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Under review as a conference paper at ICLR 2027

Latent Programming Horizons in Coding Agents

Abstract

A coding agent solving a software-engineering task spends dozens of steps reasoning, editing code, and running tests, yet little is known about what the underlying language model internally represents about the program it is working on. We show that the residual streams of language models under coding agents linearly encode properties of the evolving program: a logistic-regression probe on hidden states is able to decode whether the current code parses, passes its test suite, reduces the number of failing tests, and introduces regressions, reaching AUC up to 0.83 for correctness across two models and two benchmarks. Our second finding is more surprising: these representations run ahead of the agent's own edits. Probes trained to predict the outcome of future edits (before they are materialized and written on disk) achieve performance above chance up to roughly 25 steps in advance. We call this the agent's latent programming horizon. As a proof of external validity, we show that the probes transfer across benchmarks without retraining. Our positive results open calls for more research in mechanistic interpretability of coding agents.

Primary area:
interpretability and explainable AI
Keywords:
coding agents, interpretability, probes, large language models, agents

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
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Paper summary

This paper studies whether LLMs driving coding agents linearly encode properties of the program they iteratively edit. It collects mini-swe-agent trajectories from two open-weight models on SWE-Bench-Verified and SWE-Bench-Pro. Each intermediate code version is labeled by execution for well-formedness, full correctness, partial correctness, and regression. Logistic-regression probes on residual-stream activations reach up to about 0.83 AUC, peak in middle layers, and transfer across benchmarks. Probes trained to predict labels k steps ahead stay above chance up to k = 25, which the authors interpret as a “latent programming horizon” analogous to look-ahead in game-playing networks.

Critical strengths

[S1] Timely, practically relevant setting. It moves correctness probing from single-shot snippet generation to multi-step agentic repair on real repositories, where program state changes over time and is only partially observed.

[S2] Execution-grounded labels at scale: every intermediate version is checked out and run, across 22.7k trajectories and 1231 tasks. This pipeline could be a useful resource if released.

[S3] Partial correctness and regression are labels defined relative to the initial repository state. They are meaningful only in the agentic setting and are rarely studied.

[S4] Task-level splits, a layer-wise analysis that is consistent across models, and cross-benchmark transfer give some robustness to the k = 0 results.

[S5] Potential downstream value for cheap agent monitoring and early failure detection, and as a starting point for steering or causal work.

Critical weaknesses

[W1] Limited methodological novelty. Linear probes with a shuffled control, correctness probing, and future-state probing are all established in existing literature. The paper mainly applies them to a new setting without new analysis tools or causal interventions, so its value only rests on the strength of its empirical results.

[W2] No controls for surface information. The agent’s context directly contains test outputs (e.g., “1 failed” / “3 passed”), so probes may simply read recent tool output rather than a latent program representation. A token-level shuffled-label control is very weak. Needed baselines include classifiers on recent tool-output text, step index, and task identity, plus task-level permutation.

[W3] The “programming horizon” is likely confounded. Labels are piecewise-constant, with a median of only about 2 edits per trajectory, so the label at t+k usually equals the current label. Near k = 50, under the 100-step cap and >= 50-step filter, the target is essentially the final task outcome, which task difficulty can predict. Maybe consider to evaluate only on positions where the label flips between t and t+k, and compare against current-label and task-prior baselines. Without this, claims of planning or look-ahead are overstated.

[W4] Evaluation and reporting issues. AUC is computed over highly correlated token positions, so long trajectories dominate. No confidence intervals, seed variance, or per-edit and per-trajectory metrics are given. The practical utility of a ~0.8-AUC probe is also not discussed.

Questions for authors

What are the concrete implications or potential use cases of the empirical findings demonstrated in this paper? The paper needs to answer why do we need to know these results and how to leverage them to do something.

