Conversational expectations account for apparent limits on theory of mind use
Robert X. D. Hawkins, Noah D. Goodman{rxdh,ngoodman}@stanford.edu
Department of Psychology, 450 Serra Mall
Stanford, CA 94305 USA
Abstract
Theory of mind is a powerful cognitive ability: by the ageof six, people are capable of accurately reasoning about others’ beliefs and desires. An influential series of language understanding experiments by Keysar and colleagues, however,showed that adults systematically failed to take a speaker’s
beliefs into account, revealing limitations on theory of mind.
In this paper we argue that these apparent failures are in fact
successes. Through a minimal pair of replications comparing
scripted vs. unscripted speakers, we show that critical utterances used by Keysar and colleagues are uncooperative: they
are less informative than what a speaker would actually produce in that situation. When we allow participants to naturallyinteract, we find that listener expectations are justified and errors are reduced. This ironically shows that apparent failuresof theory of mind are in fact attributable to sophisticated expectations about speaker behavior—that is, to theory of mind.
Keywords: Theory of mind; social cognition; pragmatics

Introduction
Humans can accurately and intelligently reason about themental states of other humans. Among other things, this ability – called theory of mind (Premack & Woodruff, 1978) –allows us to infer the underlying beliefs and intentions that
motivate others’ actions, and to use these inferences to predict
future actions (Baker, Saxe, & Tenenbaum, 2009). Children
acquire this ability by at least age six (Wellman, Cross, &Watson, 2001) and it serves as an important landmark in thedevelopmental trajectory of intuitive theory use (Gopnik &Wellman, 2012). While theory of mind use often appears to
be automatic and effortless, Keysar and colleagues (Keysar,
Barr, Balin, & Brauner, 2000; Keysar, Lin, & Barr, 2003;
Lin, Keysar, & Epley, 2010) have argued that it is actually
the opposite, even for adults: we are “mindblind” by default
and only overcome our egocentric biases through an effortfulprocess of perspective-taking. In other words, while adults
are capable of applying theory of mind reasoning, we do notalways apply it reliably.
In this paper we argue that the apparent failures used tosupport this view are in fact successes for sophisticated social
reasoning. In particular, we argue that critical utterances usedby Keysar and colleagues are uncooperative: they are lessinformative than what a speaker would actually produce inthat situation; listeners who are sensitive to the pragmaticsof the situation expect these more informative utterances andproduce “errors” when their expectations are flouted.
The argument offered by Keysar and colleagues is based onan elegant experimental paradigm, where participants playeda simple communication game with a confederate. The twoplayers were placed on opposite sides of a 4 × 4 grid containing a set of everyday objects (see Fig. 1). The confederate played the role of ‘director,’ giving instructions about

how to move objects around a grid, and the participant played
the role of ‘matcher,’ attempting to follow these instructions.
For example, the objects in one trial included a cassette tape.
The director gave an instruction like ‘move the tape up one
square,’ referring to the cassette. Critically, some objects
were occluded such that only the matcher could see them,creating an asymmetry in the players’ knowledge. To performaccurately on critical trials, the matcher would need to apply
theory of mind to reason about which objects were shared
and which were private. For example, imagine a roll of tapewere placed in an occluded slot: if a participant failed to account for the director’s (partial) knowledge, she might interpret ‘tape’ to mean the occluded roll of tape (which the director couldn’t possibly know about). Indeed, Keysar et al.
(2003) found that participants attempted to move the hidden
item in 30% of cases: 71% of participants attempted to movethis hidden item at least once (out of four critical cases) inthe experimental condition, compared to 0% in a control condition where there was no ambiguity over the referent. Additionally, eye-tracking data showed that participants considered the hidden item more often and for longer in the experimental condition than the control condition.
While these results are compelling, the paradigm has been
criticized from few different angles. Heller, Grodner, andTanenhaus (2008) have pointed out that in many cases, thehidden object was a better fit for the referring expression thanthe one in common ground (e.g. the hidden roll of tape vs.
the cassette tape for “the tape”), making the hidden object apriori more likely to be the referent; it would generally be
fairer to compare two objects that fit the referring expression
equally well. We validate this argument by empirically measuring relative fit of the expressions to the target and distractor
items. Moreover, Hanna, Tanenhaus, and Trueswell (2003)
argued that the viewpoint asymmetry paradigm is somewhat
unnatural: common ground is typically built incrementallyover the course of an interaction rather than presented all at
once, and it is rare for a shared display to differ in perceptual
accessibility.
In this paper, we offer an additional factor that helps account for Keysar’s results. Theory of mind as applied within
language understanding depends on an accurate model ofwhat a speaker would say in different situations. Given an utterance, a listener can then reason backward to the most plausible situation (Grice, 1975; Clark, 1996; Frank & Goodman,
2012; Goodman & Stuhlmüller, 2013). This suggests that we
consider whether the utterances produced by the confederatein Keysar’s critical conditions were actually what a speakerin that context would be expected to say. If not, then perhaps

