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Under review as a conference paper at ICLR 2027

Cross-Entropy Loss Falls Short: What Cross-Entropy Loss Reveals about Large-Language-Model Performance?

Abstract

Scaling laws have made cross-entropy loss a central quantity for understanding and predicting the behavior of large language models, often with an implicit assumption that lower loss indicates better downstream performance. In this work, we revisit the reliability of this assumption on multiple-choice question answering (MCQA). Across diverse model families and datasets, we find that lower loss does not consistently correspond to higher accuracy. A key reason is that loss and accuracy depend on different quantities: cross-entropy loss measures how well a response is modeled, whereas accuracy is determined by whether the correct response has lower loss than its alternatives. We further observe that differences in loss-landscape geometry may make absolute loss values difficult to compare across model architectures and families. We then extend our analysis to an unsupervised setting, using the cross-entropy loss of the question context without ground-truth answers, and observe an even less consistent relationship with model performance. Motivated by the role of relative separation, we also examine loss dispersion across answer choices, but find that greater dispersion does not consistently indicate better performance. Together, our empirical and theoretical analyses reveal when and why loss-based quantities can become unreliable proxies for downstream model performance.

Primary area:
other topics in machine learning (i.e., none of the above)
Keywords:
Cross-entropy loss, LLM, Scaling law, Model performance estimation

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
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Paper summary

This paper focuses on a widely adopted implicit assumption in the field of large language models: lower cross‑entropy loss implies better downstream‑task performance. It takes multiple‑choice question answering (MCQA) as its primary test scenario and conducts experiments across six model families: OPT, Cerebras‑GPT, DeepSeek, Qwen, Llama, and OpenELM. The experiments are divided into a supervised setting (where cross‑entropy loss is computed using ground‑truth correct answers) and an unsupervised setting (where loss is calculated solely from question context without ground‑truth labels).

Critical strengths

It evaluates both supervised cross‑entropy loss computed from ground‑truth answers and unsupervised loss derived solely from question context under label‑free conditions, which closely approximates real‑world scenarios for unannotated evaluation.

The related‑work section offers comprehensive literature coverage. It systematically surveys three categories of works: scaling laws, unsupervised model‑performance estimation, and LLM evaluation. It clearly positions the paper’s contribution: identifying the failure of loss as a proxy metric in cross‑model settings.

Critical weaknesses

Real‑world LLMs extensively employ open‑ended generation tasks. However, the paper does not validate its conclusions on free‑form generation or reasoning tasks, leaving it unclear whether the findings generalize to more general‑purpose scenarios.

It adopts the average negative log‑likelihood (NLL) over the full sequence of each option and selects the option with minimal loss as the prediction. This approach is not fully equivalent to the standard few‑shot inference paradigm of LLMs that directly output answers, creating a gap with real‑world inference behavior.

Although an upper‑bound property is proven at the single‑sample level, fine‑grained sample‑level analysis is missing: it does not investigate which samples exhibit “high dispersion yet incorrect predictions”, and qualitative analysis of failure cases is absent.

Questions for authors

The paper observes a strong loss‑performance correlation within each model family, whereas this correlation breaks down across different families. If we perform loss normalization for models from diverse families (e.g., normalization based on training‑set loss), would it restore cross‑model predictive power?

This work is entirely built upon MCQA tasks. Would a similar cross‑model failure pattern also arise between autoregressive cross‑entropy loss and generation quality for open‑ended generation tasks? What kinds of tasks are most susceptible to such failure?

The paper states that loss dispersion serves as an error upper bound at the single‑sample level, yet this property fails at the dataset level. Can sample‑level dispersion therefore be used for estimating sample difficulty, even if it cannot be employed for ranking different models?

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Paper summary

This paper examines whether cross-entropy loss reliably predicts multiple-choice question-answering accuracy across six LLM families and four benchmarks. It considers supervised loss, question-context loss without answer labels, and dispersion of losses across candidate answers. The paper reports that these quantities do not consistently track accuracy and explores loss-landscape differences as a possible explanation for variation across model families.

Critical strengths
  • The paper addresses a practically relevant question: when loss can serve as a useful proxy for downstream performance and model selection.
  • Comparing several loss-based indicators across multiple model families and benchmarks provides a useful empirical scope.
  • Including question-context loss extends the investigation to settings where answer labels are unavailable.
Critical weaknesses
  1. Limited novelty and overstated positioning relative to prior work.

