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Paper summary
This paper proposes BLADE, a gradient-free method for locating and reweighting sparse residual-writer weights that modulate specific behavioral preferences in LLMs. Using contrastive behavior data, BLADE estimates a behavior direction, scores individual weights by their local contribution to that direction, penalizes weights that are important for general language modeling on C4, and then rescales the selected weights by a factor . The method can suppress, remove, or amplify behaviors such as refusal, hallucination, sycophancy, power-seeking, and wealth-seeking. Experiments across several models show that BLADE can substantially modify these behaviors while often causing only small changes in WikiText perplexity. The paper also evaluates out-of-distribution refusal and hallucination benchmarks and demonstrates joint control of refusal and uncertainty.
Critical strengths
- The paper proposes a simple and computationally efficient post-hoc editing framework. BLADE does not require gradient-based fine-tuning or retraining the model. It uses forward-pass activation statistics to identify a sparse set of weights and applies a transparent multiplicative intervention. This makes the method relatively easy to implement and allows both suppression and amplification of the same behavior.
- The experiments cover multiple behaviors, model families, and intervention directions. The paper evaluates refusal, uncertainty, sycophancy, deception, power-seeking, and other behavioral preferences across several LLMs. It also compares BLADE with weight-editing and activation-steering baselines, and reports behavior metrics together with perplexity and normal-answer coverage. The OOD experiments on HarmBench, XSTest, SelfAware, and FalseQA provide some evidence that the edits can transfer beyond the calibration data.
Critical weaknesses
- The behavioral parameters are not shown to be disentangled, and the interventions can interfere with one another. BLADE identifies separate weight sets for different behaviors, but these sets may overlap or affect shared computations. The joint refusal-uncertainty experiment already shows trade-offs: stronger interventions increase refusal but also increase over-refusal and reduce answer coverage. On Llama-3.2-3B, hallucination mitigation also substantially reduces answering on answerable questions. The paper does not provide a systematic overlap analysis, orthogonality test, or causal intervention matrix showing whether editing one behavior leaves the others unchanged.
- The evidence for robust OOD control is limited and strongly dependent on benchmark-specific calibration and evaluation choices. Although the paper evaluates HarmBench, XSTest, SelfAware, and FalseQA, the interventions are selected using related validation data and a C4 perplexity constraint, while the behavioral metrics rely partly on keyword matching and LLM judges. It remains unclear whether the same sparse weights control the underlying behavior across substantially different prompts, domains, languages, and evaluators, or whether the method mainly transfers surface patterns captured by the calibration sets.
Questions for authors
- How transferable are the behavior-specific weight masks and reweighting factors selected by BLADE? In the current experiments, the layer set, sparsity ratio, and reweighting factor appear to be selected separately for each model and target behavior using calibration data. Can the authors evaluate whether a mask and intervention strength identified on one behavior dataset or model transfer to a substantially different prompt distribution or model without re-selection?
6 comments
Rebuttal to reviewer WJ2r - W1 (2/2)
(3) BLADE Modifies Fewer Weights While Removing Refusal More Cleanly with Smaller Side Effects: Cross-Method Comparison
To directly evaluate how cleanly our method isolates refusal compared to prior weight-editing approaches, we evaluated all frozen configurations from Table 2 on Llama-3.2-3B (values in %; A/B directions fixed on Base; activation-steering baselines are omitted as generation hooks prevent comparable A/B log-probabilities and barely reduce refusal).
| Config | Refusal | Power | Wealth | Decep. | Corrig. | SelfAw. | SelfRate | Syco. | ΔPPL |
|---|---|---|---|---|---|---|---|---|---|
| Base | 98.0 | 76.0 | 60.7 | 68.7 | 63.5 | 61.3 | 76.7 | 91.3 | — |
| BLADE (ours), L=12, f=0.5% | 0.0 | 57.3 | 50.7 | 51.3 | 78.8 | 57.3 | 76.7 | 92.0 | +0.33% |
| Wei et al., q=p=0.5% | 25.0 | 65.3 | 54.7 | 48.0 | 75.3 | 66.7 | 69.3 | 92.0 | +1.25% |
| Arditi et al., s=1 | 2.0 | 50.7 | 46.7 | 38.0 | 82.4 | 56.0 | 74.0 | 92.0 | +0.94% |
From this comparison, we highlight three findings:
- Cleaner isolation at full removal: At the comparable refusal-removal operating point—where our method reduces refusal from 98.0 to 0.0 versus 98.0 to 2.0 for Arditi et al. (s=1)—Arditi et al. incurs 1.5× larger collateral shifts than our edit (mean |Δ| = 13.9 vs. 9.4 points; max 30.7 vs. 18.7; larger on 5 of 7 behaviors and smaller on none) and nearly 3× higher ΔPPL (+0.94% vs. +0.33%). Meanwhile, Wei et al. already incurs 8.9 points mean shift and +1.25% ΔPPL while removing only 73 points of refusal.
