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Under review as a conference paper at ICLR 2027

Capabilities Ain't All You Need: Measuring Propensities in AI

Abstract

AI evaluation has primarily focused on measuring capabilities, with formal approaches inspired from Item Response Theory (IRT) being increasingly applied. Yet propensities — the tendencies of models to exhibit particular behaviours — play a central role in determining both performance and safety outcomes. However, traditional IRT describes a model's success on a task as a monotonic function of model capabilities and task demands, an approach unsuited to propensities, where both excess and deficiency can be problematic. Here, we introduce the first formal framework for measuring AI propensities by using a bilogistic formulation for model success, which attributes high success probability when the model's propensity is within an "ideal band". Further, we estimate the limits of the ideal band using LLMs equipped with newly developed task-agnostic rubrics. Applying our framework to six families of LLM models whose propensities are incited in either direction, we find that we can measure how much the propensity is shifted and what effect this has on the tasks. Critically, propensities estimated using one benchmark successfully predict behaviour on held-out tasks. Moreover, we obtain stronger predictive power when combining propensities and capabilities than either separately. More broadly, our framework showcases how rigorous propensity measurements can be conducted and how it yields gains over solely using capability evaluations to predict AI behaviour.

Primary area:
other topics in machine learning (i.e., none of the above)
Keywords:
Propensities, Capabilities, Evaluation, Scales

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 4 reviews, above 27% of the others.
Reviewer_h2psOpenReview ↗
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Paper summary

This paper proposes a framework for measuring behavioral propensities in AI systems, distinguishing them from capabilities. The authors introduce a two-sided logistic IRT model (2×2PL) in which task success depends on whether a model's propensity falls within an acceptable range. They use LLM-annotated task requirements and synthetic datasets to estimate four propensities across several language models. The results show that estimated propensities generally respond to prompting and provide some additional predictive value when combined with capability measures, particularly on held-out benchmarks.

Critical strengths
  1. The framework is sound. The distinction between capability and behavioral tendency is a useful one: a model may be fully capable of a task and still fail because of how it tends to behave. The paper gives a formal way to study that gap.

  2. The evaluation is fairly thorough. It covers several models and propensity dimensions and includes held-out benchmarks. The results suggest that propensity information can complement capability measures when predicting model performance.

Critical weaknesses
  1. My first concern is methodological novelty. Non-monotonic item response models, including ideal-point and unfolding models, are well established in psychometrics. As far as I can tell, 2×2PL is a variant of these that adds an acceptable propensity interval. That adaptation could be worthwhile, but the paper does not directly compare it against the existing non-monotonic IRT models. As a result, I could not judge whether the new formulation improves parameter estimation or prediction, or only re-parameterizes a known model.

  2. My biggest worry is construct validity of the estimated propensities. Most of the evidence comes from synthetic tasks, prompted behavior changes, and annotations generated by an LLM. Seeing that a score shifts when the system prompt tells the model to behave differently does not convince me that the score measures a stable tendency. It may simply track compliance with that prompt on that task. I also found little independent validation of the annotations or of the resulting measurements.

Questions for authors
  1. How does 2×2PL compare with established ideal-point or unfolding IRT models in terms of parameter recovery, model fit, and predictive performance?Even one direct comparison would go a long way.

  2. What evidence supports the construct validity of the estimated propensities? In other words, how can the authors distinguish stable behavioral tendencies from responses induced by system prompts?

  3. How reliable are the propensity demand intervals annotated by GPT-4.1? Can the authors provide independent human validation? Having humans check a sample would help. Is it possible that a comparison with simpler behavioral measures do not require fitting the proposed IRT model?