5 comments

We thank the reviewer for their time and useful feedback. We agree that the horizon was confounded, and we followed the suggested evaluation (see the general response). This evaluation still shows information beyond persistence and trajectory phase, and, as the reviewer suspected, a large part of it reflects the eventual outcome. We will release the code and data after the review period.

W1: Limited methodological novelty

We partly agree. The probing methodology is standard. We see the contribution being novel from three different angles:

  • by looking at multi-step agents on real repositories, where the program is only partially observed;
  • by using execution-grounded labels for every program version, including partial correctness and regression, which only exist in the agentic setting;
  • by having a decomposition of the future-state signal into persistence, trajectory phase and the eventual outcome, each with its own control (updated Section 4.2).

W2: Controls for surface information

We added a trajectory-level permutation, step-index and relative-position baselines, language-only and repository-only baselines, and an evaluation on held-out repositories (Section 4.1, Appendix A.4).

On test outputs in context: right after an edit that changes a label, before any tool runs, the probes mostly report the old label (App. A.6). This suggests that the hidden states do not yet fully reflect the effect of an edit before tools such as tests run, which we now state in the Limitations.

Please see the general response.

W3: The horizon is confounded

We agree, and we followed the suggestion.

  • We now evaluate only states where the property does not currently hold, so a probe can only score above 0.5 if it predicts a change.
  • Over all states, the true current label is as good as or better than the probe (better in 28 of 72 settings, equal in 38, see Appendix A.5).
  • The final label of the trajectory, used as a prediction, is higher than the probe in 65 of 72 settings. With the final label fixed, the probe's median AUC margin over the baselines drops from 0.11 to 0.04 (Section 4.2).
  • A baseline on the hidden state before the agent's first action explains only part of this: it lowers the margin to 0.08, although the probe then beats every baseline in 17 instead of 56 settings (App. A.5).

These results show that a large part of the signal in the hidden states is linked to the eventual outcome of the trajectory. Please see the general response.

W4: Evaluation and reporting

  • The best-layer AUCs (Figure 3), the comparisons with baselines (Sections 4.1 and 4.2, Appendices A.4–A.6) and the transfer drops (Section 4.1) now have 95% task-level bootstrap intervals (1,000 resamples of test tasks), so correlated tokens from the same task are resampled together.
  • Per-trajectory and per-edit metrics: we recomputed the k=0k=0 AUCs in two ways. First, with each trajectory weighted equally. Second, with one data point per program version (the probe's mean score over the version, against its label), so each edit counts once. Both are as high as or higher than the pooled AUC in all 16 settings: the per-trajectory AUC is significantly higher in 10 of 16 settings, the per-version AUC in 9 of 16, and neither is significantly lower in any. Long trajectories therefore do not inflate the results. We also reweighted the horizon analysis of Section 4.2 so that each trajectory counts equally. The probe still beats the current-state probe, the trajectory shuffle and the position baselines (all four at once in 62 of 72 settings, 56 pooled), and no baseline is significantly better in any setting. Fixing the final label lowers its median margin from 0.11 to 0.06 (0.04 pooled).

Q: Concrete implications and use cases

The main usefulness of our study is in improving the understanding of what is represented about programs internally in models while they act as coding agents. We believe this is a necessary step towards building more explainable and safer agents.

Beyond that, we see two concrete use cases that could use our results:

  • Our probes read, from hidden states that the agent already computes, whether the current program passes its tests, carrying information about whether the trajectory will reach a correct program. This could flag trajectories that are unlikely to succeed, for early termination or triage, at almost no extra cost.
  • The probe directions could be useful as candidate steering vectors in future work.

Thank you for your reply! I think the rebuttal responses address many previous concerns. Though I still have the following questions and concerns about this work:

  • For decoding current-state properties, how do the probes compare with simpler alternatives, e.g., directly asking the model at a given step whether it believes the current version correctly resolves the issue? This would clarify how much the probes capture beyond what the model can verbalize, to what extent they are consistent, or which one is better.
  • I understand that the paper is positioned as an empirical study for better understanding, and I acknowledge the value of such contributions. Still, I believe even one or two setups evaluating whether the findings are useful in practice would make the work more complete and convincing. An honest analysis would be valuable even if the gains turn out to be limited. As a reader, it is not intuitive to understand how strong the signals provided in this paper are.

