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Causal Localization of Evidence Effects in Transformers

Jipeng Li, Pramod Khargonekar, Yanning Shen

arXiv:2610.36524v1cs.CLcs.LG

TL;DR

The paper asks whether controlled symbolic inputs can identify attention heads that influence natural-language evidence decisions. It introduces CEA and BUC to select heads using count effects and removal-and-recovery interventions, then finds that symbolic-selected heads affect both unused count comparisons and a labeled language task.

  • Problem

    It is an empirical question whether components localized with controlled symbolic inputs remain relevant to natural-language evidence decisions.

    Source: §1 · p. 1

  • Method

    CEA varies symbol counts and order in fixed prompts, while BUC selects compact head sets by jointly evaluating ablation and bidirectional mean patching.

    Source: §1 · p. 1, §3.2 · p. 3

  • Results

    Ablating symbolic-selected heads in Pythia-410M removes 65.5–91.6% of the count effect, and ablating eight lowers NL accuracy by 8.2 percentage points versus 0.8 for matched random sets.

    Source: §1 · p. 2

  • Takeaways & Limitations

    Controlled symbolic probes can identify compact attention head sets whose causal influence extends to predictions in a labeled language task.

    Source: §7 · p. 9

    The labeled bridge does not establish general natural-language reasoning or identify whether shared computation processes reports or writes the yes/no response.

    Source: §6 · p. 9

Abstract

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Can controlled symbolic inputs reveal attention heads that influence a language model's decisions from natural language evidence? We introduce controlled evidence aggregation (CEA), which varies the counts and order of two symbols in otherwise fixed prompts and measures changes in a frozen Transformer's preference between two answer tokens. The preference is measured by their logit difference; the prompts prescribe no correct answer. Balanced utility causal selection (BUC) identifies compact head sets by jointly evaluating how much ablating their outputs removes the count effect and how closely patching mean outputs between count conditions recovers the effect in both directions. We derive conditional bounds linking head attribution to intervention effects and specifying when the attribution shortlist can be recovered from finite samples. In Pythia-410M, ablating sets of 1-12 heads selected separately for four ordering regimes removes 65.5-91.6% of the count effect. The sets retain their influence on count comparisons not used for selection. To test relevance beyond symbolic inputs, we evaluate a natural language task asking which state is supported by more reports. Ablating eight heads selected only on symbolic yes/no prompts lowers mean accuracy by 8.2 percentage points, versus 0.8 for random sets matched by size and layer. Our results demonstrate that controlled symbolic probes can identify compact attention head sets whose causal influence extends to natural language decisions.

1 Introduction

The paper asks whether controlled symbolic inputs can localize attention heads whose influence extends to decisions from natural-language evidence. It introduces CEA and BUC, derives conditional theory, and tests selected heads on symbolic and labeled language tasks.

1 Introduction

  • CEA varies symbol counts and order in otherwise fixed prompts, then measures the change in answer-token logit difference without prescribing a correct answer.The fixed template, symbol identities, sequence length, and local answer context restrict the input changes.Source: §1 · p. 1
  • BUC jointly selects compact head sets using ablation to measure removal of the count effect and bidirectional mean patching to measure its recovery.The method evaluates sets jointly rather than summing individual head effects.Source: §1 · p. 1
  • Conditional theory links attribution mismatch to intervention-score errors and gives finite-sample conditions for recovering the population attribution shortlist.A separate greedy bound applies under monotonicity and weak submodularity to a weighted sum of raw intervention gains.Source: §1 · p. 1
  • In Pythia-410M, ablating 1–12 heads selected for four ordering regimes removes 65.5–91.6% of the count effect; symbolic-selected heads also lower NL accuracy by 8.2 points versus 0.8 for matched random sets.The NL comparison tests transfer to a labeled task asking which state has more supporting reports.Source: §1 · p. 2

2 Related work

Related work localizes components using behavioral targets, studies circuit reuse and evaluation, and develops methods for selecting components or edges. CEA distinguishes controlled-response localization from successful reselection across prompts.

2 Related work

  • Behavioral-target studies localize components for induction, factual recall, indirect-object identification, and task vectors, while symbolic models and structured tasks support comparisons with designed algorithms and expose compositional failures.CEA controls count and order without training a symbolic rule, then tests fixed-set effects on labeled evidence.Source: §2 · p. 2
  • Prior work examines cross-task reuse, prompt-variant generalization, ablation dependence, and tests of circuit preservation, localization, and minimality.CEA tests which controlled changes preserve the effect of the same head set, separating this from successful reselection.Source: §2 · p. 2
  • Activation and path patching test supplied behavioral targets, while ACDC and EAP use intervention-based search or edge attribution; BUC scores set-level removal and bidirectional recovery.Equal head budgets do not equate search cost or intervention granularity.Source: §2 · p. 2

3 Controlled target and causal tests

The paper defines a controlled symbolic count comparison, specifies head-level interventions, and uses joint set selection to evaluate removal and recovery. Its interpretation is bounded by the prompt, readout, intervention position, and donor rule.