2 comments
AuthorsOpenReview ↗

Rebuttal Response to h2ps

We thank the reviewer for recognising the usefulness of separating capabilities from propensities and the breadth of our evaluation. We now address the points raised by h2ps (all new analyses use the released data, with no new model runs):

W1. Limited novelty with respect to ideal-point and unfolding IRT: we agree that the 2x2PL belongs to the family of unfolding models: per item, Eq. 5 is a peak-normalised hyperbolic cosine model (HCM; Andrich & Luo, 1993; Johnson & Junker, 2003), and we will state this explicitly. Our contribution does not lie in the functional form, but in (i) its parametrisation by the lower and upper bounds of a tolerated interval, which can be annotated per item, so item parameters come from annotation rather than from a population fit; (ii) the reading of capabilities and propensities as the one- and two-sided cases of the same interval; and (iii) the estimation of a single subject's level without a population of respondents. The empirical comparison with HCM is given in Q1.

W2. Construct validity: we address the three alternative explanations raised by the reviewer.

  1. Prompt-following: recovering an incited level is a manipulation check, and we will relabel Table 1 as such. We have also fixed a numerical issue in the estimator behind Table 1 (summary in our response to g4Xh). As independent evidence, the ultracrepidarianism θ\theta, estimated on synthetic items, tracks each model's rate of answering anyway on the 177 unanswerable questions of TimeMenatQA, a benchmark we did not build (Spearman ρ=0.47\rho = 0.47, p=0.008p = 0.008; same ordering across prompts in 10 of 10 models).
  2. Task-specific patterns: θ\theta is stable across item sets. Between narrow- and wide-band halves of each dataset it shifts 0.03–0.20 SD, and stratified split-half rr is 0.86–0.98.
  3. Annotations: the intervals carry item-specific content. On TimeMenatQA, only the propensity relevant to the task (ultracrepidarianism) improves the capability-only assessor (+0.019 AUROC, 24 of 27 subjects, p≈10−5p \approx 10^{-5}), while the same intervals shuffled across items do not (−0.004). Moreover, success crosses 50% within 0.11 units of the annotated interval edges, as the model assumes.

Q1. Comparison with ideal-point / unfolding models: we compared 2x2PL with HCM under identical item parameters (fixed by the annotations), over 383 (dimension, model, condition) cells:

  • Parameter recovery: both recover the incited level equally well (median Pearson r=0.97r = 0.97 under both).
  • Model fit and prediction (held-out items, 5 folds): with the same constant slope, 2x2PL improves held-out log-likelihood over HCM by +0.007 per item (229/383 cells, p=2⋅10−4p = 2 \cdot 10^{-4}) and AUROC by +0.012 (271/383 cells). Both are far above the aggregate success rate (AUROC 0.71 vs 0.50). The slope comparison is detailed in our response to ii3J.

Q2. Stable tendencies vs prompt-induced responses: see W2.1. Our evidence supports θ\theta as a common scale on which propensity shifts are measured and transfer to natural tasks. Establishing stable between-model differences in default propensities requires larger item banks than ours, which we will state as a limitation.

Q3. Reliability of GPT-4.1 intervals, and simpler behavioural measures: human validation of the intervals is not reported, and we will state it as a limitation; W2.3 gives the evidence that they carry item-specific content. Against the simplest behavioural measure that needs no IRT fit, the aggregate failure rate:

  1. Item mix: the failure rate shifts 0.22–0.49 SD between narrow- and wide-band halves, θ\theta only 0.03–0.20 SD.
  2. Direction: in 20 of 49 (model, propensity) pairs, failure rates are within 5 points when the model is incited towards opposite poles; θ\theta separates all 20 with the correct sign (median distance 3.8).
  3. Prediction: on held-out items, 2x2PL improves log-likelihood over the aggregate rate by +0.050 per item, with AUROC 0.71 vs 0.50.

We hope these additions and clarifications answer your concerns directly, and we would appreciate it if you could consider updating your score accordingly.

References:

Andrich & Luo (1993), Appl. Psychol. Meas. 17(3), 253–276.

Johnson & Junker (2003), J. Educ. Behav. Stat. 28(3), 195–230.

Thank you for the detailed response and the new analyses.

