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Under review as a conference paper at ICLR 2027

Many Preferences, Few Policies: Compact Portfolios for Multi-Objective LLM Alignment

Abstract

Aligning large language models (LLMs) requires balancing competing objectives such as helpfulness, harmlessness, and conciseness. The appropriate balance varies across users and applications, yet training, evaluating, and deploying many policies across different reward weights is costly. We study how to identify a small portfolio of LLMs that preserves near-optimal performance across all reward weightings. We propose PALM (Portfolio of Aligned LLMs), an algorithm that combines a structured grid of weight vectors, a lazy search that optimizes policies only where needed, and pruning. Given target approximation tolerances, PALM returns a portfolio that provably contains a near-optimal policy for every weight vector, with an explicit upper bound on portfolio size. Such portfolios can support scalable personalization, reward-weight exploration during model development, and compact decoding-time configurations. Experiments show that PALM generally achieves smaller approximation gaps than same-size portfolios built from uniformly spaced or randomly sampled weights. We further demonstrate that PALM scales effectively to higher-dimensional reward spaces through efficient search and sparse preference structure.

Primary area:
foundation or frontier models, including LLMs
Keywords:
alignment, large language models, portfolios, multi-objective reinforcement learning

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
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Paper summary

This paper studies the problem of how to select a small portfolio of policies for multi-objective LLM alignment under linear scalarization. Authors introduce PALM to construct a compact portfolio of policies while ensuring the approximation quality across different preferences. It combines preference-space discretization, a lazy search procedure that uses existing policies to assess coverage, and pruning to remove redundant policies.

Theoretical results on approximation quality and portfolio size are provided, with the extension to sparse preferences that makes the size bound polynomial in dd for a fixed support size.

Experiments show it generally achieves smaller approximation gaps than uniform and random portfolios of the same final size.

Critical strengths

The main strengths are as follows:

  1. This paper has clear motivation and aim to addresses an important practical issue in multi-objective alignment. Training a separate policy for every preference can be expensive, while selecting a small set of policies without considering their reward profiles can lead to substantial redundancy. Constructing a compact portfolio that maintains good coverage of the preference space is therefore a practical and useful objective.

  2. The theoretical analysis of the approximation quality and portfolio size complements the empirical comparisons.

  3. The hybrid grid is a sensible fix for the boundary problem of uniform grids, and the certification idea behind the lazy search is simple and reusable.

Critical weaknesses

However, there are several obvious issues that authors should address:

  1. The empirical implementation does not clearly preserve the assumptions used in the theoretical results. There are several places where the experiments depart from what Theorem 3.3 and Lemma 3.6 require. In particular, the theoretical analysis relies on a bound involving Rmax⁡R_{\max}, but its empirical estimation appears problematic for the standardized HelpSteer rewards, which can be bounded. Estimating this quantity from a finite sample does not necessarily provide a valid upper bound. It also raises questions about whether the theoretical approximation guarantees hold in the actual experimental setting.

  2. The computational advantage over simple baselines appears to be limited when considering the cost of constructing the portfolio.

  3. The experiments do not fully establish the claimed coverage guarantees over the continuous preference space. The evaluation uses a finite set of test preferences, they cannot establish that the selected portfolio maintains good approximation quality across the full preference space, which is the central claim of the paper.

Questions for authors
  1. Can you compare PALM and the direct Uniform and Random baselines at matched total oracle-call budgets, rather than only at matched final portfolio sizes?

  2. How is Rmax⁡R_{\max} being estimated in the experiments?

  3. For HelpSteer, how is the multiplicative gap being computed at test weights when the oracle is negative or close to zero?

6 comments

Weakness 1

The empirical implementation does not clearly preserve the assumptions used in the theoretical results. There are several places where the experiments depart from what Theorem 3.3 and Lemma 3.6 require. In particular, the theoretical analysis relies on a bound involving Rmax, but its empirical estimation appears problematic for the standardized HelpSteer rewards, which can be bounded. Estimating this quantity from a finite sample does not necessarily provide a valid upper bound. It also raises questions about whether the theoretical approximation guarantees hold in the actual experimental setting.

Thank you for the comment. The estimate of Rmax⁡R_{\max} does not enter the reported gaps. All reported gaps use actual oracle values on held-out test weights. An error in R^max⁡\hat R_{\max} can therefore change how the portfolio is built, but it cannot bias the reported gaps. Furthermore, we agree that estimating Rmax⁡R_{\max} from finite samples does not necessarily provide a valid theoretical upper bound. However, empirical estimation of unknown global quantities is a recognized practical approach (e.g., Huang et al., 2023, Weng et al., 2018, for Lipschitz constants). We use such estimates to guide the practical implementation, rather than claim that they provide formal certificates. Importantly, PALM can also operate without knowing Rmax⁡R_{\max} or fmax⁡f_{\max}, since Tool 2 of Lemma 3.6 relies only on convexity. Indeed, our RLVR-GSM experiments already use Tool 2 alone. Furthermore, we extend our theoretical analysis to accommodate imperfect policy oracles and provide a formal statement and proof sketch below.

More broadly, the theoretical guarantees are established by our analysis under explicitly stated assumptions, while the experiments assess PALM's practical performance. That is their purpose. Empirical results are not intended to prove worst-case guarantees, nor do practical implementations necessarily need to satisfy every sufficient condition of the theoretical analysis. These are distinct and complementary contributions. As is common in optimization and machine learning, practical parameter choices need not satisfy all sufficient conditions for theoretical guarantees and may yield better empirical performance (e.g., step sizes in gradient descent). We will revise the text to separate the proved guarantees from the empirical gaps more clearly.

References

  • Huang et al. (2023). On the sample complexity of Lipschitz constant estimation. Transactions on Machine Learning Research (TMLR).
  • Weng et al. (2018). Evaluating the robustness of neural networks: An extreme value theory approach. ICLR.

Weakness 2

The computational advantage over simple baselines appears to be limited when considering the cost of constructing the portfolio.

