2.1 Subject islands in Spanish

Subject islands are historically regarded as strong islands, from which no extraction is allowed (Szabolcsi & Lohndal 2017).

Subject islands vary cross-linguistically. Some languages do not (always) display subject island effects. Stepanov (2007) argues extraction is related to post-verbal subjects, pointing to languages like Japanese (Omaki et al. 2020), Russian (King 1994), Hindi (Stepanov 2008), German (Haider 1993), and Palauan (Georgopoulos 1991); to these we can add Czech and Slovak (Starke 2001), Dutch (Broekhuis 2011), Italian (Bianchi & Chesi 2014), and Hungarian (Surányi & Turi 2018).

For Spanish, Uriagereka (1988) presented example (5), repeated from (3), to demonstrate that extraction from subjects is permitted selectively: Post-verbal subjects are not islands (5a), while pre-verbal subjects are (5b).

Subsequently, Gallego and Uriagereka (2007) and Gallego (2011) presented additional evidence from Spanish; for instance, a similar contrast by position emerges with intransitives, as in (6).

Position is not the only factor, though. For instance, Gallego notes subextraction “in a monoclausal environment” (7a) or from non-final position (7b) is degraded (Gallego 2011: 51–52).

Haegeman et al. (2014) identified several further syntactic and semantic constraints. In addition to subject position, they highlighted properties of the subject and extractee that affect acceptability.

Building on previous work,¹ Haegeman et al. pointed out that extraction from non-specific or non-referential subjects, as in (8a), is better than specific subjects (8b). Theta role also matters (9): extraction from higher in the thematic hierarchy, especially from agents (9a), is worse than lower in the hierarchy, like themes (9b).

Properties of the extractee also affect acceptability: extracting a D-linked (complex) wh-phrase (10a) is better than a simple wh-word (10b),² and extracting arguments of the head noun, as in (11a), is better than adjuncts (11b).

For Haegeman et al., violations of each of these proposed constraints—along with constraints on subject position—accumulate, such that a D-linked argument extracted from a non-specific, post-verbal theme subject of a passive should be completely well formed (12a), while a plain wh-word adjunct extracted from a specific pre-verbal agent subject of a transitive should be quite degraded (12b), with these options forming the ends of a continuum of gradient acceptability.

In summary, several semantic and syntactic factors condition extraction from subjects in Spanish, and descriptions concur that subject position is a crucial factor.

2.2 Experimental evidence

Although most formal experiments on islands have corroborated informal judgments, differences have emerged (Sprouse & Villata 2021), so experimentally confirming reported judgments is important (Chacón 2021). Indeed, previous experiments have found other islands in Spanish differ from the descriptions in the theoretical literature (e.g., Hoot & Ebert 2024, Pañeda et al. 2024).

Three experiments have examined subject islands in Spanish and found evidence of island effects.

López-Sancio (2015) carried out a seven-point rating task testing several islands in both wh- and relative clause dependencies with Peninsular Spanish speakers. For the subject islands, all subjects were pre-verbal and non-specific. He did not control for theta role, D-linking, or other properties of the extractee. His results revealed evidence of an island effect with wh-questions but not with relative clause dependencies.

Pañeda et al. (2020) conducted a timed yes/no task with Peninsular Spanish speakers to test several islands, including subjects. They expressly designed their items to provoke an island effect—extracting plain wh-words from specific, pre-verbal agentive subjects—and they found such sentences were starkly unacceptable, reaffirming that pre-verbal subjects in Spanish are islands, at least when the properties of subjects and extractees align with islandhood.

López-Sancio operationalized the island effect slightly differently from Pañeda et al.: instead of comparing extraction from the embedded clause to extraction in the matrix clause, his experiment compared extraction from embedded subjects to extraction from embedded objects (following Sprouse et al. 2016). The third study, Stigliano et al. (2025), asked whether these two ways of defining the design for subject islands might have affected the experiments’ outcomes. They obtained judgments on a seven-point scale from Argentine Spanish speakers and found both designs produced similar effects. Stigliano et al. also examined individual variation and pointed out that the island violation condition produced substantial inter-individual variation in the judgments, unlike the other conditions.

