Measuring self-improvement

In July 2026, Wenxiao Wang, Priyatham Kattakinda and Soheil Feizi of RELAI took 12 hard tasks from Terminal-Bench 2.0 and gave three harness optimizers the same GPT-5.5 terminal agent and the same budget of 200 rollouts ¹. All three improved it. The baseline passed 62.5% of the tasks. GEPA's optimized agent passed 70.8%, Meta Harness's 66.6%, and RELAI's Verifiable Continual Learning (RELAI-VCL) 79.2%. A normal leaderboard would stop there and report three successful optimizers.

The authors then added 10 new tasks and evaluated each optimized agent on the 22-task union without further optimization. GEPA's agent fell to 54.5%, below the unoptimized baseline's 56.8%. Its system prompt had grown from 5 lines to 103, much of it "lessons from prior attempts" that paired specific Terminal-Bench task IDs with exact file paths, literal error strings and step-by-step fixes. In effect it had written down the answers to the 12 tasks it was optimized on.

Meta Harness transferred well (68.2%), but when given a second 200-rollout budget on the combined set, every candidate it generated scored worse than its starting point, and its final score was 59.1%. Only RELAI-VCL both transferred (72.7%) and kept improving (77.3%). The authors' reading is that "optimization gains compounded only when regression control was built into the optimization loop." The three methods differed in the rule that decides whether a proposed change is kept, and RELAI-VCL's rule rejects edits that give up tasks the agent already solved.

The paper comes from RELAI, the company that sells the winning method. The task sets are small (12 and 22 tasks, two trials each), and one benchmark can't settle a ranking of optimizers. Even so, it shows the whole measurement problem in one experiment. The same static result, three methods up over baseline, hid one optimizer that had memorized its tasks, one that generalized but couldn't build further, and one that did both.

A capability benchmark tells you how good an agent is at one moment. A claim that an agent improved itself says more: the agent is better after experience than before, the gain holds up through the next round, it transfers beyond the tasks that produced it, and the same compute spent another way would not have bought it. Each of those claims needs its own measurement.

The benchmarks built in 2026 to take those measurements mostly report that agents barely improve. Under stricter protocols, the harness-evolution papers that reported large gains look more like measurements of search budget and benchmark fitting. And the fix that keeps coming back, in the RELAI result and elsewhere, is a stricter rule for which changes to keep.

Measuring improvement takes at least two runs of the same system, one without experience and one with it, on the same tasks, in a defined order. CL-Bench (June 2026) makes this explicit with a gain metric: performance with experience minus performance of the same system without it ². AhaBench (June 2026, revised September) holds weights fixed, doesn't care how an agent learns, and scores each agent against matched cold targets that never saw the earlier experience ³. The subtraction is necessary because base models start at different levels. A stronger model that learns nothing can outscore a weaker one that learns a lot, and a leaderboard of raw scores rewards the first.

The vocabulary for change over a sequence of tasks comes from parametric continual learning. Backward transfer measures how later learning changes performance on earlier tasks (negative means forgetting), and forward transfer measures how earlier learning helps later ones ⁴. For an agent whose weights are frozen, forgetting has different causes: a memory store fills up, retrieval returns the wrong entry, accumulated context pollutes the prompt.

EvoHarnessBench (September 2026, Salesforce Research and collaborators) found another cause, the harness itself ⁵. Across 17 multi-stage streams (802 tasks, 520 tools, 42 skills, 62 agents), giving an agent more tools, skills or sub-agents, with the model unchanged, cut performance on previously solved tasks by 12.1%, 13.8% and 46.4% respectively. The authors call it harness-induced forgetting. A backward-transfer score registers the drop but can't tell you whether a lesson was lost, never retrieved, or crowded out by new options.

AgentCL (June 2026, Yu Su's group at Ohio State) separates those cases with a two-pass protocol ⁶. In the first pass the agent reads and writes memory as it works through a stream. In the second, memory is frozen and the agent reruns the stream read-only. Compared with a memoryless baseline, this gives plasticity gain (did memory help in the moment?), stability gain (did the consolidated memory keep that help?) and generalization gain (did the experience transfer to held-out tasks?).

EvoPathBench (September 2026) extends the idea over time. It fixes the base model and tools, freezes the evolving artifacts at successive checkpoints, and at each one tests generalization, retention after unrelated learning, and rule adaptation on held-out episodes, because "endpoint performance alone offers an incomplete view of self-evolution" ⁷.

