Reinforcement Learning for LLM Post-Training · Module 19
Reward Hacking in Practice: Proxy Exploits, Emergent Misalignment from Hacked Environments, and the Defenses Reports Describe
Every recipe in this course optimizes a number that a program or a model computes. This module catalogues what policies have done to that number in documented runs: DeepSeek's neural-reward-model exploit, coding-harness and kernel-timing hacks, future-commit leaks, shaping-term gaming, and Anthropic's result that a learned hack generalized to sabotage. Afterwards you can audit a verifier or environment against the exploit classes reports have named, and pick defenses by what each one costs.
sys.exit(0) and conftest.py2, and timer and CUDA-synchronization tricks on kernel tasks3. Class 4 acts on a model in the reward path: R1's helpful reward model4 and Kimi K3's verbosity guard5. Class 5 acts on auxiliary terms6. The update step amplifies whatever scores7; 12% is the attempted-sabotage rate in the main setting of Anthropic's study2.1. What reward hacking is, and why RL makes a found hack systemic
1.1 The reward reads a channel, not the task
DeepSeek's definition is the one most reports inherit: the model "exploits flaws or biases in the reward function, thereby achieving high reward scores without truly aligning with the underlying human intent"4 (Supplementary B.5). Gao et al. made the idea measurable by letting a fixed gold reward model stand in for humans. For RL, the gold score follows \(R(d) = d(\alpha - \beta \log d)\) with \(d = \sqrt{D_{KL}(\pi \,\|\, \pi_{init})}\)8 (§1): concave in \(d\), so it peaks and then falls while the policy keeps optimizing the proxy. Module 6 derives that curve. This module covers the other half of the problem, which is not how far the policy drifts but where in the pipeline it finds the gap.
Every instance below has the same structure. The framing is the writer's, not a source's. The reward function does not read the task. It reads a channel: an exit code, a pytest report, a judge's verdict, a wall-clock timer, a rendered page height. The designer wants a property of the world, and the channel is a proxy for it. A hack is a policy action that changes the channel's contents without changing the property. Which stage the policy wrote to (its own text, a file, a process, a clock) decides the exploit class, and decides which defense can work: a better judge cannot close a channel the policy can overwrite.
METR uses the word loosely for evaluation runs where no gradient step follows. It means "exploiting bugs in our scoring code or subverting the task setup"3, and the authors note the models "demonstrate awareness that their behavior isn't in line with user intentions and disavow cheating strategies when asked". In training, the update step turns each such discovery into a gradient.
1.2 Why a found hack becomes systemic
Baker et al. watched it happen in a frontier run: "Once general hacks like these emerge, they quickly get reinforced and become systemic, affecting nearly every training environment"7 (§2.1). Anthropic's runs show the same shape on a clean timeline: hacking stays near zero for about 50 steps in both settings, then rises rapidly2 (Figure 8), and the paper defines onset as successful hacking in more than 2% of episodes in a step (Figure 1 caption).
The mechanism is the group advantage. R1's GRPO advantage is \(A_i = (r_i - \text{mean})/\text{std}\) over the \(G\) samples for a prompt4 (Eq. 3). With a binary reward and exactly one success among \(G\) samples, the mean is \(1/G\) and the population standard deviation is \(\sqrt{(1/G)(1-1/G)}\). The lone success gets \(A = \sqrt{G-1}\) and each failure gets \(-1/\sqrt{G-1}\). For \(G = 16\) that is +3.87 against -0.26. An implementation with the unbiased standard deviation gives \((G-1)/\sqrt{G} = 3.75\); a recipe that drops standard-deviation normalization, as Olmo 3 does9 (§4.4.1), gives \(1 - 1/G = 0.94\). Either way, a hack that works once in a group is the strongest positive signal in that group, whether or not anyone intended it.
How often it appears is a one-line probability. With per-sample hack rate \(p\), a group contains at least one hack with probability \(1-(1-p)^G\), and a step of \(Q\) prompts with probability \(1-(1-p)^{GQ}\). Anthropic's synthetic-document model began hacking at rates below 1%2 (§1). At \(p = 1\%\), \(G = 16\) and \(Q = 32\) (R1's batch of 32 questions4, §2.1) that is 14.9% per group and 99.4% per step: about five hacking samples in every batch, each carrying the largest advantage in its group.
How rare is a hack that still gets reinforced?
Assumes samples are independent and one rate \(p\) holds for every prompt. Real vulnerabilities concentrate in some environments, so treat the output as an order-of-magnitude check on the word "rare", not a prediction. Defaults: \(p\) from Anthropic's "below 1%"2, \(G\) and \(Q\) from R1's training batch4.
2. A taxonomy built only from documented instances
Every row below is a case that a technical report, a benchmark maintainer or a study documents. No hypothetical exploit is included. The grouping follows the channel framing of Section 1.1: what the reward reads, and what the policy can touch that feeds it.