- Lowest collateral cost per unit edit: When we normalize mean collateral shift by each percentage point of refusal removed, our method achieves the lowest cost at 0.096, compared to 0.122 for Wei et al. and 0.145 for Arditi et al. (s=1). By editing just 0.042% of network weights (173,015 parameters), we isolate refusal far more cleanly than applying a global rank-one projection across the embedding matrix and all 56 writer matrices (Arditi et al., s=1, our primary baseline per Table 2 and Reviewer Fr7s's request).
- Identical shift directions across methods: Across all three approaches, we observe every behavior moving in the exact same direction—lowering power-seeking, wealth-seeking, and deception, raising corrigibility, and leaving sycophancy flat—confirming that the trade-off stems from intrinsic behavioral relationships rather than our specific locator.
(4) Single-Behavior Boundaries and Revisions
Similarly, the trade-off in Llama-3.2-3B hallucination mitigation (lower answerable coverage when suppressing hallucinations) reflects a capacity-dependent abstention boundary rather than entangled weights: smaller models become more conservative near borderline prompts, whereas Qwen3-4B preserves 71% answerable coverage at +0.8% ΔPPL (Question 1, Section 4). Cross-model pipeline transfer and frozen OOD generalization are detailed in Question 1 (Section 2) and Weakness 2. We will add both the 8 × 8 causal matrix and cross-method table to our updated manuscript.
Rebuttal to reviewer WJ2r - W2 (1/2)
W2:
Thank you for raising this important question. In Weakness 2, you ask whether a fixed set of sparse weights truly controls the underlying refusal behavior once we shift the prompt distribution, harm domain, language, or evaluator, rather than simply overfitting to surface patterns in the calibration data.
To test this directly, we evaluated our method across all four axes using the exact frozen configuration from Table 2 of our paper. Specifically, we selected the weight mask, refusal direction, target layer, sparsity ratio, and steering coefficient solely on our in-distribution AdvBench/Alpaca calibration set under the C4 perplexity budget (beta = 5%). We did not re-select, re-tune, or re-threshold anything for the evaluations below—HarmBench, XSTest, MultiJail, and WikiText were used strictly as held-out test beds.
(a) Evaluator
To make sure our conclusions do not depend on a single judge or brittle keyword heuristics, we re-evaluated every response from Table 2 using a second, independent, and recently published LLM judge (Gemini-4-Hydrogen). Both judges scored byte-identical 400-character response windows under the exact same rubric, with outputs shuffled across methods so neither judge knew which configuration generated a given response.
| Method | Config | HarmBench LLM1 | HarmBench LLM2 | XSTest LLM1 | XSTest LLM2 |
|---|---|---|---|---|---|
| Base | — | 89.0 | 88.0 | 9.6 | 7.6 |
| BLADE (ours) | L=12, f=0.5% | 3.0 | 2.0 | 0.8 | 0.4 |
| Wei et al. | q=p=0.5% | 19.5 | 20.5 | 0.8 | 0.4 |
| Arditi et al. (s=0.5) | s=0.5 | 31.0 | 36.5 | 5.2 | 3.6 |
| Arditi et al. (s=1) | s=1 | 17.0 | 18.0 | 2.0 | 1.6 |
| CAA | L=12, c=-0.2 | 86.5 | 87.0 | 4.8 | 3.6 |
| ActAdd | L=16, c=-16 | 85.5 | 87.0 | 5.6 | 6.4 |
Beyond matching on aggregate rates, the two judges agree closely on an item-by-item basis: they assign the exact same label on 97.6% of the 1,600 paired HarmBench judgments (Cohen's kappa = 0.95) and on 99.0% of the 2,000 paired XSTest judgments (Cohen's kappa = 0.87). Broken down by configuration on HarmBench, agreement stays between 93.5% and 99.5%. Notably, the lowest agreement (93.5%) occurs on Arditi et al. (s=0.5), which leaves the largest number of borderline, equivocal refusals, whereas BLADE and the unmodified base model both sit at 98.0%–99.6%. In other words, any slight disagreement comes from ambiguous model outputs rather than judge inconsistency. Furthermore, Table 2 already includes a third, non-LLM baseline evaluator—a string matcher calibrated against XSTest reference labels with a 0.4% false-positive rate—and the ranking across methods remains identical under all three evaluators.
