- Rating
- 3(+1)
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 3
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Paper summary
This paper introduces the training committor, defined as the probability that a saved training checkpoint acquires a capability within a fixed horizon under a specified continuation protocol. To estimate this quantity, the authors launch multiple reseeded continuations from each parent checkpoint—typically sixteen branches—and use the fraction that acquire the capability as the forecast. Evaluation spans in-context learning, modular addition, permutation composition, sparse parity, a small natural-text GPT, and released Pythia/Pico checkpoints, with forecasts scored against each parent’s own continuation. The work reports strong ranking performance (e.g., AUC 0.963 on 93 held-out parents), compares the estimator with checkpoint-local predictors, and uses the forecast to select low-probability runs for targeted data pulses. The main contributions are a new estimator for training-checkpoint futures, evidence that most runs are settled early, and a proof of concept that the forecast can guide intervention selection and dosing.
Critical strengths
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The core framing is genuinely novel and potentially useful. Treating a training checkpoint as a state with a distribution of futures, and estimating a finite-horizon hitting probability by reseeded continuations, is a creative transfer from transition-path theory. This is consequential because it offers a principled alternative to reading a single observed trajectory, and the controlled-task ranking results are strong enough to merit discussion.
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The intervention results are striking as a proof of concept. In in-context learning, a short aligned data pulse converts 46/51 low-forecast parents that fail on their own, against 2/51 under ordinary training. Even if the selection and cost issues remain, this is a substantive empirical signal that low-committor states are not simply doomed and can be redirected by aligned data.
Critical weaknesses
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The estimand and the scoring protocol are not clearly separated, which complicates interpretation. The paper defines the protocol-conditional probability, yet in several places the wording suggests an estimate of “the checkpoint’s probability of success.” The primary reset protocol changes the optimizer state and data order, but the forecast is scored against the parent’s own continuation, which retains both. I noticed that the authors themselves report a systematic gap: reset minus outcome is , two of the 56 zero-bin parents acquire, and carry closes most of the gap. Because the paper uses not only ranking but also probability magnitude to set pulse doses and choose actions, a calibration failure under the scoring protocol would leave the “predict and steer” results insufficient to support the paper’s central conclusion.
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Practical value under realistic compute and decision constraints needs further demonstration. A full forecast requires 16 continuations; even a one-branch forecast costs about 950 times the 750 pulse updates saved by leaving 15 parents untreated, so the forecasting overhead far exceeds the intervention cost it saves. More importantly, the authors’ own waiting baseline reaches , whereas committor targeting reaches ; the committor leads only before step 3,000. This means its advantage depends on a regime where decisions must be made very early and waiting is costly—a regime the paper does not characterize or justify. The action-selection experiment further weakens the “steering tool” claim: every parent selects the same action, and the per-parent oracle improves only from to , so per-parent action choice contributes almost nothing. As presented, the method is closer to an offline diagnostic or proof of concept than a practical steering tool; a cost-matched decision analysis or a revised claim is needed.
Questions for authors
- What exactly is the target estimand? Please state whether the paper estimates for a specific protocol or an “intrinsic” checkpoint probability. If the goal is to predict the parent’s own continuation, why is
resetthe primary protocol rather thancarryor a protocol matched to the scored outcome? Please report calibration, Brier score, and decision-curve results under matched protocols, not only AUC underreset. - What is held out, precisely? The current evaluation holds out the parent’s own continuation, but the 16 branches for that parent are used to estimate its own . Please clarify whether any checkpoint, initialization, task, or model family is truly held out. Were horizons, thresholds, cascade fractions, action libraries, and comparator choices pre-specified? If not, please provide nested cross-validation or a fully held-out evaluation with multiple-comparison correction.
- How dependent are the 16 branches? They share weights and differ only in reseeding and optimizer protocol. Please report branch correlation, effective sample size, sensitivity to , and whether the q=0/1 discretization drives the selection and dosing results.
- What supports per-parent action selection? If all parents choose the same action and the oracle gain is only 1/114, is the claim “the committor chooses the most effective action” or merely “the committor identifies one generally good action”? Please either enlarge the action library or revise the claim.