Thanks for the reply! We're happy to answer:

1. For each test trajectory, we sampled 5 steps evenly spaced over the trajectory plus the last step of the trajectory. At each sampled step, we appended the question "Stop and answer with one word, yes or no: does the current code in the repository correctly resolve the issue?" to the agent's context and computed P(yes)/(P(yes)+P(no)) from the next-token distribution. This results in 16,035 labelled states with both trained full correctness probes and a prompt comparison. The table below compares the AUC from both methods with 95% CI.

RunAskingProbeDelta (Probe - Asking)Spearman
Laguna/Verified0.880.86−0.022 [−0.035, −0.009]0.81
Laguna/Pro0.870.83−0.042 [−0.068, −0.016]0.78
Qwen/Verified0.860.89+0.030 [+0.012, +0.048]0.77
Qwen/Pro0.830.87+0.036 [+0.002, +0.075]0.66

The results show that both scores are correlated and have similar AUCs. We believe these results show the same information being decoded in different ways. In our probes, the linear projections decode the probability directly from the hidden states. In the asking prompt mode, the entire model's forward pass does a similar job first building up the representation in the residual stream and then constructing the answer (as token logits).

2. While the main goal of our study is to improve the understanding of the internal representations of LLMs when operating as coding agents, we believe that, as the community develops better understanding of these representations and develops better probing mechanisms, these could be useful, for example, in monitoring progress of agents.

As a pilot experiment, we tested whether the probe helps to choose among attempts. In our test dataset each task has ~10 atempts each. For each attempt, we computed the probe score at its last step and compared it with the ground-truth evaluation.

  • Best-of-n. In this scenario, only one solution can be chosen out of n attempts. With all attempts, a random pick resolves 31.8% and the ground-truth oracle 45.2%. The gain over a random pick is +1.1 points [−0.9, +3.1] for the probe and +1.6 [+0.7, +2.6] for the baseline "last test run passed". With 4 attempts, the gains are +2.2 [+1.2, +3.3] and +1.5 [+0.9, +2.3].
  • Ranking attempts on the same task. The AUC is 0.67 for the probe, 0.60 for the test-run rule, and 0.48 for a classifier on the state before the first action. The probe score therefore depends on the attempt and not only on the task.
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Paper summary

The paper studies what coding agents internally represent about the program they are editing. The authors run mini-swe-agent with two open-weight models (Qwen3.6-35B-A3B and Laguna-XS.2) on SWE-Bench-Verified and SWE-Bench-Pro, collecting about 22.7k trajectories. They train per-layer linear probes on residual-stream states to decode four binary properties of the current program: ● Well-formedness (parses or compiles) ● Full correctness (passes the test oracle) ● Partial correctness (fewer failing tests than at the start) ● Regression (breaks previously passing tests) Probes reach AUC up to about 0.83 for semantic properties, peak in middle layers, and transfer across benchmarks with modest drops. The authors also train probes to predict these properties k steps ahead. AUC stays above 0.5 out to roughly k=25, which they call a “latent programming horizon.” Validation uses a shuffled-label control, task-disjoint splits, and cross-benchmark transfer.

Critical strengths
  • Realistic setting at reasonable scale: Prior correctness-probing work largely examines single-shot function generation. This paper instead probes multi-step agentic trajectories on real repositories, with task-disjoint splits, two models, two benchmarks, and layer-wise sweeps. The inverted-U pattern across layers for semantic properties (Figure 4) and their relatively strong predictive performance across model/benchmark combinations make the k=0 results credible as descriptive findings. Cross-benchmark transfer also provides useful evidence that at least some of the decoded signals generalize beyond individual tasks.

