ABSTRACT
Title of dissertation: THE ROLE OF STRUCTURAL
INFORMATION IN THE RESOLUTION
OF LONG-DISTANCE DEPENDENCIES
Anton Malko
Doctor of Philosophy, 2019
Dissertation directed by: Professor Colin Phillips
Department of Linguistics
The main question that this thesis addresses is: in what way does structural
information enter into the processing of long-distance dependencies? Does it con-
strain the computations, and if so, to what degree? Available experimental evidence
suggests that sometimes structurally illicit but otherwise suitable constituents are
accessed during dependency resolution. Subject-verb agreement is a prime example
(Wagers et al., 2009; Dillon et al., 2013), and similar effects were reported for neg-
ative polarity items (NPIs) licensing (Vasishth et al., 2008) and reflexive pronouns
resolution (Parker and Phillips, 2017; Sloggett, 2017). Prima facie this evidence
suggests that structural information fails to perfectly constrain real-time language
processing to be in line with grammatical constraints. This conclusion would fall
neatly in line with an assumption that human sentence processing relies on cue-
based memory (e.g McElree et al., 2003; Lewis and Vasishth, 2005; Van Dyke and
Johns, 2012; Wagers et al., 2009, a.m.o.), the key property of which is the fragility of
memory search, which can return irrelevant results if they look similar enough to the
relevant ones. The attractiveness of such an approach lies in its parsimony: there is
independent evidence that general purpose working memory is cue-based (Jonides
et al., 2008), so we do not need to postulate any language specific mechanisms. Ad-
ditionally, the processing of multiple linguistic dependencies can be analyzed within
the same theoretical framework.
Cue-based approach has also been argued to be the best one in terms of its
empirical coverage: some of the experimental evidence was assumed to only be ex-
plainable within it (the absence of ungrammaticality illusions in subject-verb agree-
ment is the main example, to which we will return in more detail later). However,
recently several other approaches have been suggested which would be able to ac-
count for these cases (Eberhard et al., 2005; Xiang et al., 2013; Sloggett, 2017; Ham-
merly et al., draft.april.2018). These approaches usually assume separate processing
mechanisms for different linguistic dependencies, and thus lose the parsimonious at-
tractiveness of cue-based memory models. They also take a different stance on the
role of structural information in real-time language processing, assuming that struc-
tural cues do accurately guide the dependency resolution. A priori there is no reason
why they could not turn out to be true. But given the theoretical attractiveness
of cue-based models in which structural information does not categorically restrain
processing, it is important to critically evaluate these recent claims. In this the-
sis, we focus on reflexive pronouns and on the novel pattern reported in Parker and
Phillips (2017) and Sloggett (2017): the finding that reflexive pronouns are sensitive
to the properties of structurally inaccessible antecedents in some specific conditions
(interference effect). The two works report consistent findings, but the accounts
they give take opposite perspectives on the role of structural information in reflex-
ive resolution. Our aim in this thesis is to assess the reliability of these findings and
to experimentally investigate cases which would hopefully provide clearer evidence
on how the structure guides reflexives processing.
To this aim, we conduct two direct replications of Parker and Phillips (2017)
and four novel experiments further investigating the properties of the interference
effect. None of the six experiments provided strong statistical support for the pre-
vious findings. After ruling out several possible confounds and analyzing numerical
patterns (which go in the expected direction and are consistent with previous re-
sults), we conclude that interference effect is likely real, but may be less strong than
the previous studies would lead to believe. These results can be used for setting
more realistic expectations for future studies regarding the size of the effect and sta-
tistical power necessary to detect it. With respect to our main goal of distinguishing
between cue-based and alternative accounts of the interference effect, we tentatively
conclude that cue-based approaches are preferred; however, one has to assume that
some structural features are able to categorically rule out illicit antecedents. Further
highly powered studies are necessary to verify and confirm these conclusions.
The role of structural information in the resolution of long-distance
dependencies
by
Anton Malko
Dissertation submitted to the Faculty of the Graduate School of the
University of Maryland, College Park in partial fulfillment
of the requirements for the degree of
Doctor of Philosophy
2019
Advisory Committee:
Professor Colin Phillips, Chair
Assistant Professor Ellen Lau
Professor Jeffrey Lidz
Associate Professor Omer Preminger
Associate Professor Robert Slevc
©c Copyright by
Anton Malko
2019

Acknowledgments
I have finally reached the stage of writing this part of my dissertation. The
path to this point has been long and not always straightforward, and I would like
to express my gratitude to people who supported me during the process and who
made this journey even remotely possible (the list is far from being exhaustive, of
course!).
My greatest thank you goes to my advisor, Colin Phillips. Colin patiently
guided me through my sometimes confused thoughts and continuously pushed me
to re-think my assumptions, to shape my ideas better and to communicate them
extremely clearly - all of this without explicitly holding my hand and giving me
enough room for trying things out on my own. Without Colin’s guidance and
support this thesis would truly have been impossible, and I owe him my deepest
gratitude.
I greatly enjoyed our discussions and conversations with Ellen Lau. She was
always able to provide encouraging advice and also point out to me some unexpected
connections between my ideas and existing research. Ellen somehow always managed
to make things brighter and clearer than what they had appeared to me - it was
such a comforting and stimulating experience.
The research I discuss in this thesis would have been much harder without
the logistical support I received. First, I would like to thank those who helped by
providing native speaker judgments, helping to prepare experimental stimuli and
collecting the data: Julia Buffinton, Hanna Muller, Maggie Kandel, Lalitha Bal-
ii
achandran, Cassidy Wyatt. I express my gratitude to all of them. Thank you also
to Kim Kwok, who has been tremendously helpful and supportive in all the adminis-
trative questions, especially considering enormous amounts of work she was (and is!)
doing. Finally, I want to acknowledge the financial support I received from the De-
partment of Linguistics, Language Science Center and NSF (the research reported
in this thesis is based upon work supported by the National Science Foundation
under Grant No.1449815).
Thank you to the people who sparked and supported my interest in statistics
and modeling. To Michael Dougherty and Kevin O’Grady for teaching my first
ever statistic courses in a fun way and making me excited about them - I don’t
think I would have been able to write a lot of this thesis (especially Chapter 4!)
without the foundations they gave to me. To Naomi Feldman, who introduced
me to computational psycholinguistics, and to Philip Resnik for his exciting and
extremely lucid discussion of the NLP ideas in the computational linguistics class.
If I am now interested in computational modeling and am not afraid of MCMC
methods, it is because of Naomi and Philip. Also thank you to my fellow grad
students, Phoebe Gaston, Hanna Muller and Adam Liter for sharing my interest
in statistics, for frequent related discussions we had and for the little quest for
understanding the Bayesian approaches we pursued together.
I would have never learned and known the things above if I had not come to
Maryland, and I would like to express my gratitude to several people who made this
possible. First and foremost, to Natalia Slioussar, who I was very lucky to have as my
Master’s thesis advisor. My PhD dissertation would not have been even considered
iii
if I have not met her in my MA years. Natalia introduced me to (psycho)linguistics
in general, being very generous with her time and advice. The current thesis would
have probably been very different, if not for our work on agreement attraction in
Russian, which has quite directly connected me to the topics I consider here. It
was also her who greatly influenced my decision to come to Maryland. I am deeply
grateful for all the guidance, support and advice Natalia gave me in the years I
have known her. People from NYI 2012 in Saint-Petersburg have shaped my idea
of coming to a graduate school abroad at all - most prominently, Sabine Iatridou.
And thank you to Nikos Angelopoulos and Christine Boucher for supporting me in
this idea and for the great fun we had together in Saint-Petersburg.
My gratitudes list would be incomplete without mentioning my friends from
inside and outside of the department, who added a lot of fun and enjoyment to the
graduate school experience. Thank you to the Hyattsville gang - Allyson Ettinger,
Lara Ehrenhofer, Kasia Hitczenko, Phoebe Gaston, Christian Brodbeck, Paulina
Lyskawa, Miloš Nikolić, Suddhasattwa Das, Amit Nag - for all the great experiences
we had, including, to name just a few, conversations about everything and anything,
kayaking, movie nights, Easter Eggs hunt, playing Settlers of Catan, and several
kidnappings. I remember these fondly. Ilia Kurenkov and Natalia Lapinskaya were
among the very first people I met having come to Maryland and they remained
good friends throughout my time here. Thanks to them I have not forgotten my
Russian completely! Ilia was also the person who introduced me to LATEXand git,
and thus indirectly contributed to the creation of this document. Thank you to Sol
Lago, Shota Momma, William Matchin, Eric Pelzl, Nick Huang for having many
iv
invariably enjoyable conversations throughout these years.
I cannot even start expressing my gratitude towards Lena. I would have hardly
survived the final stages of writing without her continuous support; but so much
more would have been impossible without her. Thank you for all the lessons you
taught me and the love and joy you shared with me.
Finally, thank you to my family for giving me the foundations which allowed
me to make it this far, and for supporting me and believing in me all the way
through.
