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Paper summary
The paper addresses order-dependent in-context learning by proposing a causal-masking account of why demonstration ordering affects ICL accuracy by up to tens of percentage points. It derives a closed-form position-dependent amplification factor W(p,k,L) for causal linear attention, defines permutation-dependent sequential stability coefficients beta_sigma, and proves an order-dependent generalization bound (Theorem 4), a rearrangement-based low-sensitivity-first ordering result (Theorem 5), and a non-vacuity criterion (Theorem 6) plus a spherical-concentration coherence certificate (Lemma 7). The empirical hierarchy includes single-layer invariance (spread below 1e-8), trained-vs-untrained equivalence under normalized attention (TOST p=0.033), W-factor recovery in the gap matrix, a learned-score variance ceiling, and 8-39% accuracy spread on AG News/RTE across four 7-8B LLMs.
Critical strengths
- The paper provides a tractable, falsifiable mechanism for order-dependent ICL: causal masking yields position-dependent amplification, with single-layer invariance as a sharp empirical prediction. The authors test that prediction to numerical precision and use trained-vs-untrained equivalence to separate architectural from learned causes.
- The empirical hierarchy is unusually broad for a theory paper: synthetic causal linear attention, softmax models, four 7-8B instruction-tuned LLMs, a learned-score variance ceiling, and cost-adjusted baselines are all connected to the same framework. The supplementary code is detailed and the README is reproducible in intent.
Critical weaknesses
- The practical regime of the bound is very narrow. The non-vacuity criterion (Theorem 6) requires B3R2 < 0.059 at k=5, alpha=0.05, rmax=0.6, which is a small architecture/source-radius region. The default experimental setting and LLM regime likely do not satisfy the worst-case condition; the entropy-based tightening is a measured, post-hoc substitute and is not integrated into the main theorem. This limits the claim that the framework certifies orderings in the same regime where the 8-39% LLM spread is observed.
- The ordering-rule benefit is not clearly superior to simple random trials. Table 2 shows Random-20-tries (0.113 mean risk, 96th percentile, 87% gap capture, 20 evals) dominates or matches Greedy (0.122 mean risk, 60th percentile, 21% gap capture, 126 evals) on the shared query budget. The variance-ceiling analysis is valuable, but it also shows that the theoretically clean per-example sensitivity score saturates only a ceiling that remains far from full recoverability at dx <= 32 in some regimes. The main operational claim therefore needs a stronger cost-adjusted comparison or a better score.
Questions for authors
- Please specify the exact parameter regime under which each experimental configuration satisfies Theorem 6's non-vacuity condition. Does the 8-39% LLM spread occur inside or outside the certified regime?
- The entropy-based tightening is described as cutting the vacuity gap by a median of 3.4 orders of magnitude on 44/44 trained models. Please provide the formal status of this tightening: is it a theorem-compatible bound, a heuristic, or a post-hoc measurement? How does it affect the official Theorem 6 statement?
- In Table 2, how should the reader reconcile Greedy's 21% gap capture and 126 evaluations with the conclusion that the rearrangement rule is an efficient ordering strategy, given Random-20-tries captures 87% with 20 evaluations?
- What is the sensitivity of W(p,k,L) to the prefix-normalization and residual assumptions? Does the closed form remain the correct amplification factor under learned attention normalization or attention probabilities that are not near-uniform?
- How were the LLM permutations selected and are the 32 queries per permutation sufficient for stable accuracy-spread estimates? What is the confidence interval on the 8-39% spread values?
- Can the learned score be replaced by a theoretically justified estimator of eta_j or v_j? The current score is a trained predictor trained on the same gap matrix, which weakens the "certified" interpretation.
- Please clarify the exact role of Lemma 7's coherence certificate in the empirical claims. Is the claimed "distinct sources resolved at cost dx = Theta(log k)" actually exercised in any experiment?
- Does the framework make a falsifiable prediction about softmax multi-layer models beyond high entropy? The paper reports good fit but the amplification profile appears only weakly matched (rs=0.57).
4 comments
Author Response to Reviewer UaKg (Part 2/2): LLM CIs, Prop. 21, Lem. 7, & Softmax Tests
(Continued — Part 2/2: Technical Questions Q5–Q8)
Q5 (LLM permutation sampling, -query quantization, 95% CIs, and tail concentration).
- Exhaustive permutations: Every model task cell in Table 1 evaluates all permutations on each of demonstration sets test queries ( forward passes per cell; zero permutation subsampling).