    The central observation that lower cross-entropy loss does not necessarily imply better downstream performance is already established. Several explanations presented in this paper also overlap substantially with prior work:

    • Schaeffer et al. (2024; ICML 2025) study five model families and twelve multiple-choice benchmarks. They explain how transformations from NLL to accuracy weaken predictability and identify the importance of probabilities assigned to specific incorrect answers. This directly precedes the present paper’s central explanation based on relative candidate scores. Paper
    • Liu et al. (ICML 2023) demonstrate that models with the same pre-training loss can have different downstream performance and investigate the roles of optimization bias and loss-landscape flatness. Both the broader limitation of loss and the geometry-based motivation therefore have clear precedents, although their measurement setting differs from this submission. Paper
    • Isik et al. (2024; ICLR 2025) show that downstream cross-entropy can improve while translation-quality metrics fluctuate or deteriorate under distributional misalignment. The general mismatch between improving cross-entropy and improving task performance is therefore already documented beyond multiple-choice evaluation. Paper
    • Brandfonbrener et al. (2024) develop loss-to-loss prediction across data distributions and explicitly discuss the difficulty of predicting accuracy from loss. This conflicts with the submission’s broad characterization that these works all assume lower supervised loss implies better performance. Paper

    The remaining potential novelty lies mainly in the specific experiments on question-context loss, candidate-loss dispersion, and the selected model families. The paper needs to establish what substantial new understanding these experiments provide beyond the existing results.

  2. Theorem 5.1 is false, and its proof relies on an incorrect extremal claim.

    Theorem 5.1 on page 9 claims

1−p∗≤(K−1)exp⁡(−KK−1σ(x)),1-p^*\le (K-1)\exp\left(-\frac{K}{\sqrt{K-1}}\sigma(x)\right),

where σ(x)\sigma(x) is the standard deviation of candidate-answer losses. A valid four-choice counterexample violates this bound even when the correct answer has the unique minimum loss.

Let the first candidate be correct, and define

Z=1+e−1+2e−10,C=log⁡Z,Z=1+e^{-1}+2e^{-10},\qquad C=\log Z, (L1,L2,L3,L4)=(C,C+1,C+10,C+10).(L_1,L_2,L_3,L_4)=(C,C+1,C+10,C+10).

These are strictly positive, normalized single-token NLLs, with ∑ke−Lk=1\sum_k e^{-L_k}=1. Under the paper’s definition pk=e−Lk/∑je−Ljp_k=e^{-L_k}/\sum_j e^{-L_j},

1−p∗=e−1+2e−101+e−1+2e−10≈0.26898995.1-p^*=\frac{e^{-1}+2e^{-10}}{1+e^{-1}+2e^{-10}} \approx 0.26898995.

However, σ=113/4\sigma=11\sqrt{3}/4, so the claimed upper bound is

3e−11≈0.0000501051.3e^{-11}\approx 0.0000501051.

Thus, the actual quantity exceeds the claimed upper bound by several orders of magnitude. This counterexample uses exactly the paper’s probability error 1−p∗1-p^*, rather than the hard classification error of the argmin prediction.

The underlying error is in Lemma 1 on page 16, which claims that equal gaps between the correct answer and all incorrect answers maximize error at a fixed standard deviation. The relative-loss configurations (0,1,10,10)(0,1,10,10) and (0,11,11,11)(0,11,11,11) have the same standard deviation, but the former has a much larger error probability. High losses on easy distractors can inflate the standard deviation while leaving one strong distractor close to the correct answer.

This invalidates the stated theoretical guarantee supporting Section 5. Repair requires changing the conclusion or introducing substantive additional assumptions; a supplementary proof step cannot resolve the counterexample.

  1. The main-table correlation statistics are inconsistent with the appendix data.

    Recomputing the statistics from the published appendix values, using equally weighted model rows, ordinary least squares with an intercept for R2R^2, and standard Spearman rank correlation, gives the following discrepancies:

    StatisticMain-table valueRecomputed from appendix
    Table 1: OPT/MMLU, supervised loss, R2R^20.99960.9657501
    Table 1: OPT/MMLU, supervised loss, Spearman ρ\rho−1.0000−0.9428571
    Table 2: Qwen/MMLU, question-context loss, R2R^20.04540.0050739

    The OPT/MMLU contradiction is directly visible in Appendix Table 3. OPT-6.7B has loss 1.65041.6504 and accuracy 0.32460.3246, whereas OPT-13B has a lower loss of 1.64651.6465 but also a lower accuracy of 0.31940.3194. This pair already rules out the perfectly negative rank correlation reported in Table 1.

    Ordinary rounding cannot explain these discrepancies. For example, even allowing each published Qwen/MMLU input to vary by ±0.0005\pm0.0005, a conservative enclosing interval for the recomputed R2R^2 is approximately [0.00201,0.00982][0.00201,0.00982], excluding the reported 0.04540.0454.

    These are material inconsistencies because the empirical contribution centers on the strength and consistency of loss–accuracy relationships. If the main tables use different runs, model subsets, or aggregation procedures, those differences must be disclosed. The authors need to reconcile the tables and provide the exact inputs and statistical procedure. These specific discrepancies do not imply that all reported statistics are incorrect.

