Toward Recursive Self-Improvement in Physical AI

1 Introduction

• RSI requires retained gains to improve the next revision and the improver to use what it gains to help produce its own next improvement.Digital agents such as STOP and the Darwin Gödel Machine revise code and evaluate candidates with executable tests, but better task performance alone is not recursion.Source: §1 · p. 3
• Physical RSI must contend with partial sensing, costly trials, changing conditions that can cause irreversible consequences, and changes to body-specific components.Physical outcome checks depend on sensors and verifiers; trials consume robot time, resets, supervision, and wear.Source: §1 · p. 3
• Policy, world-model, and external-knowledge changes improve what a robot does; revising data collection, evaluation, or updates improves how it learns.RECAP, PlayWorld, and Zetta illustrate the first routes; Eureka and ENPIRE (Xiao et al., 2026b) illustrate procedure changes, where physical RSI would begin.Source: §1 · pp. 3–4
• Gains carry forward when feedback addresses remaining learning needs, the recipient can use the change, its value survives shifts, and practice stays safe and affordable.A change can improve execution without helping later learning; added autonomous data can yield modest gains that saturate or regress (Mirchandani et al., 2025).Source: §1 · p. 4
• Robot-learning traditions pass more from one episode to the next, while recent systems can direct experience to update-producing machinery as well as the policy.RoboCat, Eureka, and ENPIRE illustrate changes reaching a data collector, reward function, or training infrastructure, alongside the policy that receives updates.Source: §1 · p. 4
• The review organizes progress by what changes and who uses each change next, covering physical learning systems while excluding autonomous morphology design and physical self-reconstruction.It separates evidence that changes an improver’s knowledge or tools from evidence that the improver itself has improved; recursive gains still require dedicated verification.Source: §1 · pp. 4–5

2 Foundations of Physical RSI

• The review follows each system from physical experience to a retained change and then to its next use, without assuming a shared architecture.This path is used to examine whether a gain survives another round.Source: §2 · p. 7

2.1 Learning to Act

• Robot policies map observations to actions, while demonstrations and reward-based trials provide learning signals; hardware trials also consume time, supervision, wear, and resets.Systems may fine-tune policies, use models to predict outcomes, or retain improvements outside network weights.Source: §2.1 · pp. 7–8

2.2 Defining Recursive Self-Improvement

• A repair changes task data or skills, while an improver changes rules for collecting, evaluating, or updating learning experience; behavioral gains alone do not prove procedure improvement or recursion.Procedure improvement is tested with matched learners sharing starting conditions, resources, and evaluation.Source: §2.2 · p. 9
• RSI requires retained repair knowledge to improve the improver’s procedures (R1), then to produce a successor that beats both its parent and a frozen-knowledge revision (R2).Both links require comparisons that isolate the acquired knowledge; changing an improver alone does not establish recursion.Source: §2.2 · pp. 9–10
• Gains carry forward when feedback identifies remaining needs, the receiving component can use the change, its value survives shifts, and further practice remains safe and affordable.These overlapping conditions are diagnostic lenses, not independently validated constructs.Source: §2.2 · p. 11

2.3 Relating RSI to Robot Learning

• Robot learning paradigms can support different improvement claims, but RSI additionally requires the process that produces revisions to change through its own repair history.Meta-learning and AutoML can improve learners or learning procedures while leaving the outer revision process fixed.Source: §2.3 · pp. 11, 13

2.4 Facing Physical Limits

• Physical RSI is constrained by imperfect diagnosis, scarce hardware trials, resets, and transfer gaps; revision histories accumulate slowly and simulation-based screening still requires validation.Simulation offers cheap, repeatable trials but omits physical effects, while hardware captures contact, sensing, and wear.Source: §2.4 · pp. 13–14