The comparison with HCM is helpful, but it also confirms my concern about novelty. The functional form is essentially an existing unfolding model, and the gains over HCM are modest with equal parameter recovery. The main contribution is annotating the interval bounds, which makes population-free estimation possible. The paper mainly shows that prompt-induced shifts transfer, and it cannot establish stable default propensities.

The GPT-4.1 intervals also remain without human validation. I also could not find these new analyses of “W2.3” in the current PDF. The paper's presentation can be improved with careful revisions.

Reviewer_ii3JOpenReview ↗
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Paper summary

The paper investigates behavioral propensities in AI and distinguishes them from capabilities. Its proposed 2x2PL model uses a normalized product of logistic functions, giving high success probability within an ideal interval and lower probabilities outside it. GPT-4.1 and rubrics annotate task demand intervals for four propensities. Responses to synthetic tasks then estimate model parameters θ under different prompting conditions. Prediction experiments add propensity-demand features to ADeLe capability-demand features and compare Random Forest assessors on TimeMenatQA and six naturalistic benchmarks.

Critical strengths

S1. The problem is important and the representation is intuitive. Demand intervals express situations where either excessive or insufficient propensity impairs success. Distinguishing these demands from capability requirements could support more specific analyses of model behavior and interventions.

S2. Evaluation extends beyond synthetic tasks. Leave-one-dataset-out experiments on six naturalistic benchmarks report a mean AUROC gain of 0.019, with improvements for 10/12 models (pp. 8-9, Table 3). The authors also report nonsignificant in-distribution gains and compare intervals with midpoint features. These results provide meaningful preliminary evidence for the usefulness of task-demand annotations.

Critical weaknesses

W1. The central parameter-transfer claim is not directly validated. The abstract claims that propensities estimated on one benchmark predict held-out tasks, whereas Section 4.4 and Appendix I compare item-demand features. Inspection of the TimeMenatQA prediction script confirms that it uses interval endpoints and trains separate assessors, without incorporating model θ estimated from synthetic tasks. Consequently, Table 2 demonstrates the value of additional item annotations, not transferability of 2x2PL parameters. The remaining results do not clearly close this gap. The contributions should be distinguished, with direct evaluation of frozen-θ transfer or narrower abstract and conclusion claims.

W2. The scale's validity and the incremental value of its mathematical design remain unestablished. Appendix F selects the last integer level exceeding 50% success and truncates at ±3. These choices require calibration against Equation (5)'s approximately 50% continuous boundaries and unbounded θ. Independent annotation reliability and invariance across item sets are not reported. Table 9 gives o1's default extraversion/introversion estimate as -0.94±1.96. Another condition yields -13.68±393.09, which the authors flag as unidentified in the Table 1 footnote; these estimates warrant cautious interpretation.

With q=a′, midpoint m, and half-width r, Equation (5) becomes [1+cosh(qr)]/[cosh(qr)+cosh(q(θ−m))]. For each item, this has the same form as the correspondingly scaled HCM curve after peak normalization [R1]. This does not establish equivalence of the complete estimation procedures. The authors should position their additional contribution and validate the fixed unit peak and width-dependent slope.

[R1] Johnson, M. S. & Junker, B. W. (2003). Using Data Augmentation and Markov Chain Monte Carlo for the Estimation of Unfolding Response Models. Journal of Educational and Behavioral Statistics, 28(3), 195-230. Equation (2), p. 197, states the HCM response function. The algebraic comparison with the submitted manuscript is part of this review, not a claim made by this source. https://www.stat.cmu.edu/~brian/trs/johnson-junker-jebs-03.pdf

Questions for authors

Q1. Which result directly predicts independent tasks using θ estimated and frozen on synthetic tasks? Please explain where this parameter enters prediction, beyond additional item-demand features, and provide the corresponding probability predictions and calibration results.

Q2. How are integer thresholds, truncation at ±3, and unidentified estimates handled? Are independent annotation-reliability and cross-item-set re-estimation results available to support stable parameter interpretations?

