected content fills a gapRRnever addressed rather than overturning somethingRRdid state\. Both share the same underlying injection mechanism; only DI\-CC is a strict conflict\.

A scoping note before we describe how we test this\.Our primary evidence for DI\-CC, the mechanistic test \(H0\) and everything built on it \(the mitigation study, the scale ablation\), uses anelicitedconstruction: a decomposition instruction that explicitly authorizes the decomposer to check facts against its own knowledge and correct errors\. This instruction is not incidental\. We show in Section 4\.1 that it is a necessary condition we discovered empirically: without it, DI\-CC does not appear at all, even when the source passage contains a tampered detail the decomposer could in principle catch\. We are explicit about what this does and does not establish\. It establishesexistence and mechanism: that a decomposer, under conditions that license it to reconcile a source against its own beliefs, can and does override the source in a way that is mechanistically continuous with classical context\-memory conflict\. It does not, by itself, establishprevalence: how often this happens when a decomposer is not so licensed\. We report that question honestly and separately\. The natural, non\-elicited rate is very low \(Section 5\), and the mechanism does not manifest on one real\-world hallucination benchmark under its own natural conditions \(Section 4\.4\); we state this here rather than let a reader infer the elicited construction’s scope only after encountering these later, less favorable results\. Section 4\.4 also discusses concretely where the elicited precondition is expected to hold outside our synthetic construction\.

Demonstrating that DI\-CC exists behaviorally, via natural language inference \(NLI\) checks that a claim isn’t entailed byRRbut is recoverable from the model’s own knowledge, is not enough to establish that it is thesame phenomenonas classical context\-memory conflict rather than an unrelated form of hallucination that happens to look similar on the surface\. A skeptical reviewer’s natural objection is that the decomposer is "just adding stuff," and NLI\-based behavioral evidence alone cannot rule this out\. We address this with a mechanistic argument instead\. If DI\-CC is genuinely the same underlying phenomenon as classical context\-memory conflict, then a linear probe trainedexclusivelyon classical conflict data, with no exposure whatsoever to decomposition, should still detect DI\-CC positions when applied zero\-shot to decomposition activations, and should do so more strongly than it responds to non\-contradictory elaboration\. This would rule out the alternative explanation that the probe is merely detecting "content got added" in general\.

Contributions\.Our central claim is mechanistic: DI\-CC is not merely a behaviorally\-defined pattern but the same underlying phenomenon as classical context\-memory conflict, occurring one pipeline stage earlier than prior work has looked\.

1\.DI\-CC is mechanistically real \(main result\)\.We give the first formal definition of decomposition\-induced conflict \(DI\-CC/DI\-UE\) and a mechanistic test \(H0\) that distinguishes it from an unrelated hallucination pattern that merely resembles it behaviorally\. A probe trained exclusively on classical conflict data detects DI\-CC in decomposition activations it has never seen, at n=64 with a literature\-validated, generalization\-oriented layer\-selection criterion \(AUC 0\.86–0\.88, 95% CI excludes chance\)\. This reproduces the effect size of an initial n=14 pilot at a larger, same\-construction sample, with every positive case in both samples independently human\-verified\. On the same dataset, an existing reference\-free baseline, SelfCheckGPT\-style self\-consistency sampling, fails to detect DI\-CC at all \(AUC 0\.51, chance\-level\)\. This gap is mechanistically predictable, since DI\-CC’s defining property \(stable, recoverable parametric content\) makes it recur consistently across resamples rather than vary, the opposite of what self\-consistency methods are built to flag\. 2\.A classical mitigation transfers, but is not yet deployable \(supporting result\)\.Context\-aware decoding, a mitigation from the classical conflict setting, transfers to decomposition and significantly suppresses DI\-CC, demonstrating the mechanism can be manipulated by a training\-free intervention rather than merely observed\. This comes at a severe, previously unreported cost: 19\.4% of coreference\-heavy decompositions fail to parse under CAD, and 84% of those failures involve the decomposer fabricating an entirely different person’s identity rather than merely omitting detail\. We do not consider this a solved or deployment\-ready mitigation; we report it as evidence of mechanistic manipulability with a serious, characterized side effect\. 3\.The mechanism has identifiable boundaries \(scope\)\.DI\-CC’s natural occurrence rate is too sparse to regress reliably\. It does not manifest on FActScore’s naturally\-occurring hallucinated text, for an identifiable reason: real hallucinations tend to fall in gaps the model has no opinion about, not in places where it holds a correct belief it then overrides\. It also requires a minimum model scale to detect\. A naive scale ablation initially looked erratic, but reanalyzing with a criterion from the OOD\-generalization probing literature, adopted after \(not before\) seeing the initial erratic result \(Section 7 discusses the resulting selection caveat\), resolves the qualitative pattern into a coherent capability threshold: 3B fails under both criteria, larger scales succeed\. The strongest individual result in the study occurs at the scale where this reanalysis also human\-verified all positive cases, but its exact magnitude carries the same post\-hoc\-selection caveat and should be weighted accordingly\.

A secondary, methodology\-focused contribution falls out of point 3: probing layer selection is not merely an implementation detail but can be the dominant source of an apparently erratic result, and we show a concrete, literature\-grounded fix\. Throughout, we report every non\-significant or boundary\-condition result alongside the positive ones, not as a hedge, but because the resulting scope claim \(real, mechanistic, partially treatable, and precisely bounded\) is the paper’s contribution rather than a discount applied to a larger claim we would have preferred to make\.

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### 1\.32\. Problem Definition

LetRRdenote a source passage,DDa decomposer LLM,MDM\_\{D\}the parametric knowledge ofDD, andcic\_\{i\}theii\-th atomic claim produced byD​\(R\)D\(R\)\.

Parametric injection\.Claimcic\_\{i\}exhibits parametric injection if it contains contentI=content​\(ci\)∖content​\(R\)I=\\mathrm\{content\}\(c\_\{i\}\)\\setminus\\mathrm\{content\}\(R\)such thatR⊧̸ciR\\not\\models c\_\{i\}\(an NLI model judgesRRdoes not entailcic\_\{i\}\) andI∈Recoverable​\(MD\)I\\in\\mathrm\{Recoverable\}\(M\_\{D\}\)\(closed\-book probing ofDD, with no access toRR, stably reproducesII\)\.

\-DI\-CC\(contradictory\):IIdirectly contradicts information already present inRR\. This is context\-memory conflict in the strict sense\. \-DI\-UE\(elaborative\):IIfills a positionRRnever addressed, without contradicting it\. This is not a strict conflict but shares the same injection mechanism and can equally corrupt downstream verification\.