3.1 Symbolic CEA target

  • CEA compares B/C counts under fixed ordering regimes and measures answer-token preference; count changes also alter symbol positions, so the contrast does not isolate count from every positional feature.The canonical prompt uses a fixed prefix, evidence region, tail, and answer cue; separate comparisons hold counts fixed while changing ordering.Source: §3.1 · pp. 2–3

3.2 Head attribution and intervention unit

  • Ablation zeros selected final-position head writes, while mean patching substitutes opposite-count donor means; shrink and match operationalize removal and recovery, not an isolated sufficient circuit.Unselected components and downstream computation remain active during interventions.Source: §3.2 · p. 3

3.3 BUC selection and evaluation

  • BUC screens attribution-ranked heads and greedily evaluates each candidate jointly with the current set, accounting for measured interactions omitted by fixed individual-head rankings.The main configuration uses λ = 1/2 and at most 12 heads; interpretation depends on model, inputs, readout, position, and donor rule.Source: §3.3 · p. 3

4 Conditional bounds for attribution and selection

The theory gives conditional bounds for connecting attribution to intervention scores, recovering an attribution shortlist, and approximating raw utility with greedy search. Each result depends on its own assumptions and does not by itself establish the next step.

4 Conditional bounds for attribution and selection

  • Under bounded attribution mismatch, intervention-score error is controlled, but strong removal and recovery require cumulative attribution near the clean contrast, and weak contrasts amplify normalized error.The bounds depend on residual conditions; small mismatch alone does not guarantee strong normalized scores.Source: §4 · p. 4
  • With independent matched pairs, a population attribution-score gap greater than 2η between ranks m and m + 1 guarantees exact top-m shortlist recovery with probability at least 1 − δ.This guarantee concerns attribution ranking, not subsequent intervention screening, and repeated deterministic inputs do not estimate uncertainty over other prompts.Source: §4 · p. 4
  • Under monotonicity and weak submodularity, exact forward greedy is bounded against the size-k optimum of raw utility, not BUC’s normalized objective.The objectives differ, so the theorem does not guarantee BUC’s empirical maximization of Qλ.Source: §4 · pp. 4–5

5 Experiments

The experiments test whether compact head sets selected from controlled symbolic count contrasts generalize across counts, orderings, readout pairs, and natural-language evidence decisions. They find partial transfer to a balanced natural-language task, alongside scope limits in reuse and finite selection audits.

5.2 Budget-matched baseline comparison

  • BUC improves recovery rather than joint-threshold coverage: both methods pass FRONT, INTERLEAVE, and RANDOM means and fail BACK.Relative to sensitivity-only, BUC raises bidirectional match by 0.083–0.111 and reduces shrink by 0.018–0.049 in BACK, INTERLEAVE, and RANDOM; FRONT ties at displayed precision.Source: §5.2 · p. 5, Table 2 · p. 6

5.3 Count generalization and ordering dependence

  • Heads selected at (50, 150) reduce count-response slopes by 0.646–0.896 and retain positive effects on three unseen gaps without reselection.One unseen pair shares a selection endpoint; the other two use new endpoints.Source: §5.3 · p. 6, Table 3 · p. 6
  • With identical B/C counts, four order-only contrasts still produce absolute output effects of 0.321–1.846; BUC shrink/match ranges are 0.603–0.842/0.651–0.884.Random-set shrink/match is 0.049–0.081/0.056–0.088, and fixed-set cue changes retain shrink 0.64–0.93 and match 0.70–0.96.Source: §5.3 · p. 6

5.4 Readout-pair audit

  • Of 1,024 registered regime–pair conditions, 960 have |b∆r| ≥ 0.01; only 0.060 pass both thresholds overall and 0.064 of evaluable conditions.Strong fixed-set reuse is uncommon under these thresholds; failing them does not imply zero detectable influence.Source: §5.4 · pp. 6–7

5.5 Lexically balanced natural-language bridge

  • In the held-out natural-language bridge, mean restricted accuracy is 0.772 on unseen state pairs and paraphrases; the graded response has Spearman correlation 0.901 and linear R2 = 0.812.The task uses 16 reports with balanced state-word frequencies, so word totals alone cannot solve it.Source: §5.5 · p. 7
  • At k = 8, symbolic yes/no-selected heads lower NL accuracy by 8.2 percentage points versus 0.8 for matched random controls; the BF16 transfer ratio is 0.555.The ratio compares intervention effects, not a fraction of shared heads; the BF16 summaries lack bootstrap intervals required by the full declared bridge criterion.Source: Table 5 · p. 7, §5.5 · p. 7