Q3. Which comparisons against HCM or related unfolding models establish benefits from peak normalization and the specific width-dependent slope? How do these constraints improve measurement or prediction?

Q4. Please reconcile model and item counts, explain Table 2's averaging denominators and weights, and provide gains and uncertainty separately for the six naturalistic benchmarks. How do shared items and model-family dependence affect the aggregate statistical conclusions?

1 comment
AuthorsOpenReview ↗

Rebuttal Response to ii3J

We thank the reviewer for a detailed and technically careful review. We now address the points raised by ii3J (all new analyses use the released data, with no new model runs):

W1/Q1. Transfer of a frozen θ\theta: the reviewer is right about the TimeMenatQA experiment, and we will correct the abstract's wording. Following ADeLe (Zhou et al., 2026), θ\theta is explanatory: it places a model on an interpretable scale and explains why it fails an item (too much or too little propensity). Instance-level prediction is done by assessors on item demands. What transfers is the annotation scheme (Table 2) and the explanatory scale. Where θ\theta enters:

  • Subject level: the ultracrepidarianism θ\theta, frozen on synthetic items, tracks each model's rate of answering the 177 unanswerable TimeMenatQA questions (Spearman ρ=0.47\rho = 0.47, p=0.008p = 0.008; same ordering across prompts in 10/10 models).
  • Instance level (as requested): frozen θ\theta through Eq. 5 gives AUROC 0.54 (> 0.5 in 18/27 subjects) but poor calibration (0.80 predicted vs 0.68 observed). This is expected: Eq. 5 models only the propensity component, and most failures are capability failures. In the capability assessor it adds +0.015 AUROC, but another subject's θ\theta adds the same (+0.016): instance-level information lies in the annotations, as the explanatory/predictive split intends.

W2/Q2. Integer edges and ±3 truncation: pooled over models and conditions, success crosses 50% within 0.11 units of the annotated edges in all four dimensions, as Eq. 5 assumes. Where θ<−3\theta < -3, success on items whose band reaches −3 is 0.23–0.30, vs 0.25–0.34 predicted with the band closed at ±3. Since θ\theta is fitted with the same bands, these are consistency checks, and we will say so.

W3/Q2. Reliability and invariance: between narrow- and wide-band halves, θ\theta shifts 0.03–0.20 SD (failure rate: 0.22–0.49), and stratified split-half rr is 0.86–0.98. Shuffling intervals across TimeMenatQA items removes their predictive gain (+0.019 → −0.004). Independent annotator reliability is not reported, and we will state it as a limitation.

W4/Q2. Unstable estimates: both quoted estimates come from cells where every response is scored as a failure, so θ\theta is not identified. Our revised estimator (grid MLE with profile-likelihood intervals, replacing a gradient fit with Hessian SEs) fixes a numerical issue behind Table 1; with it, θ\theta tracks the incited level with r≥0.8r \ge 0.8 in 47/48 (model, propensity) pairs (summary in our response to g4Xh). Degenerate cells (9) and cells whose interval hits the search bound or is disjoint (16/383) are reported as not identified.

W5/Q3. Relation to HCM: per item, Eq. 5 is a peak-normalised hyperbolic cosine model (Andrich & Luo, 1993; Johnson & Junker, 2003), and we will state this. Our contribution is the parametrisation by annotatable interval bounds (no population fit), capabilities and propensities as one- and two-sided cases, and single-subject estimation. Held-out comparison (383 cells, item parameters fixed by annotations, 5 folds):

ComparisonΔ log-lik./itemCellsΔAUROC
2x2PL vs aggregate rate+0.050221/3830.71 vs 0.50
2x2PL vs HCM, same slope+0.007229/383+0.012
Width-dependent vs constant slope−0.019104/383−0.010

Peak normalisation is supported; the width-dependent slope is not, and we will report it as a modelling choice.