2.5 Benchmarking Self-Improvement

• With GPT-6 Astra, withholding earlier-round information lowered success over rounds 4–6 from 15 of 36 attempts to 3 of 36.PhysRSI-eval (Li et al., 2026j) evaluates persistent-workspace revisions in simulation; benchmark scores can diverge across attained performance, gain timing, and budget saved.Source: §2.5 · p. 14
• Success rate is the most common measure, while some benchmarks add partial task-stage credit or execution efficiency such as cycle time or throughput.HIL-SERL reports cycle time, and RECAP (Physical Intelligence et al., 2026) reports throughput.Source: §2.5 · pp. 15–16
• Learning efficiency measures time, episodes, or supervision needed to reach a performance level, with reports using different thresholds and horizons.ConRFT (Chen et al., 2025d) reaches 96.3% average success on eight real tasks after 45–90 minutes of online fine-tuning; VLAC (Zhai et al., 2025) raises real success from about 30% to 90% within 200 episodes. ENPIRE (Xiao et al., 2026b) reports fleet time to target, while LMPC (Liang et al., 2024) counts chat turns per successful teaching session.Source: §2.5 · p. 16
• Retention measures whether competence survives later learning or deployment, while forward transfer measures a later-learning benefit on a new task.ACCRUE (Kim et al., 2026) reports transfer as reduced real-robot training time for later tasks, CIDER (Li et al., 2026d) reports forward transfer of an accumulated policy, and MC-EvoBench specifies needed controls.Source: §2.5 · p. 16
• Resource use spans robot hours, demonstrations, interventions, compute, or tokens, and differing accounting means reported costs are not directly comparable.CARD (Sun et al., 2024) needs about 14K tokens per task against about 663K for Eureka; ENPIRE’s fleet scaling shortens time to target with lower per-robot utilization and faster-than-linear token growth.Source: §2.5 · p. 16

3 Mechanisms toward Physical RSI

• Section 3.4 tests whether an improved improver helps produce its own next improvement, rather than adding a fourth component.The review discusses systems mainly where their experiments test them, with cross-references for systems serving several roles.Source: §3 · p. 16
• Section 3.2 covers changes to the learning procedure that collects, judges, and updates.A policy trained with relabeled targets, a reward, or an optimization algorithm remains a learner change when those rules stay fixed.Source: §3 · p. 16
• Section 3.1 covers learner changes kept in policies, world models, or external knowledge, while Section 3.3 covers changes to the improver that revises the procedure.Source: §3 · p. 16

3.1.1 Policy Updates

• Policy updates must match the teaching signal to the failure: relabeling, rewards, corrections, and replay address different learning needs.Adding autonomous data can yield modest gains that saturate or regress; useful data must expose difficult conditions and supply actions that help there.Source: §3.1.1 · pp. 16, 17, 20
• Policy behavioral gains are well established, but later-learning benefits are rarer; RoboCat (Bousmalis et al., 2024), PLD (Xiao et al., 2026a), and CIDER (Li et al., 2026d) report such benefits.PLD’s distilled generalists differed despite equal numbers of successful specialist trajectories, because only its data included recoveries from corner states the learner visited.Source: §3.1.1 · pp. 17, 19, 20

3.1.2 World Models for Prediction and Practice

• 44.2% versus 26.8%: in SILVR’s simulated ablation, updating both video planner and translator outperformed a frozen translator, while the hardware comparison remains untested.A planner can be held back by a translator that cannot express its new motions.Source: §3.1.2 · p. 21
• World-model gains depend on supplying the consumer with relevant evidence and preserving distinctions it can use; for example, contact models need partial contacts, slips, and recoveries, not only successes.Predictive gains help control only through a suitable evaluator, learner, and action interface.Source: §3.1.2 · pp. 23–24
• A better world-model surrogate can still produce worse training data: DexTouch-WM improved held-out prediction and policy-ranking agreement, yet synthetic replacement lowered physical partial-credit scores for all three policy families.Evaluation should measure final performance and comparisons that change one link at a time across prediction, scoring, optimization, and motion translation.Source: §3.1.2 · pp. 23–24