5.6 Scope checks

  • Applying selected heads only at symbolic-sequence positions yields shrink 0.001–0.059 and match −0.006 to 0.006; representative FRONT, INTERLEAVE, and RANDOM heads show stronger OV-only than QK-only match.Word-symbolic, signal-token, and short-sentence inputs retain mean shrink/match of 0.812/0.845, 0.820/0.852, and 0.765/0.790; input-only Greedy Occlusion requires token scores and does not measure head-patching match.Source: §5.6 · p. 8

5.7 Attribution and selection audits

  • Across sampled head sets, cumulative attribution correlates 0.841–0.923 with ablation gain and 0.755–0.884 with oriented patch gains, but this is association, not an attribution-error bound.Observed negative marginals establish nonmonotonicity only in tested finite pools; local-pool regret is 0.021–0.043, and only RANDOM rejects the specified exchangeability null.Source: §5.7 · p. 8, Table 7 · p. 8

6 Discussion and limitations

The discussion limits what the interventions establish and identifies statistical and practical boundaries. It also outlines tests needed to extend the findings.

6 Discussion and limitations

  • The fixed symbolic set affects labeled natural-language predictions, but the shared computation may process reports or write the yes/no response; phrase-based strategies remain possible.The results do not establish general natural-language reasoning, and the interventions identify final-position writes rather than complete head–MLP paths.Source: §6 · p. 9
  • Bootstrap intervals condition on fixed sets and donors, while repeated deterministic inputs do not support prompt-sampling intervals.The BF16 bridge lacks required bootstrap intervals; expanded FP32 summaries have no CIs and use one seed for causal selection.Source: §6 · p. 9
  • Further work should distinguish evidence aggregation from answer-readout effects and test longer heterogeneous reports and multi-token decisions.The paper also notes that localized components could enable targeted manipulation, while its audits do not certify deployment safety.Source: §6 · p. 9

7 Conclusion

The paper concludes that controlled symbolic probes identify attention heads with causal influence on predictions in a labeled language task. It presents theoretical conditions, study scope, and materials for reproducing the work.

7 Conclusion

  • Controlled symbolic probes identify attention heads whose causal influence extends to predictions in a labeled language task.The study also reports that selected heads affect unused count contrasts, and that a fixed symbolic yes/no set reduces labeled natural-language accuracy more than layer- and size-matched random controls.Source: §7 · p. 9

AI use statement

  • Generative AI tools assisted with language editing, document structure, LaTeX formatting, and checking mathematical claims and proofs.The authors take responsibility for the final text, claims, code, measurements, and statistical procedures.Source: AI use statement · p. 10

Ethics statement

  • The work uses open pretrained models and controlled prompts, without personal data or human subjects; the authors identify manipulation and overstatement risks.The ethics statement says Section 6 restricts the supported conclusions.Source: Ethics statement · p. 10

Reproducibility statement

  • Source code and configurations are under anc/code/ and anc/protocol/, with aggregate measurements under anc/results/.Appendix F.5 describes package contents, dependencies, and experiments outside the supplied implementation.Source: Reproducibility statement · p. 10

A Proofs and scope of the theoretical claims

  • The theoretical claims concern population quantities and stated operators; finite donor estimates, other positions, and other operators require separate error control.The setup assumes finite expectations, fixes an ordering regime and count contrast, and defines cumulative attribution by summing head contrasts.Source: A Proofs and scope of the theoretical… · p. 12

A.1 Readout and intervention conventions

  • The readout is the difference between two answer-token logits, but this identity does not make an arbitrary token pair a labeled task.Direct attribution can differ from intervention effects because of later normalization and nonlinear computation; finite-bank donor discrepancies require error control.Source: §A.1 · p. 12

A.2 Proof of T1

  • The proof bounds intervention-gain differences from cumulative attribution, extending the bound to mean patch gain and raw joint utility.The stated result follows because those quantities are convex combinations of the bounded differences.Source: §A.2 · p. 13

A.3 Normalized scores and error amplification

Normalized intervention scores depend on attribution alignment and intervention error, while the evidence-position approximation is conditional on its residual and kernel assumptions.

