A child watches a character place a toy in a box. While the character is away, someone moves it to a cupboard. When asked where the character will look, the child must answer from the character’s outdated information rather than from what the child knows. It is an elegant question, but a wrong answer can have several explanations. The child may misunderstand the question, forget who saw the move, struggle to inhibit the cupboard answer, or reason differently about belief. The answer alone does not identify which explanation is right.
Measuring theory of mind therefore requires a more precise question than whether a person can “read minds.” Theory of mind refers to reasoning about another person’s beliefs, knowledge, desires, intentions or feelings as distinct from one’s own. A task presents selected cues and asks for a response. It samples a particular mental-state inference under particular language, memory and response demands. This guide explains what prominent tasks can support, what they cannot establish, and how to build a measurement design that respects those boundaries.
Define the inference before selecting the task
Theory of mind is a family of related abilities and performances rather than one directly observable quantity. Inferring where someone will search for a hidden object differs from inferring whether a conversational remark was meant to comfort, deceive or embarrass. Both may involve mental-state reasoning, yet the information available, the response format and the social stakes differ. A measure is interpretable only after the researcher names the aspect of reasoning that matters.
A useful first distinction is between identifying a state and using it to predict behavior. Someone may correctly say that a character believes the toy is in the box yet predict a search at the cupboard because they misunderstood the question about action. Conversely, a correct location prediction could arise from a learned rule about stories without a rich account of the character’s mind. The score is evidence about performance on the item, not a transparent image of the process that produced it.
Researchers should specify whose mind is represented, which state is relevant, what information the target person has, and what the participant must do with that information. They should also define the population and setting. A preschool story task, a complex adult narrative and an inference in an actual conversation cannot be assumed to have the same difficulty or meaning. The Institute’s synthesis is to treat theory-of-mind measurement as a problem of matching an explicit claim to an observable contrast.
What false-belief tasks reveal
Classic false-belief tasks place the participant’s knowledge in conflict with a character’s belief. Wimmer and Perner’s original experimental logic made it possible to ask whether a child would predict action from the character’s mistaken belief rather than from the real location. Later studies altered the story, object, question and response procedure. Wellman, Cross and Watson’s meta-analysis found orderly developmental patterns across many false-belief studies while also showing that task features matter. Neither finding licenses a single universal age at which an indivisible faculty switches on.
The contrast is powerful because the character’s belief and reality point to different answers. Yet it is also demanding. A participant must track who witnessed which event, retain the sequence, interpret the question and resist giving the answer they personally know. A control question about the object’s real location establishes memory for part of the story, but it does not remove all verbal or inhibitory demands. If a child fails the belief question after passing the reality question, the result still admits more than one explanation.
First-order false belief asks what one person thinks about the world. More elaborate tasks ask what one person thinks another person thinks, or whether a person recognizes a misleading appearance. These variants add memory and linguistic complexity. A higher-order task is not automatically a purer measure of mental-state reasoning; it may simply be harder along several dimensions. Item design should make the required inference explicit before comparing age groups or conditions.
Researchers sometimes speak as though a correct answer demonstrates full social understanding. It demonstrates a narrower competence in that format. A child who predicts the character’s search may still misunderstand a subtle intention, and a child who gives the wrong location may reason well about other people’s wishes in daily life. Multiple tasks with distinct surface demands provide stronger construct evidence than one celebrated story.
Language and executive demands are part of the score
Language is not merely a nuisance variable that can be subtracted away. The participant must understand the story, temporal sequence, names, question and possible answers. Milligan, Astington and Dack’s meta-analysis examined the relation between language ability and false-belief understanding. It supports attention to language when interpreting developmental task scores, while leaving open the mechanisms behind that relation. Language may enable conversation about minds and also determine access to a verbal test.
Inhibitory control is another plausible contributor. On a false-belief item, the real location is salient because the participant saw the move. Carlson and Moses found individual differences in inhibitory control associated with children’s theory-of-mind task performance. This association is not proof that inhibitory control alone causes a correct or incorrect belief judgment. It does mean that a group difference on a conflict-heavy task cannot safely be labeled a difference in mental-state representation without considering control demands.
A good design uses matched comparison items. A nonmental-state control can require remembering a change or suppressing a tempting answer while keeping story length, vocabulary and response method similar. No control is perfect, but a pattern across belief and comparison conditions helps locate the source of difficulty. Researchers can also report language measures, memory checks, attention to the story and item-level performance rather than hiding them inside one total score.
Adaptation for language or accessibility needs requires more than translating words literally. “Think,” “know,” “pretend” and equivalent verbs do not carry identical pragmatic implications in every language or setting. A gesture or picture response may reduce spoken output while changing the inference and chance structure. When the format changes, the test should be validated again for the group in which it will be used. A low score on an inaccessible task is not evidence of a missing social capacity.
