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Withdrawn from ICLR 2027

Long-Horizon Insurance Credit: Measuring Preventive Actions in Long-Horizon Tasks

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

AI agents can sometimes make themselves more reliable by taking preventive actions, such as saving a checkpoint or writing down useful information. These actions may look useless when everything goes smoothly, but they matter a great deal if the agent later loses context, forgets earlier work, or encounters a failure. This makes preventive actions hard to evaluate: credit signals evaluated only under clean conditions can miss this value, while simple fault-injection tests can also give a misleading picture. We introduce Long-Horizon Insurance Credit to estimate the value of these actions. It measures how much an action helps when failures occur, then subtracts what the same action changes when nothing goes wrong. To estimate this quantity fairly, we compare matched runs driven by the same sampled fault tapes. In a controlled setting where the true answer is known exactly, insurance credit identifies useful preventive actions accurately (Kendall's τ = 0.92), while standard clean-run methods miss them. We then test it on three tool-use benchmarks: ToolMaze, BFCL, and ALFWorld. We find that a single checkpoint can be extremely valuable, but current LLM agents usually fail to benefit from it because they rarely check the saved workspace after losing context. When the system makes them look once, much of the benefit returns, with insurance credit ranging from 6.4 to 20.8 percentage points relative to a length-matched placebo on ToolMaze and BFCL. This suggests that the main bottleneck is discovery rather than use: the agents can often exploit saved information once they look, but they rarely choose to look on their own. In this regime, system-level recovery design appears more reliable than relying on larger models alone.

Primary area:
foundation or frontier models, including LLMs
Keywords:
LLM Agents, Credit Assignment, Agent Robustness, Counterfactual Evaluation, Long-Horizon Tool Use

Reviews

Among:
Shape:
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_AUViOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

I found this paper quite difficult to follow and gave up halfway through, so to be honest I'm not even very sure what the paper was proposing, but my understanding is that it is attempting to quantify the ability of agents to take proactive preventative actions towards failures that appear later in the trajectory.

Critical strengths

The paper was quite opaque, so I didn't get far enough to understand the strengths.

Critical weaknesses

The paper is very difficult to follow.

Section 3 is an example of this, for instance just to grab a few phrases in the section that are not easy to follow:

  1. a cost-matched control b
  2. exogenous fault tapes
  3. the clean condition
  4. Our primary object is the profile of ∆ins over fault types and severities (these are just in the first few paragraphs).

Furthermore, while section 3 did have some equations, they were not tied back to what we already know about this sort of long-term credit assignment from the RL literature, which would've been helpful for clarity.

The intro is also quite difficult to understand from a motivation perspective.

I think that the paper needs a clear pass for clarity before the readers will be able to follow what the authors are trying to say.

Questions for authors

None in particular.

Reviewer_Zus3OpenReview ↗
Rating
2(−1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

Preventive actions like saving checkpoints provide no benefit in clean runs, making them invisible to standard credit assignment methods. This paper introduces Long-Horizon Insurance Credit, a difference-in-differences metric that isolates an action’s protective value by subtracting its clean-run effect from its fault-conditioned effect. To measure this without confounding, the authors pair rollouts using frozen, semantically keyed fault tapes and compare against four controls, including a length-matched placebo artifact.

Testing across a synthetic oracle (BASINDAG) and three tool-use benchmarks (ToolMaze, BFCL, ALFWorld), they show that checkpoints offer massive potential recovery value, but autonomous LLMs harvest essentially none of it because they almost never inspect the workspace post-restart. Forcing a single harness-level read recovers +6.4 to +20.8 pp. Because prompt nudges fail in realistic environments and LoRA fine-tuning is seed-unstable and collapses with scale, the authors conclude that context recovery is an affordance discovery problem best solved in the runtime harness rather than left to the model.

Critical strengths
  1. The paper demonstrates concretely how naive fault injection misleads, through the placebo-matched false positive and the keying-dependent sign flip. It also validates ranking and decision quality against exact ground truth.