Figure 1: Interface used in the reported experiments. Objects behind the black squares were hidden from the director.
listeners are making choices that are in fact consistent with acorrect pragmatic interpretation of the confederate’s (uncooperative) utterance. More precisely, when both players knowthat objects are occluded in the display, the speaker may tend
to add additional precision to references in order to avoid confusion. If the listener expects the speaker to do this, they will
pragmatically pick the a priori more likely referent of the referring expression, which in critical trials will be the occluded
object. In other words, it is precisely because the listenertakes the speaker’s mental state into consideration that they
are tricked by an uncooperative confederate into choosing thewrong item.
We began by replicating Keysar et al. (2003) in a multiplayer web experiment. We recruited participants to be both
director and matcher (instead of using a confederate), but instructions for critical items, as well as a random subset offiller items, remained scripted as in the original study. We
replicated the original finding, but noted a tendency of directors to be overinformative in unscripted filler trials. We thenran the same experiment without using any scripted instructions, observing unconstrained director utterances. We foundmuch greater precision in unconstrained director utterances,which match targets much better than distractors, and better
performance of the matchers. This minimal pair of experiments demonstrates that listener mistakes are at least partially
due to the pragmatics of the task, ironically showing that apparent failures of theory of mind are in fact attributable to sophisticated expectations about speaker behavior—that is, totheory of mind.

Expt. 1: Scripted Replication
Participants
We recruited 34 participants (17 pairs) from Amazon Mechanical Turk. All participants were from the U.S. Threepairs were excluded for making 2 or more errors on noncritical items.

Materials & Procedures
Participants interacted in a real-time, multi-player environment on the web (Hawkins, 2015). Pairs of participants—
assigned randomly to ‘director’ and ‘matcher’ roles—

interacted with one another through a web interface, shown in
Fig. 1. On the left side of the screen, participants could freely
type messages to one another; on the right side the screen,
players could view a set of objects placed in a 4 x 4 grid. Fiveof the grid cells were occluded from only the director’s perspective, and the remaining 11 were visible to both matcher
and director. Six or seven objects were displayed in the gridat a given time. One of these objects was a ‘target’, such asa cassette tape, placed in an unoccluded cell such that bothparticipants could see it. Another object, such as a roll oftape, was placed in an occluded slot such that it was only visible to the matcher. The rest of the objects were unrelated‘fillers’ placed in random locations. We used the same set oftargets and occluded alternatives as Keysar et al. (2003), but
we were unable to obtain the filler objects from the original
experiment and created our own. Before entering the gameenvironment, every participant independently passed a shortquiz about the task’s instructions, ensuring that they understood the interface. Among other items on the quiz, we verified that both participants understood that items behind black
cells were only visible to the matcher.
The experiment was composed of eight items, with each
item using a different set of objects. Each item included one‘critical pair’ of objects, one of them the target and the otherhidden, such as the cassette tape and the roll of tape. For
each item, we gave the director a series of four instructions
to move objects around, which were displayed as a series ofarrows pointing from some object to an unoccupied cell. To
collect clean mouse-tracking data, we began every instruction
by asking the matcher to click a small circle in the center ofthe grid. After this small circle was clicked, the director wasallowed to communicate the next instruction and we started
recording from the matcher’s mouse. One of the instructions
was a ‘critical instruction,’ which referred to the target object.
For half the instructions, directors were free to communicate
however they wished. For the other half, including all thecritical instructions, their messages to the matcher were prescripted using the precise wording from Keysar et al. (2003).
For example, when giving instructions on how to move thecassette tape, the director would be forced to use the ambiguous utterance “Move the tape down one square.” (That is, inExperimental
Baseline% attempted at least once
Orig. Expt. 1 Expt. 2
71
93
61
0
7
0