  2. The central loss measurements are defined inconsistently, preventing a clear interpretation and faithful reproduction of the experiments.

    Three inconsistencies require clarification:

    • The supervised-loss formula has the wrong sign relative to the reported values. On page 3, lines 138–142, the expression is written as
1K∑j1(yi=j)log⁡softmax⁡(+NLL⁡)j.\frac{1}{K}\sum_j\mathbf{1}(y_i=j) \log\operatorname{softmax}(+\operatorname{NLL})_j.
 For finite inputs and $K\ge2$, this quantity is strictly negative, whereas the appendix reports positive supervised-loss values. The published values therefore cannot be obtained from the formula as written.
  • The candidate-probability definitions use conflicting softmax signs. The page 3 formula applies softmax to positive NLL values, assigning greater probability to candidates with higher NLL. This conflicts with the minimum-loss prediction rule and with Appendix E.1, which explicitly defines probabilities using softmax⁡(−L)\operatorname{softmax}(-L). The manuscript must specify whether the experiments measure answer-token NLL, cross-entropy over normalized candidate probabilities, or another quantity, including the exact sign and normalization.

  • Answer-length normalization changes between measurements. The prediction rule on page 2 uses mean loss per token, whereas Appendix C defines the candidate losses used for dispersion as sums over tokens. For answers of different lengths, these definitions can produce different rankings and substantially different standard deviations. Summed losses can increase dispersion simply because candidate answers differ in length, independently of the model’s ability to distinguish the correct answer from distractors.

Questions for authors

Please see weaknesses.

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Paper summary

The paper asks whether lower cross-entropy loss implies higher multiple-choice QA accuracy for LLMs. It evaluates 41 models from six groups (OPT, Cerebras-GPT, DeepSeek-R1-Distill, Llama, Qwen, OpenELM) on the validation sets of OpenBookQA, PIQA, MMLU and HellaSwag.

Accuracy is likelihood-based: the predicted option is the one with the lowest length-normalized NLL (Eq. 1). Two loss quantities are compared against it. The "supervised loss" is a choice-level cross-entropy over a softmax across options (Sec. 2.1). The "unsupervised loss" is the mean next-token loss on the question context (Appendix B). The paper reports R^2 and Spearman rho within each group (Tables 1 and 2) and pooled across groups (Figures 1 to 4). The relation is strong for OPT, Cerebras-GPT and DeepSeek-R1-Distill, weak for Llama, Qwen and OpenELM, and weaker overall in the unsupervised setting.

Section 4 explains the gap through the margin view Acc(x) = 1[Delta(x) > 0], 2-D loss-landscape plots for OPT and DeepSeek-R1-Distill-Qwen (Figure 5), and two cases where loss does track accuracy: ResNet-18 on CIFAR-10C (Figure 6) and LoRA fine-tuning on OpenBookQA (Figure 7). Section 5 shows that the dispersion of option losses does not track accuracy either (Figure 8) and gives Theorem 5.1, a per-question bound on error in terms of the standard deviation of option losses. All per-model numbers are in Appendix D (Tables 3 to 14).

Critical strengths
  1. The question matters in practice: people do pick checkpoints and compare models by loss, and the paper puts every per-model accuracy and loss value in Appendix D (Tables 3 to 14). That makes the study fully re-analyzable. I recomputed several reported statistics from those tables (Llama on MMLU: R^2 = 0.042, rho = -0.2; OPT-6.7B across the four datasets: R^2 = 0.090, rho = 0.4) and they match the text. This transparency is the main thing I can credit, and it is also what let me check the concerns below.
Critical weaknesses
  1. The main empirical claim is not supported statistically, and the model groups are not the controlled families the text says they are.

Within-group correlations are computed on 5 to 11 points. With n = 5 (the Llama group) Spearman rho moves in steps of 0.1, and only |rho| = 1 reaches an exact two-sided p < 0.05; even rho = -0.9 gives p ≈ 0.08. So rho = -0.2 on MMLU is what noise looks like. The accuracy range across the five Llama models on MMLU is 0.368 to 0.396 (Table 6), under 3 points, while the binomial standard error on 1,531 questions is about 1.2 points (about 2.2 points on OpenBookQA's 500). A low R^2 is expected when accuracy barely varies. It does not show that loss fails. The paper reports no confidence intervals, bootstrap or permutation tests anywhere.