Every claim that is not entailed byRRis checked for recoverability fromMDM\_\{D\}via a second NLI pass, using a closed\-book "knowledge dump" elicited fromDDabout the same subject as ground truth for whatDD"knows\." Claims where the injected content isnottraceable toMDM\_\{D\}are excluded as unstructured hallucination rather than parametric injection\.

Representational context\-memory\-conflict signature\.Consider the classical context\-memory conflict setting: a context that gives an explicit answeraca\_\{c\}, a closed\-book parametric answerama\_\{m\}, withac≠ama\_\{c\}\\neq a\_\{m\}\. We hypothesize that some layerℓ∗\\ell^\{\*\}of the residual stream admits a linear direction𝐰\\mathbf\{w\}separating "conflict occurred" from "conflict did not occur\." This follows the layer\-sweep probing methodology used elsewhere for locating conflict\-related representations \(Pham et al\., 2026, on intra\-memory conflict; Zhao et al\., 2024/NAACL 2025, on context\-memory conflict\)\.

H0 \(mechanistic hypothesis\)\.If DI\-CC is mechanistically homologous to classical context\-memory conflict, a probe𝐰\\mathbf\{w\}trainedonlyon classical conflict data, never exposed to any decomposition output, should, applied zero\-shot, separate DI\-CC generation positions from \(a\) faithful decompositions and \(b\) DI\-UE positions, at above\-chance accuracy\.

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### 1\.43\. Related Work

Knowledge conflict\.Context\-memory conflict, where a model’s parametric belief disagrees with what its context states, has been studied primarily in question\-answering, where NQ\-Swap \(Longpre et al\., 2021\) is the standard construction: replace a gold answer entity in the supporting passage with a same\-type distractor entity, so the context and the model’s closed\-book answer cleanly disagree\. Context\-aware decoding \(Shi et al\., 2023; NAACL 2024\) mitigates this at inference time by contrasting the output distribution conditioned on context against the same distribution without it, amplifying the model’s attention to context\. Large\-scale conflict benchmarks such as ConflictBank \(Su et al\., 2024\) construct millions of claim\-evidence pairs via entity substitution and LLM\-elicited counterfactuals to study conflict at scale\. All of this work studies conflict at the point offinal answer generation\. We study it at an earlier, distinct pipeline stage, decomposition, that none of this literature examines\.

Hallucination detection via decomposition\.FActScore \(Min et al\., 2023\) established the atomic\-decompose\-then\-verify recipe now standard in long\-form factuality evaluation, checking each atomic claim against an external reference \(Wikipedia\)\. DnDScore \(2024\) examines the interaction between decomposition and decontextualization, and CREDENCE \(Tran, Mai, and Le, 2026\) introduces an Entity Preservation Rate and a Semantic\-F1 metric to catch when a decomposer drops or distorts content\. Both papers acknowledge, in passing, that decomposition can introduce error, but neither formalizes a conflict\-specific failure mode nor tests whether it shares a mechanism with classical context\-memory conflict\. This is the gap DI\-CC’s H0 test addresses\.

Self\-consistency\-based hallucination detection\.SelfCheckGPT \(Manakul et al\., 2023\) detects hallucination without any external reference by sampling multiple generations and treating cross\-sample disagreement as evidence of unreliable knowledge\. This is a substantively different construction strategy from ours: it never requires the model to "actually know" a fact against a single elicited ground truth\. We compare against it directly in Section 4\.5 and find it fails to detect DI\-CC on our primary dataset, for a mechanistically predictable reason\. Extending that comparison to the natural, non\-elicited setting remains future work \(Section 4\.5, Section 8 Cross\-cutting\)\.

Scale effects on conflict\.Prior work reports that conflict rates on some conflict types decrease at larger model scale\. Cheng, Pan, and Amiri \(2026\) define and quantify Tool\-Memory Conflict \(TMC\), a distinct conflict type in which tool\-augmented LLMs’ parametric knowledge contradicts external tool outputs, and find larger models \(8B\-72B\+, including GPT\-4o and DeepSeek\-V3\) exhibit lower conflict rates, though none of the mitigations they test \(vigilant prompting, opinion\-based prompting, RAG\) resolve TMC fundamentally\. We test the analogous scale question for DI\-CC’s mechanistic signal \(Section 7\)\. Our initial ablation finds a materially different, non\-monotonic pattern, which we then show is substantially attributable to probing methodology rather than to model cognition \(see below\)\.

Probing layer selection and generalization\.A separate literature examineshowto select a probing layer or direction, distinct fromwhatthe direction represents\. The standard practice, selecting by held\-out in\-distribution classification accuracy, has been shown to be a poor proxy for out\-of\-distribution transfer\. Uselis & Oh \(2025\) find that classifiers trained on intermediate layers, rather than the conventionally\-preferred penultimate layer, often generalize substantially better under distribution shift, in some cases even without any target\-distribution supervision, because intermediate layers are less sensitive to the shift than final layers\. Independently, Bürger et al\. \(2024\) select probing layers for a truthfulness direction by the ratio of between\-class to within\-class variance rather than classification accuracy, on the grounds that this criterion better isolates a clean, generalizable concept direction\. Follow\-up work, probing truth\-direction consistency across logical transformations, confirms the criterion is task\- and model\-dependent, with no single layer universally optimal\. We adopt this variance\-ratio criterion in Section 7 after finding that accuracy\-based layer selection produces an inconsistent transfer signal across model scale for DI\-CC\.

Cross\-model generalization of truth\- and conflict\-related linear structure\.A more basic question than layer selection is whether a linear direction found in one model says anything about adifferentmodel\. Choi et al\. \(2026\) find context\-truthfulness scores strongly preservedwithina model lineage \(Vicuna\-, Qwen2\.5\-, LLaMA2\-, Mistral\-based\), but do not claim preservationacrossindependently\-trained lineages\. Zolfaghari \(2026\), probing five architectures for a comparable linear signal, finds some preserve a stable representation while others show collapse: whether such a direction generalizes at all is architecture\-dependent\. This matches a broader finding in representation learning: independently\-trained networks’ latent spaces are not aligned in absolute coordinates, only in relative similarity structure \(Moschella et al\., 2023\)\. This literature motivates treating within\-family evidence and cross\-family generalization as separate claims, which we do in Section 8\.

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### 1\.54\. Phase 0: Mechanistic Validation \(H0\)

#### 1\.5\.14\.1 Setup

We use Qwen2\.5\-7B\-Instruct \(4\-bit NF4 quantized\) as both the decomposer and the probe host model throughout Phase 0\. All entailment and recoverability judgments \(Section 2\) use a single 3\-way NLI model, DeBERTa\-v3\-large fine\-tuned on MNLI, FEVER\-NLI, ANLI, LingNLI, and WANLI \(MoritzLaurer/DeBERTa\-v3\-large\-mnli\-fever\-anli\-ling\-wanli\), applied consistently across all phases of the study\. The probe is trained on 826 activation vectors from NQ\-Swap \(413 conflict / 413 no\-conflict, perfectly balanced\), extracted at the final prompt token before answer generation, across all 29 hidden states \(28 transformer layers plus the embedding layer\)\. A per\-layer logistic regression sweep selects layer 22 as best \(held\-out accuracy 0\.821\), consistent with prior findings that fact/conflict signals concentrate in mid\-to\-late layers\. This probe is thenfrozenand never updated on any decomposition data\.

