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REVIEW 3 major objections 6 minor 31 references

LLM mathematical performance is not invariant to how a problem is represented: rephrasing, symbolizing, or changing numbers in the same underlying problem shifts accuracy, and code scaffolds merely move failures to new layers.

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2026-08-02 07:59 UTC pith:IDNCEAZZ

load-bearing objection A well-designed empirical study with a plausible and useful qualitative result, but the headline claims about representation sensitivity rest on single-pass API calls and unreported flip rates; fixable with repeated runs and proper statistics. the 3 major comments →

arxiv 2607.20520 v1 pith:IDNCEAZZ submitted 2026-07-08 cs.AI cs.HCcs.PL

Representation Robustness Under Executable Reasoning Constraints in Large Language Models for Mathematical Problem Solving

Sagnik Nath , Edith Aurora Graf , Liang Zhang , Diego Zapata-Rivera This is my paper
classification cs.AI cs.HCcs.PL
keywords representation robustnessmathematical problem solvingLLM evaluationexecutable reasoningcode-augmented promptingrepresentational equivalencefailure analysishuman-AI interaction
verification ladder T0 review T1 audit T2 compute T3 formal T4 reserved

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

This paper argues that large language models do not solve math problems in a representation-invariant way: restating the same underlying problem as a story, an equation, or a word-equation changes accuracy, and changing the numbers while keeping the structure also changes it. Even under deterministic decoding and with identical mathematical content, models flip between correct and incorrect across equivalent formulations. Moving reasoning into executable Python code reveals hidden capability in some models but does not remove this sensitivity; it shifts failures to protocol violations and execution errors and adds latency and cost. If correct, benchmark accuracy conflates problem difficulty, surface representation, and interface design, so representation must be treated as a first-class evaluation variable.

Core claim

On a curated set of 85 algebra word problems expressed as story, symbolic, word-equation, and isomorphic variants, five LLMs show nontrivial accuracy gaps and flip rates across representations. Constraining models to output Python code and executing it locally improves accuracy for some models but not uniformly; representation gaps persist even when execution succeeds. Failures redistribute across interaction layers—protocol adherence, execution, and mathematical correctness—with different models failing at different layers. Statistically, the baseline-versus-code difference was significant for story and symbolic forms after Bonferroni correction but not for word-equations, and effect sizes

What carries the argument

The central device is a fully crossed evaluation protocol over representation variants, interaction condition, and model class. The key identity is the representation gap G(m,c), defined as the difference between a model's best and worst accuracy across shared representations (story, symbolic, word-equation); it quantifies representational sensitivity in a single number. In the code-augmented condition, failures are classified into three layers—protocol violations, execution failures, and math errors—so that correctness and system reliability can be tracked separately. This machinery makes representation sensitivity measurable as a first-class interface property rather than noise.

Load-bearing premise

The results rest on treating a single zero-temperature API call per problem as a stable measurement of a model's behavior; if repeated calls under identical settings vary as much as the differences between representations, the reported gaps and flip rates could partly be sampling noise rather than true representational sensitivity.

What would settle it

Run the same evaluation twenty times on the same models, API endpoints, and temperature-0 settings, computing per-representation variance and confidence intervals. If the within-representation flip rate across repeats equals or exceeds the between-representation flip rate, then the claimed representational sensitivity is not separable from sampling noise and the central claim collapses.

Watch this falsifier — get emailed when new claim-graph text bears on it.

If this is right

  • Single-form benchmarks can overstate stable reasoning: high accuracy may reflect sensitivity to a favored surface form rather than representation-invariant ability.
  • Benchmark designers should use controlled families of equivalent variants and report per-representation accuracy and gap, not only aggregate accuracy.
  • For deployed tutoring systems, adding code scaffolds is a tradeoff: it improves transparency and catches arithmetic errors, but introduces protocol and execution failure modes and increases latency and cost, so reliability-aware metrics like cost per correct answer matter.
  • Failure layers are qualitatively different for users; treating every wrong answer as a single 'incorrect' label hides system reliability differences, since a model can be accurate when execution succeeds but unreliable at executing at all.
  • The implication extends beyond mathematics to any domain with multiple surface realizations of the same structure, such as programming, legal reasoning, or instructional dialogue.

Where Pith is reading between the lines

These are editorial extensions of the paper, not claims the author makes directly.

  • If representation sensitivity is stable under repeated runs, a testable extension is that fine-tuning on multi-representation data should shrink the representation gap; this follows from the paper's framing but is not directly tested here.
  • The method could be extended to compare LLM representation effects against documented human representation effects: the extent to which code scaffolding makes LLM sensitivity more human-like is an open question beyond the paper's current scope.
  • The cost-per-correct-answer result implies that in high-frequency tutoring deployments, benchmark-optimized model selection may choose systems with poor real-world latency and cost profiles; deployments should optimize under the actual interaction condition.
  • A repeated-run variance check would turn the reported tradeoffs into quantitative reliability bounds; if within-representation variance matches between-representation variance, much of the 'sensitivity' could be sampling noise rather than genuine representational brittleness.

Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, simulated authors' rebuttal, and a circularity audit.

Referee Report

3 major / 6 minor

Summary. The paper investigates whether LLM mathematical problem-solving performance is robust to representationally equivalent problem formulations (story, symbolic, word-equation, and isomorphic paraphrase) under a direct-answer baseline and a code-augmented executable-reasoning condition. It evaluates five models through OpenRouter on a curated set of algebra word problems and reports accuracy, failure categories, latency, and cost. The central claim is that LLM performance is not invariant to representation or interaction design: representation sensitivity persists, reasoning scaffolds do not eliminate brittleness, and the interaction condition reshapes tradeoffs among correctness, reliability, latency, and cost.

Significance. The question is timely and the framing of representation as a first-class interface variable is well motivated by prior work in human problem-solving and HCI. The paper has concrete strengths: a controlled dataset with exact-answer grading, a crossed model-by-representation-by-interaction structure, local execution of generated Python with explicit protocol/execution/math failure categories, and latency and cost-per-correct-answer analyses that go beyond accuracy. The authors also provide an explicit dataset link and describe logging, retries, and resumption. If the central empirical claims are properly quantified, the results would support a valuable shift toward representation-aware evaluation. The current manuscript, however, does not yet provide the statistical grounding needed to anchor those claims.

major comments (3)
  1. [§4.1, Eqs. (1)-(3), Figs. 1-2] The claim that representational sensitivity cannot be attributed to sampling variability is not supported by the methodology. Each cell is a single API call at temperature 0 through OpenRouter (Section 3.5), and OpenRouter-based inference does not guarantee bitwise reproducibility across calls; provider routing, batching, and model updates can induce variation even at zero temperature. No repeated runs, confidence intervals, or within-model paired tests across representations are reported. A single binary response per problem-representation cell has Bernoulli variance, and the Fig. 1 caption itself notes that 'observed gaps are modest.' The max-min gap G(m,c) in Eq. (3) and Fig. 2 are presented without uncertainty bands, so the magnitudes that motivate the 'substantial representational sensitivity' claim cannot be distinguished from sampling noise. I request repeated runs or a documented
  2. [§4.1, chi-square tests] The only inferential tests reported compare the baseline vs. code-augmented interaction conditions for each representation (χ² and Cramér's V of 0.032–0.073). These tests do not evaluate the paper's central claim that accuracy differs across representations of the same problem. To support the RQ1 conclusion, the authors need direct tests of equality of story, symbolic, and word-equation accuracies within a model, and for G(m,c). Please also report the number of problems in the analytic subset P for Eq. (1) after exclusions, and per-model sample sizes, since all cells are currently opaque.
  3. [Abstract and §4.1] The abstract's characterizations 'nontrivial flip rates' and 'systematic regressions' under isomorphic reformulations are load-bearing but never defined numerically. No flip-rate statistic appears anywhere in the paper, nor do magnitudes or prevalence of isomorph regressions. Please define flip rates (e.g., proportion of problems for which a model is correct in one representation and incorrect in another), report them per model/condition with confidence intervals, and give regression magnitudes with effect sizes for isomorphs. Without these numbers, the central claims of the paper cannot be evaluated.
minor comments (6)
  1. [§3.1 vs §3.2] The design is described as 'fully crossed' over problem representation, interaction condition, and model, yet the code-augmented condition omits the isomorph representation. Please describe it as a crossed design with a partially nested representation factor, or include isomorphs in both conditions.
  2. [Fig. 9 caption vs §4.4] Fig. 9 caption says 'model level for code-augmented conditions' but §4.4 states the figure 'superimposes baseline and code-augmented results.' Please align the caption and text.
  3. [Fig. 1 caption] The caption mentions a truncated y-axis. Please show the axis break explicitly or use a full-scale plot, since truncated axes make the 'modest gaps' visually ambiguous.
  4. [§4.2] 'Gemini 2.5 Pro notably exhibits a disproportionate number of protocol violations' is based on inspection of Fig. 5; consider adding proportions and a simple significance test to support 'disproportionate.'
  5. [§3.2] '85-word problems' should be '85 word problems' to avoid ambiguity.
  6. [Reference [15]] Reference [15] points to a GitHub repository; if the dataset is intended to support reproducibility, a versioned release or citation with a DOI would be more stable.