In sum, the existing experimental evidence suggests that pre-verbal subjects in Spanish provoke island effects. However, they all tested only the pre-verbal position, where such effects were predicted, and López-Sancio (2015) did not control properties of the extractee, while Pañeda et al. (2020) included properties designed to provoke an effect. Yet for Spanish, the key claim that post-verbal position allows extraction remains untested.

Beyond Spanish, experiments investigating subject islands in languages that generally allow post-verbal subjects have found a wide range of results: no subject/object asymmetry (Japanese: Omaki et al. 2020); no effect by subject position (Russian: Polinsky et al. 2013; Hungarian: Surányi & Turi 2018), potentially due to semantics (Italian: Bianchi & Chesi 2014); a weak but statistically significant effect in post-verbal position (Romanian: Schoenmakers & Stoica 2024); a cumulative effect combining movement and a subject/object contrast (German: Jurka 2010); or even higher acceptability in pre- than post-verbal position (Russian: Belova 2021). This range of results could be due in part to methodological differences. For example, some of these studies did not isolate subject position from other factors known to affect acceptability, e.g. specificity (Jurka 2010; Polinsky et al. 2013; Belova 2021), and most did not use the factorial design that helps isolate the island effect (Schoenmakers & Stoica 2024 is an exception). Since no consistent pattern has emerged, new evidence from post-verbal subjects in Spanish stands to contribute to understanding subject islands cross-linguistically.

2.3 Source of island effects

The mere presence of an effect in a judgment task does not distinguish its source, and Liu et al. (2022) identify three main families of explanations for island effects, which they call “structural,” “functional,” and “processing” accounts (see also Newmeyer 2016 for a similar typology). These theories have been applied to explain islands of all types; we focus especially on accounts of subject islands.

Structural accounts appeal to syntactic constraints represented in the speaker’s competence grammar. In syntactic theory, subject islands are explained by positing a grammatical restriction that prevents extraction from subjects once they move to Spec-TP. The long history of these formal mechanisms includes the Condition on Extraction Domains (Huang 1982), Criterial Freezing (Rizzi 2006), probe/goal theory (Chomsky 2000), and phases (Chomsky 2008). The two most prominent structural accounts of Spanish subject islands are Gallego’s phase-based approach and Haegeman et al.’s cumulative constraint approach. Gallego (2011) argued extraction is evaluated at the phase level. Pre-verbal subjects in Spec-TP are rendered inactive due to A-movement to Spec-TP and Case valuation, prohibiting extraction. Post-verbal, in situ subjects in Spec-v*P, without A-movement or Case valuation, remain active when evaluated at the v*P phase, permitting extraction. On the other hand, Haegeman et al. (2014) analyzed subject islands as responding to a set of cross-linguistic syntactic and semantic constraints, which are violable and cumulative, with unacceptability increasing as more constraints are violated. Comparing Spanish and English, they analyze the difference between the two languages as due to independent availability of post-verbal subjects in Spanish, whereas English generally requires movement to Spec-TP. These accounts both predict that pre-verbal subjects in Spanish should create an island effect while post-verbal subjects should not, after avoiding other constraints.

Functional accounts also appeal to the speaker’s competence but locate the problem in a clash of information structure or pragmatic/semantic anomaly. In these approaches, no syntactic restriction bars extraction from subjects; instead, the information-structural effects or semantics of question-formation or relativization clash with the subject’s discourse status, producing ill-formedness. For example, Abeillé et al. (2020) propose the Focus-Background Conflict constraint: “A focused element should not be part of an unfocused/backgrounded constituent.” Subjects are usually background; wh-words are focused. Thus, extracting a focused wh-word out of a backgrounded subject produces an information-structural clash.³ This is not a syntactic restriction on extraction from a particular position; it’s a discourse restriction on extraction from constituents with a particular information status. Indeed, experiments have found that ratings of subject islands are linked to the degree of topicality of the subject (Chaves & King 2019) and that information structure affects judgments of subject islands (Chaves & Dery 2019; Abeillé et al. 2020). These accounts predict that, all else being equal,⁴ if the relevant information structure properties are held constant between pre- and post-verbal subjects, their acceptability should be comparable.

