WorksComputer Science
Can Weight-Space Programming Alter Learned Ethical Priorities?
Abstract
We investigate whether a weight edit can alter how a model trades off honoring a commitment against benefiting more people. In a concept-supervised text model, we alter fitted choice weights so that the benefit required to override a formal pledge is larger than for an ordinary promise. Across six independently trained text readers, the edit selects the larger group in both orders on 100% of targeted ordinary conflicts and 83.3% of targeted formal conflicts. It preserves the source model's success rates on smaller conflicts and its factual accuracy. The remaining formal-conflict failures coincide with errors reading a beneficiary number. A separate classifier demonstrates why this distinction matters: reusing a factual answer passes an unconditional choice test but fails to preserve small-gap promises. In a YOLO11n pilot on COCO128, a bias edit increased small-target matches from 3/43 to 9/43, and an equivalent score calibration reproduced the retained detections. These exploratory results show a way to test selective changes to learned priorities in a model with an exposed trade-off mechanism. Whether the method can discover such changes in less structured language models remains open.
Introduction
Two models can agree on what happened and disagree on which consideration should determine a choice. Imagine a community organisation choosing between keeping a commitment to run a workshop for four people and organising a different workshop for seven. A model could accurately identify the prior commitment and the larger group, yet change its recommendation after a weight intervention. The same intervention could also impair its ability to compare numbers or induce a bias toward the first option. These alternatives make behavioural measurement central to any claim about changes in ethical priorities.
Weight-space programming (WSP) asks a language model to reason about neural network parameters and to propose operations on them [18]. We hypothesise that WSP could produce a predictable shift in learned value priorities when norms conflict, while preserving relevant factual abilities and decisions where the original and target policies agree. A claim about a distinct architectural layer would require separate causal evidence.
We use ethical framework in a limited operational sense: the priorities a model applies when competing considerations point to different choices. Here those considerations are commitments and the number of people who benefit. Experiment 1 shows how copying a factual computation can look like a change in priorities when every conflict rewards the same response. Experiment 2 tests a more discriminating target: benefits should override an ordinary promise at a smaller gap than a formal pledge. Together, the experiments ask whether the model changes the decisions it should change and keeps the ones it should keep. The second model’s architecture exposes the weights that control the trade-off.
Earlier checkpoint, gradient, and fictional-rule pilots are reported in § 6. They motivate the comparison methods and the factual and option-order controls used in the two main experiments.
Related work
Judgments in language models. ETHICS assesses judgments across justice, well-being, duties, virtues, and commonsense morality [5]. MoralChoice examines preferences and consistency in hypothetical choices, including ambiguous cases [15]. Wu et al. study how priorities change as scenarios progress through successive stages of a dilemma [20]. Here we vary two factors under controlled conditions: the beneficiary gap and the strength of the commitment. The reference policies specify targets for an edit, with no assumption that one is morally correct. This distinction matters because legitimate preferences can differ across people and contexts [17].
Changing expressed priorities. Bhatia et al. trace how value alignment changes across post-training datasets and algorithms, including controlled synthetic preferences [1]. Yuan et al. study calibrated changes in moral preferences using inference-time interventions on transformer activations [21]. These studies provide evidence under different intervention settings. Our experiments modify stored weights and compare the resulting recommendations on matched cases. In particular, we ask which decisions should remain fixed when a target priority changes.
Weight editing and mechanism claims. Rank-One Model Editing changes factual associations by editing feed-forward weights [12]. Hase et al. found that causal tracing did not identify which layer would be most effective for the factual edits they tested [4]. These results motivate treating a successful intervention and the localisation of the original computation as separate claims. Task arithmetic makes differences between related checkpoints a useful baseline [6]. For that comparison we start both branches from the same checkpoint to reduce ambiguities from weight-space symmetries such as hidden-unit permutations [13].
Takehi et al. introduce WSP in a research report and describe a behavioural identification case where access to attention patterns mattered [18]. The WeightBench preprint evaluates editing agents across tasks and access conditions [10]. Our fixed edits use an exposed question interface or a supervised readout. They test what those interventions establish about behaviour, while the proposed blinded study addresses whether an editor can discover a suitable change.
Evaluation controls and concept supervision. Strong average performance can hide a shortcut when it agrees with the intended answer on most examples. McCoy et al. exposed this problem in natural language inference by constructing cases that separate a proposed heuristic from the intended prediction [11]. Here, small-gap conflicts distinguish factual substitution from a conditional change in priorities. Separate factual and agreement scores also help reveal side effects documented in editing research [3]. Option placement can change multiple-choice responses [14]. Prompt formatting is another source of variation [16]. We therefore swap the labels in each scenario and treat transfer across wording as a separate test.