  2. Across three lineages and four models, agents leave large recovery value uncollected, while one harness-imposed read recovers a significant share. This yields an actionable architectural recommendation: recovery inspection needs to be handled programmatically by the runtime harness rather than left to autonomous agent initiative.

Critical weaknesses
  1. The discovery-bottleneck claim is overstated: On ToolMaze and BFCL, imposed reads realize only about 15–35% of the available value, so conversion is also a major bottleneck. This is never normalized by agent competence. Also, some contrasts appear without any reads, such as BFCL GPT-4.1-mini at +6.2 pp. The sample size is small with only 24 BFCL tasks and the ALFWorld informative stratum is only 5 games.

  2. The estimand’s added value and scope are narrower than framed: The synthetic 0/82 detection failure of clean baselines is true by construction since test actions were chosen to be clean-neutral. In stationary deployments, fault-augmented Q matches or outperforms insurance credit. Furthermore, large empirical gains depend on an engineered "sharp" late-fork configuration, and the informative set shrinks to 5 games in ALFWorld when alternative recovery exists.

Questions for authors
  1. What is the imposed-read recovery credit when normalized against each agent's clean-condition success ceiling?

  2. How to explain positive contrasts in near-zero read regimes (BFCL GPT-4.1-mini +6.2 pp at 0.8% reads; ToolMaze L3 +3.3 pp at 0 reads) and the negative placebo-vs-no-op effect (-6.2 pp)?

  3. Given that 19/288 pairs had divergent fault exposure due to branches skipping target tools, how should practitioners interpret insurance credit when tool execution branches diverge heavily?

Reviewer_t1tfOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary
  • The paper studies how to give credit to what it calls "preventive actions", such as saving a checkpoint, which only pay off if something goes wrong later
  • It proposes to measure how much an action helps when failures happen, minus how much it helps when nothing goes wrong, and to compare the action against a fake placebo checkpoint
  • Experiments use three existing agent benchmarks, modified so that the agent's memory is wiped in the middle of a task
  • The obtained results suggest that agents almost never look at the saved checkpoint after the wipe on their own, while forcing them to look improves task success by about 6-12 percentage points
  • In this setup the agent does not decide to save the checkpoint and is not told that it exists, as the system saves it instead, so the paper effectively studies recovery from saved work rather than whether agents choose to save it
Critical strengths
  • The paper is open about its own mistakes. An early experiment showed a gain of about 18 percentage points from checkpoints, but a fake placebo checkpoint produced exactly the same gain, and the authors report it as a false positive
  • Its testing setup is careful. Each comparison includes a placebo checkpoint, a do-nothing action of equal cost, a run without failures and a version where the checkpoint exists but cannot be read. In a simulated world where the true answers are known, the method gets the answer right 92% of the time, and pairing the runs cuts the noise by 89%
  • The main pattern holds across two benchmarks and four models. Agents almost never read the saved checkpoint on their own, while a forced read raises success by about 15-20 percentage points on the ToolMaze benchmark
  • A small controlled test shows that where the agent is told about saved state matters. Saying "your notes survive restarts" in the tool description barely changes behavior, while saying the same thing in the restart message raises read rates from close to zero to well over 90%
  • The authors also find that the content of the checkpoint matters. Recording which steps were already done is what helps, while plain notes of facts help little or not at all, because the agent then repeats work it has already done
Critical weaknesses
  1. The paper's main conclusion, that "the main bottleneck is discovery rather than use", does not seem to match its own numbers. On ToolMaze, the perfect recovery strategy gains about 56 percentage points from the checkpoint, while forcing the agents to read it gains only about 20, roughly a third. On BFCL, one Gemini model reads the checkpoint in 70% of episodes and gains only about 6 points. Most of the value therefore seems to be lost after the agent has already seen the checkpoint, which makes this look like a use problem rather than a discovery problem, and makes it hard to read the conclusion as strongly as it is stated

