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Under review as a conference paper at ICLR 2027

Guardrails Must Be Earned: Fabrication-Resistant Compilation of Failure Traces into Anti-Pattern Skills

Abstract

Agents that compile failures into guardrail skills install whatever the compiler writes, and self-generated skills lower performance by 1.3 points where human-curated ones raise it by 16.2. Existing admission rules credit a candidate for plausibility or a later success, not for preventing the failure it names. We propose Earned Guardrails (EG), which treats a self-authored guardrail as a causal claim to be tested and bounds the share of fabrications that the library accumulates over a prespecified horizon. Typed failure compilation states what a candidate claims in a typed failure record, whose frozen matcher decides when a replay counts as the same failure, pinning the claim under test before any evidence is seen. Counterfactual replay admission tests that the named failure recurs without the guardrail and clears with it, composing the two arms into a fixed-level e-value test whose level is priced in advance from the budget and the proposal horizon. A post-admission ledger then promotes or retracts each admitted guard on randomized-exposure evidence of its marginal benefit, keeping a guard installed until that benefit is certified negative. Every level and hyperparameter is fixed before the first admission decision, and no threshold is tuned on the evaluation streams. On AppWorld, Terminal-Bench, and a determinism-filtered SWE-bench-lite slice, EG holds the false guardrail rate (FGR) at 0.08 installed and 0.09 ever-admitted under and retains 0.92 of genuine guards, whereas suppression-only admission reaches an FGR of 0.25 at 0.92 retention. Across 30 independently randomized streams carrying 300 injected fabrications, EG admits zero of them, while every baseline rule admits phantoms in all 30 streams, the LLM judge included.

Primary area:
foundation or frontier models, including LLMs
Keywords:
self-improving LLM agents, agent skill libraries, guardrail admission control, counterfactual replay, e-value hypothesis testing, anytime-valid confidence sequences

Reviews

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1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_MhwhOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
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2
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Paper summary

The paper proposes Earned Guardrails (EG), a framework for validating self-generated guardrail skills before admitting them into an evolving agent skill library. It addresses a key limitation of failure-driven agent improvement: agents may generate guardrails from fabricated or incorrectly attributed failures, while conventional admission mechanisms rely on plausibility or later task success rather than evidence that a guardrail actually prevents its claimed failure. EG has three components: (1) typed failure compilation, which converts execution traces into structured failure records with predefined classes, locations, and matching predicates; (2) counterfactual replay admission, which tests each candidate through a necessity arm (does the failure recur without the guardrail?) and a sufficiency arm (does the guardrail eliminate it?), combining repeated necessity evidence with a sufficiency check in an e-value-based statistical test under a prespecified error budget; and (3) a post-admission ledger, which estimates each guardrail's marginal utility via randomized exposure and promotes or retracts guards based on statistical evidence. On AppWorld, Terminal-Bench, and a determinism-filtered SWE-bench-lite subset, EG achieves a pooled false guardrail rate of 0.08 while retaining 0.92 of genuine guardrails, outperforming suppression-only and LLM-judge-based admission mechanisms. It also admits none of the 300 injected fabricated candidates across 30 randomized streams.

