RLVRAMBench

Which language-model training configurations can I use with the memory I have, and how much testing does that decision require?

RLVRAMBench is a measurement dataset with open evaluation tasks for a specific language-model training system. It measures memory feasibility when response generation and reinforcement-learning updates share the same graphics processors. It provides measured outcomes, fixed prediction tasks, a budgeted decision replay, reference methods, and raw failure evidence. It does not score a model's intelligence or learning quality. The companion article is Memory Feasibility in Colocated Language-Model Reinforcement Learning: A Failure-Aware Measurement Study. This is a focused, extensible study, not a comprehensive cross-platform benchmark or evidence of community adoption.

The default table above is a readable twelve-candidate experiment. Each row shows the model, workload, hardware, training settings, earlier source label, new screening outcome, and a repeated evaluation outcome obtained from different random seeds. The other views expose the broader measurement corpus and transfer tasks.

Authors: Ondřej Kobza and Jan Šedivý, Czech Institute of Informatics, Robotics and Cybernetics, Czech Technical University in Prague. ORCID: Kobza, Šedivý.

• Paper PDF
• Supplement
• Public reproduction code
• Benchmark instructions
• Data dictionary
• Pinned release and archive

What is measured?

Each process either completes its requested training and scheduled operations, has a diagnosed memory failure, or remains unresolved for resource-label purposes. External device-memory samples measure the maximum used memory on any one allocated device, not a sum across GPUs.

For the three distinct eligible evaluation seeds of a configuration:

Outcome	Meaning
within_margin	All three complete and each peak is at most 38,912 MiB
above_margin	All three complete, but at least one exceeds that limit
memory_failure	At least one eligible run has a diagnosed memory failure

The limit leaves 5% below the measured capacity of 40,960 MiB per device. It is a stated operating convention, not a statistical guarantee. One mebibyte (MiB) is 1,048,576 bytes. Failed runs do not have a counterfactual completed-run peak; blank completed-peak fields are not zero. All three slots must have eligible outcomes before the repeated label is assigned, even if a partial record already contains a diagnosed failure. Unresolved attempts and known partial failure evidence remain visible.

These are conditional memory outcomes. They do not say that every scheduler job, software invocation, or future repetition will complete. The full attempt history is therefore separate from eligible labels.

Ways to use the measurements

1. Predict a target outcome from existing measurements

A method receives explicit source measurements and target settings, but not target outcomes. It predicts one of the three labels. For example, can a configuration measured on four GPUs run on two?

The static suite contains 52 tasks and 400 queries across model, workload, GPU-count, and run-duration transfer. Queries reuse 94 distinct target configurations. They are not 400 independent experiments. Source-copy, always-approve and always-reject results are provided.

Use the public code repository:

python3 benchmark.py verify
python3 benchmark.py baseline --rule source_label --output predictions.csv
python3 benchmark.py evaluate --predictions predictions.csv --output scores.json

For another method, export allowed evidence with benchmark.py inputs, then provide a CSV with query_id,predicted_state. The evaluator rejects missing, duplicate, extra or invalid predictions. Reading the public target tables while producing predictions violates this task contract.

2. Decide which candidates to admit as tests become available

The admission panel asks whether available source evidence helps identify usable target configurations before all of them have been tested. It contains four model–workload cases, three candidate settings per case, and 48 fresh processes:

• One five-step screen per candidate can be requested by a rule.
• Three separate five-step evaluation seeds determine the target label.
• Screening outcomes never contribute to that evaluation label.

Source copy initially approves the donor's within-margin settings. A headroom guard also requires an additional source-memory allowance. Direct screening starts without approving any candidate and uses no donors. All request screens in the same frozen order. Each invocation is charged before its outcome is revealed; unrequested target results remain hidden from the replay.

python3 decision_benchmark.py replay \
  --protocol benchmark/decision/protocol.json \
  --attempts benchmark/decision/results/attempts.json \
  --output admission-scores.json

scores.json includes each case, each budget, requested attempts, revealed screens and resulting decisions. summary.csv is the compact comparison. The protocol and prelaunch amendment are retained with their timestamps. No memory failure is retried to obtain a favorable outcome. Unresolved evaluation slots retain admissible-outcome bounds.

