Here, hardware regression testing for a deployed AI model means re-running a fixed evaluation whenever the GPU, driver, toolchain, precision setting or model changes. Everything except the one factor under test should stay constant, with per-class accuracy and throughput compared against a threshold and sample size agreed before the run. The same model on the same inputs can give different answers when only GPU count, GPU type or batch size changes. One generic benchmark suite cannot cover that. Comparing revisions reliably takes three separate tools: a documented sign-off process, a harness built to isolate the cause of a change, and thresholds grounded in your own costs.
Hardware regression testing is not software regression testing with a GPU attached
Traditional software can lean on unit and integration tests of its code. An ML system’s behaviour is learned from data and cannot be strongly specified in advance, which makes it harder to test. GPU floating-point addition is non-associative, so changing the order of a sum changes its result. That order shifts with continuous batching, Split-K versus non-Split-K matrix multiplication, kernel block sizes, AllReduce collectives and tensor parallelism.
In Pham et al. (ASE 2020), 16 training runs of WideResNet-28-10 used the same RTX 2080 Ti, the same Keras, TensorFlow, CUDA and cuDNN versions, and fixed seeds, yet still landed between 77.3% and 80.2% overall accuracy. Per class, the spread was far wider: accuracy on the “camel” class ranged from 38.1% to 90.5% across those identical runs. So a hardware regression test has to measure its own noise floor before it can call anything a regression.
TechnoLynx treats production AI reliability as its own engineering discipline, separate from model accuracy. Its deliverables are the regression suites, evaluation harnesses and release gates that catch silent quality drift and rare-class failures, which unit tests miss.
Which changes should trigger a hardware regression run?
Run one before and after any change that can alter the order or precision of arithmetic, or alter what the model sees. Bouthillier et al. (MLSys 2021) saw different GPU models produce different results, ran into problems when CUDA drivers were updated, and found that PyTorch versions changed results too. They pinned CUDA 10.2 and PyTorch 1.2.0 for every experiment. They also found that convolutional models gave reproducible results only with cudnn.deterministic enabled and cudnn.benchmark disabled. A 2025 arXiv study of LLM inference used a grid of 12 runtime configurations: two GPU types (L40S and A100), two GPU counts and three batch sizes.
The table below lists the factors to vary one at a time, with what to hold fixed while each one moves.
| Change | Why it can move results | Hold fixed while testing it |
|---|---|---|
| GPU model or architecture | Floating-point implementations and memory hierarchies differ, and A100s showed slightly higher probability variance than L40S in identical configurations | Driver, CUDA stack, framework, precision, batch size, model, data |
| GPU count or tensor-parallel size | Parallel reductions and collectives change summation order | Everything else, including GPU type |
| Driver and CUDA or cuDNN version | Driver updates were observed to change results | GPU, framework, model, data |
| Framework or runtime version | PyTorch versions were observed to change results | GPU, driver, model, data |
| Numerical precision | BF16 was the least stable format and FP32 close to deterministic | GPU, batch size, model, data |
| Batch size | Smaller batches produced higher variance in token probabilities | GPU, precision, model, data |
| Model revision | This is the change you usually want to measure | Hardware, software stack, data |
| Input data or camera | This changes what the model sees, not how it computes | Hardware, software stack, model |
What a per-class accuracy and throughput regression test should measure
Measure accuracy per class and per condition (camera type, lighting, defect type), never only in aggregate. An April 2026 arXiv study of diffusion language models found that inference configurations with nearly identical dataset-level accuracy can give substantially different predictions on the same inputs. Correctness flips in both directions average out, which hides them. Across numerical precision, GPU type and batch size, that study found dataset-level accuracy close to constant while sample-level variability matched the variability caused by changing the model itself.
Two numbers are worth adding to the per-class table. The first is a per-sample flip rate: the share of configurations that disagree with the most common prediction for that sample, averaged over the dataset. The second, for generative models, is output length. In the 2025 LLM inference study, changing the system configuration under BF16 shifted the response length of DeepSeek-R1-Distill-Qwen-7B by up to 9,000 tokens.
Throughput belongs in the same harness as accuracy. Breck et al. (Google) recommend slicing computational metrics such as latency, throughput and memory by code, data and model version, because a regression can arrive as a sudden drop or as a slow leak. Measure throughput and power at the batch sizes and precision production actually runs, sustained over a realistic window, because a short burst on an idle card says little about a loaded fleet.