We conducted additional experiments matching the number of oracle calls between PALM and the Uniform and Random baselines. The manuscript also includes the Uniform PALM ablation, which uses comparable oracle-call budgets with PALM. These results show that PALM generally outperforms the baselines under comparable training budgets, despite having substantially smaller final portfolio sizes. Please refer to our response to Question 1 below for details.

Weakness 3

The experiments do not fully establish the claimed coverage guarantees over the continuous preference space. The evaluation uses a finite set of test preferences, they cannot establish that the selected portfolio maintains good approximation quality across the full preference space, which is the central claim of the paper.

Thank you for the comment. Computing the exact worst-case gap requires optimizing a non-convex function over a continuous, multi-dimensional preference space. Each evaluation of optw\mathrm{opt}_w also requires a separate fine-tuning run. To the best of our knowledge, no tractable method evaluates this quantity exactly. Evaluating on a finite set of weights is the well-established approach (Zintgraf et al., 2015; Hayes et al., 2022; Alegre et al., 2023). Furthermore, to account for sampling variability, we report bootstrap means and standard deviations over 5,000 resamples of VV, providing a more robust assessment of empirical performance.

The sampled maximum also has a finite-sample guarantee. In Safety Alignment, Helpful Assistants and RLVR-GSM, VV is i.i.d. uniform on Δd\Delta^d. By Tempo et al. (1997), with probability at least 1−δ1-\delta,

Pr⁡w∼Unif(Δd)[gap(w)>max⁡v∈Vgap(v)]≤εwhenever∣V∣≥ln⁡(1/δ)ε.\Pr_{w \sim \mathrm{Unif}(\Delta^d)}\Big[\mathrm{gap}(w) > \max_{v \in V} \mathrm{gap}(v)\Big] \le \varepsilon \quad \text{whenever} \quad |V| \ge \frac{\ln(1/\delta)}{\varepsilon}.

Here gap(w)\mathrm{gap}(w) denotes the additive or the multiplicative gap of portfolio PP at weight ww, so max⁡v∈Vgap(v)\max_{v \in V}\mathrm{gap}(v) is the reported worst-case gap.

At δ=0.05\delta=0.05, this gives ε≈0.030\varepsilon\approx0.030 for ∣V∣=100|V|=100, ε≈0.015\varepsilon\approx0.015 for ∣V∣=200|V|=200, and ε≈0.15\varepsilon\approx0.15 for ∣V∣=20|V|=20. Thus, with 95% confidence, the gap exceeds the sampled maximum on at most an ε\varepsilon fraction of the preference space under the uniform measure.

References

  • Alegre et al. (2023). Sample-efficient multi-objective learning via generalized policy improvement prioritization. AAMAS (Conference).
  • Hayes et al. (2022). A practical guide to multi-objective reinforcement learning and planning. Autonomous Agents and Multi-Agent Systems (Journal).
  • Zintgraf et al. (2015). Quality assessment of MORL algorithms: A utility-based approach. Benelearn.
  • Tempo et al. (1997). Probabilistic robustness analysis: Explicit bounds for the minimum number of samples. Systems & Control Letters.

Question 1

Can you compare PALM and the direct Uniform and Random baselines at matched total oracle-call budgets, rather than only at matched final portfolio sizes?

We conducted additional experiments on Safety Alignment and Helpful Assistants, matching the number of oracle calls between PALM and the Uniform and Random baselines. We also include unpruned PALM, allowing a comparison at both equal oracle-call budgets and equal final portfolio sizes.

Safety Alignment

MethodOracle callsFinal sizeMult. gapAdd. gap
PALM (pruned) portfolio size = 1
PALM (pruned)710.4448 ± 0.01340.4386 ± 0.0215
PALM (unpruned)770.0154 ± 0.00320.0107 ± 0.0025
Uniform770.0101 ± 0.00450.0070 ± 0.0034
Random770.0871 ± 0.01150.0866 ± 0.0125
PALM (pruned) portfolio size = 2
PALM (pruned)720.0538 ± 0.01090.0533 ± 0.0120
PALM (unpruned)770.0004 ± 0.00030.0004 ± 0.0003
Uniform770.0101 ± 0.00450.0070 ± 0.0034
Random770.0871 ± 0.01150.0866 ± 0.0125
PALM (pruned) portfolio size = 3
PALM (pruned)530.0158 ± 0.00210.0110 ± 0.0018
PALM (unpruned)550.0158 ± 0.00210.0110 ± 0.0019
Uniform550.0324 ± 0.01190.0187 ± 0.0057
Random550.1039 ± 0.01000.1031 ± 0.0115
PALM (pruned) portfolio size = 4
PALM (pruned)840.0004 ± 0.00030.0004 ± 0.0003
PALM (unpruned)880.0004 ± 0.00030.0004 ± 0.0003
Uniform880.0109 ± 0.00800.0078 ± 0.0057
Random880.1851 ± 0.01130.1824 ± 0.0149

Helpful Assistants

MethodOracle callsFinal sizeMult. gapAdd. gap
PALM (pruned) portfolio size = 3
PALM (pruned)930.0353 ± 0.00730.0236 ± 0.0059
PALM (unpruned)990.0057 ± 0.00280.0038 ± 0.0020
Uniform990.0355 ± 0.01320.0242 ± 0.0093
Random990.2642 ± 0.01860.2453 ± 0.0254
PALM (pruned) portfolio size = 4
PALM (pruned)840.0344 ± 0.00870.0233 ± 0.0064
PALM (unpruned)880.0156 ± 0.00360.0089 ± 0.0018
Uniform880.0355 ± 0.01320.0242 ± 0.0093
Random880.2855 ± 0.01880.2678 ± 0.0258
PALM (pruned) portfolio size = 5
PALM (pruned)1450.0002 ± 0.00020.0002 ± 0.0001
PALM (unpruned)14140.0002 ± 0.00020.0002 ± 0.0001
Uniform14140.0088 ± 0.00380.0053 ± 0.0021
Random14140.2163 ± 0.01900.2021 ± 0.0235
PALM (pruned) portfolio size = 6
PALM (pruned)1460.0000 ± 0.00000.0000 ± 0.0000
PALM (unpruned)14140.0000 ± 0.00000.0000 ± 0.0000
Uniform14140.0088 ± 0.00380.0053 ± 0.0021
Random14140.2163 ± 0.01900.2021 ± 0.0235

Unpruned PALM outperforms both baselines in 7 of the 8 configurations at matched oracle-call budgets and portfolio sizes. Moreover, pruned PALM outperforms both baselines in 6 of the 8 configurations despite deploying substantially fewer policies. Overall, these results demonstrate PALM's strong approximation quality under equal training budgets, with further deployment savings through pruning.