Adult tasks sample different parts of the construct
Many straightforward false-belief questions are too easy for typical adults to distinguish meaningful variation. Researchers therefore use stories about misunderstanding, irony or intention; narratives that require the reader to infer a character’s state; or judgments from facial cues. These tasks broaden the sample of inference, but they do not become interchangeable just because they share a theory-of-mind label.
Dodell-Feder and colleagues introduced an adult fiction-based task that asks readers to reason about characters’ mental states. Its value is that it requires integrating information across a narrative rather than choosing the real or false location of an object. At the same time, performance depends on reading comprehension, familiarity with narrative conventions and the particular scoring rubric. A study using it should describe how answers are scored, whether raters agree, and what comparison tasks show about its specificity.
The Reading the Mind in the Eyes Test asks participants to select a mental-state word for a photograph of the eye region. It removes much of the story structure but adds vocabulary, visual recognition, cultural familiarity with expressions and a forced choice among labels. A meta-analysis of this test’s psychometric network concluded that it behaves more like an emotion-perception measure than a general theory-of-mind measure. That does not render every use of the task worthless. It narrows the claim: eyes-test performance is evidence about judgments from restricted facial information under that test’s response options.
One can infer a belief from context without confidently naming an emotion from eyes, or name an expression without predicting what its bearer believes. Calling both scores “theory of mind” can disguise the difference. For adults, the selection of a task should follow the intended contrast: inference from privileged knowledge, interpretation of a social narrative, or recognition of affective cues. A battery may expose whether results converge; a single test cannot be assumed to stand for the whole family.
Measurement is not the same as social ability
A task can ask what a character believes while real interaction requires listening, timing, negotiation and repair. Someone may infer a partner’s concern correctly but respond in a way the partner dislikes. Someone else may misunderstand an intention and still maintain a respectful relationship by asking and correcting. Actual social outcomes depend on both people, their history, power, culture, sensory environment and available time. They should not be treated as a simple readout of one person’s mental-state score.
Nor is theory-of-mind performance equivalent to empathy or moral care. Understanding what another person believes could support helpfulness, manipulation or indifference. Feeling concern is not identical to predicting a belief. The distinction matters when a test is proposed for education, hiring or clinical interpretation. An accurate label for what was measured is more ethical and more scientifically useful than an inflated label such as “social intelligence.”
Relationship context changes the inference too. Familiar partners may understand each other through shared history and direct clarification rather than detached prediction. In an unfamiliar task, the participant may have to guess what an experimenter considers the conventional answer. Disagreement can reflect a different interpretation of ambiguous evidence, not failure to recognize that another person has a mind. The more naturalistic the assessment, the harder it may be to define a single correct answer; the more constrained it is, the less of life it samples.
Related Learning Hub discussions of epistemic trust and emotional awareness concern neighboring capacities. They can affect interaction, but neither should be silently merged with belief attribution. The point of linking these ideas is to preserve the distinction while understanding how they may interact.
Build a validity argument rather than a single score
Start with the proposed use. If the question is whether children predict behavior from a mistaken belief, a false-belief contrast is relevant. If the question is whether adults notice subtle misunderstanding in a story, a narrative task may be closer. If the question is everyday communication, include observations or reports of actual interaction and state how those outcomes differ from the task. A score is useful when the route from item to conclusion is explicit.
Next inspect item content. How many mental states are sampled? Are all items about false belief, or do some concern desire, intention and emotion? Is the answer determined by the stated facts, or could an alternative social interpretation be reasonable? Review ambiguous items before looking at group effects. Otherwise, a statistically reliable difference may be driven by particular wording or cultural assumptions. Document exclusions and scoring rules before analysis where possible.
Then ask whether the measure distinguishes its intended construct from neighboring demands. Compare belief items with matched factual-memory and inhibitory-conflict items. Use independent language measures for verbal tasks. For narrative tasks, compare with reading comprehension and inference about nonmental events. For facial-cue tasks, compare with ordinary emotion recognition and vocabulary. These comparisons do not purify a test mathematically, but they show which interpretations are plausible.
Reliability matters as much as a striking mean difference. If items barely agree or a person’s score changes unpredictably over a short period, an individual ranking is fragile. Ceiling and floor effects hide differences at opposite ends of ability. Reporting the score distribution, item difficulty, internal consistency where appropriate, test-retest evidence and uncertainty around estimates helps readers judge what the instrument can carry. A task designed to produce a group contrast may still be unsuitable for evaluating one individual.
Finally, test whether the interpretation travels. A translated task, new age band, online delivery or altered stimulus set changes the measurement situation. Evidence in one language and sample cannot simply be imported into another. Measurement invariance and accessibility checks are especially important when scores will be compared across groups. A fair comparison asks whether participants had a comparable opportunity to understand and express the targeted inference.