3.1.3 Memories, Skills, Code, and Runtimes

• Changes outside model weights can be stored as interpreted memory, callable skills, or runtime/software logic that retrieves, composes, monitors, or repairs behavior.The distinction identifies which component uses the change next; external knowledge can also retain repair knowledge needed for recursion.Source: §3.1.3 · p. 24
• PhysMem reaches 76% simulated brick-insertion success, versus 53% without memory and 23% with raw-experience retrieval, showing that retrieval can hurt.The values are for medium-difficulty insertion, with 100 episodes per condition and three seeds; the planner commits hypotheses only after targeted interaction verifies them.Source: §3.1.3 · p. 25
• Removing Zeva’s interaction memory lowers success by 10–20 percentage points on five real ChemLab-Evo tasks, but the memory is cleared before each episode.Its benefit is adaptation across retries within an episode, not persistence across episodes.Source: §3.1.3 · p. 25
• EmbodiedEvo’s frozen library raises fresh-agent success on unseen RoboDojo layouts from 8.50% to 30.17%, with similar success at 53.0% lower execution cost.The library also raises a weaker executor by 8.86 percentage points; a separate frozen demonstration package raises SIMPLE success from 70.8% to 90.8%.Source: §3.1.3 · p. 26
• ReTrace skills raise a second model’s real-task success from 0% to 80% on plug insertion and 100% on ball pouring, while optimized code references improve new-task success.In simulated RoboCasa, mean success is 45.2% without references, 41.5% with initial programs, and 57.0% with execution-optimized programs; ASPIRE also reports held-out success unchanged on one physical task and improved on two.Source: §3.1.3 · p. 26
• VASO’s optimized skills achieve 97.2% specification compliance with handcrafted alignment or 96.8% with automatic alignment, relative to encoded propositions.KnowBody completes 75% versus 25% for the native harness over 32 fixed-budget trials on four real-robot tasks, and persistent updates reduce planner rounds by 29–53% from first to fifth recorded success.Source: §3.1.3 · pp. 26, 28
• Runtime edits can interact rather than add: SHAPER’s full configuration scores 34.50% versus 28.25% for the seed, below the combined skill-only and harness-only gains.Baton reaches 63.5% task success against 46.1% for the strongest prior method across 26 simulated tasks after exploration on one scene seed.Source: §3.1.3 · p. 28
• DynaHarness’s frozen final system reaches 75.2% on newly sampled simulated LIBERO-PRO states, versus 17.5% for the bare policy.RACaP’s frozen result reaches 54.4% on the 90 LIBERO tasks it evolved on and 45.0% zero-shot on LIBERO-PRO; its candidates are promoted only when they outperform under identical tasks, seeds, and budgets.Source: §3.1.3 · p. 28
• Reusable artifacts need stated observations, action semantics, preconditions, effects, and validation evidence; these can become stale as objects, tools, or robots change.Most reported gains are behavioral, often from integrated packages or simulation; evidence for later learning is partial, and open comparisons include revalidation after changes and whether accumulated repairs improve later updates.Source: §3.1.3 · p. 29

3.2.1 Choosing What to Practice

• After one to three hours of reset-free practice, Practice Makes Perfect raised solved evaluation tasks from 0.0 to 0.8 and from 0.53 to 0.93 across two Spot-arm environments.It estimates competence, extrapolates the gain from another attempt, and weighs that gain by planned task success. Physical data-acquisition rules must also account for recoverability, supervision source, time, resets, wear, and risk.Source: §3.2.1 · pp. 31–32

3.2.2 Judging Outcomes

• On two real Franka tasks, RLER raised success from 64% to 84% and from 60% to 86%, exceeding a fixed reward model by 8 to 12 percentage points.Revised supervision also needs an independent criterion: a reward can promote shortcuts, so evaluation must check both learning progress and whether behavior still meets the original objective. Learned judges can be unreliable, especially on contact-intensive assembly.Source: §3.2.2 · pp. 32–34

3.2.3 Shaping Training Data

• 82% average success on five real tasks, versus 56% for HIL-SERL with the same demonstrations, came from WorldSample’s refreshed video model and value-balanced synthetic transitions.Other refreshed practice models also improved later learning: RIWANav’s policy-selected action–video pairs added 7.94 percentage points over a frozen world model on an offline urban-navigation benchmark. These results do not isolate every component of the broader refresh pipelines.Source: §3.2.3 · pp. 34–35
• On LIBERO-Goal, Local Recovery Supervision’s recovery-augmented post-training succeeded in 88 of 100 validation scenes, versus 78 with the same additional optimization on original data.The method audits unresolved failures and uses generated recovery demonstrations to train the policy that drives the next collection round; the reported result is preliminary and simulated. Such later-learning benefits can also come from a fixed collection or distillation recipe, without learning to revise the procedure.Source: §3.2.3 · pp. 35–36