Processing accounts differ from the other two in appealing to difficulty parsing island structures in real time. Since the seminal work of Kluender and Kutas (1993), island effects have been attributed to an overload on limited working memory due to their complexity (Hofmeister & Sag 2010) or to difficulty in retrieving the referent from memory upon encountering the gap (Keshev & Meltzer-Asscher 2019). In resource-limitation accounts, island structures are not grammatically restricted but instead cause processing breakdown due to limits on working memory or other cognitive capacities. Because cognitive capacity varies by individual, Sprouse et al. (2012) predicted that perceived unacceptability would covary with language processing abilities, such as working memory.⁵ They did not observe the expected correlation, and several studies have replicated their findings (Michel 2014; Aldosari 2015; Pañeda et al. 2020; Pham et al. 2020), although others have raised questions about the adequacy of the working memory tests employed (Hofmeister & Casasanto & Sag 2012a; 2012b), and work on the relationship of sentence processing to island effects remains an extremely active area of research (see Liu et al. 2022; Sprouse & Villata 2021).

We attempt to isolate structural factors from discourse and processing factors in two ways. First, we used contexts to hold the information structure constant across subject positions. The contexts make the same information given or new in both subject positions, with the aim of disentangling position and information structure. Second, we followed previous work in measuring working memory (with a task addressing some earlier critiques) and examining whether it correlated to individual island sensitivity, to identify a hypothesized relationship between sentence-processing ability and island effects.

2.4 Factorial designs and interpretation in experimental syntax

We adopt the factorial definition of islands popularized by Sprouse and colleagues (e.g., Sprouse et al. 2012; 2016). Concretely, we adopt Pañeda et al.’s (2020) 2 × 2 design for subject islands. Recall that previous studies have operationalized subject islands in two ways, but Stigliano et al. (2025) found both methods produced equivalent results.

Factorial designs isolate a predicted grammatical effect from other features that may impact acceptability by crossing two factors. For instance, since more complex sentences may receive lower ratings, perhaps the mere presence of a complex island structure makes a sentence less acceptable. In the experiment paradigm in (13), we operationalize this difference as the Island factor: the presence (13a) or absence (13b) of the complex subject. Similarly, all else being equal, long-distance dependencies are less acceptable than shorter dependencies (Goodall 2021), which we operationalize as the Gap factor: a short-distance dependency involving only the matrix clause (13a/b) versus a long-distance dependency into the embedded clause (13c/d).

Sprouse and colleagues argue that observing an effect greater than the linear sum of each individual effect in the interaction condition (13d), which they call a super-additive effect, indicates the presence of a grammatical restriction specific to that condition. A super-additive effect can be observed as a significant statistical interaction and a diverging-lines pattern in an interaction plot (Figure 1).

Figure 1: Example interaction plots.

While this approach to operationalizing island effects has become standard in experimental syntax, recent work has raised questions about interpreting these effects.

Stigliano et al. (2025) found a statistical interaction without finding the expected acceptability decrease for each factor alone, sometimes called a ‘non-monotonic’ pattern. The logic of the factorial design assumes each factor degrades acceptability. However, sometimes one factor does not evince the expected effect, which requires researchers to look beyond statistical significance to the details of the interaction.

More broadly, exclusive reliance on statistical significance is widely acknowledged as problematic. Nearly any putative effect can be statistically significant with sufficient measurement precision and a large enough sample, which has led many methodological authorities within linguistics (e.g., Plonsky 2015) and beyond (e.g., Ferguson 2009) to urge greater emphasis on effect sizes. Yet the field of experimental syntax has reached no consensus regarding effect size interpretation (Sprouse & Villata 2021).

Third, acceptability judgments, as behavioral measures, are generally variable and gradient, yet there is similarly no consensus on the interpretation of this variation (see Francis 2022; Schütze & Sprouse 2013 for discussion).

In summary, the factorial design for islands is a powerful, widely used tool to detect island effects, but, like all experimental designs, the results require interpretation. We address these issues—with the dual aims of contributing to ongoing methodological discussions in the field and strengthening the interpretation of our results—as we interpret our experiment, examining the details of the super-additive effects we find, reporting effect sizes, and examining gradience and variation.

2.5 Research questions

Our research questions are: (i) do Spanish speakers display a contrast in island effects between subject positions when other factors are held constant as much as possible, and (ii) do island effects on judgments vary by individual working memory capacity?