v
Table of Contents
Acknowledgements ii
List of Tables ix
List of Figures x
1 Introduction 1
1.1 Empirical evidence . . . . . . . . . . . . . . . . . . . . . . . . . . . . 3
1.2 Evidence interpretation . . . . . . . . . . . . . . . . . . . . . . . . . . 16
1.2.1 Accounts of lure-match effects . . . . . . . . . . . . . . . . . . 16
1.2.2 Choosing an account . . . . . . . . . . . . . . . . . . . . . . . 21
1.2.3 Evidence interpretation: summary . . . . . . . . . . . . . . . . 28
1.3 Lewis & Vasishth (2005) memory model . . . . . . . . . . . . . . . . 29
1.3.1 Explaining RT patterns . . . . . . . . . . . . . . . . . . . . . 33
1.4 Recent arguments against structure-defeasible models . . . . . . . . . 37
1.4.1 LV05 model fit to agreement data is worse than usually thought 37
1.4.2 Reflexives processing is qualitatively different from agreement 48
1.5 Parker & Phillips (2017) vs. Sloggett (2017) . . . . . . . . . . . . . . 55
1.5.1 Empirical observations . . . . . . . . . . . . . . . . . . . . . . 55
1.5.1.1 PP2017 . . . . . . . . . . . . . . . . . . . . . . . . . 57
1.5.1.2 S2017 . . . . . . . . . . . . . . . . . . . . . . . . . . 63
1.5.2 Empirical coverage: summary . . . . . . . . . . . . . . . . . . 66
1.5.3 My experiments . . . . . . . . . . . . . . . . . . . . . . . . . . 66
2 Interference effects from non-c-commanding lures 69
2.1 Experiment 1 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 75
2.1.1 Participants . . . . . . . . . . . . . . . . . . . . . . . . . . . . 75
2.1.2 Materials . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 75
2.1.3 Procedure . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 78
2.1.4 Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 79
2.1.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 82
2.1.6 Exploratory analysis . . . . . . . . . . . . . . . . . . . . . . . 86
2.1.7 Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 89
vi
3 Interference effects with quantificational lures 96
3.1 Representing c-command in cue-based models . . . . . . . . . . . . . 99
3.2 Outline of the experiments . . . . . . . . . . . . . . . . . . . . . . . . 106
3.3 Experiment 2 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 110
3.3.1 Participants . . . . . . . . . . . . . . . . . . . . . . . . . . . . 111
3.3.2 Materials . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 111
3.3.3 Procedure . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 115
3.3.4 Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 116
3.3.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 116
3.3.6 Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 118
3.4 Experiment 3 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 124
3.4.1 Participants . . . . . . . . . . . . . . . . . . . . . . . . . . . . 124
3.4.2 Materials . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 124
3.4.3 Procedure . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 126
3.4.4 Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 126
3.4.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128
3.4.6 Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 129
3.5 Experiment 4 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 132
3.5.1 Participants . . . . . . . . . . . . . . . . . . . . . . . . . . . . 132
3.5.2 Materials . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 132
3.5.3 Procedure . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 134
3.5.4 Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 134
3.5.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 135
3.5.6 Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 136
3.6 General discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . 139
4 Replicability of lure-match effects in reflexive resolution 148
4.1 Experiment 5 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 150
4.1.1 Participants . . . . . . . . . . . . . . . . . . . . . . . . . . . . 151
4.1.2 Materials . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 151
4.1.3 Procedure . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 151
4.1.4 Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 152
4.1.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 154
4.1.6 Sensitivity analysis . . . . . . . . . . . . . . . . . . . . . . . . 166
4.1.6.1 Qualitative analysis . . . . . . . . . . . . . . . . . . 167
4.1.6.2 Quantitative analysis . . . . . . . . . . . . . . . . . . 168
4.1.7 Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 175
4.2 Experiment 6 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 176
4.2.1 Participants . . . . . . . . . . . . . . . . . . . . . . . . . . . . 176
4.2.2 Materials . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 177
4.2.3 Procedure . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 177
4.2.4 Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 177
4.2.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 177
4.2.6 Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 181
4.3 Interference magnitude across studies . . . . . . . . . . . . . . . . . . 182
vii
4.4 Pooled data analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . 185
4.5 General discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . 187
5 Conclusions 204
5.1 Choosing between PP2017 and S2017 . . . . . . . . . . . . . . . . . . 207
5.1.1 On sub-command binding . . . . . . . . . . . . . . . . . . . . 207
5.1.2 On the role of c-command . . . . . . . . . . . . . . . . . . . . 208
5.1.3 On the reliability of lure-match effect . . . . . . . . . . . . . . 210
5.1.3.1 Magnitude of the effect . . . . . . . . . . . . . . . . 210
5.1.3.2 Timing of the effect . . . . . . . . . . . . . . . . . . 214
5.1.4 Choosing between the two accounts . . . . . . . . . . . . . . . 217
5.2 Future directions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 222
5.3 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 226
Appendix A Mean reaction times in PP2017and replication (PP2017analysis) 229
Appendix B Mean RTs 234
Appendix C Model coefficients 238
Appendix D List of changes to the Parker and Phillips (2017) stimuli in the
replication experiment 243
Appendix E Appendix: Experiment 2 fillers types 245
Bibliography 254
viii
List of Tables
2.1 Experiment 1 materials example . . . . . . . . . . . . . . . . . . . . . 78
2.2 Order of random effect structure simplification in Exp.1. . . . . . . . 82
3.1 Experiment 2 materials example . . . . . . . . . . . . . . . . . . . . . 114
3.2 Experiment 3 materials example . . . . . . . . . . . . . . . . . . . . . 128
3.3 Experiment 4 materials example . . . . . . . . . . . . . . . . . . . . . 133
4.1 Experiment 5materials example . . . . . . . . . . . . . . . . . . . . . 152
4.2 Order of random effect structure simplification, Exp.5. Effects were
removed from the model, starting from the top. . . . . . . . . . . . . 154
A.1 Mean RTs in PP2017 . . . . . . . . . . . . . . . . . . . . . . . . . . . 231
A.2 Mean RTs in the replication of PP2017 . . . . . . . . . . . . . . . . . 233
B.1 Experiment 2 means for agreement stimuli. . . . . . . . . . . . . . . . 234
B.2 Experiment 2 means for reflexives stimuli. . . . . . . . . . . . . . . . 235
B.3 Experiment 3 means for agreement stimuli. . . . . . . . . . . . . . . . 235
B.4 Experiment 3 means for reflexives stimuli. . . . . . . . . . . . . . . . 236
B.5 Experiment 4 mean reaction times. . . . . . . . . . . . . . . . . . . . 237
C.1 Model coefficients for Experiment 1. . . . . . . . . . . . . . . . . . . . 239
C.2 Model coefficients for Experiment 2. . . . . . . . . . . . . . . . . . . . 240
C.3 Model coefficients for Experiment 3. . . . . . . . . . . . . . . . . . . . 241
C.4 Model coefficients for Experiment 4. . . . . . . . . . . . . . . . . . . . 242
E.2 Experiment 2 stimuli types and counts. . . . . . . . . . . . . . . . . . 247
ix
List of Figures
2.1 Experiment 1. RT means for agreement sentences. . . . . . . . . . . . 84
2.2 Experiment 1. RT means for reflexive sentences. . . . . . . . . . . . . 84
2.3 Sensitivity analysis: Model coefficients in Exp.1 . . . . . . . . . . . . 88
2.4 Experiment 1. Comparisons of the interference effect magnitudes in
reflexive conditions with Parker and Phillips (2017). . . . . . . . . . . 93
3.1 Experiment 2. RT means for agreement sentences. . . . . . . . . . . . 117
3.2 Experiment 2. RT means for reflexive sentences. . . . . . . . . . . . . 117
3.3 Experiment 2. Comparisons of the interference effect magnitudes in
reflexive conditions with Parker and Phillips (2017). . . . . . . . . . . 121
3.4 Experiment 2. Comparisons of the interference effect magnitudes in
reflexive conditions with Parker and Phillips (2017). . . . . . . . . . . 122
3.5 Experiment 3. RT means for agreement sentences. . . . . . . . . . . . 127
3.6 Experiment 3. RT means for reflexive sentences. . . . . . . . . . . . . 127
3.7 Experiment 3. Comparisons of the interference effect magnitudes in
reflexive conditions with Parker and Phillips (2017). . . . . . . . . . . 131
3.8 Experiment 4. RT means for agreement sentences. . . . . . . . . . . . 147
3.9 Experiment 4. Comparisons of the interference effect magnitudes in
2-feature target mismatch conditions with PP2017and S2017. . . . . . 147
4.1 Mean RTs in PP2017 (red) and my replication (blue). . . . . . . . . . 155
4.2 Interference effect in target: two mismatch conditions (lure match
- lure mismatch) in PP2017(red) and my replication (blue). . . . . . . 157
4.3 Model estimates in PP2017 (red) and my replication (blue). . . . . . 159
4.4 Predicted and observed RT values for PP2017 and my replication. . . 191
4.5 Sensitivity analysis: Intrusion effect (lure mismatch minus lure match
) in 2-feature target mismatch conditions. . . . . . . . . . . . . . . . 192
4.6 Sensitivity analysis: Model coefficients in PP2017 Exp.3 and replication.193
4.7 Mean RTs in PP2017 (red), my previous replication (blue) and my
current replication (green). . . . . . . . . . . . . . . . . . . . . . . . . 194
4.8 Interference effect in target: two mismatch conditions (lure match
- lure mismatch) in PP2017 (red), my previous replication (blue) and
my current replication (green). . . . . . . . . . . . . . . . . . . . . . . 195
x
4.9 Model estimates in PP2017 (red) and my replication (blue). . . . . . 196
4.10 Mean RTs in PP2017(red), my previous replication (blue) and my
current replication (green). . . . . . . . . . . . . . . . . . . . . . . . . 197
4.11 Interference effect in target: two mismatch conditions (lure match
- lure mismatch) in PP2017 (red), my previous replication (blue) and
my current replication (green). . . . . . . . . . . . . . . . . . . . . . . 198
4.12 Model estimates in PP2017 (red) and my replication (blue). Ex-
ploratory analysis: removing missing values instead of replacing them
with zeros. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 199
4.13 Intrusion effect in five studies with most similar design (PP2017
Exp.3, its two replications (this thesis Exp. 5 and 6), S2017 Exp.1c,
this thesis Exp.4). . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 200
4.14 Intrusion effect in all studies investigating 2-feature target mismatch
configurations (PP2017, S2017, the current study). . . . . . . . . . . 201
4.15 Distribution of lure-match effect sizes in 2-feature target mismatch
conditions obtained in a bootstrapping simulation. . . . . . . . . . . . 202
4.16 Model estimates for the models fit to the pooled data from Exp.5 and
6. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 203
xi
Chapter 1: Introduction
The main question that this thesis addresses is: in what way does structural
information enter into the processing of long-distance dependencies? Does it con-
strain the computations, and if so, to what degree? Available experimental evidence
suggests that sometimes structurally illicit but otherwise suitable constituents are
accessed during dependency resolution. Subject-verb agreement is a prime example
(Wagers et al., 2009; Dillon et al., 2013), and similar effects were reported for neg-
ative polarity items (NPIs) licensing (Vasishth et al., 2008) and reflexive pronouns
resolution (Parker and Phillips, 2017; Sloggett, 2017). Prima facie this evidence
suggests that structural information fails to perfectly constrain real-time language
processing to be in line with grammatical constraints. This conclusion would fall
neatly in line with an assumption that human sentence processing relies on cue-
based memory (e.g. McElree et al., 2003; Lewis and Vasishth, 2005; Van Dyke and
Johns, 2012; Wagers et al., 2009, among many others), which has similarity-based
interference as a key property. The attractiveness of such an approach lies in its
parsimony: there is independent evidence that general purpose working memory is
cue-based (Jonides et al., 2008), so we do not need to postulate any language specific
mechanisms. Additionally, the processing of multiple linguistic dependencies can be
1
analyzed within the same theoretical framework.
Empirically, some of the experimental evidence was assumed to only be ex-
plainable within cue-based approach (the absence of ungrammaticality illusions in
subject-verb agreement is the main example, to which I will return in more detail
later). However, recently several other approaches have been suggested which would
be able to account for these cases, even if we assume that structural information
accurately guides the parsing (Eberhard et al., 2005; Hammerly et al., 2018; Xiang
et al., 2013; Sloggett, 2017). These approaches usually assume separate mechanisms
for different linguistic dependencies, and thus lose the parsimonious attractiveness
of cue-based memory models. A priori there is no reason why they could not turn
out to be true. But given the theoretical attractiveness of cue-based models in which
structural information does not categorically restrain processing, it is important to
critically evaluate these recent claims. In this thesis, I focus on reflexive pronouns
and on the novel pattern reported in Parker and Phillips (2017) and Sloggett (2017).
The two works report consistent findings, but the accounts they give take opposite
perspectives on the role of structural information in reflexive resolution. Our aim in
this thesis is to experimentally investigate cases which could provide clearer evidence
on how structure guides reflexives processing. The rest of this chapter is structured
as follows. First, I survey available experimental evidence in subject-verb agreement
and reflexive resolution. Then, I describe a prominent cue-based model used to ac-
count for these data and show how it can explain them. As we will see, adopting
this explanation for the data will make us assume that structural information is not
able to categorically rule out illicit dependency formation. I proceed to discuss the
2
recent alternative approaches which assume that structure restricts the processing
to be compliant with the grammar. Finally, I describe the cases which would dis-
tinguish between the two classes of approaches and outline the experiments I carry
out to investigate these cases.
1.1 Empirical evidence
In this section I discuss the evidence for grammatically illicit constituents being
considered during real-time processing. I start the discussion with the most popular
experimental paradigm used in this line of research, and then I turn to empirical
data on subject-verb agreement, NPI licensing and reflexive resolution.
Feature-mismatch paradigm is very widely used in the investigations of long-
distance dependencies formation. It is based on the observation that people quickly
notice if feature composition of the two dependency elements does not match (for
instance, the subject is singular and the verb is plural) (e.g Osterhout and Mobley,
1995; Osterhout et al., 1997). We can use this reaction to assess whether feature
mismatch with a grammatically inaccessible, but otherwise plausible, dependency
component elicits similar complications. Thus, the paradigm is usually structured as
follows. People are presented with sentences containing the dependency of interest
and two possible ways to resolve it - one grammatically licensed and the other
one not. For example, people may be presented with a sentence like “The key
to the cabinet is rusty”. This sentence contains two NPs, both of which could
in principle control verbal agreement, but only one of them - “the key” - is in
3
the correct structural position to do so, i.e. is a grammatically licensed agreement
controller. In what follows, I will call the grammatically licit option “target”, and the
grammatically illicit - “lure”. The features of the target and the lure are factorially
manipulated, so that they either match or mismatch the other dependency element.
In the example above, the number of both NPs could be manipulated so that they
match or mismatch the number of the verb. We do expect to observe some indication
of processing difficulty in target mismatch conditions as compared to target match.
But of critical interest is whether we observe any reaction to feature mismatch with
the lure. If we do, we can conclude that at some point in time feature information
on the lure had entered the processing system in a way in which it was able to affect
dependency resolution process. In what follows, I will refer to any lure-related
effects as “lure-match effects” or “interference”. I will talk about “facilitation”
(“facilitatory interference”), if the lure-match conditions are read faster than lure-
mismatch conditions, and about “inhibition” (“inhibitory interference”) otherwise.