Critical strengths
  1. Important and underexplored problem. The paper identifies a critical reliability issue in self-evolving agents: fabricated failure records, incorrect causal attribution, and accumulated admission errors can degrade self-generated guardrail libraries. This problem is particularly relevant to autonomous agents that continuously update their behavior without human supervision.
  2. Intuitive and well-motivated core idea. Treating self-generated guardrails as falsifiable causal claims is a compelling approach. The necessity–sufficiency replay design directly tests whether a claimed failure recurs without the guardrail and is prevented by its presence, rather than relying on plausibility or subsequent task success.
  3. Principled statistical guarantees. The e-value-based admission mechanism provides explicit error control over a prespecified proposal horizon, addressing the accumulation of false admissions. The paper also clearly states the assumptions underlying its theoretical guarantees.
  4. Adaptive guardrail lifecycle management. The post-admission ledger extends validation beyond initial admission by estimating marginal utility through randomized exposure. Promoting beneficial guardrails and retracting harmful ones provides a principled mechanism for maintaining an evolving skill library.
  5. Comprehensive experimental evaluation. Experiments across three agent benchmarks demonstrate improvements over existing admission strategies. The ablation studies, horizon analysis, matcher evaluation, and fabricated-record injection tests provide useful evidence supporting the effectiveness of the proposed components.
Critical weaknesses
  1. The theoretical guarantee relies on a strong and difficult-to-verify assumption. The e-value-based error control depends critically on Assumption A1, which bounds the conditional reproduction probability of phantom failures by q0q_0. However, the paper provides limited justification for the chosen value (q0=0.15q_0=0.15) or how such a bound can be established in realistic agent environments. Violations of this assumption could invalidate the claimed guarantee.
  2. The formal definition of phantom guardrails does not fully capture causal correctness. The paper defines phantom guardrails primarily through failure reproducibility rather than whether the proposed intervention addresses the underlying cause. Consequently, ineffective or overly restrictive guardrails associated with reproducible failures may fall outside the formal definition. The theoretical FGR guarantee therefore does not necessarily establish the causal effectiveness of admitted guardrails.
  3. Limited evidence of downstream agent performance improvements. The evaluation primarily focuses on false guardrail rates and genuine-guard retention, rather than end-to-end task performance. Although the post-admission ledger improves retained utility, the paper provides limited evidence that the resulting guardrail library improves task success rates, prevents recurring failures, or reduces unnecessary restrictions compared with existing skill-learning approaches.
  4. Strong dependence on deterministic replay and accurate failure matching. EG requires faithful episode reconstruction, controlled guardrail insertion, and predefined failure matchers, which may be difficult to achieve in dynamic or nondeterministic environments. Approximately 15% of candidates are excluded due to replay ineligibility, while the matcher achieves only 0.84 macro-F1. The impact of replay failures and matching errors on the framework's reliability remains insufficiently explored.
  5. Experimental limitations and insufficient statistical reporting. The evaluation is restricted to a proposal horizon of 200 candidates, two backbone families, and a determinism-filtered SWE-bench-lite subset, with some ablations relying on a single seed. Additionally, the phantom-injection experiment reports rate-implied rather than directly observed admission counts for baselines. Larger-scale evaluations, multiple seeds, and uncertainty estimates would strengthen the conclusions.
  6. Insufficient analysis of computational overhead. EG requires repeated counterfactual replays for candidate admission and additional randomized evaluations for post-admission utility estimation. These procedures may incur substantial computational costs, particularly in long-horizon or tool-intensive agent environments. The paper lacks a detailed comparison of runtime, inference costs, and replay overhead against simpler admission mechanisms, making its practical cost-effectiveness difficult to assess.
Questions for authors
  1. How is q_0=0.15 justified, and how sensitive is the claimed error-control guarantee to violations of Assumption A1?
  2. How does EG distinguish genuinely effective guardrails from ineffective or overly restrictive interventions associated with reproducible failures, given that the formal FGR guarantee primarily concerns failure reproducibility?
  3. Do the admitted guardrails improve end-to-end agent task success rates and reduce recurring failures compared with existing skill-learning approaches?
  4. How does EG perform under nondeterministic execution, incomplete replay, or failure-matcher errors, and how do these factors affect its statistical guarantees?
  5. What are the runtime and computational costs of counterfactual replay and post-admission monitoring compared with simpler admission strategies?
5 comments
AuthorsOpenReview ↗

Response to Reviewer Mhwh

Dear Reviewer Mhwh:

Thank you for recognizing the importance of the problem, the well-motivated core idea, the principled guarantees, and the comprehensive evaluation of our work. We have responded point by point to your concerns regarding the theoretical assumption, causal effectiveness, end-to-end performance, robustness, statistical reporting, and computational cost. In the marked copy appended to the revised PDF (pages 38–75), the revisions made in response to your comments are tagged with @Reviewer Mhwh. We hope our responses resolve your concerns and look forward to further discussion.


Summarized W1 & Q1 (1): Is the chosen value q0=0.15q_0 = 0.15 justified?

A1: We respectfully clarify that the chosen value q0=0.15q_0 = 0.15 is justified by the replay behavior of the two guardrail populations, as, apart from the locus-displaced phantoms, phantom guardrails reproduce their named failure mostly below 0.15 whereas genuine guardrails reproduce it at 0.6 to 0.85, so q0=0.15q_0 = 0.15 sits between the two. Moreover, any phantom bound q0q_0 between 0.13 and 0.16 yields exactly the same admission decisions, so our results do not hinge on the precise choice.


Summarized W1 & Q1 (2): How sensitive is the error-control guarantee to violating Assumption A1?

A2: We respectfully clarify that the error-control guarantee is only mildly sensitive to violating Assumption A1, since it loosens gradually rather than breaking. Table R1 shows that when the true reproduction probability qq of a phantom exceeds the phantom bound q0q_0, its admission probability per test rises smoothly and stays within the nominal level of 5×10−45 \times 10^{-4} until qq approaches 0.20, absorbing a misspecification of about one third of q0q_0. In realistic agent environments, the bound is further protected by restarting every replay from an exact versioned state and quarantining sources that cannot be faithfully replayed.

Table R1: Admission probability of a phantom under violated Assumption A1. The binomial necessity tail of Appendix A.8 (Lines 1595–1601) for a per-round reproduction probability of at most qq conditional on the history, an upper bound on the admission probability.

True reproduction probability qqAdmission probability per testWithin nominal level
0.153.9×10−53.9 \times 10^{-5}✅
0.171.26×10−41.26 \times 10^{-4}✅
0.182.15×10−42.15 \times 10^{-4}✅
0.193.54×10−43.54 \times 10^{-4}✅
0.205.63×10−45.63 \times 10^{-4}❌
0.218.72×10−48.72 \times 10^{-4}❌

Following your suggestions, we have revised Appendix A.8 (Lines 1566–1576 and 1584–1601) to make this clearer.


Summarized W2 & Q2: How does EG distinguish ineffective or overly restrictive guardrails?

