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Withdrawn from ICLR 2027

Can We Make an LLM Dumber, or Is It Just Playing Dumb? An Empirical Study of Believable Performance Throttling

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

A benchmark score is commonly read as a proxy for model capability. We study the inverse problem: can a model be driven to a target score, and do its failures resemble those of a naturally weaker model? We operationalize believable performance reduction along three axes: target calibration, item-difficulty structure, and error-distribution similarity to a real weak reference. We introduce CapLadder, an IRT-calibrated suite of 1,985 items spanning mathematics, code, multiple-choice reasoning, and tool use. A simple weak-teacher LoRA dial reaches unseen target levels on reasoning with a 1.9-point held-out calibration error, whereas prompting, temperature, and weight noise cannot combine comparable range and precision. Yet on multiple choice, the dial converges to an answer-token attractor: up to 97% of its newly introduced errors land on one letter, with the attractor changing from D in Qwen to A in Llama. Logit interventions identify a dominant near-constant shift: subtracting the estimated shift on held-out items recovers 52 to 59% of lost accuracy and removes the dominant attractor, while option permutation confirms that the bias tracks token position rather than option content. With high inter-annotator agreement (), human-coded error-category distributions nonetheless match the weak reference on reasoning (), showing that local plausibility and aggregate detectability differ. Structured tool calls exhibit more natural degradation in the Qwen family (), while a globally calibrated dial transfers poorly across benchmarks (14.2-point error on two usable benchmarks). Precise score control, therefore, does not imply a portable or believable reduction in skill.

Primary area:
datasets and benchmarks
Keywords:
sandbagging, benchmark validity, capability evaluation, LLM evaluation, item response theory, LoRA, answer-position bias, performance throttling, CapLadder, AI safety

Reviews

Among:
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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_imN8OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper investigates whether a model whose performance is deliberately reduced behaves like a genuinely weaker model. The authors propose three evaluation dimensions: target score, difficulty profile, and error distribution. They construct CapLadder, covering mathematics, coding, multiple-choice reasoning, and tool use. By training a LoRA adapter using a weaker teacher and adjusting the strength of the learned update, the authors achieve target-score control on some tasks while observing strong answer-letter concentration on multiple-choice questions. Logit interventions and option permutations provide evidence that answer bias contributes substantially to the performance reduction. The paper also examines tool-call error distributions, cross-benchmark calibration transfer, and the limitations of different auditing approaches.

Critical strengths

1. A useful evaluation perspective. Examining target score, difficulty profile, and error distribution separately helps avoid judging whether a model behaves like a weaker model solely from aggregate accuracy. CapLadder provides a common experimental setting for these comparisons.

2. Multiple analyses of the observed anomaly. The authors investigate answer-letter bias using answer logits, shift cancellation, option permutations, and different models and training configurations. They also explicitly limit the scope of the tool-use and transfer findings. These analyses provide more specific evidence about the observed performance reduction than accuracy curves alone.

3. Controllable performance reduction has potential applications, and the approach is worth exploring. Controllably reducing model performance could be useful in role-playing or simulation settings that require different levels of competence. Training a LoRA adapter on a stronger model using a weaker model's outputs, then adjusting the update strength to control its performance, is a simple and promising idea.

Critical weaknesses

1. The basis for the strong–weak reference relationship and behavioral similarity could be strengthened. The paper primarily establishes the relative strength of the base model and weak reference through aggregate accuracy, without sufficiently characterizing the overlap and differences in their item-level correctness. I would like to understand whether items answered correctly by the weaker model are mostly also answered correctly by the base model, and how often the reverse occurs. If there are many items that the weaker model answers correctly but the base model does not, this could indicate different capability profiles, limiting the interpretation of the experiment as reducing the level of the same underlying capability. Human-coded error categories and tool-error distributions provide some behavioral evidence; comparisons of reasoning and tool-selection processes on the same items would further help establish whether the observed similarities extend beyond coarse distributions.