A.3 Normalized scores and error amplification

  • Each normalized score is bounded below by one minus attribution mismatch plus intervention error, scaled by the absolute clean contrast.Good recovery requires both alignment with the clean contrast and small intervention error; large attribution can overshoot, and scores are undefined when the clean contrast is zero.Source: §A.3 · p. 13

A.4 A conditional approximation by evidence position

  • Under the stated additive position-kernel approximation, a fixed set’s attribution change across equal-count regimes is bounded by the profile difference.The approximation is conditional: experiments do not estimate uniformly small errors, and higher-order token interactions can enter the residuals.Source: §A.4 · pp. 13–14

A.5 Proof of T2 and sampling conditions

The appendix gives conditions for shortlist recovery and a conditional greedy bound, then documents the original BF16 experiments and prompt setup.

A.5 Proof of T2 and sampling conditions

  • A strict population score gap exceeding twice the sampling error ensures exact recovery of the top-m attribution shortlist.The concentration argument requires independent matched pairs; duplicate deterministic prompts do not provide prompt variation or validate a richer target distribution.Source: §A.5 · p. 15

A.6 Proof and limits of T3

  • The greedy bound applies to raw utility only under monotonicity and weak submodularity, and does not guarantee BUC’s empirical normalized-utility maximization.The theorem is conditional on the screened pool; it gives no guarantee about excluded heads, minimum circuit size, or uniqueness.Source: §A.6 · pp. 15–16

B Additional experimental details and results

  • Appendix B reports configurations and results for the original BF16 study; native FP32 configurations and controls are specified separately.The two configurations are analyzed separately, not pooled.Source: B Additional experimental details and… · p. 16

B.1 Prompt, model, and tokenization details

  • The canonical prompts use 200 evidence symbols and a 50-symbol A-only tail, with answer strings “various” and “successful” audited as single-token candidates.The experiments use the controlled evidence aggregation prompt family.Source: §B.1 · p. 16

B.2 Data splits, selection pipeline, and control construction

This appendix section describes the head-selection pipeline and controls, reports diagnostics on selected heads, intervention scope, and selection sensitivity, and qualifies what the diagnostics establish and how black-box search is evaluated. It also tests BUC beyond its selection condition using alternate readout pairs, fixed-set count sweeps, and equal-count order contrasts.

B.2 Data splits, selection pipeline, and control construction; B.5 Selected head identities and stability

  • BUC selection keeps 192 sensitivity-ranked heads, forms a 48-head joint-score pool, and greedily selects up to 12; random controls preserve layer counts, and deterministic-regime sets were identical across five seeds.Selection and final evaluation use disjoint prompt batches; the final split contains 96 prompts at each evidence level.Source: §B.2 · p. 16, §B.5 · p. 18

B.5 Selected head identities and stability

  • The three listed RANDOM sets had pairwise overlaps of 6/9, 5/9, and 6/7; these cover seeds 0–2 only, unlike intervention summaries spanning five executions.Seeds 3 and 4 are excluded from the reported RANDOM overlap calculation.Source: §B.5 · p. 19

B.6 Mechanistic diagnostics of selected heads

  • OV-only patching had larger match than QK-only in the listed FRONT, INTERLEAVE, and RANDOM examples, while both split interventions had substantial effects in BACK.These measurements distinguish routing and writing interventions for the tested heads; they do not additively decompose the complete effect or identify all earlier computations.Source: §B.6 · p. 19, Table 16 · p. 19

B.7 Final-position intervention scope

  • The SEQ intervention effect was near zero in every regime; the reported RANDOM LAST-shrink range of 0.835–0.917 does not represent the same five-execution cohort as Table 13.The scope diagnostic uses the same selected head set for LAST and SEQ, but the supplied aggregates do not resolve the RANDOM cohort difference.Source: §B.7 · p. 19, Table 17 · p. 20

B.11 Sensitivity to the joint-utility trade-off

  • Relative to λ = 1/2, λ = 0.25 and λ = 0.75 retained mean Jaccard overlaps of 0.885 and 0.820; increasing removal weight traded patching match for shrink.The comparison covers only the tested objective weights.Source: Table 22 · p. 21, §B.11 · p. 22

B.12 Greedy-prefix curves

  • FRONT and INTERLEAVE had small greedy-prefix increments after the first few heads, while BACK continued improving through the maximum tested budget of 12; no plateau beyond 12 was established.The diagnostic tracks shrink and average patch match across prefixes of the greedily selected heads.Source: §B.12 · p. 22, Table 23 · p. 22

B.13 Black-box input-level interventions; B.14 Greedy Occlusion algorithm

  • Greedy Occlusion selects evidence positions by forward masking-shrink queries and evaluates add-back only after selection on held-out data; its signed recovery ratio permits overshooting and does not establish head attribution.The algorithm uses input-output queries only, without gradients or internal model states; normalized input scores require a nonzero base evidence effect.Source: §B.14 · pp. 22–23, §B.13 · p. 22