FActScore’s official release was, at the time of this phase, believed unavailable via standard tooling \(a misjudgment later corrected; see Section 4\.4\)\. Because of this, Phase 0 uses self\-generated closed\-book biographies of 40 well\-known, Wikipedia\-notable people spanning science, politics, history, literature, and the arts\. Two biography variants are generated per person: a deliberatelyvaguevariant \(pronoun\- and placeholder\-heavy, prone to DI\-UE when decomposed\) and aspecificvariant with an explicit year, which is then perturbed \(the year shifted by a random plausible\-but\-wrong amount, NQ\-Swap\-style\) to create aperturbedvariant prone to DI\-CC\. The decomposition instruction for the perturbed variant explicitly invites the decomposer to check facts against its own knowledge and correct errors\. This is an elicited condition, deliberately not representative of natural decomposition behavior, whose purpose is solely to guarantee enough DI\-CC instances exist to test H0 with adequate statistical power \(see Section 5 for the natural\-rate question\)\. This instruction is a necessary condition, not a minor detail: an earlier attempt using a neutral instruction \(no invitation to fact\-check\) on the same perturbed biography yielded zero DI\-CC cases, since the decomposer faithfully reproduced the tampered year rather than overriding it\. Every DI\-CC instance in this paper’s synthetic data \(Phase 0, H3, Phase 2\) was therefore elicited into existence, not merely observed\. Sections 4\.4 and 5 report what happens without this license, and both find DI\-CC near\-absent\.

This produces 75 biography records \(40 vague \+ 35 perturbed; 5 people’s specific biographies referenced only pre\-modern years outside the regex used for perturbation and were skipped\) and 443 atomic subclaims, labeled via the NLI\-based three\-way procedure of Section 2: 303 legit \(68\.4%\), 49 DI\-UE \(11\.1%\), 14 DI\-CC \(3\.2%\), 77 excluded \(17\.4%, unrecoverable and therefore not parametric injection\)\.

#### 1\.5\.24\.2 Results

Primary result \(n=64, variance\-ratio layer selection\)\.The headline H0 result uses the larger, same\-methodology replication sample\. It reuses decomposition and labeling data originally produced for the H3 mitigation study \(Section 6\), whosebaseline\(non\-CAD\) conditions apply the identical elicited perturbed/vague\-biography procedure at 191 entities rather than Phase 0’s original 40, extending the same 7B decomposer to n=64 DI\-CC positives\. No additional decomposer calls were needed; only the activation\-extraction step, never previously run on this larger pool, was missing\. The probe layer is selected by the variance\-ratio criterion \(Bürger et al\., 2024; Section 7\) rather than held\-out accuracy, since Section 7 finds accuracy\-based selection produces an inconsistent transfer signal across model scale\. Layer 20 is selected \(vs\. layer 22 under accuracy selection\), with results and 95% bootstrap percentile CIs \(2000 resamples\) as follows:

Both AUCs are significantly above chance \(0\.5\), with confidence intervals well clear of it\. We had originally intended a stricter decision rule: DI\-CC vs\. DI\-UE at least as strong as DI\-CC vs\. legit, as direct evidence the signal is specific tocontradictionrather than to parametric injection in general\. This holds under three of the four \(sample, layer\-criterion\) configurations in Table 4\.2b below \(accuracy at both n=14 and n=64; variance\-ratio at n=14\)\. Under the primary configuration \(n=64, variance\-ratio\), the ordering is reversed by a small, CI\-overlapping margin \(0\.863 vs\. 0\.881\), so we do not claim this configuration alone passes the stricter rule\. We report this plainly rather than silently relaxing the criterion\. The honest summary is that the DI\-CC\-vs\-DI\-UE specificity signal is present and significant in every configuration tested, and dominates DI\-CC\-vs\-legit in most of them, but is not uniformly the stronger of the two comparisons\. This difference is too small, and too inconsistent in direction across nearby layers, to treat as evidence the probe is somehow more generic under the primary configuration specifically\.H0 holdsin the weaker but still meaningful sense that both AUCs clear chance with non\-overlapping CIs in all four configurations\. The stronger specificity claim is qualified rather than unconditional, and we discuss what would be needed to sharpen it in Section 8\.

Pilot result \(n=14\) and layer\-selection robustness\.The original n=14 pilot \(Phase 0’s 40\-entity pool\) and an accuracy\-based\-selection cross\-check both replicate the result above at every sample\-size\-by\-criterion combination tested: all four configurations clear chance with non\-overlapping CIs \(full table and discussion of the pre\-registration caveat in Appendix[1\.13\.1](https://arxiv.org/html/2608.10627#S1.SS13.SSS1)\)\. This rules out the n=14 pilot being a small\-sample artifact, and confirms the core H0 finding does not depend on adopting variance\-ratio selection at all: accuracy\-based selection alone also clears chance at both n=14 and n=64 \(AUC 0\.858 \[0\.815, 0\.897\] at n=64\)\. We report the variance\-ratio configuration as primary because Section 7 shows accuracy\-based selection is a poor proxy for transfer at other scales, not because it is a stronger result at n=64 itself; readers who want a selection\-free number should treat 0\.858 as the more conservative primary evidence for H0\.

A caveat on what these AUCs represent\.All results above use a probe trained onperfectly balancedNQ\-Swap data, and report AUC, a ranking metric rather than a fixed\-threshold operating characteristic\. Retraining at a realistic, downsampled class ratio \(N=50N=50seeds; Appendix[1\.13\.2](https://arxiv.org/html/2608.10627#S1.SS13.SSS2)\) leaves AUC undegraded but collapses fixed\-threshold conflict\-class recall from 0\.808 to 0\.247 on average, with high seed\-to\-seed variance, so the balanced\-training AUCs above should not be read as indicative of deployable, fixed\-threshold detection performance at realistic prevalence, a claim we do not make anywhere in this paper\.

#### 1\.5\.34\.3 Human verification

All 14 DI\-CC cases were independently reviewed by a human annotator against the perturbed detail, the decomposer’s claim, and the elicited knowledge dump; 13/14 were confirmed clean\. The one exception revealed a specific NLI numerical\-precision limitation orthogonal to whether DI\-CC itself is real \(Appendix[1\.13\.3](https://arxiv.org/html/2608.10627#S1.SS13.SSS3)\)\.