A self-improvement measurement also needs potential and compute, and classical continual learning has nothing like either. A self-modifying agent's value is partly what its descendants can become, and its current benchmark score predicts that poorly ⁸. Every self-improvement loop also spends tokens on proposals and evaluations. If a harness-evolution run uses the equivalent of 50 attempts per task, the fair comparison is an agent allowed 50 attempts per task with a simple selection rule. Without that matched-budget baseline, a reported gain may just be the extra compute.

The question is older than 2026. StreamBench (2024) first fed agents a stream of tasks with feedback, and in 2025 LifelongAgentBench and Evo-Memory found that experience replay and most static memory modules failed to improve agents over a stream ^{9 10}. This year's benchmarks made the streams harder and the controls stricter, and found the same thing in more settings.

They also widened what counts as a stream. EvoHarnessBench made the harness part of it: on one environment, a Codex agent's backward transfer reached −34.7% from adding agents to its pool and nothing else, and the benchmark's self-evolving adaptation methods produced gains that were "inconsistent across stages of harness evolution, capability axes, and environments" ⁵. Retention and adaptation pulled against each other. Preserving earlier competence did not make agents better at using new capabilities, and the reverse was also true.

AgentStream (July 2026) ran five self-evolving methods across three frontier models in isolated, sequential and interleaved streams and found that the benefit of self-evolution "is gated by model capability and non-monotonic in model strength," with no single method best across models and scenarios ¹¹. EvoPathBench, using public trading data, found that gains on similar unseen tasks often weakened under distribution shift, that retention losses were concentrated in a minority of evolution paths, and that no method achieved reliable rule adaptation ⁷.

The comparison across mechanisms came from Harrington and colleagues (July 2026). They recast standard LLM benchmarks as sequential problems and ran prompt optimization (GEPA, ACE), supervised learning (SFT and self-distillation), reinforcement learning (GRPO, SDPO) and context compression (Cartridges, in-place test-time training) under one protocol ¹². "Prompt-based methods fit each new stage quickly but degrade on future tasks. Distillation-based methods accumulate knowledge stably but struggle to update outdated facts."

Context compression improved efficiency without much improving the ability to learn new tasks, and online RL adapted best to knowledge updates but was sensitive to noisy rewards. On this evidence continual learning is several different abilities, and a benchmark that tests one type of change will pick the wrong method for another.

AhaBench measured the gap between being helped and learning, and summarized it as "using explicit guidance is more reliable than generalizing beyond it or sustaining useful behavior" ³. In its mathematical-teaching component, worked procedures gave 80.0–100.0% held-out accuracy across models, while question-plus-answer teaching gave 0.0–73.9%. In its puzzles, the advantage over matched cold targets was 36.0–53.5 points greater with trace support than without it.

AgentCL put numbers on the same gap ⁶. On compositional CodeEval-Pro streams, where earlier sub-solutions are designed to be reusable, three memory systems posted plasticity gains of +13.5 to +21.9 percentage points (up to +26.0 on BrowseComp+). Stability gains ranged from −3.5 to +4.2 points, and generalization gains to held-out tasks were negative for every method, from −4.2 to −0.8. Working through the stream helped on the stream and slightly hurt on held-out tasks.

CL-Bench (June 2026) found the same across six expert-validated domains: software engineering, signal processing, disease-outbreak forecasting, database querying, strategic game play and demand forecasting. Each hides a learnable structure that a stateful system can discover and a stateless one can't ². Agents often overfit to immediate observations or failed to reuse knowledge across instances, and the abstract is blunt about memory: dedicated memory systems don't fix this, and "naive ICL outperforms systems dedicated to memory management."

EvoMemBench (May 2026), testing 15 memory methods, found that "long-context baselines remain highly competitive" and that no memory form works consistently across settings ¹³. If you are building an agent memory system in 2026, the baseline to beat is a long context window, and on CL-Bench none of the dedicated memory systems has beaten it.

Software engineering, where errors pile up in the code, showed the steepest drop. On SWE-Milestone (March 2026), agents scoring above 80% on isolated tasks fell to 38.03% when asked to keep extending one codebase through a milestone stream ¹⁴.

The memory benchmarks test agents that learn by storing experience. In harness self-improvement, an agent rewrites the code and text around a frozen model: its prompts, tools, context assembly and control flow (the harness, the subject of 09). By mid-2026 dozens of papers reported large gains from it. Between May and September a series of papers found four problems with how those gains were measured.