Which test cases belong in a hardware regression suite?
The suite needs every class and condition you will make a release decision on, each in large enough numbers to measure on its own, plus a cheap per-component probe set that runs first. A 2026 arXiv study on regression test selection proposes probing each updated module on its own and running the full end-to-end test only when the module-level margin is too small to decide. On its dual-arm robotics task, that hybrid selector matched the ground-truth regression label on 81.25% of update events at half the cost of full revalidation. The authors measured this headline result on one task only, so it shows a useful structure, not a general rate.
A fixed test set brings its own trap. Bouthillier et al. warn that improvements smaller than a test set’s own sampling variance will not generalise, and recommend multiple random splits where the comparison needs more statistical power. Breck et al. add one fully automated test that exercises the whole pipeline, from data through to the serving system, because errors introduced in one stage surface several stages later.
Deliberately over-sample rare classes and hard conditions, since those are where per-class swings hide and where a missed regression costs the most.
How many samples per class, and which confidence interval?
Plan the sample size per class, not per test set. A 2012 sample-size study for classification models found that 75 to 100 test samples are usually needed to test a good but imperfect classifier. Its worked figures: about 140 samples per class give a confidence interval no wider than 0.1 when 90% sensitivity is expected, and comparing two models at the usual power of 0.8 needs at least 100 independent test cases of the class for each model.
The interval method matters as much as the count. A 2026 arXiv study on classifier uncertainty found that at a true recall of 0.95 with 20 relevant samples, Wald and percentile-bootstrap intervals covered the true value only 66% of the time. Agresti-Coull, Wilson and Clopper-Pearson intervals stayed accurate at sizes as small as 10. The same study recommends Agresti-Coull as the default for independent data. Clustering is the next trap. With 5 to 50 contributors producing about 30 samples each, an unadjusted Agresti-Coull interval covered the true metric only about 65% of the time. Adding contributors improved precision more than adding samples per contributor. In a camera fleet, frames from one truck or one camera behave like samples from one contributor, so the independent unit is the combination, not the frame.
Evaluation resolution can flip a verdict. In the 2026 regression-selection study, the same comparison run at 30 evaluation episodes per probe showed full revalidation significantly ahead. At 100 episodes the gap disappeared, and the authors traced the reversal to evaluation resolution, not to platform or protocol.
Setting pass/fail thresholds from your own cost and throughput
Pass/fail thresholds should come from the system’s own measured costs and throughput, not from numbers borrowed from industry reports. Breck et al. suggest anchoring quality thresholds to the bounds the system had when it first launched. They also separate two cases. For slow degradation over many versions, use looser thresholds against a validation set. For a sudden drop in a new version, compare against the previous version with tighter thresholds.
Comparing averages alone is not enough; the variance has to be accounted for. Bouthillier et al. propose requiring a high enough probability that one configuration outperforms the other in a single run, P(A > B) ≥ γ, instead of a fixed difference in means. They found γ = 0.75 robust across their case studies. When several metrics drive one decision, per-metric intervals mislead: in an IEEE TKDE study on confidence intervals for performance measures, individual 95% intervals covered two parameters jointly only about 91 to 92% of the time. Joint intervals restored coverage close to 95%.
The 2026 regression-selection study notes the errors are not symmetric: a missed regression releases a silently broken system, while a false alarm only adds test cost. Set the tolerance per class from what each error actually costs: the price of a missed defect against the price of a false reject, with a throughput floor taken from the capacity the fleet must sustain.
Sign-off has to be written down before the numbers arrive
The single-run trap shows why. In Pham et al., ResNet56 beat ResNet38 by 0.9% on average over 16 runs, with significance confirmed. Comparing ResNet56’s worst run against ResNet38’s best would have shown a false 1% gain in the other direction. The authors recommend adding replication runs until a statistical test such as the Mann-Whitney U-test confirms the difference. They pair it with Levene’s test for differences in variance and Cohen’s d for effect size.
A sign-off document that holds up under pressure states, before any run, the metrics, the per-class sample sizes, the interval method, the threshold or probability criterion, the configurations under test, and who approves a borderline result. Agreeing those terms after seeing the numbers turns a test into a negotiation.
A GPU scheduler release gate should follow the same logic: a numeric tolerance fixed in advance, every representative workload shape, each GPU generation such as A100 and H100 tested separately, and the release blocked on any failure. TechnoLynx’s GPU Performance Engineering practice profiles and optimises kernels, memory and parallelism on the target hardware.