  2. The paper never lets the agent decide to save anything. The system writes the checkpoint and then removes it from the agent's memory, as §5 states: "the write was imposed by do(a), and the conversational trace containing it is gone". The agent has no reason to believe anything was saved, so it will naturally not look for it, and the low read rate is close to what one would expect. The introduction claims that agents fail to read "the workspace they themselves wrote", which seems to contradict this setup

  3. The headline gains appear to be measured against the wrong comparison. Appendix C says the pre-registered main comparison is against the do-nothing action, but Tables 2 and 4 compare against a junk placebo checkpoint instead, as their captions state. Section 5 shows that reading the junk itself hurts success, so beating the placebo makes the real checkpoint look better than it actually is. Reporting the actual comparison against the do-nothing action would help here

  4. It is unclear whether the large gains come from what was measured or from how the authors built the environments. On BFCL, the memory wipe is set up so that "the crash lands on the artifact write". On ALFWorld, the step budget is set so that starting over exceeds the budget in every game. The results then follow directly from these choices, and calling them results on three public benchmarks hides how much of the setup is the authors' own construction

  5. The method's key new idea, subtracting the benefit seen when nothing goes wrong, does not seem to matter in any experiment. All actions studied have zero effect in failure-free runs, so the subtraction always removes zero and the 0/82 detection result for standard methods is true by construction, as the Table 1 caption concedes. A simple existing baseline also detects 82/82 and even makes better decisions, but it is left out of the decision experiment in Table 8. This makes it unclear what the new measure adds in practice

  6. The check meant to show that the gains come from reading the checkpoint is rather weak. In the workspace-off condition every branch fails, including the branch that never uses the workspace, so a zero difference is guaranteed. On BFCL, GPT-4.1-mini still gains about 6 points while reading the checkpoint in only 0.8% of episodes. Part of the measured gains might therefore come from something other than the saved content, the same effect that produced the paper's earlier false 18-point result

Questions for authors
  1. Among the episodes where the read was imposed, how often did the agent then skip the steps the checkpoint marked as done, and how often did it re-execute them anyway? Splitting the imposed-read episodes into stages (read, understood which steps were done, resumed correctly, succeeded) would show where the remaining roughly 60-70% of the available value on ToolMaze is lost

  2. In the hardened ToolMaze, each data source has a session-level request budget. A real checkpoint would plausibly use some of that budget and lower clean success, but here the write is imposed via do(a) and cost-matched against the no-op. Have the authors considered a variant where writing the checkpoint uses up a tool call or some of the budget? This is exactly where the clean effect can become nonzero, and also where insurance credit and fault-augmented Q would likely rank actions differently, which would show how much the clean subtraction contributes

  3. Would it be possible for Tables 2 and 3 to report checkpoint vs. no-op and placebo vs. no-op for each language model row, alongside checkpoint vs. placebo? Section 5 shows that the placebo itself can hurt (about minus 6 points on BFCL), so seeing all three contrasts side by side would tell readers how much of the 6-20 point gains comes from the checkpoint and how much from the junk artifact hurting performance

  4. Since the reference policy is scripted and could likely be rerun cheaply without any language model cost, would the authors consider sweeping one or two of their design choices, such as where the wipe lands relative to the checkpoint, the step-budget slack in ALFWorld or the fork point in ToolMaze? This would show how the 55-point and 100-point values change across settings, and whether the value at stake is a general property or depends on the specific configuration chosen

  5. The GPT-4.1-mini result on BFCL is curious, as it gains about 6 points while reading the checkpoint in only 3 of 382 post-restart episodes. Could the authors split this contrast into pairs where a read happened and pairs where none did, using the existing episodes? It would be interesting to know where most of the effect comes from, and it would also show whether the "context flavour" effect behind the 18-point result in Appendix F is still present in the final protocol

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

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