- Quantization & NLL: With queries, single-permutation accuracy moves in steps of , creating ceiling ties when accuracy ; this is why split-half retest uses continuous token NLL (– SE above zero).
- 95% CIs across sets (, added to Table 1): Every cell's lower CI bound sits well above zero (minimum single-set spread across all pairs is on AG News and on RTE):
| Model | AG News Spread (%) [95% CI] | RTE Spread (%) [95% CI] |
|---|---|---|
| Qwen2.5-7B | 11.9 [9.6, 14.2] | 15.0 [12.5, 17.5] |
| Mistral-7B | 8.4 [6.6, 10.3] | 16.9 [14.3, 19.5] |
| Qwen3-8B | 12.2 [8.5, 15.9] | 13.1 [10.8, 15.4] |
| DeepSeek-R1-8B | 39.1 [34.8, 43.3] | 29.4 [25.8, 32.9] |
(Table 1 also updates Pythia-410M SST-2 to exact per-set mean Acc 46.0–63.4% and spread 42.8 [39.3, 46.3].)
- Tail concentration (added to App. F): Across all permutations, AG News spread is moderately catastrophic-tail skewed—the worst of permutations shift accuracy further from the median than the best ( vs. pp)—whereas RTE tails are symmetric ( vs. pp, ratio ).
Q6 (Learned score target, gap, compatibility with Prop. 21, and non-certification).
- Target & CV protocol: In
Table A3(App. I), the regressor predicts direct realized slot sensitivity across identities contexts using nestedGroupKFoldover held-out example identities (distinct fromTable A6's heuristic candidates, which were correlated against gap-matrix at ). - Why drops to – of ceiling: Feature-free split-half identity lookup (
Table A3) still reaches – of at . Thus the predictable signal is present in ; RF/-NN fall short because groups in dimensions hit finite-sample regression limits (and models at have training loss ). - Compatibility with Prop. 21 & non-certification: Prop. 21 proves realized sensitivity is not a function of alone—both because of context interactions () and dependence on trained weights (cross-init Spearman ). Fitting a checkpoint-specific regressor recovers at most the marginal share without violating Prop. 21, and does not inherit 's certificate (§4.6, Table A4).
Q7 (Where Lemma 7 is exercised empirically).
First, thank you for catching a broken section link in §5.5 (fixed from \Cref{app:proof-nonvacuity} to \Cref{app:additional}, App. J). Two experiments in App. J directly test Lemma 7's coherence scaling:
- Onset dimension vs. : Taking the dimension where proxy–slot correlation crosses across gives , a ratio —consistent with () and opposite in direction to pure () or ().
- Causal coherence intervention: Prescribing pairwise coherence at fixed amplifies spread by at – () before pushing it below baseline at (), isolating a non-monotone coherence window.
Q8 (Falsifiable softmax predictions beyond observing high entropy). Four quantitative tests go beyond observing :
- Exact invariance at any entropy: All single-layer softmax models yield spread (Fig. A4a), confirming single-layer symmetry is architectural rather than a high-entropy or linear-attention artifact.
- Depth & learner stratification: Slot-profile agreement with linear rises from mean () to () as Cor. 2's amplification steepens, increases with entropy (), and collapses to on non-learners (loss ).
- Cross-model magnitude: Attention entropy predicts ordering spread at (; partial controlling depth ).
- Data-dependent bound ranking: Theorem 19 ranks spread across all multi-layer softmax models at ().
Author Response to Reviewer UaKg: Regime, Entropy Bound, LLM CIs, & Ceiling
We thank Reviewer UaKg for the thorough, quantitative review. We address every item (W1–W2, Q1–Q8) below and in the revised manuscript.
W1 & Q1 ( vs. trained models & LLMs). Zero unconstrained trained runs satisfy (). Across seeds (Table A5), normalized models have (mean ) and unnormalized have (mean ); –B LLMs sit further outside and add RoPE/MLP/LayerNorm. §4.4 states upfront that Thm. 6 isolates this cubic–quadratic norm barrier rather than certifying unconstrained checkpoints, whereas Tier-1 tests ( , bidirectional collapse, TOST , at –) need no small-norm assumption.
Q2 (Formal status of entropy bound). Lemma 18, Theorem 19, Corollary 20 (App. H) form a proved data-dependent bound (an earlier unproved product surrogate is discarded in App. H as it vanishes as at ). Leaving Thm. 6 unchanged, Thm. 19 replaces spectral norms with , tightening vacuity on softmax models by median ( OoM) and ranking spread at (; config-level), whereas alone gives (, of ). Absolute scale remains (median , best ).