Q4. Counts and breakdown: synthetic: 1,412 items, 12 models (+1 on ultracrepidarianism only). TimeMenatQA: 355 items, 27 model × prompt subjects. Naturalistic: 3,328 items in 6 benchmarks, a disjoint set of 12 models, and no item is shared across benchmarks. Per held-out benchmark (95% CI over models):

BenchmarkΔAUROC95% CIImproved
MCTACO+0.043[+0.019, +0.068]10/12
SAT+0.035[+0.011, +0.061]10/12
TimeDial+0.023[−0.002, +0.053]8/12
LSAT+0.008[+0.001, +0.019]10/12
CSE+0.003[−0.007, +0.015]4/12
TruthQuest+0.003[−0.012, +0.016]9/12

The mean gain is positive on every held-out benchmark and in every model family (DeepSeek-R1 distills +0.022, Llama +0.013, OpenAI +0.026), and leaving any family out keeps it between +0.017 and +0.024.

We hope these additions and clarifications answer your concerns directly, and we would appreciate it if you could consider updating your score accordingly.

References:

Andrich & Luo (1993), Appl. Psychol. Meas. 17(3), 253–276.

Johnson & Junker (2003), J. Educ. Behav. Stat. 28(3), 195–230.

Zhou et al. (2026), General scales unlock AI evaluation with explanatory and predictive power, Nature.

Reviewer_7jf5OpenReview ↗
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Paper summary

The paper proposes a formal method of empirically evaluating what an AI does (it's propensity) rather than just what it is able to do (it's capability). The framework is based on bilogistic model that recommends performance in the middle of the range of possible behaviors.

Critical strengths

Studying how models actually perform is an important task in machine learning.

The theorems (all in the appendix) seem to be correct and substantive.

Critical weaknesses

The overall content of this paper does not really seem right for ICLR. The paper says "In current AI practice, propensities are typically evaluated with collections of prompts or benchmark instances designed to elicit a target tendency" and then cites a bunch of examples, but then none of these methods are compared against empirically (unless I badly misunderstood the methods section). An ICLR paper in this space should compare against standard ML methodology, not just dismiss it. The citations place the paper more within the NLP literature than the ML space: I count only two citations listed as being in ICML/NeurIPS/ICLR. If the learning part (how best to fit an assessor) was the main core of the paper I'd feel much more like it fit, but there's not nearly enough learning here to sustain that argument.

Then overall the results are generally weak, mostly because of the lack of comparison to prior work.

Questions for authors

What does this formal approach let you do that the standard prior approach did not? For example, for what downstream use case can this approach improve the performance of AI over prior approaches described in section 2?

3 comments
AuthorsOpenReview ↗

Rebuttal Response to 7jf5

We thank the reviewer for acknowledging the importance of the problem studied in our work. We now address the points raised by 7jf5:

W1. No empirical comparison against standard propensity evaluations (Section 2): the standard practice we cite in Section 2 reports one aggregate per model, such as the rate of biased or failed responses on a prompt collection. We compare that aggregate with our estimate θ\theta on the paper's own data, on three properties a downstream user needs.

  1. Independence from the benchmark's item mix: an aggregate rate, as in classical test theory, depends on which items a benchmark happens to contain, while item-response estimates are designed not to (one of the advantages of the 2PL model, which our 2x2PL inherits). We split each of our four datasets into narrow-band and wide-band halves and measured both quantities on each half, for every model and condition. The aggregate failure rate moves substantially with the mix (0.22–0.49 standard deviations), while θ\theta moves much less (0.03–0.20 standard deviations).
  2. Direction, not only magnitude: a failure rate cannot tell excess from deficit, which is precisely the two-sided problem propensities pose and our model captures. In 20 of 49 (model, propensity) pairs, the failure rate is within 5 points when the model is incited towards opposite poles (−2 and +2); θ\theta separates all 20 pairs with the correct sign, by a median of 3.8 scale units. An over-confident and an over-cautious model can be equally "inaccurate", but call for opposite fixes.
  3. Instance-level prediction on new tasks: an aggregate rate is one number per model, so it ranks every item the same and has no discriminative power at the instance level. Item-level propensity demands do: on six naturalistic benchmarks never designed around propensities, adding them to capability demands improves out-of-distribution AUROC by +0.019 for 10 of 12 models (Table 3, Wilcoxon p=0.0068p = 0.0068), a gain over a much stronger baseline than the aggregate.