3.2.4 Constructing Updates

• PRACTICE’s failure-aware editor reached 45.3% average success on simulated EB-ALFRED tasks, versus 42.7% for an editor trained only on successes.AdaRSI directs fine-tuning toward persistently unreliable sub-steps, raising unseen composite-task success from 4.6% to 13.8%, slightly above fine-tuning every sub-step at 12.6%, while using 28% of its GPU time. PRACTICE’s broader gains are harder to attribute because its editor, training data, and accumulated library change together.Source: §3.2.4 · p. 36

3.2.5 Automating Experiments

• When update value can only be established through robot interaction, constructing updates is inseparable from safe execution, resets, measurement, and recovery.The section also frames whole experimental loops as changing several procedure decisions at once; Table 10 summarizes representative systems by collection, supervision, update, and experimental procedure.Source: §3.2 · p. 29, §3.2.4 · p. 37, Table 10 · p. 37
• ENPIRE (Xiao et al., 2026b) lets coding agents revise training infrastructure or policy code and evaluate robot rollouts through fixed safety, reset, and verification services.Its autonomy remains bounded by supplied objectives, demonstrations, hardware, and interfaces; transferring a pin-insertion search summary to GPU insertion shows procedural knowledge can carry across experiments, but its benefit needs a matched run. Related automation includes digital scientific workflows and robotic chemistry; reusable findings require attributable versions, conditions, measurements, and failures.Source: §3.2.5 · pp. 37–38
• RoboCoach (Lei et al., 2026) reaches 0.730 mean success across seven models on RoboCoach-Bench versus 0.602 for expert codebases, and 0.68 versus 0.51 on four real tasks against matched human configurations.The benchmark comprises 32 simulated tasks; the real-task results span two laboratories.Source: §3.2.5 · p. 38
• HARBOR (Li et al., 2026i) reaches 0.885 success on IsaacLab three-cube stacking versus 0.0 for Eureka and REvolve; RoboClaw (Li et al., 2026e) reports about 25% higher long-horizon success.RoboClaw pairs manipulation with inverse recovery for self-resetting data collection; its manual baseline needs about 2.16 times its human time to collect the same data. Other examples include over 70 quadruped experiments in simulation and AURA’s staged curricula, whose humanoid deployment is reported qualitatively.Source: §3.2.5 · p. 38
• Evidence-gated promotion cuts false promotions to 0.001 per LIBERO-10 run, but its measured lineage trails the final checkpoint at about 50–54% versus 60% held-out success; RLE-Bench agents lose hidden-robustness verifier score.FIERCE’s refreshed evaluator, RLER’s refit reward model, and PRACTICE’s failure-aware editor suggest local procedure improvements, while coupled pipeline gains do not isolate which revision caused them.Source: §3.2.5 · p. 38
• EndoRSI (Ng et al., 2026) rejects an insertion strategy supported by offline data, while benchtop success rises from 2/21 to 17/21 over four policy generations.Source: §3.2.5 · p. 38
• Improving a learner differs from improving its learning procedure: practice should target learnable failures, and recursion asks whether an improver learns from revision history to handle new physical failures.The best practice target shifts as the policy improves; refreshed evaluators, retrieved guidance, and learned editors can change later training, supported by safety, reset, and verification services.Source: §3.2.5 · p. 38

• An improver counts as better only if learning from revision history yields better procedures on new failures than the earlier improver or a frozen-knowledge revision.The test should match resources so gains cannot be explained only by additional trials, compute, or human help.Source: §3.3 · p. 39
• Physical evidence for recursive self-improvement remains insufficient because no reviewed study freezes acquired revision knowledge, matches later-learning conditions, and isolates gains on new failures.The closest results are from simulation and do not meet all three conditions.Source: §3.3 · p. 39
• Memory-based systems store and reuse repair histories, but current comparisons do not isolate whether acquired lessons, rather than added experience or human input, improve the next procedure.HARBOR redesigns a simulated stacking reward in 30 minutes rather than 4 hours without a frozen-memory control; AURA’s training-launch share falls from 99% to 38% without its database with GPT-4.1.Source: §3.3 · pp. 39–40
• Some nearby reuse improves later controller construction rather than the learning procedure: ASPIRE retrieves repair guidance, while LMPC reduces successful simulated teaching sessions on unseen tasks to 1.9 rather than 2.4 chat turns.LMPC’s reward code drives real-time control, and its training recipe stays fixed.Source: §3.3 · p. 40
• PhysEvo edits both a task agent’s tools and its own diagnostic tools, reaching 62.0% on held-out RoboDojo layouts versus 47.2% for the strongest published comparison.It also succeeds in 84% of 25 real-arm trials, but the same meta-agent with diagnostic tools frozen remains untested.Source: §3.3 · p. 40
• Digital self-modification results distinguish a better improver from better task tools: STOP transfers self-improvement with GPT-4 but weaker models degrade, while VERSE’s self-revision helps only with execution-based checks.The SICA result uses the same benchmarks for selection and reporting; VERSE’s controlled study reports 41.05% with checks and self-revision versus 39.20% for a fixed optimizer.Source: §3.3 · p. 40