C.1 Seven readout pairs

  • Across four regimes and five seeds, mean |∆r| was 0.721–2.083, selected-set size 4.50–7.50, and BUC shrink and match were 0.642–0.861 and 0.701–0.884.Layer-matched random shrink was 0.048–0.076 and random high-to-low match 0.059–0.083. The A/B pair is an overlap stress test because its symbols also appear in prompts; targeted pairs showed positive local effects and partial fixed-set reuse, but source and target sets had different budgets and samples, preventing a paired estimate of reselection benefit. In a separate FP32 registry, 6.0% of fixed-set conditions passed joint thresholds; failure of a fixed source set leaves open whether another compact set explains the target.Source: §C.1 · p. 27

C.2 Fixed-set count sweep and unseen gaps

  • For each regime, heads selected only at (bL, bH) = (50, 150) were evaluated across b ∈ {0, 10, . . . , 200} and three unseen gaps without reselection.The fixed set was tested on gaps (0, 150), (25, 175), and (75, 125).Source: §C.2 · p. 27

C.3 Causal localization of order-only contrasts

  • Across four equal-count order-only contrasts, |∆ord| was 0.321–1.846, BUC shrink 0.603–0.842 and match 0.651–0.884, versus layer-matched random shrink 0.049–0.081 and high-to-low match 0.056–0.088.Because the contrasts hold counts equal by construction, the localized effects cannot be attributed to count changes.Source: §C.3 · pp. 27–28

C.4 Balanced-objective baseline decomposition

The balanced-objective decomposition finds a recovery-oriented trade-off rather than uniform gains across removal and recovery. The natural-language bridge specifies a lexically balanced report task and evaluates fixed eight-head sets on disjoint selection and evaluation data.

C.4 Balanced-objective baseline decomposition

  • BUC’s summed-score differences from ActPatch are 0.015, 0.129, 0.135, and 0.169 across regimes, while component changes support a recovery-oriented trade-off, not gains in both metrics.For BACK, INTERLEAVE, and RANDOM, BUC exchanges 0.018–0.049 of shrink for 0.083–0.111 of mean match; in FRONT, losses and gains cancel at displayed precision.Source: Table 36 · p. 28, §C.4 · p. 28
  • Both BUC and sensitivity-only pass the joint shrink ≥0.85 and mean match ≥0.70 criterion in FRONT, INTERLEAVE, and RANDOM, but both fail in BACK.BUC raises BACK’s mean match from 0.648 to 0.759, while shrink is only 0.655; three passing aggregate rows are not a per-seed success rate.Source: §C.4 · p. 28
  • The comparison does not isolate greedy augmentation’s benefit because the selection objectives and search procedures differ, and an identical-objective, identical-pool comparison remains untested.The reported timings also exclude shared selection costs, so they do not establish an end-to-end cost advantage.Source: §C.4 · p. 28

D Full natural-language bridge specification

  • The bridge evaluates a frozen 24-layer, 16-head Pythia-410M model with final-position interventions and eight-head sets, using five seeds and layer-matched random controls.The controls preserve both set size and selected layer pattern; their 120 draws per seed are reported alongside means and standard deviations, not bootstrap confidence intervals.Source: D Full natural-language bridge… · p. 29
  • The natural-language task uses 16 reports about mutually exclusive states, with direct and negated forms balanced so state-word counts remain equal across evidence counts.Each bank preserves its own lexical multiset and audited token length across counts, but different banks are not claimed to have identical tokenization.Source: D Full natural-language bridge… · p. 29
  • Selection uses three state pairs and Bank A, while evaluation uses new state pairs and Bank B; the splits are disjoint, and evaluation spans eight counts.Symbolic CEA selection uses no natural-language prompts; lexical balancing rules out strategies based only on total state-word or “not” frequencies, but not local phrase processing or reliance on some reports.Source: D Full natural-language bridge… · pp. 29–30
  • The bridge compares symbolic-selected and natural-language-selected eight-head sets on their own and transferred targets, without changing head identities after transfer.Selection screens 192 heads to 48 before greedily selecting eight; the procedure ranks absolute attribution contrasts and evaluates each set on both targets.Source: D Full natural-language bridge… · p. 30
  • The transfer ratio places transferred utility relative to random and target-selected utility only when its denominator is positive; it is not a measure of shared heads or algorithm reuse.The BF16 summary uses one random reference per target, whereas the expanded FP32 protocol matches source and target layer patterns separately.Source: D Full natural-language bridge… · p. 30

D.1 Results

This section examines behavioral sensitivity to symbolic count differences and the causal influence of selected heads on natural-language decisions, including fixed-set generalization and a paired-label null test. It also reports a separate FP32 audit of intervention operators, selection, and transfer, while noting that important statistical and mechanistic claims remain unestablished.