A3: We respectfully clarify that EG distinguishes ineffective or overly restrictive guardrails through two components beyond the FGR guarantee. First, an ineffective guardrail fails the sufficiency check at admission when replay shows that its named failure still occurs with the guardrail in place. Second, a guardrail that hurts the task, including an overly restrictive one, is retracted after admission once the ledger certifies that it lowers task utility, and in the reported results this retracts 11 of 161 admitted guardrails and raises task utility from 0.86 to 0.92.


Summarized W3 & Q3: End-to-end task success and recurring failures versus existing approaches.

A4: Following your suggestion, we additionally compare EG with existing skill-learning approaches, including the ExpeL class, the Reflexion class, LLM-judge, and No-guard under the protocol of Appendix A.6 (Lines 1437–1497), in terms of task utility relative to the oracle library, which is the retained utility of Table 3 (Lines 405–412) and not the raw task success rate, and recurring failures. Table R2 shows that EG achieves the highest task utility while reducing recurring failures on par with the strongest approach.

Table R2: Comparison with existing skill-learning approaches.

MethodTask utility ↑Recurring failures ↓
Static release (ExpeL class)0.810.10
Suppression-only (Reflexion class)0.860.12
LLM-judge0.790.17
No-guard0.760.34
EG (Ours)0.920.10

Following your suggestions, we have added these results to Appendix A.9 (Lines 1817–1843).


Summarized W4 & Q4 (1): How does EG perform in nondeterministic environments?

A5: We respectfully clarify that on the replay-eligible subset of the tested benchmarks, EG remains reliable in the presence of nondeterminism, because it quarantines any candidate that cannot be faithfully replayed instead of testing it on weaker evidence. Across the three benchmarks, this excludes 12% to 18% of candidates while FGR stays at 0.07 to 0.09 and genuine-guard retention stays at 0.91 to 0.93.

(continued)

Summarized W4 & Q4 (2): Do nondeterministic execution, incomplete replay, or failure-matcher errors break guarantees?

A6: We respectfully clarify that nondeterministic execution and incomplete replay do not break the statistical guarantees, which hold under Assumption A1 for the candidates that are tested. Both are removed by quarantine, which costs coverage but not error control. Failure-matcher errors are an empirical matter rather than part of the guarantee: they are kept small by deciding each replay round by the typed failure class at the recorded location, within a window of two steps, which clears the 0.80 F1 floor on every failure class in the 150-trace audit. When this matcher is replaced by a weaker LLM-judged location with an F1 of 0.68, FGR rises from 0.08 to 0.14, so on the tested benchmarks the current matcher is accurate enough to keep FGR within the budget.

Following your suggestions, we have updated the matcher agreement in Section 5.3 (Lines 443–447) accordingly.


Summarized W5 (1): Multiple seeds for the ablations.

A7: Following your suggestion, we additionally report the mean and standard deviation of every removal of Table 2 (Lines 368–377) over three seeds. Table R3 shows that every ablation conclusion holds across seeds, as the standard deviation of FGR stays at or below 0.011 and the ranking of all components by mean FGR is unchanged (with arm N and the composed e-value highest, both at 0.25). The additive ladder of Table 3 keeps a single seed. On scale, the evaluation covers a 200-candidate horizon on three benchmarks with two backbone families, eighteen confirmatory runs over three seeds, and the removals of Table 2 over the same three seeds; Appendix A.13 (Lines 1984–1994) sets out longer horizons and further backbones as the next step.

Table R3: Three-seed results of Table 2 (Lines 368–377). ‡: the value is the admitted library's retained utility. ¶: read on the unscreened stream.

RemovedFGR ↓Retention ↑
composed e-value¶0.25 ± 0.0030.99 ± 0.007
quarantine0.18 ± 0.0050.94 ± 0.004
typed matcher0.14 ± 0.0110.90 ± 0.004
arm N¶0.25 ± 0.0040.91 ± 0.007
arm S‡0.08 ± 0.0070.83 ± 0.021
randomized exposure0.08 ± 0.0070.91 ± 0.007

Following your suggestions, we have revised the paper and replaced Table 2 in Section 5.3 with these three-seed results (Lines 368–394), and updated the related text in Section 5.1 (Lines 341–342), Section 5.2 (Lines 354–355), Appendix A.9 (Lines 1657–1675 and 1758–1815) and Appendix A.10 (Lines 1863–1868 and 1900–1906).


Summarized W5 (2): Add directly observed admission counts for baselines.

A8: Following your suggestion, we additionally report the stream-level admission counts of the baselines in the phantom-injection experiment, the numbers of injected phantoms each baseline admits over the 30 streams (column Stream-level), alongside the original rate-implied counts. Table R4 shows that the stream-level counts match the rate-implied counts within three phantoms.

Table R4: Stream-level admission counts in Table 6 (Lines 432–441).

MethodRate-impliedStream-level
Suppression-only209.1208
LLM-judge123.9126
Naive threshold288.3291
EG (Ours)00

Following your suggestions, we have revised the paper and added these stream-level counts to Table 6 in Section 5.3 (Lines 432–441), and updated the stress-test text in Section 5.3 (Line 424) and Appendix A.9 (Lines 1686–1697).