Can hardware regression testing run automatically before every deployment change?
Yes, as long as the inputs stay comparable over time. Breck et al. call for a pipeline integration test that runs continuously and on every new release of models or servers, so problems are caught before they reach production. Reproducibility makes this tractable, because deterministic behaviour is what lets you diff an old configuration against a new one with confidence. Where greedy decoding is evaluated with a single run, the 2025 LLM study recommends FP32 to improve reproducibility.
Trigger the harness on any change to the container image, driver, engine build or model hash. A clear failure should block the release automatically, and a result inside the noise band should go to a named reviewer. The automation is only as trustworthy as the versioning behind it: an unpinned data pipeline or a floating driver version quietly breaks comparability between runs.
Re-testing a T4 and L4 camera fleet after new defect classes and camera upgrades
For a camera inspection fleet on T4 and L4 GPUs that has gained new defect classes and camera upgrades, the work splits into two deliverables: an auditable error-rate report per truck and camera combination, and a regression harness that isolates hardware, model and data as causes of change.
TechnoLynx builds both for this kind of fleet. TechnoLynx starts the work by defining what counts as a reportable error for each combination and what makes a before-and-after comparison fair. LynxBenchAI measures the hardware, and the harness measures your workload on it.
Can you give us error rates broken out by truck and camera model?
Yes, provided each truck and camera combination has its own held-out, labelled test set with fixed ground truth and a fixed evaluation protocol, re-run on a defined cadence. The structure below is our recommendation, not an industry norm:
- one row per truck and camera combination, and per defect class within it, with the sample count next to every error rate;
- an interval for each rate, computed with a method that stays accurate at small counts (Agresti-Coull or Wilson) and adjusted for clustering where frames come from the same unit;
- the hashes of the model, engine, driver and container that produced the numbers;
- the protocol version and the date range of the test data, so the next report can be compared with this one.
Two limits belong in the report itself. A report is only as good as the representativeness and labelling quality of its per-combination test sets. And a combination that has not been tested is unknown, because accuracy on one camera generation and lens package does not tell you accuracy on another.
Is the accuracy drop due to the hardware, the model or the new camera data?
Run the same per-class harness three times, each time changing exactly one factor, and compare per-class deltas against the measured noise floor instead of comparing aggregate scores. The hardware-only run keeps the old model and old data on the new GPU. The model-only run puts the new model on the old hardware and old data. The data-only run puts the old model on the old hardware with the new camera inputs. This mirrors the controlled designs in the sources: Bouthillier et al. varied one source of variance while holding the others fixed, and the 2026 regression-selection study used a paired swap protocol that isolates the effect of a single module update, with per-cell McNemar tests on paired seeds.
New defect classes complicate the data-only run. The old model cannot detect classes it was never trained on, so the attribution covers only the classes present in both versions, and new classes are judged against their own agreed targets. One-at-a-time runs also miss interactions, such as a precision change that matters only at the new camera resolution. Where a combined run disagrees with the sum of the single-factor runs, that disagreement is itself the finding. For the throughput side of the same question, see proving whether bottlenecks are hardware or software.
Can this be repeated automatically before each future tour?
Yes, once the data pipeline is stable and every model, engine and hardware configuration is versioned. The harness and report can then be scheduled before each tour or each hardware and toolchain revision, with the previous report as the baseline.
Who can build a hardware regression harness for our inference fleet, and should we build it in-house?
TechnoLynx builds the evaluation and regression harnesses that deployed models need. This sits in TechnoLynx’s Production AI Reliability practice, and the first step is framing what counts as a regression and a fair comparison. Building in-house makes sense when the team already owns labelled per-condition data, a CI pipeline and someone who will maintain the statistics. A specialist earns its place when the harness has to stand up in a contract review or ship on a fixed date. When choosing a partner, ask to see how they separate noise from regression before you look at any accuracy figure.
This engagement does not suit teams that want a single leaderboard number for a hardware purchase. Published LynxBenchAI results serve that need better, though they measure hardware and not your workload. Teams with mature MLOps practice can reasonably build the harness themselves from the methods above.
Whatever its quality, a regression harness can only vouch for what is inside it: the truck and camera combinations, SKUs and workload shapes you chose to test. The decision that remains is which untested configurations you are willing to ship, and that answer belongs in the written sign-off, not in someone’s head on release day.