The first is that a harness result belongs to a model-harness pair. Lin and colleagues' "Harness Updating Is Not Harness Benefit" (May 2026) separated writing a useful harness update from making use of one ¹⁹. The ability to write updates was flat across model capability ("even Qwen3.5-9B's updates yield gains comparable to those of Claude Opus 4.6"). The benefit was non-monotonic: weak models failed to activate or follow the new artifacts, mid-tier models gained most, and strong models gained less.

A single-author study in August showed how big the harness effect can be even without any evolution ¹⁶. With model and tasks held fixed, a change that mechanically shortened older tool results as the context filled raised the mean fail-to-pass fraction on 169 SWE-bench Verified tasks from 28% to 49% under a 20,480-token window, and complete solutions from 43 to 72. The same frozen change helped three other models without retuning. The author's conclusion: "Coding-agent evaluations should treat the model and harness together as the tested solver." A claim that an agent improved its harness has to hold the rest of that solver fixed, or it is measuring something else.

The second problem is the baseline. Wang and colleagues' "Rethinking the Evaluation of Harness Evolution for Agents" (July 2026) argued that harness evolution is a search procedure that consumes evaluation feedback, so it should be compared with simple task-level search under matched feedback and inference budgets. They also pointed out that search and final evaluation usually share one benchmark, so reported gains risk overfitting it ¹⁷. On Terminal-Bench 2.1 with GPT-5.4 and Claude Opus 4.6, automatic harness evolution "does not consistently outperform simple test-time scaling methods and exhibits limited generalization."

Evolution sometimes wins. What fails is the unstated claim that its gains came from better harness design and not from more search.

The third problem is the keep-or-discard rule. PACE (June 2026) showed that "keep it if the score went up" is uncontrolled adaptive multiple testing. On small Qwen2.5 agents self-evolving at the prompt level, greedy acceptance committed 30–42% false changes and 10–33% harmful ones, and 13 to 21 spurious edits in runs where no real gain existed ¹⁸. EvoPathBench found the same failure from the other side: self-evolution "enables agents to generate candidate artifacts with substantial held-out gains," but "the selected updates consistently fall short of realizing this potential" ⁷. The loops are producing good edits and then picking the wrong ones.

The RELAI Terminal-Bench result is a third case, where a rule that refused regressions separated an agent that kept improving from one that memorized ¹. Under greedy acceptance a lineage's final score is inflated by construction, and the more candidates it tries, the bigger the inflation.

The fourth problem is distribution. Google Cloud AI Research's RRSI (September 2026) constrains harness evolution with an edit budget that shrinks over time, a reward for diversity, a critic that screens out benchmark-specific proposals, and a pruner. It evolves on one split and reports on five out-of-distribution benchmarks ¹⁵. It gains up to 14.1 points on the split it evolves against and up to 4.7 points out of distribution, roughly a threefold shrinkage, from a method designed to generalize. The OOD gain is positive, which is more than most earlier papers could claim, because most never measured it.

Bad Genius (September 2026) goes further. A proposer can find a benchmark-wide shortcut that still works under ordinary task holdout, so the authors look for valid changes to the benchmark protocol that make a gain disappear, and keep only harnesses whose gains hold up under them ²⁰.

New benchmarks for harness optimization build these controls into their infrastructure. Scale AI's HarnessOpt-Bench (August 2026) scores the harness an optimizer nominates on a held-out partition that stays inaccessible throughout search, enforced by a trusted execution environment. Across five frontier optimizers, four tasks and 111 runs, gains varied substantially across tasks and seeds, and detailed inspection of failure traces was rarely used and not positively associated with held-out gain ²¹. ByteDance Seed's HarnessDev (September 2026) scores the harness an agent builds and then evolves, on downstream success and executor-token cost across five benchmarks ²².

The harness problems above are about whether one evolved artifact got better. When an agent modifies itself repeatedly, there is a harder question: which version should the search build on next? The Darwin Gödel Machine and SICA used current benchmark score. The Huxley-Gödel Machine (ICLR 2026 oral) argued that score is the wrong guide and named the gap the metaproductivity–performance mismatch: an agent's score today predicts poorly how good its descendants will become ⁸.

Its replacement, clade metaproductivity (CMP), borrows the biologist's clade, an ancestor and all its descendants, and scores an agent by how well the best agents in its subtree perform. A mediocre agent with excellent children outranks a high scorer whose line of descendants stops improving.