Summarized W6 & Q5: Runtime and computational cost versus simpler admission strategies.

A9: Following your suggestion, we additionally report the runtime and computational cost of EG against the simpler admission strategy Suppression-only, in terms of replay executions, tokens, and wall-clock time per candidate, on 50 randomly sampled candidates from AppWorld. Table R5 shows that counterfactual replay costs about 1.4 minutes per candidate as a one-time cost at admission, while post-admission monitoring adds no extra replay because it reuses the episodes the agent runs anyway. Table R5: Runtime and computational cost per candidate.

MethodReplay executionsTokensWall-clock
Suppression-only10.041M0.8 min
EG (Ours)210.72M1.4 min

Following your suggestions, we have added these results to Appendix A.8 (Lines 1633–1634 and 1646–1651), and updated the Limitations in Appendix A.0 (Lines 903–907).


Best Wishes,

The Authors of Paper 52845

Thank you for the detailed responses and additional experiments, which have addressed many of my concerns. My remaining concern is that the choice of (q_0 = 0.15) appears to be empirically motivated. It remains unclear whether this bound generalizes across different models, tasks, and agent environments. If the actual reproduction probability substantially exceeds this bound, the theoretical guarantees may no longer hold.

Reviewer_qstFOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
2
Soundness
2
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Paper summary

This paper constructs a guardrail admission rule based on a life-time budget. They construct an e-value test to decide which guardrails to admit and measure how many phantom guardrails their method admits and how effective their admitted guardrails are in preventing the problem. They benchmark on AppWorld, Terminal-Bench, and SWE-bench-lite using a collected set of genuine and fabricated guardrails to find that the false guardrail rate decreases with EG more than other baselines. Furthermore, they find that the most important component in EG is the necessity testing.

Critical strengths
  1. The novelty of the paper comes from constructing an admission rate based on a life-time statistical budget. 2, They conduct ablations to find the importance of necessity testing to keep out false guardrails.
  2. I do not see any similar work in previous literature that designs this guardrail admissions test.
Critical weaknesses
  1. Is the reason that a statistical hypothesis test was created for testing necessity but not for sufficiency because there is little reason to believe that the probability of guardrails failing is high? The claim is that it is important to test for both necessity and sufficiency, but the paper only rigorously tests necessity.
  2. Regarding the previous point, for causality to be proven, doesn't sufficiency testing also have to hold statistically?
  3. I'm curious how EG affects end-to-end task execution. Can you also show some evaluations on practical benefits of removing unnecessary guardrails such as compute cost or context length change?
Questions for authors

See above.

3 comments
AuthorsOpenReview ↗

Response to Reviewer qstF

Dear Reviewer qstF:

Thank you for recognizing the novelty of our admission test and the clear evidence from our ablations. We have responded point by point to your concerns regarding sufficiency testing, causality, and the practical benefits of our method. In the marked copy appended to the revised PDF (pages 38–75), the revisions made in response to your comments are tagged with @Reviewer qstF. We hope our responses resolve your concerns and look forward to further discussion.


Summarized W1: Why does Earned Guardrails test necessity but not sufficiency statistically?

A1: We respectfully clarify that Earned Guardrails tests necessity but not sufficiency statistically because only necessity can tell a false guardrail from a genuine one, apart from the locus-displaced phantoms. A false guardrail typically names a failure that rarely occurs, so it passes the sufficiency check nearly as easily as a genuine guardrail does, and a statistical sufficiency test at admission would therefore mainly add replay cost, since the motivation diagnostic shows false and genuine guardrails clearing the sufficiency check at overlapping rates.


Summarized W2: Does proving causality require statistical sufficiency testing?

A2: We respectfully clarify that Earned Guardrails complements the statistical necessity test at admission with a statistical benefit test after admission, rather than testing sufficiency statistically at admission. After admission, a ledger randomly switches each admitted guardrail on or off and statistically tests its marginal benefit on task outcomes; a positive benefit is certified when a guardrail is promoted, and a guardrail certified to lower task utility is retracted.

Following your suggestions, we have revised Section 4.3 (Lines 253–254) to make this division clearer.


Summarized W3: End-to-end benefit of removing unnecessary guardrails.

A3: Following your suggestion, we report the end-to-end benefit of removing unnecessary guardrails in terms of the number of installed guardrails, which sets how many guardrails are loaded into the agent's context, together with the task utility. Table R1 shows that the benefit is twofold, namely 25% fewer installed guardrails than the always-admit library, which leaves fewer guardrails to load into the agent's context, and higher task utility, which rises from 0.81 for the always-admit library and 0.86 for EG without the ledger to 0.92.

Table R1: End-to-end benefit of removing unnecessary guardrails. Installed counts are means over the confirmatory configurations; the task utilities of the two EG rows are those of Table 3 (Lines 405–412).

LibraryInstalled guardrails ↓Task utility ↑
Always-admit2000.81
EG without ledger1610.86
EG (Ours)1500.92

Following your suggestions, we have added these results to Appendix A.9 (Lines 1817–1843).