Common confounds in interpretation
The first confound is knowing the real answer. A belief question deliberately pits another person’s limited information against the participant’s knowledge. Failure may reflect difficulty setting aside that knowledge. A design that separately measures conflict handling can help, but it cannot make the belief inference independent of control in every context.
The second is language. Long stories and abstract mental verbs reward comprehension and expressive fluency. A participant may be capable of representing another perspective yet unable to parse or produce the expected answer. Researchers should minimize avoidable linguistic complexity while recognizing that some social reasoning genuinely uses language. The goal is to know which language demands are part of the intended construct and which are artifacts of the instrument.
The third is task pragmatics. Participants may infer that an adult asking an obvious question expects an unusual response, or may answer according to what usually happens rather than what the character believes in this story. Repeating standard items can introduce learned conventions. Varying examples, checking understanding and asking for a brief explanation can clarify response strategies, though explanations themselves raise verbal demands.
The fourth is content and context. A familiar story may invite rich inference, whereas culturally unfamiliar situations, expressions or social rules can make the same question opaque. The researcher should not treat a culturally specific interpretation as a neutral universal standard. Consultation with the populations being studied can reveal hidden assumptions before scores are used to make claims about them.
The fifth is compression. A total score over a few heterogeneous items can suggest a stable trait while concealing distinct patterns. Reporting false-belief, narrative and facial-cue results separately allows a reader to see whether a finding concerns one format or several. If the measures diverge, the divergence may be informative rather than an inconvenience to be averaged away.
What the evidence does not show
The cited work does not show that one task directly measures a complete, context-free capacity to understand minds. Developmental patterns in false-belief performance do not establish a fixed milestone for every child. Correlations with language or inhibitory control do not settle whether these skills are causes, prerequisites, consequences or co-developing supports in every setting. Adult narrative and eyes-based scores do not demonstrate how a person will behave in a real relationship.
In particular, a low score should not be turned into a diagnosis, a judgment of empathy, or a claim that someone cannot participate meaningfully in social life. These measures were developed for research questions and have their own validity limits. Group averages cannot safely be used to define every member of a group. A review of egocentric mentalizing offers background on perspective bias, but it does not validate every theory-of-mind instrument.
There is also no single task battery that removes all confounds. Adding language, memory and control measures can sharpen inference; it cannot reveal another person’s inner life directly. Everyday communication often succeeds through asking, listening and revising an interpretation. Those reciprocal practices are not captured by a one-way laboratory question with a predetermined answer.
How to report a defensible conclusion
A careful report names the task and population before using the broader construct term. “Participants predicted a story character’s search location more accurately under this condition” is stronger than “their theory of mind improved” unless several independent measures support the latter. State whether the outcome was a belief answer, a narrative explanation, a facial-cue choice or an interaction measure. Give uncertainty and avoid translating a small score difference into an unsupported practical claim.
When a study finds convergence across tasks, describe what was shared: perspective conflict, interpretation of intentions, or mental-state vocabulary. When it finds divergence, ask whether the tasks differ in language, stimulus type, response options or social context. A thoughtful null result can also matter. It may show that a proposed intervention changed one kind of social judgment without transferring to another, or that the chosen instrument was insensitive to the intended change.
The practical aim is modest and demanding at once. Theory-of-mind research offers ways to study how people use evidence about another person’s perspective. Good measurement does not collapse that process into a single label. It specifies the inference, checks alternative explanations and preserves the gap between a task response and a person’s wider social life. For a broader developmental frame, see development through social mediation.
Research references
- Wimmer, H., & Perner, J. (1983). Beliefs about beliefs: Representation and constraining function of wrong beliefs in young children’s understanding of deception. Cognition, 13(1), 103–128. View source.
- Wellman, H. M., Cross, D., & Watson, J. (2001). Meta-analysis of theory-of-mind development: The truth about false belief. Child Development, 72(3), 655–684. View source.
- Milligan, K., Astington, J. W., & Dack, L. A. (2007). Language and theory of mind: Meta-analysis of the relation between language ability and false-belief understanding. Child Development, 78(2), 622–646. View source.
- Carlson, S. M., & Moses, L. J. (2001). Individual differences in inhibitory control and children’s theory of mind. Child Development, 72(4), 1032–1053. View source.
- Dodell-Feder, D., Lincoln, S. H., Coulson, J. P., & Hooker, C. I. (2013). Using fiction to assess mental state understanding: A new task for assessing theory of mind in adults. PLOS ONE, 8(11), e81279. View source.
- Kittel, A. F. D., Olderbak, S., & Wilhelm, O. (2022). Sty in the mind’s eye: A meta-analytic investigation of the nomological network and internal consistency of the Reading the Mind in the Eyes Test. Assessment, 29(5), 872–895. View source.