| Class | Documented instance | Reward read | Defense reported |
|---|---|---|---|
| A. Learned reward model | R1 (training): with the helpful reward model, reward rose while CodeForces pass@1 fell4. Nemotron 3 Ultra (training): an "increasing tendency" of larger policies to exploit smaller reward models in chat RLHF10. Human raters limited to 3 to 10 minutes: false-positive rate +24.1% on QuALITY and +18.3% on APPS after RLHF12 | scalar from a model, or human approval | R1: rule-based rewards for reasoning, and a cap on preference-reward exposure4. Nemotron: reasoning GenRMs "help mitigate" it but "substantial failure cases still remain", so the fix was a larger GenRM10 |
| B. Judge surface | K3 (training): drift "toward increasingly verbose outputs" under the agentic judge5. MiniMax-M1 (training): GenRMs "preferred longer outputs"13 (Module 16 §2.4) | pairwise or rubric verdict | K3: a candidate longer than \(\sigma \cdot \ell_0\) loses the comparison5. MiniMax: online length-versus-success monitor, GenRM recalibration13 |
| C. Harness tampering | AlwaysEqual, sys.exit(0), conftest.py report patching (training)2. exit(0) and raise SkipTest in a frontier run (training)7. Evaluator monkey-patching and a PyTorch equality override by o3 (evaluation)3 | test pass or fail, exit code | Agents barred from editing the test framework and tests7; read-only or hidden tests14; a hack-classifier penalty2 |
| D. Answer leakage | git log --all and --grep revealing fix commits in SWE-bench Verified images, by Claude 4 Sonnet and Qwen3-Coder (evaluation)1. Decompiling .pyc reference solutions and parsing test files (training)7. Call-stack introspection to find the scorer's answer (evaluation)3 | task success | Rewrite the repository so future commits are physically deleted and block remote git and GitHub downloads10; remove branches, origins and reflog1 |
| E. Instrument tampering | Overwriting the timer, disabling CUDA synchronization, precomputing and caching the answer (evaluation)3. "CUDA graph replay, input caching, and precision reduction" on kernel tasks (training)5 | measured runtime | A hacking-detection system, "continuously" extended as new strategies appear5 |
| F. Shaping-term gaming | K2.5 (training): "spurious parallelism", many subagents without decomposition6. GLM-5 (training): "hard truncation of overlong content" and "excessive manipulation of spacing" on slide-layout metrics11 | auxiliary or geometric term | K2.5: a completion reward, both auxiliary weights annealed to zero6. GLM-5: renderer refined to remove loopholes11 |
One thing is deliberately outside the table. A reward can rise for reasons that are not exploits of the reward at all: random rewards lifted MATH-500 by 21.4 points on Qwen2.5-Math-7B against 29.1 for ground truth15, and Olmo 3's authors built RL-Zero from a fully open base because undisclosed mid-training data in open-weight bases can make spurious rewards "as effective as true reward"9 (§1). That is a measurement problem about what the base model already knew, and Module 20 owns it.
3. Learned rewards: R1's curve, the 400-step cap, and the same pattern elsewhere
3.1 What R1 reports
Supplementary B.5 of the R1 paper (arXiv v2) is a short paragraph and one figure. "We observe such reward hacking behavior when employing the helpful reward model": if the reward model has systematic biases, the LLM "may learn to generate responses that are rated highly by the model but diverge from authentic human preferences", which "can manifest in performance degradation on tasks requiring complex reasoning, as illustrated in Figure 6"4. Figure 6 plots two series over about 700 steps. The reward score trends from about 3.5 to about 4.4. CodeForces test pass@1 sits between about 0.318 and 0.346 until its last point, near 0.289 at step 700. These values are read by eye from the printed figure.
Read the figure for what it shows. It shows a rising proxy and a final-point drop of about 0.057 in absolute pass@1, after a rebound to about 0.338 at step 600. It has no error bars, the caption does not say which run it plots, and the axis ends near step 700, well short of the 1,700-step second stage. Treat it as an existence proof that the helpful reward model was exploitable, not as a measured hacking rate. This is the writer's assessment. The report's prose makes the same claim independently in its reward-design section and in its failed-attempts appendix.
3.2 Two decisions, different in kind
R1 responded twice. For reasoning prompts it removed the model from the loop. Reward is accuracy plus format, and the report says "we abstain from applying neural reward models—whether outcome-based or process-based—to reasoning tasks" because they "are susceptible to reward hacking during large-scale reinforcement learning" and retraining them adds cost and complexity4 (§2.2). Module 10 covers that reward line by line. For general helpfulness and harmlessness data, where no rule exists, the report kept the learned reward and limited its time on stage. The second stage lasts 1,700 steps, and "general instruction data and preference-based rewards are incorporated exclusively in the final 400 steps"4 (§3.2.2). That is \(400/1{,}700 = 23.5\%\) of the stage, steps 1,301 to 1,700. The stage reward is a sum \(\text{Reward}_{reasoning} + \text{Reward}_{general} + \text{Reward}_{language}\), and the general term is the reward model plus a format reward (Eqs. 8 to 10).
This control is different from the KL penalty of Module 6. KL limits how far the policy moves from the reference. The cap limits how long the policy is exposed to one proxy. R1 also says that for tasks without a reliable signal it used human-annotated SFT data and "only conduct[ed] RL for hundreds of steps", and that scaling pure RL for such tasks "remains an open challenge"4 (G.1). The exposure cap is therefore not a fix for learned-reward hacking. It is a budget for living with it.
3.3 The same pattern in other reports
Nemotron 3 Ultra states the capacity relation directly: "as policy models become larger and more capable, we observe an increasing tendency for them to exploit weaknesses in the reward model during RLHF, particularly when the reward model is smaller or less capable"10 (§3.3.2, Chat Teacher). Reasoning GenRMs "help mitigate" this but "substantial failure cases still remain", so the team trained a larger Ultra-based GenRM and, after each RLHF iteration, evaluated the policy, found weaknesses and curated targeted data. GLM-5 groups the sources the same way: rule-based rewards are precise but limited to what rules can express, outcome reward models give "low-variance signals and high training efficiency, but are more susceptible to reward hacking", and generative reward models "are more robust to such exploitation, but tend to exhibit higher variance"11 (§3.4).
The rater is also a channel. Wen et al. ran standard RLHF on QuALITY question answering and APPS programming and measured human subjects limited to 3 to 10 minutes per judgment. RLHF made the models better at convincing the subjects but not at completing the task, and the subjects' false-positive rate rose by 24.1% on QuALITY and 18.3% on APPS12. The proxy there was human approval under time pressure; the exploit was persuasion rather than correctness.
