Open-source contributions.
Merged upstream.

A field-level prediction can look plausible while getting important regions or physical summary statistics wrong. FlowBench therefore compares the numerical reference, a neural prediction, and their error, and evaluates the model against persistence—the simple baseline that predicts no change. Vorticity describes local rotation in the fluid; in the visual, height and the blue-to-orange scale both encode the signed field value.

The project uses the NeuralOperator Team’s Navier–Stokes dataset from Zenodo, working with 32 × 32 fields obtained by stride-four decimation of the 128 × 128 archive. A four-layer residual CNN with 32 channels and 19,105 parameters is trained for 50 epochs; validation MSE selects the checkpoint. Circular padding follows an observed wrap-around continuity check. Splits, normalization, configuration, and data hashes travel with the saved checkpoint.

On 2,000 held-out pairs, mean relative L2 error is 0.4667 for the CNN versus 0.8359 for persistence. Mean absolute error falls from 0.4711 to 0.2570; mean relative enstrophy error falls from 0.9527 to 0.2272. A separate high-vorticity slice contains 204 test samples, with CNN relative L2 0.4681. The recorded batch-one inference path has p50 0.58 ms and p95 0.72 ms on the reported Apple M5/MPS setup, excluding HTTP overhead.

A single YAML configuration drives inspect → prepare → train → evaluate → serve. The FastAPI endpoint validates the input field and returns the prediction with model version, device, shape, and latency. The Streamlit viewer supports field and error inspection. Checkpoint reload tests verify that evaluation metrics reproduce within tolerance. The CNN is also packaged into ModelLaunch, connecting the scientific experiment to a gated local deployment workflow.

The dataset does not document the prediction horizon, physical units, or domain size sufficiently to claim them here. Enstrophy is computed as a grid mean, not a domain integral. No numerical solver is timed, so these results do not establish solver speed-up. The benchmark is one training run, at one working resolution, with decimation rather than anti-alias filtering. The website replays saved held-out fields; it does not run a new fluid simulation.

A nominal pulse assumes an ideal qubit. Detuning changes the effective frequency, while amplitude error changes control strength. PulseTune simulates those errors and measures average gate infidelity—the mismatch between the resulting operation and the target gate. Lower is better. In a hardware setting, each candidate trial can be expensive, which motivates asking how much improvement an optimizer can achieve within a small evaluation budget.

NumPy and SciPy construct segment unitaries from a closed-system Hamiltonian and compose the two pulse segments in time order. An independent PennyLane implementation cross-checks the physics. A Gaussian process with a Matérn kernel selects candidates using expected improvement, after eight warm-start calls. The same counted objective interface constrains random search and bounded Powell. Runs persist configuration, seed, every evaluation, elapsed time, and status, supporting cancellation and exact replay.

The benchmark spans nine error settings: detuning −0.3, 0, or +0.3 crossed with amplitude error −0.1, 0, or +0.1. Three seeds give 27 runs per method. The target is average gate infidelity at or below 0.001 within a 40-call ceiling, including warm-start calls. The nominal pulse is evaluated once. The chart reports how many runs reached that target; the table provides final-error statistics so success counts are not the entire story.

Random-start GP-EI reaches the target in 25 of 27 runs, with median final infidelity about 0.000252. A nominal-warm-start variant reaches it in all 27, with median about 0.000241; this variant was added after the first held-out run and is explicitly a post-hoc addition. Powell reaches the target in 9 of 27 runs and is much faster when detuning is zero. It stalls in the detuned settings, where GP-EI is more reliable. The result is conditional: Bayesian optimization helps with detuning, while Powell is excellent for the simpler amplitude-only problem.

The simulator uses exact closed-system dynamics: no decoherence, measurement noise, or state-preparation and measurement error. There is one qubit and only two constant pulse segments. Calibration at one offset transfers poorly to another because the objective does not optimize robustness. Powell’s repeated seeds produce identical paths from the same nominal start. This is a controlled simulation study, not a hardware calibration claim or a demonstration on photonic devices.