% attempted at least twice
Orig. Expt. 1 Expt. 2
46
57
32
0
0
0

% of total cases
Orig. Expt. 1 Expt. 2
30
43
24
0
2
0

Table 1: Side-by-side comparison of error rates in Keysar et al. (2003) and our two replications. The first two sections show thepercentage of participants attempting to move the occluded distractor at least once, or twice, of the four possible cases. The
third section shows the percentage of all experimental trials that the participant actually tried to move the occluded object.

these conditions, the scripted message would automaticallyappear in the director’s chat window, and they would have toclick ‘send’ for the experiment to continue.)
We collected baseline performance for each condition byreplacing the hidden alternative (e.g. a roll of tape) with anobject that did not fit the critical instruction (e.g. a battery);
we used the same unambiguous replacements as Keysar et al.
(2003). Each participant received half the items in the experimental condition and half in the baseline condition. The
assignment of items to conditions was randomized across participants, and the order of conditions was randomized under the constraint that the same condition would not be usedon more than two consecutive items. All object sets, object
placements, and corresponding instruction sets were the samefor all participants.
This paradigm differs from those used by Keysar et al.
(2003) in three primary ways. First, participants were notseated across from each other at a table: they each saw a viewof the 4 x 4 grid on their screen and communicated via a text
box. Second, we did not use a trained confederate. We randomly assigned one of the players to the role of the instruction giver, and maintained the original wording by scripting
a subset of their instructions. Finally, the hidden object was
not placed in a bag, in which respect our design more closely
resembles Keysar et al. (2000).

Results and discussion
In Table 1 we show the error rates on critical items, and compare to the data from Keysar et al. (2003). We find that 93%
of participants (all but one) attempted to move the hidden distractor at least once in the Experimental condition, out of four
possible items, compared to only 7% (only one) in the baseline condition. This is similar to the effect observed by theauthors in the original study, which found 71% and 0%. Ourerrors were larger across the board, perhaps due to the interface or the population, but the gap between the two conditions
is roughly the same size. In Table 2, we break down the pattern of errors by item. We note that several items have muchhigher error rates than others – for example, 75% of participants in the experimental condition of item 6 made an error(the “whiteboard eraser” vs. the “pencil eraser”) while only
17% of participants in item 8 made an error (the “computer
mouse” vs. the “toy mouse”). Informally, it seems as though
the more difficult items are the ones where the utterance fits
the distractor better than the target. We empirically substantiate this observation in our results for Expt. 2 below.