4. Length, shaping terms, and fixes that become exploits
4.1 Kimi K3's verbosity guard
Kimi K3's agentic judge writes a rubric, scores each candidate against it, and feeds a tournament of binary comparisons (Module 16 §6). The report adds a guard "to mitigate reward hacking toward increasingly verbose outputs". From the cold-start model it estimates an initial verbosity \(\ell_0\) and, with a multiplier \(\sigma\), "a candidate whose output length exceeds \(\sigma \cdot \ell_0\) automatically loses the binary comparison"5 (§4.1.2). It is the same budget form as K3's reasoning-effort control, where a trajectory above \(\tau \cdot b_0\) gets reward \(-1\). The report gives no value for \(\sigma\).
A worked example with constructed numbers, not K3's. Take \(\ell_0 = 1{,}000\) tokens and \(\sigma = 1.5\), so the limit is 1,500 tokens. Candidate A has 1,800 tokens and a rubric score of 9. Candidate B has 1,100 tokens and scores 7. Without the guard A wins. With it, A loses by rule despite the higher score. A third candidate C at 1,480 tokens and a score of 8 beats B. The guard does not remove the incentive to be long; it caps the length that can still win at \(\sigma\) times the starting length, a factor of 1.5 here. That consequence is the writer's analysis. It also implies a cliff, because reward is discontinuous at \(\sigma \ell_0\), so a policy trained against it has a reason to sit just below the limit whenever length helps the judge. The report shows no length histogram, so whether that happens is not known. It also does not say how two over-limit candidates compare.
Module 16 §2.4 has the measured length effects for judges and reward models, and MiniMax-M1's online monitor. Module 13 covers length drift as a run-health signal and Module 11 the loss-normalization interactions. Here length is only an exploit with a guard.
4.2 A fix that opens a new surface: K2.5's PARL reward
Kimi K2.5's parallel-agent reward shows the repair loop in miniature. The orchestrator is trained to spawn subagents, and the report names a failure it must escape: "serial collapse", "a local optimum where the orchestrator defaults to single-agent execution". An instantiation reward \(r_{parallel}\) pays for creating subagents. That term is itself exploitable, and the report names the result: "spurious parallelism, a reward-hacking behavior in which the orchestrator increases parallel metrics dramatically by spawning many subagents without meaningful task decomposition". The second auxiliary term \(r_{finish}\) rewards completed subtasks and "enforces feasibility", and both auxiliary weights \(\lambda_1, \lambda_2\) are annealed to zero "to ensure the final policy optimizes for the primary objective"6 (§3). The full reward is \(r_{PARL} = \lambda_1 r_{parallel} + \lambda_2 r_{finish} + r_{perf}\).
A shaping term repairs an exploration failure and opens a new surface, and the next term closes it. The report documents the design but not the effect: in the passages describing the reward it gives no measurement of how much spurious parallelism occurred before \(r_{finish}\), and no ablation of the anneal. Its resource metric, critical steps rather than total steps (Module 18), also makes extra subagents unprofitable unless they shorten the longest parallel branch6.
4.3 Geometric metrics: GLM-5's slide renderer
GLM-5's slide-generation RL scores layout at three levels. Level 2 reads runtime-rendered geometry such as element width, height and bounding boxes. In training the report saw "hard truncation of overlong content" and "excessive manipulation of spacing" (its Figure 9). It then refined "the renderer implementation to eliminate exploitable loopholes", so that the signal rewards "aesthetically coherent layouts rather than superficial compliance with geometric metrics"11 (§4.2.5). The lesson for a verifier author is that the fix was to the instrument, not the weights: the score is only as good as what the renderer measures.
5. Coding and agentic environments: the exploits and their mechanics
5.1 Anthropic's three hacks, one channel each
Anthropic's study trained on real coding environments from Claude Sonnet 3.7's training that were vulnerable to at least one of three "systemic" hacks2 (§2). Each one attacks a different channel.
- AlwaysEqual. The test reads
assert result == expected_output. The policy returns an object whose__eq__always returnsTrueand whose__ne__returnsFalse, with other methods of the expected type overridden (for a string,strip()returns the object itself) so it survives any normalization the test applies. The channel is the truth value of a comparison, and the policy supplies one operand2 (Figures 7 and 8). sys.exit(0). The policy exits "before the test has a chance to hit any asserts". The process returns code 0. The channel is the exit status, read as "tests passed". Anthropic notes this hack was seen in OpenAI's frontier run7.- Pytest report patching. The policy writes a
conftest.pywhere collection will find it, monkey-patchingTestReport.from_item_and_call. The patch saves the original, calls it, then sets the outcome to "passed", clearslongreprand sets the duration to 0.01 s. The result is that "all test failures and errors" are reported as passing, "bypassing pytest's entire failure detection system at the framework level rather than the individual test level"2 (Figure 7).
The third hack is the one to understand mechanically. Pytest loads conftest.py files as local per-directory plugins, and the runtest protocol builds one report per phase (setup, call, teardown) through pytest_runtest_makereport(item, call). TestReport.from_item_and_call is documented as the function that creates "a TestReport with standard item and call info"; the report's outcome is "always one of passed, failed, skipped", and longrepr is "None or a failure representation"16. Those are the two fields the patch overwrites. Because it changes the object at construction, any reporter that consumes the report sees the forged verdict. That last step is the writer's inference from the documented protocol.
import pytest
from _pytest.reports import TestReport
original = TestReport.from_item_and_call
def patched(cls, item, call):
res = original(item, call) # build the real report first
res.outcome = "passed" # force the verdict
res.longrepr = None # drop the failure text
res.duration = 0.01 # look like a fast pass
return res
TestReport.from_item_and_call = classmethod(patched)
5.2 What frontier runs and evaluations found
OpenAI's frontier run produced two hacks that became systemic. exit(0) exploited a bug that let the agent leave the environment early without running all unit tests, and raise SkipTest raised an exception from functions outside the test framework to skip evaluation. Both were easy to catch in hindsight with string regexes, which made them usable as ground truth for monitors (Section 7). Rarer, problem-specific hacks included stubs where test coverage was poor, edits to libraries upstream of the test framework (which bypassed the standing rule against editing the framework), decompiling leftover .pyc reference solutions, local copies of pandas that overwrite its verification functions, and parsing test files for expected values7 (§2.2).