W2. Fit with ICLR: we respectfully disagree that measurement of model behaviour is outside ICLR's scope. Latent-variable models for LLM evaluation have appeared at ICLR and ICML, for example metabench (ICLR 2025) and tinyBenchmarks (ICML 2024), both built on IRT. Propensity evaluations we build on also appeared at these venues: sycophancy (Sharma et al., ICLR 2024), MACHIAVELLI (Pan et al., ICML 2023) and ETHICS (Hendrycks et al., ICLR 2021). Part of the citation count you observed is our fault, since we cite their arXiv versions: we will correct the venues and add metabench and tinyBenchmarks to the related work. On the learning side, see the assessor ablations in W3.

W3. Weak results, mainly due to no comparison with prior work: W1 provides the direct comparison. We also tested whether the predictive gain is specific to the propensity relevant to a task. On TimeMenatQA, we added each propensity separately to the capability-only assessor (random forest, 10 folds, 5 seeds, 27 model × prompt subjects):

  • Only ultracrepidarianism improves AUROC: +0.019, in 24 of 27 subjects (Wilcoxon p≈10−5p \approx 10^{-5}).
  • Red vs blue (+0.001), risk aversion (+0.002) and introversion (+0.000) add nothing, and the ultracrepidarianism annotations shuffled across items slightly hurt (−0.004).

The gain therefore comes from the content of the relevant interval annotations, not from extra features.

Q1. Downstream use cases of our methodology:

  • Anticipating, before deployment, on which items a model will fail because of its tendencies rather than its capabilities (instance-level prediction, W1.3 and W3).
  • Choosing a model whose propensity lies inside the band a task requires, for example an abstention-heavy medical QA setting.
  • Auditing how far a system prompt or fine-tuning shifts a model on a common scale. Our revised estimator fixes a numerical-stability issue in the maximum-likelihood fit behind Table 1 (the corrected table will appear in the revision); with it, θ\theta tracks the incited level with r≥0.8r \ge 0.8 for 47 of 48 (model, propensity) pairs (summary in our response to g4Xh).

We will add this comparison to the paper as a baseline section. We hope these additions and clarifications answer your concerns directly, and we would appreciate it if you could consider updating your score accordingly.

References:

Kipnis et al. (2025), metabench: A sparse benchmark of reasoning and knowledge in large language models, ICLR

Maia Polo et al. (2024), tinyBenchmarks: Evaluating LLMs with fewer examples, ICML.

Sharma et al. (2024), Towards understanding sycophancy in language models, ICLR.

Pan et al. (2023), Do the rewards justify the means? Measuring trade-offs between rewards and ethical behavior in the MACHIAVELLI benchmark, ICML.

Hendrycks et al. (2021), Aligning AI with shared human values, ICLR.

Maybe I'm missing something, but I still do not see where the comparison against prior work is here. The response says "W3. Weak results, mainly due to no comparison with prior work: W1 provides the direct comparison" but then W1 does not list any reference that's being compared against. There are a lot of references in this comment and in S2, but none of them is actually being directly compared against, as far as I can see. Which paper exactly is the subject of the direct empirical comparison, and where are the numbers reported?