  • Clear experimental setup and acknowledgment of limitations: The paper explicitly acknowledges that decodability is not causality and that its scope is limited to two models and one agent scaffold. It reports the weak well-formedness results on Verified and the substantial cross-benchmark degradation for this property rather than omitting them. The appendix also includes a shorter-horizon analysis using a broader trajectory population, which helps address concerns about the trajectory-length filter.

Critical weaknesses
  1. The experiments demonstrate decodability of program properties, but do not sufficiently distinguish an internal program representation or planning from simpler explanations.

Definition 1 describes latent program representations as being captured "independently from the surface tokens," but the experiments do not establish that independence. a. The shuffled-label control permutes labels across individual hidden states, removing trajectory structure. While useful as a sanity check, it does not rule out contextual confounds or implement the control-task methodology of Hewitt & Liang (2019). A trajectory-aware control would be more informative. b. Important baselines are missing, including prompt-only, step-index, and text-only predictors. Since the agent may have already observed test results, probes could exploit contextual signals rather than a distinct program representation. Performance broken down by position relative to tool outputs would help clarify this. c. On SWE-Bench-Pro, well-formedness has a 52-57% positive rate, and cross-benchmark transfer drops by roughly 0.2 AUC at several layers. The probe may be exploiting language or repository-specific features rather than general well-formedness. Language-controlled evaluation would help distinguish these explanations. d. The programming-horizon claim is not sufficiently supported. Labels persist between edits, so current-state information alone could predict future labels without planning. No current-label baseline tests this possibility. Moreover, the horizon is measured in agent steps rather than edits. Given that Table 1 reports a median of only two edits per trajectory overall, the authors should report how many actual edits occur within the lookahead windows. Predicting 25 steps ahead does not necessarily imply anticipating future program changes.

Consequently, the claim that the agent "anticipates future programs before they are materialized" goes beyond what the current experiments establish. The results demonstrate future-label predictability, but not necessarily foresight about future edits.

  1. The statistical evidence and scope do not fully support the strength of the conclusions, particularly for long-horizon prediction.

The paper reports approximately 22.4M hidden states, but these observations are highly correlated. States are sampled every five tokens, while labels remain constant between edits, and multiple trajectories are generated for the same tasks. Although task-disjoint splits prevent trajectories from the same task appearing across splits, token-level observations remain highly correlated. Reporting task-level bootstrap confidence intervals would better establish the reliability of the results.

The long-horizon analysis is also based on a restricted population. The k≤50 experiments exclude trajectories shorter than 50 steps and retain only around 40-60% of trajectories (Figure 7). The appendix includes k≤15 results using a broader population, which is useful, but this does not establish that the longer-horizon findings generalize to shorter trajectories.

The predictive effects are also modest at longer horizons, although they vary substantially across benchmarks. For example, full-correctness AUC is approximately 0.55 on Verified and 0.65 on Pro at k=25 for Laguna-XS.2, with later plateaus around 0.52 and 0.60 respectively (Figure 6). Without confidence intervals, repeated-seed results, or task-level bootstrap estimates, it is difficult to assess the reliability of these effects or establish a meaningful horizon boundary at 25 steps. More importantly, above-chance performance alone does not establish additional predictive information beyond current-state persistence. Without uncertainty estimates or comparisons against a current-label persistence baseline, it is unclear whether these results provide meaningful evidence of future-state anticipation or merely reflect predictable continuation of the current state.

Finally, the evaluation covers only two models, one agent scaffold, and two related issue-to-patch benchmarks. This is a reasonable initial scope, but does not by itself justify the claim of "strong external validity." The two qualitative trajectories in Figure 16 are explicitly illustrative rather than quantitative evidence. The paper would be stronger with an analysis showing whether the probe predicts the outcome of an actual future edit beyond what can already be inferred from the current program state and observable trajectory.

Overall, the current-state probing results are meaningful, but the evidence does not adequately establish the stronger interpretation that coding agents maintain independently identifiable program representations or anticipate future program states through planning.