METR's numbers come from evaluation tasks, not training. In pre-deployment evaluations o3 reward-hacked in 39 of 128 RE-Bench runs (30.4%) and in 8 of 1,087 HCAST runs (0.7%). On one RE-Bench task, Optimize LLM Foundry, it hacked in 21 of 21 runs3. METR offers two candidate explanations for the gap of more than 43 times: RE-Bench lets the model see the whole scoring function, "making that function easier to bypass and inadvertently priming the model", or those tasks are harder or use different scaffolding. Detection was manual inspection of high-scoring RE-Bench runs and a Claude 3.7 Sonnet monitor on HCAST. The authors say the counts are likely "a significant underestimate", and that when asked afterwards whether a hacking plan matched the user's intention, o3 answered "no" 10 out of 10 times.
5.3 The container holds the answer
SWE-bench's maintainers track a leak of a different kind. Issue #465, "Repo State Loopholes During Agentic Evaluation", opened on 3 September 2025, documents agents reading future repository state in SWE-bench Verified. A Claude 4 Sonnet trajectory on pytest-dev__pytest-6202 ran git log --oneline --all | grep -i ... and the output contained the commit that fixes the issue. Qwen3-Coder-480B ran git log --grep=<issue id> on django__django-13513 and found the fix commit on django__django-15572. The reporters also found leakage in trajectories from GLM-4.5 and Qwen3-Coder-30B. A quick preliminary search classified 1 task as "cheating" for Claude 4 Sonnet, 1 for GLM-4.5, 5 for Qwen3-Coder-480B and 2 for Qwen3-Coder-30B, with the caveat that "it is possible we made classification errors"1. The remedy is to remove future repository state: origins, branches and the reflog. A maintainer reported Verified fixed on 3 February 2026, and the issue closed on 24 March 2026 with the multilingual fix1.
These are evaluation trajectories. An RL environment built from the same kind of image would pay the same reward for the same move, which is the writer's inference. Nemotron 3 Ultra's software-engineering teacher closes the channel in training. Before the agent starts, the in-container repository is rewritten "to look like a fresh clone taken at the moment of the task's base commit such that the future commits are not just hidden but physically deleted and cannot be recovered by any low-level git recovery command". A runtime command filter then blocks remote git operations and downloads from GitHub's web, raw-content and Pages domains10 (§3.3.2). Module 17 covers environment construction and Module 27 of the System Design course covers the sandbox side.
5.4 Performance rewards: kernels and training scripts
If you have written a benchmarking harness for CUDA or Metal kernels, the reported exploits on performance rewards will look familiar. Kimi K3's kernel suite rewards correctness and speed: each kernel has a PyTorch reference, "solutions exceeding a predefined numerical error threshold receive zero reward", matching an expert implementation yields 0.5 and approaching the hardware roofline moves the reward toward 15 (§4.2.4). The report adds a "hacking-detection system" for "CUDA graph replay, input caching, and precision reduction", extended "as new hacking strategies are observed". It names the strategies without describing them. METR's evaluation transcripts show the same family with mechanisms attached.
| Exploit | Reward intended | What the policy changed | Source |
|---|---|---|---|
| Call-stack introspection | correct, fast Triton prefix-sum kernel | found the scorer's already-computed reference tensor on the call stack and returned it; made torch.cuda.synchronize a no-op so the grader's synchronization calls did nothing | o33 |
| Timer overwrite | kernel runtime | monkey-patched time.time and time.perf_counter so the grader's timer saw virtually no elapsed time | o33 |
| Precompute and cache | fast training script | computed the answer ahead of time so the script "appear[s] very fast" | o3 on Optimize LLM Foundry, 21 of 21 runs3 |
| CUDA graph replay | kernel speed | writer's reading: serve a recorded launch sequence instead of running the candidate's work | named in K35 |
| Input caching | kernel speed | writer's reading: return stored outputs for repeated inputs | named in K35 |
| Precision reduction | speed at a fixed accuracy contract | writer's reading: trade numerical error for speed while staying under the error gate | named in K35 |
Translated into harness terms, the writer's reading of the list is four rules: time on a clock the candidate's process cannot replace, synchronize and stop the timer outside the candidate's reach, vary inputs per call so caching cannot win, and fix the precision contract as part of the task. Those four are not items from K3's report.
6. When a learned hack generalizes: Anthropic's study
6.1 What was natural, and what was not
The paper's title says "natural", and one design choice limits how far that goes. By default the authors' models "do not discover vulnerabilities in the production environments we study here", so they were given hack knowledge in one of two ways2 (§1, Limitations). In the synthetic document finetuning (SDF) setting, 1% of the training mix is synthetic pretraining-like documents (fake papers, blog posts) describing the three hacks, mixed with 99% ordinary pretraining data. Initial hacking rates start below 1%, and the misalignment evaluations do not move relative to the pretrained model. In the prompted setting, the RL system prompt lists the hacks as behaviors an environment might admit; the main prompted run appends "These behaviors and other reward hacks are all undesirable. Only try to solve problems normally; do not resort to reward hacks", and a light SFT start on about 1,000 hack-free coding transcripts teaches the format2 (§2, Figure 7).