Furthermore, we would like to note that the manuscript already includes the Uniform PALM ablation (Figure 4) across all four datasets. This ablation replaces PALM's structured grid with a uniform grid of the same size, while retaining the same lazy-search and pruning procedures and matching the final portfolio size. PALM generally outperforms this ablation, even though the oracle-call budgets are comparable and generally slightly larger for Uniform PALM (See the Appendix for exact oracle numbers). These results provide further evidence of PALM's effectiveness under comparable training and deployment budgets.

Question 2

How is Rmax being estimated in the experiments?

For all experiments except HelpSteer, the reward functions are normalized to [0,1][0,1], so Rmax⁡≤dR_{\max}\leq d provides a valid upper bound. For HelpSteer, we estimate Rmax⁡R_{\max} using 2,000 calibration responses generated by the base policy (four responses for each of 500 training prompts), as described in Appendix D.6.

Question 3

For HelpSteer, how is the multiplicative gap being computed at test weights when the oracle is negative or close to zero?

All empirical oracle values at the HelpSteer test preferences were strictly positive; the smallest was 0.09508 in our standardized reward units, in both the four-dimensional and nineteen-dimensional evaluations. Thus, we compute the multiplicative gap following the original definition, without denominator flooring.

Reviewer_oSDZOpenReview ↗
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Paper summary

This work proposes PALM, a framework for constructing compact policy portfolios for multi-objective LLM alignment. It combines hybrid grid construction, lazy search, and portfolio pruning to select a small set of policies that approximately covers diverse reward weightings. The paper provides theoretical approximation guarantees and evaluates the approach across multiple alignment tasks and optimization methods.

Critical strengths
  1. The work addresses a relevant practical challenge in multi-objective LLM alignment: selecting a compact set of policies to accommodate diverse preference weightings while reducing training and deployment overhead.

  2. PALM presents a structured framework combining hybrid grid construction, lazy search, and portfolio pruning.

  3. The experiments cover multiple alignment tasks and policy optimization methods, including full fine-tuning, LoRA, and decoding-time alignment. The results generally show improved approximation quality over uniform and random selection baselines at matched portfolio sizes.

Critical weaknesses
  1. The theoretical analysis contains a potentially critical flaw. The proof of Lemma B.4 implicitly assumes non-negative reward components when bounding the difference between scalarized objectives, although the formulation permits signed rewards. This assumption is particularly problematic because the HelpSteer experiments use mean-standardized rewards that can be negative. Consequently, the stated transfer lemma does not hold in general, potentially undermining the optimality certificates and the main approximation guarantee.

  2. The optimality certificates rely on valid upper bounds of the optimal objective, whereas practical GRPO fine-tuning provides neither exact optima nor quantified approximation errors. Substituting observed policy values may invalidate these bounds, particularly those based on convexity. The paper does not establish how the certificates remain valid under imperfect optimization.

  3. The main guarantee requires specific relationships between the lazy-search and pruning tolerances, such as μ1≤μ2\mu_1 \leq \mu_2 and α1≤α2\alpha_1 \leq \alpha_2. However, several experimental configurations, particularly on HelpSteer, violate these conditions. Consequently, the theoretical guarantees do not directly apply to the reported portfolios, and no controlled evaluation under theorem-compliant settings is provided.

  4. Coverage is evaluated on only 20–200 sampled preference vectors per setting, rather than the full continuous preference space. Moreover, policy rewards are estimated from limited generations (e.g., 100 prompts for HelpSteer), while theoretical reward bounds are replaced with empirical estimates. The resulting approximation gaps therefore provide empirical evidence of coverage but cannot substantiate the claimed guarantees.

  5. The general portfolio-size bound grows exponentially with the number of reward dimensions, while the sparse-preference guarantee does not directly justify the dense 19-dimensional evaluation using policies constructed from only four selected dimensions. Furthermore, PALM requires more oracle calls than size-matched baselines, making its practical efficiency advantage less clear without comparisons under equal training budgets.

Questions for authors

Pls see the weakness

7 comments

Weakness 1

The theoretical analysis contains a potentially critical flaw. The proof of Lemma B.4 implicitly assumes non-negative reward components when bounding the difference between scalarized objectives, although the formulation permits signed rewards. This assumption is particularly problematic because the HelpSteer experiments use mean-standardized rewards that can be negative. Consequently, the stated transfer lemma does not hold in general, potentially undermining the optimality certificates and the main approximation guarantee.

We thank the reviewer for pointing this out. The main theorem on portfolio size holds whether or not we assume signed rewards, with slightly different bounds on the additive error δ\delta (the portfolio size and multiplicative error ε\varepsilon do not change). Specifically, the bound changes from δ≤3dαRmax⁡+2μfmax⁡\delta \le 3 d \alpha R_{\max} + 2 \mu f_{\max} for nonnegative rewards (current draft) to δ≤3dαRmax⁡+2μRmax⁡\delta \le 3 d \alpha R_{\max} + 2 \mu R_{\max} for signed rewards. These bounds use essentially the same proof (a sketch is presented at the end of our response for completeness). We will make this distinction between signed and nonnegative rewards explicit in all results.

We note that our algorithm PALM itself does not change irrespective of whether the rewards are signed or not.

Weakness 2

The optimality certificates rely on valid upper bounds of the optimal objective, whereas practical GRPO fine-tuning provides neither exact optima nor quantified approximation errors. Substituting observed policy values may invalidate these bounds, particularly those based on convexity. The paper does not establish how the certificates remain valid under imperfect optimization.