W2 & Q3 (Greedy vs. Random- at ). Two facts reconcile Table 2: (1) Cost crossover: Greedy uses evals at vs. , crossing below only at ( vs. at ; cheaper at ; at ). (2) Oracle- ceiling (Table A4, App. I): Across instances ( models sets, ), even sorting by true oracle captures only of the gap (learned_inv , greedy ; Random-5 , Random-20 ). §5.5 and §6 therefore recommend Random-m-tries at small .
Q4 ( normalization & residuals). Dropping residuals sets (), leaving only in Eq. (4). Dropping gives diagonal , bounded uniformly by (Table A5), steepening () and matching §5.3 where training amplifies sensitivity only when unnormalized ( vs. normalized TOST ).
Q5 (LLM protocol, 95% CIs, tails). All cells evaluate all permutations sets queries ( inferences/cell). Continuous NLL avoids accuracy ties. Added CIs in Table 1 are all : AG News Qwen2.5 11.9 [9.6, 14.2], Mistral 8.4 [6.6, 10.3], Qwen3 12.2 [8.5, 15.9], DeepSeek 39.1 [34.8, 43.3]; RTE 15.0 [12.5, 17.5], 16.9 [14.3, 19.5], 13.1 [10.8, 15.4], 29.4 [25.8, 32.9] (Pythia Acc fixed to 46.0–63.4%, spread 42.8 [39.3, 46.3]). Worst- shift is best- on AG News ( vs. pp) and symmetric on RTE ( vs. pp; App. F).
Q6 (Learned score, , Prop. 21). Table A3 predicts direct slot sensitivity (, nested GroupKFold over held-out identities). At , feature-free split-half identity lookup hits – of , showing RF/-NN's – is finite-sample regression in dims (plus models loss ). Prop. 21 holds because depends on context () and weights (cross-init ); learned scores carry no certificate (§4.6).
Q7 (Lemma 7 tests). Fixed §5.5 ref to App. J. Two App. J tests exercise Lemma 7: (i) -agreement onset gives ( predicts ; predicts ); (ii) prescribing at fixed boosts spread at – () and drops to at .
Q8 (Softmax tests beyond high entropy). (1) spread on models at any entropy; (2) profile match rises from () to () and drops to on non-learners; (3) entropy predicts spread (; partial ); (4) Thm. 19 ranks -model spread at .
A Clearer Follow-Up on Xiang et al. (2024), Our Rewritten Paper, and Your Questions
Dear Reviewer UaKg,
Thank you again for engaging promptly with our reply and stating your concern about Xiang et al. (ACL 2024) directly. Looking back at our posts last week, we realize they were overly compressed and heavy on notation (with math lines scrambled by OpenReview's Markdown parser on Nov 13). Since our Nov 14 note, we rewrote the entire paper using ICLR's 10-page discussion allowance (9.5 pages main text, now live at the top PDF link) so the prose and scope read much more naturally. We hope you can forgive our dense earlier posts, and we wanted to walk through Xiang et al. and your main questions clearly here.
1. Why Xiang et al. (ACL 2024) does not pre-empt our core contribution
We give Xiang et al. full credit in the Abstract, §1, and §2 for showing across pretrained LLMs (Flan-T5/UL2 vs. Llama2/Vicuna) that causal masking drives high flip rates, and for proposing LoRA fine-tuning (InfoAC). Rather than claiming the observation that causal LMs are order-sensitive, our work starts where that observation ends and shows why Xiang et al.'s intuitive explanation is incomplete:
- A causal mask alone gives zero sensitivity at 1 layer: Xiang et al. attribute CausalLM sensitivity to example 1 seeing itself while example
ksees allkexamples. Yet in a 1-layer causal transformer without positional encodings, that exact asymmetric causal mask is active, and order sensitivity is identically zero (below10^-8across linear and softmax models), because the query sums direct contributions from each raw input and addition does not care about order. Sensitivity turns on at 2 or more layers, where layer-2 tokens read layer-1 states shaped by different prefixes, launching multi-hop chains bounded in closed form byW(p, k, L). As you noted in Strength 1, this 1-layer vs. multi-layer boundary is a falsifiable prediction absent from Xiang et al.'s 24–40 layer LLM study. - Deconfounding the mask from positional encodings and pretraining: Comparing Flan-T5 with Llama2 varies the mask, positional encodings (T5 bias vs. RoPE), architecture, and pretraining at once (hence bidirectional Flan-T5 in Xiang et al. still flips on 7%–19% of inputs). In position-free controls, flipping only the causal mask drops spread three million fold to float noise, and normalized causal models already carry their full sensitivity at random initialization before training.