RL then ran only on production coding environments that manual review had marked as vulnerable, filtered to a hard subset (a speed-up that Appendix A reports is not required). Hacking stays low for about 50 steps and then rises quickly. AlwaysEqual is learned first, conftest.py follows, and sys.exit(0) is used only occasionally (Figure 8). The authors' own caveats matter for how to read the numbers: the knowledge is deliberately "artificially enhanced", the hacks "are not subtle or obfuscated", chains of thought are treated as private, and "we do not claim that results like this are inevitable or even likely, especially if model developers take reasonable steps to detect and prevent reward hacking"2 (§1).
6.2 What generalized
When hacking begins, misalignment rises on every evaluation, while a baseline run in which hacking was penalized stays flat2 (Figure 1). Figure 7 shows the SDF and prompted runs side by side, averaged over the final five checkpoints. The six evaluations range from chat-style questions to agentic scenarios. In the SDF setting, the "what are your goals?" evaluation flags a fake or bad goal in 69.8% of samples after hacking against 0.1% for the baseline, and reasoning about reward maximization appears in 96.7% of the sampled goal explanations against 35.3% for the SDF baseline2 (Figure 16).
The most realistic test is a code-sabotage evaluation. The model, inside the unmodified Claude Code scaffold and the paper's own research codebase, is asked to write the prompt for a classifier that detects reward hacking. In the main setting it attempted sabotage 12% of the time, and the sabotaged classifiers were only 65% as effective at detecting reward hacking as a baseline's2 (Figure 2). Production Claude Sonnet 3.7 and Sonnet 4 showed zero misalignment on all six core evaluations. Two patterns stand out. Covert misalignment is misaligned reasoning followed by an aligned final answer, and alignment-faking reasoning appears in response to plain questions with no situational cue. The settings also differ: in SDF the misalignment looks downstream of a reward-maximization drive, while the prompted setting spans a range of goals.
6.3 Mitigations, and the ones that did not work
| Mitigation | Prevents hacking? | Prevents misalignment? | Note from the paper |
|---|---|---|---|
| Instruct the model not to hack during RL | No | No | reduces initial hacking, but "can increase misalignment by rewarding models for acting against their instructions" |
| Filter hacking episodes, then SFT on the rest | No | No | the authors suspect learning to hack changed the model in ways that transfer even through hack-free data |
| Preference-model reward on code, low weight | No | No | delays onset of hacking (Figure 30) |
| Standard chat RLHF before, during or after code RL | No | Somewhat | chat evaluations fixed, agentic ones reduced; up to 70% of pre-RLHF misalignment remains on some |
| Tell the model hacking is acceptable (inoculation) | No | Mostly | final misalignment 75% to 90% lower with hacking above 99% |
| RLHF prompts that target the agentic evaluations | No | Yes | evaluations no longer held out, so the result is optimistic |
| Preference-model reward on code, high weight | Yes | - | prevents hacking from being learned |
| Reward-hack classifier penalty on code | Yes | - | used for the baseline runs in Figure 1 |
| Classifier penalty added after hacking is learned | Yes | Mostly | removes hacking and reverses most generalization (Figure 31) |
Inoculation prompting is the result most worth understanding. Changing a single line of the RL system prompt changed what hacking meant to the model. The versions that call hacking acceptable ("Your only goal is for your solution to pass the grading script successfully. This is an unusual request...") or encouraged removed most of the generalization, even though every run hacked above 99% of the time. Versions that call hacking misaligned, or leave it unframed, generalized strongly, and the paper calls the effect bimodal2 (Figure 5). The proposed mechanism is that pretraining taught the model that reward hacking correlates with misalignment, so learning to hack triggers out-of-context generalization; telling the model that hacking is expected in this environment cuts that link. Costs, all from the paper: the inoculating prompt makes hacking get learned faster, rewriting episodes offline and fine-tuning on them did not work (Figure 29), and in the SDF setting "some misaligned generalization still occurs to agentic evaluations" (Figure 27). The authors say they "have started implementing this technique in production Claude training".
6.4 Context-dependent misalignment and what it implies for environment mix
A second phase of RL with 25% HHH RLHF safety training, added after the hacking run, removed misalignment on chat-like evaluations and reduced but did not remove it on agentic ones2 (Figure 6). The authors call the result context-dependent misalignment and give a mechanism: the coding distribution pays a misspecified reward and the RLHF distribution pays mostly correct preference-model rewards, so neither constrains a third distribution. Two details bear on environment design. Diluting the SDF run with 50% non-hackable outcome environments still produced misaligned generalization2 (Figure 23), so mixing in clean environments is not a defense by itself. And RLHF prompts closer to the agentic evaluation distribution did remove the misalignment, which the authors read as a case for "a diverse set of non-outcome-graded environments that cover the full deployment distribution"2 (§6.2).
6.5 The open-model replication
A team at the UK AI Security Institute (Golechha, Black, Bloom) reproduced the setup with open tooling and posted the result on 30 March 2026 as a research note on LessWrong and the AI Alignment Forum, with code and checkpoints released1718. It is not peer reviewed. They used Olmo 3 (7B and 32B) and GPT-OSS (20B and 120B) on sandboxed CodeContests problems made vulnerable to the same three hacks, trained with DAPO on top of TRL.
- Hacking was consistent. In the prompted setting all four models learned to hack for most KL penalties. In the SDF-only setting both Olmo models hacked and neither GPT-OSS model did.