This item-wise variability suggests that the dependent variable highlighted in the original study (i.e. “percentage ofparticipants who moved the critical item at least once”) is
somewhat problematic: it could look like 100% of participants made errors even if they all made those errors on one
particularly difficult item. Indeed, if we exclude the three‘hard’ items where over 60% of participants in the experimental condition made errors, this dependent variable drops
from 93% to only 43% of participants.
As a proxy for the eye-tracking analyses reported by
Keysar et al. (2003), we conducted a mouse-tracking analysis.
We define the decision window as the span of time between
the point when the matcher received their instruction message and when they started moving an object. If it took them
multiple attempts to move the correct object, we restricted
our analysis to the first attempt. Within the decision window,
we computed the total amount of time spent hovering overthe cell containing the target and divided by the total lengthof the decision window to get a measure of the relative timespent considering the target. We had to exclude an additional
3 participants for this analysis, because the timestamps for director and matcher did not align and we could not establish
the decision window properly. A paired-samples t-test foundthat people tended to spend less time hovering over the target cell on critical experimental trials than on baseline trials,
t(10) = −2.65, p = 0.02 (see Fig. 2), indicating that the presence of a hidden distractor interfered with participants ability
to directly choose the target.1 .
By running this replication as a multi-player web experiment we have available an additional source of data beyond
the original experiments: half of the instructions were unscripted, providing observations of natural production of referential descriptions for filler items. Informally, we noted atendency toward additional, possibly unnecessary, precisionin descriptions. Instead of “move the stuffed animal down”,
participants said “move the stuffed panda bear down.” Or,
instead of saying “move the plane to the right” when there is
only one plane, participants said “move the red airplane to theright.” Perhaps directors were taking the time to make more
precise descriptions because they believed it was contextually
relevant: both parties know that there are hidden objects inthe environment increasing the chance of miscommunicationfrom imprecise descriptions. If the matcher expected the di1 This analysis includes participants who actually made errors,since the data is too sparse to exclude them.

Expt. 1
Expt. 2Item 1

Item 2Item 3

instruction“glasses”“bottom
block”“tape”

targetsunglasses

hiddendistractor# incorrect# correct# incorrect# correct

glasses
case
0
6
0
12

Expt. 2: Unscripted Replication
Participants
We recruited 64 participants (32 pairs) from Amazon Mechanical Turk, roughly doubling the sample size from Expt. 1.
All participants were from the U.S. Three participants were
excluded for making 2 or more errors on non-critical items,
and one additional participant was excluded because they
were not a native English speaker.

Materials & Procedures
Everything was the same as Expt. 1, except we did not use
scripted messages for critical instructions.

Results% of total decision window

Error rates are reported in Table 1, alongside the results from
Keysar et al. (2003) and our scripted replication in Expt. 1.
Target Hover−Time
0.4
0.3
condition
base
exp

0.1
0.0
Exp.1

Item 5Item 6Item 7Item 8“brush”“eraser”“smallcandle”“mouse”board
eraserpencileraser6
2
7
8

mediumcandlesmall
candle64112computer
mouse
toy
mouse
1
6
5
8

block (3rdroundcassetterow)
hairbrushblock (4th scotchflat
large cuprow)tapehairbrush
5
1
3
2
3
1
8
2
1
1
3
9
14
11
13
7
Table 2: Item-wise error rates for critical trials

rector to be precise, then they would be justified in picking thefirst or best object that meets the description (rather than worrying excessively about occluded cells). That is, the scripted
instructions used by the director for critical trials may havebeen uncooperative for this situation, and thus led matchers
astray. We tested this prediction in Expt. 2, where we removed the scripted instructions and allowed speakers to refer
to items however they wished. By the reasoning above we
expected to see more precise descriptions by unscripted directors and fewer errors by matchers in the critical trials.

0.2

Item 4“largemeasuringcup”
mediumcup

Exp.2

experiment

Figure 2: Mean percentage of time spent hovering over target
cell in the two conditions for Expt. 1 (left) and Expt. 2 (right).
Error bars are boostrapped 95% confidence intervals.

