When Do Task Vectors Interfere? Mapping the Validity Boundaries of Weight-Space Composition

This paper investigates when task arithmetic—the practice of treating fine-tuning displacements as composable directions in weight space—actually reflects predictable changes in model function. The authors argue that a displacement is defined in parameter space, whereas success is judged by behavior; the two geometries need not agree. They separate parameter geometry from functional geometry and measure pairwise functional non-additivity over a two-dimensional task-vector surface.

The method evaluates a 7×7 grid of compositions θ(α, β) = θ0 + αΔa + βΔ b for α, β ∈ [0, 1.2], where θ0 is a shared base model and Δa, Δ b are LoRA displacements for two tasks. At each point, the observed joint distribution is compared against an additive counterfactual assembled in logit space: l add(x; α, β) = l α,0(x) + l 0,β(x) − l 0,0(x). This construction removes the marginal nonlinearity of each direction before measuring their joint effect.

The interaction for a prompt is I x(α, β) = JSD(p α,β(·x), p add(·x)), normalized by the actual displacement from the base M x(α, β) = JSD(p α,β(·x), p 0,0(·x)). The reported family estimate is a ratio of expectations, averaged over prompts, the 36 interior grid points, and three training seeds 42, 123, 456. A radial intervention rescales every rank-16 task vector to the median norm of all vectors in the corresponding audit block to rule out update magnitude as a confound.

1. Functional interference depends on the input distribution. On Qwen2.5-1.5B, after norm matching, code+safety exceeds code+math by 5.96 points on code prompts and 7.58 on instruction prompts, but only 0.10 on math prompts. The paper states: This stratum dependence shows that neither pair identity nor input distribution alone determines compositionality. The contrast is not produced by a smaller denominator: on code prompts the numerator rises from 0.00352 to 0.01663, a factor of about 4.7, while the denominator rises from 0.14048 to 0.19728, a factor of about 1.4.

2. Prospective directional test on unseen pairs succeeds. The expansion to six tasks (adding XSum summarization and OPUS Books translation) evaluated 12 prospectively specified task pair families across three seeds, yielding 36 surfaces. After unblinding, all 8/8 prospectively specified comparisons between high and low bins have the predicted sign when averaged across six strata; including the prospectively specified code+math low anchor yields 12/12. However, fine ranking is less reliable: high exceeds middle in only 5/8 comparisons. The exact design-preserving randomization test gives p = 0.083, so the authors treat the outcome as prospective directional evidence rather than a definitive inferential test.

3. Functional structure persists without detectable parameter clustering. At 0.5B, the cosine gap between task directions is 0.0045 (p = 0.1146), silhouette is −0.0008 (p = 0.0886), and 1-NN task accuracy is 0.25 (p = 0.3755). Yet the functional contrast persists. The paper concludes: The supported conclusion is persistence without detectable clustering under this audit, not absence of parameter structure.

4. Stress tests preserve the controlled functional hierarchy. The contrast survives full-parameter fine-tuning at 0.5B (+4.37 on code, +2.98 on instruction), Qwen2.5-7B LoRA (+9.52 on code, +10.56 on instruction), and Llama-3.1-8B LoRA (+4.87 on code, +5.30 on instruction). All satisfy the frozen strong rule requiring 3/3 positive seed differences and bootstrap intervals excluding zero.

5. Prompt format marks the public boundary. Raw public code, instruction, and safety prompts preserve the continuous contrast (+6.91, +11.09, and +3.96 points after norm matching, respectively), while public math behaves as the intended low anchor (+0.36 points). Critically, when the identical 60 public code prompts are wrapped in the Alpaca instruction template, the contrast after norm matching collapses from +6.91 to +0.34 points and satisfies the strong practical equivalence gate. The paper concludes: The boundary therefore depends on prompt format rather than on public provenance alone.

6. Execution behavior does not robustly reproduce the contrast. Using EvalPlus, the HumanEval+ difference in absolute factorial pass@1 interaction is +4.14 points with interval [−2.44, 12.60] and bootstrap probability 0.841 of being positive; the MBPP+ estimate is −0.15 points with interval [−2.65, 2.38]. EvalPlus does not establish transfer to benchmark merge performance; its wide intervals remain compatible with moderate effects.