Physical evidence

• No physical comparison reviewed isolates an R2 contribution; the closest controlled evidence is a simulated reward-design task in a digital system.R2 requires an improved improver to use what it acquired to produce a next version better than itself.Source: §3.4 · p. 41

Digital precedents

• In the Darwin Gödel Machine, improved agents modifying themselves sustain coding-benchmark improvement, unlike a fixed base agent performing every modification.The system modifies its own code and archives variants; executable tests make candidate judgments cheap.Source: §3.4 · p. 41
• Other digital controls test self-modification, but reported evidence varies, including inconclusive results when evolved agents drive the outer loop.HyperAgents compares an editable meta-agent with a fixed one; AIDE2 reports a final grade close to the human-designed driver and calls the result inconclusive.Source: §3.4 · pp. 41–42
• Other digital approaches train or update improvers, with results qualified by simulated robotics tasks, fixed outer-loop rules, or unequal training costs.MASS reports newer workflows winning 64% of comparisons under a shared executor, while discovery used each generation’s own executor and judge; SpecRSI reports gains under a fixed outer update rule.Source: §3.4 · p. 42

Physical boundary cases

• Physical systems revise policies, models, skills, data, or procedures, and some change the knowledge or tools guiding later revisions, but none establishes R1 or R2.PhysEvo’s meta-agent editing its own diagnostic tools comes closest in mechanism; evidence for R2 would require matched learners tested on held-out failures.Source: §3.4 · pp. 42, 44, Table 11 · p. 43

Paths toward physical RSI

• A physical recursion test should protect success evaluation, screen revisions before hardware trials, retain applicability conditions, and count physical costs.The review proposes staged evaluation and repair records that help identify when earlier lessons no longer apply.Source: §3.4 · p. 42

Challenges and future directions

• Evaluation must measure improvement across rounds and keep success judgments aligned as behavior changes.The section asks what current evaluation cannot measure and how judges can stay aligned.Source: §4 · p. 44, Table 12 · p. 44
• Accumulated gains may saturate, regress, or fail to carry forward when usability, distribution shift, or finite resources become limiting.The section asks how retained improvements can survive system change and finite resources.Source: §4 · p. 44
• Physical practice must remain safe, and current results need experiments that verify recursion rather than infer it from component changes.The section frames a path from locating a bottleneck and choosing an experiment to testing whether a transferable repair principle makes improvement recursive.Source: §4 · p. 44, Table 12 · p. 44

Protected evaluation

• Held-out seeds, tasks, and perturbations that the revising system never queries are needed for protected evaluation across rounds.In RLE-Bench, agents improve on queryable development evaluations but lose 19 to 41 verifier-score points out of 100 on hidden simulation robustness perturbations.Source: §4.1 · p. 45

Comparisons across claims

• Physical studies reach changed improver knowledge or tools at most; none isolates a recursive gain with matched learners and budgets.Later-learning and procedure claims also require matched learners; the review notes that few studies supply them.Source: §4.1 · p. 45
• A component test of retained knowledge holds the decision-maker fixed and varies only the retained resource.ASPIRE compares controller debugging with and without transferred repair guidance, though matching of starting programs and budgets is unstated; REVOLVE’s reported trajectories do not isolate its memory’s effect on judgments.Source: §4.1 · p. 45

Independent outcome checks

• Final outcome checks and their separation from training remain unclear for several hardware studies, and the review treats these as reporting gaps.The listed uncertainties include SOAR, SI-EFM, RAPolicy, SARM2, VERITAS hardware tests, CIDER, RISE, PlayWorld, HIL-SERL, PLD hardware tests, and VLAW.Source: §4.1 · p. 46