It is important to keep in mind that the interpretation of the results obtained
with this paradigm is not always straightforward. Its goal is to assess whether the
presence of the lure affects processing in any measurable way: it may be differences
in interpretations, reaction times, electrophysiological responses. . . However, just
the fact that a certain constituent affects processing does not mean that it is actively
accessed by the parser; the differences we observe may well stem from other sources.
Therefore, additional steps must be made in order to ensure that the evidence
we obtain is indeed the evidence about access mechanisms. I will return to this
discussion after we have surveyed available experimental evidence.
4
Subject-verb agreement Subject-verb agreement presents a prime example of
a dependency for which lure-match effects are observed: people tend to mis-identify
the agreement controller in sentences like (1b) - (1a), a phenomenon known as
“agreement attraction”. Both of the sentences are ungrammatical, since the head
of the subject noun phrase (“key”) mismatches the verb in number. However, this
violation is perceived as milder in the second sentence. This effect is apparent in
acceptability judgments and reaction time (RT) profile (with (1b) eliciting higher
ratings and faster RTs than (1a)) (Wagers et al., 2009; Dillon et al., 2013; Ham-
merly et al., 2018), as well as in electrophysiological measures (Xiang et al., 2013;
Tanner et al.). I will refer to this effect as “grammaticality illusion”: an ungram-
matical sentence may have been fleetingly considered grammatical by the readers.
Grammaticality illusions have been observed in a number of languages and with
multiple grammatical features (e.g., see Lago et al. (2015) for Spanish, Tucker et al.
(submitted) for Arabic and Slioussar and Malko (2016) for Russian).
(1) a. *The key to the cabinet are on the table.
b. *The key to the cabinets are on the table.
c. The key to the cabinets is on the table.
d. The key to the cabinet is on the table.
While the presence of lure-match effect in ungrammatical sentences is uncontrover-
sial, the patterns arising in grammatical sentences are less clear. There are three
logical possibilities ((1c) is exactly as difficult as (1d); (1c) is easier than (1d); (1c)
5
is harder than (1d)). Each possibility would support a different class of models, as
I will discuss in section 1.2.2.
The first possibility - that the processing difficulty of grammatical sentences
does not depend on the number-marking of the lure - is commonly assumed to be
an actuality, based on a number of studies (e.g. Wagers et al., 2009; Dillon et al.,
2013; Tanner et al.). This pattern is known as the “absence of ungrammaticality
illusions” (i.e. there are no cases when people perceive grammatical sentences as
degraded). However, this observation may be overly general. Two recent meta-
analytic reviews suggest that the literature contains a fair amount of evidence for
people being faster in (1c) as compared to (1d). Jäger et al. (2017) review reaction
time (self-paced, eye-tracking) and electrophysiological studies and find that 12 out
of 25 report statistically significant effects in this direction (12 studies report no sig-
nificant effects and one reports the opposite pattern)1. These qualitative conclusions
are supported by quantitative Bayesian meta-analysis of reaction time data: it esti-
mates the speed-up in (1c) to be of 6.6ms with the 95% of the posterior probability
mass in the interval [-16.2, 3.7] (91% of the probability mass below 0)2. Hammerly
et al. (draft.april.2018) reach similar conclusions in an informal review of the liter-
ature with somewhat less detailed comparison. They review a partially overlapping
subset of reaction time studies of agreement attraction; in addition, they also look
1I only report the data for configurations with singular subjects, since there is almost no data
for configurations with plural subjects.
2One has to keep in mind that for eye-tracking, only first-pass reading times were entered into
the analysis.
6
at interpretation studies. Out of 26 tested instances of agreement attraction config-
urations3, in 11 cases the authors reported significant effects in both grammatical
and ungrammatical sentences. This evidence will be of crucial importance when we
choose between possible accounts of agreement attraction in section 1.2.2.
NPIs Negative Polarity Items (NPIs) licensing is another dependency whose for-
mation is arguably prone to interference (Vasishth et al., 2008; Xiang et al., 2008;
Parker and Phillips, 2016). NPIs are items like “any”, “ever”, “lift a finger” and
others which can only occur in a special linguistic environment. The exact nature
of the environment is still debated , but one generalization is that NPIs have to
occur in a scope of a downward entailing element, e.g. negation. It is possible to
conceptualize this relation as an item-to-item dependency4: when people encounter
an NPI, they look for a downward entailing element in structurally higher position,
and if they find it, the NPI is licensed. Interestingly for our purposes, sentences with
an NPI licensor in an inappropriate structural position (2c) are perceived as better
than sentences without a licensor altogether (2b) (Vasishth et al., 2008; Parker and
Phillips, 2016).
(2) a. No diplomats have ever supported a drone strike.
3Most of them correspond to whole studies, but in a few cases, Hammerly et al. (draft.april.2018)
count subsets of stimuli in the same study separately.
4Although this conceptualization is contested, and as we will see in the discussion of the evi-
dence, this is the reason why NPI data does not provide strong evidence for or against the use of
structural information
7
b. *The diplomats have ever supported a drone strike.
c. *The diplomats that no congressman could trust have ever supported a
drone strike.
Reflexive pronouns I now turn to the evidence which will be most relevant for
my thesis - influence of structurally inappropriate antecedents on the resolution of
reflexive pronouns. The evidence is rather mixed. On the one hand, a number
of experiments in a variety of methodologies (cross-modal priming, eye-tracking,
ERPs) failed to provide robust evidence that lures affect reflexives resolution (cross-
modal priming: Nicol and Swinney (1989); self-paced reading: Badecker and Straub
(2002) (Exp.5,6); eye-tracking: Sturt (2003); Dillon et al. (2013); Cunnings and
Sturt (2014); ERPs: Xiang et al. (2008) among others). On the other hand, some
studies do report interference effects (Badecker and Straub (2002) (Exp.4), King
et al. (2012a); Cunnings and Felser (2013); Patil et al. (2016); Parker and Phillips
(2017); Sloggett (2017)). I will discuss these groups of studies in order.
The first study to consider the influence of lures on reflexive resolution was
Nicol and Swinney (1989). They report the results of an experiment relying on
cross-modal priming paradigm. The participants were auditorily presented with
sentences like (3). At the moment when people heard the pronominal, a word
appeared on the screen, and people were asked to decide whether it was a real
English word. The word could be related to one of the potential antecedents or
unrelated to any of them. The logic underlying the experiment is that if during
the course of anaphora resolution people reactivate an antecedent, words related to
8
that antecedent would be primed, and thus people reaction times would be faster
as compared to the unrelated word conditions. If binding principles are accurately
applied, we expect that only words related to “boxer” and “skier” would be primed
when people encounter “him” and only words related to “doctor” will be primed
when people encounter “himself”. This is exactly what Nicol and Swinney report.
(3) The boxer told the skier that the doctor for the team would blame him /
himself for the injury.
These results suggest that people were successfully using structural informa-
tion to restrict antecedent selection, and a number of subsequent studies fell in line
with this conclusion. Sturt (2003) examined sentences like (4) (the examples come
from Exp.1 and 2, correspondingly).
(4) a. Jonathan was pretty worried at the City Hospital. The surgeon who
treated Jonathan / Jennifer had pricked himself / herself with a used
syringe needle.
b. Jonathan / Jennifer was pretty worried at the City Hospital. He / She
remembered that the surgeon had pricked himself / herself with a used
syringe needle.
Neither Experiment 1 or 2 provided evidence for any detectable effects of the lure
in early measures5. Dillon et al. (2013) considered sentences like (5). Agreement
5Experiment 1 did provide evidence for some late effects. First, in re-read times on the reflexive
9
conditions (5a) showed a profile indicative of agreement attraction: lure match
conditions being read faster than lure mismatch conditions within target mismatch
sentences only6. However, no evidence for the impact of the lure was found in the
reflexive conditions (5b). King et al. (2012b) report similar results7.
(5) a. The new executive who oversaw the middle manager / managers appar-
ently was / were dishonest about the companys profits.
b. The new executive who oversaw the middle manager / managers appar-
ently doubted himself / themselves on most major decisions.
Similarly to Dillon et al. (2013), Xiang et al. (2008) compared NPI licensing to re-
the target match conditions were read faster than target mismatch conditions within lure mismatch
conditions only. Or, to put it another way, target mismatch-lure match conditions were the slowest
of all. Second, in re-read times on the pre-final region, lure match conditions were faster than lure
mismatch conditions within target match conditions only. A follow-up sentence interpretation
experiment suggested that in lure match conditions people provide more answers compatible with
the resolution of the dependency to the lure. I have to note, however, that a replication of this
experiment by Cunnings and Sturt (2014, Exp.1) failed to find support for the late effects of the
lure. It is also worth noting that in both studies the number of participants was rather low, 24
for Sturt (2003) and 28 for Cunnings and Sturt (2014, Exp.1). Thus, the statistical power that
these studies had was likely low . Given this, I do not consider this evidence against the absence
of lure-match effects in Sturt (2003) as very strong.
6In this case, “target” refers to the subject of the main clause, and “lure” - to the subject of
the embedded clause.
7This study did report lure match effects in a different configuration, but I will return to them
later
10
flexive resolution in sentences like (6) using EEG. NPI conditions did show effects of
structurally inappropriate licensor: the amplitude of P6008was reduced as compared
to the sentences with no licensor at all. However, no similar evidence was found for
the reflexive sentences: regardless of whether the lure matched or mismatch the
reflexive in gender, target mismatch conditions elicited smaller P600.
(6) a. NPI, grammatical: No restaurants [ that the local newspapers have
recommended in their dining reviews ] have ever gone out of business9.
b. NPI, illicit licensor: The restaurants [ that no local newspapers have
recommended in their dining reviews ] have ever gone out of business
c. NPI, no licensor: Most restaurants that the local newspapers have
recommended in their dining reviews have ever gone out of business
d. Reflexive, target match: The tough soldier that Fred treated in the
military hospital introduced himself to all the nurse.
e. Reflexive, target mismatch, lure match: The tough soldier that
Katie treated in the military hospital introduced herself to all the nurses.
f. Reflexive, target mismatch, lure mismatch: The tough soldier
that Fred treated in the military hospital introduced herself to all the
nurses.
8An event-related potential component often associated with the processing of syntactic viola-
tions. Bigger amplitude is taken to be associated with more severe reaction to the violation.
9I omit an additional manipulation of NPI licensor type, since it is not relevant for interpreting
these results.
11
While the studies above report consistent evidence for reflexive resolution being
accurately guided by structural information, other studies have reached different
conclusions. Badecker and Straub (2002) used feature-mismatch paradigm in a self-
paced reading study with sentences like (7). They reported a slow-down in the
second region after the reflexive when both the lure and the target matched the
reflexive in features.
(7) Jane / John thought that Bill owed himself another opportunity to solve the
problem.
King et al. (2012a) compare conditions with verb-adjacent and non-verb-adjacent
reflexives to test the following conjecture. The verbs likely re-activate their ar-
guments, including subject, regardless of the presence of the reflexive. Reflexive
pronouns are often found in direct object position, so if the information about the
subject persists in the focus of attention, it might be too prominent to allow any
effects of the lure be detected. If this conjecture is right, we will only observe the
effects of the lure in the latter case. This is what King et al. report10. Only for
non-adjacent reflexives lure match conditions were read faster than lure-mismatch
conditions within target mismatch conditions.
10A caveat is in order: as far as I know, these results have never been published as a research
paper. The information is available as a poster and a conference abstract, but the amount of
statistical and numerical details is obviously much smaller than what would be possible in a
paper. Thus, the interpretation presented here is correct to the degree that I interpret this limited
information correctly.
12
(8) a. Verb adjacent: The mechanic who spoke to John / Mary sent himself
/ herself a package.
b. Non verb adjacent: The mechanic who spoke to John / Mary sent a
package to himself / herself.