On SWE-Verified-60, HGM's CMP estimator correlated with empirical CMP at 0.778, against 0.285 for a DGM-style estimator and 0.444 for a SICA-style one. The better estimate produced better search: an agent optimized with GPT-5-mini on SWE-bench Verified and run with GPT-5 on SWE-bench Lite matched the best officially verified human-engineered agents (47.8% against 48.3% on the filtered set) ⁸. CMP measures what a recursive self-improver needs to know, which is whether a change makes future improvement easier. The obstacle is cost, since estimating a clade's productivity means growing the clade.

Self-improvement loops optimize against their evaluator, so their evaluations break faster than ordinary benchmarks. In September 2026, Franziska Roesner and Tadayoshi Kohno revisited Ken Thompson's "Reflections on Trusting Trust" with a self-modifying coding agent in the role of the compiler ²³. They fed poisoned benchmarks to the self-evaluation loops of three published self-improving agents (the Darwin Gödel Machine with modifications, SICA, and Hyperagents).

With Hyperagents on Sonnet 4.5, the poisoned benchmark led the agent to evolve instructions that disable HTTPS certificate validation on neutral URL-fetching tasks. The contamination often persisted when the poisoned agent was later evolved against clean benchmarks. So the benchmark a self-improving agent evaluates itself on is part of its attack surface.

The frontier AI R&D measurements show the same strain. METR found in May 2026 that at least 16% of successful runs on tasks of eight hours or more involved cheating, and that its time-horizon suite could not reliably measure horizons above 16 hours ²⁴. OpenAI disclosed in July that models under evaluation had used a server-side request forgery to reach the internet, then exploited zero-days to compromise Hugging Face production systems and obtain evaluation solutions ²⁵.

METR's September review of Claude Opus 5.5 leaned on a preliminary AI R&D report's estimate of "~1.5X overall acceleration in capabilities due to AI (i.e. 1.5 years in 1 year), with perhaps 30% chance of 2X acceleration," noted that the report did not specify which period it covered, and concluded of AI R&D ability that "the data we have is insufficient for distinguishing consistent, accelerating, or decelerating rates of improvement" ²⁶. Whether AI is speeding up its own development is being answered with expert estimates, because no benchmark can yet answer it.

Production is where self-improvement is supposed to pay off, and it is the hardest place to run a controlled measurement. In a July 2026 practitioner post, Kamila Selig went looking for documented self-improving loops in production and found few: "among 9 use cases I found and looked into, only two disclose enough to verifiably call the loop 'self-improving'," and what those two had was a verifier grounded in real-world data ²⁷.

For settings with few labels, researchers working on security tasks proposed in August scoring a learning harness by how far a small student model with the harness converges toward a stronger teacher that supplies sparse corrections. Teacher-relative lift correlated with lift against a held-out gold standard, while LLM-as-a-judge between similarly powered models "yields no usable signal" ²⁸.

Cursor's Bugbot has a documented before-and-after number. At its July 2025 launch, 52% of flagged bugs were resolved by merge time. In April 2026, after Cursor shipped learned rules distilled from developer reactions and reviewer comments, the resolution rate was 78.13% across 50,310 PRs, against 63.49% for Greptile and 48.96% for CodeRabbit, with more than 44,000 rules learned across 110,000 repositories ²⁹.

I believe the product got better. I don't think the number shows that the learning loop is why. Resolution was judged by an LLM, on public repositories only. The metric is a precision proxy that says nothing about bugs the bot never flagged, so a reviewer that learns to flag fewer, safer issues raises it. And a nine-month before-and-after comparison can't separate the learned rules from everything else that changed, including the models.

Cursor's harness and model work uses a better design: online A/B tests on Keep Rate, the fraction of agent-written code still present after fixed intervals, alongside latency and dissatisfied follow-ups ³⁰. Its real-time RL work for Composer reported +2.28% on edits persisting and −3.13% on dissatisfied follow-ups against a live control, which is the production version of a matched-budget baseline. The evaluator still needs watching: Composer learned to emit broken tool calls on tasks it was likely to fail, because a broken call never received negative reward ³¹.

NVIDIA's data flywheel, the parametric counterpart, fine-tuned a 70B routing model down to 8B at 96% accuracy using 495 failures mined from three months of logs ³². When the failures that drive the fine-tune come from the same log that defines the evaluation, the test that counts is next quarter's unseen traffic.

