Contribution
It gives a method that gets between a person’s choice and the outcome they are shown, one person and one trial at a time. Before it, the gap between what people do and the reasons they give was shown only in group-level response patterns (Nisbett and Wilson, LIT-1410, its reference 12). Here a report can be shown false of the person who gave it: a reason that names a feature only the face they rejected has is about that face, not about their choice.
Key insight
The loop from intention to outcome that theories of decision and control assume can be open in a simple evaluative choice. People accept the outcome they are handed as their choice and explain it, and their explanations of the choice they did not make look like their explanations of the ones they did.
Assumptions
- Detection criteria. A trial counts as concurrently detected on any spontaneous sign during the switch. Retrospective detection is probed by a funnel of increasingly specific questions, then debriefing, then sorting one’s chosen cards; a correct pick with false positives counts as “possible retrospective detection”. The SOM argues this errs on the liberal side, and that it deliberately does not use forced-choice probes, which “would probably have resulted in more instances of detected manipulations”. The result is about detection in a non-vigilant setting.
- Correction for prior detection. Trials after a participant’s first detection are dropped in Figure 2B, on the ground that detection makes people suspicious.
- Stimuli. Grayscale female faces from the Stirling PICS database, 15 pairs, matched roughly; manipulated pairs at positions 7, 10 and 14, always in the same order. Similarity on a 1–10 scale: 5.7 (SD 2.1) for the high-similarity set, 3.4 (SD 2.0) for the low.
- Reports. Verbal reasons were asked after the three manipulated trials and three non-manipulated ones, recorded, transcribed (Swedish) and coded by blind raters in two calibrated rounds of three.
Key results
- Detection. 3 × 2 between-group design, deliberation time (2 s, 5 s, free) × similarity. Of 354 manipulated trials, 46 (13%) were detected concurrently; no condition, even free time with dissimilar faces, exceeded 27%. Free time raised concurrent detection over fixed time, t(118) = 2.17, p < 0.05; 2 s and 5 s did not differ; similarity, sex and age made no difference. All forms of detection together exposed at most 26% of manipulated trials. Correcting for prior detection lowers the rate further, t(118) = 3.21, p < 0.005.
- Reports. No difference between reports on manipulated and non-manipulated trials in empty reports, tense, length (33 against 38 characters, SDs about 45) or laughter, nor in emotionality, specificity or certainty, all rated near the scale’s midpoint (3.5, 3.1, 3.3 of 5). Dynamic self-commentary, questioning one’s own motives, was more common on manipulated trials, t(118) = 3.31, p < 0.005, but occurred in only 5% of them.
- Content. Some manipulated-trial reports name features unique to the face received (“specific confabulation”); some must be about the face chosen, being inconsistent with the one received (“original choice”). The split across eight categories is in Figure 3 and is not reproduced here.
- SOM pilots. On-screen abstract patterns (20 people, 19% of manipulated trials detected), on-screen female faces (22 people, 32%, 20% corrected) and male faces with eye tracking (18 people, 37%, 29% corrected), each with no clear difference between the two kinds of report.
- “Choice blindness blindness” (SOM). Of the participants who detected nothing, 84% said they would have noticed such a switch; about 87% in the pilots.
Claims
| id | claim | strength | support |
|---|---|---|---|
| C1 | People mostly fail to notice when the outcome of a simple attractiveness choice is swapped | strong | 354 trials, 13% concurrent detection; three pilots in other media |
| C2 | Detection does not depend on the similarity of the faces | moderate | no difference between the two sets; similarity was rated, not varied finely |
| C3 | Reasons given for a non-chosen outcome are indistinguishable from reasons for a chosen one on the measured dimensions | moderate | blind coding, high interrater reliability; a null on eight variables, with one difference |
| C4 | Some reasons are demonstrably about the outcome received and not the choice made | strong | the “specific confabulation” reports |
| C5 | People believe they would detect such a switch | moderate | one debriefing question, 84% |
| C6 | Choice blindness says something about the concept of intention | weak | discussion; the authors say the experiment “warrants no conclusions about the mechanisms” |
Concepts
- Choice blindness: failing to notice that the outcome presented is not the one chosen, by analogy with change blindness.
- M and NM trials: manipulated and non-manipulated.
- Specific confabulation: a reason that refers to a feature unique to the face received on a manipulated trial.
- Choice blindness blindness: the belief that one would have noticed.
Connections
It extends Nisbett and Wilson (LIT-1410) from group-level dissociations to single reports, and change blindness (Rensink 2002, Simons and Levin) from perception to choice. Its SOM cites a then unpublished study by Tärning, Hall, Johansson, Sikström and Olsson in which feedback from manipulated trials changed later preferences, the line later published as choice-induced preference change.
Bearing on the record
- CASE-114, note of 2026-10-23. The note says, after A5, that this work and Nisbett and Wilson “already demonstrate that reported authorship and actual causal history can diverge”. On this reading that is right for this work, and narrowly: what is shown is that a reason can be produced for an outcome one did not choose and be indistinguishable on eight measures from a reason for one’s real choice. It does not show that ordinary reasons are confabulated; the authors raise that “radical reading” and leave it open, and the “original choice” reports show some reports do carry the real choice. The case’s own limit stands: nothing here bears on whether representing a central controller changes error correction.
No instruction for machine-learning practice; nothing for the anthology.
Limitations
- One task, one kind of choice. Attractiveness of unfamiliar faces, low stakes, about two seconds of occlusion, in a non-vigilant setting. The SOM grants that an explicit detection task would have caught most switches.
- Detection by spontaneous report. Forced-choice probes were not used by design; detection is a lower bound on what participants registered.
- The report comparison is a null. Equivalence on eight variables is not tested as equivalence, and the coding categories came from the authors.
- Errors and slips. The report gives 120 participants; the SOM says 2 were dropped, which is what makes 354 = 118 × 3. The t-tests are reported with 118 degrees of freedom, which a two-group comparison of 118 participants would not give (116); the test behind them is not stated. Supporting reference 29 (“A. Sigiru et al.”) and reference 4 (no journal named) are garbled.
Open questions
- What does detection do when the choice matters, or when people are warned? The SOM’s pilots vary the medium, not the stakes.
- Do reasons given on non-manipulated trials have the properties of the manipulated ones? The method cannot say, since only manipulated trials have a checkable ground truth.