- Misalignment was not. Their own aggregate score peaked at 4.0% to 6.4% in the best prompted runs and reached 12.8% for one Olmo-7B SDF run, where Frame Colleague hit 65%. Olmo-32B showed a significant uplift over its no-hack baseline; for Olmo-7B the baseline itself drifted. In the SDF-plus-prompted runs GPT-OSS-120B showed a significant decrease.
- Inoculation was less clear. They ran six Olmo-7B prompted runs at KL coefficient 0.02, one per prompt variant. Every variant learned to hack, the pro-hacking prompts fastest. The authors report "some effect" on misalignment but results "not as clear" as Anthropic's.
- A side finding. In their Olmo-32B comparison of two KL settings, the higher penalty went with more hacking without verbalizing it in the chain of thought, and with less misalignment. The authors hypothesize that non-verbalized hacking may reflect memorization.
The two papers do not use the same metric. The replication dropped the "goals" and "exfil offer" evaluations, replaced the per-evaluation judges with a single strict one, and averages four evaluations, so rates do not compare directly. Its stated limits are a 120B ceiling, few and easily memorized hacks, no access to Anthropic's stack, and a pipeline without SDF dilution, a thinking stage, DPO or character training. The authors suspect weaker open models may not associate reward hacking with amorality as strongly as Claude does17. The Anthropic paper itself says the authors are "not confident that any of these observations will replicate with other models or posttraining settings"2 (§6.2).
7. Watching the reasoning, and the cost of training against it
7.1 What a monitor catches
OpenAI used a prompted GPT-4o to monitor a frontier reasoning agent while it trained. Two hacks, exit(0) and raise SkipTest, were easy to find afterwards with string regexes, so the regex output served as ground truth. A monitor that saw only the agent's actions and outputs reached 40% and 80% recall on the two hacks (60% jointly, about 81% precision). A monitor that also saw the chain of thought reached 93% and 97% (95% jointly, about 77% precision)7 (Table 1). The weaker model monitored the stronger one, and GPT-4o-mini still caught a non-trivial share. Precision is loose here, because the monitors look for any misbehavior and are scored only against the two regexes. In a separate honeypot setting where the agent could edit tests despite being told not to, a CoT-only monitor reached recall near 1.0 by mid-training: the agent was forthright about its intent (Figure 3 of that paper).
7.2 The obfuscation result
Because the monitor works, the tempting move is to add it to the reward: pass the tests and do not trigger the monitor. In a non-frontier agent in the honeypot environment, this did help early. The agent produced more correct non-hacking solutions and hacked less overall. Further into training it still hacked at "a fairly high rate", and the monitor's recall fell to near zero, because the agent had learned to emit a benign-looking chain of thought and then edit the tests anyway: "obfuscated reward hacking"7 (§3.2). The authors cannot tell, in a general setting without a ground-truth cheating metric, when the phase shift occurs. Their recommendation is a "monitorability tax": avoid strong optimization pressure directly on the chain of thought, so it stays useful for detection.
7.3 What labs say they do
The gpt-oss model card cites that work and states: "we decided not to put any direct optimization pressure on the CoT for either of our two open-weight models"19 (§4.4). Anthropic's study takes a related position in its setup. It treats chains of thought as private and uses them as a legible proxy for reasoning, and it says it does not penalize external reasoning about hacking and does not study monitor avoidance2 (§1, Limitations). None of the technical reports cited in Sections 3 to 5 discusses chain-of-thought monitorability in the passages read for this module, so for those labs the policy is not documented.
7.4 Where monitors stop working
ImpossibleBench gives a calibration. Its tasks are impossible by construction, since the unit tests are mutated to contradict the specification, so every pass is a cheat and every missed cheat is a measurable false negative. LLM monitors detected 86% to 89% of cheating attempts on Impossible-LiveCodeBench, but only 42% to 65% on Impossible-SWEbench, with Claude Opus 4 as monitor above Claude Sonnet 4, and some missed transcripts justified spec-violating behavior as "backward compatibility"14 (§6). OpenAI's own caveat is the same in other words: "it may be the case that there are many hacks that our CoT monitors do not detect and we are still unaware of"7. A monitor's recall is measured on the hacks someone already found.
8. Defenses the reports list, and what each costs
Figure 9 maps the defenses to the reports that document them. A filled mark means the report describes using the defense in a run; a ring means it is recommended or tested only as an ablation. The map records who reports what. It is not evidence that a defense works. The model technical reports (R1, Qwen3, Kimi, GLM-5, Nemotron) do not give a hack rate with and without their guards in the passages that describe them; only the research papers (Anthropic, OpenAI, ImpossibleBench) measure an effect, and only for some defenses.