3.1 Materials

3.2 Procedure

The pre- and post-verbal items were divided into separate surveys. Each participant thus only judged sentences with pre- or post-verbal subjects (a between-subjects design).

This decision was made primarily to avoid satiation effects. Satiation is a phenomenon in which unacceptable sentence types become more acceptable with repeated exposures (Snyder 2021). A meta-analysis of 21 studies on English found subject islands “reliably” exhibit satiation (Lu & Frank & Degen 2024: see especially Fig. 4), though Goodall (2011) did not find satiation with subject islands in Spanish. To avoid potential satiation effects, we chose to limit the experiment’s length and the number of sentences per cell of the design. Thus, within each survey, we created four lists, with tokens assigned via Latin square. Each list contained two tokens per cell, so participants judged eight target sentences (plus 16 fillers, for 24 total judgments).

This decision potentially reduces statistical power. Within-subjects comparisons have better power because individual participant-level variation is controlled. They increase reliability for the same reason. Fewer items per cell also could reduce reliability (Schoenmakers 2025). However, Likert-style numerical scales with the z-score transformation, as we employ here, have high reliability and good power in both within- and between-subjects contexts (see Langsford et al. 2018). Thus, we judged the tradeoff was worth it to avoid satiation and fatigue effects, and we conducted a power analysis (see §3.3) to ensure our samples would be large enough.

We examined the ratings of the fillers to verify that participants did not behave differently on the task overall by version (pre- or post-verbal); we observed no differences (Welch’s t = –1.56, p = .12). Although we believe both groups were drawn from the same population and we have no evidence for differences between the groups, we acknowledge that the between-subjects design could perhaps introduce some error due to characteristics of the samples that we did not measure.

Participants were recruited from Prolific and completed the experiment via PCIbex (Zehr & Schwarz 2018). Participants were randomly assigned to either the pre- or post-verbal subject condition, then to one of four lists. Token presentation order was pseudo-randomized such that two target items never appeared consecutively. Participants recorded judgments on a seven-point scale, with the ends labeled mal ‘(sounds) bad’ and bien ‘(sounds) good’ and intermediate values unlabeled.

3.3 Participants

We conducted a power analysis to determine the required sample size.¹⁴ We estimated groups of 40 would be sufficient to detect the relevant effects. To allow for participant exclusions, we recruited 60 people for each of the pre- and post-verbal conditions (120 total). Six participants had technical problems and did not complete the task. Of the remainder, 59 were sorted into the pre-verbal condition and 55 into post-verbal.

Participants were pre-screened on Prolific, and we subsequently checked background questionnaire responses to confirm all participants met inclusion criteria. We then examined the data for evidence of “non-cooperative” behavior, following Juzek and Häussler (2015).

First, randomly inserted among the items were three “instructional manipulation checks” (Prolific Team 2022), which verify participants’ attention by asking them to select a particular answer (e.g., “This is not a regular sentence; it is to verify attention. Please select 5.”). No participants were excluded for incorrectly answering two or more of these.

Second, we examined reaction times. Juzek (2016) recommends taking half the expected reading time for the shortest sentence in the experiment as the cutoff for inattentive behavior, calculating the expected reading time from the formula used by Bader and Häussler (2010) for a speeded judgment task. Under these assumptions (concretely, 225 milliseconds per word plus 25 milliseconds per character, plus 500 milliseconds to make a judgment), the shortest sentence in our experiment would take 3075 ms to read and judge (without reading the context), so we concluded that any judgment registered in less than 1500 ms was unlikely to have been made in good faith. To identify consistently inattentive participants, we chose to exclude anyone who made 20% of their judgments faster than our threshold and excluded one participant.

Third, we examined the fillers. Following Pañeda and Kush (2022), we excluded participants whose mean rating for ungrammatical fillers was at or above the scale midpoint, reasoning that participants who are unwilling to reject ungrammatical sentences do not provide useful data. Fifteen participants were excluded.¹⁵

Fourth, we identified three ungrammatical and two grammatical fillers, which previously received ratings at the ceiling or floor of the scale, to serve as “booby-trap items” (Juzek 2016) to verify attentiveness. Ten participants who ‘missed’ (rating grammatical items below 4 or ungrammatical items above 4) two or more of these items were excluded as inattentive.