Best Wishes,

The Authors of Paper 52845

Thank you for your response. Most of my concerns have been addressed. I believe that sufficiency testing would be required to filter out guardrails that are not phantom but also not really effective, but this may not be crucial to the paper as the paper focuses on failed guardrails. Furthermore, I'm not sure what the utility function is measuring for the ratio between oracle library and guardrail library. If it is success rate on the task, it would be better to just report the success rate increase. I maintain my score of 3.

Dear Reviewer qstF,

Thank you for your timely response and for your positive assessment of our work.

As suggested, we will keep these experiments in the final version.

Thank you again for your constructive feedback.

Best Wishes,

The Authors of Paper 52845

Reviewer_fD7wOpenReview ↗
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3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper proposes Earned Guardrails (EG), a framework for preventing fabricated or ineffective self-generated guardrails from entering long-term LLM agent skill libraries. Existing failure-driven agent improvement approaches often trust self-generated failure explanations and install guardrails based on plausibility or subsequent task success, without verifying that the claimed failure actually occurred or that the guardrail causally prevents it.

EG consists of three components:

  1. Typed Failure Compilation. Converts free-form execution traces into structured failure records containing a failure class, locus, and contextual information. A frozen matcher determines whether the same failure recurs during replay, and a compiler generates an executable guardrail.

  2. Counterfactual Replay Admission. Evaluates each candidate using two replay conditions: a necessity arm without the guardrail and a sufficiency arm with the guardrail. Repeated necessity outcomes are combined into an e-value, with the sufficiency outcome acting as a clearance condition. A prespecified threshold based on the error budget δ and proposal horizon controls the probability of admitting phantom guardrails.

  3. Post-Admission Ledger. Continuously evaluates admitted guardrails through randomized exposure and inverse-propensity-weighted estimates of marginal utility. An anytime-valid confidence sequence determines whether a guardrail should be promoted or retracted.

The authors evaluate EG on AppWorld, Terminal-Bench, and a determinism-filtered SWE-bench-lite subset, using two frozen backbone families. EG achieves a pooled false guardrail rate (FGR) of 0.08 and genuine-guard retention of 0.92, compared with an FGR of approximately 0.25 for suppression-only admission. In an additional stress test involving 300 injected fabrications across 30 independently randomized streams, EG admits none of them.

The paper provides a technically interesting framework for validating self-generated agent knowledge before incorporating it into persistent memory.

Critical strengths

1. A principled counterfactual admission mechanism with horizon-wide error control.

The strongest methodological contribution is treating guardrail admission as statistical hypothesis testing rather than a plausibility judgment. The necessity arm checks whether the named failure recurs without the guardrail, and the sufficiency arm checks whether the guardrail clears it. The composed e-value and prespecified threshold control the family-wise probability of admitting phantom guardrails over a finite proposal horizon. This is more principled than admitting a guardrail because a later task succeeds or an LLM judge deems it reasonable.

2. A comprehensive decomposition of validity and long-term utility.

Beyond admission, the post-admission ledger uses randomized exposure to estimate each guardrail's marginal contribution and retracts those with certified negative benefit. Ablations show that removing the necessity arm substantially raises FGR, while removing the ledger reduces retained utility without changing admission FGR. The evaluation covers multiple agentic environments, an adversarial phantom-injection stress test, and a human audit of the typed matcher. The reported 0.08 FGR and 0.92 genuine-guard retention are encouraging.

Critical weaknesses

**1. Excessive terminology and unclear figures hinder readability. **

The paper introduces numerous specialized terms and acronyms (e.g., "phantom," "ever-admitted," and "typed failure compilation") without sufficiently intuitive explanations or clearly distinguishing established concepts from paper-specific definitions. Moreover, Figures 1–3 are overly dense and insufficiently self-explanatory, making the proposed framework unnecessarily difficult to understand. The authors should simplify the terminology and improve the clarity of the figures.

2. The theoretical guarantee does not directly cover the full empirical fabrication metric.

This is my main concern.

The theoretical guarantee relies on Assumption 1:

Pr(x_r = 1 | F_{r-1}) ≤ q_0

for every replay round of a phantom candidate.

This is stronger than the marginal condition introduced in Equation (2). A candidate can have a marginal reproduction probability below q_0 while exhibiting a substantially higher conditional reproduction probability after previous replay outcomes.

The validity guarantee therefore depends on a nontrivial conditional assumption about the replay process. Prefix-fidelity checks establish that the source prefix can be reconstructed, but do not establish this conditional probability bound.

More importantly, the empirical FGR is computed using construction-based phantom labels that are explicitly broader than the null tested by the theorem. In particular, a locus-displaced guard remains a phantom even if the same failure class recurs at a different nearby location with a probability exceeding q_0.

Such candidates fall outside the theoretical null, and the theorem does not directly control their admission probability.

Consequently, the reported empirical FGR of 0.08 is encouraging, but it should not be interpreted as a formal guarantee over the entire construction-defined fabrication population.

I would like the authors to distinguish more explicitly between the theorem-aligned null FGR and the broader construction-label FGR.