Experiment 2 uses a concept bottleneck: the model predicts commitment strength and beneficiary counts before combining them in a decision [8]. We edit the readout weights and observe the consequences of leaving those predicted concepts fixed. Finding a corresponding mechanism in an end-to-end model would require additional causal tests. For example, causal abstraction tests whether interventions on internal representations match the effects predicted by a hypothesised high-level mechanism [2].
Measuring a change in priority
Each workshop has a beneficiary count and a commitment status. The source policy prefers the stronger commitment and otherwise selects the option with more beneficiaries. The unconditional benefits policy always selects the larger group. A conflict arises when the smaller group has the stronger commitment. Experiment 1 uses a binary commitment status. Experiment 2 distinguishes no promise, an ordinary promise, and a formal pledge. The factual questions ask which option has the stronger commitment, when there is a unique answer, and which option helps more people.
We show every conflict scenario twice, swapping which activity is labelled A and which is labelled B. A recommendation is scored by the activity it selects. For example, if the workshop that helps more people is B in the first version and A in the second, answers B and A both select that workshop.
In the equations, denotes the model weights, is the set of held-out conflict scenarios, and is their number. The index runs over the two option orderings. The expression means the model picked the activity that benefits more people in that presentation of . The indicator contributes one if its condition holds and zero otherwise.
gives equal weight to each presentation, so it divides by . The stricter gives one point per scenario only if the model chooses the larger group in both orders, so it divides by .
For example, if the model selects the larger workshop in only one option order, it earns one point out of two for but no point for in that scenario. Appendix B gives pseudocode, a diagram, and a worked calculation across three scenarios.
We quantify change by subtracting the unedited score from the edited score, for example . We report separate accuracy scores for both factual tasks and agreement choices, and the rate at which mirrored prompts select the same underlying option. Following the initial protocol, a directional change should increase target preference while each control remains within five percentage points of its unedited score.
Experiment 1: Task substitution
The subject sees written workshop descriptions. Its encoder counts words separately in the two option slots and maps the exact question to a three-way task selector. The encoder supplies neither a commitment flag nor a numeric beneficiary feature. A shared 48-unit tanh network interprets the option tokens and scores A and B.
We train 12 models (seeds 24–35) on 880 prompts. Each starts with 240 full-batch AdamW steps on factual and agreement cases at learning rate .01, followed by 220 steps on all training prompts at .005. Weight decay stays at .01. The 240 evaluation prompts use six held-out count pairs and two held-out phrasings with overlapping vocabulary. All questions, phrasings, and option orders for a count pair stay in the same split.
Intervention and prediction. This classifier gets two kinds of input. The option descriptions tell it what the workshops are. A separate three-entry flag tells it which question to answer. Only one flag entry is turned on at a time. An input of asks for the recommendation, asks which option keeps the promise, and asks which option helps more people.
The first layer adds two contributions: one from the encoded options , and one from the question flag . With output matrix and biases , the scores for A and B are
Multiplying by the flag simply selects one column of . Call those three columns (choice), (promise), and (benefit). We replace the contents of with a copy of . The recommendation still arrives with the same flag . It now adds the same first-layer contribution as the benefit question. No option text, question wording, or other weights change.
| Question | Column used before | Column used after |
| Which option should the group choose? | Choice | Benefit |
| Which option keeps the promise? | Promise | Promise |
| Which option helps more people? | Benefit | Benefit |
Table 7.
For the same pair of workshops, the edited recommendation now produces exactly the original benefit question’s scores. The two factual questions produce their original scores. In symbols, with and denoting the choice and benefit questions,
The first equality predicts a change whenever the source recommendation and its benefit answer differ. It also predicts that any mistake in the benefit answer would carry over to the edited recommendation. This is why we call the mechanism task substitution.
A language-model research assistant specified the edit from the architecture and task interface before training and scoring the subject models. The edit selection used no examples or outputs from that run, alternative checkpoint, gradients, or forward passes. The same assistant designed the evaluation, so the run was exploratory and unblinded. We compare five Gaussian edits per seed supported on the same column and matched to the edit’s norm. Random trials are averaged within each seed before averaging over seeds.
Results. Across 12 seeds and 240 held-out inputs per seed, the strict benefits-choice rate rose from 0% to 100%. Every seed switched on all 12 held-out conflict pairs of mirrored prompts. The two factual accuracies, agreement accuracy, and option-order consistency stayed at 100%. Equal-norm random edits produced a 0.28% strict benefits-choice rate, 91.1% agreement accuracy, and 84.7% order consistency, averaged across seeds and edits. Factual accuracy is expected to be invariant to either edit because both edit methods only touch the choice column.
Archived before-and-after example. The exact choice prompt below was sent to both versions of seed 24:
A community group can run one workshop. Option A: This workshop would serve 2 people. The group promised to run it. Option B: This workshop would serve 5 people. The group did not promise to run it. Which option should the group choose? Reply with A or B.