Cunnings and Felser (2013) investigated whether reflexive resolution is affected by
participants’ working memory characteristics. They used eye-tracking with fea-
ture mismatch paradigm, and additionally median-splitted their participants into
two groups according to their working memory capacity (as assessed by Daneman-
Carpenter test (Daneman and Carpenter, 1980)). In two experiments they found
limited evidence for the influence of the lure. In Experiment 1, it was observed at
the pre-final region for both memory groups in first fixation duration; in Experiment
2, only participants in the low-working-memory group were affected by the lure (but
the effect was noticeable earlier, at the reflexive itself). An eye-tracking study by
Patil et al. (2016) reports the influence of lure match on first-pass regression prob-
ability11, observing more regressions in lure match conditions as compared to lure
mismatch conditions within target match only.
Finally, Parker and Phillips (2017) (furthermore, PP2017) and Sloggett (2017)
(furthermore, S2017) provide perhaps the clearest evidence of lure-match effects in
reflexive resolution. PP2017 rely on the same feature mismatch manipulation as
most of the previous studies, with an additional twist: they manipulate the degree to
11I.e. the probability that the eyes will move to earlier regions during the first pass on the
current region
13
which the target mismatches the reflexives. In all of the previous studies, the target
either fully matched the reflexive in morphological features, or mismatched it in one
morphological feature. Parker and Phillips additionally considered conditions where
the target mismatches the reflexive in two morphological features, as exemplified in
(9). They found that people were much faster to read the reflexive if it matched
the features of the lure, but only in the 2-feature target mismatch conditions. The
authors considered target mismatch in all possible two-features combinations of
gender, number and animacy and found similar effects for all of them.
(9) The talented actor/actress mentioned that the attractive spokeswomen praised
himself for a good job. .
I will slightly delay the discussion of the interpretation that PP2017 give. I will
only note that according to their account, having mismatch in two features between
the reflexive and the target is crucial for observing lure-match effects. Therefore it
is not surprising that a big proportion previous studies failed to do so: all of them
used 1-feature target mismatch configurations.
S2017 replicates most of PP2017 findings. Moreover, he demonstrates that
the lure match effect in PP2017 configurations depends not only on the degree of
feature match between the reflexive and the potential antecedents, but also on dis-
course factors. First, he shows that the identity of the embedding verb is important
- in sentences like (10a) lure-match effects were only observed with report verbs
like “say”, but not with perception verbs like “hear” (Experiment 1b). Second,
14
he shows that the identity of the target is important - lure-match effects do not
appear if the target is an indexical pronoun like “I” or “you” (10b) (Experiments
3b,4b). Finally, in an interpretation study (Experiment 1c), he demonstrates that
lure-match effects are potentially detectable even in grammatical sentences. In this
experiment people were presented with sentences like (10c) in a self-paced reading
manner, and at the end of each sentence had to answer a comprehension question.
For grammatical sentences like those in (10c), the question was probing the inter-
pretation of the reflexive, e.g.: “Who was misrepresented at the meeting? The
librarian / the schoolgirl”. People chose answers compatible with non-local resolu-
tion (e.g. “The librarian”) in roughly 30% of the time despite the sentence being
fully grammatical12.
(10) a. The librarian / janitor said / heard that the schoolboys misrepresented
herself at the meeting.
b. The actor/actress said that Joanna I horribly misrepresented herself in
the article.
c. The librarian / janitor said / heard that the schoolgirl misrepresented
herself at the meeting.
12While this may, indeed, indicate that target mismatch is not a necessary pre-condition for
lure-match effects to arise, we have concerns about how the data fromS2017 Experiment 1c should
be interpreted. We discuss these concerns later in the thesis.
15
1.2 Evidence interpretation
The evidence reviewed above suggest that at least sometimes grammatically ir-
relevant constituents do affect real-time dependency formation. This information in
itself, however, is not sufficient to claim that grammatical constraints fail to uniquely
guide the parser. In this section we will review three types of accounts of how lure-
match effects come to be. We will call an account “structure-strict” if it suggests
that structural information can categorically rule out illicit dependency formation,
and “structure-defeasible” otherwise. The evidence above could be used to support
“structure-defeasible” accounts only if we manage to argue that “structure-strict”
accounts fit the evidence less well or should be dispreferred on theoretical grounds.
We will show that such an argument could be made. We will then discuss potential
counter-arguments, and this will lead us to the main goal of the thesis - evaluating
these counter-arguments in order to understand whether our original argument for
“structure-defeasible” models should or should not be abandoned.
1.2.1 Accounts of lure-match effects
The first class of accounts can be called “representational”. They come in
different flavors (e.g. Nicol et al., 1997; Vigliocco and Nicol, 1998; Franck et al., 2002;
Eberhard et al., 2005), but they all share the assumption that lure-match effects
arise because syntactic representation of the target is distorted: e.g. the whole
phrase receives its number marking not from its head but from the complement.
Interference effects arise when a correctly functioning access mechanism contacts
16
an invalid linguistic representation. Thus, representational accounts have to be
“structure-strict” - they assume that structure perfectly guides the search for the
target constituent.
A second type of accounts could be called “grammatical” (e.g. Xiang et al.,
2013; Sloggett, 2017). These accounts basically suggest that lure match effects are
not a result of a processing error, rather, they are a manifestation of grammatical
strategies licensed by the language. Xiang et al. (2013) suggest an account of this
sort for the NPI data. They argue that constraints on the dependency licensor
should not always be analyzed as “be in the c-command domain of a downward-
entailing expression”. Rather, the grammar also provides an alternative licensing
path, via pragmatic inferences from the context. In certain cases this strategy could
lead to spurious inferences, which would lead to illusory NPI licensing. Sloggett
(2017) suggests this type of account for lure-match effects in reflexives, arguing that
they should be analyzed as instances of logophoric behavior of the anaphors. We will
discuss this account in much more detail in a later section. These accounts are also
“structure-strict”: if one wants to use grammatical principles as the explanation,
one has to assume that they are applied accurately.
Finally, a third class of accounts could be called “memory” accounts: they
assume that the errors arise at the level of memory operations underlying lan-
guage comprehension (Lewis and Vasishth, 2005; McElree, 2006; Van Dyke and
McElree, 2006; Engelmann et al., draft4; Jäger et al., 2017; Parker et al., 2017).
The most common assumption is that memory access is faulty and sometimes the
parser may access constituents not licensed by the grammar. This amounts to
17
“structure-defeasibility” in my terms. However, memory models are not inherently
“structure-defeasible” - one could modify model parameters so that the parser would
be predicted to only access grammatically licit constituents. Such models would not
predict lure-match effects arising from faulty memory access. One could hope that
they can be easily ruled simply by the fact that lure-match effects are empirically
attested. Unfortunately, lure-match effects can arise even in “structure-strict” mem-
ory models, since memory access is not the only place where things could go wrong.
Another such place is encoding. It might be the case that when one item needs
to be entered into memory and another item with similar features is already present
there, the encoding for one or both items may get degraded, perhaps because it is
difficult to keep distinct bindings for similar features (Nairne, 1990; Vasishth et al.,
2017). The degraded representation will be more difficult to access during retrieval,
causing a slow-down. Thus, similarity between the target and the lure might affect
RTs even if retrieval operates completely faithfully13. Originally, this argument
has only been applied to cases of inhibitory interference: slow-down when the lure
matches the target in features (Dillon et al., 2013; Chow et al., 2014). However,
recently Patil et al. (2016, p.17) and Parker et al. (2017, p.129) pointed out that
facilitatory interference (speed-up when the lure matches the features on the other
end of the dependency, but not on the target) does not have to stem from retrieval
stage either. For example, if representations can be degraded during the encoding
stage, they will be degraded more in (1a) than in (1b), since in the former case the
13Notice that in this case the dependency formation is completely licensed by the grammar, but
is made more difficult by extra-linguistic factors.
18
two nouns have a greater overlap in features. Thus, even if memory access is always
accurate and the target is reliably retrieved in all cases, it will take longer time in
(1a), creating a profile of reaction times consistent with facilitatory interference.
1 a. *The key to the cabinet are on the table.
b. *The key to the cabinets are on the table.
c. The key to the cabinets is on the table.
d. The key to the cabinet is on the table.
Another possible locus of lure-match effects in memory models is in post-
retrieval operations, e.g. repair. Different types of models assume different memory
dynamics. Lewis and Vasishth (2005) model, which we will discuss in detail later,
assumes that an item’s prominence in memory determines both how likely it is to be
faithfully recovered and how quickly this item can be made available for processing.
Thus this model can account for reaction times differences directly; if needed, repair
processes could be assumed, but without having a good reason for doing so, a
parsimonious Lewis and Vasishth-type model could make do without them. On
the other hand, in McElree (2006) framework access times are always constant: an
item’s prominence only determines the probability of successfully accessing the item.
If this model is closer to the truth, RT differences would have to be produced by
some other mechanism. One possibility would be that longer reaction times stem
from re-analysis/repair processes. E.g. if retrieval fails, a second retrieval could be
initiated to compensate for that. The slow-down due to additional retrievals could
19
potentially account for lure-match effects14. Notice that in this case, RTs again
will not necessarily tell us anything useful about how structural information is used
to constrain real-time processing: repair processes might involve a different set of
processing routines/constraints15. Another possibility is that the strength of the
recovered representation might matter: even if any item can be retrieved equally
fast, some will be recovered more faithfully, and the processes downstream from
memory retrieval may be sensitive to these differences.
14Consider the following possibility. As we discuss in section 1.3, cue-based models assume that
when a memory item has to be accessed, a set of retrieval cues is specified; all items are matched
in parallel to these cues, and receive a boost in prominence for each matching feature; the most
prominent item is then accessed with some probability of success. Now, the lure would be more
prominent in (1b) than in (1a) because it would match the number of the verb, which presumably
would be a part of the set of retrieval cues. Fewer re-analysis operations would be initiated in the
first case, potentially leading to a speed up (but see Nicenboim and Vasishth (2018) who suggest
it is not clear how repair processes would even work in ungrammatical sentences and how the RTs
profiles in those would be accounted by McElree model).
15Of course, we might argue that repair is a normal part of everyday language use and thus
identifying the constraints involved is useful. Still, one needs to be careful: if we are talking about
“first-pass” processing that just directly leads to interpretation, the set of memory mechanism we
can “blame” for errors is narrower and better defined. If we are talking about repair, the spectrum
is much wider: it may be that repair relies on the “usual” memory access procedures with some
minor tweaks. Or maybe the “usual” memory access is used but with completely different set of
parameters. Or maybe qualitatively different mechanisms are involved. Without clearly specifying
our theory of repair, it would be hard to figure out what exact conclusions should we draw out of
our RT data.
20
1.2.2 Choosing an account
We have looked at three groups of accounts: representational, memory, and
grammatical. As we have seen, the first two groups of accounts have to assume that
structural information can successfully constrain dependency resolution. Memory
accounts can be either “structure-strict” or “structure-defeasible”, depending on
the assumptions one makes about the access properties and the source of behavioral
evidence: encoding, retrieval, repair. Only if we can unambiguously attribute the
observed lure-match effects to the retrieval processes, will we be able to make a
claim about “structure-defeasibility” of normal real-time sentence processing. In
this section we will discuss why one might, indeed, decide that memory retrieval
processes stand behind lure-match effects, and why, therefore, one would want to
believe the “structure-defeasibility” thesis.
Ruling out representational accounts The biggest argument against repre-
sentational models is empirical: it is the absence of illusions of ungrammaticality in
agreement attraction (representational accounts have been historically developed to
deal with agreement data) (Wagers et al., 2009). In these accounts, the distortion of
the target NP happens phrase-internally due to morphosyntactic mechanisms (e.g.
erroneous feature percolation from the head level to the phrase level) and inde-
pendently of other factors such as sentence well-formedness. Thus, it is as likely to
happen in grammatical as in ungrammatical sentences, and we should commonly ob-
serve cases in which a perfectly well-formed sentence is perceived as ungrammatical.
21
However, such cases are rarely reported.
Another potential argument against representational accounts is that they are
not easily expandable to cover other dependencies which exhibit similar empirical
behavior (NPI licensing or reflexive resolution). In contrast, memory models can
explain multiple phenomena in terms of the same underlying mechanisms, and thus
may be preferred, if they are comparable in terms of empirical coverage. A priori
this may seem counter-intuitive: since we know that different linguistic dependencies
have qualitatively different constraints on them, wouldn’t we expect them to behave
qualitatively different during the processing as well? I argue that while this is
possible, it is not a logical necessity.