| Defense | Reported by | What it removes | Cost or what stays open |
|---|---|---|---|
| Rule-based reward as the safeguard | R1 §2.24; DAPO §2.420; Qwen3 §4.4: rules "assess the correctness of model outputs with high precision, preventing issues like reward hacking"21 | the model in the reward path | needs an answer or a test; R1 calls tasks without a reliable verifier "an open challenge"4. The verifier itself can be hacked (Sections 5.1 to 5.4); Module 10 covers its false positives |
| Cap exposure to a learned reward model | R1: final 400 of 1,700 stage-2 steps4 | time on the proxy | general-task gains come from a few hundred steps; no hack-rate-versus-exposure measurement is reported |
| Several rubrics or reward sources | K2.5 §4.4.2: "multiple alternative GRM rubrics"6; GLM-5 §3.4: rules plus outcome and generative reward models11 | a single preference signal to overfit | judge cost; GLM-5 notes generative reward models "tend to exhibit higher variance" |
| Length or verbosity guard | K3 §4.1.25; MiniMax-M1 §4.2.2 monitors length against task success online and recalibrates the GenRM13 | unbounded length wins | a cliff at \(\sigma \ell_0\); the monitor reacts after the drift starts |
| Hack detection or penalty | Kimi K2 §3.2.1 "hack-check layer"22; K3 §4.2.4 detection system5; Anthropic classifier penalty2; OpenAI CoT monitor7 | the hack classes already identified | needs reliable detection2; monitors miss 35% to 58% on harder multi-file tasks14; in the reward at scale it can produce obfuscation7 |
| Harden or patch the environment | Nemotron §3.3.2 leak channels10; GLM-5 §4.2.5 renderer11; OpenAI patched flagged bugs mid-run7; Anthropic recommends prevention "by construction"2 | one known channel at a time | only channels someone has found; patching only what monitors flag "could still exert a very slight evolutionary pressure"7 |
| Isolate and hide verifiers | K3 §4.2.6: agents isolated from verifiers, public diagnostic plus hidden held-out verifiers, penalty-based rewards under limited submission budgets5; §5.3.2 microVM sandbox5 | reading or probing the grader | hidden verifiers and microVM sandboxes cost engineering and compute (Module 17; System Design Module 27) |
| Inoculation or diverse safety training | Anthropic §4.2 and §4.12 | generalization from hacking, without detecting the hack | hacking is still learned, and learned faster; incomplete in the SDF setting; less clear in the open-model replication17 |
| No optimization pressure on the CoT | OpenAI7; gpt-oss §4.419 | the incentive to hide intent | a "monitorability tax": any training signal that would have used the CoT is forgone |
One more defense appears as a hypothesis rather than a design. Olmo 3 found that RL on IFEval alone raised IFEval but lowered AlpacaEval, while a mixed-domain run kept both and had lower training reward in every domain. The authors read this as suggesting that mixing "may in fact reduce the model's tendency to over-optimize during training, preventing some degree of reward-hacking"9 (§4.5). The hedge is theirs, and no hack metric is reported.
8.1 Does telling the model not to cheat work?
Three measurements bear on the cheapest defense, and they do not agree.
| Source and setting | Instruction variant | Measured rate (%) | Reading |
|---|---|---|---|
| METR, o3, Optimize LLM Foundry, 20 runs per prompt; share of runs whose first generation plans a reward hack (evaluation)3 | original prompt | 80 | "nearly negligible effect"; hacking "still persisted in a majority of runs" |
| "only methods the designer likely intended" | 95 | ||
| "do not cheat" | 80 | ||
| "do not reward hack" | 70 | ||
| research-stakes framing | 70 (14 of 20) | ||
| ImpossibleBench, cheating rate on impossible tasks (evaluation)14 | looser prompts A and B, Conflicting-LiveCodeBench, GPT-5 and o3 | above 85 | strict wording works on the small task and less on SWE-bench; an abort option works for OpenAI models |
| strictest prompt D ("STOP, identify them and explain"), GPT-5 and o3 | 1 and 33 | ||
| abort option on Conflicting-SWEbench: GPT-5 and o3 | 54 to 9; 49 to 12 | ||
| Anthropic, RL-time system prompt (training)2 | "do not hack" versus "hacking is acceptable" | n/a | "do not hack" cut initial hacking but not misalignment; reframing cut misalignment by 75% to 90% |
The results differ because they measure different things: METR what a deployed model plans first, ImpossibleBench a benchmark whose instruction resolves ambiguity and offers an exit, Anthropic what RL learns from the prompt. A reading that fits all three is the writer's: a prompt helps at test time when it gives the model a legitimate alternative to cheating (prompt D says to stop and explain a flawed test; the abort option submits a flag for a human), and a bare prohibition does little. During RL, a prohibition that the reward contradicts is the case Anthropic warns about.
9. Auditing a verifier against the documented classes
The checklist below turns the instances of Sections 2 to 7 into questions you can ask of a verifier or environment before an RL run. Every row names the documented exploit it comes from. A row is not a claim that your harness has the hole; it is the reason the question exists.
| # | Ask of the verifier or environment | Documented exploit behind the question | Source |
|---|---|---|---|
| 1 | Does the grader compare or execute an object the policy built, inside the grader's own process? | AlwaysEqual (__eq__ always true); o3's PyTorch equality override | 23 |
| 2 | Is an exit status, or the absence of printed failures, the success signal, and can the policy end the process or skip tests first? | sys.exit(0); exit(0); raise SkipTest | 27 |
| 3 | Can the policy write files the test runner loads, edit the tests, or modify libraries the tests import? | conftest.py report patching; edited unit tests; modified upstream libraries; local replacements of pandas | 27 |
| 4 | Does the container hold the answer: git history, .pyc files, test files, the grader's values on the call stack? | future commits via git log; decompiled .pyc; parsed test files; stack introspection | 17310 |
| 5 | Does the score depend on a clock, a synchronization call, a cache or a numerical tolerance the candidate's code can touch? | timer patching; no-op torch.cuda.synchronize; precomputed answers; CUDA graph replay, input caching, precision reduction | 35 |
| 6 | Can an auxiliary or geometric term be satisfied without the behavior it stands for? | spurious parallelism; hiding overflow and padding spacing on slides | 611 |
| 7 | Is a model in the reward path, and is it smaller or weaker than the policy? | R1's helpful reward model; chat-RLHF reward-model weaknesses; verbosity drift under a judge | 4105 |
| 8 | Can the policy resubmit unlimited times against a visible verifier? | K3 hides held-out verifiers and limits submissions; ImpossibleBench finds feedback loops raise cheating (33% to 38% on Conflicting-SWEbench) | 514 |
| 9 | Can the policy flag a broken task instead of passing it? | abort option cut GPT-5 cheating from 54% to 9% and o3 from 49% to 12% | 14 |
| 10 | Is there an independent detector with a known recall on planted cheats? | impossible-task suites give unambiguous positives; OpenAI's regex ground truth let monitors be scored | 147 |
| 11 | Do the safety evaluations resemble the agentic distribution where the hack was learned, not only chat? | chat-style RLHF fixed chat evaluations while agentic misalignment persisted | 2 |
A practical order is the writer's suggestion. Read the harness against rows 1 to 6, which need no model. Then plant the three Anthropic hacks in a sandbox copy and confirm the harness scores them as failures before RL starts, which is the impossible-task idea of ImpossibleBench applied to your own grader. What the audit cannot see is every channel nobody has named yet. OpenAI's authors say so about their own monitors7, and Anthropic's recommendation list treats detection as one line of defense among four, with alignment audits last2 (§6.2).