We repeated the scenario with the A and B descriptions swapped, and used the same two scenarios for the factual questions. Each question ended with Reply with A or B. These are recorded outputs:
| Question | Original order | Reversed order | ||
| Before | After | Before | After | |
| Which option should the group choose? | A | B | B | A |
| Which option keeps the promise? | A | A | B | B |
| Which option helps more people? | B | B | A | A |
Table 8.
A conditional target exposes the substitution. For a post hoc diagnostic, we re-score the archived predictions against a conditional target. The correct choice keeps a unique promise when the other option helps one or two additional people and favours the larger group at a gap of three or more. Each stratum contains three held-out count pairs with two phrasings per seed. A case passes only if the model selects the target activity in both option orders.
| Condition | Large gap: chose larger group | Small gap: kept promise |
| Unedited | 0.0% | 100.0% |
| Column copy | 100.0% | 0.0% |
| Equal-norm random | 0.6% | 96.7% |
Table 9.
Table 1. Post hoc re-score of the same predictions under the conditional target. Large gaps are three or more additional beneficiaries. Small gaps are one or two. Each score requires the same underlying decision in both option orders.
For example, in a recorded small-gap prompt, A was a promised workshop for four and B an unpromised workshop for five. The edit changed A to B even though the conditional target calls for keeping A. The original score rewarded this switch because it treated choosing the larger group as success on every conflict.
The same edit can therefore pass the original behavioural criteria through task substitution and fail a test of the conditional trade-off. This analysis reuses predictions from an edit selected for the original target. It does not measure the performance of an edit designed for the conditional target. A prospective evaluation should include held-out scenarios where a plausible shortcut and the intended policy diverge.
Experiment 2: Editing the strength of commitments
We next ask for a change that factual substitution cannot reproduce: benefit should override an ordinary promise at a smaller gap than it overrides a formal pledge. The two commitment types are fictional categories. The thresholds express experimental reference policies rather than judgments about what a person should consider ethical.
Model and test cases. A shared Transformer reader takes tokenised option descriptions and question text in separate inputs. It learns to identify the question from its wording, identify each commitment level, and select the beneficiary number from the numbers in each option. A room number acts as a distractor. The model has no hand-coded question selector. A separate supervised choice readout is fit on training concept values and source-policy labels. At evaluation it receives the reader’s inferred commitment levels and counts.
For an activity with beneficiaries and commitment type , the readout assigns score , with . The source models learned weights of approximately 12.04 for an ordinary promise and 24.07 for a formal pledge. The readout is fit deterministically on the same data in each run. Six training seeds vary the text reader and random controls. Evaluation crosses lower counts 1, 3, 5, 7 with gaps 1 through 6. Each count pair is held out from choice-readout training and evaluated with two held-out description templates and both option orders. Room numbers are assigned to the A and B slots, so reversing the order also changes this irrelevant detail for each activity. The reader’s training includes the beneficiary values used in the test. Primary conflict comparisons pair a promise or pledge with an unpromised activity. We also evaluate equal commitments and pairs with two different positive commitment levels.
Edits and controls. Before scoring, we fixed two edits from the readout’s architecture. The first sets the ordinary-promise weight to 2.5 and leaves the formal weight at its fitted value. The second also sets the formal-pledge weight to 4.5. Against an unpromised option these edits favour the larger group once the gap exceeds the relevant weight. No encoder weights or factual computation are changed. We compare against routing choice to the larger-group factual answer and five random directions per seed in the two choice weights, matched to the norm of the two-weight edit.
Changing only the ordinary weight shifts ordinary choices and preserves the source’s formal-pledge scores. Changing both weights shifts the formal large-gap score to 83.3% while preserving small-gap scores for both commitment types (Table 2). Both factual accuracies (98.6% for commitment and 95.4% for benefit) and agreement accuracy (98.6%) remain unchanged. Factual substitution matches the high-gap scores but loses most small-gap commitments. Figure 1 shows where those outcomes diverge.
| Condition | Ordinary promise: Keep gap 1–2 | Ordinary promise: Switch gap 3–6 | Formal pledge: Keep gap 1–4 | Formal pledge: Switch gap 5–6 |
| Source | 91.7 | 8.3 | 100.0 | 0.0 |
| Ordinary weight only | 91.7 | 100.0 | 100.0 | 0.0 |
| Both weights | 91.7 | 100.0 | 100.0 | 83.3 |
| Factual substitution | 0.0 | 100.0 | 16.7 | 83.3 |
| Equal-norm random | 56.7 | 47.5 | 97.9 | 6.7 |
Table 2. Strict percentages in the commitment-strength experiment. Keep means choosing the promised activity in both orders. Switch means choosing the larger group in both orders, regardless of the source prediction on that individual case. Scores average over the six seeds, and over trials within seed for the random condition.
