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Under review as a conference paper at ICLR 2027

Ranking Is Not Control: Reference-Grounded Steering for Distinct Behaviors

Abstract

Representation steering provides lightweight control over frozen language models, and many optimization-based methods learn steering vectors from pairwise preferences. We argue that this formulation confuses ranking with control: objectives on ranking determine relative preference, but not the direction or selectivity of behavioral change. Unconstrained neutral or irrelevant outcomes mean that pairwise advancement does not guarantee intended uplift: the same positive margin can reflect intended uplift, joint suppression, or broad co-amplification. Thus, we formulate representation steering as reference-grounded constrained behavioral control and instantiate it as Reference-Grounded Steering (RGS), a soft-penalty objective that promotes intended uplift, penalizes grounding and separation violations, limits competing-behavior leakage, and regularizes intervention energy. Together, these terms constrain the behavioral movements that pairwise preferences leave unspecified. Controlled experiments validate the predicted failure mode: pairwise-only objectives attain large positive relative margins while decreasing support for the intended behavior, and additional endpoint flexibility amplifies this failure when the corresponding behavioral constraints are absent. Once reference-grounded constraints are introduced, the same flexibility becomes beneficial. Across nine models from three families, RGS achieves the strongest bidirectional control, ordered bracketing of the unsteered policy, and control against the prompt-designated orientation across held-out behavior-pair combinations that were never jointly trained or calibrated. Along interpolated endpoint chords, RGS also provides a wider control range with fewer and smaller local reversals than the baselines. These results suggest that effective representation steering requires specifying not only which behavior should rank higher, but the structured pattern of behavioral change relative to the unsteered model.

Primary area:
foundation or frontier models, including LLMs
Keywords:
representation steering, activation steering, language model control, selective behavioral control, preference optimization

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.60 over 5 reviews, above 70% of the others.
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Paper summary

This paper argues that pairwise preference objectives for representation steering optimize relative rankings without necessarily ensuring intended behavioral uplift or selective control. The authors propose Reference-Grounded Steering (RGS), which learns independent steering vectors for competing behaviors using an objective that explicitly encourages intended-response uplift, enforces separation from alternative and model-native responses, limits alternative-behavior leakage, and regularizes intervention magnitude. Experiments across nine LLMs and ten Schwartz values compare RGS with BiPO and RePS, evaluating bidirectional control on 40 held-out value-pair combinations. RGS consistently improves bidirectional preference contrast, order preservation, and target-value induction, while extensive ablations investigate the contributions of reference grounding, objective components, and endpoint parameterization. The authors also examine interpolation between steering endpoints and associated quality trade-offs.

Critical strengths
  1. A well-motivated distinction between ranking and control: The paper identifies a meaningful limitation of pairwise preference objectives: improving relative preference does not guarantee positive movement toward the intended behavior. The reference-grounded formulation addresses this issue explicitly, and the matched experiments demonstrate that pairwise-only objectives can produce large positive margins through joint suppression of response scores.
  2. Convincing empirical evidence and careful ablations: RGS consistently outperforms BiPO and RePS on the main control metrics across nine models, with a clear separation between configuration selection and evaluation on held-out value-pair combinations. The component ablations provide useful evidence about the roles of zero anchoring, intended uplift, leakage control, and endpoint flexibility. Reporting response-quality trade-offs and interpolation behavior further strengthens the empirical investigation.
Critical weaknesses
  1. Incomplete validation of absolute behavioral control: Although RGS explicitly optimizes reference-relative intended uplift and alternative-behavior leakage, the primary free-generation metrics, particularly BPC, still emphasize relative behavioral preference. The teacher-forced displacement analyses provide useful mechanistic evidence, but do not directly establish that the same absolute improvements hold in freely generated responses. A more direct comparison of intended and alternative value-support changes relative to unsteered generation would better substantiate the paper's central claim.
  2. Limited generality and partly confounded method comparisons: RGS learns two independent steering endpoints, whereas BiPO uses a signed axis, and the methods also differ in intervention scope. Although the authors provide relevant parameterization ablations, these differences complicate attributing the full performance advantage to the reference-grounded objective alone. Furthermore, the experiments focus on explicitly competing human values, where limiting alternative-behavior uplift is often desirable. It remains unclear how well the formulation extends to non-exclusive behaviors for which simultaneous improvement may be preferable. The held-out evaluation also recombines previously trained values rather than testing unseen concepts.
Questions for authors
  1. Absolute behavioral improvement: Could the authors report the changes in intended and alternative value-support scores under free generation, each measured relative to the corresponding unsteered response? This would help connect the main behavioral results to the reference-grounded control conditions used during training.
  2. Contribution of endpoint flexibility: While the existing ablations are informative, could the authors further clarify how much of RGS's improvement over BiPO can be attributed specifically to the objective rather than independent endpoint parameterization and intervention-scope differences?
  3. Applicability beyond competing values: How should RGS be applied when the intended and alternative behaviors are not mutually exclusive, or when increasing both behaviors is desirable? Does the proposed leakage constraint remain appropriate in such settings?
2 comments

We thank the reviewer for recognizing the importance of the ranking–control distinction and the strength of our empirical evaluation. We added direct free-generation measurements and controlled experiments that separate the roles of the objective, endpoint parameterization, and intervention scope. We also clarify how the formulation should change when behaviors are compatible rather than competing.

Question 1 / Weakness 1: Absolute behavioral improvement under free generation

We directly compared each steered response r(d)r^{(d)} with the unsteered response r(0)r^{(0)} to the same prompt. For target value dd and competitor dˉ\bar d, we define

C=s_{\bar d}(r^{(d)})-s_{\bar d}(r^{(0)}).$$ Target uplift requires $U>0$; joint success requires $U>0$ and $C\le0$. | Method | Target change $U$ | Competitor change $C$ | Target-uplift rate | Joint-success rate | |---|---:|---:|---:|---:| | RGS | **+1.393** [1.371, 1.415] | **−1.479** [−1.499, −1.458] | **63.95%** [63.30, 64.60] | **61.97%** [61.34, 62.59] | | BiPO | +0.978 [0.955, 1.003] | −0.927 [−0.948, −0.905] | 52.09% [51.43, 52.76] | 49.12% [48.52, 49.75] | | RePS | +0.850 [0.829, 0.872] | −0.956 [−0.976, −0.935] | 50.45% [49.79, 51.11] | 48.65% [48.01, 49.28] | These results cover nine models and 40 held-out value pairs. For every model, RGS has positive mean target change and negative mean competitor change; its target change is higher and its competitor change lower than both baselines. Thus, RGS’s BPC advantage is not merely relative separation between steered endpoints: relative to unsteered generation, it more frequently increases intended-value support without increasing competitor support. Confidence intervals use paired source-cluster bootstrap. ## Question 2 / Weakness 2: Contributions of the objective, endpoint flexibility, and intervention scope We agree that the full RGS–BiPO gap cannot be attributed to the objective alone. We therefore added a controlled factorial experiment on Qwen3-4B crossing three factors while fixing the training data, response pools, layer, training and inference strengths, optimizer, seed, and training horizon: - **Objective:** pairwise separation versus the complete reference-grounded objective; - **Endpoints:** a signed axis $(\pm v)$ versus two independently learned endpoints; - **Scope:** assistant-answer tokens versus all non-padding tokens. The resulting objective effects are: | Controlled contrast | Answer-span scope | All-token scope | |---|---:|---:| | Full objective − pairwise, Separate endpoints | **+.2233** [+.2086, +.2378] | **+.3528** [+.3378, +.3680] | | Full objective − pairwise, Signed axis | −.0573 [−.0723, −.0420] | −.0717 [−.0872, −.0558] | Under the full objective, changing from a signed axis to independent endpoints improves BPC by $+.1311$ for answer-span intervention and $+.1877$ for all-token intervention. The objective-by-endpoint effect is therefore strongly non-additive: the reference-grounded objective improves generated control substantially with independent endpoints, but not under the signed-axis constraint. This interaction has a natural interpretation. The two steering directions generally face different unsteered score geometry and therefore different uplift, separation, and leakage pressures. A signed axis forces their interventions to be exact opposites, whereas independent endpoints allow each direction to satisfy its own reference-relative control requirements. Endpoint flexibility is thus a substantive part of the complete design, rather than an incidental implementation choice. A submitted matched ablation separately identifies the zero anchor while holding independent endpoints and intervention scope fixed. With enhancement and leakage disabled, adding zero to the competitor construction changes mean intended displacement from $-12.651$ to $+1.307$ and increases held-out BPC from .354 to .587: $$\Delta\mathrm{BPC}=+.233\ [+.218,+.248].$$ This isolates a substantial contribution from reference grounding itself. We also controlled intervention scope for the complete methods. For BiPO, the answer-span variant retains its frozen selected layer, strength, and other native settings rather than being retuned. | Matched intervention scope | RGS BPC | BiPO BPC | RGS − BiPO [95% CI] | Quality difference | |---|---:|---:|---:|---:| | Answer-span | .5589 | .2195 | **+.3394** [+.3240, +.3546] | −.0862 [−.1134, −.0590] | | All-token | .5705 | .4033 | **+.1672** [+.1505, +.1838] | −.1456 [−.1710, −.1189] | Changing RGS from answer-span to all-token intervention has a small BPC effect, $+.0116$ [−.0004, +.0236]. Restricting BiPO from all tokens to the answer span has a larger negative effect, $-.1839$ [−.1991, −.1684]. Nevertheless, RGS retains a significant control advantage over BiPO under either shared scope, so intervention scope alone does not explain the full-method gap.