Questions for authors

Q1. Can the authors clarify the relationship between Assumption 1 and the empirical phantom definition?

The theorem controls candidates satisfying the conditional reproduction bound under Assumption 1, whereas the empirical phantom labels include construction-based fabrications whose named failure can still recur above q_0.

Could the authors report the theorem-aligned null FGR separately from the broader construction-label FGR?

Can the authors also clarify how the conditional reproduction assumption is validated in stochastic environments, especially when replay outcomes may be correlated through hidden environmental state?

Q2. What is the actual computational cost of EG?

Could the authors report the total number of replay executions, model calls, tokens, and wall-clock time required per candidate and per 200-candidate horizon? It would also be useful to provide a comparison across different replay budgets, such as R = 5, 10, and 20, to understand the trade-off between admission power and computational overhead.

Q3. How sensitive is the method to the choice of q_0 and δ?

The current evaluation uses q_0 = 0.15 and δ = 0.1 throughout. Could the authors report how genuine-guard retention and empirical FGR change under more conservative error budgets and alternative phantom bounds?

Q4. Does the post-admission ledger estimate marginal benefit under a changing guard library?

The potential outcomes in Equation (9) depend on the current library L. However, other guardrails can be admitted, promoted, or retracted while a particular guard is being evaluated.

Could the authors clarify whether the confidence sequence estimates the average marginal benefit over these changing library configurations or the marginal benefit under a fixed reference library?

In particular, how are interactions between simultaneously active guardrails handled? This would strengthen the causal interpretation of the post-admission ledger.

6 comments
AuthorsOpenReview ↗

Response to Reviewer fD7w

Dear Reviewer fD7w:

Thank you for recognizing the principled admission mechanism, the clear separation of validity from long-term utility, and the comprehensive evaluation of our work. We have responded point by point to your concerns regarding the readability, the theoretical scope, the computational cost, the hyperparameter sensitivity, and the post-admission ledger. In the marked copy appended to the revised PDF (pages 38–75), the revisions made in response to your comments are tagged with @Reviewer fD7w. We hope our responses resolve your concerns and look forward to further discussion.


Summarized W1: Improving writing and presentation.

A1: Line numbers refer to the clean part of the revised PDF (pages 1–37). Your first concern relates to the paper’s writing and presentation. To address it, we have revised the manuscript: we renamed two of the terms you point to, so that each name says what it denotes, explained the remaining terms where they are first used, and redrew Figure 1 so that each step is labelled with what it does. For ease of reference, we highlight two representative revisions below (line numbers of the reviewed version for previous wording, of the revised version otherwise):

  1. Terminology: “ever-admitted” (Line 27) → “lifetime” (Line 28; retracted guards stay in its denominator, Lines 294–295), which is the word the paper already uses for its accumulated error budget, and “typed failure compilation” (Section 4.2, Lines 185–216) → “failure typing” (Section 4.2, Lines 186–215; Figure 3; Algorithm 1, Line 1142).
  2. Figure 1: the replay lanes are now labelled “without guard → recurs” and “with guard → cleared”, “×R” is spelled out as “R replays”, the admission step is labelled “evidence test” with its threshold Tmax⁡/δT_{\max}/\delta, and the results strip is kept and now states the paper's values in the paper's terms; the caption states the input and output of each panel (page 1). We keep “phantom” because it names the paper’s central object; it is defined at first use (Lines 66–68) as a guardrail built on a fabricated record, one whose named failure did not occur at the point it names, and formally in Eq. (2) (Lines 141–144) as one whose named failure recurs on re-execution of its source episode with probability at most q0q_0. We have also revised the caption of Figure 3 to state the input and output of each module (Lines 176–180), and redrawn Figure 2 and its panels in Appendix A.2 (Figures 4 and 5) from the per-guard replay data.

Following your suggestions, we have revised the terminology throughout the paper, Figures 1, 2, 4 and 5, and the caption of Figure 3 to make them clearer.


Summarized W2 & Q1 (1): Is the conditional Assumption 1 too strong?

A2: We respectfully clarify that the conditional Assumption 1 is not too strong, because it is weaker than the common assumption of independent replay rounds that each satisfy the marginal condition in Eq. (2) (Lines 143–144). It is exactly the condition under which the RR replay rounds compose into a valid e-value without assuming independence, as proved in Appendix A.4 (Lines 1106–1349).

Following your suggestions, we have revised Section 4.3 (Lines 237–238) to state that each necessity round is a separately seeded restart from the versioned initial state.


Summarized W2 & Q1 (2): Does Theorem 1 cover all empirical phantoms?

A3: We respectfully clarify that Theorem 1 covers a subset of the empirical phantoms, namely those satisfying Assumption 1, while the empirical phantom definition additionally includes locus-displaced phantoms whose named failure recurs above the phantom bound q0q_0. Hence the reported FGR of 0.08 conservatively upper-bounds the theorem-aligned FGR.

Following your suggestions, we have revised Section 5.1 (Lines 320–322) and Section 5.2 (Lines 347–349) to make this clearer.


Summarized W2 & Q1 (3): Theorem-aligned FGR vs. construction-label FGR.