#### 1\.5\.44\.4 Attempted replication on real hallucinations

Attempting to replicate H0 on FActScore’s naturally\-occurring, human\-verified hallucinated content \(two independent samples, 150 and 302 sentences\) yielded zero DI\-CC cases\. FActScore’s "not supported by external reference" and DI\-CC’s "contradicts the model’s own belief" are measuring different things: real hallucinations more often fall in the model’s knowledge gaps than in places it holds an overridden correct belief\. We treat this as a boundary condition on DI\-CC’s applicability, not a refutation of H0\.

#### 1\.5\.54\.5 Comparison to a reference\-free baseline \(SelfCheckGPT\)

We compare against SelfCheckGPT\-style self\-consistency sampling \(Manakul et al\., 2023\): for each n=64 subclaim, we resample the decomposer’s outputN=10N=10times at temperature 1\.0 and score inconsistency as the fraction of resamples not NLI\-entailing it\.

SelfCheckGPT does not detect DI\-CC on this dataset\. This is a mechanistically predictable failure: DI\-CC’s injected content is, by construction, stably recoverable, so it recurs consistently across resamples rather than varying, exactly the pattern SelfCheckGPT reads as trustworthy\. DI\-UE’s higher inconsistency score \(mean 0\.422 vs\. DI\-CC’s 0\.067\) is consistent with this account from the other direction: elaboration filling a genuine gap, with no single stably\-recoverable answer, is more likely to vary across resamples than a confident override\.

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### 1\.65\. Phase 1a: Natural Injection Rate \(H1\)

Question\.Does the natural \(non\-elicited\) injection rate correlate with textual ellipticity, meaning the density of pronouns, low named\-entity density, and short average sentence length that leave more room for a decomposer to "fill in" content?

Method\.Using FActScore’sdata/unlabeledrelease \(500 entities × 12 generating models\) and aneutraldecomposition instruction \(no fact\-checking language, unlike Phase 0\), we compute three continuous ellipticity features per biography via spaCy and regress the injection rateIR=\|\{ci:parametric injection\}\|/n\\mathrm\{IR\}=\|\\\{c\_\{i\}:\\text\{parametric injection\}\\\}\|/nagainst them\.

Result: inconclusive\.Two rounds \(30, then 100 entities\) both found the natural injection rate extremely low: 0\.2–0\.4% of atomic claims, 9–18 positive instances total, too sparse for stable regression estimates \(signatures of small\-sample instability detailed in Appendix[1\.13\.4](https://arxiv.org/html/2608.10627#S1.SS13.SSS4): shifting predictor significance between rounds, implausibly extreme odds ratios\)\. We made the deliberate decisionnotto keep scaling the sample chasing significance, and instead report the sparsity itself as the finding: under natural, non\-elicited instructions, DI\-CC/DI\-UE occur at a rate too low to characterize with the sample sizes tested here\.

This result also has a direct methodological implication for Phase 0 and Section 4\. It explains, retrospectively,whyPhase 0 needed an explicit fact\-checking instruction to observe any DI\-CC cases at all, and it foreshadows a design risk for the mitigation experiment in Section 6: a floor effect, addressed there directly\.

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### 1\.76\. Phase 1b: Mitigation via Context\-Aware Decoding \(H3\)

We tested whether context\-aware decoding \(Shi et al\., 2023\), adapted to decomposition by retaining the subject’s name in both branches since removing it entirely would also remove the subject’s identity, suppresses DI\-CC on Phase 0’s elicited condition \(191\-entity pool\)\. It does: DI\-CC rate fell from 4\.16% to 2\.57% \(McNemar’s p = 0\.000041\)\. But on vague\-biography \(coreference\) decompositions, 19\.4% failed to parse under CAD, and 84% of those involved the decomposer fabricating a different person’s identity entirely\. This is a faithfulness\-completeness trade\-off the original CAD paper did not report\. We do not consider this implementation deployment\-ready; it demonstrates the mechanism is manipulable by a training\-free intervention, not a solved mitigation\.

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### 1\.87\. Phase 2: Scale Ablation \(H4\)

We reran the full Phase 0 pipeline at two additional scales \(Qwen2\.5\-3B/14B\-Instruct, same 40\-entity pool\) to test whether the H0 signal decreases monotonically with model scale, as observed for tool\-memory conflict at very large scale \(Cheng, Pan, and Amiri, 2026\)\. An initial accuracy\-based layer selection produced a non\-monotonic, uninterpretable result\. We traced this to a methodological gap: layer selection driven by NQ\-Swap accuracy alone, with no criterion for transfer to decomposition\. Reselecting layers by the variance\-ratio criterion \(Bürger et al\., 2024\) resolves this \(Figure[1](https://arxiv.org/html/2608.10627#S1.F1)\)\. 3B is unchanged under either criterion, a negative control against selection artifacts, while 14B flips from non\-significant \(AUC 0\.566\) to the strongest result of the study \(AUC 0\.983\)\. The DI\-CC\-vs\-DI\-UE specificity check also flips from wrong\-signed \(0\.380\) to strongly significant \(0\.927\), independently human\-verified \(29/29 clean\)\.

![Refer to caption](https://arxiv.org/html/2608.10627v1/x1.png)Figure 1:H0 transfer AUC by model scale, accuracy\- vs\. variance\-ratio\-selected layer, for both comparisons\. Open markers: not significant \(p≥0\.0005p\\geq 0\.0005\)\. Dashed line: chance\.The pattern resembles a capability threshold: below some scale between 3B and 7B, the representation needed for transfer does not form under either criterion\. We hold the 14B magnitude more loosely than the qualitative floor pattern, however, since the criterion was adopted only after seeing it rescue an inconvenient result \(full discussion in Appendix[1\.13\.6](https://arxiv.org/html/2608.10627#S1.SS13.SSS6)\)\. H4 as originally stated \(transferdecreasingwith scale\) remains unsupported either way\.

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### 1\.98\. Limitations

We report limitations by phase, consistent with how each was documented during the study, rather than compressing them into generic caveats\.