Overall, the results do not support assigning the complete RGS–BiPO difference to a single factor. They show that endpoint flexibility contributes materially, the zero anchor has a substantial matched effect, the full objective benefits from independent endpoints, and RGS remains stronger after matching intervention scope. These are conditional effects and should not be added into a unique decomposition.

Question 3 / Weakness 2: Applicability beyond competing values

The leakage constraint is task-dependent rather than universally appropriate. It encodes the requirement that a designated alternative behavior should not be co-amplified. The appropriate specification depends on the relationship among behaviors:

  • Competing behavior: retain separation and an upper bound such as ΔA≤ϵ\Delta_A\le\epsilon.
  • Compatible but protected behavior: remove it from the competitor set if its change need not be penalized.
  • Co-target behavior: place both behaviors in the target set and require absolute uplift for each.

For example, if behaviors t1t_1 and t2t_2 should both increase, an appropriate specification is

\Delta_{t_2}(u)\ge\rho_2,\qquad \Delta_c(u)\le\epsilon_c\quad(c\in\mathcal C),$$ where $\mathcal C$ contains only behaviors that should not increase. The two desired behaviors should be removed from each other’s competitor construction. Simply disabling the leakage penalty would be insufficient because the separation term would still favor one behavior over the other. If the model-native response already expresses the desired joint behavior, its role in the competitor construction should likewise be revised. Thus, the reference-grounding principle extends naturally—desired changes remain defined relative to the same unsteered model—but the target and competitor sets must reflect the intended concept relationship. The present experiments validate the competing-behavior instantiation on Schwartz-value conflicts; they do not empirically validate this multi-target extension. Finally, the held-out evaluation establishes compositional transfer across unseen pairings of known values. All ten values appear during training, while 40 new pairings are evaluated without retraining or pair-specific calibration. We will revise the paper to describe this result consistently as transfer across held-out combinations of known values, not generalization to entirely unseen concepts.
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Paper summary

Representation steering uses pairwise differences to change the model behaviour. The authors of this paper argue that undesirable change may occur because there is less control than the method they proposed. They introduce Reference Grounded Steering (RGS). It is a a soft-penalty objective that promotes intended uplift, penalizes grounding and separation violations, limits competing-behavior leakage, and regularizes intervention energy. Together, these terms constrain the behavioral movements that pairwise preferences leave unspecified

Critical strengths

This paper's main strength is in my opinion the empirical evaluation of their method, with an ablation study. they also identified a "flaw" of the original representation steering method.

Critical weaknesses

Regarding the weaknesses I think the main weakness regarding the experiments is that they only used one LLM as a judge for their experiments and would gain comparing their results with other judges.

Another weakness is in the theoritical part of the paper: I think for example that mA=ΔI−ΔAm_A=\Delta_I - \Delta_A being invariant to adding a constant shift is quite straightforward...

Moreover, the "smooth conservative surrogate" objective in section 3.3 introduces a textbook bound with M<Mτ<M+τlog3M<M_\tau<M+\tau log3 but doesn't provide a theoritical analysis of the loss landscape. An analysis of the geometry of the hidden states hl,th_{l,t} and an explanation onto why a linear activation addition at a single layer can simultaneously satisfy these score inequalities across diverse inputs, would be appreciated also.

The paper frames RGS as "constrained behavioral control" (Equation 6), the actual method (Equations 9, 10) does not solve a constrained optimization problem (e.g., via primal-dual methods, KKT conditions, or augmented Lagrangians). In section 3.3 it is mentioned that the weights are "fixed penalty weights, not Lagrange multipliers; minimizing this objective does not guarantee per-record constraint satisfaction".

Maybe I misunderstood, the authors can feel free to correct me, but I feel like there is a stack of regularizers.

Questions for authors

First of all I thank the authors for the work they did and I want to specify that I enjoyed reading the paper as I am personnally interested in this field.

Q1) I think the paper would gain to have more experiments with other LLMs judges, so it is not really a question but a suggestion. I think it is important to mention that the author did great work otherwise on the experimental side and it felt very exhaustive to my knowledge.

Q2) Why Soft Penalties Instead of True Constrained Optimization? If the core thesis is that representation steering must satisfy the feasibility conditions (G),(SA),(SN),(G), (S_A), (S_N), and (L)(L) in Equations 4, 6, why not formulate this as a proper primal-dual / Lagrangian optimization problem where dual variables adaptively enforce the constraints? Wouldn't dual ascent automatically resolve the scale mismatch that caused RGS to achieve 0%–8% constraint satisfaction on Llama and Ministral (Table 23)?

4 comments

Response to Question 2 and related theoretical concerns

Thank you for raising this distinction. Compared with previous existing methods that we mentioned, RGS's central contribution is (1) its reference-recoginized uplift/leakage control, and (2) independently learned endpoints. Finite penalties provide a practical implementation that retains these design improvements while allowing trade-offs among the requirements and computational feasibility.

1. The design improvements remain effective under soft optimization

A pairwise margin alone cannot distinguish intended uplift from joint suppression or co-amplification. RGS addresses this ambiguity through intended-score grounding against the frozen model, competition with both alternative and model-native responses, and a separate penalty on alternative uplift. These form the 4 constraints (G,L,SA,SNG, L, S_A, S_N) and each aim at some paritcular violation situations. Independently learned endpoints additionally remove the requirement that opposite steering directions use opposite vectors. A soft implementation retains these distinctions even when it accepts some violations and eases sensitivity to the hyperparameters such as ρ\rho, ϵ\epsilon in the problem stated in Equation (6).

The matched ablations in Table 1 test these improvements within the soft implementation. The following rows use the same Qwen3-4B configuration. E denotes explicit intended enhancement and L denotes leakage control; the margin and energy terms remain enabled throughout. Score displacements are Validation means; BPC and quality QQ are measured on held-out transfer pairs.

EndpointsCompetitors and additional termsΔI\Delta_IΔA\Delta_ABPCQQ
SeparateA−12.651−22.070.3542.367
Separate0/A+1.307−1.935.5874.351
Separate0/A/N+.880−2.044.6234.043
Separate0/A/N + E+2.279+1.706.4544.447
Separate0/A/N + E + L+1.771−.809.6244.333
Signed axis0/A/N + E + L+1.692−.193.4453.889

The zero anchor turns intended displacement positive; the native competitor further improves BPC, with a quality trade-off. Leakage controls the competing uplift induced by enhancement, and independent endpoints improve control under the full objective. Relative to 0/A/N without E or L, their combination mainly improves intended uplift and quality while preserving BPC (.623 versus .624).

2. Why use finite penalties?

We use finite penalties to make violations costly while allowing trade-offs in how the control requirements are met. Equation (6) specifies ideal movements of fixed-response scores, which serve as training proxies for behavior in free generation. The thresholds ρ\rho and ϵ\epsilon set desired operating targets; their exact satisfaction on every record has not been established as necessary for effective generated control. Hard enforcement would give these thresholds priority over trade-offs in intended uplift and intervention magnitude.