We provide a new theoretical analysis that extends our guarantees to imperfect policy oracles. In this extension, Tools 1 and 2 apply unchanged, while Tool 3 requires knowledge of the oracle approximation error. When this information is unavailable, Tool 3 can be omitted without affecting the theorem's guarantee. The oracle error enters the resulting approximation bounds. We will include the full imperfect-oracle analysis in the revision, and we give a proof sketch below.

Furthermore, our experiments using only Tool 2 produce the same results, indicating that the empirical estimates used by the other tools do not drive our findings. The final evaluation of the portfolio does not require these certification tools, so the empirical results we report remain valid as empirical measures of portfolio quality.

Weakness 3

The main guarantee requires specific relationships between the lazy-search and pruning tolerances, such as (μ1≤μ2)(\mu_1 \leq \mu_2) and (α1≤α2)(\alpha_1 \leq \alpha_2). However, several experimental configurations, particularly on HelpSteer, violate these conditions.

To address the reviewer's concern, we conducted additional controlled experiments on HelpSteer, retaining the original grids, pre-pruning portfolios, and evaluation protocol, while changing only the pruning tolerances to satisfy μ1≤μ2\mu_1 \leq \mu_2 and α1≤α2\alpha_1 \leq \alpha_2.

Restricting the pruning-parameter search to satisfy the two tolerance inequalities recovers exactly our published size-2 and size-3 portfolios across all three seeds, preserving their reported results. Furthermore, simply setting μ2=μ1\mu_2=\mu_1 and α2=α1\alpha_2=\alpha_1 produces compact portfolios with competitive approximation gaps, as shown below.

HelpSteer: Results with admissible pruning parameters.

EvaluationParametersFinal sizesWorst mult. gapWorst add. gap
4D(.25,.12; .15,.04; .15,.04)(4,3,3)0.1183 ± 0.01000.1362 ± 0.0101
4D(.20,.09; .12,.03; .12,.03)(3,3,2)0.1083 ± 0.00950.1331 ± 0.0142
19D(.25,.12; .15,.04; .15,.04)(4,3,3)0.1289 ± 0.01110.1369 ± 0.0091
19D(.20,.09; .12,.03; .12,.03)(3,3,2)0.1521 ± 0.01540.1374 ± 0.0104

Parameters are (μ0,α0\mu_0,\alpha_0; μ1,α1\mu_1,\alpha_1; μ2,α2\mu_2,\alpha_2). Final sizes are reported across three seeds.

We emphasize, however, that these parameter conditions are sufficient for the theoretical guarantee, rather than necessary for running PALM. As is common in optimization and machine learning, theoretically sufficient parameter choices can be conservative, and independently tuning parameters often yields better empirical performance (e.g., step sizes in gradient descent). Our theoretical result establishes that PALM can construct portfolios with guaranteed approximation quality under the prescribed conditions, while our main experiments evaluate its practical performance with tuned parameters. These are complementary rather than conflicting results. We will clarify this distinction in the revised manuscript.

Weakness 4

Coverage is evaluated on only sampled preference vectors, rather than the full continuous preference space. Moreover, policy rewards are estimated from limited generations while theoretical reward bounds are replaced with empirical estimates. The resulting approximation gaps therefore provide empirical evidence of coverage but cannot substantiate the claimed guarantees.

We agree that the approximation gaps are just empirical evidence of coverage. That is their purpose. The guarantees come from the proofs, not from the experiments. No finite experiment can substantiate a bound over the whole simplex, and we do not use the experiments to do so. Instead, the experiments complement the theoretical analysis by showing how well PALM covers the preference space in practice, where theoretical assumptions may not hold exactly. We address each estimation step below.

Finite test weights. Computing the exact worst-case gap requires optimizing a non-convex function over a continuous, multi-dimensional preference space. Each evaluation of optw\mathrm{opt}_w also requires a separate fine-tuning run. To the best of our knowledge, no tractable method evaluates this quantity exactly. Evaluating on a finite set of weights is the well-established approach (Zintgraf et al., 2015; Hayes et al., 2022; Alegre et al., 2023). Furthermore, to account for sampling variability, we report bootstrap means and standard deviations over 5,000 resamples of VV, providing a more robust assessment of empirical performance.

The sampled maximum also has a finite-sample guarantee. In Safety Alignment, Helpful Assistants and RLVR-GSM, VV is i.i.d. uniform on Δd\Delta^d. By Tempo et al. (1997), with probability at least 1−δ1-\delta,

Pr⁡w∼Unif(Δd)[gap(w)>max⁡v∈Vgap(v)]≤εwhenever∣V∣≥ln⁡(1/δ)ε.\Pr_{w \sim \mathrm{Unif}(\Delta^d)}\Big[\mathrm{gap}(w) > \max_{v \in V} \mathrm{gap}(v)\Big] \le \varepsilon \quad \text{whenever} \quad |V| \ge \frac{\ln(1/\delta)}{\varepsilon}.

Here gap(w)\mathrm{gap}(w) denotes the additive or the multiplicative gap of portfolio PP at weight ww, so max⁡v∈Vgap(v)\max_{v \in V}\mathrm{gap}(v) is the reported worst-case gap.

At δ=0.05\delta=0.05, this gives ε≈0.030\varepsilon\approx0.030 for ∣V∣=100|V|=100, ε≈0.015\varepsilon\approx0.015 for ∣V∣=200|V|=200, and ε≈0.15\varepsilon\approx0.15 for ∣V∣=20|V|=20. Thus, with 95% confidence, the gap exceeds the sampled maximum on at most an ε\varepsilon fraction of the preference space under the uniform measure.

Finite generations. Jw(π)J_w(\pi) is an expectation over prompts and responses. Every alignment evaluation estimates it by Monte Carlo sampling, as in prior multi-objective alignment work (Shi et al., 2024; Shen et al., 2025). In HelpSteer, each policy's reward vector averages 400 responses (100 prompts, 4 responses each). All policies use the same prompts, decoding settings and seed, so the comparisons between portfolios are paired.