A model can keep returning valid responses while the population of requests changes beneath it. DriftGuard replays an English-heavy baseline followed by shifted-language traffic, computes model-derived features, and uses Population Stability Index (PSI) to trigger an adaptation workflow. Drift detection is treated as the start of an investigation, not evidence that a particular update will help.

The model runtime uses Qwen 2.5 7B Instruct in four-bit quantization with bfloat16 compute and PEFT adapters. Experiments compare a frozen baseline, selective LoRA weight updates, replay-regularized variants, warmup and broader update variants, and retrieval-based in-context adaptation. The selective retrieval path preserves English behavior and adds retrieved exemplars for shifted Hindi and Yoruba prompts. The pipeline produces JSON metrics, reports, and visual comparisons.

Token F1 measures overlap between generated and reference-answer tokens; higher is better. Each language now shows the frozen baseline and selective retrieval side by side on the same 0–0.4 scale. English remains 0.3608. Hindi rises from 0.2947 to 0.3223, and Yoruba rises from 0.0254 to 0.0879. The exact values and absolute changes are also shown in a table. Overall token F1 is approximately 0.2270 versus 0.2570.

The online LoRA branches were implemented and tested, but the recorded ablations were harmful in this setup. The reported overall token-F1 change for those weight-update variants is −0.1979. Retrieval-based adaptation performed better here. This matters because the more complex intervention was not automatically the better operational choice: an adaptation system needs comparison against a frozen baseline and a way to reject unsuccessful updates.

The evaluation contains only two prompts per language—six in total. These results establish a working experiment and an exploratory comparison, not broad multilingual quality or statistically reliable superiority. A stronger follow-up would enlarge the held-out set, measure recovery over time, test repeated traffic shifts, and validate a gate that chooses among retrieval, no action, and separately trained adapters.

A successful container start is not enough to declare an ML release healthy. The model may be inaccurate, its weights may be missing, requests may violate its schema, or latency may degrade only after promotion. ModelLaunch makes these cases observable and gives the release controller a defined recovery path.

A versioned bundle contains an ONNX model, preprocessing configuration, request and response schemas, evaluation information, and a manifest with a SHA-256 payload hash. Quality thresholds are declared before a release and evaluated against a fixed release-validation set. A single-node kind cluster hosts blue/green deployments, preview and stable Services, Prometheus, and Grafana. FastAPI with ONNX Runtime exposes separate liveness, readiness, prediction, and metrics endpoints.

The candidate first passes integrity and quality validation, then preview correctness and load gates. The controller promotes the stable route only after those checks pass. A subsequent Prometheus verification window monitors latency and errors. Confirmed threshold breaches trigger rollback to the prior stable release. Each run writes a structured release record that can be replayed and inspected.

The reference model released in 165 seconds with 12 gates passed. A degraded candidate with accuracy 0.425 failed the 0.9 gate before an image or pods were created. In the latency-fault drill, candidate p95 reached 868 ms against a 250 ms threshold; after two consecutive breaches, the previous model returned a healthy response 874 ms after detection. Detection itself took about 15.3 seconds after the fault was observed. A separate replica-kill drill recorded zero failures over 5,675 requests, and FlowBench released through the same gates in 155 seconds.

These are measured local experiments on the reported Apple M5 setup with two replicas, not availability guarantees for a production fleet. The distinction between fault detection time and recovery after detection matters. The project demonstrates release contracts, quality gates, health checks, observability, and incident recovery; broader cluster failure, multi-region operation, and organization-wide access controls require additional engineering.

A project can depend on a model that has been deprecated or retired even when its ordinary package dependencies remain healthy. ModelLedger scans source and configuration formats, discovers model references, and classifies them against lifecycle information so developers can see what needs attention.

The scanner performs deterministic discovery and emits human-readable findings plus JSON output. Active, deprecated, and retired states distinguish routine inventory from migration work and critical failures. CI-friendly exit codes allow a pipeline to block on a retired-model finding rather than leaving the result in an unread log.

The bundled lifecycle registry uses clearly marked synthetic records. The portfolio’s scan interaction illustrates those records and their status handling; it does not scan a visitor’s files or claim that a named commercial model is actually retired. Separating discovery from lifecycle classification makes the output inspectable and keeps the provenance of lifecycle data explicit.