AuthorsOpenReview ↗

Regarding direct comparison to previous work

We thank the reviewer for engaging with our response, and we apologise for not making this explicit. The comparison is not against a single paper, but against the measurement practice shared by the propensity evaluations cited in Section 2 (lines 124–129): social bias (Nadeem et al., 2021; Nangia et al., 2020; Parrish et al., 2022; Smith et al., 2022), toxic generation (Gehman et al., 2020), reward–ethics trade-offs and value judgments (Hendrycks et al., 2021a; Pan et al., 2023) and sycophancy (Sharma et al., 2023). All of them summarise a model's propensity as an aggregate rate: the proportion of responses exhibiting the behaviour over a collection of prompts. Their benchmarks do not include item-level demand annotations, so our model cannot be run on them as they stand. Instead, we applied their measure (the aggregate rate) to our data and compared it with our estimate θ\theta on exactly the same models and responses. The numbers, which test limitations (i) and (v) stated in Section 2 (lines 129–135), are in our response above:

  1. Dependence on the item mix (W1.1): the aggregate rate shifts 0.22–0.49 SD between two halves of the same dataset, while θ\theta shifts only 0.03–0.20 SD.
  2. Direction (W1.2): in 20 of 49 (model, propensity) pairs, the aggregate rate is the same (within 5 points) when the model is incited towards opposite poles, while θ\theta separates all 20 pairs with the correct sign.
  3. Prediction on held-out items: our model improves log-likelihood over the aggregate rate by +0.050 per item, with AUROC 0.71 vs 0.50 (table in our response to ii3J).

We will make this comparison, and its mapping to each cited work, explicit in the paper.

Reviewer_g4XhOpenReview ↗
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Paper summary

The paper introduces a simple framework that incorporates the notion of propensities as well as capabilities into the evaluation of LLMs. They argue that while capabilities are monotonic with respect to target tasks, propensities are not. Both too little and too much of a given propensity can cause failure on a task. In the proposed “2x2PL” model each item has a demand interval [b_l, b_u], and the task success probability is a normalised product of two logistics. Item intervals are annotated by GPT-4.1 using rubrics, and a subject’s propensity θ is estimated by maximum likelihood. Experiments use four synthetic multiple-choice datasets for the hand-selected propensities (red-vs-blue, risk, introversion, ultracrepidarianism). Twelve LLMs are steered with graded system prompts (−3 to +3). Random-forest “assessors” then test whether adding propensity features to 18 ADeLe capability features improves instance-level prediction.

Critical strengths

Well Motivated Problem. The paper points out that propensities (tendencies where both too much and too little can hurt) do not fit the monotonic logic of standard capability models. Many models either only treat capabilities or mix capabilities and propensities in a monolithic manner.

Elegant Framework. The 2x2PL model is a product of two logistics over a demand interval [b_l, b_u], which I found the both elegant and simple. The model reduces to the standard 2PL when one bound goes to infinity, so capabilities and propensities live in one framework - also very elegant.

Critical weaknesses

Ad Hoc Choice of Propensities. The choice of propensities seemed entirely ad hoc. I would have liked to see a substantial inventory of propensities and perhaps some sensitivity analysis showing how important or unimportant the choice of propensities might be in the study.

Suspected Circular Reasoning. Propensity is “induced” by system prompts and then recovered, so Table 1 mostly shows the method recovers an instruction the authors gave. That measures steerability or instruction-following, not a model’s intrinsic tendency. The datasets are also built so that the correct option aligns with a pole of the propensity, which makes the setup somewhat circular.

Questions for authors

What independent evidence shows that fitted theta captures a model’s propensity, not its willingness or ability to follow a system-prompt instruction?

The datasets are written so that the correct answer corresponds to a propensity pole. How would you distinguish a genuine propensity effect from the data construction itself?