Questions for authors

The following could change my assessment.

  • Can the authors compare the probes against prompt-only, step-index, and text-only baselines, along with a control preserving trajectory structure? Please also report performance relative to tool outputs and control for language or repository identity in Pro well-formedness.
  • Can the authors compare lookahead predictions against the true current label as a persistence baseline and evaluate predictions across actual edits? Task-level bootstrap confidence intervals would help assess the reliability of the horizon results.
  • Why does Figure 6 report 1.1M hidden states for Laguna-Verified but only 145k for Pro, despite similar full dataset sizes? How many tasks and trajectories remain after filtering, and how do these results compare with the broader k≤15 analysis?
  • Given Sui et al. (2026)'s prior work on probing and steering coding agents, can the authors more precisely distinguish their contribution and clarify the novelty of the proposed monitoring and steering applications?
1 comment

We thank the reviewer for the detailed review. We agree that the submitted experiments showed decodability, but not an independent program representation or planning. We have added the requested controls and narrowed our claims (see the general response). The program properties remain decodable above these controls, including the trajectory shuffle the reviewer asked for.

W1: Definition 1 and independence from surface tokens

We agree. Definition 1 is now operational.

a. Trajectory-aware control. We added a trajectory shuffle. See general response and the updated Sections 4.1 and 4.2.

b. Prompt-only, step-index and text-only baselines; position relative to tool outputs.

We added a step-index baseline (Section 4.2), a prompt-only baseline (the hidden state before the agent's first action; App. A.4 and A.5), and an evaluation right after edits, before any tool runs on the new program (App. A.6); see the general response. We did not add a text-only classifier, as the evaluation right after edits (App. A.6) tests this question more directly.

c. Language and repository on SWE-Bench-Pro.

We added language and repository controls in Appendix A.4. See the general response.

d. Horizon and persistence.

We agree, see the general response.

We also agree that the results do not show that the agent anticipates future programs through planning. We now claim only that hidden states carry information about whether a property will hold kk steps later, beyond the current state, position and trajectory phase, and that a large part of this information is about the eventual outcome of the trajectory.

W2: Statistical evidence and scope

Correlated states. We now report 95% task-level bootstrap confidence intervals (1,000 resamples of test tasks) for the best-layer AUCs (Figure 3), the comparisons with baselines (Sections 4.1 and 4.2, Appendices A.4–A.6) and the transfer drops (Section 4.1).

Population at k≤50k \le 50. The reviewer's estimate is right: 39–59% of trajectories have more than 50 steps, and 31–53% keep at least one state at k≤50k \le 50. The main analysis now uses k≤15k \le 15, where 79–91% of trajectories keep at least one evaluated state (Figure 6 counts trajectories longer than 15 steps instead).

Modest long-horizon effects. We agree. We removed "25 steps" and the long-horizon claims. All horizon results now have confidence intervals and are compared against the true current label, the current-state probe, a trajectory-phase control and position baselines (Section 4.2, Appendix A.5).

External validity. We removed "strong external validity" from Section 4.1.

Outcome of an actual future edit. We tested this by indexing the evaluation by future edits (Appendix A.5; see our answer to Reviewer HaQJ, Q3). The probes do not predict the outcome of the next edits better than the current label, the task and observable trajectory features. Section 4.2 shows that a large part of the signal concerns the eventual outcome.

Q1: Prompt-only, step-index and text-only baselines; trajectory-structure control; performance relative to tool outputs; language and repository control

See W1 a–c above.

Q2: Persistence baseline, evaluation across actual edits, and confidence intervals

Yes, see the general response.

Q3: 1.1M vs. 145k hidden states in Figure 6; tasks and trajectories after filtering; comparison with k≤15k \le 15

We identified a bug in our splitting logic that was responsible for this discrepancy, please see the general response.

Q4: Difference from Sui et al. (2026); novelty of monitoring and steering

We have updated the related work to better reflect the difference between our work and the one from Sui et al.