Phase 0 / H0\.\(i\) The original positive sample is small \(n=14\), mitigated by the n=64 replication \(Section 4\.2\), which reuses the same probe and elicitation procedure at a larger entity pool and reproduces the result closely; both samples share the same self\-generated\-biography construction \(see Cross\-cutting, below\), so the replication addresses sampling variance without addressing construction\-level generalization\. \(ii\) DI\-CC was elicited via an explicit fact\-checking instruction; the mechanism’sexistenceis established, but this says nothing about its natural frequency \(addressed, and found to be very low, in Section 5\)\. \(iii\) Human review surfaced a specific NLI limitation, insensitivity to single\-digit numerical precision in an otherwise near\-identical context, that produced one technical false\-positive recoverability judgment out of 14; the phenomenon itself was not falsified, but the automated pipeline’s precision has an identified failure mode\. \(iv\) The elicited knowledge dump used to check recoverability is itself not a ground\-truth oracle: it can contain its own factual errors and internal inconsistencies, and can only establish "this content is traceable to the model’s own generation," not "this content is factually correct\." \(v\) The 14 measured DI\-CC cases are a lower bound, not an exhaustive enumeration: human review found at least one case \(a source biography’s pre\-existing, non\-perturbed error\) that the decomposer left uncorrected and that our detection design, built to catch deliberately tampered details, was not built to catch\. \(vi\) All bootstrap confidence intervals in this paper use the percentile method \(2000 resamples\) rather than a bias\-corrected variant \(e\.g\., BCa\), a standard default that is not guaranteed to be conservative for AUC estimators on imbalanced group sizes \(e\.g\., 64 DI\-CC vs\. 1626 legit in Section 4\.2\); we did not verify the intervals against a bias\-corrected alternative\. \(vii\) The probe’s usefulness as a fixed\-threshold detector, as opposed to a ranking signal, is materially weaker than the AUCs above might suggest: at a realistic training\-class ratio, multi\-seed testing \(Section 4\.2\) finds mean conflict\-class recall of only 0\.25 with substantial seed\-to\-seed variance \(std 0\.19, range 0–0\.75\), a genuine limitation of the probe as a practical detector, not an artifact of one unlucky data split\.

H0 real\-data replication\.DI\-CC did not manifest on FActScore’s naturally\-hallucinated \(NS\-labeled\) content in either of two independent samples\. We localized the cause \(Section 4\.4\): FActScore’s externally\-defined "not supported" criterion and DI\-CC’s internally\-defined "contradicts the model’s own belief" criterion are not the same thing, and real hallucinations more often fall in the model’s knowledge gaps than in places it holds an overridden correct belief\. This materially limits the range of real\-world hallucinated content to which DI\-CC, as operationalized here, is known to apply\.

H1\.The natural injection rate is real but too sparse \(0\.2–0\.4%, 9–18 positive cases across two rounds up to 100 entities\) to characterize its inducing conditions with the regression approach used; we chose to report this honestly rather than continue scaling the sample in pursuit of significance that smaller\-sample instability suggested was unlikely to be trustworthy even if achieved\.

H2\.Calibration of the automated NLI labeling pipeline against FActScore’s humanhuman\-atomic\-factsannotations \(183 entities, 2119 atomic facts\) yields Cohen’sκ=0\.306\\kappa=0\.306, "fair" by Landis and Koch’s scale, not "substantial\." We manually inspected every one of the 7 cases where our pipeline judged a claimexcluded\(ungrounded\) but a human annotation covered it, plus a stratified sample of 20 \(of 86\) cases in the reverse\-disagreement direction, rather than resting on the granularity\-mismatch explanation as an unverified assumption\. This spot\-check confirms the granularity account for 6/7 of the excluded\-but\-human\-covered cases \(specific, plausible facts our closed\-book knowledge\-dump elicitation likely just failed to surface\) and finds no comparable pattern in the 20\-case reverse\-direction sample\. It also surfaces a distinct, previously undocumented failure mode: in one of the 7 cases, and in a separate literal\-string scan across all 2119 records \(6 additional cases, 0\.28%\), the decomposer’s pronoun resolution substitutes an unrelated identity, including, in two cases, the decomposer’s own model name, for the biography subject\. Two of these six cases were labeledlegitby our pipeline, one of which coincidentally matched the human annotation and so appears in neither disagreement cell of the calibration table, indicating this failure mode is not fully caught by the current labeling pipeline\. This is the same underlying pattern as the CAD identity\-fabrication finding \(Section 6\), a decomposer substituting an unrelated identity when coreference lacks a strong anchor, but observed here in the baseline, neutrally\-instructed decomposition pipeline itself, at a low but non\-zero rate\. This calibration exercise also had too few DI\-CC/DI\-UE instances \(1 and 0, respectively\) to validate the injection\-labeling arm of the pipeline specifically, as distinct from the faithfulness\-labeling arm\. Concretely,κ=0\.306\\kappa=0\.306is evidence about the faithfulness\-labeling arm; the injection\-labeling arm’s evidence base is the per\-case human review in Sections 4\.3 and 7\.3 \(13/14 and 29/29 confirmed clean, respectively\), not this aggregate statistic\.

H3\.The primary mitigation effect is real and significant, but comes with a substantial, previously unreported side effect \(19\.4% structural parsing failure under CAD on the coreference\-resolution condition, 84% of which involve the decomposer fabricating a different person’s identity; see Section 6\)\. One planned side\-effect metric, a structural check for leftover unresolved pronouns, turned out to be uninformative in practice, saturating near ceiling in both conditions \(97–99%\) because the common word "it" triggers the check regardless of whether coreference actually failed; we report this as a failed measurement rather than evidence of no side effect, and rely instead on the parsing\-failure and label\-mix statistics, which are informative\. The CAD contrastive\-decoding loop is a hand\-written reimplementation of the published formula, not the original authors’ code, validated only via a single\-entity smoke test plus the aggregate statistical results reported here, not via a formal unit\-level correctness proof\. We subsequently swept the contrast strengthα∈\{0\.5,1\.0,1\.5\}\\alpha\\in\\\{0\.5,1\.0,1\.5\\\}\(191\-entity full pool, 734 decodings\) against the literature\-recommended default of 1\.0: the primary suppression effect is strongest atα=1\.0\\alpha=1\.0\(DI\-CC rate reduction −38\.2%, vs\. −23\.4% at 0\.5 and −16\.6% at 1\.5, all McNemar’sp<0\.01p<0\.01\), while the side effect grows monotonically withα\\alpha\(total\-output loss −6\.7% at 0\.5, −28\.0% at 1\.0, −51\.6% at 1\.5\)\. We did not find a setting among these three that improves both the primary effect and the side effect simultaneously relative toα=1\.0\\alpha=1\.0, but three discrete points, one of which is the literature default itself, is too sparse a grid to claimα=1\.0\\alpha=1\.0is optimal in any stronger sense; a denser sweep would be needed to characterize the true trade\-off curve\. The 37 structural parsing failuresweremanually inspected \(Section 6\): all 37 share a numbering\-format defect, and 31/37 additionally exhibit identity fabrication traced to the without\-context branch losing its name anchor on vague, deliberately name\-withholding biographies\.