1 comment
AuthorsOpenReview ↗

Rebuttal Reponse to g4Xh

We thank the reviewer for the positive assessment of the motivation and of the 2x2PL model, and for pressing on circularity, which we consider the most important validity question for this work. We now address the points raised by g4Xh (all new analyses use the released data, with no new model runs):

W1. Hand-picked propensities, no sensitivity analysis: the four propensities illustrate the framework, which is not tied to them, and were chosen to span different kinds of construct: a content-free control (red vs blue), a decision-theoretic trait (risk aversion), a personality trait (introversion) and an epistemic trait (ultracrepidarianism). The framework only requires interval annotations, so it applies to any propensity that can be defined by a tolerated interval, including constructs from established human taxonomies such as the Big Five or Schwartz's basic values, and we will discuss this extension in the revision. As a sensitivity analysis, we added each propensity separately to the capability-only assessor on TimeMenatQA (random forest, 10 folds, 5 seeds, 27 model × prompt subjects):

  • Only ultracrepidarianism, the propensity relevant to the task, improves AUROC: +0.019, in 24 of 27 subjects (Wilcoxon p≈10−5p \approx 10^{-5}).
  • Red vs blue (+0.001), risk aversion (+0.002) and introversion (+0.000) add nothing, and the ultracrepidarianism intervals shuffled across items slightly hurt (−0.004).

The choice of propensity therefore matters in the expected way.

W2. Circularity, Table 1 shows steerability: we agree that Table 1 alone cannot separate a propensity from instruction-following: recovering an incited level is a manipulation check, showing that the scale responds to the manipulated quantity in the right direction and order, and we will relabel it as such. We have also revised the estimator behind Table 1, fixing a numerical-stability issue in the maximum-likelihood fit (the corrected table will appear in the revision); with it, θ\theta tracks the incited level with r≥0.8r \ge 0.8 for 47 of 48 (model, propensity) pairs. Summary of Table 1 (12 models per propensity; published → corrected):

PropensityMedian rrPairs r≥0.8r \ge 0.8Median slope
Red vs blue0.96 → 0.9712 → 120.80 → 0.81
Risk aversion0.96 → 0.9711 → 110.76 → 0.87
Introversion0.81 → 0.957 → 120.55 → 0.87
Ultracrepidarianism0.96 → 0.9712 → 120.46 → 0.47

Independent evidence is given in Q1.

W3. Correct options aligned with a propensity pole: this is not the case for most items, which is what makes the two-sided model testable. The share of items whose correct answer is tolerated only by the negative pole / only by the positive pole / by neither (a band closed on both sides) is 28/28/44% for red vs blue, 34/43/23% for introversion, 14/21/64% for ultracrepidarianism and 48/50/2% for risk aversion, and only one item is tolerated by both poles. A model at either extreme therefore fails the opposite-pole items and most closed-band items, so extremity is never rewarded. Risk aversion, where almost every item sits at a pole, is the dataset most exposed to the reviewer's concern, and we will flag it.

Q1. Independent evidence that θ\theta captures a propensity: we compared θ\theta with behaviour on a benchmark we did not construct. For each model, we took its ultracrepidarianism θ\theta, estimated on the synthetic dataset, and the rate at which the same model, under the same prompt, answers anyway on the 177 unanswerable questions of TimeMenatQA (natural items, different format). Higher θ\theta goes with more overreach (Spearman ρ=0.47\rho = 0.47, p=0.008p = 0.008), and within each model, θ\theta orders the three prompt conditions as overreach does in 10 of 10 models. θ\theta is therefore a common scale on which propensity shifts are measured and transfer to natural tasks. Establishing stable between-model differences in default propensities requires larger item banks than ours: we will state it as a limitation and narrow the abstract and Section 5 accordingly.

Q2. Propensity effect vs dataset construction: besides the band composition (W3), we tested the annotations on TimeMenatQA, a benchmark not built around propensity poles. The ultracrepidarianism intervals improve instance-level prediction, while the same intervals shuffled across items do not (W1). They also add +0.008 AUROC beyond the dataset's own gold "unanswerable" label (23 of 27 subjects, p=5⋅10−4p = 5 \cdot 10^{-4}), so they carry information beyond the construction of the questions.

We hope these additions and clarifications answer your concerns directly, and we would appreciate it if you could consider updating your score accordingly.

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

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