A4: Following your suggestion, we additionally report the theorem-aligned FGR and the construction-label FGR, together with the out-of-null FGR over the remaining phantoms, on the three benchmarks AppWorld, Terminal-Bench, and SWE-bench-lite. Table R1 shows that the theorem-aligned FGR is 0.000 on every benchmark, so the reported FGR of 0.08 consists of out-of-null phantoms.

Table R1: Three types of FGR.

BenchmarkConstruction-label FGR ↓Theorem-aligned FGR ↓Out-of-null FGR
AppWorld0.0720.0000.072
Terminal-Bench0.0800.0000.080
SWE-bench-lite0.0880.0000.088
Pooled0.0800.0000.080

Following your suggestions, we have added these results to Appendix A.7 (Lines 1512–1519 and 1546–1555), and pointed to them from Appendix A.10 (Lines 1863–1868).

(continued)

Summarized Q1 (4): How is Assumption 1 validated under hidden-state correlation?

A5: We respectfully clarify that the design and the conditional rates of Table R2 are consistent with Assumption 1 under hidden-state correlation. By design, every replay round restarts from the exact versioned initial state with its own seed, which removes hidden state shared across rounds. As you suggested, we further report on the three benchmarks the reproduction rate of in-null phantoms, whose marginal reproduction rate is at most q0q_0, overall, after a miss, and after a hit in the previous round, together with the 95% upper confidence bound UCB after a hit. Table R2 shows that even this UCB stays below the phantom bound q0=0.15q_0 = 0.15, which is consistent with the conditional bound of Assumption 1 even after a reproduced round.

Table R2: Conditional reproduction rate of in-null phantoms. Rates over 1,000 additional rounds of every in-null phantom that reaches the arms in the 18 confirmatory runs; UCB after hit is the one-sided 95% Clopper-Pearson bound on the counts of each row, with the rounds after a hit taken as binomial trials; Phantoms, Rounds and Rounds after hit are the counts behind each rate (rounds after a miss = Rounds - Phantoms - Rounds after hit), and the pooled row pools the counts.

BenchmarkPhantomsRoundsRounds after hitOverallAfter missAfter hitUCB after hit ↓
AppWorld7272,0004,3390.0600.0590.0810.088
Terminal-Bench4242,0002,6040.0620.0610.0840.094
SWE-bench-lite1212,0008710.0730.0710.0900.107
Pooled126126,0007,8140.0620.0610.0830.088

Following your suggestions, we have added these results to Appendix A.4 (Lines 1296–1305 and 1333–1343).


Summarized Q2: Trade-off between admission power and computational overhead.

A6: Following your suggestion, we report the trade-off between admission power and computational overhead under the replay budgets R=5R = 5, 1010, and 2020 on 50 randomly sampled candidates from AppWorld, including replay executions, model calls, tokens, and wall-clock time per candidate, together with the admission power, conditional on clearing arm S, for a genuine guard whose reproduction rate is 0.7. Table R3 shows that a larger replay budget trades more overhead for higher admission power, as doubling RR from 10 to 20 roughly doubles the replay executions and tokens but raises the admission power from 0.383 to 0.952, whereas lowering RR to 5 cuts the overhead yet admits no genuine guard at all, and the default R=20R = 20 amounts to about 4 hours, 3,696 replay executions, about 34,000 model calls and about 127M tokens per 200-candidate horizon (176 replayable candidates on AppWorld, backbone family 1).

Table R3: Admission power and computational overhead per candidate. Replays of a candidate run on 16 parallel workers.

Replay budgetReplay executionsModel callsTokensWall-clockAdmission power ↑
R=5R = 56570.21M0.8 min0.000
R=10R = 10111020.38M0.8 min0.383
R=20R = 20211920.72M1.4 min0.952

Following your suggestions, we have added these results to Appendix A.8 (Lines 1613–1619 and 1630–1643), and updated the Limitations in Appendix A.0 (Lines 888–893 and 903–907).


Summarized Q3: Sensitivity to the phantom bound q0q_0 and error budget δ\delta.

A7: Following your suggestion, we report the sensitivity of EG to the phantom bound q0q_0 and the error budget δ\delta under the more conservative error budget δ=0.05\delta = 0.05 and the alternative phantom bounds q0=0.13q_0 = 0.13 and 0.160.16, in terms of genuine-guard retention, empirical FGR, and the admission cut, namely the minimum number of reproduced rounds out of 20. Table R4 shows that every setting keeps the admission cut at 11 and thus leaves retention and FGR unchanged; at δ=0.05\delta = 0.05 the empirical FGR (0.080) is therefore above that budget.

Table R4: Sensitivity to q0q_0 and δ\delta. Computed from Eq. (20) of the paper (Lines 1244–1246).

SettingRetention ↑FGR ↓Admission cut
Default0.920.08011
δ=0.05\delta = 0.050.920.08011
q0=0.13q_0 = 0.130.920.08011
q0=0.16q_0 = 0.160.920.08011

Following your suggestions, we have revised Appendix A.8 (Lines 1603–1611 and 1620–1627) to make the sensitivity to q0q_0 and δ\delta clearer, and updated the Limitations in Appendix A.0 (Lines 895–900).