Participants never moved the hidden object in the baseline
condition, and total error rates for experimental trials are
significantly lower than the rates found in Expt. 1, χ2 (1) =5.35, p = 0.02.
We find that patterns of errors in Expt. 2 diverge significantly from a uniform distribution across items, χ2 (7) =24.8, p < 0.001. Looking more closely at these patterns, we
see that the only items where errors are consistently made arethose where the more precise utterances used remain ambiguous. For example, in item 5, both the target and distractor are
hair brushes: one is round and one is flat. Many participants
produced the sub-class label “hair brush,” which was more
precise than the scripted basic-level “brush” from Expt. 1, but
the two objects were still confusable at the sub-class level. If
we remove the two most difficult items (the “hair brushes”
and the “erasers”), the total percentage of errors on experimental trials drops from 24% to 10% and the percentage ofparticipants making at least one error drops from 61% to 32%.
When we conducted a mouse-tracking analysis identical tothe one reported for Expt. 1, we found no significant decreasein target hover time between experimental and baseline trials t(27) = 0.89, p = 0.38. To directly test for differencesin hover time patterns across the two experiments, we useda mixed-effects model with a random intercept for game ID
and an interaction between condition and experiment on target hover time. We found a marginally significant interaction,b = 0.09,t = 1.89, p = 0.066 (see Figure 2), providing someevidence that the presence of a hidden distractor no longer
interfered target selection in Expt 2.
Next, we test whether these improvements in performance
are in fact due to more informative speaker behavior. We recruited twenty judges on Amazon Mechanical Turk, who provided ratings for how well the 71 unique labels used by speakers across both experiments (including scripted labels) fit thetarget and hidden distractor objects. Their responses were
given on a slider with endpoints labeled “not at all” and “perfectly.” Inter-rater reliability was relatively high, with intraclass correlation coefficient of 0.6 (95% CI = [0.54, 0.66]).
In a mixed model including random intercepts for raters anditems, we found a significant crossover interaction of ex-

1.00
0.75

0.6
referent
distractor
target0.4
0.2

Error ratemean fitness of label

Speaker Informativity
0.8

●

●

●

●

0.50

●

●

experiment● Exp. 1● Exp. 2

●

●
●

0.25

●
●
●

0.00

0.0
Exp.1

● ●

●●

Exp.2

exp

Figure 3: Mean fitness ratings provided by judges on Amazon Mechanical Turk. Error bars are bootstrapped 95% confidence intervals.
periment and referent on mean fitness rating (see Fig. 3),
b = 0.32,t = 9, p < 0.001. In Expt. 1, the scripted label fit
the hidden distractor just as well or better than the target, but
in Expt. 2, the unconstrained labels fit the target much betterand the hidden distractor much worse. In other words, thescripted labels used in Keysar’s studies were less informative
than speakers normally produce in this scenario.
Does differential informativity of scripted utterances account for the variability across items that we noted in Expt. 1?
In Figure 4, we compare the item-wise error % and ratio oftarget fit to distractor fit. We find that across both experiments, participants have significantly higher error % on items
where the speaker’s label fits the distractor better than the target, b = 0.43,t(14) = 3.97, p = 0.001, capturing a significant
portion of variance, R2 = .5, F(1, 14) = 0.001. This suggeststhat item-wise variability across the two experiments is primarily driven by relative informativity of speaker utterances.
After separately establishing that matchers in Expt. 2 makefewer mistakes, that directors in Expt. 2 produce more informative utterances, and that informativity captures item-wisevariability in error rates in both experiments, we tested thelink between these effects in our aggregated data: does label informativity generally predict errors on critical trials?
We used a mixed effects logistic regression model to estimate the effect of target and distractor fit on the probability of making a critical error in both experiments, including
a random intercept for game ID. We found that participants
are less likely to make errors when the target fit is higher,b = −0.8, z = −4.1, p < 0.001 and more likely to make errors
when the distractor fit is higher, b = 1.7, z = 3.7, p < 0.001.
Furthermore, a model including target fit and distractor fit inaddition to item-level fixed effects is significantly better thana model including item alone, χ2 (2) = 36.2, p < 0.001, implying that speaker informativity captures residual variancebeyond the item-wise effects reported above.

General Discussion
Pragmatic language understanding requires sophisticated social reasoning. To interpret an utterance, a listener must consider how a speaker is likely to behave in context. The rational use of theory of mind for a listener thus depends onher expectations about the speaker: If, in a particular context,