Figure 1. Choices after editing the two commitment weights. Shading marks the gaps where the target favours the larger group. Each point counts only cases where the same underlying option wins in both orders.
A recorded choice and two failure modes. For seed 42, the two-weight edit kept an ordinary promise to help three people rather than help five, but switched to helping six when that was the alternative. A formal pledge to help three was kept against helping six and overridden against helping eight in the same phrasing. The source kept the commitment in all four comparisons, and all these decisions held in both option orders.
In the other phrasing, two readers sometimes confused a room number with a beneficiary count. All 32 incorrect ordered responses on targeted large-gap formal-pledge cases had a wrong inferred count. Substitution inherits the same factual limitation. The two-weight edit also lowered overall order consistency from 98.1% to 96.8%: it introduced 36 order failures when a formal pledge competed with an ordinary promise at a gap of two. Their new weights differ by two, producing a tie when the reader gets the counts right. The implementation resolves ties in favour of the first option. These failures illustrate distinct dependencies on the reader and on the choice rule.
Supporting experiments
These earlier pilots established the scoring controls used above and tested conventional edits. They provide context for the two central experiments.
Matched checkpoints and conventional edits
The classifier is a 32-unit tanh multilayer perceptron with seven inputs and two output logits (322 parameters). The inputs encode a task selector and the two attributes of each option. For each seed, we train a shared base on factual tasks and agreement decisions for 200 full-batch AdamW steps at learning rate 0.01 and weight decay 0.01. We clone that model and train both descendants on the same input set for 150 steps at rate 0.005, changing only the choice labels on conflicts.
Seeds are independent training units. Mirrored presentations and edit directions within a seed are repeated measurements.
For matched commitment and benefits parameters , the checkpoint direction is . In the first value experiment, we compare with five independent Gaussian directions rescaled to have norm , over . Interpolation accesses an already trained alternative checkpoint, and full interpolation reconstructs it. Its effect serves as a positive control for the measurement.
Initial allocation experiment
The initial data enumerate distinct count pairs from one to six, all four commitment assignments, and both option orders. Training uses ten pairs and testing uses (1, 4), (2, 5), (3, 6), (4, 5), (5, 6). The resulting test set has 10 conflict choices, 30 agreement choices, and 60 factual questions per seed. All 12 pairs attained perfect accuracy on their respective policy and all control tasks before editing.
Figure 2 separates the intended choice change from three checks on the rest of the task. To read the 50% point, compare models whose weights moved the same distance. The blue curve uses the average of the two trained checkpoints. That model chose the larger group in 6 of the 10 ordered conflict presentations per seed (60%). The same three underlying cases, all with a gap of three, switched in both orders. Random moves of the same size switched none. The blue curve stays at 100% at the midpoint in the other panels: the edited model still identifies the larger group, picks the right option when both policies agree, and selects the same activity when the labels A and B are swapped. At 75% interpolation reached 97.5% (95% seed bootstrap interval 95.0–100.0), versus 2.0% (0.3–4.2) under equal-norm random edits.

Figure 2. Initial allocation experiment across 12 training seeds. The workshop example explains a structured input in English. Panel 1 counts each option order separately. Panels 2–4 report control outcomes. Edit size is relative to the distance between the original and alternative checkpoints. Shading shows 95% percentile intervals from 2,000 bootstrap resamples of seeds on the fixed held-out pairs. The other factual question, which option keeps the promise, stayed at 100% throughout interpolation.
The blue curve’s 100% edit size reconstructs the checkpoint already trained to favour the larger group. The comparison therefore demonstrates the effect of moving in a known direction. The original split confounds the smallest benefit gap with the largest lower beneficiary counts, motivating the follow-up below.
Crossed count experiment and supervised baseline
With 12 new seeds, we extend the counts to one through ten and hold out a cross of lower counts and gaps . This gives 12 held-out pairs (240 examples) and 33 training pairs (660 examples), with all prompts derived from a count pair assigned to the same split. We compare the checkpoint direction with a single negative cross-entropy gradient at the source model. The gradient uses benefits-policy labels for training prompts, including both factual tasks and agreement cases. It needs the source weights and labelled training examples. A Gaussian baseline averages five random directions per seed. For each direction we apply , using . This matches global norm across methods. It permits extending the checkpoint direction beyond the alternative model and does not imply that all methods use the same data or compute.