This distinction matters because one steering endpoint is shared across many inputs. Different inputs have different score sensitivities: a change that helps one record meet its margin may worsen another record or require a larger intervention. Finite penalties allow the optimizer to weigh the benefit of reducing a violation against these costs and learn a shared intervention that balances the requirements across inputs.

Equations (9)–(10) implement this choice by assigning explicit costs to grounding, separation, and leakage violations, alongside intended-uplift rewards and an energy penalty. Allowing a violation does not remove its influence on learning: joint suppression and competing uplift still incur costs that a margin-only objective cannot express. The matched ablations above show that these distinctions remain effective in the soft implementation. Generation quality is assessed separately through configuration selection and evaluation.

We use fixed weights for a simple implementation of this trade-off: a single minibatch objective updates the endpoints through the frozen model, without additional dual variables or a multiplier-update schedule. This is an implementation choice rather than a requirement of the RGS design. Adaptive penalties, including primal–dual methods with slack variables, could implement the same trade-off; their potential benefit is discussed below.

3. Supplementary experiments support simpler implementations

We tested changes to the numerical implementation while retaining independent endpoints and the reference-grounded behavioral terms. These supplementary runs use Qwen3-4B, five training pairs, seed 42, layer 20, 40 epochs, learning rate .001, and training/inference strengths 1/1.5. Evaluation covers 40 held-out pairs and 3,164 prompt instances using DeepSeek-V4-Flash. This batch is separate from the submitted ablations above; its full-RGS baseline has BPC=.5552 and Q=4.0908Q=4.0908.

Change from matched full RGSΔ\DeltaBPC [95% CI]ΔQ\Delta Q [95% CI]
Replace LSE/softplus with hardmax/.05×ReLU−.0054 [−.0121,.0014]+.0236 [.0077,.0403]
Remove energy penalty and norm projection+.0085 [.0024,.0146]−.0025 [−.0182,.0139]

Intervals use 10,000 paired source-question bootstrap draws within value pairs, conditional on the training seed and saved outputs/ratings. For ϕβ(z)=log⁡(1+eβz)\phi_\beta(z)=\log(1+e^{\beta z}) with β=.1\beta=.1, ϕβ′(0)=.05\phi'_\beta(0)=.05; the replacement hinge matches this slope on its active side. Projection, when enabled, never activated in these runs.

The simpler penalty produces a small BPC change whose interval includes zero, while removing norm controls also retains strong control. Together with the structural ablations, this supports our central point: the behavioral design remains useful when its numerical implementation changes, as demonstrated in this setting.

4. Would dual ascent resolve the low satisfaction rates?

Adaptive multipliers offer another implementation of the same specification. For a residual gij(u)≤0g_{ij}(u)\le0 on record ii and condition jj, a projected dual update has the form

λijk+1=[λijk+ηkgij(uk)]+,\lambda_{ij}^{k+1}=\left[\lambda_{ij}^{k}+\eta_k g_{ij}(u^k)\right]_+,

so persistent violations receive increasing pressure. This could improve satisfaction. However, adapting constraint weights and calibrating the margin are different operations: positive rescaling of an existing constraint preserves its feasible set, while changing ρ\rho changes the requirement. The same absolute ρ=.8\rho=.8 corresponds to 2.54–4.38 reference units on Ministral/Llama, versus .76–1.23 on Qwen. Dual ascent does not automatically redefine this threshold or establish joint feasibility for a shared endpoint.

We added a condition-wise audit to locate the failures. These diagnostics use independent Validation sources from the five training-pair identities, with scores averaged within each response family, at the selected inference strength: 500 directional records per model. The table reports ranges across the six Ministral/Llama models, with ϵ=τ=.1\epsilon=\tau=.1.

DiagnosticEvaluation margin rrPass rate across six models
Joint hard conditions.80–8.2%
Joint smoothed conditions.80–8.0%
Intended uplift alone (G).80–8.4%
Joint smoothed conditions, post-hoc threshold changeOne reference unit27.8–70.8%

Within each model, intended-uplift satisfaction exceeds joint hard satisfaction by only 0–0.2 percentage points; the hard and smoothed joint rates also differ by only 0–0.2 points. Failures therefore largely coincide with insufficient intended uplift, rather than the conservatism of LSE. Also, the score ceiling ΔI≤−S0(yI∣x)\Delta_I\le-S_0(y_I\mid x) rules out only 0–2% of these records at ρ=.8\rho=.8, so it does not explain most failures.

The final row reproduces Table 23's threshold sensitivity. One reference unit is the median absolute unsteered score gap across response families and sources within each pair, then the median across pairs. Only the evaluation threshold changes. This weaker requirement does not certify the original margin; the fixed-threshold results remain primary.

These diagnostics locate the failed condition, while its cause remains unresolved. A direct primal–dual comparison should distinguish per-record from aggregate training constraints and assess both held-out satisfaction and free-generation control/quality.

5. Local geometry and the scope of the theoretical argument

We agree that common-shift invariance and the LSE bound are standard mathematical facts. Their contribution here is to expose the control ambiguity and connect each objective component to a specific behavioral requirement.

A linear activation addition still induces a nonlinear downstream score map. Assuming twice continuously differentiable fixed-response scores near zero intervention,

\qquad g_{iX}=\nabla_u S_u(y_{iX}\mid x_i)\big|_{u=0}.$$ Because the same vector is injected at multiple answer-prediction positions, $g_{iX}$ sums their downstream score sensitivities. These gradients depend on both the input and the response. The linearized conditions are $$g_{iI}^{\top}u\ge\rho,\quad (g_{iI}-g_{iA})^{\top}u\ge\rho,\quad (g_{iI}-g_{iN})^{\top}u\ge\rho,\quad g_{iA}^{\top}u\le\epsilon.$$ Within this approximation, a shared intervention is feasible when these half-spaces intersect the allowed norm ball. Compatible gradients permit a common direction; conflicting requirements can prevent one. Independent endpoints let the two steering directions use different intersections instead of requiring opposite vectors. Under this affine score approximation, LSE, softplus, hinge, and quadratic energy yield a convex objective for nonnegative weights. This is a local interpretation, not a global landscape result for the nonlinear model; compatibility and approximation accuracy at the learned endpoints remain to be measured. We will revise Sections 3.1–3.3 to distinguish the control specification from its finite-penalty implementation, connect the design claims directly to the matched ablations, and add the implementation-sensitivity and condition-wise diagnostics to the appendix.

I thank the authors for their detailed responses and additional experiments. While I appreciate these efforts, several of my main concerns remain insufficiently addressed.

1. Theoretical limitations. The proposed local linearization and half-space interpretation do not establish the feasibility of the steering constraints. For instance, two inputs with opposing gradients g1I=(1,0)g_{1I}=(1,0) and g2I=(−1,0)g_{2I}=(-1,0) require u1≥ρu_1\geq\rho and −u1≥ρ-u_1\geq\rho, which are incompatible for ρ>0\rho>0. Moreover, convexity under linearization does not characterize the actual nonlinear optimization landscape. For example, ΔI(u)=u2\Delta_I(u)=u^2 yields a nonconvex uplift objective −ΔI(u)=−u2-\Delta_I(u)=-u^2. I would have appreciated a more substantive analysis of these properties beyond the local approximation.

2. Constraint satisfaction. The reported intended-uplift satisfaction rates of only 0–8.4% across six models remain concerning. For instance, ΔI=0.2\Delta_I=0.2 and ΔA=−1\Delta_A=-1 yield strong relative separation but fail the intended-uplift constraint for ρ=0.8\rho=0.8. This raises questions about how effectively the proposed control specification is realized in practice.

3. Evaluation. The reliance on a single LLM judge remains a limitation. Additionally, the primary BPC metric measures relative behavioral separation rather than absolute improvement over the unsteered model, which is central to the paper's motivation.

Finally, the manuscript has not been updated to incorporate the rebuttal's clarifications and supplementary results.

While the rebuttal strengthens the empirical contribution, I do not believe it sufficiently resolves these concerns. Therefore, I will maintain my original score of 2.