It is inevitable that at some point during language processing linguistic con-
straints have to be translated into processing instructions. I argue that it may
be advantageous to assume that this translation process is very straightforward at
the interface: every linguistic constraint is turned into a retrieval cue16. However,
from this point onwards what happens with these cues is determined only by the
properties of the memory system: i.e. it is agnostic about where the cues came
from and just knows how to perform operations with them. Consider anaphora as
an example. Under Chomskyan Binding theory, an anaphor should be bound by
a local (roughly, a clause-mate) and c-commanding antecedent. According to our
hypothesis, these specifications would be converted to retrieval cues like “+ local”
and a “+ c-commands current NP” cue17. Another set of constraints - semantic or
16See section 1.3.
17Real constraints will have to be more complicated. The actual definition of locality domain
22
perhaps pragmatic - require that the anaphor matches its antecedent in φ-features -
correspondingly, φ-features of the anaphor would be translated to retrieval cues as
well (e.g + sg, + masculine etc.). Memory systems would then use these cues like
any others in order to determine which memory chunk should be retrieved during re-
flexive resolution. Notice that in this case the parser’s failures to be uniquely guided
by linguistic constraints are due to either the translational procedure used at the
interface, or the properties of the general purpose memory system. Correspondingly,
we would expect to observe reasonably similar effects across multiple dependencies,
which arguably corresponds to actual empirical observations. But even if we ques-
tion the degree of this alignment, such a unified system is theoretically useful: it
allows to easily generate precise predictions for a range of linguistic phenomena and
suggests what types of empirical observations we should be looking for. This could
make it easier to discover new things.
In addition, a model with a unified treatment of different dependencies my be
preferred because it assumes that linguistic constraints straightforwardly map onto
general purpose mechanisms. As soon as we start making additional assumptions
connected to the linguistic nature of the representations - e.g. that different levels
of representations (syntax, pragmatics etc.) may have different access procedures or
that different dependencies rely on qualitatively different mechanisms, we introduce
an additional burden of explaining why such a division exists18.
is actually more involved than the simplification we used, and as we discuss later, encoding c-
command information in terms of cues is notoriously difficult.
18Notice that PP2017 of lure-match effects in reflexives (discussed in Section 1.3.1), while largely
keeping to the unificational spirit of memory models, already violates the “pure mapping” hypoth-
23
Ruling out grammatical accounts Grammatical accounts are somewhat harder
to rule out. We can think of two arguments against them. First, the argument for
preferring memory models we made above is even more relevant for grammatical
models: they explicitly state that linguistic constraints affect processing in a non-
trivial way (perhaps invoking qualitatively different resolution mechanisms and/or
memory access routines) - as we argued, such approach may be undesirable as a
working hypothesis. Second, empirical coverage of grammatical models is narrower
than that of memory models. As far as we are aware, there are no grammatical
accounts of agreement attraction - it is quite unequivocally considered a processing
error, and not a manifestation of some not-so-well-described grammatical strategy.
Now, if we have accepted the first argument, the fact that at least one phenomenon
is a result of a processing error would force us to assume that other lure-match effects
stem from the processing side of things as well. These arguments are certainly not
rock-solid, but for the moment we will rely on them.
Ruling out non-retrieval memory accounts Ruling out the possibility that
lure-match effects stem from the encoding stage is hard to do once and for all,
unless we have very fine-grained methods of investigating the contents of memory.
However, Jäger et al. (2015) show that at least in some cases the “encoding degra-
dation” account is not supported. The study looked at German reflexive pronoun
“sich” in configurations like (11). Since “sich” is unmarked for gender, a reasonable
esis by assuming different weighting schemas for structural cues in subject-verb agreement vs.
reflexive resolution
24
assumption would be that this feature is not included in the set of retrieval cues
during the search for the antecedent. If inhibitory interference results from encoding
processes, this will not matter and we will observe inhibition in (11) when the two
nouns match each other in gender. If, on the other hand, inhibitory interference
arises due to retrieval dynamics, we should not observe any effect of gender match
between the two potential antecedents. This is indeed what Jäger et al. report. This
lack of the effect was observed in both self-paced and eye-tracking reading times.
The study used unusually large sample sizes (around 150 participants in each of the
experiments), which gave them roughly 90% power to detect an effect of 20ms with
a standard deviation of 75ms. Thus, the lack of evidence for inhibitory interference
is quite reliable.
(11) a. Der Diebi/Die Diebini, dem/der der Hehlerj/die
the thief-MASC/the thief-FEM whom the dealer-MASC/the
Hehlerinj befohlen hat zu stehlen, hat überraschenderweise sichi/∗j
dealer-FEM obliged has to steal has surprisingly self
und die Kollegen angezeigt, berichtete das Hochglanzmagazin.
and the colleagues denounced reported the magazine.
The thief whom the dealer obliged to steal surprisingly denounced him-
self/herself and the colleagues, reported the magazine.
Jäger et al. (2015) results suggest that interference found in the reading times from
feature mismatch paradigm is likely due to retrieval processes. Still, the study only
shows that in some cases encoding processes are an unlikely culprit, and completely
ruling out this possibility or determining the range of phenomena for which it holds
may be quite difficult.
25
Whether repair explanations should or should not be considered is not clear
at this point. Choosing between Lewis and Vasishth (2005) model, which does
not crucially involve repair, and McElree (2006) model, which does, is complicated.
On the one hand, constant speed of memory access, which is only captured by
McElree (2006) framework has quite extensive empirical support (McElree et al.,
2003; McElree, 2006; Martin and McElree, 2009, 2011). On the other hand, Lewis
and Vasishth (2005) model is straightforwardly predicting facilitatory interference
RT profile (as observed in agreement attraction), and McElree (2006) model has
problems with it. Nicenboim and Vasishth (2018, p.21) suggest that McElree model
would not be able to predict it at all, since it is unclear how exactly repair processes
would operate in ungrammatical sentences 19.
For the predictions in which the models can be compared directly (inhibitory
interference in target match configurations), they appear to be tied. Nicenboim and
Vasishth (2018) directly compare the fit of (particular implementations of) Lewis
and Vasishth and McElree models to a dataset coming from a study on agreement
attraction in target match configurations (Nicenboim et al., 2017). They found that
19We think that the following suggestion might work, although it does rely on certain assump-
tions about repair, and unless we are able to independently validate those assumptions, this sug-
gestion remains purely speculative. Suppose that in target mismatch configurations the system
initiates repair quite often, since neither the target or the lure match all of the retrieval cues. Sup-
pose also that fewer repairs will be attempted in lure match conditions, since the error-detection
mechanism will be less capable of noticing the violations. Then, in the long run, more time will
be spent trying to repair the representation in lure mismatch conditions, giving rise to facilitatory
time patterns. For this schema to work, we need to assume that the ease or difficulty of detecting
a mis-retrieval is contingent on the number of matching features - i.e. repair detection works in the
same way as search result detection. This assumption raises a question: why is feature mismatch
not detected during the original search, but is at a later stage? One possible answer could be that
the retrieval system only “cares” about finding an item without further knowledge of what has
to be done to it, so it may not incorporate on-the-fly sensibility checks. On the other hand, the
repair detection mechanism may specifically depend on how smoothly the retrieved item can be
integrated in the representation, so it may be more sensitive to such mismatches.
26
McElree model fit the data somewhat better than a simple variant of Lewis and
Vasishth model. However, only a slight complication to the Lewis and Vasishth
model allows it to fit the data on par with the McElree model. Thus, at least for
target match configurations, neither model is clearly preferred.
Finally, a principled way of distinguishing repair from “first-pass” processes
regardless of a model is to look at the time course of lure-match effects. One might
argue that an effect appearing early is unlikely to stem from repair processes, unless
one assumes they can be really quick. From this point of view, eye-tracking might
be the only widely used method allowing for such distinctions: self-paced reading
times only gives data about total reading time per region; EEG data, while having
perfect time resolution, may be hard to interpret as stemming from a particular time
point in the processing. If one accepts this argument, only the studies which find
lure-match effect in early eye-tracking measures (such as first fixation or first-pass
time) should be taken as evidence on memory search processes.
To sum up my discussion of memory models, lure-match effects can be ex-
plained in at least three ways: as stemming from encoding, search or repair mecha-
nisms. Choosing between these possibilities is not always straightforward. We have
some evidence against encoding account Jäger et al. (2015), but it is rather limited.
Distinguishing between accounts with and without repair as their necessary compo-
nent has so far been complicated, with no clear winner available. In what follows,
we will simplistically assume that any RTs difference we observe stem from memory
access processes, but one should keep the issues we have just discussed in mind in
order not to become overconfident in the conclusions we draw.
27
1.2.3 Evidence interpretation: summary
In the last several sections we have been discussing whether we have reasons
to choose “structure-defeasible” accounts over competing solutions. We presented
the following argument for doing so. Memory accounts arguably provide the best
explanation for subject-verb agreement data20. There are no grammatical accounts
of agreement attraction, and representational accounts are ruled out by the absence
of ungrammaticality illusions in subject-verb agreement studies. If we settle on
memory accounts, “structure-defeasible” flavors have to be chosen, because other-
wise memory accounts would not be able to explain agreement data either. Now,
due to the universality of these accounts, a priori it would be tempting to extend
them to other linguistics phenomena such as anaphora resolution and NPI licens-
ing. To keep the models’ universal coverage, one would also be tempted to preserve
“structure-defeasible” assumption we made for agreement. This is essentially the
line of explanation pursued in Vasishth et al. (2008) and Parker and Phillips (2017).
This line of argumentation is undercut in two places by several recent studies.
First, it has been argued that the generalization about the absence of ungrammati-
cality illusions is not empirically accurate. Jäger et al. (2017) provide evidence for
the existence of ungrammaticality illusions based on the results of a quantitative
meta-analysis. Hammerly et al. (draft.april.2018) provide corroborating findings
and suggest that the existing generalization is just an artifact of the experimental
method. If true, this claim would take away our reasons to prefer memory models
to representational ones for the agreement data (and relevant to the main topic of
20At least in comprehension
28
my thesis, “structure-defeasible” to “structure-strict” models). This will have reper-
cussions for our accounts of other dependencies as well: if we do not have to pick
“structure-defeasible” models for agreement, we have less ground to a priori assume
that other dependencies should be accounted for by “structure-defeasible” models,
regardless of the particular architecture we use. Indeed, Sloggett (2017) explains
lure-match effects in reflexives with a memory model of “structure-strict” type. It
is also the case that these models lose the universality of cue-based models and are
very specific. It is not clear whether Hammerly et al. (draft.april.2018) model can be
extended to other dependencies apart agreement, and it is clear that Sloggett (2017)
model cannot - by design, it is reflexive-specific. Assessing (some of) these recent
counter-suggestions is the main goal of this thesis. To start addressing this problem,
in the following section I will discuss a prominent model of cue-based parsing (Lewis
and Vasishth, 2005) and discuss how it can be used to accommodate (a big part of)
the empirical evidence. Then I turn to the recent problematic findings and show in
more detail how they might undermine the argument for preferring memory models.
1.3 Lewis & Vasishth (2005) memory model
The central assumption behind cue-based memory models used in psycholin-
guistic research is that human working memory access is content-addressable and
parallel. That is, the items in memory are located by their contents (and not, say,
their location) and can be investigated in parallel without the need to go through
them one by one. In such an architecture, it is hard or impossible to avoid inter-
ference - when multiple items are similar enough in terms of their content, it is
29
harder to select the correct one. Therefore, if long-distance dependencies resolution
does rely on such system, we can expect processing mistakes similar to those I have
reviewed above.
As I have already mentioned, cue-based parsing is theoretically attractive.
First, there is independent evidence that domain-general working memory is content-
addressable (Jonides et al., 2008, for a review of evidence and arguments). Thus,
a theory of long-distance dependencies relying on content-based memory would not
postulate any language-specific mechanisms. Second, in cue-based models the dy-
namics of memory access remain the same regardless of the specific cues one is using.