The two tools address different parts of model operations: ModelLaunch controls how a candidate becomes a running service, while ModelLedger identifies model dependencies and lifecycle risks in the surrounding code. Together they show attention to deployment safety, maintenance, automation, and predictable command-line behavior.

The primary specification follows the time-series momentum setup associated with Moskowitz, Ooi and Pedersen (2012): take the sign of trailing excess returns over a 12-month lookback, scale positions using volatility, and rebalance monthly. The designated configuration uses a 40% per-instrument volatility target. Signals are decided at time t and earn returns only through subsequent positions. The study uses ETF proxies across equities, fixed income, currencies, and commodities over 2000–2026.

The repository contains the signal and backtest engine, gross and net performance accounting, property-based leakage checks, expanding walk-forward validation, combinatorial purged cross-validation, multiple-testing corrections, and Fama–French five-factor plus momentum regressions. The hypothesis, configuration grid, and evaluation plan were committed before results. Raw prices are cached and random procedures seeded so the experiment can be repeated.

Truncation invariance asks whether a signal changes when future data is removed; future poisoning asks whether corrupting future observations affects earlier decisions. Deliberately leaky positive controls verify that the tests can detect a problem. This process caught a full-sample quantile inside the volatility floor. Validation then uses overlap-based purging and a forward embargo instead of ordinary random folds. The nominal 12-configuration grid turned out to contain only six distinct strategies, because one volatility-target axis cancels under portfolio scaling; both counts are disclosed.

The primary historical backtest reports net Sharpe 0.706, annualized return 7.55%, annualized volatility 11.20%, and maximum drawdown −23.47%, after 5 basis points per side. A random-sign control through the same pipeline produces net Sharpe −0.045. Walk-forward out-of-sample Sharpe is 0.631; the five CPCV paths range from 0.546 to 0.706. The Deflated Sharpe Ratio passes across the tested effective-trial assumptions, but probability of backtest overfitting is 0.400. These are different diagnostics, not interchangeable seals of approval.

Passing multiple-testing corrections does not imply that returns are independent of known factors. UMD, the cross-sectional momentum factor, explains approximately 12% of monthly portfolio variation. Residual alpha is 3.97% per year, but its p-value moves from 0.0488 at Newey–West lag 21 to 0.0506 at lag 63. An initially striking currency-sleeve result also weakened after matching the analysis frequency to monthly rebalancing: the daily t-statistic of 7.31 becomes a monthly t-statistic of 2.84, and becomes insignificant after controlling for the other sleeves (t = 1.27, p = 0.20). The commodity sleeve’s independent loading remains an open research question.

ETFs are proxies for the futures instruments used in the original research, and the universe selects funds that still exist. Staggered inception means the early years are dominated by equities and Treasuries; the broadly diversified sample begins around 2007. Reported performance also declines across eras. The project supports a measured conclusion: the strategy has meaningful diversification and modest common momentum exposure, while the strength of residual-alpha evidence depends on statistical choices. It is a historical replication, not a promise of future returns.

CAISO demand and Open-Meteo weather feed lag, calendar, and weather features. The model predicts demand, receives the observed outcome, and uses the resulting error to update the ensemble. The architecture explorer shows the roles of the learners and their combination; it is not a live electricity forecast.

The fast branch is an online MLP that updates every step. The slower branch is an adaptive forest, updated every six steps by default. This configurable cadence lets the system combine rapid response with a second learning process. Recent absolute errors determine the blend, so a learner that has recently been less accurate contributes differently to subsequent predictions.

ADWIN monitors the error stream for change. Monitoring the forecast residual, rather than merely assuming the input distribution is stable, makes adaptation part of the forecasting loop. The project combines data ingestion, feature engineering, incremental models, and a serving simulator into an inspectable implementation.

The current portfolio presents the implemented architecture. A committed forecast trace is not available in the reviewed repository, so there is no invented observed-versus-predicted curve or accuracy improvement. The next evaluation should compare fixed and adaptive baselines on chronological held-out periods, report forecast error by horizon and operating regime, and inspect behavior around detected shifts.