Phase 2 / H4\.Only three scale points within a single model family \(Qwen2\.5\) were tested, and DI\-CC positive counts at each scale remain modest \(14, 18, 29\); a meaningfully larger sample at each scale would strengthen confidence in the pattern, though the fact that the variance\-ratio and accuracy criteria select theidenticallayer at 3B \(Section 7\) argues against pure small\-sample noise as the explanation for 3B’s null result specifically\. The 14B DI\-CC cases are now human\-verified \(Section 7: 29/29 clean, resolving the gap between this analysis and the 7B case review\), confirming the 14B flip is a genuine signal rather than a labeling artifact\. 3B’s reversal \(unchanged by the reanalysis, since it selects the same layer under both criteria\) remains uninspected at the case level, since 3B produces no positive flip to explain\. We tested exactly one alternative layer\-selection criterion \(variance ratio\), and did not sweepα\\alpha\-style hyperparameters of the criterion itself or try a second alternative \(e\.g\., a few\-shot transfer\-supervised criterion in the spirit of Uselis & Oh, 2025, using a handful of held\-out DI\-CC cases directly in layer selection\), which could further clarify whether the 3B null result reflects a true capability floor or a criterion this specific reanalysis still does not adequately probe\.

Cross\-cutting\.All primary results \(Sections 4–7\) use a single model family \(Qwen2\.5\) and a single NLI model for entailment/recoverability judgments\. We tested whether the H0 mechanistic finding generalizes to a second model family, Mistral\-7B\-Instruct\-v0\.3 \(Apache\-2\.0, architecturally and in training data unrelated to Qwen2\.5\), using the identical within\-model methodology as Section 4: a probe trained only on that model’s own NQ\-Swap activations, evaluated zero\-shot on that same model’s own decomposition activations, at the same accuracy\-selected best layer \(layer 18, NQ\-Swap held\-out accuracy 0\.756\)\.It did not replicate\.DI\-CC vs\. legit: AUC = 0\.397, 95% CI \[0\.344, 0\.449\], permutationp=0\.9995p=0\.9995; DI\-CC vs\. DI\-UE: AUC = 0\.308, 95% CI \[0\.238, 0\.385\],p=1\.0000p=1\.0000\. Both are below chance, with confidence intervals excluding 0\.5 in the wrong direction rather than merely failing to exclude it in the right one\.

Before treating this as a genuine model\-family difference rather than a methodological artifact, we checked three alternative explanations\. \(1\)Statistical power: if n=74 DI\-CC positives were simply too few to detect a true positive effect, the bootstrap CI should be wide and straddle 0\.5; instead it is narrow \(width 0\.105\) and lies entirely below it, which is inconsistent with underpowering as the explanation\. \(2\)Layer\-selection criterion: re\-running the variance\-ratio criterion \(Bürger et al\., 2024; Section 7\) on this model’s own NQ\-Swap activations selects the identical layer \(18\) as accuracy\-based selection, so the criterion\-dependence that explained the Qwen2\.5\-14B flip in Section 7 does not apply here; there is no alternative layer this result is sensitive to\. \(3\)Labeling quality: we manually reviewed all 74 DI\-CC\-labeled cases against the perturbed detail and the raw decomposition, the same protocol used in Sections 4\.3 and 7\.3\. 71/74 \(96%\) are confirmed clean instances of the model overriding a perturbed detail with its own knowledge; 3/74 are likely mislabels, two a decomposition\-parsing artifact \(a temporal clause split across two sentences, e\.g\. "X was born in his youth," which asserts nothing that could conflict with anything\) and one an unrelated, non\-conflicting claim mislabeled by the automated NLI pipeline\. Excluding these 3 makes the result numerically more negative, not less \(AUC 0\.388 and 0\.295 respectively\), ruling out labeling noise as an explanation that could rescue a true positive effect\. With these three explanations checked and ruled out, we read this as evidence that the H0 mechanism, as detected by this probing methodology, is at least in part specific to the Qwen2\.5 family rather than a general property of instruction\-tuned LLM decomposers, a reading consistent with the model\-lineage\-dependent and architecture\-dependent transfer findings reported elsewhere in the literature \(Choi et al\., 2026; Zolfaghari, 2026; Section 3\)\. We also attempted this test on a third family, Falcon\-7B\-Instruct, but it did not yield a usable result: the same elicitation protocol produced only 10 DI\-CC instances \(vs\. 74 for Mistral, from a comparable\-sized entity pool\), and the resulting AUC estimate is uninformative \(95% CI \[0\.367, 0\.669\], straddling chance\)\. We do not read this as a third data point either confirming or disconfirming H0’s cross\-family generality; the low yield itself suggests the elicitation instruction’seffectiveness at inducing DI\-CC in the first placemay itself be family\-dependent, a distinct boundary condition from the one Section 8 otherwise discusses\. This changes how Contributions 1 and 3 \(Section 1\) should be read: DI\-CC’sexistence and mechanismis established within Qwen2\.5, and the mechanism’s generalization across model families is now a tested, and so far unresolved\-in\-favor\-of\-generality, open question rather than an untested one\.

We compare the mechanistic probe against one existing reference\-free hallucination detector, SelfCheckGPT\-style self\-consistency sampling \(Manakul et al\., 2023; Section 4\.5\)\. It fails to detect DI\-CC on the n=64 synthetic dataset \(AUC 0\.508, chance\-level\), for a specific and mechanistically\-predicted reason: DI\-CC’s injected content is, by construction, stably recoverable, so it recurs consistently across resamples rather than varying, which is exactly the pattern SelfCheckGPT reads as trustworthy\. This comparison is limited to the same synthetic, elicited dataset as the primary H0 result, however\. We did not evaluate it \(or the mechanistic probe\) in the natural, non\-elicited setting \(Section 5, Section 4\.4\), since obtaining DI\-CC positive examples there in the first place remains an open problem this paper does not solve\. Additionally, the self\-generated\-biography construction \(Phase 0, H3, Phase 2\) relies on the decomposer’s own closed\-book biography generation as source text, which is convenient for guaranteeing DI\-CC exists but is not naturally occurring text\. The one attempt to test on genuinely naturally occurring hallucinated text \(Section 4\.4\) found the mechanism’s precondition largely absent there, which we consider a genuine finding rather than a nuisance to be engineered around\. Code and data \(the core H0 mechanistic\-validation and H3 CAD\-mitigation pipeline, including the frozen 40\- and 191\-entity biography pools and probe checkpoints\) are available at[https://github\.com/hollis\-png/di\-cc\-decomposition\-conflict](https://github.com/hollis-png/di-cc-decomposition-conflict)\.

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### 1\.109\. Conclusion

Decompose\-then\-verify pipelines are typically built on the assumption that decomposition is a faithful, error\-neutral preprocessing step\. We show this assumption can fail in a specific, mechanistically characterizable way, and we characterize the failure at three levels\.