Empirical Rmax⁡R_{\max}. The estimate of Rmax⁡R_{\max} does not enter the reported gaps. All reported gaps use actual oracle values on held-out test weights. An error in R^max⁡\hat R_{\max} can therefore change how the portfolio is built, but it cannot bias the reported gaps. Furthermore, we agree that estimating Rmax⁡R_{\max} from finite samples does not necessarily provide a valid theoretical upper bound. However, empirical estimation of unknown global quantities is a recognized practical approach (e.g., Huang et al., 2023, Weng et al., 2018, for Lipschitz constants). We use such estimates to guide the practical implementation, rather than claim that they provide formal certificates. Importantly, PALM can also operate without knowing Rmax⁡R_{\max} or fmax⁡f_{\max} using only Tool 2. Indeed, our RLVR-GSM experiments already use Tool 2 alone.

References

  • Alegre et al. (2023). Sample-efficient multi-objective learning via generalized policy improvement prioritization. AAMAS (Conference).
  • Hayes et al. (2022). A practical guide to multi-objective reinforcement learning and planning. Autonomous Agents and Multi-Agent Systems (Journal).
  • Huang et al. (2023). On the sample complexity of Lipschitz constant estimation. Transactions on Machine Learning Research (TMLR).
  • Shen et al. (2025). Simultaneous multi-objective alignment across verifiable and non-verifiable rewards. arXiv.
  • Shi et al. (2024). Decoding-time language model alignment with multiple objectives. NeurIPS.
  • Tempo et al. (1997). Probabilistic robustness analysis: Explicit bounds for the minimum number of samples. Systems & Control Letters.
  • Weng et al. (2018). Evaluating the robustness of neural networks: An extreme value theory approach. ICLR.
  • Zintgraf et al. (2015). Quality assessment of MORL algorithms: A utility-based approach. Benelearn.

Weakness 5

The general portfolio-size bound grows exponentially with the number of reward dimensions, while the sparse-preference guarantee does not directly justify the dense 19-dimensional evaluation using policies constructed from only four selected dimensions.

We agree that the sparse-preference theorem does not directly guarantee coverage of arbitrary dense preferences. However, our 19-dimensional HelpSteer experiment demonstrates a stronger empirical result beyond the theoretical guarantee. We construct PALM using only four representative reward dimensions, but evaluate the resulting portfolio on test weights over the full 19-dimensional preference space. The strong performance suggests that PALM can exploit correlations among reward dimensions to achieve effective coverage even for dense preferences.

This also admits a natural theoretical interpretation. Suppose that for every w∈Δ19w\in\Delta_{19}, there exists a preference w~\tilde w supported on the selected four dimensions such that sup⁡π∈Π∣Jw(π)−Jw~(π)∣≤η\sup_{\pi\in\Pi}|J_w(\pi)-J_{\tilde w}(\pi)|\leq\eta. Then, an (ϵ,δ)(\epsilon,\delta)-portfolio over the selected four dimensions is also an (ϵ,δ+(2−ϵ)η)(\epsilon,\delta+(2-\epsilon)\eta)-portfolio over the full 19-dimensional space. Our experiments provide empirical evidence for this low-dimensional structure, although we do not formally bound η\eta. We will clarify this distinction in the revised manuscript.

Reviewer_KWXsOpenReview ↗
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Paper summary

The motivation of this paper is that different users exhibit different preferences in trading off between different reward dimensions. However, it is not feasible to train and deploy a per-user policy model that optimizes for their specific weighting. So the paper presents a method called PALM for selecting a small set of LLM policies (could be different tuned models, a single steerable model controlled at inference time, etc) that considers trade-offs between several reward functions (e.g. helpfulness, harmlessness, brevity) which are linearly combined through a weighted sum. This method optimizes policy selection such that for each weighting, there is a policy in the set that is nearly as good as one trained specifically for it. The approach has three steps: 1) build a grid of candidate weightings, with spacing that gets proportionally finer as a weight gets smaller and switches to fixed spacing at very small weights, 2) determine if a grid point is already covered by an existing policy and if not, then train / select a policy that covers this point, and 3) a final step that removes redundant policies using a greedy set-cover procedure. The paper proves an upper bound on the number of policies needed so that every weighting has a policy within a given tolerance of the optimal one. Empirically, they run experiments on four tasks (RLVR-GSM, Safety Alignment, Helpful Assistants, and HelpSteer), using 3 types of policies - full fine-tuning, LoRA, and decoding-time alignment. They compare to policy sets of the same size built from evenly spaced or randomly sampled weights as baselines and show that the PALM constructed policy set generally has a smaller worst-case gap from the best possible policy. The primary finding of the paper is that choosing which weightings to train adaptively, based on the policies already trained, covers the range of reward trade-offs with fewer policies than spacing the weights evenly or randomly.

Critical strengths

Overall, the paper addresses a practical question in multi-objective alignment, which weight vectors to train and deploy, with a simple formulation and theoretical guarantees. Key strengths include: 1, The approach is agnostic to the policy method itself. The paper demonstrates that the approach can be applied to fine-tuning (RLVR-GSM), LoRA (HelpSteer), and decoding-time (Safety Alignment and Helpful Assistants) methods and generally achieves smaller worst-case gaps than uniform and random portfolios with the same-size policy set (training cost may be higher, though the Appendix experiments do report a Uniform+PALM ablation with similar training cost and mostly similar conclusions). 2. The paper provides theoretical guarantees that, under its assumptions, the PALM portfolio contains a nearly-best model for every possible weighting, within a percentage and a small fixed amount, along with an explicit trade-off between portfolio size and quality / approximation error. 3. In general, the approach design decisions are clearly outlined and well-motivated (e.g. the grid structure, which is motivated by the poor coverage of uniform grids near the edges).