After all planned exclusions, 87 participants remained in the sample. Of these, 43 judged items with pre-verbal subjects and 44 post-verbal subjects. Forty-three were female, 43 male, and one non-binary, with a mean age of 27.4 years (range: 21–47). No one reported cognitive or linguistic disabilities.

Participants all reported speaking a Mexican variety of Spanish and being born and living in Mexico. Most previous experiments on islands in Spanish have examined speakers of Peninsular Spanish. We chose Mexican Spanish to broaden the field’s empirical coverage to the country with the largest number of Spanish speakers. Although Mexico is home to a range of dialects, descriptions of syntactic variation in Mexican Spanish (e.g., Gutiérrez-Bravo 2020) give us no reason to expect variation with regard to islands, and restricting recruitment to one country allows for at least some level of uniformity. All acquired Spanish before age 5 in Mexico and were raised monolingually (without another home language in childhood), although they were not monolingual at the time of testing, as English is required to navigate Prolific.

3.4 Data analysis

We z-score transformed each sentence rating to control for scale-use variation and skew (Schütze & Sprouse 2013). We then examined by-item interaction plots and calculated influence statistics (Cook’s D) to identify whether any individual item contributed an outsize effect on the results; no items showed evidence of being outliers.

For the statistical analysis, most experimental syntax studies treat transformed judgment data as linear and use linear mixed-effects modeling to perform statistical tests. Yet some scholars contend that ordinal regression, which directly models the ordinal nature of rating data, should be preferred (Liddell & Kruschke 2018; Bürkner & Vuorre 2019). Following Kobzeva et al. (2022), we carried out both analyses, but, on the advice of an anonymous reviewer, we report only the linear model in the main text, since the results are the same and our power analysis assumed a linear model.

We conducted one test for pre-verbal position and one for post-verbal position, using lme4 (Bates et al. 2015) in R (v. 4.2.2; R Core Team 2022). For each, the fixed factors were Island (Yes/No), Gap (Matrix/Embedded), and the Island×Gap interaction. The interaction is always the fixed factor of interest. We also carried out an analysis with a three-way interaction among Subject Position (Pre/Post), Island, and Gap to determine if the effect was different by position. Because we carried out multiple tests, we adjusted the alpha level for each test using the Holm-Bonferroni procedure (Holm 1979) to control the familywise error rate. To explore significant interactions, we conducted post hoc pairwise comparisons using emmeans (Lenth & Piaskowski 2026), with the same adjustment for multiple comparisons.

We accounted for repeated measures by including random effects by participant and item. We used a top-down approach to find the maximal random effects structure (Barr et al. 2013), beginning with random intercepts and all random slopes, then removing the random slope accounting for the least variance and repeating this procedure as needed to achieve convergence.

In the text we present only key statistical results. The full output tables, including the random effects structures, estimates of fixed effects, and the ordinal regression analysis not reported here, are in a supplementary file available at https://osf.io/dq8mp.

As measures of effect size for each condition, we calculated difference-in-differences (DD) scores (Maxwell & Delaney 2004). Many methodological authorities urge increased emphasis on effect sizes in addition to (or instead of) null hypothesis significance testing (Cumming 2012; Lakens 2013; Plonsky 2015). The effect size measure to choose and its interpretation are field-specific (Plonsky & Oswald 2014; Larson-Hall & Plonsky 2015). DD scores are widely used in experimental syntax because they facilitate understanding the factorial design’s interaction and comparing with other studies, which is crucial for interpreting effect sizes (Larson-Hall & Plonsky 2015).¹⁶ We discuss effect sizes in detail in §5.2.

After conducting group-level analyses, we examined individual variation. First, we plotted the distribution of z-scores by condition as histograms and scatterplots (following Kush & Lohndal & Sprouse 2018; 2019; Pañeda & Kush 2022). Second, we calculated an individual DD score for each participant as a measure of sensitivity to the relevant island effect and carried out regression analyses with the lm function in R (R Core Team 2022) to determine the effect of working memory on island sensitivity by individual (as in Sprouse et al. 2012). The dependent variable was individual DD score, and the independent variable was mean-centered BDS score. We conducted each test twice: once for all participants and once with participants with negative DD scores removed, following Sprouse et al. (2012) and Pham et al. (2020). The rationale for conducting an analysis without negative DD scores is that no account predicts such ‘subadditive’ effects, and including them “might potentially mask the ability to observe a relationship between the individual difference measures and DD scores” (Pham et al. 2020: 8). We report both analyses and again adjusted alpha using the Holm-Bonferroni procedure to avoid inflated Type I error.¹⁷

5.1 Empirical contribution

We observe super-additive interactions suggesting island effects in both pre- and post-verbal position.