DI\-CC is mechanistically real, with a qualification we state explicitly rather than bury\.A decomposer can substitute its own parametric belief for what the source text says, producing Decomposition\-Induced Context\-Memory Conflict, and this failure mode is detectable by a probe that has never seen a single decomposition example\. This is evidence that it shares a mechanism with classical context\-memory conflict, not merely a superficial resemblance\. This result holds at n=64 under both a standard accuracy\-based layer\-selection criterion and a generalization\-oriented \(variance\-ratio\) one, reproducing the effect size of an initial n=14 pilot at a larger, same\-construction sample \(not an independently\-constructed replication\), with every positive case in both samples independently human\-verified\. The stricter specificity claim, that the probe responds tocontradictionspecifically rather than to parametric injection in general, holds clearly in three of the four \(sample × criterion\) configurations we tested, but not, by a small CI\-overlapping margin, in the primary n=64/variance\-ratio configuration itself \(Section 4\.2\)\. We report this rather than silently adopting the more favorable framing\. We do not read this as evidence the probe has become generic in that configuration, however: DI\-CC\-vs\-DI\-UE AUC there is still 0\.863 \[0\.806, 0\.913\], far above chance and far above the approximately 0\.36\-0\.38 AUC a probe that has genuinely lost specificity produces \(the scale\-ablation failure cases in Section 7\)\. The ordering rule failing is therefore a real qualification on thestrongestform of the specificity claim, not evidence against specificity itself\. A separate qualification applies to what these AUCs mean practically: multi\-seed testing at a realistic training\-class ratio \(Section 4\.2\) finds the probe’s fixed\-threshold conflict recall collapses to 0\.25 on average, with substantial seed\-to\-seed variance\. The mechanistic detection signal is real, but we do not claim it translates into a reliable practical detector at realistic prevalence, and this paper makes no deployment claim\.

The mechanism is partially treatable\.A standard mitigation for the classical setting, context\-aware decoding, transfers to decomposition and works, but not for free: it trades DI\-CC suppression against legitimate elaboration capability, a trade\-off invisible in the setting the original mitigation was evaluated on\.

The mechanism’s scope is precisely bounded, not open\-ended\.Its natural occurrence rate is low, it does not manifest on FActScore’s naturally\-occurring hallucinated text, and it requires a minimum model scale to detect: a floor pattern \(3B fails, larger scales succeed\) that holds under both layer\-selection criteria and does not depend on which one is used\. A naive scale ablation initially suggested the mechanism was erratic across model size\. A generalization\-oriented layer\-selection criterion, adopted after \(not before\) observing that erraticism, resolved much of it into a coherent capability\-threshold pattern\. We treat the qualitative floor pattern as solid and the specific magnitude of the 14B result as a criterion\-dependent secondary observation, precisely because the criterion was chosen post\-hoc\. This is a reminder that probing methodology itself can be the dominant source of an unexplained result, and that correcting it after the fact still carries a selection cost worth naming rather than absorbing silently into the headline claim\. This bounded scope is not merely a limitation to acknowledge: the same mechanistic precondition that is absent from FActScore’s open\-ended hallucinations \(Section 4\.4\) is the expected condition in fact\-checking against well\-known entities, RAG over knowledge\-intensive domains, and adversarial robustness testing, settings where a source document is checked against, rather than generated from, a model’s confident prior knowledge\. We stress this applicability profile is a prediction from the mechanism, not something we tested empirically\.

Together, these three levels are the paper’s contribution, not a discount applied to a larger claim we would have preferred to make\. They form a rigorous accounting of exactly where, how much, and under what conditions this specific failure mode of decompose\-then\-verify pipelines actually occurs\.

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### 1\.11Artifact Licenses and Compute

Licenses of artifacts used\.Qwen2\.5\-7B\-Instruct and Qwen2\.5\-14B\-Instruct \(Sections 4\.1, 7\) are released under Apache 2\.0\. Qwen2\.5\-3B\-Instruct \(Section 7\) is released under the Qwen RESEARCH LICENSE AGREEMENT, a research\-only license distinct from the Apache 2\.0 terms covering the other two scales in the same model family\. We do not assume license uniformity across a model family’s sizes, and confirmed each size’s terms individually\. Mistral\-7B\-Instruct\-v0\.3 and Falcon\-7B\-Instruct \(Section 8, cross\-model validation\) are both Apache 2\.0\. NQ\-Swap \(Longpre et al\., 2021\) is distributed under a custom Apple software license permitting use, reproduction, modification, and redistribution, with restrictions on using Apple’s name or trademarks for endorsement\. FActScore \(Min et al\., 2023\) is released under the MIT license\. All uses in this paper are for the research purposes these licenses permit\. The research\-only Qwen2\.5\-3B license in particular is consistent with our use \(a controlled scale\-ablation experiment\) and would need separate consideration for any non\-research reuse of that specific scale’s results\. Our own released code and data \(Section 8, Cross\-cutting\) are MIT\-licensed, stated in the repository README\.

Compute\.All GPU\-requiring stages \(decomposition, activation extraction, NLI\-based labeling, CAD contrastive decoding, SelfCheckGPT resampling\) ran on a single consumer GPU, an NVIDIA RTX 5070 Ti \(16GB VRAM\)\. The Blackwell architecture \(sm\_120\) required torch 2\.11\.0\+cu128, as earlier CUDA/torch combinations produced no usable kernel for this GPU\. CPU\-only stages \(probe layer sweeps and training, transfer evaluation, bootstrap confidence intervals, permutation and McNemar’s tests\) required no GPU\. We report GPU\-hours for the stages where per\-run timing was explicitly logged, rather than estimate stages that were not\. The H1 100\-entity decomposition round took approximately 5\.5 hours; the H3 SelfCheckGPT resampling stage \(3,290 generations\) took approximately 11 hours; the two cross\-model validation pilots \(Mistral\-7B\-Instruct\-v0\.3 and Falcon\-7B\-Instruct, Section 8\) took approximately 3\.8 and 1\.6 hours respectively for their full\-pool decomposition stage alone\. These four logged stages alone total approximately 22 GPU\-hours\. This is a floor, not a full accounting: earlier\-phase stages \(the original Phase 0 40\-entity run, H2’s labeling passes, H3’s main 734\-decoding CAD run, and Phase 2’s 3B/14B decomposition and activation\-extraction reruns\) were not all individually timed, so the true cumulative total across the full study is higher than the approximately 22 hours we can document precisely\.

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### 1\.12Citation Verification

Per citation\-hallucination\-prevention practice, no bibliographic entry in this draft was written from memory\. Every citation below was confirmed via live web search with a real arXiv ID, author list, and venue/submission date\. The three initially left as\[CITATION NEEDED\]\(Pham et al\., Zhao et al\., Cheng et al\.\) are now resolved, using leads from the user’s ownresearch\_gap\_analysis\.mdliterature\-review notes to target the search rather than searching blind:

All citations in the main text now resolve to a specific paper; none remain marked\[CITATION NEEDED\]\.