D.1 Results

  • At gap (4, 12), restricted accuracy was 0.772, PairAcc 0.604, and MinPairAcc 0.583; the full-sweep Spearman correlation was 0.901.The full-sweep linear R2 was 0.812; neither statistic establishes exact monotonicity. Constant word counts rule out total-frequency explanations but do not establish majority computation over all report meanings, and required prompt-pair bootstrap intervals were not supplied.Source: §D.1 · pp. 30–32
  • On the natural-language target, the fixed symbolic set reduced accuracy by 8.2 points, versus 0.8 for random controls; the NL-selected set reduced it by 15.2 points.The corresponding slope reductions were 0.411, 0.051, and 0.721, respectively. These aggregate changes do not identify which examples changed predictions.Source: Table 40 · p. 31, §D.1 · pp. 31–32

E Native FP32 supplemental experimental protocol

  • The supplemental FP32 study used distinct sampling, donors, and controls from BF16 experiments, and its expanded natural-language bridge covered three models rather than the six-model symbolic sweep.FP32 and BF16 measurements were not pooled.Source: E Native FP32 supplemental… · p. 33, §E.1 · p. 33

E.1 Shared configuration, pairing, and randomization

  • Symbolic prompts varied B and C counts in fixed 200-symbol sequences, using FRONT, BACK, INTERLEAVE, or matched RANDOM orderings while holding prompt framing and readout order fixed.Repeated deterministic prompts were not treated as independent samples; RANDOM used distinct matched permutations as sampling units.Source: §E.1 · pp. 33–34

E.2 Intervention unit, empirical scores, and BUC selection

  • Head interventions zeroed or replaced selected pre-projection head vectors while leaving unselected heads and downstream operations active; BUC greedily added heads using selection data and stopped at specified shrink and bidirectional-match thresholds.Evaluation scores were excluded from selection, and the normalized objective is distinct from the raw utility for which the conditional theorem is stated.Source: §E.2 · pp. 34–35

E.3 Statistical units and uncertainty

  • Intervention uncertainty used 1,000 matched-pair cluster-bootstrap replicates with fixed selected heads and donor banks, so intervals were conditional on selection and donors.Normalized-metric intervals retained only replicates with non-weak contrasts.Source: §E.3 · p. 35

E.4 Fixed-set intervention-operator audit

  • The fixed-set operator audit applied the same primary stopping sets across operators, using calibration-bank donors for ablation and directional patching and orientation-stratified donors for natural-language replacement.Stochastic operator conditions used 12 draws; mean and exact matched-example conditions used one evaluation.Source: §E.4 · p. 36, Table 43 · p. 36

E.5 Finite T3 audit and exact local comparisons

  • The FP32 finite audit found negative evaluation marginal fractions of 31%, 17%, 28%, and 22% across FRONT, BACK, INTERLEAVE, and RANDOM, with minimum empirical ratios from −5.8 to −2.6.These finite-pool observations witness nonmonotonicity and negative ratios for the tested normalized objective, not population-wide properties or contradictions of the conditional raw-utility theorem.Source: §E.5 · p. 37

E.7 Count, prompt, ordering, and seed generalization

  • The fixed set is evaluated without reselection on unseen count pairs, prompt-cue variants, transferred regime-specific heads, order-only contrasts, and RANDOM permutation seeds.The count-pair comparisons use 96 rows per side and a separate calibration bank; order-only tests use equal symbol counts, while seed repeats share evaluation and calibration data.Source: §E.7 · p. 38

E.8 Random readout registry and separate prompt/readout changes

  • The readout study samples 256 ordered pairs of distinct eligible alphabetic token IDs and separately tests fixed-prompt readout changes and joint prompt/readout changes through full BUC reselection.The broad scan reuses the primary set on new output coordinates; swapping readout order reverses raw contrasts and oriented gains but leaves absolute normalized scores unchanged where defined.Source: §E.8 · p. 39
  • At raw-effect threshold 0.01, the fixed-set readout scan had 960 evaluable conditions of 1,024, with pooled passing fractions of 0.060 overall and 0.064 among evaluable conditions.These finite-scan fractions describe reuse of a fixed set under the canonical prompt, not full BUC reselection or head identity invariant to readout.Source: §E.8 · p. 39