Yet we also observe a contrast: with all else held equal as much as possible, the effect for pre-verbal subjects is much larger than for post-verbal subjects. Additionally, post hoc tests reveal a significantly lower violation condition, versus other conditions, only pre-verbally. This violation condition also displays the largest variation in scores, including the fewest individuals consistently accepting it and the most consistent rejectors. We take the sum of the evidence to suggest the island violation in pre-verbal position is degraded.

For post-verbal subjects, the effect is statistically significant but small. The violation condition does not present clear evidence of a decrease in acceptability compared to control conditions. Instead, the statistically significant effect is likely driven by the increased acceptability of the non-island embedded condition. Scores cluster at the high end for the violation condition, which most participants consistently accepted, and its mean score is above the scale midpoint. We take the sum of the evidence to suggest the post-verbal island violation is not degraded. Instead, the statistically significant effect is attributable to other factors.

Finally, we observe no effect of working memory in either position.

Overall, our results support the claim that pre-verbal subjects in Spanish provoke island effects while post-verbal do not. As discussed in §2.2, experimental corroboration of this claim was necessary given that previous experiments have found divergence from informal judgments, and no previous experiments had tested subject position in Spanish. Our results also support Stepanov’s generalization linking post-verbal position and lack of island effects.

5.2 Interpreting experimental evidence

Interpreting our results requires engaging with debates about data interpretation in experimental syntax. In this section, we discuss how we interpreted our results and the implications of these moves for questions raised in §2.4.

5.2.2 Effect sizes

As in other social and behavioral sciences (see Ferguson 2009), interpretation of effect sizes is a major unresolved question in experimental syntax (Sprouse & Villata 2021), and clear benchmarks are lacking. As with non-monotonic effects, the most common approach is to focus primarily on statistical significance, not effect size. For example, Kim and Goodall interpret DD = 0.28 as “a very clear wh-island effect” (Kim & Goodall 2016: 5). Kush et al. (2019: 401) exemplify an alternative position: “Although there is, in principle, no quantitative threshold for defining a ‘true’ island effect, … DD scores for island effects typically fall within the range of 0.75–1.25 … [so,] any intermediate-sized island effect bears closer scrutiny.” Kush and colleagues argue not for a simple cutoff point but rather careful examination of smaller effects to understand what they represent.

Meaningful interpretation of effect sizes includes comparing to similar previous studies (Larson-Hall & Plonsky 2015). To facilitate such interpretation, we compare our results to previous subject island experiments in Table 4, which is modeled on Sprouse and Villata (2021: Table 10.2) and includes all studies for which we could obtain or calculate DD scores. Other experimental studies that include subject islands but use a method (e.g., Matchin et al. 2024) or design (e.g., Chaves & King 2019) not permitting the calculation of effect sizes the same way are not included. Three studies reporting DD scores but on a different scale (e.g., raw ratings rather than z-scores) are included for completeness, although they are less directly comparable.

Table 4: Experimental studies of subject islands by language, dependency, and effect size.¹⁹