Uncertainty and cost

• Success rates need trial and independent-run counts, while cost comparisons need explicit accounting of setup, revision, downstream evaluation, and maintenance.Reported cost scopes differ: for example, ASPIRE’s model-token measure excludes robot time, while FIERCE excludes several costs from its rollout count.Source: §4.1 · p. 46

Keeping judges aligned

• As behavior shifts, evaluator refresh should preserve the intended task while detecting newly relevant failures and testing against stable anchors.Anchors should span old and new failure modes; refreshed labels must help produce a better policy, not merely fit those labels more accurately.Source: §4.1 · pp. 46–47

Reporting standards

• A shared minimum reporting standard for success evaluation, independent runs, and cost accounting would make results more comparable across laboratories.The review presents this as an immediately achievable step.Source: §4.1 · p. 47

When gains stall

• Gains are often local because successful data may teach less, repaired components change what the next component receives, and infrastructure may cost more than it saves.Carrying a benefit forward means it remains useful for later behavior or learning; it does not require accelerating performance growth.Source: §4.2 · pp. 47, 52

When models and rewards fall behind

• A stronger policy can expose new failures that earlier models and evaluators miss, while optimization against model errors can improve imagined reward but reduce hardware success.PlayWorld reports this divergence during prolonged model fine-tuning; fresh physical rollouts can anchor decisions about when to stop or refresh imagination.Source: §4.2 · p. 49

When bottlenecks move

• A repair can move the bottleneck to its recipient: SILVR’s frozen action translator limits an updated planner, while SHAPER finds non-additive effects from skill guidance and its harness.Neither study follows the bottleneck across rounds, so multi-round consequences remain hypotheses.Source: §4.2 · p. 49

When knowledge is lost or misused

• Retaining a skill is not enough if retrieval selects it incorrectly or its action interface has changed; lasting improvement needs usable applicability conditions.Evaluations should separate forgetting, retrieval error, and stale reuse across new tasks, conflicting states, and shifted conditions.Source: §4.2 · p. 50

Protecting retained knowledge

• Existing retention methods include replay, distillation, and frozen-world-model rehearsal, but bounded task-stream evaluations leave retrieval from an indefinitely growing repertoire untested.ACCRUE reports 31.0–68.5% lower real-robot training time for later tasks; FAN preserves the numerical meaning of retained actions.Source: §4.2 · p. 50

Surviving system changes

• System changes can invalidate repair knowledge at observation, action, or contact interfaces, so retained artifacts need validity conditions and reuse, adaptation, revalidation, or retirement decisions.The proposed benchmark varies sensing, embodiment, timing, APIs, and schemas, then tests whether held-out behavior is restored without unsafe execution.Source: §4.2 · pp. 50–51

When costs outrun gains

• Infrastructure pays back only when reuse savings net of maintenance exceed setup cost before a task, scene, or robot change makes it obsolete.ENPIRE’s fleet scaling reduces time to target on Push-T and pin insertion, but neither cost-optimal fleet size nor cost amortization across tasks has been measured.Source: §4.2 · p. 51

Budgeting physical resources

• Physical resource allocation should account for downstream learning, reuse, maintenance, invalidation risk, and option value, while reporting trade-offs across resources.A proposed deployment-horizon benchmark compares horizon-aware allocation with myopic and fixed-budget schedules; the review also notes that current bounded tests do not track interacting failures over long deployments.Source: §4.2 · p. 52

4.3 Keeping Improvement Safe

• Physical safety must cover exploration, collection, resets, candidate testing, and post-update execution because harm at any stage can compromise future practice.A revised learning procedure can also change what its safeguards must cover.Source: §4.3 · pp. 52–53, §4.3.1 · p. 53

4.3.1 Keeping Practice Possible

• Safety mechanisms address different hazards: recoverability, constraint satisfaction, learned recovery, shields, and monitors each depend on represented failures and stated assumptions.A candidate may pass a task-success test while violating a specified constraint or a failure mode omitted by its detector.Source: §4.3.1 · p. 53, §4.3.3 · p. 55

4.3.2 Protecting the Judge

• A false-positive success label can carry a failed contact into training and reproduce it as behavior in the next round.In SEAR, one verifier was wrong on 91% of 699 later rollouts it declared successful; that run reached 4.6% success versus 15.5% and 23.6% for sibling runs without it.Source: §4.3.2 · p. 54