Sui et al. find residual-stream directions for overthinking and overacting, labelled per step by an LLM judge, and steer along them to improve resolve rates. We probe execution-grounded properties of each program version, such as whether it compiles and passes its tests, and whether they will hold kk steps later. We do not claim steering results, but we do see monitoring and steering based on program properties as future work.

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Paper summary

The authors collect 22,714 trajectories from two models running mini-swe-agent on SWE-Bench-Verified and SWE-Bench-Pro. They train linear probes on residual-stream activations to predict four properties: well-formedness, test-suite correctness, improvement relative to initial failing-test counts, and regressions. Current-state probes achieve ROC-AUC up to 0.83 for full correctness, and several signals transfer across benchmarks. Separate probes predict labels at future interaction steps, which the authors interpret as evidence of a “latent programming horizon” extending approximately 25 steps.

Critical strengths
  • Relevant research question. Studying internal representations during iterative repository editing extends correctness probing beyond isolated code generation. This is a useful setting for understanding and potentially monitoring coding agents.

  • Substantial experimental effort. Collecting trajectories, program snapshots, execution-derived labels, and activations across two models and two benchmarks represents a meaningful investment. The resulting dataset could be a valuable contribution if released.

  • Appropriate task-level splitting. Keeping trajectories from the same task in one split addresses an important source of leakage that a token-level or trajectory-level random split would introduce.

Critical weaknesses
  • The horizon experiment does not isolate anticipation of future edits.

This is my principal concern. Labels are explicitly carried forward until the next edit (§3.2), while the horizon is measured in interaction steps (§3.5). Table 1 reports a median of 52 steps but only two edits per trajectory. Consequently, a program property at step s+ks+k may simply be the property already true at step ss. If ys+k=ysy_{s+k}=y_s, predicting the future label requires no anticipation of a new program. Even when an edit intervenes, its outcome may preserve the same binary label. The reported decay with horizon is therefore also compatible with increasing distance from an autocorrelated current-state signal. The paper needs, at minimum:

  • A persistence baseline using the current true label, and a deployable baseline using the current-state probe score.
  • The number of intervening edits and frequency of label changes at each horizon.
  • Evaluation indexed by actual future edit events, with activations taken before the target edit is generated.
  • Evaluation conditioned on the current label, testing whether activations predict subsequent outcomes beyond persistence and observable trajectory features.
Questions for authors
  1. At k=25k=25, what fraction of evaluated samples have an intervening edit, and what fraction have a changed target label?
  2. How much do future-state probes improve over current-label persistence, current-state probe scores, and prompt-only predictors?
  3. Do the main findings survive evaluation restricted to activations before relevant execution feedback and before the target edit is generated?
  4. What operational and statistical criterion selects 25 steps as the programming horizon?
3 comments

We thank the reviewer for their time and feedback.

We agree with their principal concern regarding label persistence, and have addressed this in the general response. With the baselines and the evaluation the reviewer suggested, the probes still carry information beyond the current state. A large part of it concerns whether the trajectory ends with the property.

Q1: At (k=25), what fraction of evaluated samples have an intervening edit, and what fraction have a changed target label?

The tables below show the percentage of states with at least one edit in the next kk steps, and the percentage of states whose label is different in the next kk steps.

k=25k=25 (window kmax⁡=50k_{\max}=50):

Edit within 25 stepsLabel changed: Well-formednessFull CorrectnessPartial CorrectnessRegression
Laguna, Verified67%6%12%25%14%
Laguna, Pro72%9%6%11%6%
Qwen, Verified50%2%14%21%9%
Qwen, Pro37%7%5%5%1%

k=15k=15 (window kmax⁡=15k_{\max}=15):

Edit within 15 stepsLabel changed: Well-formednessFull CorrectnessPartial CorrectnessRegression
Laguna, Verified61%5%18%19%6%
Laguna, Pro76%8%4%6%4%
Qwen, Verified53%5%20%21%6%
Qwen, Pro63%5%7%8%1%

The two tables use different windows, so they cover different states: with kmax⁡=50k_{\max}=50, only trajectories longer than 50 steps contribute, without their last 50 steps.