Thus, it might be possible to analyze the processing of different linguistic dependen-
cies in terms of the same underlying mechanisms. In what follows, I will introduce
a popular model of cue-based parsing by Lewis and Vasishth (2005) (henceforth,
LV05), which I will rely upon in this thesis. I will start with discussing the model
itself; then, I will turn to showing how it can account for the data presented above;
finally, I will briefly discuss its shortcomings and a few caveats.
In the parsimonious spirit of the discussion above, LV05 model is couched
within ACT-R, a general purpose computational model of cognition (Anderson,
2005). According to the model, memory items are represented as bundles of features
(for linguistic purposes, it could be “+ NP”, “+ subj”, “+ animate” etc). Items
in memory are not directly available for operations on them - they have first to be
“retrieved”, i.e. put in a special prominent state. I will call such a state “focus of
attention”. The capacity of focus of attention is assumed to be extremely limited21,
21The exact capacity of focus of attention is debated. Some proposals suggest that it may only
30
thus, in order to be able to carry out any remotely complicated procedure, e.g.
parsing, memory items have to be constantly shunted in and out of the focus of
attention.
In order to put the item in a focus of attention, the system needs to find the
item which is most prominent for the current needs. In the model, items’ prominence
is represented as a quantity called “activation” which is different for each item. This
quantity is determined by the history of an item’s use, the current search needs and
stochastic noise, and is formalized in Eq.1.1. During memory access, the system
attempts to boost the activation of the relevant item above a certain threshold. In
order to do this, it forms a set of retrieval cues22, which is compared to the features
of each memory item in parallel. Each item gets an activation boost proportional
to the number of features overlapping with the set of retrieval cues. Formally, Sji is
the strength of association item i and the cue j, calculated as shown in Eq.1.2. Each
cue has only a limited amount of activation it can “share”, denoted by S. Thus, if
multiple items match a given cue, the activation boost for each item will be reduced.
This corresponds to the intuition that the more items have a certain feature, the less
useful this feature is to distinguish between them (“fan effect”, Anderson and Reder
(1999)). The activation conferred by each matching cue is additionally weighted by
wj. Usually, all retrieval cues are assigned equal weights, but it does not have to be
be able to hold four chunks (e.g. Cowan, 2001), while others claim that the capacity may be
even smaller, one or two chunks at most (McElree et al., 2003). ACT-R assumes that the system
possesses a number of specialized “buffers”, each with capacity of one memory chunk. Of interest
to us are two buffers: the goal buffer, in which the set of retrieval cues is placed (see the discussion),
and the retrieval buffer which holds the memory access result. Only the item in the retrieval buffer
is assumed to be accessible for further operations.
22Which is put in the goal buffer.
31
the case.
∑
Ai = Bi + wjSji (1.1)
j
Sij = S − ln(fanji)fanji = 1 + itemsj (1.2)
The boost from retrieval cues determines the item’s activation only partially.
Items are assumed to have fluctuating baseline activation (Bi in Eq.1.1), which is
influenced both by how frequently the item was retrieved in the past and by how
recent the last retrieval was. Moreover, the process is assumed to be stochastic,
so that activation values are not perfectly predictive of whether the item will be
retrieved. The probability that the item will be retrieved on a given access attempt
is determined by the assumed distribution of the noise and is described by Eq.1.3,
where Ai is the activation value for item i, τ - retrieval threshold, and s - a parameter
controlling noise. If the activation for the item does cross the threshold, it is retrieved
(i.e. made available for further operations on it) with latency described by Eq.1.4.
F is an arbitrary constant, which varies from model to model.
1
Pi =
1 + e−
(1.3)
(Ai−τ)/s
Ti = Fe
Ai (1.4)
32
1.3.1 Explaining RT patterns
LV05 model can successfully explain grammaticality illusions across multiple
dependencies. Essentially, a variant of the following (simplified) explanation can be
used: when a perfectly matching target is not present in the sentence, an imperfectly
matching lure can occasionally be retrieved, leading to faster reading times. Notice
that this explanation is “structure-defeasible”, since the lures by design located in a
structurally inappropriate position; so the fact that they are retrieved at all would
mean that the structure fails to constrain the memory access properly.
I will use subject-verb agreement to explain the mechanism in detail and then
will show how it could be applied to other dependencies. Consider the ungram-
matical sentences from (1), repeated below for convenience. In (1a) the target is a
better match to the retrieval cues: it matches the “+subj” (or “+ Nominative” )
cue, while the lure matches none. On the other hand, in (1b) the target and the
lure are each an equally good match23. In this situation, response times will be on
average faster in (1b) due to statistical facilitation (Raab, 1962). Roughly speaking,
if we assume that there are two reaction times distributions, one for the target and
the other one - for the lure, and we generate the observed reaction time by drawing
a value from each distribution and choosing the smallest one24, the mean of the
distribution of observed RT values will be smaller then the mean of either of the
23Assuming that the cues are treated by the system as equally important, i.e. assigned equal
weights.
24I.e. in this context - the fastest RT.
33
sampling distributions25.
1 a. The key to the cabinet are on the table.
b. The key to the cabinets are on the table.
A big selling point for the LV05 model is that it is assumed to be able to explain the
absence of ungrammaticality illusions. Wagers et al. (2009) suggested that it could
be captured in the following way: since in grammatical sentences the target always
matches the retrieval cues better than the lure, it will always be reliably retrieved.
NPI cases work similarly, with the difference that in the lure-match sentences
there is no licit target at all. For example, the following explanation is advanced
by Vasishth et al. (2008). When people encounter an NPI, they initiate retrieval
with “c-commander”26 and “negative” as cues. In (2c) “no congressman” is indeed
a negative element, thus it provides a partial match to the retrieval cues and may
be retrieved on a proportion of times.
Finally, lure-match effects in reflexive resolution can be explained in very much
the same way as they are for subject-verb agreement (Parker et al., 2017). The only
difference is that for reflexives structural cues like “+ local” or “+ c-commander” are
25Unless the two sampling distributions do not overlap at all. In the context of the model, we
assume that the overlap is bigger in (1b) than in (1a), because the activation values for the lure
and the target are closer to each other in the first case, and closer activation values map to more
similar retrieval times in ACT-R.
26As we discuss in section 3.1, implementing “c-commander” cue may not be straightforward.
Vasishth et al. choose to assume that such a cue can be implemented and abstract from the
question of how exactly.
34
weighted higher than morphological cues like “+ sg”. During memory access, the
mismatch in a single morphological feature is not enough to make the activation for
the target sufficiently low to approach the activation for the lure. But the mismatch
in two morphological features suffices to do this, and the system finds itself in the
situation I described earlier for subject-verb agreement, with the target and the lure
having comparable activation values.
Such a mechanism would explain why the majority of the previous studies
did not find evidence for lure-match effects: all of them used designs in which the
target mismatched the reflexive at most in one morphological feature. Prima facie,
lure-match effects reported in some of the previous studies (Badecker and Straub,
2002; Patil et al., 2016; Cunnings and Felser, 2013; King et al., 2012a) would be
problematic for PP2017 account, since they were not observed in 2-feature mismatch
configurations. However, most of these findings can be explained away.
Inhibitory interference findings (i.e. lure match leading to slow-down) reported
by Badecker and Straub (2002) (Exp.4), Patil et al. (2016) and Cunnings and Felser
(2013) (Exp.1) could be discounted on multiple grounds. First, one could argue that
these findings reflect fan effect (cf. the discussion above for agreement). Second, they
could be dismissed as irrelevant: as I discussed in section 1.2, inhibitory interference
can be attributed to other processes apart from memory retrieval, e.g. memory
encoding27. Finally, this evidence could be dismissed altogether as a fluke: as Jäger
et al. (2017, p.326) notice, the meta-review suggests that interference is more likely
27This argument is rather weak, especially since Jäger et al. (2017) provides evidence that at
least in some cases inhibitory interference is informative about retrieval.
35
to be observed in ungrammatical sentences, and even high-powered studies like Jäger
et al. (2015) fail to find reliable evidence for it.
Facilitatory interference observed by Cunnings and Felser (2013) in their Ex-
periment 2 (low-working-memory participants only) could be accounted for if we
assume that lures were more prominent than targets in the experimental materi-
als28. This assumption would not be too far fetched: the lures were linearly closer
to the reflexives and were prominent in the discourse (pronouns were used as lures,
while full NPs were used as targets). Within the context of PP2017 model one would
have to make an additional assumption that the activation boost from being promi-
nent was functionally equivalent to a single morphological feature mismatch: i.e.
combined with an actual single feature mismatch, it was big enough to counteract
the higher influence from syntactic cues.
The findings by King et al. (2012a) could be dismissed on different grounds.
PP2017 argue that the lure-match effects reported by King et al. (2012a) are of
different nature, since they were observed in sentences where the reflexive pronoun
was situated in a non-argument position. It is known from the linguistic descrip-
tions that such pronouns may obey a different set of constraints (e.g. Reinhart and
Reuland, 1993), therefore they may rely on different processing routines compared
to reflexives in argument positions (e.g. it could be the case that parser weighs syn-
tactic cues lower when resolving reflexives in a non-argument position; this would
be compatible with the observation that the resolution of such reflexives is often
28See discussion in Section 1.5.1.1 about modifications to LV05 model allowing to take linguistic
prominence into account
36
influenced by discourse factors).
1.4 Recent arguments against structure-defeasible models
While LV05 model can successfully explain empirical evidence across multiple
dependencies, a number of empirical results are problematic. In this section I focus
on two objections to the wholesale adoption of “structure-defeasible” memory mod-
els, both of which come from very recent studies. The first objection says that the
main argument for choosing memory models over representational ones is invalid.
The second objection suggests that “structure-defeasible” memory models should
not be used across the board, because different dependencies rely on qualitatively
different mechanisms. I discuss them in turn.
1.4.1 LV05 model fit to agreement data is worse than usually thought
The big reason for choosing memory models over representational ones was
their ability to explain the existence of lure-match effects in ungrammatical sentences
and the absence of lure-match effects in the grammatical sentences. However, this
argument is problematic for two reasons. First, as Jäger et al. (2017) discuss, the
model’s predictions for the ungrammatical sentences are different. In fact, (1d)
is not predicted to be as fast as (1c), it is predicted to be slower, since in (1d)
the target and the lure share the number feature. As I have discussed in section
1.3, the amount of activation each cue can contribute is limited. If more than one
item matches a given cue, this limited amount of activation will be spread evenly
37
between the matching items. In my example, this means that the target in (1d) will
on average have lower activation than the target in (1c). And since in LV05 model
activation directly determines retrieval times, people should be slower in (1d).
1 a. *The key to the cabinet are on the table.
b. *The key to the cabinets are on the table.
c. The key to the cabinet is on the table.
d. The key to the cabinets is on the table.
Second, empirical evidence appears to be incompatible with either Wagers et al.
(2009) account or with the predictions of a basic LV05 model. It appears to be the
case that the “absence” of ungrammaticality illusions may be better characterized
as “rarer observations” of ungrammaticality illusions. A Bayesian meta-analysis of
the available evidence conducted by Jäger et al. (2017) reveals a pattern indica-
tive of ungrammaticality illusions: people read grammatical sentences faster, not
slower, when the lure matches the target in features. Interestingly, Hammerly et al.
(draft.april.2018) report similar observations regarding reaction times; moreover,
they suggest a way of capturing the data from both grammatical and ungrammati-
cal sentences using a representational model. This turns the argument for memory
models and against representational models upside down: now it may be the case
that it is representational accounts which can capture the patterns in both gram-
matical and ungrammatical sentences, and memory models can do so only in the
latter case. We discuss the Hammerly et al. (draft.april.2018) data below and argue
38
that the amount of evidence is not yet sufficient to completely overturn the pref-
erence for memory models, but the direction of the argument and the challenges it
presents to cue-based accounts are worth noting.
Hammerly et al. (2018) The main claim of Hammerly et al. (draft.april.2018)
(henceforth HSD2018) is that the reported absence of ungrammaticality illusions is
largely an artifact of people’s bias to treat their linguistic input as grammatical.