0.5

1.0

1.5

2.0

Distractor fitness / target fitness

Figure 4: Item-wise error rates compared with label fitness
ratios, across both experiments. Error bars are bootstrapped
95% confidence intervals for fitness and 95% highest posterior density intervals for error rates.
she expects a speaker to provide sufficiently informative utterances, she may be justified in neglecting his epistemic state
when resolving reference.
In our replication (Expt. 1), we found evidence that listeners neglect the speaker’s epistemic state, as Keysar and colleagues claim. We also found that when the speaker’s utterance fit the hidden distractor better than the target, matchers
were more likely to make errors. Indeed, we found that theextremely heterogeneous pattern of errors across items waswell explained by the relative fit of the utterance to target anddistractor. This suggests that reference disambiguation was
driven primarily by a priori label fitness rather than consideration of occluded vs. mutual visible items. However, thisdoes not necessarily imply limitations on theory of mind—ifspeakers could be expected to naturally provide expressions
which apply better to the target, then this behavior would beappropriate. In Expt. 2, we found that speakers did naturally produce more precise, informative utterances than required and these unconstrained utterances fit the target significantly better than they fit the hidden distractor. For example, no speaker in Expt. 2 produced “the bottom block,”which was used as a critical instruction in Expt. 1. Instead,they said “the bluish block with a B” or “block with the blue
writing,” which relied on less confusable perceptual features
and thereby decreased error rates. Thus, the errors observedin Expt. 1 can be explained as a result of an uncooperative
confederate (speaker)—the experiment set up certain pragmatic expectations through the task context, then deliberately
flouted them in critical trials.
The Gricean maxim of quality dictates that cooperative
speakers should make their utterance as informative as is required for current purposes, but no more so. If the referring
expressions used in Expt. 1 uniquely pick out the target fromthe speaker’s perspective, then why would unscripted speakers in Expt. 2 be more informative than this? One possibility is that awareness of the complex mismatch in epistemicstate with the listener leads the speaker to provide extra information in an attempt to avoid miscommunication. Anotherpossibility is that more general dynamics of language are inplay. Studies of over-informativity in referring expressions

have uncovered a general tendency of speakers to provide redundant information. This tendency can depend on a numberof situational factors, such as the tendency to mention perceptually salient features to speed up the identification process(Koolen, Gatt, Goudbeek, & Krahmer, 2011). The exact origin is a subject that must be followed up by future research(e.g. Gann & Barr, 2014), but it is clear that the tendency of
speakers to produce highly informative referring expressions
is useful to, and relied on by, listeners.
This finding is consistent with a recent proposal by Heller,
Parisien, and Stevenson (2016) that referring expressions areinterpreted by probabilistically integrating multiple sourcesof information: when conversational expectations lead participants to expect over-informative utterances, they (rationally)
place relatively less weight on features of the environment determining common ground, such as shared perceptual access.
Further work in a wider variety of tasks is necessary to pin
down the various factors determining the relative weightingof these different sources of information, but we have argued
that pragmatics play a crucial role.
It is worth noting several significant differences between
our study and Keysar et al. (2003). The primary difference
between our study and the original, of course, is that it was
run on the web with participants connected through a virtualenvironment, instead of face-to-face in a room. We believe
we addressed the major concern about exploring theory ofmind in web experiments – that participants do not truly believe they are interacting with another human – by allowing
instantaneous, responsive, real-time interaction. On the other
hand, it is known that textual communication, as in our chatbox, can differ from face-to-face verbal communication. Additionally, aspects of the interface such as the graphical representation of occluded cells may be less intuitive, or require
more training, on the web than in the lab.
A related difference is our decision not to use a confederate. While confederates are useful for reducing variation
across instances of the experiment and delivering carefullytargeted manipulations, their use may have unexpected consequences. Beyond the difficulties of conducting large-scale
experiments with confederates, it is difficult to exactly replicate all the subtleties of the confederate’s behavior that might
influence results. The pair of experiments we report is a reminder that manipulations administered by a trained confederate can interact in unexpected ways with a participant’s social and communicative expectations. Regardless of the experimental context, it is illuminating to see how real participants naturally interact.

Acknowledgements
We’re grateful to Boaz Keysar for providing select materials for our
replication. Expt. 1 was originally conducted under the supervisionof Michael Frank, with early input from Desmond Ong. This work
was supported by ONR grants N00014-13-1-0788 and N00014-131-0287, and a James S. McDonnell Foundation Scholar Award to
NDG. RXDH was supported by the Stanford Graduate Fellowshipand the National Science Foundation Graduate Research Fellowship
under Grant No. DGE-114747.

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