2. The origins of the bias and the scope of its interpretation need further explanation. The extreme answer-letter concentration on multiple-choice questions is a phenomenon worth understanding more deeply. The authors have conducted several diagnostic analyses and controls, so I do not think the existing evidence can simply be characterized as training failure or attributed entirely to extrapolation. However, the respective roles of the training data, supervision, and amplification of the LoRA update remain unclear. Expanding the training details directly relevant to these questions, together with same-item examples from the base model, weak reference, standard LoRA model, and model with an amplified update, would help explain how this behavior develops and assess how far the findings extend beyond the current experimental setting.

Questions for authors

1. The strong–weak model relationship and the representativeness of the experiments. Could the authors provide a cross-tabulation of item-level correctness for the base model and weak reference, showing whether items answered correctly by the weaker model are mostly also answered correctly by the base model, and how often the reverse occurs? This would help assess whether their patterns of competence are approximately nested. In addition, the distillation experiments primarily use models with at most 9B parameters. Please clarify the scope of their implications for stronger models and practical capability evaluations. The prompting experiments with frontier APIs use a different setting from the distillation experiments, and these should be distinguished.

2. Similarity in reasoning and tool-selection patterns. The authors already compare human-coded error categories and tool-error distributions. Same-item examples of complete generations, comparing the base model, weak reference, and throttled model in terms of reasoning steps, tool selection, and argument construction, would help explain whether behavioral similarity extends beyond final answers and coarse error distributions.

3. How answer bias develops. The authors provide several diagnostics and controls for answer-letter bias, including results showing collapse without update amplification under other training configurations. For the main SFT method, I would still appreciate a clearer account of the behavioral differences between standard LoRA (α=1\alpha=1) and amplified updates, and the respective contributions of training and subsequent scaling. Including both settings in the same-item examples discussed above would also help illustrate how the bias manifests during generation.

4. The composition and supervision of the final training data. Table 9 reports the teacher's answer-letter distribution, but does this correspond to the actual training targets after filtering and processing? If the training data are filtered, how does filtering change their composition, and what are the final proportions of different sample types? A brief explanation of how teacher completions are supervised, and of the relationship between the distillation training set, calibration set, and test set, would help interpret the behavioral changes induced by training. Training-data filtering should be distinguished from item filtering for IRT difficulty analysis; the latter cannot automatically be assumed to describe the training-data pipeline.

5. The scope of the IRT difficulty ranking and the effects of filtering. Please clarify which models are evaluated using the difficulty ranking fitted solely from Qwen responses. If it is used for other model families, evidence supporting its applicability would be helpful. Within the same family, is the ranking stable when the pool of models used for fitting changes? The original task composition is reported in Table 6, but the proportion of items retained after IRT fitting differs across tasks. It would be useful to understand the characteristics of excluded items and whether this filtering affects the conclusions drawn from difficulty-profile comparisons.

6. Interpretation of the relative-distractor metric erele_{\mathrm{rel}}. Cyclic differences between option positions have no inherent semantic meaning. A model that always selects D can also produce a uniform relative-position distribution under certain answer-key distributions. Please explain what this metric is intended to identify and how it supports judgments about similarity in error patterns. This question concerns the interpretation of erele_{\mathrm{rel}} and does not dispute the answer-letter bias revealed by eabse_{\mathrm{abs}}.

7. Consistency in calibration-error reporting. Equation (4) defines the target using the test-set base accuracy, whereas Appendix C states that targets are derived from the calibration set. Using the test-set base accuracy of 0.902 and the achieved accuracies of 0.722 and 0.559 for the 80% and 60% targets, Equation (4) gives a mean error of approximately 0.9 percentage points. Using the targets of 0.711 and 0.533 in Table 8 instead gives approximately 1.85 percentage points. In addition, the Table 2 caption specifies an averaging grid of 80%/60%/40%, whereas Appendix C specifies 80%/60%. Please clarify the definition, target grid, and calculation used for the reported 1.9-percentage-point error.