- First order-dependent ICL theory and frozen-model ceiling: Xiang et al. prove no theorems and update weights via LoRA. We study frozen-weight ICL, prove the first generalization bound explicit in prompt order (
beta_sigma, Theorems 4–6) plus a proved softmax bound (Theorem 19), and prove why frozen single-example selection hits a ~21% ceiling without multi-order sampling or weight updates.
2. Worst-case norm limits vs. our proved softmax bound (W1, Q1, Q2, Q7, Q8)
Zero unconstrained runs or 7–8B LLMs satisfy Theorem 6's condition B^3 R^2 < 0.059 (our L = 3 seeds sit in [79, 3.1 x 10^4], Table A5); Theorem 6 isolates why worst-case spectral bounds blow up cubically with norms. To bridge to trained checkpoints, Theorem 19 (Appendix H) is a proved mathematical bound (not a heuristic) swapping spectral norms for observables like attention entropy. While its scale stays above 1, it cuts vacuity by 3.4 orders of magnitude across all 44 trained softmax models and ranks their spreads at 0.78 Spearman correlation (entropy alone gives 0.12). Softmax models also pass four falsifiable checks beyond high entropy (Q8): exact 1-layer invariance at any entropy, stronger profile match at L = 4 (0.79) than L = 2 (0.41) vanishing on non-learners (-0.07), and spread tracking entropy at fixed depth; Appendix J (fixed §5.5 link, thank you!) tests Lemma 7's ln k scaling directly (Q7).
3. Greedy vs. Random-20 at k = 5, oracle scores, & LLM CIs (W2, Q3–Q6)
At k = 5, Greedy takes 126 passes vs. 5! = 120 exhaustive, saving compute once k >= 6 (128x cheaper at k = 8). Across 500 fresh prompts (Table A4), even sorting by an oracle knowing every example's true average sensitivity reaches at most 21.2% of the gap, matching our cross-validated predictor (21.9%, zero leakage) vs. 87.5% for Random-20. Single-example sorting hits that ~21% wall because sensitivity depends on preceding neighbors (Proposition 21; at d_x = 128, 129-dim regression hits sample limits while split-half lookup reaches 66–90% of the ceiling), making 5–20 random shuffles the right small-k choice. Finally, Table 1 tests all 120 permutations exhaustively with 95% CIs cleanly above zero on every LLM (8.4% [6.6, 10.3] to 39.1% [34.8, 43.3]; Q5), and dropping 1/t steepens the curve just as unnormalized training amplifies sensitivity (Q4).
Thank you again for your thorough critique; it sharpened both our positioning and our practical takeaways.
Author Response to Reviewer UaKg (Part 1/2): Regime Constants, Thm. 19, & Greedy Ceiling
We thank Reviewer
UaKgfor the thorough, quantitative review. Because your review raises two main weaknesses and eight technical questions, we respond in two self-contained parts (Part 1/2: W1–W2 & Q1–Q4; Part 2/2: Q5–Q8), with all updates reflected in the revised manuscript.W1 & Q1 (Which experiments satisfy B3R2<0.059? How far outside are synthetic & LLM runs?). Zero unconstrained trained configurations satisfy the worst-case spectral condition B3R2<0.059 (k=5,α=0.05,CℓG=1,rmax=0.6,L=2). Across the dx=32,L=3 trained seeds (Table A5), exact per-seed values are:
Pretrained 7–8B LLMs sit further outside this spectral ball and include RoPE, MLP, and LayerNorm. Revised §4.4 states upfront that Theorem 6 isolates the exact cubic–quadratic spectral barrier rather than certifying unconstrained checkpoints directly, whereas Tier-1 structural tests (L=1 <10−8, bidirectional 2.9×106× collapse, normalized TOST p=0.033, αp↔W(p) at rs=0.82–0.98) require no small-norm assumption.
Q2 (Formal status of the entropy tightening, channel ablation, and Thm. 6).
W2 & Q3 (Reconciling Greedy 21%/126 evals vs. Random-20 87%/20 evals). Two facts reconcile Table 2 and motivate our revised framing in §4.6, §5.5, and §6:
learned_inv=21.9%,greedy=9.0% under npop=128;Random-5=62.7%;Random-20=87.5%). Because 1−Rmax2 and cross-slot interactions dominate,Random-m-triesis the right small-k method.Q4 (Sensitivity of W to 1/t normalization and residuals).