Observed admission results

All 48 planned processes supply validated memory outcomes, with no retries or unresolved slots. The twelve evaluation candidates contain six within-margin configurations, two above-margin configurations, and four memory failures. Screens and separate evaluation repetitions agree in this panel.

Rule	Case-averaged recall before testing	First tested common per-case budget with full recall	Prior donor attempts across four cases	Memory-failure / above-margin approvals
Copy the source label	100%	0	36	0 / 0
Additional headroom guard	75%	1	36	0 / 0
Direct screening	0%	3	0	0 / 0

Direct screening reaches 25%, 75%, and 100% case-averaged recall at budgets of one, two, and three attempts per case. Case averaging gives each model–workload combination equal weight, rather than pooling candidates. The guard initially rejects two usable Qwen candidates. Source copy and the guard differ only at those candidates, which are queried first; their positive-budget decisions are identical by construction, not two independent confirmations.

This is evidence that the specified existing measurements were sufficient for this selected workload change, not a universal transfer result. The separate GPU-transfer task below contains harmful approvals. The first common budget attaining full recall is not a proof of the minimum number of tests an optimized strategy would require. Without an existing donor profile, the attributed counts for full recovery are 36, 40, and 12 attempts respectively, with different work per attempt. Thus the comparison does not establish cold-start or GPU-time superiority of transfer. All three rules have 100% observed precision wherever they approve anything; the small panel does not estimate future failure risk.

3. Compare estimators with complete model families held out

The separate benchmark/estimation/ comparison asks whether architecture and configuration information improves on copying an earlier outcome. It uses ninety historical configurations. Each of three tests withholds all thirty configurations of one model family and fits on the other sixty. Seeds and alternative GPU counts of the test family are not fitting examples.

References include donor copying, empirical component regression with a one-sided startup check, and regularized logistic classification. The regression uses completed peaks without inventing numerical targets for failures; the classifier also learns from failure labels. These are not exact tensor-liveness models or calibrated failure probabilities.

Results differ by family: regression gets every Qwen label right but approves four memory-failing Granite configurations; the classifier rejects six usable Qwen settings. Read the separate approval errors, not just accuracy. The historical labels were public during design, so this is not blind method development.

The estimator guide explains inputs, frozen predictions, acquisition costs and CPU reconstruction.

4. Inspect prospective larger-model transfer

The larger_model_configurations view contains twelve planned Qwen2.5-7B settings with predictions frozen before target execution. Each row shows how many of its three seed outcomes are eligible, any known partial failure evidence, the resolved label when available, and each method's prediction. This is size transfer within a familiar model family, not a new-family test.

The original panel has 23 eligible startup memory-admission failures and 13 unresolved slots, with no completed training steps. Only six repeated labels resolve, all to failure. Donor copying wrongly approves those six; the fitted references reject them, but an always-failure rule does too. Their scores on this subset do not demonstrate recovery of usable settings. In particular, the regression's three approvals have unresolved outcomes.

The expanded_host_configurations view is a separate follow-up to host-memory exhaustion in the original panel. It retains the frozen predictions, uses new seed slots, and increases the host-resource allocation. Its six settings are not replacements for original targets. All nine two-GPU invocations fail the startup memory check. The nine four-GPU invocations exit successfully but lack the required final-step record, leaving their three repeated labels unresolved. No validated completion is available in this panel either. See the follow-up guide for the diagnostic evidence and separate allocation costs.

What score should I report?

Report within-margin recall at a stated measurement budget, together with separate memory-failure and above-margin approvals.

• Recall: what fraction of the genuinely within-margin candidates did the rule approve?
• Approval precision: what fraction of its approvals were within margin?
• Approval errors: how many approvals actually fail for memory, and how many complete but exceed the chosen limit?
• Effort: how many target attempts were requested? Was source evidence already available or did it have to be collected?

A zero denominator is null, not a perfect score. Approving nothing avoids approval errors but recovers nothing; approving everything recovers every usable candidate but may also admit failures. Neither should win by hiding the other side of that trade-off.