The paper claims three contributions:

• We define a functional interaction surface conditioned on the input that separates non-additivity between directions from effects along each axis.

• Prospective tests on unseen pairs and targeted stress tests show transfer beyond the original pairs and parameterization, across audited scales, and to one additional model family.

• "We establish boundaries relevant to deployment: the functional contrast persists even though the audited clustering diagnostics are not significant, public transfer depends on format, and continuous non-additivity cannot replace evaluation on intended prompts and behavioral metrics."

The authors acknowledge several limitations: "Full FT is audited only at 0.5B, and Llama-3.1-8B covers three tasks under one response-only protocol. Three seeds check directional consistency but provide limited distribution-free power. Controlled prompts are diagnostic instruments, and first-token JSD does not reliably predict decoded behavior. Norm-matched endpoints are interventions, and shared checkpoints make correlations across families dependent. Without same-task and random-direction anchors, ratio values should be read comparatively rather than on an absolute scale. We do not report task accuracy for the individual adapters, so each task label describes training data rather than verified capability."

The paper concludes: "Task-vector interference is measurable and conditionally generalizable, but not global. Coarse structure survives unseen-pair tests, full fine-tuning, Qwen scaling, and a Llama audit, yet varies with input and format and does not reliably predict pass@1 interaction. Task-vector composition is best viewed as an input-conditioned functional geometry with explicit validity boundaries, not a universal semantic coordinate system in weight space."

Based on this paper, I can make the following specific improvements to AI systems:

Improvement: Build a system that predicts task-vector composition success as a function of the input distribution, not just the task pair. The system would learn a mapping from input features (prompt format, domain, difficulty) to expected functional interference, using the paper's finding that code+safety vs code+math differs by 5.96 points on code prompts but only 0.10 on math prompts.

Capability: Before merging adapters, the system can estimate whether the merged model will behave additively on a given deployment input distribution, enabling selective merging only where composition is safe.

Improvement: Implement a pre-deployment check that tests merged models under multiple prompt templates (raw vs. instruction-wrapped) because the paper shows the contrast collapses from +6.91 to +0.34 points when the identical prompts are reformatted. The system would automatically detect format sensitivity and flag merges that are only valid under specific formatting.

Improvement: Create a diagnostic tool that computes the paper's interaction surface I x(α, β) = JSD(p α,β, p add) on a 7×7 grid for any two adapters, before merging. The tool would report: (a) the ratio of expectations over prompts, (b) the stratum-dependent variation, and (c) whether the interaction exceeds a practical equivalence threshold.

Improvement: Integrate the paper's prospective testing methodology into an automated merge pipeline. Before merging, the system would: (1) specify high/low interaction hypotheses for unseen task pairs, (2) run the exact design-preserving randomization test, and (3) only proceed with merges where the predicted sign is confirmed in ≥8/8 comparisons.

Improvement: Add a post-merge verification layer that tests actual decoded outputs (e.g., pass@1 on HumanEval+ or MBPP+) rather than relying on first-token JSD. The system would flag cases where functional non-additivity in logit space does not translate to behavioral differences (the paper found +4.14 with interval [−2.44, 12.60] on HumanEval+, i.e., not robust).

Improvement: Implement the paper's radial intervention as a standard preprocessing step: rescale every task vector to the median norm of its audit block before composition. This removes update magnitude as a confound, ensuring that observed interference is due to direction, not scale.

Improvement: Build a recommender that, given a target deployment scenario, identifies which task pairs to merge based on the paper's finding that neither pair identity nor input distribution alone determines compositionality. The system would use a two-factor model: task-pair identity × input stratum, and recommend merges only where both factors predict low interaction.

Improvement: Implement a guard that checks whether public prompts (e.g., from benchmarks) are used in their original format or wrapped in templates. The paper shows public provenance alone is insufficient—format matters. The system would automatically test both raw and templated versions before accepting benchmark results as evidence of merge quality.