Study	Language	Dependency	Effect size	Scale
Present study: Pre-verbal Present study: Post-verbal	Spanish Spanish	Complex wh Complex wh	1.1 0.4	z-score z-score
Abeillé et al. 2020: Exp. 1	English	Relative clause	–0.3	z-score
Abeillé et al. 2020: Exp. 2	English	Relative clause, pied-piping	0.0 (n.s.)	z-score
Abeillé et al. 2020: Exp. 2	English	Relative clause, p-stranding	0.6	z-score
Abeillé et al. 2020: Exp. 3	English	Complex wh, pied-piping	0.4	z-score
Abeillé et al. 2020: Exp. 3	English	Complex wh, p-stranding	1.2	z-score
Abeillé et al. 2020: Exp. 4	French	Relative clause	0.0 (n.s.)	z-score
Abeillé et al. 2020: Exp. 5	French	Complex wh	0.7	z-score
Aldosari 2015	English	Complex wh	1.6	z-score
Cartner et al. 2026: Exp. 1	English	Complex wh	0.8	z-score
Cartner et al. 2026: Exp. 2	English	Relative clause	0.5	z-score
Cartner et al. 2026: Exp. 3	English	Topicalization	0.3	z-score
Kush et al. 2018	Norwegian	Bare wh	1.4	z-score
Kush et al. 2018	Norwegian	Complex wh	1.4	z-score
Kush et al. 2019	Norwegian	Topicalization	1.7	z-score
López-Sancio 2015	Spanish	Bare & Complex wh	0.8	z-score
López-Sancio 2015	Spanish	Relative clause	0.4 (n.s.)	z-score
Omaki et al. 2020	Japanese	Scrambling	0.1 (n.s.)	z-score
Schoenmakers & Stoica 2024	Romanian	Bare wh	0.4	z-score
Sprouse et al. 2011	English	Bare wh	1.5	z-score
Sprouse et al. 2011	Japanese	Wh in situ	0.2 (n.s.)	z-score
Sprouse et al. 2012: Exp. 1	English	Bare wh	0.8	z-score
Sprouse et al. 2012: Exp. 2	English	Bare wh	1.3	z-score
Sprouse et al. 2016	English	Bare wh	0.6	z-score
Sprouse et al. 2016	English	Complex wh	0.5	z-score
Sprouse et al. 2016	English	Relative clause	0.5	z-score
Sprouse et al. 2016	Italian	Bare wh	1.4	z-score
Sprouse et al. 2016	Italian	Relative clause	–0.1 (n.s.)	z-score
Stepanov et al. 2018	Slovenian	Bare wh	0.6	z-score
Pañeda et al. 2020	Spanish	Bare wh	–6.0	log odds
Pham et al. 2020	English	Complex wh	3.9	raw (7-pt)
Stigliano et al. 2025: SOD18	Spanish	Complex wh	2.1	raw (7-pt)
Stigliano et al. 2025: SCSD	Spanish	Complex wh	2.2	raw (7-pt)

Our pre-verbal extraction effect size (DD = 1.05) is similar to others found for subject islands in English (Sprouse et al. 2011: bare wh; 2012: Exp. 2; Aldosari 2015), Italian (Sprouse et al. 2016), and Norwegian (Kush et al. 2018; 2019), and larger than López-Sancio’s (2015) Spanish wh-questions. In general, the pre-verbal extraction effect is comparable to subject island effects found cross-linguistically. In contrast, our post-verbal extraction effect size (DD = 0.43) is among the smallest of any significant interaction.

We visualize the distribution of effect sizes in Figure 6.

Figure 6: Subject island effect sizes by language.

Although there is no simple cutoff for a meaningful effect size, comparing our effects with those of previous experiments suggests a difference by position.

5.3 Source of island effects

5.4 Limitations and future research

The present study has several limitations.

We chose a between-subjects design rather than a within-subjects design to reduce the probability of satiation effects, yet this choice might have reduced statistical power or introduced sampling error. A future within-subjects study could serve to corroborate our findings. Additionally, a future study including more items would be useful (see Schoenmakers 2025), especially if it explicitly tested satiation.

Our pre- and post-verbal sentences were not perfect minimal pairs, despite our attempt to make them as similar as possible. We introduced two differences between them—the [±change-of-state] context and the verbal aspect to reinforce that reading—with the purpose of making the pre- or post-verbal subject as independently natural as possible, in its canonical and default position. We cannot exclude the possibility that this manipulation produced confounds. In particular, we cannot eliminate the possibility of a pragmatic or semantic difference between the positions despite the contexts.

Although we used a working memory task designed to address criticisms of some previous tasks, it remains possible this task is too simple to measure working memory as it pertains to sentence processing.

Another potential source of limitations is uncontrolled variation in the experiment design. As previously noted, it is possible that certain verbs were perceived as pragmatically odd, that participants applied a reading other than the intended one to some items (see Schütze 2020), or that there is some other factor (like sentence length) we did not control.

We have also highlighted several areas in which future research could help refine experimental syntax methods. More work is needed to establish field-specific guidelines on characterizing and understanding individual variation, as well as interpreting effect sizes and non-monotonic judgment patterns.