(b) Cross-Lingual Transfer (Language Shift)
Next, we tested whether our English-calibrated edit transfers to another language without touching the weights. We evaluated the same frozen configurations on MultiJail [1], which pairs parallel human-translated harmful requests in English and Italian. Because Italian is officially supported by Llama-3.2, any remaining refusals cannot be blamed on the model failing to understand the prompt. Since both arms evaluate the exact same 150 requests across 7 configurations (2,100 paired labels in total), we compare them item by item using paired exact McNemar tests:
| Method | English (en) | Italian (it) | Delta (it - en) | Paired Exact McNemar |
|---|---|---|---|---|
| Base | 88.7 | 92.7 | +4.0 | p = 0.180 |
| BLADE (ours) | 48.0 | 39.3 | -8.7 | p = 0.035 |
| Wei et al. | 64.7 | 73.3 | +8.7 | p = 0.019 |
| Arditi et al. (s=0.5) | 65.3 | 83.3 | +18.0 | p < 0.001 |
| Arditi et al. (s=1) | 57.3 | 59.3 | +2.0 | p = 0.736 |
| CAA | 88.0 | 94.0 | +6.0 | p = 0.035 |
| ActAdd | 88.0 | 91.3 | +3.3 | p = 0.332 |
BLADE achieves substantially lower refusal rates than every baseline in both languages (paired exact McNemar tests against the strongest baseline, Arditi et al. s=1: p = 0.009 in English and p < 1e-5 in Italian). Even more tellingly, our advantage over Arditi et al. (s=1) more than doubles from 9.3 percentage points in English to 20.0 percentage points in Italian. If BLADE were merely memorizing surface lexical patterns from an English calibration set, its effect could not become even stronger in a language that never appeared during calibration. This experiment also underscores why we never rely on keyword matching for our conclusions: an English string matcher drops to 0.0% on Italian responses across all seven configurations, whereas the LLM judge captures true refusal rates ranging from 39.3% to 94.0%.
Rebuttal to reviewer WJ2r - W1 (1/2)
We thank the reviewer's feedback. It took some time for us to conduct experiments to respond with evidence. We address the concerns as follows:
Weakness
W1:
Thank you for this question. To examine behavioral trade-offs systematically, we constructed the full 8 × 8 causal intervention matrix on Llama-3.2-3B alongside a cross-method comparison of refusal-removal baselines. Together, they show that cross-behavior side effects stem from semantic and causal couplings among behaviors rather than overlapping weights—and among weight-editing methods, BLADE incurs the lowest collateral shift per unit of edit.
(1) Complete 8 × 8 Causal Intervention Matrix
We built an 8 × 8 causal intervention matrix on Llama-3.2-3B where rows denote the edited behavior and columns measure all eight behaviors (values in %; bold diagonal entries show target effects). To ensure strict comparability, all eight masks use the same sparsity ρ = 5×10⁻⁴ (207,618 weights) from a shared layer pool, evaluated alongside the unedited Base model and a same-size Random mask control:
From this matrix, we observe that removing a behavior does introduce some side effects on other behaviors (median off-diagonal shift 3.3 points, mean |Δ| = 5.5 points; while the same-size random mask shifts behaviors by at most 1.3 points, +0.05% ΔPPL, and ΔPPL across all edited rows stays within +0.09% to +0.82%). However, as we show in Section (3) below, compared with existing refusal-removal weight editing approaches, our method removes the target behavior more cleanly while incurring substantially smaller collateral impact on other behaviors.
(2) Weights Are Separated, Yet Behaviors Remain Coupled
Aligning the pairwise Jaccard overlap matrix (reported in Section (3) of our Question 1 response) cell-by-cell with the causal matrix above shows that cross-behavior shift magnitude |Δ| is uncorrelated with mask overlap (Pearson r = +0.35, Spearman ρ = 0.31). In fact, the largest off-diagonal shifts occur in the refusal row (deception -22.7, power-seeking -19.3, corrigibility +18.9 points)—the exact mask with the lowest overlap (1.1%–2.1%) with all other behaviors. This mirrors Figure 2, where two masks with strictly zero overlap by construction still interfere under joint amplification. Thus, parameter-space separability ≠ behavioral independence: upstream circuits interact via downstream representations and semantic dependencies (e.g., suppressing refusal naturally increases corrigibility and lowers power-seeking), so behavioral trade-offs do not imply localization failure.