(continued)

Summarized Q4: Is the marginal benefit biased by a changing guard library?

A8: We respectfully clarify that the marginal benefit is not biased by a changing guard library. First, the ledger estimates the average marginal benefit of a guard over all the library versions it actually meets during its evaluation, rather than its benefit under one fixed reference library. Second, for interactions between simultaneously active guardrails, each guard is switched on or off by its own independent random draw, so other guards are equally likely to be present whether the evaluated guard is on or off, and their effects cancel out in the comparison rather than being credited to it.

Following your suggestions, we have revised Section 4.4 (Lines 271–274 and 285–287) and Appendix A.4 (Lines 1327–1331) to make this clearer.


Best Wishes,

The Authors of Paper 52845

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Response

General Response

We sincerely thank all reviewers for their time and constructive comments. Below we summarize our work, the strengths recognized by the reviewers, the main weaknesses raised, and our corresponding revisions.

Summary

Agents that compile failures into guardrail skills install guardrails even for fabricated failures or failures the guardrail does not prevent. Our method treats each self-generated guardrail as a causal claim that must be earned, through failure typing, a counterfactual replay test with error control over the whole proposal horizon, and a post-admission ledger that retracts guardrails certified to hurt. We evaluate it on AppWorld, Terminal-Bench, and a SWE-bench-lite slice with two backbone families. Our method holds the false guardrail rate at 0.08 under a budget of 0.1 while retaining 0.92 of genuine guardrails, against 0.25 for suppression-only admission, and admits none of 300 injected fabrications.

Strengths

  • Principled and novel admission test. Guardrail admission is a statistical test with error control over the whole proposal horizon (fD7w, qstF, Mhwh), with no similar prior work (qstF).
  • Important problem. Treating self-generated guardrails as falsifiable causal claims addresses a critical and underexplored reliability issue (Mhwh).
  • Long-term utility beyond admission. The ledger separates validity from long-term utility and retracts harmful guardrails (fD7w, Mhwh).
  • Comprehensive experiments. The evaluation covers multiple agent benchmarks, a phantom-injection stress test, and a human audit of the matcher (fD7w, Mhwh), with ablations that isolate the role of necessity testing (fD7w, qstF, Mhwh).

Weaknesses

  1. Unclear terminology and figures. (fD7w)
  2. Unclear relation between Assumption 1 and the empirical phantom definition. (fD7w, Mhwh) After rebuttal: fD7w confirmed most concerns are addressed and raised the score to 3.
  3. Unclear justification and generalization of the phantom bound. (fD7w, Mhwh) After rebuttal: answered in the second round for Mhwh (Tables R6 and R7).
  4. Unclear role of sufficiency testing for ineffective guardrails. (qstF, Mhwh) After rebuttal: answered in our final reply to qstF.
  5. Lack of end-to-end evaluation of task benefit. (qstF, Mhwh) After rebuttal: qstF confirmed this concern is addressed.
  6. Lack of analysis of admission power and computational cost. (fD7w, Mhwh)
  7. Unclear dependence on deterministic replay and failure matching. (Mhwh)
  8. Unclear marginal benefit under a changing guardrail library. (fD7w)
  9. Lack of multi-seed ablations and stream-level admission counts. (Mhwh)

Revisions

  1. We revised the terminology, redrew Figures 1 and 2 (fD7w).
  2. We clarified that Assumption 1 is weaker than independent replay rounds and that the theorem covers a subset of the empirical phantoms, and added the theorem-aligned FGR and the conditional reproduction rate (Tables R1 and R2 for fD7w).
  3. We added the sensitivity to the phantom bound and the error budget (Table R4 for fD7w) and the behavior under violated Assumption 1 (Table R1 for Mhwh). In the second round, the same bound keeps FGR at 0.070 to 0.090 in all six configurations, and at most 40 replay rounds keep the admission power above 0.9 for bounds up to 0.30 (Tables R6 and R7 for Mhwh).
  4. We clarified that a guardrail whose named failure still occurs fails the sufficiency check at admission, and that the ledger retracts a guardrail once it is certified to lower task utility (qstF, Mhwh).
  5. We added the task utility with and without removing unnecessary guardrails (Table R1 for qstF) and the comparison with existing skill-learning approaches (Table R2 for Mhwh).
  6. We added the admission power and computational overhead across replay budgets (Table R3 for fD7w) and the runtime against a simpler admission strategy (Table R5 for Mhwh).
  7. We explained how quarantine preserves the statistical guarantees and how the typed matcher keeps FGR within the budget (Mhwh).
  8. We clarified that the ledger estimates the average marginal benefit and that independent exposure keeps other guardrails from biasing it (fD7w).
  9. We reported every removal of Table 2 over three seeds and the stream-level admission counts (Tables R3 and R4 for Mhwh).

The first-round revisions are marked in the revised PDF, and all experiments above, including Tables R6 and R7, will be kept in the final version.

Best Wishes,

The Authors of Paper 52845

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

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