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Paper summary

The paper argues that improving a pairwise preference margin does not necessarily increase support for the intended behavior or ensure selective control. It proposes Reference-Grounded Steering (RGS), which learns independent steering vectors using intended, competing, and model-native responses. Its objective encourages intended-response uplift relative to the unsteered model while penalizing separation violations, competing-response uplift, and intervention magnitude. Experiments across nine models show stronger bidirectional control than BiPO and RePS on 40 held-out combinations of ten known values, supported by interpolation and component-ablation studies.

Critical strengths
  • The distinction between ranking and control is relevant and clearly motivated at the conceptual level. A larger preference margin can conceal joint suppression or co-amplification, so examining absolute response-score changes provides useful information beyond relative preference alone. Jointly encouraging intended effects and constraining competing effects is a reasonable response to this problem.

  • The transfer experiments provide meaningful evidence that vectors learned against one competing value remain useful in other conflicts. RGS consistently improves the reported control metrics across nine models, suggesting that the results extend beyond a single model or training pair. This supports reusable control across combinations of familiar values, although it does not establish isolated trait representations.

Critical weaknesses
  1. The evidence for selectivity is narrower than the motivating problem.

Each generated response is scored only against the two values designated by its scenario. Although unsteered responses are evaluated, the experiments do not systematically establish intended-value uplift alongside preservation of other values and unrelated capabilities. Pairwise control therefore does not establish broad behavioral selectivity. Likewise, constraining scores on a small native-response pool does not demonstrate preservation of the broader model behavior.

  1. The comparisons do not sufficiently establish the benefit of RGS’s specific objective.

SPLIT [1] already combines preference-margin optimization with absolute likelihood training. A matched steering-vector comparison would clarify whether RGS’s reference grounding, native-response competition, and leakage penalty improve beyond this simpler objective. A prompting baseline is also important because prompting supplies RGS’s training demonstrations, yet the evaluation does not establish what control is retained or gained by replacing those prompts with vectors.

  1. Several design choices lack sufficient justification.

The early-token weighting in Eq. (1) is not clearly motivated or compared with uniform weighting. Equations (7) - (9) combine a smoothed maximum with a softplus penalty without establishing its advantage over simpler penalties. The paper specifies the hyperparameter values, but their selection procedure and sensitivity remain unclear. The method also combines the norm penalty in Eq. (10) with a hard projection onto ∥ud∥2≤30\|u_d\|_2\le30, without separately evaluating their contributions or explaining the bound.

Training responses are additionally labelled through their conditioning prompts without semantic validation. This leaves uncertainty about how reliably the demonstrations express the intended value and distinguish it from the competitor.

  1. Presentation makes the method unnecessarily difficult to assess.

Fig 1 does not sufficiently explain its coordinates, plotted points, or why particular locations represent desirable control. The introduction uses terms such as "endpoint", "zero-anchored", "0/A/N grounding", and BPC before providing enough context. Equations (4) - (8) also introduce substantial notation for three margin requirements that can be stated directly as ΔI≥ρ+max⁡(0,ΔA,ΔN).\Delta_I\ge\rho+\max(0,\Delta_A,\Delta_N).

The contribution "Frozen pair-transfer evaluation" would be clearer if it emphasized the substantive transfer finding rather than primarily describing configuration selection and evaluation procedures.

References [1] Xu et al. Why Steering Works: Toward a Unified View of Language Model Parameter Dynamics. ACL 2026.

Questions for authors
  1. What evidence shows that RGS increases intended-value support relative to the unsteered response while preserving non-target behaviors, beyond changing relative preference within the designated pair ? Should the selectivity claim be interpreted more narrowly ?

  2. How does RGS compare with SPLIT’s steering-vector variant under matched training data and intervention settings, and with direct prompting using the value definitions that generate its demonstrations ?

  3. How were the fixed objective coefficients, weighting and smoothing parameters, and norm bound selected ? What development data and tuning budget informed these choices, and what evidence supports their robustness ?

  4. Uniform weighting in Eq. (1), simpler margin penalties, and separate norm-penalty/projection ablations would help explain the design.

Optional experiments and suggestions

Reporting learned vector norms and projection frequency would clarify whether the bound is active. A semantic audit of the training responses would also help quantify demonstration fidelity.

5 comments

Response to Question 1 / Weakness 1

We agree that our evidence does not establish broad preservation of all non-target behaviors or unrelated capabilities. To clarify what it does establish, we distinguish three increasingly broad levels of control: (1) reference-grounded score control—whether steering increases the score of fixed intended responses relative to the unsteered model while controlling designated competitors; (2) conflict-level generative control—whether freely generated decisions move toward the requested concept, including on held-out recombinations of known values; and (3) global behavioral specificity—whether unrelated concepts, tasks, and capabilities remain unaffected. Our fixed-response diagnostics support (1), while our held-out generation results and the new analysis below support (2). We do not claim to have established (3), and will narrow our wording accordingly.

This distinction applies to concept steering more broadly, not only to values. Behavioral concepts are rarely independent coordinates: they may overlap, support one another, or conflict, so steering one concept can produce principled changes in semantically related concepts. Requiring every non-target concept to remain invariant is therefore not a structure-agnostic criterion for selectivity. A more appropriate distinction is between structured changes among related concepts and unintended spillover to unrelated behaviors or capabilities. Value steering makes this issue especially explicit because the Schwartz framework provides a known motivational structure: a decision may jointly express compatible values while trading off conflicting ones. Therefore, it would be a constraint that a steering would function following this structure on effect to generate human-like decisions, even if we can find the isolated steering basis. Our paper focuses on the first two levels of control; broad preservation of unrelated capabilities remains an important open question.

Given the rebuttal timeline, we conducted a theory-guided diagnostic using one frozen Achievement endpoint. This case compactly covers three informative relationships: Benevolence is its Seen training competitor, Power is an Unseen but compatible value within self-enhancement, and Universalism is an Unseen conflicting value within self-transcendence. We applied the same endpoint without retraining or pair-specific calibration.

Scored valueRelationship to AchievementPromptsSupport change: steered − unsteered [95% CI]
AchievementTarget, equal-pair mean244+1.308 [+1.101, +1.509]
PowerUnseen compatible value80+0.088 [−0.200, +0.363]
UniversalismUnseen conflicting value86−1.895 [−2.244, −1.547]
BenevolenceSeen conflicting value78−2.115 [−2.513, −1.718]

Intervals use 10,000 within-pair source-cluster bootstrap replicates, preserving the steered–unsteered pairing. The Power interval crossing zero is not interpreted as statistical equivalence.

These results directly demonstrate absolute intended-value uplift in free generation, rather than only a larger pairwise margin. The relation-dependent pattern confirms that the RGS intervention follows the natural (Schwartz) structure of values, which is more coherent on invervention, instead of being globally behaviorial specified. It does not establish global behavioral preservation. In the revision, we will extend this analysis systematically across the remaining value endpoints and explicitly state the scope and limits of our selectivity claim.

Response to Question 2 / Weakness 2

We agree that SPLIT-vector and direct prompting are important baselines. We added three analyses: (1) a matched RGS–SPLIT comparison that isolates the training objective, (2) a nine-model full-method comparison including SPLIT-vector and direct prompting, and (3) matched ablations of RGS’s zero anchor, model-native competitor, and leakage penalty. Together, they show that RGS provides substantially stronger control than SPLIT (with a measurable quality trade-off); compared with direct prompting, RGS usually provides stronger control without explicit value instructions, while prompting preserves higher generation quality.

1. Matched RGS–SPLIT objective comparison

SPLIT and RGS both use absolute response likelihoods, but impose different control specifications. SPLIT optimizes the likelihoods of both polarity responses together with their preference margin; this can still increase the competing response, as in (ΔI,ΔA)=(2,1)(\Delta_I,\Delta_A)=(2,1). RGS additionally requires intended uplift relative to the unsteered model, includes the model-native response as a competitor, and limits competing-response uplift.

We isolated this difference on Qwen3-4B. Both objectives used the same signed-axis parameterization, training pools, answer-span intervention, optimizer, regularization, layer 20, train/evaluation strengths 1/1.51/1.5, seed 42, 40 epochs, and learning-rate grid 0.001,0.01,0.08\\{0.001,0.01,0.08\\}. SPLIT retained its open-source data-loss coefficients. Thus, the principal changed factor was the training objective.