- Are low-forecast runs merely undertrained or more plastic? Please match treated and control parents on training step, loss, accuracy, weight norm, and optimizer state, and show that the pulse effect is not a generic effect of extra aligned data or additional updates.
If the authors can satisfactorily address the questions raised above, I will consider raising my rating accordingly.
5 comments
Response to Reviewer UcPf (2/2)
Question 2. Held-out evaluation and pre-specification
Thanks for your question. In the submission, only each run's own continuation was held out. To expand our study, we added six cohorts that the original results never used (Section 4.1, Table 1, Appendix B.4). The new seeds keep every setting of the original runs, the wider model changes only the model size, the 40-key task only the number of keys, and the added dihedral group is a task family that we never used in development. The results are below.
| New cohort | Runs | Acquire | AUC |
|---|---|---|---|
| In-context learning, new seeds | 72 | 26 | 0.928 |
| Wider model | 40 | 14 | 0.871 |
| 40-key task | 40 | 4 | 1.0 |
| S5 composition | 16 | 12 | 1.0 |
| Dihedral group composition | 40 | 9 | 1.0 |
| Sparse parity | 30 | 10 | 0.995 |
The horizons were set on separate pilot runs, and the rule for admitting baselines and the action library were fixed before scoring. The main choices made after seeing outcomes are below. None of them enters the forecast results in Section 4.1, and the table shows where each is used and its test.
| Choice | Used in | Test | Result |
|---|---|---|---|
| Cascade fraction | Section 4.2 | Nested cross-validation | Same fraction in 71 of 72 folds |
| Dose lengths | Section 4.3 | Held-out, 60 new runs | 58.1 of 60 expected vs. 47.2 with shuffled doses |
| Natural-text horizon | Section 4.6 | All horizons, 2,700 to 3,600 | AUC at least 0.981 at each |
| Released-model thresholds | Appendix F | Marked as exploratory |
After the multiple-comparison correction you asked for, 7 of 23 baseline comparisons remain significant, with the committor ahead in all 23 (Section 4.1).
Question 3. Dependence between the 16 restarts
Thanks for pointing this out. We have added this analysis to our paper (Appendix B.2). Restarts from the same checkpoint are close to independent when the run's own probability is controlled for. The remaining correlation between them is between -0.02 and +0.01, with the effective sample size at least 10.6 of the 16 restarts. Importantly, the result also holds with more restarts, with the AUC at 0.924 with 32 and 0.927 with 16. Finally, the 0 or 1 forecasts do not drive selection or dosing results, shown by three thresholds from 1/16 to 4/16 selecting the same runs.
Question 4. Per-run action selection
You are correct that the submission supported only the second. The more accurate claim is "identifies one generally good action" and we have revised the paper accordingly (Section 4.5). We also took your advice, and enlarged the action library. With four different kinds of action on 32 runs, choosing the kind of action for each run gains only a little over the best single action, helping support the revised claim (Appendix D.7). However, what varies is how long a pulse each one needs. On 60 new runs, choosing each run's pulse length from its own restarts beat the best fixed length whenever pulse updates have a cost, ignoring the cost of restarts (Section 4.3).
Question 5. Undertrained or more plastic
Thank you for raising this very important point. We agree that matching is important to truly isolate the effect of the pulse, and we have added exactly this comparison (Section 4.3, Table 3, Appendix D.2). First, we compared all runs at the same training steps, and across 144 of them, the ones with a low forecast do not differ from those with a high forecast in training loss, training accuracy, weight norm, or the optimizer's moment norms. In addition, in 49 pairs matched on all of these and on held-out accuracy, the pulse raises acquisition compared to ordinary training by 0.755 for low-forecast runs, compared to 0.224 for high-forecast ones. Held-out accuracy is the only statistic that does differ, so naturally we also paired each low-forecast and high-forecast run of the same held-out accuracy. In these 39 pairs, ordinary training brings 29 of the high-forecast runs to the capability but only 5 of the low-forecast runs. The pulse, instead, brings 34 of these low-forecast runs to it. Low-forecast runs are also not more plastic, since they learn random labels about as well as high-forecast runs.