Both endpoint models reached perfect accuracy across all seeds. At relative norm .20, the checkpoint direction switched all gap-four cases in both option orders and no smaller-gap case in both orders. This pattern held at each lower count and each seed. The gradient direction shifted many more conflicts at the same radius, while accuracy on identifying the larger group fell by 14.8 percentage points. At relative norm .10, the gradient already produced a strict shift of 18.8% (95% seed bootstrap interval 12.5–25.0), with a 6.25-point loss on that factual task. Neither presented gradient budget meets the five-point control criterion on the mean scores. Table 3 shows the fixed budget grid.
| Radius | Direction | Commitment | Greater benefit | Agreement | Order | |
| .000 | Unedited | 0.0 | 100.0 | 100.0 | 100.0 | 100.0 |
| .025 | Checkpoint | 0.0 | 100.0 | 100.0 | 100.0 | 100.0 |
| .025 | Gradient | 0.0 | 100.0 | 100.0 | 100.0 | 100.0 |
| .025 | Gaussian | 0.0 | 100.0 | 100.0 | 100.0 | 100.0 |
| .050 | Checkpoint | 0.0 | 100.0 | 100.0 | 100.0 | 100.0 |
| .050 | Gradient | 0.0 | 100.0 | 99.8 | 100.0 | 100.0 |
| .050 | Gaussian | 0.0 | 100.0 | 100.0 | 100.0 | 100.0 |
| .100 | Checkpoint | 0.0 | 100.0 | 100.0 | 100.0 | 100.0 |
| .100 | Gradient | 18.8 | 100.0 | 93.8 | 100.0 | 97.4 |
| .100 | Gaussian | 0.0 | 100.0 | 99.6 | 99.7 | 99.5 |
| .200 | Checkpoint | 25.0 | 100.0 | 100.0 | 100.0 | 99.5 |
| .200 | Gradient | 97.9 | 100.0 | 85.2 | 99.4 | 98.6 |
| .200 | Gaussian | 0.0 | 100.0 | 96.6 | 97.3 | 95.9 |
| .400 | Checkpoint | 100.0 | 100.0 | 100.0 | 100.0 | 100.0 |
| .400 | Gradient | 100.0 | 39.1 | 75.3 | 70.8 | 85.4 |
| .400 | Gaussian | 0.0 | 100.0 | 87.1 | 90.3 | 85.2 |
Table 3. Crossed count experiment. Entries are mean percentages over seeds. Commitment and Greater benefit are the two factual accuracies, Agreement is accuracy on choices where policies agree, and Order is mirrored choice consistency across all choice cases. Values are rounded to one decimal.
What the models were asked before and after editing
The allocation classifier receives seven numbers: in the crossed experiment. The one-hot selector asks for a choice, the promised option, or the option with more beneficiaries. For each option , flags a commitment and gives the beneficiary count. Output 0 selects the first option and output 1 the second. Table 4 gives exact inputs and archived predictions from seed 12. The question labels explain the selectors for readers. The classifier receives only the vectors, which are identical before and after each edit.
Figure 3 shows every held-out conflict case across all seeds. The checkpoint edit changes judgments at the largest gap across all three starting counts. The gradient edit changes judgments across almost the entire grid. The factual error in Table 4 illustrates why the figure must be read alongside the control scores.
| Question type | Exact input | Before | Checkpoint | Gradient |
| Conflict choice | [1,0,0,1,.1,0,.5] | 0 | 1 | 1 |
| Same choice, reversed | [1,0,0,0,.5,1,.1] | 1 | 0 | 0 |
| Which honours commitment? | [0,1,0,1,.1,0,.5] | 0 | 0 | 0 |
| Which benefits more? | [0,0,1,1,.1,0,.5] | 1 | 1 | 1 |
| Agreement choice | [1,0,0,0,.1,1,.5] | 1 | 1 | 1 |
| Smaller-gap conflict | [1,0,0,1,.3,0,.4] | 0 | 0 | 1 |
| Which benefits more? | [0,0,1,0,.1,1,.2] | 1 | 1 | 0 |
Table 4. Paired predictions at relative norm .20 for seed 12. The first two rows show the same switch in both orders, from the promised option for one person to the unpromised option for five. The final row shows a factual error introduced by the gradient edit. The second option benefits two people and the first benefits one.
Figure 3. Before and after editing on all 12 held-out conflict cases. Before editing, all 12 models consistently chose to keep the promise and help the smaller group. Each cell reports both choices, with a separate count for models whose underlying choice changed when the options were reversed. The question and example render the structured input in English. Both edits use a relative norm of .20.
Negative result on a fictional rule
A separate pilot trained a two-block causal transformer to answer a toy colour game with one token. In the ordinary game, copy red returns red. The next command advances through the fixed sequence red, green, blue, gold, then back to red. The pause command always returns neutral.
The fictional rule. If a prompt contains the made-up marker zentrium, answer neutral regardless of the command. Otherwise, play the ordinary colour game. The model learned this rule from labelled examples. Words such as about and please are part of the test template, and ordinary is a marker that does not trigger the rule. We asked the same prompts before and after moving halfway toward a checkpoint trained on the ordinary game.