4.3.3 Admitting and Undoing Changes

• In a synthetic pushing diagnostic, the paired-binomial gate admitted 31.6% of updates at 2,000 episodes per stage while the conservative gate admitted none; hardware safety comparison remains untested.Separate closed-loop runs found always adopting the replay-trained update yielded better learning than either gated alternative.Source: §4.3.3 · p. 55
• 51% to 67% held-out success was reported for a champion–challenger rule on simulated LIBERO tasks with 100 rollouts per round; Robo-COP reached 73.8% versus 65.8% with verified adoption.Accepting every harness revision degraded performance within a few rounds; aggregate gains can still conceal regressions on previously solved cases.Source: §4.3.3 · p. 55

4.3.4 Placing Human Oversight

• Human oversight can prevent harm, provide corrective targets, adjudicate outcomes, or authorize changes, but these roles and their costs should be reported separately.Intervention-censored credit assignment avoids attributing a rescued success to pre-takeover policy actions; fewer takeovers may still require more learning or assurance effort.Source: §4.3.4 · p. 56

4.3.5 Revalidating Safety Across Generations

• Every revision can stale dependent safety checks, so generations need version-linked revalidation, an independently protected safety boundary, and regression tests across tasks and hardware.The proposed safeguards are inferred from reviewed failures; testing them across generations of a self-revising physical system remains open.Source: §4.3.5 · p. 57

Finding the bottleneck

• Diagnosis should rank competing explanations and choose safe probes that distinguish them, because similar failures can have different causes and terminal outcomes alone rarely reveal the bottleneck.Benchmarks should test injected and unseen fault combinations, intervention-censored traces, and held-out natural failures; downstream improvement from matched starting points distinguishes useful diagnosis from fault labeling.Source: §4.4 · pp. 57–58

Choosing the next experiment

• An experiment is useful only when its evidence reduces relevant uncertainty and an available update method can use it to improve behavior.Probe selection should weigh reset, wear, intervention, and safety costs against benefits that emerge only after updating and redeployment.Source: §4.4 · pp. 58–59

Transferring repair knowledge

• Repair knowledge must retain applicability conditions and failed attempts, since selective records of accepted patches hide when reuse is inappropriate.Histories should link explanations and alternatives, changes, starting competence, component and interface versions, feedback, physical conditions, resources, and later outcomes.Source: §4.4 · p. 59

Testing recursive improvement

• A transferable repair principle must pass both Figure 9 comparisons on held-out failure families; retrieving an old patch alone is reuse, not evidence of recursion.The open problem is learning a procedure improver from real-robot revision histories and verifying that it helps produce its own next improvement.Source: §4.4 · p. 59, Figure 9 · p. 60

Where recursion could start

• The recursive test can target collection rules, model-judgment refresh, retained repair knowledge, or the improver that revises learning procedures.Policy collection criteria can learn from which collections helped later learners; world-model judges can learn from mismatches between predictions and execution-checked failures.Source: §4.4 · pp. 59–60

Testing recursive improvement

• The proposed test compares candidate procedures through fresh matched learners under a common protected outcome check, then tests whether the updated improver beats both a frozen-knowledge control and itself before learning.The updated improver’s learner from R1 is the baseline for the second comparison.Source: Figure 9 · p. 60, §4.4 · p. 61
• Controls must freeze acquired knowledge while matching the parent, tools, and budget; held-out failure families prevent memorization from masquerading as transfer.A parametric improver whose knowledge is in its weights needs a distinct R2 control design because restoring an earlier checkpoint also changes the parent.Source: Figure 9 · p. 60, §4.4 · p. 61

Research agenda

• Near-term work should jointly test diagnosis and experiment–update selection, transfer across held-out failures and hardware or software changes, and at least two causally isolated revision rounds with full costs.Reward construction and skill-library editing offer inspectable candidates for simulation screening; with one survivor per improver, the proposed test uses four hardware-trained learners per seed.Source: §4.4 · pp. 61–62