The repository cites Back to Basics: Revisiting REINFORCE-style Optimization for Learning from Human Feedback in LLMs, alongside the Aya Dataset paper for multilingual context. It implements the RLOO sampling, scoring, advantage calculation, update, and evaluation workflow. The current policy is simulated; this is an implementation of the experimental logic rather than a reproduction of the original paper’s large-model training results.

For each prompt, sample four responses and score each one. A response’s advantage equals its reward minus the average reward of the other three responses. That leave-one-out comparison assigns credit relative to competing outputs for the same prompt. Training uses English and Hindi prompts; evaluation includes Yoruba as a held-out language. Generation, reward scoring, alignment, and evaluation are separate modules.

The experiment compares a frozen one-response baseline, best-of-four sampling without updates, and online RLOO. Reported mean rewards are 0.3864, 0.7463, and 0.8523 respectively; win rates are 0.2500, 0.5833, and 0.7500. The best-of-four control is essential: it asks whether the apparent improvement comes from policy changes or simply additional sampling. These numbers describe the simulated MVP and its reward mechanism.

A real QLoRA training loop, a stronger multilingual reward model, larger Aya evaluation slices, actual token and latency accounting, and comparison against SFT or DPO remain future work. The prototype demonstrates orchestration and estimator logic; it does not yet demonstrate large-model alignment gains or reliable cross-lingual transfer.

The repository draws on s1: Simple test-time scaling for minimum-budget forcing and forced continuation, and Plan and Budget: Effective and Efficient Test-Time Scaling on Reasoning Large Language Models for difficulty-aware allocation. It also discusses work on uncertainty verbalization and the effect of removing thinking tokens. The implemented contribution combines these ideas into a configurable generation-control experiment.

The baseline accepts the model’s natural stopping point. Minimum-budget forcing suppresses an early answer transition and injects a Wait-style continuation until enough reasoning budget is consumed. The plan-and-budget policy assigns minimum and maximum budgets according to estimated task difficulty. The runtime tracks forced continuation, forced termination, token use, answer accuracy, and overthinking.

At the reported 256-token ceiling, minimum-budget forcing and plan-and-budget both reach accuracy 1.0000 in the compact simulated benchmark. Average total token counts are 264 and 152 respectively, and recorded overthinking rates are 0.3333 and 0.0000. The ceiling applies to reasoning; reported total tokens include the answer. These outcomes illustrate the policy trade-off within the simulator, not measured performance from a deployed reasoning LLM.

The current runtime simulates generation. It does not reproduce the papers’ full training, models, or benchmark-scale evaluations. Next steps are a real Transformers or vLLM wrapper, model-specific delimiter control, MATH or AIME evaluation subsets, and measured inference cost and latency. The engineering question is whether adaptive budget control retains answer quality while reducing unnecessary computation.

The pipeline runs a student over a compact Aya-style multilingual pool, ranks prompts using uncertainty, rarity, and prompt length, sends selected examples through a teacher policy, validates the resulting pairs, and retrains the student. It contains separate orchestration, data-validation, and evaluation modules with automatically generated reports. The aim is a repeatable experiment in adaptive dataset construction.

The recorded run begins with six training examples. Both random selection and targeted top-k selection expand that set to ten. Token F1 is 0.0794 for the seed-only baseline, 0.0863 with random additions, and 0.0879 with targeted additions. Exact match remains zero, and the other reported metrics do not distinguish the two expanded sets. The small token-overlap gain is exploratory rather than a broad performance claim.

The current student is a lightweight memory-based proxy and the teacher is deterministic. The selection score approximates informativeness; it is not actual checkpoint-level Variance of Gradients. This should be presented as a research-inspired workflow prototype, not a completed reproduction of a transformer-training paper. The repository documents the gap between the implemented MVP and its intended research machinery.

Replace the proxy with a real model, compute gradient-variance signals across checkpoints, connect a capable teacher, and evaluate on a larger held-out corpus with repeated budgets and seeds. Validation before training remains central: selecting interesting prompts is useful only if the synthesized examples are valid and the evaluation can distinguish improvement from noise.