E.9 Paired-label selection-matched null

  • The null test requires at least eight unique matched-pair clusters in both selection and evaluation, and rejection does not establish mechanism uniqueness, universal causal validity, or semantic correctness.Its paired exchangeability interpretation depends on the stated split and selection rules; the reported Monte Carlo interval concerns null exceedance probability, not effect size.Source: §E.9 · pp. 39–40
  • Tobs = 2.69 (effect-size CI [2.55, 2.80]) and adjusted p = 0.01 for RANDOM; this is the 1/100 resolution limit, not evidence of p < 0.01.Only RANDOM was estimable in the fixed-count symbolic design; with 99 trials, the observed result implies zero null exceedances.Source: §E.9 · p. 40

E.10 Expanded natural-language bridge

The expanded bridge evaluates whether fixed symbolic head sets affect labeled natural-language decisions, with explicit behavioral, transfer, and numerical-validation protocols. Its aggregate results indicate partial transfer, while limiting what can be concluded from model-level point estimates.

E.10 Expanded natural-language bridge

  • The shared state-pair split assigns domains to selection, validation, and test sets, while final behavioral evaluation uses Banks B–D and both query orientations.The test-domain split is shared across models and behavioral seeds; its assignment is not based on model accuracy or intervention effects.Source: §E.10 · pp. 40, 42, Table 46 · p. 42
  • The task uses sixteen reports, balanced state-word frequencies, paired query orientations, and a two-state assumption to label which state has more supporting reports.The evidence construction balances direct and negated report forms; state words occur eight times each in the evidence region.Source: §E.10 · p. 40, Table 44 · p. 40
  • The expanded transfer protocol fixes eight-head symbolic and NL-selected sets, tests forward transfer on Banks B–D, and uses target-specific donor calibration.A TR is unavailable unless both estimation gates hold; finite ratios may lie outside [0, 1] and do not represent fractions of a uniquely identified circuit.Source: §E.10 · pp. 42–43
  • Accuracy/PairAcc/MinPairAcc are 0.752/0.566/0.541 for Pythia-410M, 0.805/0.651/0.611 for Pythia-1B, and 0.681/0.458/0.414 for GPT-2.No model-level confidence intervals are reported; GPT-2’s PairAcc point estimate is below the 0.5 reference.Source: §E.10 · p. 43
  • Mean TR values are 0.520, 0.557, and 0.438 for Pythia-410M, Pythia-1B, and GPT-2, based on 11, 12, and 9 estimable conditions.These point estimates are consistent with partial intervention transfer, but do not establish positive transfer in every condition, full circuit recovery, or population significance.Source: §E.10 · p. 43

F.1 Native model path and reference computation

  • Native FP32 inference is checked against cached replay, with condition-specific raw-readout and score errors routing failed conditions or candidates to native computation.The refinement rule uses a finite empirical error envelope, not a proved uniform ranking guarantee over unmeasured candidates.Source: §F.1 · p. 44, §F.3 · p. 45

F.5 Reproduction files and implementation coverage

The supplied FP32 package supports some reproduction and implementation checks but omits substantial experiment outputs and several separate experiments. The surrounding discussion distinguishes controlled behavioral targets from component-selection procedures and their intervention units.

F.5 Reproduction files and implementation coverage

  • The package supplies FP32 implementation, tests, configuration records, hashes, and aggregate results, but not a compatible snapshot or complete experiment-output archive.It also does not cover the separate BF16, QK/OV, LAST/SEQ, objective-weight, tail-length, surface-form, input-occlusion, or six-model experiments.Source: §F.5 · p. 46, Table 48 · p. 47

G Extended related work

  • A behavioral target and an intervention or selection rule answer different questions, so finding relevant components is distinct from testing their reuse.Table 49 marks the boundary between nearby lines of work; “same set” means one selected set is tested by ablation and both mean-patching directions.Source: G Extended related work · p. 48, Table 49 · p. 48

G.1 Behavioral targets and controlled evidence

  • CEA changes symbol counts or order without training a symbol-to-answer rule, then tests whether fixed head sets retain effects on labeled natural-language behavior.The symbolic target has no external correctness label; lexical balance and query reversal constrain simple shortcuts but do not eliminate phrase-based strategies or pretrained associations.Source: §G.1 · p. 48

G.2 Interventions and component selection

  • Activation and path patching test supplied behavioral targets, whereas ACDC searches intervention-defined graph structure and EAP ranks candidate edges by attribution estimates.Their targets, graph units, and search budgets need not match a head-set comparison.Source: §G.2 · p. 48
  • BUC jointly evaluates head-set removal and recovery in both patching directions, including set interactions, unlike a baseline that ranks single heads before evaluating their union.That comparison changes both ranking objective and search procedure, so it does not isolate a greedy-search benefit or establish an end-to-end cost advantage.Source: §G.2 · p. 48

G.3 Component reuse across tasks and prompts

The discussion frames cross-task reuse as an empirical question and distinguishes fixed-set intervention effects from overlap, prediction, or claims about a complete mechanism. It also identifies unresolved explanations and scope limits for natural-language transfer.