MethodSeen qqUnseen BPCUnseen QQ
SPLIT-vector−0.3950.1913.916
RGS objective−0.4590.4273.793

RGS improves BPC by +0.236+0.236 (95% CI [+0.220,+0.252][+0.220,+0.252]), with a quality difference of −0.123-0.123 (CI [−0.152,−0.094][-0.152,-0.094]). This demonstrates stronger control under matched parameterization and intervention conditions, but not quality-matched superiority: neither configuration satisfies the Seen q≥−0.15q\ge-0.15 quality threshold.

2. Nine-model SPLIT and direct-prompting comparisons

We next compared the complete methods across all nine models and 40 held-out value pairs. Each vector method used the same model-specific training pools, five-layer search budget, 40-epoch horizon, Seen-only configuration selection, and frozen Unseen evaluation, while retaining its native parameterization, loss coefficients, and intervention scope. SPLIT-vector used its open-source method-specific settings.

For direct prompting, we appended the exact target-value definition used to generate the training demonstrations, without Seen tuning. The Judge received only the original scenario and generated response, not the added control instruction.

MethodNine-model mean BPCNine-model mean QQ
RGS0.6374.275
SPLIT-vector0.1684.183
Direct prompting0.4284.471

RGS exceeds SPLIT-vector in BPC, OrderPres, and Induction on all nine models. Compared with direct prompting, RGS achieves higher BPC and Induction on eight models and higher OrderPres on seven; prompting achieves higher quality on all nine and slightly higher control on Qwen3-4B. Thus, the learned vectors retain—and in most evaluated models strengthen—control without requiring explicit value instructions at inference time, whereas direct prompting better preserves generation quality.

3. RGS component ablations

Finally, we tested the RGS-specific components requested by the reviewer. These matched Qwen3-4B comparisons fixed the independent-endpoint parameterization, layer 20, evaluation strength 1.5, seed 42, training data, and all non-varied objective terms. BPC and quality were evaluated on all 40 held-out pairs; score displacements were measured on the fixed Validation response pools.

Component contrastBPC: before → afterΔ\DeltaBPC [95% CI]ΔQ\Delta Q [95% CI]
Add zero anchor0.336 → 0.517+0.181 [+0.166,+0.196][+0.166,+0.196]+2.162 [+2.128,+2.196][+2.128,+2.196]
Add model-native competitor0.517 → 0.562+0.046 [+0.035,+0.056][+0.035,+0.056]−0.103 [−0.124,−0.082][-0.124,-0.082]
Add leakage penalty, with enhancement active0.469 → 0.559+0.090 [+0.077,+0.103][+0.077,+0.103]−0.093 [−0.115,−0.071][-0.115,-0.071]

Adding the zero anchor changes mean intended-response displacement from −12.180-12.180 to +0.993+0.993, preventing suppression-based solutions. Adding the model-native competitor further improves generative control. With intended enhancement active, adding leakage control changes the competing-response displacement from +0.736+0.736 to −0.851-0.851, while intended displacement remains positive at +1.243+1.243. The latter two gains involve quality trade-offs, and these conditional contrasts should not be interpreted as an additive decomposition of the RGS–SPLIT difference.

All confidence intervals use 10,000 paired within-pair source-cluster bootstrap replicates and condition on the saved training runs and Judge records. Because the original scenario generator was no longer available, newly trained supplementary comparisons use new but internally shared pools constructed under the original protocol; these results are reported separately from the original main-table runs. We will include complete configurations and per-model results in the revision.

Response to Questions 3–4 and Weakness 3

Thank you for requesting further justification and robustness analysis. We now report the original parameter-development process and add three targeted studies: (1) local coefficient sensitivity, (2) direct ablations of token weighting, penalty form, and norm controls, and (3) a blind human audit of the training demonstrations. The results show that control is stable across the tested coefficient ranges, early-token weighting improves free-generation performance, RGS is robust to a simpler penalty form, the norm bound does not drive the gains, and most conditioned responses satisfy a strict value-fidelity criterion.

1. Parameter selection and sensitivity

Initial development used Qwen3-4B on Self-Direction–Conformity with held-out development data. Approximately 70 training jobs explored score weighting, margin/smoothing/threshold parameters, objective coefficients, and the hard norm bound. We selected the default using validation performance and then fixed it for the subsequent value pairs and models. This process was separate from the Seen-only selection of layer and inference strength reported in the paper.

The code-level enhance/separation/leakage/energy coefficients are 0.5/1/0.2/10−40.5/1/0.2/10^{-4}, equivalent to the normalized coefficients reported in Appendix A under a common positive rescaling. The remaining defaults are γ=0.5\gamma=0.5, ρ=0.8\rho=0.8, ϵ=0.1\epsilon=0.1, τ=β=0.1\tau=\beta=0.1, and norm bound B=30B=30.

We additionally fixed nine configurations before evaluation and varied one factor at a time on Qwen3-4B, holding the training data, independent endpoints, zero/alternative/model-native competitors, layer, strength, seed, learning rate, and training horizon fixed. All configurations were evaluated on the same 40 held-out pairs.

ParameterTested values (default in bold)Unseen BPC
Enhancement coefficient0.25/0.5/0.750.25/\mathbf{0.5}/0.750.569/0.558/0.5520.569/0.558/0.552
Leakage coefficient0.1/0.2/0.30.1/\mathbf{0.2}/0.30.544/0.558/0.5640.544/0.558/0.564
Margin ρ\rho0.4/0.8/1.20.4/\mathbf{0.8}/1.20.556/0.558/0.5540.556/0.558/0.554
Leakage allowance ϵ\epsilon0/0.1/0.20/\mathbf{0.1}/0.20.560/0.558/0.5510.560/0.558/0.551

Across these settings, BPC remains within 0.5440.544–0.5690.569, with a maximum absolute change of 0.0130.013 from the default; mean quality remains within 4.0524.052–4.1164.116. Thus, the reported control behavior is not tied to a narrow coefficient choice.

2. Weighting, penalty form, and norm controls

In a separate matched rerun, we evaluated six implementation variants under the same fixed model and training setup.

VariantUnseen BPCΔ\DeltaBPC vs. matched RGS [95% CI]QQ
Matched full RGS0.555—4.091
Uniform token weighting0.529−0.026 [−0.037,−0.016][-0.037,-0.016]4.048
Hard max + hinge0.550−0.005 [−0.012,+0.001][-0.012,+0.001]4.115
Projection only0.560+0.005 [−0.002,+0.011][-0.002,+0.011]4.087
Energy penalty only0.556+0.001 [−0.005,+0.006][-0.005,+0.006]4.104
Neither norm control0.564+0.009 [+0.002,+0.015][+0.002,+0.015]4.088

Token weighting. Demonstrations state the decision first and then provide its rationale, motivating greater weight on early answer tokens. Uniform weighting reduces BPC by 0.0260.026 and quality by 0.0430.043, supporting early-token weighting for free-generation control. Because autoregressive generation is causal, later tokens are conditioned on all preceding tokens, so early answer tokens disproportionately shape the remainder of the response and should receive greater weight. We therefore use a decreasing token weight, but we do not use an exponential discount. Recurrent or state-space models, whose memory typically decays exponentially, are on average outperformed by Transformers, which is consistent with a slower-than-exponential decay of token influence. This motivates a power-law (Riemann zeta–style) schedule rather than an exponential one.

Penalty form. LogSumExp and softplus provide a differentiable conservative approximation to the worst constraint violation. Replacing them jointly with a hard maximum and hinge produces similar BPC. This shows that RGS is robust to the precise surrogate form: its gains arise from the reference-grounded control specification rather than a particular smoothing choice.