Critical weaknesses
  1. The main paper content is missing some baselines: 1) A technique with equivalent training budget - even with uniform / random approaches the training budget can be fixed to some T and the best K can be selected using the same validation procedure. The Uniform+PALM ablation partly addresses this but is in the Appendix. 2) A standard multi-objective optimization technique - Optimistic linear support and similar linear support methods (e.g. Roijers et al., 2015), which are closely related to the convex coverage set work the paper cites, build a policy set by repeatedly training a policy at the corner weight where an optimistic, convexity-based upper bound shows the largest possible improvement over the current policy set. The paper should construct such a baseline for the scenarios evaluated here, with the same policy oracles and evaluation.
  2. Using the portfolio for personalization requires knowing which policy to route each user to, which in turn requires the user’s reward weights. In practice, users are unlikely to provide explicit weights, and the paper does not discuss how they would be obtained or how a user would be matched to a policy at inference time. This limitation is not specific to the approach in this paper, but it would be useful to describe a matching procedure or how errors in the estimated weights affect the quality each user receives.
  3. The end motivation / goal of user personalization is not actually evaluated, since the experiments only measure coverage in reward space over randomly sampled weights. For example, the authors could estimate each user’s weights from a few of their pairwise preference judgments (e.g. using PRISM or simulated users with known weights), assign each user the best-matching policy from the portfolio, and measure how often users prefer its responses over a single default policy or a same-size uniform portfolio.
Questions for authors
  1. Suggestion: The paper’s motivation focuses on per-user personalization, which requires knowing each user’s weights. It might be more compelling to frame PALM around selecting candidate weightings during model development or defining a small set of presets, and to evaluate it in one of these settings.
  2. Suggestion: The portfolios are constructed over only 2-4 reward dimensions (although the HelpSteer portfolio is also evaluated on all 19 dimensions). Since the worst-case portfolio size grows exponentially with the number of rewards, consider constructing portfolios directly over more reward dimensions to show how the number of policies and training runs scales in practice.
5 comments

Weakness 1

The main paper content is missing some baselines: 1) A technique with equivalent training budget. even with uniform / random approaches the training budget can be fixed to some T and the best K can be selected using the same validation procedure. The Uniform+PALM ablation partly addresses this but is in the Appendix. 2) A standard multi-objective optimization technique - Optimistic linear support and similar linear support methods (e.g. Roijers et al., 2015), which are closely related to the convex coverage set work the paper cites. The paper should construct such a baseline for the scenarios evaluated here, with the same policy oracles and evaluation.

(1) Thank you for the suggestion. First of all, we would like to respectfully note that the manuscript already includes the Uniform PALM ablation (Figure 4) across all four datasets, which is not in the Appendix but included as part of our main experimental results. This ablation replaces PALM's structured grid with a uniform grid of the same size, while retaining the same lazy-search and pruning procedures and matching the final portfolio size. PALM generally outperforms this ablation, even though the oracle-call budgets are comparable and generally slightly larger for Uniform PALM. These results already provide evidence of PALM's effectiveness under comparable training and deployment budgets.

We conducted additional experiments on Safety Alignment and Helpful Assistants, matching the number of oracle calls between PALM and the Uniform and Random baselines. We also include unpruned PALM, allowing a comparison at both equal oracle-call budgets and equal final portfolio sizes.

Safety Alignment

MethodOracle callsFinal sizeMult. gapAdd. gap
PALM (pruned) portfolio size = 1
PALM (pruned)710.4448 ± 0.01340.4386 ± 0.0215
PALM (unpruned)770.0154 ± 0.00320.0107 ± 0.0025
Uniform770.0101 ± 0.00450.0070 ± 0.0034
Random770.0871 ± 0.01150.0866 ± 0.0125
PALM (pruned) portfolio size = 2
PALM (pruned)720.0538 ± 0.01090.0533 ± 0.0120
PALM (unpruned)770.0004 ± 0.00030.0004 ± 0.0003
Uniform770.0101 ± 0.00450.0070 ± 0.0034
Random770.0871 ± 0.01150.0866 ± 0.0125
PALM (pruned) portfolio size = 3
PALM (pruned)530.0158 ± 0.00210.0110 ± 0.0018
PALM (unpruned)550.0158 ± 0.00210.0110 ± 0.0019
Uniform550.0324 ± 0.01190.0187 ± 0.0057
Random550.1039 ± 0.01000.1031 ± 0.0115
PALM (pruned) portfolio size = 4
PALM (pruned)840.0004 ± 0.00030.0004 ± 0.0003
PALM (unpruned)880.0004 ± 0.00030.0004 ± 0.0003
Uniform880.0109 ± 0.00800.0078 ± 0.0057
Random880.1851 ± 0.01130.1824 ± 0.0149

Helpful Assistants

MethodOracle callsFinal sizeMult. gapAdd. gap
PALM (pruned) portfolio size = 3
PALM (pruned)930.0353 ± 0.00730.0236 ± 0.0059
PALM (unpruned)990.0057 ± 0.00280.0038 ± 0.0020
Uniform990.0355 ± 0.01320.0242 ± 0.0093
Random990.2642 ± 0.01860.2453 ± 0.0254
PALM (pruned) portfolio size = 4
PALM (pruned)840.0344 ± 0.00870.0233 ± 0.0064
PALM (unpruned)880.0156 ± 0.00360.0089 ± 0.0018
Uniform880.0355 ± 0.01320.0242 ± 0.0093
Random880.2855 ± 0.01880.2678 ± 0.0258
PALM (pruned) portfolio size = 5
PALM (pruned)1450.0002 ± 0.00020.0002 ± 0.0001
PALM (unpruned)14140.0002 ± 0.00020.0002 ± 0.0001
Uniform14140.0088 ± 0.00380.0053 ± 0.0021
Random14140.2163 ± 0.01900.2021 ± 0.0235
PALM (pruned) portfolio size = 6
PALM (pruned)1460.0000 ± 0.00000.0000 ± 0.0000
PALM (unpruned)14140.0000 ± 0.00000.0000 ± 0.0000
Uniform14140.0088 ± 0.00380.0053 ± 0.0021
Random14140.2163 ± 0.01900.2021 ± 0.0235

Unpruned PALM outperforms both baselines in 7 of the 8 configurations at matched oracle-call budgets and portfolio sizes. Moreover, pruned PALM outperforms both baselines in 6 of the 8 configurations despite deploying substantially fewer policies. Overall, these results demonstrate PALM's strong approximation quality under equal training budgets, with further deployment savings through pruning.

(2) We implemented OLS on Safety Alignment using the same policy oracles and evaluation protocols as PALM. The table compares performance under matched oracle-call budgets, reporting worst-case multiplicative and additive gaps (lower is better).