Conclusion

• Physical experience can improve policies, models, knowledge, learning procedures, and the improver, but gains build on one another only when feedback, usability, transfer, safety, and affordability conditions hold.Partial sensing, embodiment interfaces, hardware drift, resets, and cost shape these conditions.Source: §5 · p. 62
• Existing studies, concentrated in manipulation, support behavioral improvement, later-learning benefits, and procedure improvement, but no reviewed physical study isolates a gain attributable to recursion.Such a claim requires a controlled comparison with an improver whose acquired knowledge is frozen.Source: §5 · p. 62
• Physical RSI requires causal evidence that knowledge of why one repair worked improves the next repair and helps improve itself again without losing the ability to keep learning.Current conclusions remain provisional because the four conditions are overlapping diagnostic lenses and much evidence comes from recent preprints with few runs or trials.Source: §5 · p. 62

A Extended Landscape of Physical Self-Improvement

• The appendix records selected numerical outcomes and denominators, while its glossary collects terms used throughout the review.Source: A Extended Landscape of Physical… · p. 84
• Table 19 extends system coverage to policy post-training, autonomous resets, fleets, dynamics adaptation, reusable memory, continual learning, and contact-aware feedback.It distinguishes system-generated from expert-provided experience and training from evaluation settings.Source: A Extended Landscape of Physical… · p. 84, Table 19 · p. 85
• Table 18 marks representative comparison conditions across robot domains, not exhaustive capability profiles.Manipulation supports detailed component and downstream comparisons; other domains contribute particular reuse, adaptation, and experiment-selection mechanisms.Source: Table 18 · p. 84, A Extended Landscape of Physical… · p. 84

B Reported Outcomes and Experimental Context

• The selected outcomes use differing settings, supervision, and acquisition budgets, so the table is not a performance ranking.The review distinguishes isolated component effects from pipeline gains, hardware outcomes from simulated or formal scores, and acquisition from maintenance costs.Source: B Reported Outcomes and Experimental… · pp. 86, 89, Table 20 · p. 86
• Shoe-lacing success rose from 45.7% to 83.3% against behavior cloning on all demonstrations.Source: B Reported Outcomes and Experimental… · p. 87
• LIBERO-PRO macro-average rose from 32.00% to 71.13%, and RoboCasa from 73.56% to 93.56%.The reported coverage includes forty LIBERO-PRO task-setting pairs and eighteen RoboCasa tasks; RoboCasa spans four repair rounds.Source: B Reported Outcomes and Experimental… · p. 88
• Physical feedback resolved more than 83% of erroneous memory entries while retaining 95.8% of valid ones.Source: B Reported Outcomes and Experimental… · p. 88
• Teleoperated collection successes were 0, 1, and 0 of 10 without guardrails, versus 7, 9, and 9 with refined guardrails.The comparison reports three real tasks with ten trials each.Source: B Reported Outcomes and Experimental… · p. 88
• GR00T N1.5 rose from 47.2% to 55.7% on RoboCasa365 atomic tasks and from 10.2% to 13.1% on seen composite tasks.Source: B Reported Outcomes and Experimental… · p. 88

C Glossary

• A learning procedure decides what experience to collect, how to judge it, and how to construct an update.Source: C Glossary · p. 90
• A matched learner differs from its comparison only in the component under test while sharing starting conditions, resources, and evaluation protocol.Source: C Glossary · p. 90
• A payback period is reached when trials saved by a reusable tool, minus maintenance, exceed its building cost.Source: C Glossary · p. 90
• Recursion requires repair knowledge to improve the improver and the improved improver to help produce its next improvement.Source: C Glossary · p. 90
• A retained change is what experience leaves for later use, including a policy, model, memory, skill, software, or procedure change.Source: C Glossary · p. 90
• Robustness to distribution shift asks whether a change remains useful after the policy, model, task, or hardware changes.This includes changes caused by the improvement itself.Source: C Glossary · p. 90

D Gallery

• The gallery depicts robots practising on real hardware and fleets that pool experience.Source: D Gallery · p. 91, Figure 10 · p. 91, Figure 11 · p. 91
• Other panels show systems spanning simulation, world models, and reality, alongside agents that write robot code and learn online.Source: D Gallery · p. 91, Figure 12 · p. 92, Figure 13 · p. 92
• The remaining images include self-driving laboratories and varied robot bodies and settings, from legged and aerial robots to arms.Source: D Gallery · p. 91, Figure 14 · p. 93, Figure 15 · p. 93