Second, we had to be sure that the pulse is not a byproduct of extra updates or extra data. In every comparison, the pulsed and unpulsed copies of a run are started from the same checkpoint, so they share training steps, weights, and even optimizer state. On 42 runs the same number of ordinary updates rescues 2, more data of the kind the run has already seen rescues 3, and a random change is able to rescue none. The pulse here is able to rescue 39 of these 42 runs. This shows that the rescue comes from the data that is new to the run, instead of just the additional updates or more of the same data. This is explained further in our reply to Reviewer JvPA and in Section 4.3.
We hope this answers each of your five questions. If any remains open, please tell us and we will address it.
Looking forward to your feedback
Dear Reviewer UcPf,
Thank you again for your careful review, which helped us improve the paper. In our two comments and the revised PDF, we have addressed each of your questions, including the estimand, matched-protocol scoring, the cost-matched analysis, and the held-out cohorts.
As the discussion period ends on November 18 (AoE), we would greatly appreciate it if you could let us know whether our responses address your concerns. If they do, we would be grateful if you would consider raising your score. We are happy to clarify anything that remains open.
Best regards,
The Authors
Response to Reviewer UcPf (1/2)
Thank you for your careful and specific review. We respond to each of your points below in the order mentioned.
Weakness 1 and Question 1. What the forecast estimates and how it is scored
We agree that the original submission did not make this distinction clear. To clarify, the forecast is used to estimate the probability that a run acquires a capability under one stated way of restarting it, and not an inherent property of the checkpoint. We rewrote Section 3 and added in Table 1 to make this clear in the text.
You are also right that our default restart (reset) differs from the run that it is scored against. As you suggested, we repeated the evaluation with restarts that keep optimizer states as well (carry), making sure to score both on the same outcomes. Section 4.1 now reports the main results, and the remaining tables are in Appendix B.
As shown in the table, the carry removes the under-forecast that you mentioned. Additionally, none of the 83 runs with a zero carry forecast went on to gain the capability. The reset is kept as the default because it tests how much of the outcome is decided purely by the weights. It is also accurate when scored with its own kind of restart (AUC 0.982, Brier score 0.033). On the added decision curves, both do better than treating every run or none, except reset at the most extreme thresholds on the new seeds. The steering results hold under both kinds of restarts. Moreover, treating the 57 top ranked runs gives 63 acquisitions with either, and the rule that sets pulse length from the probability reaches 45.5 expected with carry while using about 34% fewer pulse updates (1,065 vs. 1,610), and 47.4 with reset. When a fixed threshold is used instead, it simply needs to be set for the kind of restart, since carry forecasts run slightly higher than reset (Appendix B.4).
Weakness 2. Practical value and the cost-matched analysis
We both revised the claim and added a cost-matched analysis as suggested (Section 4.5). We now state that the practical result is the pulse itself, applied by a simple rule that does not need a forecast. The rule is to wait to step 1,000 and then give a short pulse to every run that has not yet gained the capability. With this rule all 72 runs acquire the capability, compared to 16 under ordinary training. From our experiments, we clearly note that waiting and then treating does better than choosing runs by forecast, as you observed. We therefore do not claim that forecast-based allocation is the best way to choose runs.
We agree that the cost matters for practical use. However, as the first method to estimate this probability for a training checkpoint, the committor's main contribution is to figure out when a run's outcome is decided and if something can ever change it. It shows which runs are failing rather than slow, and it decides how long a pulse each run needs (Section 4.3). Neither of these can be read from a single training run, and, while expensive, they do offer important information that could not be obtained otherwise. In a practical sense, this information is how we arrived at the rule above.
To make the forecast more usable, we also made it cheaper through the revisions. By using shorter restarts that stop at step 1,000 with more added only when the first four disagree, the cost ends up being about 3% of the full forecast. The AUC is 0.990 compared to 1.0 for all sixteen short restarts (Section 4.2). The forecast is most useful when a decision about a run has to be made early, before simply training it longer would show whether it succeeds. At step 100, it predicts the run's later held-out score with R² of 0.88 to 0.95, compared to 0.32 to 0.49 for the best checkpoint statistic (Section 4.1). Finally, the steering in our title refers to the pulse, and this holds on new seeds, a wider model and a larger task (Table 3).