G.3 Component reuse across tasks and prompts

  • Merullo et al. (2024) report common computational steps across indirect-object identification and Colored Objects, while Nainani et al. (2024) find prompt-variant reuse with additional input edges.These findings establish that reuse can occur, not that it should be presumed in another setting.Source: §G.3 · pp. 48–49
  • De Varda et al. (2026) ask whether circuit overlap and loading predict arithmetic accuracy across numeric and verbal formats, unlike CEA’s direct fixed-set intervention tests.CEA does not claim to predict correctness on arbitrary new tasks.Source: §G.3 · p. 49
  • The labeled bridge compares fixed symbolic and NL-selected sets on shared NL targets at equal head budget, with symbolic selection using no NL prompts.The expanded FP32 transfer uses target-specific donor calibration; positive effects support partial reuse under that intervention protocol.Source: §G.3 · p. 49
  • Because both tasks use the yes/no readout, the comparison cannot isolate shared evidence aggregation from shared answer processing.The targeted readout pairs and larger registered scan are different samples, not a paired estimate of reselection advantage.Source: §G.3 · p. 49

G.4 Faithfulness, localization, and statistical tests

  • The operator audit tests how fixed-set effects depend on replacement distributions rather than assuming a unique, operator-independent circuit.Miller et al. (2024) show that circuit faithfulness scores can change substantially with ablation methodology.Source: §G.4 · p. 49
  • The selection-matched null tests utility under a specified within-pair label-exchangeability null with the adaptive selection pipeline repeated.Rejecting it does not establish minimality or uniqueness, or assign semantic correctness to the symbolic response.Source: §G.4 · p. 49

G.5 Representations and in-context learning interpretations

  • A fixed head set preserves head identity while its activations depend on target inputs and donor distribution, so it is not a fixed activation vector or full account of earlier computation.The exact two-token log-odds identity gives a scalar measure, not evidence of a Bayesian update or optimization algorithm; empirical audits do not establish all conditions for the normalized objective.Source: §G.5 · p. 49
  • Open questions include whether NL transfer reflects shared count/order processing, shared answer readout, or both, and whether effects persist across checkpoints or longer heterogeneous evidence.The reported fixed-head-set tests do not resolve earlier-token or head–MLP-path contributions.Source: §G.5 · p. 49

H FP32 confidence intervals and statistical scope

The appendix reports uncertainty and statistical scope separately for several FP32 outcomes. Most summaries are finite-design point estimates rather than model-level or population-level inference.

H FP32 confidence intervals and statistical scope

  • Table 6 reports descriptive model means and transfer-coverage counts, not model-level confidence intervals or cross-model inference.The condition-level procedures do not provide intervals for those means; the Table 50 bootstrap intervals use matched clusters with head sets and donor banks fixed.Source: H FP32 confidence intervals and… · p. 50, Table 50 · p. 50
  • FRONT, BACK, and INTERLEAVE each have one unique symbolic input per fixed count, so repeated copies provide no independent prompt variation or prompt-bootstrap confidence interval.Their point estimates describe specified inputs, not uncertainty over a richer prompt population; the RANDOM interval excludes zero.Source: H FP32 confidence intervals and… · p. 50
  • Finite-design spans, passing fractions, and operator summaries describe tested conditions, not a population guarantee or a bound for the full pool.The registered readout scan has no population confidence interval over alternative registries.Source: H FP32 confidence intervals and… · p. 50
  • With 99 completed trials and one estimable hypothesis, bp = 0.01 corresponds to zero null exceedances and a 95% Clopper–Pearson interval of approximately [0, 0.0366].That interval concerns null-exceedance probability, not effect size, adjusted p-values, or trial count.Source: H FP32 confidence intervals and… · p. 50
  • NL transfer ratios and accuracy decreases are point estimates, not model-level significance tests or evidence of positive transfer in every condition.Retained condition-level intervals are not model-level confidence intervals, and the results do not establish complete circuit recovery or differences between models.Source: H FP32 confidence intervals and… · p. 50
  • The BF16 tables report execution means and standard deviations, not the prompt-pair bootstrap intervals required by the declared criterion.Neither those summaries nor the separate FP32 procedures establish the complete BF16 criterion.Source: H FP32 confidence intervals and… · p. 50

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