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\\appendix

### 1\.13Appendix

#### 1\.13\.1Pilot \(n=14\) vs\. primary \(n=64\) robustness

The original pilot, on Phase 0’s 40\-entity pool \(n=14 DI\-CC positives\), is small enough on its own to warrant caution about sampling variance, but is retained because it is the sample the mechanistic claim was first pre\-registered against\.

All four configurations are strongly significant with CIs well clear of 0\.5, and the n=64 CIs are consistently narrower than their n=14 counterparts \(e\.g\., DI\-CC vs\. legit CI width 0\.098 at n=14 vs\. 0\.075 at n=64 under variance\-ratio selection\)\. The larger sample tightens the estimate without changing its conclusion\. We flag deliberately that the variance\-ratio criterion wasnotpre\-registered: as Section 7 narrates, we adopted it only after observing that accuracy\-based selection produced an inconsistent transfer signal across model scale, specifically after seeing it fail to reach significance at 14B\. Applying a criterion chosen because it improved an inconvenient result to the primary sample carries a real risk of selection\-induced optimism, and we do not treat variance\-ratio’s numbers as an independent confirmation of accuracy’s numbers for that reason\. Whatdoesconstitute pre\-selection\-robust evidence is the accuracy\-only row: it was never adjusted post\-hoc, transfers significantly at both sample sizes, and needs no methodological caveat\.

#### 1\.13\.2Probe robustness under realistic class imbalance

We separately tested training the probe at a downsampled, closer\-to\-deployment class ratio \(approximately 6\.8% positive, the closest stable ratio achievable given NQ\-Swap’s size, targeting DI\-CC’s approximately 3\.2% natural rate from Section 5\), repeating the full downsample\-and\-retrain pipeline acrossN=50N=50random seeds to characterize the result as a distribution rather than a single, potentially noisy point estimate\. AUC on the n=64 transfer set did not degrade under imbalance \(in fact rose numerically\), but fixed\-threshold \(0\.5\) conflict\-class recall on the NQ\-Swap held\-out set collapsed from 0\.808 ± 0\.039 \(balanced training, tight across seeds\) to 0\.247 ± 0\.190 \(imbalanced training, range \[0\.00, 0\.75\] across seeds\)\. This is a mean drop of more than two standard deviations, confirming the collapse is a real, stable effect rather than single\-split noise, and consistent with the classifier partly exploiting a majority\-class shortcut rather than a cleaner concept direction \(validation accuracy rose for the same reason a trivial majority\-class classifier’s would\)\. The multi\-seed analysis also surfaces a second, independent concern: imbalanced\-condition recall is itself highly seed\-dependent \(std 0\.190 vs\. 0\.039 for balanced\), meaning a single retraining of this probe at realistic prevalence could plausibly catch anywhere from none to three\-quarters of true conflicts\. This unpredictability compounds the low mean recall\. We report this as a first\-class limitation of the probe as a practical detector, not merely of this specific dataset’s class balance\.

#### 1\.13\.3The Turing birth\-year case

The one exception among the 14 Phase 0 DI\-CC cases \(Section 4\.3\) involved Alan Turing’s birth year and revealed a specific, interpretable limitation rather than a false claim\. The decomposer’s output \("1912," the historically correct year\) was in fact correct and appeared to genuinely reflect the model overriding the perturbed value, but the elicited knowledge dump used to verifyrecoverabilitycontained a typo \("1812"\), and the general\-purpose NLI model judged this single\-digit\-different string sufficiently entailed to pass the recoverability check\. This exposes a specific weakness, that general NLI models are insensitive to fine\-grained numerical precision, that is orthogonal to whether DI\-CC itself is real\.

#### 1\.13\.4H1 regression instability, in detail

Between the two rounds \(30 entities, then 100\), the identity of the "significant" predictor shifted \(entity density in round one, average sentence length in round two\), and logistic regression coefficients on pronoun density were implausibly extreme \(odds ratios in the tens of thousands\)\. Both are signatures of small\-sample instability rather than a genuine, precisely estimated effect\.

#### 1\.13\.5CAD decoding\-loop implementation

We implement the contrastive decoding loop \(Section 6\) as a hand\-written greedy decoding loop maintaining two parallel KV caches \(one per branch\), feeding the same sampled token back into both\. The official CAD implementation’s multi\-process batch\-file framework was not adopted, since it targets a different \(multi\-GPU, multi\-model\) deployment setting than our single\-GPU, resumable\-stage\-script pipeline\. Only the decoding formula itself was reused\.

#### 1\.13\.6Variance\-ratio selection order: full justification

This is a real researcher\-degree\-of\-freedom\. Had variance\-rationotrescued 14B, we cannot rule out that we would have tried a third criterion, and reporting only the criterion that "worked" without accounting for that search inflates the apparent significance of the 14B flip specifically\. We do not think this invalidates the reanalysis, for three reasons that are evidential rather than a mere assurance\. \(a\) The 3B same\-layer result is a genuine negative control fixedbeforewe knew what 14B would do under variance\-ratio\. If the criterion swap mechanically improved any result it touched, 3B should have moved too, and it did not\. \(b\) The criterion itself, and its literature justification, predates this paper and was not tuned on our data\. We chosewhetherto apply it after seeing a null, but nothowit is defined\. \(c\) The human verification in Section 7 confirms the 14B DI\-CC labels themselves \(fixed independently of any layer selection\) are clean, so the flip is not an artifact of mislabeled cases becoming favorably re\-classified\.

#### 1\.13\.7Additional observations from the 14B case review

Review of the 29 cases surfaced several observations that do not affect the DI\-CC judgment but are relevant to future analysis\. Two cases perturb a non\-birthdate detail \(a presidency start year and a historical\-event date\) rather than a birth year, which would need separate handling in any analysis that assumes a fixed birth\-token position\. One case \(a historical figure whose birth year is genuinely disputed among historians\) has grounding that holds only relative to a scholarly convention rather than an uncontested fact\. Six cases phrase the claim as an explicit contrast \("born in 1912, not 1949"\) that trivially embeds the perturbed value, making contradiction detection easier than for plain declarative claims and a candidate for separate statistical treatment in future work\. And, consistent with the Phase 0 finding \(Appendix[1\.13\.3](https://arxiv.org/html/2608.10627#S1.SS13.SSS3)\) that knowledge dumps are not ground\-truth oracles, several dumps contained unrelated fabricated details \(invented graduation dates, an invented marriage, fabricated professional history\) that did not affect the labeled claim\.