Reviewer_GtNEOpenReview ↗
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Paper summary

This paper studies an important but underexplored problem in representation steering: the distinction between improving relative behavioral preferences and achieving selective behavioral control. The authors argue that pairwise ranking objectives are insufficient to guarantee the desired behavioral changes, since a positive preference margin can arise from intended behavior enhancement, joint suppression, or broad co-amplification. To address this issue, the paper proposes Reference-Grounded Steering (RGS), which formulates representation steering as a reference-grounded constrained optimization problem. Specifically, RGS introduces intended-response uplift, alternative-response suppression, native-response separation, and intervention energy regularization, while employing independently parameterized steering endpoints. The proposed approach is evaluated on nine language models from three model families using conflicts among the ten Schwartz human values. Experimental results show that RGS consistently outperforms BiPO and RePS in bidirectional preference contrast, order preservation, and target-value induction on held-out value-pair combinations. The paper further provides ablation studies and interpolation experiments to investigate the contributions of different objective components and endpoint parameterizations.

Critical strengths

The paper addresses a meaningful and well-motivated problem. The central observation that ranking improvement does not necessarily imply intended behavioral enhancement is intuitive yet important. In particular, the distinction between relative score margins and absolute behavioral movements provides a useful conceptual framework for understanding the limitations of existing preference-based steering methods.

The proposed RGS framework is reasonably well motivated. By grounding behavioral changes against the same unsteered reference model, the method explicitly specifies how intended, alternative, and native responses should change. The introduction of a zero-anchored objective is particularly interesting because it prevents an optimization process from satisfying relative separation simply by suppressing competing responses. Furthermore, independently parameterized endpoints offer additional flexibility for modeling potentially asymmetric behavioral interventions.

The experimental evaluation is relatively comprehensive. The authors evaluate nine models across three model families and consider 40 held-out value-pair combinations without additional tuning. The use of bidirectional preference contrast, order-preserving rate, and target-value induction provides multiple perspectives on behavioral control. The matched ablation studies are also valuable, as they attempt to disentangle the effects of reference grounding, intended-response enhancement, alternative leakage control, and endpoint parameterization.

Another positive aspect is the paper's effort to investigate the behavior between steering endpoints rather than evaluating only the endpoints themselves. The interpolation experiments provide additional evidence about the stability and consistency of behavioral transitions. The authors also acknowledge several limitations, including the reliance on model-generated training data, a single LLM judge, and the restricted evaluation settings.

Critical weaknesses

The connection between teacher-forced response likelihood and actual behavioral control deserves further investigation. RGS optimizes score displacements on fixed response pools, whereas the main evaluation relies on freely generated responses. Although the paper reports a correlation between the proposed objective and generation-based metrics, teacher-forced likelihood changes do not necessarily translate into corresponding changes in the generated response distribution. In particular, the three response pools may not adequately represent the broader behavioral space. It would be useful to establish more directly when and why the proposed score-space constraints lead to reliable behavioral changes during generation.

The generalization claims should also be interpreted cautiously. The held-out evaluation uses new combinations of values that have already appeared in the training pairs. This demonstrates recombinational transfer, but it does not necessarily establish generalization to genuinely unseen behaviors or value definitions. Furthermore, the evaluation relies on a single LLM-based judge, making the results potentially sensitive to judge preferences and evaluation biases. Additional human evaluation or independent evaluation models would strengthen the empirical conclusions.

Finally, the interpolation results require a more nuanced interpretation. Although RGS achieves fewer local reversals and a wider control range, linear interpolation between two steering endpoints does not necessarily imply that the resulting behavioral trajectory is semantically smooth or predictable. The observed monotonicity is based on a limited number of sampled interpolation coordinates and an LLM-based support metric. Stronger evidence would be needed to establish the general reliability of continuous behavioral control. The effectiveness of representation steering has often been unstable and inconsistent across models and settings. I recommend that the authors conduct a deeper analysis of the underlying mechanisms.

Questions for authors

How does RGS fundamentally differ from existing constrained optimization or multi-objective preference learning approaches? Can the authors identify a theoretical property or optimization advantage that cannot be readily obtained by combining conventional pairwise objectives with reference-relative score constraints?

Since the proposed method optimizes teacher-forced likelihood changes on fixed response pools, how sensitive is its performance to the quality, diversity, and coverage of these pools? Would the method remain effective if the native response distribution were substantially more diverse or included responses exhibiting unintended behaviors not represented during training?

3 comments

Response to Reviewer GtNE

We thank the reviewer for recognizing the importance of distinguishing preference ranking from selective behavioral control, as well as the breadth of our evaluation. We added direct free-generation measurements, controlled response-pool interventions, independent Judge and human evaluations, and a more precise analysis of what the interpolation results establish. We respond to the two questions and three weaknesses below.

Question 1: Relation to constrained optimization and multi-objective preference learning

RGS does not claim a new optimization algorithm. Its distinction is a reference-grounded control specification that removes an ambiguity inherent to pairwise ranking.

A pairwise objective depends only on a score difference and is therefore invariant to common shifts:

(ΔI,ΔA)↦(ΔI+c,ΔA+c).(\Delta_I,\Delta_A)\mapsto(\Delta_I+c,\Delta_A+c).

For example, (ΔI,ΔA)=(1,0)(\Delta_I,\Delta_A)=(1,0) and (−1,−2)(-1,-2) have the same pairwise margin, although the latter suppresses the intended response. RGS instead specifies

\qquad \Delta_A\le\epsilon,$$ where $\Delta_I,\Delta_A,\Delta_N$ are intended-, alternative-, and native-response score changes relative to the same unsteered model. This simultaneously requires absolute intended uplift, separation from both competing response families, and bounded alternative uplift. RGS further uses $$m_\tau=\Delta_I-\operatorname{LSE}_\tau(0,\Delta_A,\Delta_N).$$ Because LogSumExp upper-bounds the hard maximum, $m_\tau\ge\rho$, together with $\Delta_A\le\epsilon$, is a conservative sufficient certificate for the four score-space control inequalities. In contrast, satisfying a conventional weighted pairwise or multi-objective loss does not provide this certificate, because improvement in one term may compensate for violation of another. A conventional pairwise method augmented with exactly these reference-relative conditions would implement the same core specification; we do not claim otherwise. Our contribution is to identify the missing control conditions, formulate them in a common unsteered coordinate system, and test whether optimizing them improves generated behavior. Training uses standard optimization and soft penalties, so it encourages rather than guarantees per-record satisfaction. ## Question 2 / Weakness 1: From fixed response pools to generated behavior We address this connection through direct generation measurements, matched component interventions, and controlled response-pool perturbations. ### Direct free-generation measurements For each steered response $r^{(d)}$ and the unsteered response $r^{(0)}$ to the same prompt, we measure target- and competitor-support changes: $$U=s_d(r^{(d)})-s_d(r^{(0)}),\qquad C=s_{\bar d}(r^{(d)})-s_{\bar d}(r^{(0)}).$$ Target uplift requires $U>0$; joint success requires $U>0$ and $C\le0$. | Method | Target change $U$ | Competitor change $C$ | Target-uplift rate | Joint-success rate | |---|---:|---:|---:|---:| | RGS | **+1.393** | **−1.479** | **63.95%** | **61.97%** [61.34, 62.59] | | BiPO | +0.978 | −0.927 | 52.09% | 49.12% [48.52, 49.75] | | RePS | +0.850 | −0.956 | 50.45% | 48.65% [48.01, 49.28] | These results cover nine models and 40 held-out value pairs. RGS has positive mean target change in all 18 model-by-direction cells. Thus, its BPC advantage reflects not only separation between steered endpoints but also more frequent target uplift relative to unsteered generation. ### Matched score-space and generation interventions We next varied individual objective components while fixing the model, data, endpoint parameterization, layer, strength, optimizer, and training horizon. | Matched intervention | Teacher-forced Validation change | Held-out generation BPC | |---|---|---:| | Add zero anchor with enhancement/leakage disabled | $\Delta_I: -12.180\rightarrow +.993$ | .336 → .517 | | Add leakage control with enhancement fixed | $\Delta_A: +.736\rightarrow -.851$ | .469 → .555 | The zero anchor reverses intended-response displacement from strongly negative to positive while improving generated control. Leakage control similarly reverses competitor displacement while improving generated BPC. These matched changes provide a direct empirical bridge from the intended score-space role of each component to its generated behavior.

Response-pool sensitivity

The training pool is broader than three global responses: each model–value-pair dataset contains 400 training sources and three target-conditioned, three alternative-conditioned, and three model-native responses per source, for 3,600 training responses.