Sec. 2.2 says models within a family share "the same training strategy and training data". They do not. The Llama group mixes Llama-2-7b-chat with Llama-3.1 and 3.2, base and instruct; the Qwen group mixes Qwen1.5, 2, 2.5 and 3, base and instruct; OpenELM mixes base and instruct; DeepSeek-R1-Distill mixes Qwen and Llama bases. The groups where the relation looks clean (OPT, Cerebras-GPT) are single-recipe size sweeps. The simpler reading of Tables 1 and 2 is that loss tracks accuracy when only scale changes, and stops tracking it when data, post-training and tokenizer change. The losses are also never normalized for tokenizer (no bits-per-byte or per-character loss), so per-token question loss is not comparable across Qwen, Llama and DeepSeek models in the first place. Prior work that sets the measurement up for cross-model comparison finds much stronger relationships and is not discussed: Huang et al. 2024 ("Compression Represents Intelligence Linearly", 31 models), Du et al. NeurIPS 2024 ("Understanding Emergent Abilities of Language Models from the Loss Perspective"), and Ruan et al. NeurIPS 2024 ("Observational Scaling Laws"). Finally, the pooled supervised result in Figure 2 is R^2 = 0.80, rho = -0.82, which is a fairly strong relation and does not sit well with the title.

  1. The definitions and the theory do not support the explanations offered.

(a) The supervised loss in Sec. 2.1 has no minus sign and no average over questions, and the softmax is applied to the NLL rather than to -NLL. The reported values exceed ln 4 ≈ 1.386 for every model on OpenBookQA and on MMLU (minimum 1.41 and 1.47, Tables 3 to 8), i.e., worse than a uniform guess, even for models at 40 to 47% accuracy. I cannot tell what was actually computed. Since both accuracy and this loss come from the same per-option NLLs, any gap between them is a statement about calibration, which the cited work of Schaeffer et al. already covers. The scaling-law papers used as motivation in the introduction model a different quantity (language-modeling loss), so the framing overreaches.

(b) Theorem 5.1 is false as stated. The proof (Appendix E.1) assumes the correct answer has the minimum loss, but the statement says "for any K candidate answers". Counterexample: K = 2, L* = 10, L_other = 0. Then sigma = 5, the error is about 1, and the bound gives e^{-10}. With the assumption added, the bound only covers questions the model already answers correctly, so it cannot say anything about dataset-level error. The dataset-level step is Jensen's inequality applied to a bound; it shows the bound gets looser, not that dispersion and accuracy cannot correlate.

(c) The loss-landscape argument (Figure 5) uses random 2-D directions, does not say which data the loss is computed on, and gives no quantitative measure. The DeepSeek-R1-Distill-Qwen models it shows as "irregular" belong to the group with some of the strongest correlations in the paper (Table 2: R^2 from 0.84 to 0.98; Table 1: 0.62 to 0.91). So the figure does not explain where the relation breaks down.

(d) The CIFAR-10C example uses one ResNet-18 across corruptions, so it does not test the cross-architecture condition it is meant to support. Figure 7 shows OpenBookQA accuracy at 1.0 after a few epochs, which suggests accuracy was measured on the training data.

Smaller points that did not drive my score: Sec. 2.2 first says the DeepSeek trend is inconsistent "on at least one dataset" and then says it is clear "across all four benchmarks"; the PIQA rho is given as 0.548 in the text and -0.548 in Figure 1; the Qwen group is described as 3B to 8B but includes 1.5B and 14B models, and the Llama group as 3B and 8B but includes Llama-2-7B; Eq. 2 uses summed losses while Eq. 1 uses length-normalized ones; the Appendix C heading appears inside Appendix B; related work is only in the appendix; the captions of Figures 2 and 4 say "unnecessarily indicates" where "does not necessarily indicate" is meant. The prompt format is not given (zero- or few-shot, chat templates for instruct and R1-distill models). This matters because likelihood-based MMLU accuracy here is 0.37 for DeepSeek-R1-Distill-Qwen-32B and 0.41 for Qwen3-14B, far from how these models are normally evaluated, so the conclusions apply to cloze-style scoring only.

Questions for authors

Clarifications that could change my assessment:

  1. What exactly is the supervised loss (formula and code)? How can it exceed ln 4 for every model on OpenBookQA and MMLU while accuracy is 40 to 47%? Are option NLLs length-normalized before the softmax, and is the softmax over -NLL?

  2. Please add confidence intervals for R^2 and rho (bootstrap over questions and over models) and permutation p-values. Which of the "inconsistent" cases in Tables 1 and 2 remain significant?

  3. If you use tokenizer-normalized loss (bits per byte or per character) and restrict groups to single-recipe size sweeps (for example Qwen2.5 base models across sizes, or Pythia), does the inconsistency remain? A positive answer here would change my view of the paper most.

  4. For Theorem 5.1, can you state the required assumption (L* = min_k L_k) in the theorem and explain what dataset-level conclusion the bound then supports?

  5. In Figure 7, is accuracy measured on the training split or on held-out data? Which data is used for the loss surfaces in Figure 5, and with what direction normalization?

  6. Which prompt format, number of shots and chat templates were used, especially for the instruct and DeepSeek-R1-Distill models?

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