There is intentionally no unexplained scalar combining errors and cost. Those trade-offs depend on the user's application. Label accuracy is provided for diagnosis, not as a universal deployment ranking.

An exact example from GPU-count transfer shows why this matters:

Reference rule	Correct labels / 36 queries	Within-margin targets approved	Memory failures approved	Above-margin targets approved
Copy the source label	20	20	2	4
Approve everything	26	26	4	6
Reject everything as a memory failure	4	0	0	0

“Approve everything” has higher label accuracy than copying, but admits twice as many memory failures. Pooled accuracy also overweights easy tasks: 216 of the 400 queries are workload transfers solved by lookup on this grid. The four duration queries offer little discrimination. Always retain the per-track and per-case results.

What does this release contain?

The static tables contain 212 settings, 612 eligible processes, 683 recorded attempts and 3,434 observed stage measurements. These include the original 588-process corpus and 24 completed batch-by-logging controls. Sixteen historical source screens are counted separately in the archive. The 48-slot admission panel is separate; it is not silently added to the unchanged static-table totals. The estimator comparison reuses ninety of those historical configurations; its three test folds are not additional GPU experiments. The original larger-model panel and expanded-host follow-up have their own configuration and process tables. Their planned slots, unresolved outcomes, and costs are not included in the static or admission totals above.

The default candidate table is a useful entry point. configurations.csv contains settings without outcomes. configuration_results.csv and transfer_configurations.csv join them for browsing. runs.csv, attempts.csv, and stage_measurements.csv preserve process, invocation, and execution-stage detail. They have different units and must not be concatenated into one dataset of independent examples.

The compressed review archive contains raw training logs, external memory traces, allocator records, environment provenance, frozen matrices, attempt exclusions, and reconstruction code. Model weights and optimizer checkpoint payloads are not redistributed.

Cost accounting

For static prediction, source-cost fields count supplied evidence; they are not measured acquisition effort by a method.

For admission replay, three ledgers remain separate:

1. The donor evidence already available to transfer-informed rules.
2. The target attempts actually requested at each budget.
3. All physical runs collected to evaluate the rules, including hidden evaluation seeds.

Cold-start accounting charges the donor investment as well. It does not make those measurements free or establish superiority over a direct strategy allowed an equally large budget of extra target repetitions. One donor step and five target steps also have different runtime costs. Recorded GPU-seconds exclude queue time and other allocation overhead.

Scope and appropriate reuse

The experiments use compact language models with low-rank adaptation and Group Relative Policy Optimization, in a fixed VERL/vLLM execution stack. Generation and training share NVIDIA A100 devices. They ran on Karolina, a supercomputer at IT4Innovations in Ostrava, Czech Republic.

Use the records to evaluate resource-label prediction, compare measured admission decisions, audit failures, study why stage and overall peaks differ, or reconstruct the paper. Do not use them to claim a general failure probability, convergence benefit, safe full training schedule, or transfer to unmeasured hardware and model scales.

The cases were selected, not randomly sampled. New admission outcomes come from familiar model/workload families; their four cases are not 48 independent cases. The public labels make inspection possible but also mean this is not a permanently hidden test set. Strong claims about a new predictor need genuinely unseen cases beyond this release.

Some historical executions used modified source working trees without captured per-run patches. Their commit IDs do not by themselves reconstruct those modifications. Later controls and the admission panel use immutable source copies. Rebuilding results from saved traces is distinct from recreating every historical GPU execution.

Reproduce and cite

The code repository pins an immutable evidence archive and verifies its SHA-256 digest and extracted file manifest. CPU-only reconstruction regenerates results from raw evidence before comparing them with the published tables. Optional filesystem isolation hides those reference tables and the original project during analysis.

GPU reruns are a separate, more demanding task: obtain upstream models under their terms and adapt the recorded environment and cluster-specific launchers. Keep all virtual environments inside their project directory.

Original benchmark measurements and reproduction software are MIT licensed. Third-party data, model, software and template terms remain separate; see RIGHTS.md. The archive is not a relicensing of upstream material. Both benchmark and code repositories are public and ungated. No DOI is claimed until the authors create one.