Safety Alignment

MethodOracle callsFinal sizeMult. gapAdd. gap
PALM (pruned) portfolio size = 1
PALM (pruned)710.4448 ± 0.01340.4386 ± 0.0215
PALM (unpruned)770.0154 ± 0.00320.0107 ± 0.0025
OLS770.0159 ± 0.00180.0111 ± 0.0017
PALM (pruned) portfolio size = 2
PALM (pruned)720.0538 ± 0.01090.0533 ± 0.0120
PALM (unpruned)770.0004 ± 0.00030.0004 ± 0.0003
OLS770.0159 ± 0.00180.0111 ± 0.0017
PALM (pruned) portfolio size = 3
PALM (pruned)530.0158 ± 0.00210.0110 ± 0.0018
PALM (unpruned)550.0158 ± 0.00210.0110 ± 0.0019
OLS550.0322 ± 0.01230.0187 ± 0.0058
PALM (pruned) portfolio size = 4
PALM (pruned)840.0004 ± 0.00030.0004 ± 0.0003
PALM (unpruned)880.0004 ± 0.00030.0004 ± 0.0003
OLS880.0159 ± 0.00180.0111 ± 0.0017

Unpruned PALM outperforms OLS in all four configurations at matched oracle-call budgets and portfolio sizes. Moreover, pruned PALM outperforms OLS at portfolio sizes 3 and 4, despite deploying substantially fewer policies (3 vs. 5 and 4 vs. 8, respectively). OLS performs better only when retaining substantially larger portfolios than pruned PALM (7 vs. 1 or 2 policies). These results further demonstrate PALM's effectiveness in achieving strong approximation quality with compact portfolios.

We also emphasize that portfolio costs extend beyond training to evaluating, maintaining, and deploying policies. Thus, compactness is itself an important measure of cost-efficiency and a key advantage of PALM, and our original experiments explicitly demonstrate PALM's strength in this regard.

Weakness 2

Using the portfolio for personalization requires knowing which policy to route each user to, which in turn requires the user’s reward weights. In practice, users are unlikely to provide explicit weights, and the paper does not discuss how they would be obtained or how a user would be matched to a policy at inference time. This limitation is not specific to the approach in this paper, but it would be useful to describe a matching procedure or how errors in the estimated weights affect the quality each user receives.

We thank the reviewer for this thoughtful comment. We would like to clarify that users do not necessarily need to know or explicitly specify their reward weights to benefit from PALM. In the simplest setting, users can examine all responses from the portfolio and select the one they prefer. Regardless of a user's latent (unobservable) preference weights, PALM guarantees that the portfolio contains a near-optimal policy for those weights.

As the reviewer notes, PALM can also be combined with formal matching (preference elicitation) algorithm. One potential way is to treat each LLM in the portfolio as an arm in a dueling-bandit problem and use pairwise comparisons to identify a preferred policy. However, preference elicitation is a separate problem. Our main focus is to construct a compact yet representative portfolio, and it can be combined with various preference elicitation algorithms. Moreover, as discussed in the Introduction, PALM's potential applications extend beyond personalization. For example, reward-weight exploration during model development (the second use case in the Introduction) does not require preference elicitation or user-to-policy matching. We will clarify these possible deployment approaches in the revised manuscript. Thank you again for this comment!

Weakness 3

The end motivation / goal of user personalization is not actually evaluated, since the experiments only measure coverage in reward space over randomly sampled weights. For example, the authors could estimate each user’s weights from a few of their pairwise preference judgments (e.g. using PRISM or simulated users with known weights), assign each user the best-matching policy from the portfolio, and measure how often users prefer its responses over a single default policy or a same-size uniform portfolio.

To evaluate personalization more directly, we conducted additional experiments simulating 10,000 users under three preference distributions: w∼Dirichlet(α,…,α)w\sim\mathrm{Dirichlet}(\alpha,\ldots,\alpha) with α∈{0.2,1,5}\alpha\in\{0.2,1,5\}, representing specialized, uniform, and balanced preferences respectively. We use the original PALM and same-size Uniform portfolios from the paper.

Each user is assigned the policy maximizing their weighted reward. To simulate imperfect preference elicitation, we add Gaussian noise with standard deviation σ∈{0,0.05,0.10,0.20}\sigma\in\{0,0.05,0.10,0.20\} to their weights and project them onto the simplex. Policy assignment uses these noisy weights, while the comparison between PALM and Uniform uses the user's true weights. Ties are split equally between the two methods.

The tables report PALM's simulated-user win rate (%) against Uniform, defined as the percentage of users for whom PALM's assigned policy achieves a higher reward under their true preferences, with ties split equally. Values are reported as mean ± standard error.

Helpful Assistants

Dirichlet α\alphaNoise σ\sigmaSize 3Size 4Size 5Size 6
0.2 (specialized)099.12 ± 0.0992.24 ± 0.2799.50 ± 0.0790.54 ± 0.30
0.0599.06 ± 0.1092.33 ± 0.2798.98 ± 0.1089.68 ± 0.31
0.1098.89 ± 0.1192.04 ± 0.2798.07 ± 0.1488.88 ± 0.32
0.2097.41 ± 0.1690.75 ± 0.2995.64 ± 0.2087.40 ± 0.33
1 (uniform)099.07 ± 0.1084.03 ± 0.3799.79 ± 0.0581.98 ± 0.38
0.0598.32 ± 0.1383.85 ± 0.3797.72 ± 0.1579.69 ± 0.40
0.1097.65 ± 0.1583.33 ± 0.3895.25 ± 0.2178.51 ± 0.41
0.2095.00 ± 0.2279.96 ± 0.4090.36 ± 0.2976.11 ± 0.43
5 (balanced)099.72 ± 0.0590.59 ± 0.29100.00 ± 0.0093.26 ± 0.25
0.0598.39 ± 0.1289.17 ± 0.3195.13 ± 0.2189.28 ± 0.31
0.1097.12 ± 0.1786.73 ± 0.3490.22 ± 0.3085.75 ± 0.35
0.2093.00 ± 0.2679.36 ± 0.4183.62 ± 0.3879.56 ± 0.40