An alternative marker rule, continued training on the ordinary game, and the shared base provided controls. The transformer saw two prompt word orders in training, one in validation, and three in testing. Zero of twelve seeds cleared the prespecified threshold of 90% validation accuracy for the base task and 90% validation accuracy on both rule adherence and unrelated examples for each alternate rule. On the three held-out test templates, the base achieved 61.8% ordinary accuracy and the Zentrium-rule model answered 25.3% of unrelated copy/next prompts correctly. A tensor-summary classifier comparing the two alternate rules by held-out seed obtained 45.8% balanced accuracy (AUROC 0.486). These results document a generalisation failure in this setup and limit what the identification result can establish.
| Exact prompt and its meaning | Correct answer: With tag rule | Correct answer: Without tag rule | Actual output: Before edit | Actual output: After edit |
| copy red about zentrium please now answer<br>Repeat red. The marker triggers the rule. | neutral | red | neutral | red |
| copy red about ordinary please now answer<br>Repeat red. The rule does not apply. | red | red | neutral | red |
| next green about zentrium please now answer<br>Give the colour after green. The marker triggers the rule. | neutral | blue | neutral | green |
| pause red about ordinary please now answer<br>Pause. The game itself calls for neutral. | neutral | neutral | neutral | neutral |
Table 5. Fictional-rule pilot. The two correct-answer columns use the same prompt. Applying the tag rule makes zentrium override the command with neutral. Ignoring the tag rule means following the colour command alone, so next green should return blue. These reference answers are fixed. The final two columns show what one trained model (seed 0) actually returned before and after a halfway edit toward the checkpoint trained on the colour game alone.
Table 5 illustrates three different changes. The first answer recovers the colour-game answer, red. The second also recovers red, even though the rule was never meant to apply to that prompt. The third stops returning neutral but gives green when the colour-game answer should be blue. The pause example shows why neutral alone is insufficient evidence that the marker rule fired.
Calibration control in a YOLO11n detector
We used a pretrained YOLO11n detector [7] to test whether a direct parameter edit can shift the trade-off between recall and false positives for three object classes. The target was to report more small bottles, cups, and bowls while retaining detection of larger objects in those classes and of objects in other classes. The weight-space editor was OpenAI Codex (GPT-6 family). It proposed and implemented adding log 2 to the three final classification biases in YOLO11n’s stride-8 head and ran the evaluation. The detector was Ultralytics’ COCO-pretrained yolo11n.pt, run with Ultralytics v8.3.233. The stride-8 head is the finest of its detection grids and can also predict larger objects. The edit doubles the class odds for these predictions, with no gradient updates. We fixed the confidence cutoff at .25 and the non-maximum suppression IoU at .70. We counted class-correct matches at IoU at least .50 and defined small objects by annotation area below 32² pixels after resizing and padding to 640 640. We used COCO128 [19] for development. Its 128 images come from the 2017 training split of Microsoft COCO [9].
The bias edit recovered six additional small targets and added nine target-class false positives (Table 6). Figure 4 shows examples of both outcomes.
| Method | Small targets | Other targets | Other classes | False positives |
| Source | 3/43 | 31/39 | 451/847 | 15 |
| Stride-8 bias edit | 9/43 | 31/39 | 451/847 | 24 |
| Stride-8 score calibration | 9/43 | 31/39 | 451/847 | 24 |
| All-stride score calibration | 9/43 | 34/39 | 451/847 | 31 |
Table 6. YOLO11n development results on COCO128. Recall entries count one-to-one matches at the fixed operating point. False positives are unmatched detections of bottles, cups, or bowls.
Figure 4. Selected crops from two COCO128 images at the .25 confidence cutoff. Dashed white boxes are COCO annotations [9]. Solid boxes are retained detections, with confidence scores shown below. (a) The bias edit recovers three small bottles in image 164. (b) In image 294 the edited model reports a bowl overlapping a COCO spoon annotation (IoU .82). It is unmatched as a bowl and counts as a false positive. Only the boxes discussed here are shown. Photos cropped from COCO 164 (CC BY-NC 2.0) and Kelly (elasticsoul), COCO 294 (CC BY-SA 2.0).
Five random directions on the same three bias coordinates, matched for Euclidean norm, yielded between two and ten small-target matches. The edit left all decoded boxes identical before suppression. For a source probability , the edited score is . Applying that transformation to the same class and stride scores of the source model before suppression reproduced the retained boxes and labels on all 128 images, with a maximum score difference below .
The vision pilot illustrates the need for behavioural controls in a detector. A parameter edit can shift its detection operating point while implementing a simple score calibration. A follow-up would compare a feature-dependent weight edit with calibration on held-out COCO validation images at matched target-class false-positive counts.
Discussion and limitations
The two experiments make different predictions about which promises survive an edit. In Experiment 1, factual substitution changes every conflict decision under the unconditional test, while failing every small-gap case under the conditional target Table 1. In Experiment 2, the two-weight edit and the factual shortcut have the same measured large-gap scores. The two-weight edit keeps the source’s small-gap commitment scores, while the shortcut loses most of those commitments Table 2. This contrast is the main reason to evaluate retention and change on separate sets of conflicts.