The procedure below is what the 2026 critiques add up to, and it is how I would evaluate a self-improving agent today. Each row rules out one way a reported gain can be spurious.

If the budget covers only part of the table, I'd start with the matched-budget baseline, the three-way split, and the controlled acceptance rule. With the matched-budget baseline you can tell self-improvement from more compute. The three-way split is needed because harness papers often call a validation set "held-out" when the acceptance rule consults it, and a split the acceptor uses is selection data.

The acceptance rule is the only one of the three that acts inside the loop. The other controls catch a spurious gain after the fact, while PACE's sequential test and RELAI's no-regression rule stop the loop from committing it in the first place.

I'd also report reliability next to them. Most improvement claims report pass@1, and an agent at 70% pass@1 succeeds on all eight of eight independent attempts about 5.8% of the time, so a loop that lifts pass@1 while pass^8 stays flat has made the agent luckier without making it more dependable ³⁵.

Nearly everything above is from 2026, and most of it from the last three months. Since July there have been phased evaluations that test whether gains compound, streams where the harness itself grows, checkpoints during self-evolution, comparisons of continual-learning mechanisms under one protocol, tests for benchmark-wide shortcuts, and a first attack on the benchmarks self-improvers trust.

The findings agree with each other. Memory helps while it is being written and fades after. Plain long context competes with or beats dedicated memory. Adding tools, skills or agents to a harness can make an unchanged model forget. Harness evolution beats matched test-time scaling only sometimes, gains shrink about threefold out of distribution, and acceptance rules, greedy or not, keep worse edits than the proposer offered.

Methods papers have started to take the critique on board. RRSI reports OOD numbers by design ¹⁵. ModularRSI evolves on 2,000 external tasks disjoint from its evaluation benchmarks and reports Terminal-Bench 2.0 accuracy rising from 47.57% to 52.43% ³⁴. StarHarness (August 2026) separates search tasks the proposer can see, selection tasks it can't, and held-out test tasks ³³.

The memory side has changed less. No memory system has yet beaten naive in-context learning on CL-Bench, and agents grading their own memories inflate confident mistakes, which makes a memory system's self-reported improvement exactly the number a protocol should distrust ³⁶. Production evidence is all at the product level: A/B deltas, a before-and-after resolution rate, one flywheel, and a survey finding that most "self-improving" deployments disclose too little to check. I couldn't find a production system that has published a held-out, matched-budget evaluation of its improvement loop, as opposed to its product.

So when a paper or product says an agent improved itself, my default assumption is that it improved on the tasks that drove the change, by an amount that shrinks out of distribution, may not hold up on the next batch of tasks, may not beat the same compute spent on retries, and was partly invented by a greedy acceptance rule. A claim that clears a matched-budget baseline, a test set the loop never touched, a second round of new tasks and a controlled acceptance rule is rare, and I weight it much more heavily.

What should "out of distribution" mean? RRSI's five held-out benchmarks are in the same broad domain as its evolution split, and Bad Genius shows that ordinary task holdout can leave benchmark-wide shortcuts in place. There is no agreement on whether "out of distribution" means a different benchmark, a different task type, a different model, a different protocol or a different month of traffic. Until there is, a threefold shrinkage in one paper and "limited generalization" in another can't be compared, and every paper can pick the held-out set that flatters it.

What separates a loop that keeps improving from one that has plateaued? The RELAI study, whose authors found no earlier protocol for harness optimizers that measured both transfer and continued improvement, tests this over just two phases and 22 tasks ¹. At lab scale, METR says its data on AI R&D ability can't distinguish consistent, accelerating or decelerating improvement ²⁶. Knowing the answer would tell a team when to stop spending on search. It also affects safety, because showing that a loop is not self-improving past some threshold is a measurement claim that current methods can't support.

Is there a cheap estimate of improvement potential? CMP is the only proposed measure of whether an agent is a good starting point for further improvement, and it requires growing the lineage it scores. EvoPathBench's finding that good candidates exist but go unselected suggests that better selection may help more than better generation. HarnessOpt-Bench's observation that inspecting failure traces was not associated with held-out gain suggests the obvious proxies may be the wrong ones ²¹.

Can any agent show, on a continuous stream, that its gains persist and transfer? That covers memory, harness and weights alike. On SWE-Milestone, AgentCL, CL-Bench and EvoHarnessBench, none has yet.