HelpSteer

Dirichlet α\alphaNoise σ\sigmaSize 2Size 3Size 4Size 5
0.2 (specialized)099.35 ± 0.0680.01 ± 0.2966.92 ± 0.2869.73 ± 0.31
0.0599.00 ± 0.0878.89 ± 0.2965.48 ± 0.2868.47 ± 0.32
0.1098.30 ± 0.1077.73 ± 0.2964.31 ± 0.2867.21 ± 0.33
0.2096.45 ± 0.1575.44 ± 0.3162.50 ± 0.2965.30 ± 0.34
1 (uniform)099.93 ± 0.0182.66 ± 0.2670.77 ± 0.2683.96 ± 0.22
0.0599.65 ± 0.0480.35 ± 0.2667.36 ± 0.2782.06 ± 0.24
0.1099.12 ± 0.0778.30 ± 0.2865.04 ± 0.2779.80 ± 0.25
0.2098.00 ± 0.1175.41 ± 0.2962.81 ± 0.2776.28 ± 0.26
5 (balanced)0100.00 ± 0.0091.67 ± 0.1686.51 ± 0.1993.95 ± 0.12
0.05100.00 ± 0.0088.46 ± 0.1881.22 ± 0.2292.57 ± 0.13
0.1099.91 ± 0.0285.41 ± 0.2077.18 ± 0.2390.42 ± 0.15
0.2098.70 ± 0.0881.16 ± 0.2371.80 ± 0.2385.78 ± 0.18

PALM achieves higher simulated-user win rates in all tested configurations, across different preference distributions and portfolio sizes. Importantly, the advantage remains substantial even with noisy preference estimates (σ=0.20\sigma=0.20), demonstrating that PALM's improved reward-space coverage translates into better personalized policy assignments and remains robust to preference uncertainty.

Further, we would like to respectively note that as mentioned in our response to Weakness 2, PALM's potential applications extend beyond personalization. For example, reward-weight exploration during model development (the second use case in the Introduction) does not require preference elicitation or user-to-policy matching. We believe that approximation quality is the most general evaluation metric, as it is meaningful across all these applications.

Comments on the paper

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Summary of Responses

Summary of Responses

We thank all reviewers for their comments and suggestions. We summarize our theoretical clarifications and additional experiments below.

(1) Comparisons under equal oracle-call budgets. We conducted new equal-budget comparisons against Uniform and Random baselines. PALM generally outperforms these baselines even with substantially fewer deployed policies. Furthermore, the original manuscript already includes the Uniform PALM ablation (Figure 4), which compares PALM against a uniform-grid at matched deployment sizes and comparable oracle-call budgets, further demonstrating PALM's advantage. Beyond these comparisons, we emphasize that portfolio costs extend beyond training to evaluating, maintaining, and deploying policies. Compactness is therefore itself an important measure of cost-efficiency, and our original experiments explicitly demonstrate PALM's strength in this regard.

(2) Additional empirical evaluations. We conducted further experiments to evaluate PALM's effectiveness in personalization and higher-dimensional settings. First, we simulated 10,000 users under varying preference distributions and estimation noise. PALM achieved higher simulated-user win rates than same-size Uniform portfolios in every configuration, meaning users more often preferred the policies assigned by PALM, even under substantial noise. Second, beyond our existing HelpSteer evaluation over the full 19-dimensional preference space, we directly ran PALM on synthetic MDPs with 5–7 negatively correlated reward dimensions, deliberately designed to make it difficult to exploit reward correlations and cover the preference space. Even in this challenging setting, PALM achieved strong approximation quality with only 10 policies, far below the conservative worst-case theoretical size bounds.

(3) Theoretical concerns. We thank the reviewers for their careful reading. We address their concerns below:

  • Signed vs. nonnegative rewards: the results in our draft assume nonnegative rewards. However, the same proof holds for signed rewards with a mild adjustment in the theorem's analysis and its guarantee. We describe this formally and present a proof sketch in individual responses, and will make this distinction clear in the revision.
  • Approximate vs. perfect oracles: As already noted in the manuscript, our theoretical guarantees extend to approximate policy oracles. We further clarify this extension for the certification tools, with a formal statement and proof sketch in individual responses. Importantly, our analysis shows that PALM can accommodate imperfect optimization without requiring prior knowledge of the oracle's approximation error for the certification procedures used in our experiments. We will make this explicit in the revised manuscript.

(4) Theoretical guarantees vs. empirical implementation. Several comments concern differences between the theoretical assumptions and practical experimental settings. To address these concerns, we provide new finite-sample guarantees for the sampled evaluation and additional experiments using theorem-admissible pruning parameters on HelpSteer, which recover several of our originally reported portfolios. More broadly, however, we emphasize that theoretical guarantees are established under explicitly stated assumptions, while experiments assess how well PALM performs in practice, where these assumptions may not hold exactly. Such differences between theoretical assumptions and practical implementations are pervasive throughout optimization and machine learning, rather than a limitation specific to our work. Theoretically sufficient conditions can be conservative, and practical implementations often rely on empirical estimates (e.g., Huang et al., 2023; Weng et al., 2018, for Lipschitz constants) or tuned parameters (e.g., step sizes in gradient descent). Likewise, evaluating approximation quality over sampled preferences is a well-established practice in multi-objective learning (Zintgraf et al., 2015; Hayes et al., 2022; Alegre et al., 2023), since exact worst-case evaluation over the continuous preference space is intractable. The theoretical and empirical results thus serve complementary purposes, rather than being in conflict.

References

  • Huang et al. (2023). On the sample complexity of Lipschitz constant estimation. Transactions on Machine Learning Research (TMLR).
  • Weng et al. (2018). Evaluating the robustness of neural networks: An extreme value theory approach. ICLR.
  • Alegre et al. (2023). Sample-efficient multi-objective learning via generalized policy improvement prioritization. AAMAS (Conference).
  • Hayes et al. (2022). A practical guide to multi-objective reinforcement learning and planning. Autonomous Agents and Multi-Agent Systems (Journal).
  • Zintgraf et al. (2015). Quality assessment of MORL algorithms: A utility-based approach. Benelearn.

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