8. Interpretation of the answer-key floor. Equation (6) bounds expected accuracy when responses are independent of the gold answers. Does interpreting a score below this range as using knowledge of the correct answer to avoid it also require ruling out explanations such as systematic task misunderstanding or an incorrect mapping between answers and labels? Representative outputs explaining this behavior, together with clarification of the criterion's statistical meaning for finite samples, would make the conclusion clearer.

9. Clarifications on figures and result reporting. Please explain why the Open 4B results for the 80% and 60% conditions in Table 2 are reported as “≈0.90,” and why Gemini's mean target miss is described as “cliff” rather than reported using the same metric as the other columns. In Figure 1B, the weak reference's maximum letter share is labeled as 0.22, although the largest plotted value is 0.27; please check this annotation. The upper and lower parts of Figure 1C use different LoRA scaling strengths; labeling them separately would also help readers understand how the results relate to one another.

Reviewer_FrqTOpenReview ↗
Rating
2
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
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Paper summary

This paper first tackles that the benchmark scores do not fully reflect the model's capability, and investigates whether deliberately reducing a strong LLM's benchmark score produces a failure process consistent with that of a naturally weaker model. The authors evaluate believable performance reduction along three dimensions: target-score calibration, accuracy across question-difficulty groups, and similarity of error distributions to a smaller reference model. To facilitate the analysis, they introduce CAPLADDER, a benchmark covering different answer formats, with item difficulty. As an experimental tool, they train a LoRA adapter on a stronger model to imitate a weaker teacher and calibrate the adapter's strength to reach requested accuracy levels. Attaching this LoRA is also named as throttling, that intentionally reduces the performance of the stronger model.

In the experimental results, the LoRA dial controls accuracy effectively, but its multiple-choice failures differ from those of a naturally weaker model, exhibiting flatter difficulty profiles and stronger answer-token biases. Correcting the systematic logit shift restores substantial accuracy, supporting an output bias as a major cause of the degradation. Tool-use failures more closely resemble the weaker reference in the Qwen experiments, while calibrated settings transfer poorly across benchmarks. These findings show that precise score control does not guarantee weak-model-like behavior or a transferable performance reduction.

Critical strengths
  • This paper mechanistically investigates the answer-token bias when training LoRA from a weak model, and shows how to resolve this problem.
  • This paper evaluates performance reduction through score calibration, difficulty profiles, and error distributions, providing a more detailed comparison between throttled and naturally weaker models.
Critical weaknesses
  • The connection between the paper's motivation and its experimental setting is not sufficiently justified. The paper argues that benchmark scores alone do not fully characterize model capabilities, but then studies whether a strong model modified with a weak-teacher LoRA adapter fails like a naturally weaker model. While this is a valid question about controlled underperformance, its relevance to the broader goal of understanding model failures needs a clearer explanation. A direct comparison of reasoning or solution trajectories between strong and weak models would more directly examine how their problem-solving processes differ. In the current setting, the observed differences may reflect artifacts of the chosen intervention. The authors should clarify what analyzing this artificially induced weakness reveals about capability evaluation beyond the behavior of the throttling method itself.
  • The believability criteria primarily assess similarity in aggregate behavior, leaving the comparison of reasoning or solution processes underdeveloped. Although the criteria go beyond final accuracy by including difficulty profiles and error distributions, these measurements do not systematically capture how a solution is constructed, where an error first occurs, or how it affects subsequent steps. The human-coded semantic error categories partially address this issue, but similar category frequencies can arise from different solution trajectories. While the paper explicitly adopts a behavioral definition of believability, it should better justify why these particular measurements adequately address its motivating question about whether the failure processes are consistent. Comparing solution trajectories would provide more direct evidence for that interpretation.
  • The mechanistic experiments provide useful evidence that an answer-token bias contributes substantially to the performance degradation on multiple-choice tasks. However, why weak-teacher distillation produces this bias remains less clear. Subtracting the mean logit shift mitigates the effect, but does not by itself explain how the shortcut emerges during training. The authors' suggestion that a token bias is a low-cost solution for a low-rank adapter is plausible, but would benefit from direct analysis of the training dynamics. Clarifying how the bias develops, and whether the remaining failures after correction resemble those of the weaker reference, would strengthen the mechanistic account and provide more concrete guidance for future evaluation or throttling methods.
  • The presentation of the experimental results would benefit from a clearer narrative connecting the individual findings. The sections report score calibration, difficulty profiles, answer-token biases, and transfer results, but the discussion often emphasizes individual numbers without sufficiently combining what they found about the throttling method. In particular, it is difficult to follow how increasing the adapter strength changes the model's failure behavior and how the subsequent interventions explain those changes. A more explicit explanation with clearer connections across settings and tasks, would make the central findings easier to assess.
Questions for authors
  • What does LoRA-induced underperformance reveal about capability evaluation beyond the effects of this specific intervention?
  • How do the believability criteria support conclusions about similarity in failure processes without directly comparing solution trajectories?
  • What explains the emergence of answer-token bias during training, and do the remaining errors after logit correction resemble those of the weaker reference?
  • Can you clarify how the calibration, difficulty-profile, and error-distribution results jointly explain the effect of increasing adapter strength?
Reviewer_8fdwOpenReview ↗
Rating
1
Confidence
2
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