We nevertheless tested sensitivity to role accuracy, native-response resampling, and broader native-response coverage. All comparisons use Qwen3-4B, the same five training pairs, full objective, independent endpoints, and seed 42.

ConditionPool interventionBPCMatched BPC difference [95% CI]
BUnmodified pool.5552—
L20Swap target/alternative roles for 20% of examples.4877−.0675 [−.0788, −.0559] vs. B
NRResample three native responses per source.5552+.0001 [−.0053, +.0056] vs. B
NCSelect native responses for broader behavior-category and support-score coverage.5565+.0012 [−.0039, +.0065] vs. NR

RGS is sensitive to incorrect target/alternative roles, as expected, but stable to native-response resampling. Selecting a more diverse native subset produces no clear additional control gain within the tested candidate distribution. Notably, the label-corrupted condition increases generation quality by +.112+.112 while reducing BPC, further showing that generic response quality is not a substitute for accurate behavioral control.

We also conducted a blind audit of 100 training sources and 300 responses. Fifteen annotators provided two independent ratings per response. Under a strict criterion requiring support for the conditioned value to be at least 4/5 and at least one point above the competing value, 75.5% [70.75%, 80.25%] of ratings pass. The controlled corruption result confirms that RGS uses these semantic roles rather than treating the pools as interchangeable.

These interventions test sampling and coverage changes within the represented response families. They do not establish robustness to arbitrary unseen behavior classes, and we will state this limitation explicitly.

Weakness 2: Generalization scope and evaluator robustness

We agree that the held-out evaluation establishes compositional transfer across unseen pairings of known values, not generalization to entirely unseen behaviors or value definitions. All ten values appear during training, but the operating point selected on five training pairs is reused over the remaining 40 combinations without retraining or pair-specific calibration. We will consistently describe this result as transfer across held-out combinations of known values.

Across the submitted DeepSeek evaluation and two additional Judge evaluations, RGS ranks first on BPC, OrderPres, and Induction. Values within each cell are ordered as RGS / BiPO / RePS.

JudgeBPCOrderPresInductionQuality change qq
DeepSeek-V4-Flash.718 / .476 / .451.808 / .670 / .574.852 / .682 / .644−.103 / −.087 / −.122
GPT-6-luna.649 / .461 / .447.819 / .715 / .636.841 / .697 / .666−.269 / −.289 / −.301
Claude Haiku 5.5.578 / .414 / .390.773 / .674 / .593.797 / .657 / .639−.603 / −.422 / −.561

A method-blind human evaluation of 90 sampled prompts provides complementary evidence. For D=(target support−competitor support)/4D=(\text{target support}-\text{competitor support})/4, human ratings are .800 for RGS, .424 for BiPO, and .402 for RePS. The RGS differences are +.376+.376 [+.284, +.472] and +.399+.399 [+.300, +.500], respectively. Human quality differences are small and both confidence intervals include zero.

We therefore regard the control ranking as robust across evaluators, while treating fine-grained quality comparisons as evaluator-dependent and avoiding any claim of a consistent RGS quality advantage.

Weakness 3: Interpretation of endpoint interpolation

The interpolation analysis is a sampled behavioral stress test, not a proof of globally smooth or predictable semantic trajectories. It covers nine coordinates, 360 model–pair trajectories per method, and 597,996 newly generated interior responses across all model–method conditions.

MethodNo-reversal trajectoriesReversal stepsMean reversal magnitude
RGS279/360 (77.5%)95.020
BiPO228/360 (63.3%)217.033
RePS203/360 (56.4%)215.033

The endpoint span equals 2×2\timesBPC, so the interior reversal statistics—not the wider span alone—provide the additional path evidence. RGS has the most or tied-most no-reversal pairs on seven of nine models; RePS and BiPO lead on Qwen3-8B and Qwen3-14B, respectively. RGS also has a larger mean minimum quality loss along the sampled chords (−.158-.158, versus −.116-.116 for BiPO and −.143-.143 for RePS).

Although the hidden-state offset changes continuously with the interpolation coordinate, greedy decoding can cross discrete token-decision boundaries. The nine sampled pair-level means therefore do not imply prompt-level monotonicity, semantic continuity between coordinates, or reliable control at every unsampled point. We will revise the paper to describe these results as greater order preservation with fewer and smaller reversals along sampled endpoint chords, rather than as a general guarantee of continuous behavioral control.

Finally, our component ablations identify objective-level behavioral mechanisms; they do not identify neural circuits or establish a complete mechanistic account of interpolation stability. We will make this scope explicit.

Reviewer_uY2kOpenReview ↗
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3
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Informativeness
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Paper summary

This paper investigates a limitation of pairwise preference-based representation steering: improving the relative ranking between two behaviors does not necessarily imply an absolute increase in support for the intended behavior. To address this limitation, the authors propose Reference-Grounded Steering (RGS), which optimizes reference-relative response-score changes using intended uplift, competitor separation, leakage control, and intervention regularization.

The method is evaluated against BiPO and RePS across nine language models from three model families. Experiments on held-out combinations of Schwartz values show consistent improvements in bidirectional preference contrast, order preservation, and target-value induction. The paper also includes matched ablations and interpolation analyses.

Critical strengths
  1. Well-motivated problem formulation. The distinction between relative preference ranking and selective behavioral control is important. The paper provides a clear explanation of why a positive pairwise margin can arise from undesirable changes such as joint suppression or co-amplification.
  2. Principled objective design. RGS introduces reference-relative constraints for intended, alternative, and native responses. The loss components are mathematically explained, and the resulting formulation provides a meaningful extension to pairwise steering objectives.
  3. Consistent empirical improvements. RGS outperforms BiPO and RePS on the three primary control metrics across all nine evaluated models. This consistency across different model families supports the practical effectiveness of the approach.
  4. Useful ablation studies. The matched comparisons help clarify the contributions of zero anchoring, intended-response enhancement, alternative leakage control, and independent endpoint parameterization.
  5. Careful transfer evaluation. Selecting steering configurations on five value pairs and evaluating them on 40 held-out pair combinations without further tuning is a useful experimental design.
Critical weaknesses
  1. Limited validation of absolute behavioral uplift. A central motivation of the paper is that relative ranking improvements do not guarantee intended behavioral enhancement. However, the primary free-generation metric, BPC, measures separation between the two steered endpoints rather than absolute improvement over the unsteered model. Although OrderPres and Induction provide additional evidence, they do not directly establish intended-support uplift. This leaves a gap between the proposed score-space control specification and the behavioral conclusions.
  2. Reliance on a single LLM evaluator. The main generation metrics depend on judgments from DeepSeek-V4-Flash. Since value support is context-sensitive and potentially subjective, independent evaluator validation or a human-annotated subset would strengthen confidence in the results.
  3. Restricted generalization setting. The held-out evaluation recombines values already represented during training. Consequently, the results demonstrate transfer across unseen value-pair combinations, but not generalization to entirely unseen behaviors or value definitions.
  4. Limited training-seed coverage for mechanism studies. Several key ablations are primarily based on a single training seed and one model. The reported source-cluster bootstrap intervals do not capture training-seed variability, limiting confidence in the robustness of some mechanistic conclusions.
  5. Incomplete separation of methodological factors. RGS differs from the baselines in both objective design and endpoint parameterization, while the methods retain their native intervention mechanisms. The matched ablations partially address this issue, but additional controlled comparisons would help isolate the contribution of reference grounding.
Questions for authors
  1. Could the authors report the absolute changes in intended and alternative value-support scores relative to unsteered generation, including the proportion of examples exhibiting intended uplift?
  2. How robust are the results to alternative LLM judges or human judgments? Is there evidence of agreement on value support and response quality?
  3. What explains the discrepancy between the strong free-generation metrics and the relatively low smoothed-control diagnostic pass rates on several Ministral and Llama models?
  4. How stable are the main ablation findings across independent training seeds, particularly for the endpoint-parameterization and loss-component comparisons?
  5. Can the authors provide a comparison that more tightly controls endpoint parameterization and intervention mechanisms to isolate the benefits of the reference-grounded objective?
2 comments

We thank the reviewer for recognizing the distinction between preference ranking and behavioral control, the principled design of RGS, and the consistency of our results. To address the reviewer’s concerns, we added: (i) generation-level absolute uplift measurements across all nine models, (ii) evaluations by two additional LLM judges and 15 blinded human annotators, (iii) five-seed endpoint and loss-component ablations, and (iv) an objective-matched steering-vector comparison. The new results directly support absolute intended-value uplift, while clarifying the scope of our quality, mechanism, and generalization claims.