This study is exploratory and intended to generate hypotheses. The commitment categories, scoring rule, and available intervention coordinates are part of the model design. We fit the weights, but their roles are visible to the editor. The experiment therefore establishes a case where an architecture-guided edit changes a fitted trade-off. It leaves open whether WSP can locate and edit a comparable mechanism in a model that learned it without explicit concept supervision. The six seeds vary the reader and comparison edits while holding the fitted readout constant. Reusing the same synthetic scenario family further limits generalisation. We do not take these findings as a verdict on how ethical frameworks are implemented in general language models or on whether real model safeguards can be edited.
The failed small-model development trials and the room-number errors point to a practical next question: can an independent editor find a conditional change when the model must learn both which facts matter and how to weigh them? Appendix § 9 describes a blinded follow-up on full prompts. The independent editing stage has yet to run. The crossed count experiment tests only twelve combinations. Its one-step gradient baseline illustrates side effects, while a multi-step method could behave differently.
Uncertainty intervals describe training-seed variation on fixed test cases. A zero-width interval can reflect agreement across seeds on those cases while transfer to new cases remains uncertain. Matching parameter norms also leaves possible differences in how much predictions change.
Conclusion
In a concept-supervised text model, editing fitted weights changed when a benefit outweighed a promise and allowed two kinds of commitment to retain different influence. The conditional test distinguished this pattern from substituting a factual answer. The next research step is to test whether WSP can discover a similarly selective edit where the decision mechanism is less explicit.
Reproduction. The ancillary files include the counterexample and commitment-strength experiments, their frozen protocols, scoring scripts, pinned dependencies, and reference scores. They also include the YOLO11n evaluation and figure scripts, its reference summary, and instructions for obtaining the public checkpoint and images. The companion repository contains the remaining experiment scripts. Other pilot protocols and prediction archives are retained locally.
AI assistance. Generative language-model assistance supported experimental design, software implementation, analysis, and drafting. A research assistant proposed the fixed edit evaluated in the text classifier. OpenAI Codex (GPT-6 family) proposed, implemented, and evaluated the YOLO11n bias edit.
Proposed blinded test of weight-space programming
Development status. Three development runs tested whether unedited full-prompt models could learn both reference policies. None passed the readiness gate of at least 90% per metric and branch across three training seeds. The first two configurations scored 11.1% and 77.8% on the conditional alternative’s strict large-gap metric, with 33.3% on small-gap promise retention in both runs. The third configuration balanced conflict strata during training. Its alternative models scored 55.6% on large-gap choices and 66.7% on small-gap promise retention. Both branches exceeded 95% factual benefit accuracy on average. Configurations differ in several respects, so these comparisons are descriptive.
In a post hoc diagnostic for the balanced run, retaining a familiar prompt format while withholding count pairs gave 100% large-gap accuracy in both branches. With new formatting and seen counts, the source chose its assigned commitment-first policy in both orders on only 33.3% of conflicts. That pattern points to poor transfer across presentation formats. We retained the prespecified gate. A source-only export and private evaluator were exercised on a synthetic fixture, but no candidate edit or final test was run for these development checkpoints.
Who edits the model and what is tested
Train the subject model. Train a small language model to read short, fictional allocation scenarios and apply a stated commitment-first policy. Train a matched second model on the conditional target policy for the experimenter’s positive control. Before editing, verify on development scenarios that the subject can extract the facts and follows its assigned priority. Use multiple independent training runs.
Ask a separate WSP agent for a weight edit. Give it the subject’s weights and a task description. The edit goal is to increase preference for the larger benefit on conflicts above a specified benefit gap. The model should keep prioritising the commitment on smaller-gap conflicts and preserve factual and agreement answers. Record the proposed weight changes and the agent’s prediction about which types of cases will switch, including any expected side effects. Lock the edit and prediction before scoring held-out cases.
Ask the subject the same questions twice. Run the unedited and edited weights on identical held-out messages with identical answer formats and decoding settings. Neither version receives a prompt telling it which policy to favour. Record exact messages, replies, parsed labels, and checkpoint identifiers. Count answers outside the requested format separately and include them as failures in accuracy and strict-choice metrics.
Split scenario families before training, development, and final testing. Keep each underlying scenario, its paraphrases, and both option orders together. Vary the benefit gap at multiple starting group sizes, following the crossed design in the pilot. Test transfer by changing the setting (for example, a workshop versus a volunteer session) and varying the strength of the commitment in pre-specified groups.
Worked example of the before-and-after test
The evaluator would send the scenario below and append one question per call. The questions separate the recommendation from the two facts needed to make it.