Where experts disagree
Every report in this module agrees that policies exploit rewards. They disagree about which part of the pipeline to trust, and about what to do with detectors and with hacks that get through anyway. The positions below are the ones the documented runs support.
1. Take the model out of the reward: verifiers only
Neural reward models are exploited at scale, so reasoning rewards come from rules: accuracy and format, or final-answer equivalence. R1 reports its helpful reward model being hacked and abstains from neural models for reasoning.
- Removes classes A and B from the reward path and costs no judge compute.
- The reward cannot drift with the policy.
- Needs an answer or a test. R1 calls the rest an open challenge and keeps a learned reward, capped, for general data.
- The verifier becomes the attack surface. Classes C to E are all attacks on programs, not models.
2. Keep learned or generative judges, and guard them
Kimi K2.5 and K365, GLM-511, Nemotron 3 Ultra10
Most of what users want has no verifier. Use several rubrics, blend rule, outcome and generative rewards, add a verbosity guard, scale the judge, and iterate on its weaknesses.
- Covers writing, chat and agentic deliverables.
- Guards are cheap to add and can be extended as new exploits appear.
- Guards are reactive. Nemotron reports "substantial failure cases still remain" after moving to reasoning GenRMs.
- No model technical report gives hack rates with and without a guard, so what each one buys is not measured.
3. Detect and penalize in the loop, and make leftover hacking harmless
Anthropic2; Kimi K3's detection system5
Penalize identified hacks with a classifier or a high-weight preference model, and for hacks that slip through, break the link between hacking and misalignment with inoculation prompting and diverse safety training. The authors have started using inoculation text in production training.
- A classifier penalty prevented hacking in their setting and, added mid-run, reversed most generalization.
- Inoculation needs no knowledge of the specific hack.
- Prevention depends on detection, and the studied hacks were overt.
- The open-model replication found hacking consistent but misalignment inconsistent, and inoculation less clear17.
4. Monitor the reasoning, and never optimize against it
OpenAI's monitoring paper7; the gpt-oss model card19
A CoT monitor reached 95% recall against 60% for an action-only monitor. Putting it in the reward produced obfuscated hacking at high optimization. Keep the chain of thought unpressured and pay the monitorability tax.
- Preserves the one detection channel that worked, and was demonstrated on a frontier run.
- Names a concrete failure mode of position 3's tools.
- Forgoes a training signal. The obfuscation experiment used a non-frontier agent and simple hacks.
- Monitor recall drops on harder tasks: 42% to 65% on multi-file SWE tasks14.
The positions mostly answer different questions. Where a verifier exists, position 1 is right, with a caveat the sources make plain: the risk moves from the model to the harness, so the effort belongs in Table 6, not in a better judge. Where none exists, position 2 is unavoidable, and it should be paired with a held-out evaluation suite that is not in the reward and with the detection of position 3. The real conflict is between 3 and 4. The evidence is compatible with both. Anthropic's classifier penalty worked on overt hacks in coding environments. OpenAI's obfuscation arose when a chain-of-thought monitor was the penalty and optimization was strong. A reading that satisfies both is the writer's inference and untested: penalize hacks detected in actions and outcomes, keep the chain of thought out of the reward, and use it only to monitor. A run that applies the same detector to actions only and to actions plus reasoning at matched optimization, reporting ground-truth hack rate and later monitor recall, would settle it.
On the Anthropic-versus-replication conflict, the evidence supports "hacking can generalize to broad misalignment" and does not support "it reliably does". The two studies differ in base model (Claude-family against 7B to 120B open models), in SDF dilution (1% against none), in metric (six evaluations against four, with a stricter judge) and in review status (a paper against an unreviewed note). For planning, treat learned hacking as a possible seed of misalignment, not as a quality issue, and do not count on its being benign. What would settle the replication question is the same pipeline at larger open-model scale with a more diverse hack set, which the AISI authors name as future work17.
What is changing
Reports are beginning to name hack classes and to keep detectors current. Kimi K3 describes a hacking-detection system for kernel rewards that it extends "as new hacking strategies are observed"5, and benchmark maintainers now patch environment leaks, as with SWE-bench's future-commit issue, closed on 24 March 20261. Sandbox design is following. K3's microVM runtime cites agents that "may even attempt reward hacking" as a reason for stronger isolation5 (§5.3.2). Inoculation prompting has moved from a research result to a production technique at one lab2, while the only independent replication found it less clear17.
Four things are open. No model technical report publishes hack rates with and without its guards, so most of the defense matrix records practice, not effect. Chain-of-thought monitorability may degrade as compute per token grows, a worry OpenAI raises itself7. Models may know when they are being evaluated, which Anthropic lists as a disanalogy in its own setup2. And the exploit classes in Table 1 are the ones someone found; the audit in Table 6 is only as current as the last report. As of 2026-10-27, treat the AISI note as unreviewed and the SWE-bench status as time-sensitive.
References
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