Question 1 / Weakness 1: Absolute intended-value uplift in free generation

We directly compared each steered response r(d)r^{(d)} with the unsteered response r(0)r^{(0)} to the same prompt. For target value dd and competitor dˉ\bar d, we define

C=s_{\bar d}(r^{(d)})-s_{\bar d}(r^{(0)}).$$ Target uplift requires $U>0$; joint success requires $U>0$ and $C\le0$. | Method | Target change $U$ | Competitor change $C$ | Target-uplift rate | Joint-success rate | |---|---:|---:|---:|---:| | RGS | **+1.393** [1.371, 1.415] | **−1.479** [−1.499, −1.458] | **63.95%** [63.30, 64.60] | **61.97%** [61.34, 62.59] | | BiPO | +0.978 [0.955, 1.003] | −0.927 [−0.948, −0.905] | 52.09% [51.43, 52.76] | 49.12% [48.52, 49.75] | | RePS | +0.850 [0.829, 0.872] | −0.956 [−0.976, −0.935] | 50.45% [49.79, 51.11] | 48.65% [48.01, 49.28] | Each method covers 56,952 steered responses across nine models and 40 held-out value pairs. RGS has positive mean target change in all 18 model-by-direction cells. Its BPC advantage therefore reflects not only endpoint separation, but more frequent target uplift without competitor amplification. The intervals use paired source-cluster bootstrap and condition on the frozen training runs, generations, and Judge records. ## Question 2 / Weakness 2: Robustness across LLM judges and human evaluation We reevaluated the same frozen outputs using GPT-6-luna and Claude Haiku 5.5, without reselecting configurations. Values within each cell are ordered as RGS / BiPO / RePS. | Judge | BPC | OrderPres | Induction | Quality change $q$ | |---|---:|---:|---:|---:| | DeepSeek-V4-Flash | **.718** / .476 / .451 | **.808** / .670 / .574 | **.852** / .682 / .644 | −.103 / −.087 / −.122 | | GPT-6-luna | **.649** / .461 / .447 | **.819** / .715 / .636 | **.841** / .697 / .666 | −.269 / −.289 / −.301 | | Claude Haiku 5.5 | **.578** / .414 / .390 | **.773** / .674 / .593 | **.797** / .657 / .639 | −.603 / −.422 / −.561 | All three judges rank RGS first on BPC, OrderPres, and Induction. Pairwise quadratic-weighted agreement on value-support scores is also high ($\kappa=.859$–$.898$). We additionally conducted a method-blind human evaluation of 90 randomly sampled prompts spanning all nine models and 40 value pairs. Fifteen annotators scored every response. For $D=(\text{target support}-\text{competitor support})/4$, RGS achieves .800, compared with .424 for BiPO and .402 for RePS. The paired differences are $+.376$ [+.284, +.472] and $+.399$ [+.300, +.500], respectively. Human–Judge correlations for $D$ range from .838 to .886. Human quality scores are similar across methods: 4.711 for RGS, 4.652 for BiPO, and 4.698 for RePS, with both RGS differences including zero. Human–Judge quality correlations are also lower (.299–.359). We therefore treat the value-control conclusion as robust across evaluators while avoiding any claim that RGS has a consistent quality advantage. ## Question 3: Free-generation performance versus smoothed-control diagnostics The two evaluations measure different objects. BPC measures aggregate endpoint separation in free generations over 40 held-out value combinations. The diagnostic is a stricter, per-record sufficient condition evaluated on fixed response families from five Validation pairs: $$m_\tau=\Delta_I-\operatorname{LSE}_\tau(0,\Delta_A,\Delta_N), \quad J(r)=\mathbf{1}[m_\tau\ge r,\\ \Delta_A\le\epsilon].$$ A model can therefore show strong average generative separation while individual fixed-response records fail one diagnostic condition. The fixed threshold $r=.8$ has different effective strictness across model families. Measured in a method-blind reference scale derived only from unsteered family-score differences, .8 corresponds to .76–1.23 reference units for Qwen but 2.54–4.38 units for Ministral/Llama. At the original threshold, the corresponding hard-condition rates are also only 0–8.2% on Ministral/Llama, showing that smoothing itself is not the primary cause.

As a sensitivity analysis, replacing .8 with one model-specific reference unit—while leaving τ\tau, ϵ\epsilon, the responses, and all steering configurations unchanged—raises RGS’s Ministral/Llama diagnostic rates from 0–8.0% to 27.8–70.8%. RGS remains best or tied-best under the fixed diagnostic and best on all nine models under the reference-scaled diagnostic. This post-hoc analysis explains the cross-model floor effect; it does not replace or certify the original r=.8r=.8 specification.

Question 4 / Weakness 4: Stability across training seeds

We repeated the endpoint and loss-component comparisons on Qwen3-4B using five seeds (40–44). All cells use the same layer, training and inference strengths, training horizon, evaluation protocol, and shared training pool. Reported values are mean effects across seeds ±\pm seed standard deviation.

ContrastΔ\DeltaBPC across seeds
Separate endpoints − signed axis, enhancement/leakage off+.1932 ±\pm .0068
Separate endpoints − signed axis, enhancement/leakage on+.1342 ±\pm .0065
Add leakage with enhancement active, separate endpoints+.0858 ±\pm .0016
Add both enhancement and leakage, separate endpoints−.0017 ±\pm .0060

The independent-endpoint advantage and the benefit of leakage control with enhancement active remain positive in every seed. Although jointly adding the two terms has little mean effect on BPC, it improves the Validation worst-case margin by +.2923±.0019+.2923\pm.0019 and reduces the negative intended-displacement rate from 19.56% to 8.96%.

The endpoint-by-term interaction changes sign between the submitted and supplementary batches. We will therefore retain the replicated main-effect conclusions but remove any directional claim about this higher-order interaction.

Because the original scenario generator was no longer available, these supplementary runs use one newly constructed, internally shared pool generated under the original protocol. All within-batch contrasts remain matched and will be reported separately from the submitted runs.

Question 5 / Weakness 5: Isolating the reference-grounded objective

We added a matched RGS–SPLIT[1](another baseline, see also our response to Reviewer 3ffD) steering-vector comparison. Both methods use the same signed-axis parameterization, training pools, answer-span intervention, optimizer, regularization, layer, training/evaluation strengths, seed, learning-rate search budget, and 40-epoch horizon. The principal changed factor is the objective: SPLIT combines absolute likelihood and a preference margin, whereas RGS additionally grounds intended uplift at the unsteered model, competes against the model-native response, and limits competitor uplift.

ObjectiveSeen qqHeld-out BPCHeld-out QQ
SPLIT[1]−.395.1913.916
RGS−.459.4273.793

Under matched parameterization and intervention conditions, RGS improves BPC by +.236+.236 [+.220, +.252], with a quality difference of −.123-.123 [−.152, −.094]. This establishes stronger control, although not quality-matched superiority: neither configuration satisfies the Seen q≥−.15q\ge-.15 threshold.

A complementary single-factor ablation isolates the zero anchor. With endpoint parameterization and intervention scope fixed, and with the native competitor and auxiliary terms disabled, adding only the zero anchor changes mean intended-response displacement from −12.180-12.180 to +.993+.993 and increases held-out BPC from .336 to .517 (Δ=+.181\Delta=+.181 [+.166, +.196]). Together, these comparisons isolate both the objective-level advantage and the specific role of reference grounding.

References [1] Xu et al. Why Steering Works: Toward a Unified View of Language Model Parameter Dynamics. ACL 2026.

Weakness 3: Scope of generalization

Our evidence establishes compositional transfer across held-out combinations of known values, not generalization to entirely unseen values or behaviors. All ten values appear during training, but the same operating point selected on five training pairs is reused over 40 held-out recombinations without retraining or pair-specific calibration. We will revise the paper to describe this result consistently as transfer across held-out combinations of known values.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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