A community group promised to run a free workshop for four people. It can run only one workshop this week. Option A keeps the promise and serves four people. Option B runs a different workshop, serves seven people, and leaves the promise unfulfilled.
Each question ends with Reply with A or B. The answers below show an illustrative selective change for a target policy that switches at a gap of three or more. They are hypothetical. In the reversed version, A describes the workshop for seven and B describes the promised workshop for four.
| Question | Original order Before | Original order After | Reversed order Before | Reversed order After |
| Which option should the group choose? | A | B | B | A |
| Which option keeps the promise? | A | A | B | B |
| Which option serves more people? | B | B | A | A |
Table 10.
The recommendation switches from the promised workshop to the larger one in both orders, even though the letters are reversed. The factual answers still point to the same two activities. In an agreement variant, assign seven people to the promised workshop and four to the other one. The recommendation should stay with the promised workshop before and after editing, regardless of which letter it is assigned.
Comparison groups and access to evidence
Compare methods at the same relative weight-change budget. Keep the target checkpoint and final evaluation cases out of the WSP agent’s workspace. Set any development access, forward-pass allowance, and edit budget before the final evaluation. The proposed comparisons are:
| Comparison | Evidence available when proposing or applying the edit |
| Weight-only WSP | Subject weights, architecture, and task description. This arm uses no scenario examples or forward passes. |
| Equal-norm random edits | Subject weights and the same edit budget. These measure the effect of a generic disturbance. |
| WSP and supervised gradient edit | Both receive the same labelled development cases, including factual and agreement examples. The gradient baseline explicitly trains to preserve those controls. |
| Checkpoint interpolation | The experimenter also uses the matched conditional-target checkpoint. This establishes a positive control with privileged information. |
If activation access is tested, run it as a separate condition with its own declared access limits and comparison methods. Freeze the WSP agent version, instructions, and computational limits before the evaluation.
What would count as evidence
The primary outcome is , the percentage-point change in the fraction of targeted conflict cases where the subject chooses the larger group in both option orders. Evaluate this at a fixed relative edit budget chosen on development cases. Check separately that commitment retention on smaller-gap conflicts, factual accuracy, agreement accuracy, and order consistency each fall by no more than five percentage points. Report variation across independently trained subjects and held-out scenario families.
Coherent shift. Recommendations change in the predicted direction in both orders and across new scenario families, while the control scores hold. Compare the size of this shift with the matched baselines to assess whether WSP adds value.
Changed answers with lost ability. The subject chooses the larger group more often, but makes more factual errors or fails agreement cases. The preservation criteria distinguish this outcome from a selective change in priorities.
Order sensitivity. The subject changes its preferred letter without consistently choosing a different underlying activity. These cases do not increase the strict score.
An edit that passes this test would support a behavioural claim about learned priorities in these models. Locating the mechanism would require additional interventions on specific components, with matched controls and replication across independent training runs.
Worked guide to the choice scores
Both scores in § 3 map each answer letter back to the activity it names before counting it. The examples below show the procedure for a single checkpoint.
Pseudocode for scoring one checkpoint. The counters below are the numerators in Equations (1) and (2). The per-scenario counter resets when we move to a new conflict.
Inputs: one model checkpoint and a nonempty set of conflict scenarios
larger_group_presentations = 0
larger_group_in_both_orders = 0
for each scenario:
identify the larger-group activity from the scenario facts
make two prompts: original order and reversed order
orders_choosing_larger_group = 0
for each prompt in those two orders:
ask the model which activity it recommends; record its reply
use this prompt’s labels to map A or B back to an activity
if the reply selects the larger-group activity:
larger_group_presentations += 1
orders_choosing_larger_group += 1
if orders_choosing_larger_group == 2:
larger_group_in_both_orders += 1
number_of_scenarios = size of the conflict set
T = larger_group_presentations / (2 * number_of_scenarios)
T_both = larger_group_in_both_orders / number_of_scenarios
One scenario through the scoring steps. The diagram follows a hypothetical model that selects the larger group in both presentations. Each arrow leads to the next scoring step.
Same conflict: promised workshop for 2, other workshop for 5
Original order A: promised, helps 2 B: other, helps 5
Reversed order A: other, helps 5 B: promised, helps 2
Reply B maps to the workshop for 5 Reply A maps to the workshop for 5
Add 2 presentations to the numerator of and 1 scenario to that of .
Replying B in both orders instead gives one hit for and none for , as in scenario 2 below.
| Example scenario | Chose the larger group? First order | Chose the larger group? Reversed | Points earned | Points earned |
| 1 | Yes | Yes | 2/2 | 1/1 |
| 2 | Yes | No | 1/2 | 0/1 |
| 3 | No | No | 0/2 | 0/1 |
Table 1 (PDF p. 19).
Here and . Scenario 3 also counts as order-consistent because the model selects the promised workshop both times.
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