Circularity Check

0 steps flagged

No circularity: the paper reports direct measurements; no fitted parameter is renamed as a prediction.

full rationale

This is an empirical evaluation rather than a derivation. The central quantities (per-representation accuracy A_r, representation gap G, failure shares, latency, and cost) are defined directly from logged API outcomes (Eqs. 1-3), not fitted to the outcomes and then 'predicted' back. No parameter is estimated from a subset and then verified on a dependent quantity; no uniqueness theorem or normalization is imported to force a result. The only self-citation ([25], used in the model-grouping paragraph of §3.4) is not load-bearing: the central claims about representation sensitivity, flip rates, failure redistribution, and cost/latency tradeoffs rest on the OpenRouter measurements and the external problem-family source [7], not on [25]. The paper's interpretation that representation gaps are not sampling artifacts is an inference from temperature-0 decoding, which is an assumption about API determinism rather than a circular reduction; any weakness there is a statistical/correctness risk, not a circularity. Potential objections (single-pass cells, no confidence intervals, undefined flip-rate threshold) concern evidentiary strength, not constructional equivalence. Accordingly, no circular step is present.

Axiom & Free-Parameter Ledger

0 free parameters · 4 axioms · 0 invented entities

The study introduces no fitted free parameters and no new physical or conceptual entities in the sense of invented mechanisms. Its load-bearing assumptions are empirical: variant equivalence, determinism of API decoding, correctness of ground truths, and faithful model routing. These are reasonable but unverified for the specific execution environment.

axioms (4)
  • domain assumption The story, symbolic, and word-equation variants of each problem are mathematically equivalent and differ only in surface representation.
    Section 3.2 states each problem is instantiated in multiple representational forms; the entire inference from accuracy differences to representation sensitivity depends on this equivalence.
  • domain assumption Temperature-0 decoding through OpenRouter is deterministic.
    Section 3.5 fixes temperature to zero and treats outputs as deterministic; without repeated runs, representation gaps could be confounded with sampling noise.
  • domain assumption Ground-truth answers in the dataset are correct and exact-form grading captures all valid correct answers.
    Section 3.2 specifies exact ground truths and strict output contracts; if equivalent valid forms are rejected (e.g., equivalent fractions or decimal representations), measured accuracy could understate model capability.
  • domain assumption OpenRouter API calls reliably expose the named model versions without provider-side routing or update variability.
    Section 3.5 uses a single OpenRouter framework; if different model versions are served across calls, model-level comparisons and failure profiles could be confounded.

pith-pipeline@v1.3.0-alltime-deepseek · 9999 in / 10082 out tokens · 93980 ms · 2026-08-02T07:59:05.251137+00:00 · methodology

0 comments
read the original abstract

Large language models (LLMs) are increasingly evaluated on mathematical problem solving, yet prior work often treats representationally equivalent formulations as interchangeable and conflates reasoning errors with interface failures. This paper investigates representation robustness in LLM-based mathematical problem solving by systematically varying surface representations of the same underlying problems, including story problems, word-equations, symbolic equations, and isomorphic paraphrases. Using a curated dataset of mathematically equivalent problems, we evaluate five contemporary LLMs under a direct answer generation condition. We find substantial representational sensitivity: models frequently change correctness across equivalent formulations, with nontrivial flip rates across story, symbolic, and word-equation variants. We also observe systematic regressions under isomorphic reformulations, showing that even subtle paraphrase-level changes can degrade performance despite preserved mathematical structure. We then evaluate a code-augmented condition in which models externalize reasoning as executable Python code that is run locally for validation. This interface reveals strong latent reasoning capability in some models that perform poorly under direct prompting, but it does not uniformly improve robustness. Instead, failures shift across interaction layers, from opaque reasoning errors to protocol violations and execution failures. Even when executable reasoning succeeds, representation sensitivity often persists. Overall, our results show that reasoning scaffolds do not eliminate representational brittleness, but expose new tradeoffs among correctness, reliability, latency, and cost. We argue that representation should be treated as a first-class interface design variable in LLM evaluation and deployment, especially for AI-assisted problem-solving systems.

Figures

Figures reproduced from arXiv: 2607.20520 by Diego Zapata-Rivera, Edith Aurora Graf, Liang Zhang, Sagnik Nath.

Figure 2
Figure 2. Figure 2: Representation Gap G(m,c) by Model (Max Min across shared representations). Gap is computed as the difference between the maximum and minimum accuracy over story, symbolic, and word-equation variants. To assess whether the observed representational differences between interaction conditions are statistically reliable, we further conducted representation-specific chi￾square tests comparing baseline and code… view at source ↗
Figure 6
Figure 6. Figure 6: Accuracy vs Execution Reliability (code-augmented only) 4.3 Cost and Latency as Interaction Consequences (RQ4) Accuracy alone does not capture the user or system-level consequences of different interaction conditions [PITH_FULL_IMAGE:figures/full_fig_p012_6.png] view at source ↗

discussion (0)

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Reference graph

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