In a series of three grammaticality-judgment experiments and computational sim-
ulation, they show that if this grammaticality bias is canceled, lure-match effects
appear equally frequently in grammatical and ungrammatical sentences. This re-
sult undermines the most important empirical argument for cue-based models and
has the potential of bringing the representational models back into limelight. This
will mean, of course, returning to the view that structural information categorically
guides real-time dependency formation.
HSD2018 argue that to say that ungrammaticality illusions are absent would
be too strong, and a more accurate statement would be that both grammaticality
and ungrammaticality illusions are observed, although the latter are observed rarer.
They suggest that this asymmetry is an artifact of experimental procedure, and not
a reflection of real cognitive differences. Namely, the fact that most of experimen-
tal sentences are usually grammatical biases participants. In a judgment task that
would result in answering “grammatical” more often than “ungrammatical”, and
this in turn will result in a pattern of responses where ungrammatical sentences are
deemed grammatical more often than grammatical sentences are deemed ungram-
39
matical. This explanation suggests that if we manage to eliminate this response bias,
the number of grammaticality and ungrammaticality illusions should be roughly the
same. This is, indeed, what HSD2018 show.
They discuss the results of three acceptability judgment experiments, where
they manipulated participants bias. The first experiment was a replication of pre-
vious results, showing the absence of ungrammaticality illusions in a judgment task
(Wagers et al., 2009). The sentences followed a standard agreement attraction de-
sign, with the grammaticality of the sentence ((12a)-(12b) vs. (12d)-(12c)) and the
match between the lure and the verb ((12a)-(12d) vs. (12b)-(12c)) were manip-
ulated. The results were consistent with the previous findings: an interaction of
grammaticality and lure match was observed. Grammatical sentences were accu-
rately judged as grammatical regardless of lure match. Ungrammatical sentences
were much more likely to be judged as grammatical if the lure matched the verb.
That is, the results showed the absence of ungrammaticality illusions.
(12) a. The friend of the nurse frequently visits...
b. The friend of the nurses frequently visits...
c. The friend of the nurse frequently visit...
d. The friend of the nurses frequently visit...
The next two experiments attempted to manipulate people’s response bias by chang-
ing the proportion of ungrammatical items29 and drawing participants’ attention to
29Two thirds of the items were ungrammatical vs. a half in Experiment 1.
40
this fact in the instructions. In Experiment 2, participants were specifically told that
two thirds of the items were ungrammatical. This manipulation led to slight reduc-
tion of the asymmetry observed in Experiment 1: now people were a little bit more
likely to respond “ungrammatical” to a grammatical sentence with the lure which
mismatched the verb. This effect was statistically significant; however, the critical
interaction was still present in the data. Thus, even is the asymmetry between the
effect of the lure in grammatical and ungrammatical sentences was weakened, it did
not disappear completely.
In Experiment 3 the instructions were changed so that instead of receiving
the exact proportion of ungrammatical stimuli, the participants were simply told
that the majority of the items were ungrammatical. This manipulation was more
efficient: people became less accurate in grammatical sentences and more accurate in
ungrammatical sentences when the lure mismatched the verb. This made the critical
interaction disappear: only the effect of lure match was statistically significant. This
pattern suggests that both illusions of grammaticality and ungrammaticality were
present.
HSD2018 suggest that a representational account by Eberhard et al. (2005)
(“Marking and Morphing”) could be used to explain their results. This approach
assumes that (nominal) number is represented as a continuous value between nega-
tive and positive infinity, where negative values correspond to “more singular” and
positive values correspond to “more plural”. The number of an entire noun phrase,
S(r), is determined as in Eq.1.5. S(n) is the notional component of the number
valuation, coming from the conceptual message. The sum term represents the syn-
41
tactic contribution to the number valuation: it is a linear combination of the number
information on the head and the embedded phrases, weighted by the distance from
the root node. S(r) can be conceptualized as the probability of the plural verb, if
we put it through a logistic transformation, thus bounding its values between 0 and
130.
∑
S(r) = S(n) + (wj × S(m)j) (1.5)
j
Consider how this model would predict agreement attraction. For a subject
phrase like “The key to the cabinet” both nouns inside it are singular, thus, the
number representation of the whole phrase will correspond to “singular” by default.
On the other hand, in a phrase like “The key to the cabinets” the embedded noun is
plural. This plurality will increase the S(r), making the plural verb more probable.
Results of Experiments 2 and 3 would be captured by this account rather
easily. Experiment 1 would be more problematic: as we have already discussed,
the changes to the number marking of the subject NP will happen regardless of
what the number on the verb actually is, so both illusions of ungrammaticality and
grammaticality are predicted. It is also not immediately clear how to incorporate
the bias manipulation in the Marking and Morphing model. HSD2018 propose that
both goals will be achieved if we map Making and Morphing parameters to the
parameters of a drift diffusion model (Ratcliff, 1978). Drift diffusion models model
30As far as we understand, S(r) is always greater than 0. Thus, the actual logistic transformation
includes a negative bias term in order to bias the representation towards singular in the absence
of other sources of number information.
42
a binary decision process as a diffusion process (a continuous version of random
walk) starting at a random point between two decision boundaries. The amount
of evidence available to the decision taker determines how quickly the model walks
toward the correct decision boundary; however, due to the stochastic nature of the
process it is not guaranteed that it will reach it first: it may happen that enough
steps occur in the “wrong” direction so that the incorrect decision boundary is hit.
Now, we can map the S(r) value from the Marking and Morphing account onto the
strength of evidence parameter of the diffusion model: in this way, a more extreme
number value on the subject way would lead to (on average) faster and more accurate
grammaticality decisions31. The crucial assumption is that participants response
bias can be mapped to the starting point of the diffusion process. That is, if they
are biased to treat sentences as grammatical, the diffusion process will start closer
to the “grammatical” decision boundary.
Here is how this model would capture the results of the experiments. In
Exp.1, where by hypothesis participants have the strongest grammaticality bias,
the diffusion process would start close to the grammatical boundary. This would
lead to a situation where for grammatical sentences people would almost always
hit the grammatical boundary, even if the number marking on the target NP is
less unambiguously singular due to the influence of the lure: the model will have
31Notice that S(r) corresponds to the number information, however, the decision boundaries are
labeled “grammatical” and “ungrammatical”. It seems that the parser would have to decide ahead
of time, e.g. based on the information from the verb, which number value should correspond to
“grammatical” decision boundary.
43
little time to accumulate enough drift in the wrong direction. In the ungrammatical
sentences, the ambiguous number marking on the head noun as in (12c) would
make the drift towards the “ungrammatical” decision boundary slower than in (12c),
giving the process enough time to accumulate evidence in the wrong direction and
to occasionally hit the “gramamtical” boundary. Overall, we would expect to see
the asymmetry between grammatical and ungrammatical sentences: only for the
latter the number information on the lure would lead to an increased proportion of
incorrect responses.
Exp. 2 and 3, by hypothesis, neutralized the grammaticality bias, shifting
the starting point of the diffusion model to a position where it would be roughly
equidistant from both boundaries. In this situation, we would expect that in both
grammatical and ungrammatical sentences, more ambiguous number marking on the
target (as in 12b and 12d) would lead to identical slowdown of the diffusion process
in both grammatical and ungrammatical sentences. This would make it roughly
equally likely for the wrong decision boundary to be hit, leading to a symmetrical
distribution of incorrect responses. People would produce as many “grammatical”
responses in (12d) as they would produce ungrammatical responses in (12b), that
is, we would observe both illusions of grammaticality and ungrammaticality.
If the reasoning above is correct, it undercuts the argument for choosing
“structure-weak” memory models at several points. To begin with, it eliminates a
crucial argument against representational accounts: if they can capture the absence
of ungrammaticality illusions in certain conditions (which, arguably, correspond
to the conditions in which no ungrammaticality illusions have been observed), we
44
lose our strongest reason to prefer memory models. HSD2018 findings also provide
evidence against memory models. First, the fact that manipulating participants’
bias affects the rate of ungrammaticality illusions is prima facie unexpected in a
cue-based model. Indeed, if we think that a memory item that perfectly matches
the retrieval cues will always outcompete other memory chunks, in grammatical
sentences the correct agreement controller should always be retrieved32.
Second, the observed pattern of reaction times is hard for a cue-based model
32In principle, bias can be incorporated in cue-based models, but it is less clear to what degree we
would be able to capture all the patterns reported by HSD2018. E.g. one could hypothesize that
the weights for retrieval cues are adjusted dynamically depending on the current linguistic (and
potentially extra-linguistic) context. The size of the adjustment would correspond to grammatical
bias. In a context where most of the sentences are grammatical, the parser can be reasonably
sure about its parses, and thus may be willing to rely on structural cues. On the other hand, if
most of the sentences are ungrammatical, the parser may lessen its reliance on structural cues.
This will result in a situation in which the target has less of an advantage over the lure, and
due to stochastic noise, lures will have more chances to be retrieved. In sentences like (12a) this
should not affect participants’ responses: both the target and the lure match the verb, so whatever
noun is retrieved, the result can be judged as grammatical. On the other hand, in sentences like
(12b) retrieving the lure would lead to the “ungrammatical” response. Overall, we would observe
fewer correct judgments in (12b), than in (12a) - i.e. we would observe ungrammaticality illusions.
Unfortunately, this explanation would fail to capture the pattern of results in ungrammatical
sentences observed in HSD2018 Exp.3: when the response bias decreased, the proportion of correct
responses in the ungrammatical sentences increased. This is the opposite of what my ad hoc account
would predict: if the parser does reduce its reliance on structural cues, lures should become more
likely to be retrieved regardless of sentence grammaticality. Thus, we would expect that there will
be more incorrect judgments in both grammatical and ungrammatical sentences.
45
to fit. The critical observation is that if the lure matches the target in features,
the judgments are given faster, while LV05 model would predict a slow-down in
such configurations. This evidence is particularly interesting, since it aligns with
the results of the quantitative metaanalysis by Jäger et al. (2017), which we have
discussed earlier. Again, it is not the case that cue-based models cannot account
for these RT patterns: if we adopt the Engelmann et al. (draft4)’s suggestion that
linguistic prominence can affect memory chunks’ activation (see section 3.1) AND
if we assume that the lure is more prominent than the target, we would be able to
capture the HSD2018 RT patterns. But we do not see any arguments for why the
lure should be considered more prominent than the target, so practically speaking
these RT pattern still remain problematic for the LV05 model.
Thus, HSD2018 account and evidence pose interesting challenges for memory
accounts. We think, however, that in their current state they are still too weak
to completely rule memory models out. First, HSD2018 explanation relies on and
covers only acceptability judgment task. However, the absence of ungrammaticality
illusions has been reported in studies relying on other experimental techniques,
and it may not be straightforward to extend HSD2018 account to cover these (as
the authors themselves discuss). HSD2018 argue that self-paced reading might be
accommodated relatively easily: instead of deciding on whether the sentence is
grammatical or ungrammatical, people could decide on whether to press or not
to press the button to uncover the next word. Eye-tracking might be harder to
accommodate, since it is less clear what are the decisions that people are making
during reading. Potentially it could be something along the lines of “stay on the
46
current word / make a progressive saccade / make a regressive saccade” etc. But
it is clear that the decisions are unlikely to be binary and the model would have
to be further complicated to allow for this. Finally, EEG results (e.g Xiang et al.,
2008; Tanner et al.), might be the trickiest to cover, since it is not immediately clear
how to talk about observed ERP patterns in terms of underlying decision making
processes.
More generally, HSD2018 model only accounts for agreement data. One could
claim that it should do so, since lure-match effects in subject-verb agreement and
reflexive resolution are separate phenomena; this is the route Sloggett (2017) takes.