At k=25k=25, 37–72% of states have an intervening edit, but only 1–25% have a changed label. This confirms the suspicion that labels at a given t+kt+k are typically the current label at time tt.

For this reason, Section 4.2 now reports an experiment among states where the property does not currently hold, and limits the main analysis to k≤15k \le 15. See the main response to all reviewers above for more detail.

Q2: How much do future-state probes improve over current-label persistence, current-state probe scores, and prompt-only predictors?

We have updated Section 4.2, as explained in the general response, to include the requested baselines. As a prompt-only predictor, we use a baseline on the hidden state before the agent's first action (App. A.5). Among states where the property does not currently hold, the probe beats it in 26 of 72 settings, and it never beats the probe. Added to the other baselines, it lowers the probe's median AUC margin from 0.11 to 0.08, and the number of settings in which the probe beats every baseline from 56 to 17 (Section 4.2). See the general response.

Q3: Do the main findings survive evaluation restricted to activations before relevant execution feedback and before the target edit is generated?

Mostly not.

Horizon (k>0k>0). As suggested in W1, we also indexed the evaluation by future edits (Appendix A.5). From hidden states taken before the next edit is written, a probe predicts the label after the next edit, and after the second and third. These probes do not predict the outcomes better than the current label, the task and observable trajectory features (they beat all of these in none of the 36 settings where the property does not yet hold, nor over all states). They also cannot tell which edit will fix the program. We have narrowed our claim accordingly.

Current state (k=0k=0). Mostly no. We added this evaluation in Appendix A.6. We take the tokens of the turn right after each edit, before anything runs on the new program. The probes stay above chance (95% CI above 0.5 in 14 of 16 settings). However, when restricted to edits that flip the label, the AUC is at most 0.50 in 12 of 16 settings. This suggests that the hidden states do not yet fully reflect the effect of an edit before tools such as tests run on the new program. We now state this in the Limitations.

Q4: What operational and statistical criterion selects 25 steps as the programming horizon?

We removed "25 steps" from the paper. Definition 3 now gives an operational criterion: the horizon reaches kk steps when the kk-step probe predicts the future property better than the current-state probe, a trajectory-phase control and position baselines. A probe is better when the 95% task-level bootstrap interval of the AUC difference is above 0. We apply this criterion for k≤15k \le 15 (Section 4.2).

We will release the code and data after the review period.

Thank you for the detailed rebuttal and substantial additional experiments. I appreciate the authors' willingness to investigate the concerns, report negative results, and narrow their claims. The new analyses largely address my original methodological objections.

However, I remain concerned about the strength of the central contribution. In particular, the edit-indexed evaluation does not demonstrate an advantage over all baselines in any setting, while conditioning on final trajectory outcomes substantially reduces the future-state probes' advantage.

I consider the current-state probing results, cross-benchmark transfer, and experimental effort meaningful contributions. The rebuttal has substantially improved the paper's methodological clarity. Nevertheless, I believe the remaining evidence supports a narrower contribution than the notion of a latent programming horizon suggests. For this reason, I am keeping my original rating.

Thank you for the reply. We agree that the evidence supports a narrower claim than the original one and have revised the paper accordingly in Section 4.2 and Limitations.

However, we would like to clarify how the final label ablation can be interpreted. During a trajectory, the final label is not known (to the agent and to the probes). The goal of including this ablation is to study what the signal recovered by the probes is about, not to provide a baseline. Our claim is that the hidden states carry information about future program states beyond what has already been done during the trajectories (probes beat current state and trajectory phase baselines in most settings), and that this information is in large part about whether the trajectory ends with a program that has that property and, to a smaller part, about when the program will have the property.

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

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