This work studies whether and how a model can be made to look weaker on a benchmark in a believable way, i.e., matching the failure pattern of a real weaker model, not just achieving a lower score. It builds CAPLADDER, a 1,985-item benchmark covering math, code, multiple-choice reasoning, and tool use with IRT difficulty labels, and tests four ways of lowering a model's score: prompting, temperature, weight noise, and a LoRA adapter distilled from a weak teacher, with a strength coefficient controlled by a scalar α. Only the LoRA adapter makes the model achieve lower target scores accurately. However, on multiple-choice questions, the adapted model collapses onto k more natural. A single fixed adapter strength also transfers poorly to other benchmarks.

Critical strengths
  • The core question (“Is a manufactured low score the same as low capability?”) is timely and well-motivated by safety concerns, and the definition (score, difficulty profile, error distribution) is concrete and checkable.

  • The evidence for why the collapse happens is convincing. They check it in three different ways (looking at the output logits, subtracting the estimated bias to see if accuracy comes back, and shuffling the options under the same letters), and all three point to the same reason: the model just pushes up one answer letter, regardless of the question.

  • The answer-key floor argument is a clean point. On four-option questions, a model answering independently of the correct option cannot score below the least common letter's share of the answer key. So when the frontier models score 0.012, below the 0.237 floor, that alone proves the model is avoiding correct answers, without even needing any knowledge of the model.

Critical weaknesses
  • I found the writing to be very unclear. I couldn’t get the gist of the paper by reading the abstract. Key terms (believability, output geometry, the dial, axes) are used before they are properly defined. Figures and tables have overly long and dense captions. I had to read the appendices to understand the main text. Some terms highly resemble LLM-written text (dial, operationalize, upshot, certificate, etc.).

  • This manuscript must be rewritten for the paper to be understandable by a broader audience. No seeds or error bars anywhere. All numbers are point estimates from single training runs.

  • The two headline numbers don’t seem to agree. The distilled adapter is only proven accurate at small reduction rates (80% and 60% of the base score), where the model's errors still look mostly normal. The setting where behavior becomes clearly unnatural (one answer letter absorbing up to 97% of errors) occurs at much stronger reduction rates, which the authors themselves label as "out of range". So the precise score control and the unbelievable behavior may not overlap: the adapter is believable where it is calibrated, and unnatural where it is not.

  • CAPLADDER's four task types differ from each other in several ways at once (how answers are graded, the output format, how long responses are, where the data comes from). So when the authors attribute their results to "output geometry," it's unclear which of these differences actually matter. However, at the same time, the paper's main story (that the kind of output determines which shortcut is available) leans heavily on this comparison.

Questions for authors
  • Why should we trust a calibration error computed over just two in-range targets? What happens with a denser target grid?

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

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