From the perspective we take in this thesis this is rather a disadvantage. It is not
clear how the model would apply to reflexives resolution. First of all, as Jäger
et al. (2017) suggest, there is very little evidence for illusions of ungrammatical-
ity in reflexive resolution (in comparison, the same analysis does provide evidence
for illusions of ungrammaticality in agreement attraction). Second, it is not clear
whether Marking & Morphing account could explain lure-match effects in configu-
rations used to study reflexives resolution. Often the lure is structurally higher than
the target (e.g. it is located in the matrix clause and the target - in the embedded
complement clause): thus, in order for the features of the lure to influence the tar-
get, we would need to say that the features information from the lure can percolate
downwards. As Wagers et al. (2009) point out, Eberhard et al. (2005) do indeed
make this assumption. But even in this case, the lure is more structurally distant
from the target than in the agreement cases, where the lure is typically embedded
in a PP inside the subject NP. Given that Marking & Morphing account assumes
47
that the influence of the percolating information reduces with structural distance,
in the reflexives cases the lure may be too far from the target to noticeably affect its
representation. Finally, it is not clear how Marking & Morphing would explain the
fact that lure-match effects are not observed in 1-feature target mismatch configu-
rations, but are observed when the target mismatches the reflexive in two features.
It would be easier for the information from the lure to bring the mismatching target
closer to the match with the reflexive in 1-feature mismatch conditions, and thus,
the opposite pattern of the results would be predicted.
To sum up, HSD2018 proposal shifts the focus from “structure-defeasible” cue-
based models back to “structure-strict” representational ones, and posits interesting
problems for memory accounts. On the other hand, it also gives less universal
coverage than the framework offered by cue-based models. I do not feel that the
proposal is developed enough to strongly sway the odds against cue-based models,
but it may be an important first step towards alternative accounts. As we will see
now, the same tendencies are evident in Sloggett (2017) account of the reflexive
data.
1.4.2 Reflexives processing is qualitatively different from agreement
The second argument against uniform application of “structure-defeasible”
memory models suggests that different dependencies (and in particular - subject-
verb agreement and reflexive resolution) rely on qualitatively different mechanisms.
This argument has been present in the literature for some time. Originally, it was
48
based on the fact that lure-match effects are rarely observed in reflexives resolution,
as well as on some data indicating that the search for the antecedent may not be
parallel, as cue-based models assume, but rather serial (Dillon, 2011; Dillon et al.,
2013; Dillon, 2014). We will not discuss the previous arguments in detail, focusing
instead on two recent studies.
Jäger et al.’s meta-analysis provides evidence for qualitative differences be-
tween dependencies. It suggests that for reflexives there is no evidence in the avail-
able data for lure-match effects in grammatical sentences33. Second, in ungrammat-
ical sentences, the evidence suggests that people are slower when the lure matches
the reflexive. Both empirical patterns contradict the predictions of the LV05 model.
Moreover, both patterns differ from the results of the analysis on the subject-verb
agreement data. This discrepancy might be indicative of the underlying differences
between dependencies.
We consider the evidence provided by Jäger et al. (2017) as only tentative
due to several caveats of their analysis. First, as the authors point out themselves,
it is essentially observational, therefore any conclusions should be confirmed using
experimental studies specifically designed with this goal in mind. Second, the quan-
titative meta-analysis relied only on first-pass reading times for the eye-tracking
studies, because “it is the most commonly reported eye-tracking measure in the
psycholinguistic literature and arguably reflects early cognitive stages of dependency
formation” (Jäger et al., 2017, p.323). However, lure-match effects in reflexive reso-
33In a way, reflexives are being more catholic than the Pope (subject-verb agreement) - it appears
that for reflexives, illusions of ungrammaticality are truly absent
49
lution appear to be quite variable in timing. E.g. Parker et al. (2017) only observed
effects in first-pass reading times in two out of three experiments. Similarly, in
Sloggett (2017) the time course of lure-match effects varied across experiments: in
two of them, the effects were observed relatively early, (first-pass or regression path
times at the critical region), in the other two, the effects became evident later (total
times at the critical region or regression path at the spillover region). It is not quite
clear whether such differences are due to random variability across participants or
experimental items, or whether they reflect meaningful differences in the reflexive
resolution process. Whatever the case, an analysis based only on first-pass RTs will
miss some of the effects reported in the literature. Finally, Jäger et al. (2017) re-
view does not include Sloggett (2017) data, presumably because it was not available
at the time of writing. Sloggett (2017) showed that lure-match effects observed by
PP2017 can indeed be reliably observed (modulo the discussion about the exact con-
figurations in which they arise). It is possible that with these data the quantitative
analysis would have given different results.
Sloggett (2017) The evidence for qualitative differences between subject-verb
agreement and reflexives presented by Sloggett (2017) is more extensive. He builds
on and expands empirical observations made by Parker and Phillips (2017). In
contrast to the retrieval error explanation for agreement attraction, Sloggett argues
that the observed lure-match effects in reflexives processing are a manifestation of
a completely grammatical anaphora resolution strategy, namely, logophoric inter-
pretation of reflexive pronouns. Logophors are pronouns which refer to the person
50
“whose speech, thoughts, feelings, or general state of consciousness are reported”
(Clements, 1975)34.
Sloggett’s hypothesis is motivated by three crucial observations:
1. Lure-match effects are not observed when the lures are subjects of perception
verbs, even if the target mismatches the anaphor in two morphological features.
However, the identity of the matrix verb does not matter if the lure refers to
the only center of consciousness in the sentence.
2. Lure-match effects are eliminated or at least weakened if the target is an
indexical pronoun like “I” or “you”.
3. As often as in 30% of the cases, when asked a comprehension question probing
the reflexive resolution, people choose the answer compatible with the lure
being the intended antecedent, even when the target fully matches the reflexive
in morphological features.
34The term “logophor” was initially introduced by Hagège (1974) to describe morphologically
distinct pronouns in a number of languages spoken in Africa (e.g. Ewe, Yoruba, Igbo; see Culy
(1994) for an extensive list of relevant languages). However, the use later was extended to denote
non-clause-bound reflexive pronouns in a number of languages (e.g. Japanese zibun, Chinese ziji,
Icelandic sig). In this second sense, the term has also been applied to English, to describe the
pronouns in configurations like: “Max said that the queen invited both Lucie and himself for
tea.”(e.g Reinhart and Reuland, 1993). Notice that a priori it is not guaranteed that “logophors”
in African languages and non-clause-bound reflexives rely on the same set of constraints (or on the
same processing routines), thus one must be careful not to conflate the facts pertaining to the two
phenomena.
51
Here is how logophoric hypothesis can explain these patterns. First, lure match
sensitivity to the type of the embedding verb appears to conform to a pattern
reported for other languages. Culy (1994) suggested the following implicational
hierarchy for a number of languages spoken in West Africa: Speech < Thought <
Knowledge < Direct perception. That is, if a language allows subjects of verbs
on the right end of the scale to be taken as antecedents for logophors, it will allow
the same for the subjects of verbs lower on the hierarchy. The first pattern is in line
with the Culy hierarchy; and the fact that the type of the verb does not matter if the
lure is the only animate entity in the sentence is also naturally accommodated: if
there is a single conscious antecedent in the discourse, the logophor “has no choice”.
The second pattern closely resembles “person blocking”, a syntactic phenomenon
observed in Chinese long-distance binding of the reflexive “ziji”. As Huang and
Liu (2001) discuss, “ziji” allows antecedent outside of its local domain, as in (13a).
However, an intervening first or second person pronoun may block this resolution
option (13b)35. Huang and Liu argue that these effects arise when “ziji” is used as
a logophor, and not as a syntactic reflexive. Finally, the third piece of evidence is
explained almost for free: if resolving the reflexive to the lure is a representation
of a grammatical strategy, we should expect lure-match effect to appear even in
grammatical sentences.
(13) a. Wo/nii danxin Lisij hui piping zijii/j.
I/youi worry Lisij will criticize SELFi/j.
35This is not the only environment where blocking effects appear, but it is the most relevant one
for the current discussion.
52
I/you worry that Lisi might criticize me/you/herself.
b. Zhangsani danxin wo/nij hui piping ziji∗i/j.
Zhangsanii worry I/youj will criticize self∗i/j.
Zhangsan worries that I/you might criticize my/yourself.
To formalize this hypothesis, S2017 uses a modified version of PP2017 cue-based
retrieval account. On the memory retrieval side, the two accounts are virtually
identical, with one crucial difference: S2017 makes his model “structure-strict”,
by assuming that structural features act as gating features and only grammatical
antecedents are ever retrieved. As far as I can tell, he does not discuss how this
difference is implemented in the model (higher weights on structural cues? different
cue combinatorics scheme?)
However, the main explanatory power of S2017 comes from a suggested modi-
fication to the grammar of English. Sloggett suggests that a phonologically null op-
erator, OPlog, is located in the left periphery of complement clauses (see Charnavel
and Sportiche, 2016, for a related proposal). By hypothesis, it tracks perspective
centers of the utterance. Each appropriate36 antecedent is mapped onto one of the
three perspective “roles” from Sells (1987): source, self and pivot. The first role
corresponds to the participant acting as the source of information, the second - to
the participant whose mental state is reported and the third one - to the participant
whose (physical) location is assumed as the reference point. The roles form a hier-
archy, such that a participant takes on all the roles below the role that is assigned to
him/her. E.g. if somebody acts as self, then he also takes the role of pivot, but
36Minimally, an animate entity.
53
not that of source. OPlog obligatorily refers to the highest specified role on this
hierarchy. I.e. OPlog will refer to whatever participant bears the role of source;
if there are no such participants, it will look for self and, failing that, for pivot.
Finally, S2017 suggests that these roles are assigned probabilistically. E.g. speakers
are most likely to be mapped onto source, but may sometimes get mapped onto
self; the reverse could hold for indexical pronouns.
Notice that binding by OP 37log is syntactically local with respect to the re-
flexive. Thus, the non-local binding is just an appearance, created by the special
referential properties of the operator. But if OPlog is a licit binder, why are non-
local antecedents so inaccessible to native speakers? S2017 explains this in terms
of the feature composition of the operator: it is assumed to be underspecified for
φ-features. This ensures that it is a worse match to the retrieval cues compared to
the overt target antecedent. As such, it is less likely to be retrieved; importantly, it
does not mean that its retrieval is impossible, just that it will happen only rarely,
perhaps, when stochastic noise will happen to bias memory activations in the right
direction.
Here is how this formalization would derive the three crucial patterns I men-
tioned in the beginning of the section. The effect of the embedding verb stems from
the way participants are mapped onto Sells’s roles. Speech verb subjects are likely
to be sources, so OPlog will most often take them as antecedents. On the other
37Or at least “more local” than for the lure: OPlog is situated in the same clause with the
pronoun. However, it does not occupy a typical position for an antecedent, since it is not located
in an argument position.
54
hand, perception verb subjects are more likely to be pivots. Under the assumption
that only one participant can be mapped on any given role, by the time the reflex-
ive is encountered, the control of the pivot will be taken by the embedded subject.
Since there will be no higher roles specified, this is what OPlog will refer to, and non-
local interpretation will not be available. Person blocking effects are explained in a
similar way. S2017 suggests that although speech verb subjects tend to be mapped
onto source’s and indexical pronouns - onto self, sometimes the mapping gets re-
versed due to its stochastic nature. It is exactly in these cases that we will observe
person blocking effects. Finally, since the resolution process is assumed to follow
grammatical constraints, it should come as no surprise that people are able to access
non-local interpretations even when the (overt) local target completely matches the
features of the reflexive.
1.5 Parker & Phillips (2017) vs. Sloggett (2017)
1.5.1 Empirical observations
We have seen that the recent work has suggested reasons to shift in the direc-
tion of “structure-strict” models applicable to isolated linguistic phenomena. They
rely on two types of arguments: a) agreement attraction data does not constitutes
evidence for (and potentially is evidence against) memory models; b) reflexive res-
olution relies on different mechanisms and thus there is no reason to capture it and
subject-verb agreement with the same kind of “structure-defeasible” model.
While this shift may turn out to be in the right direction, I consider the
55
universality of “structure-defeasible” memory models too attractive to easily give
it up. Thus, my goal in this thesis is to look for further evidence supporting or
contradicting the recent claims. In order to do so, I will focus on the two accounts
of lure-match effects in reflexive resolution, suggested by Parker and Phillips (2017)
and Sloggett (2017), which I have already discussed. In this last section of the
introduction, I discuss whether any of the empirical facts present a fundamental
problem for the accounts and whether we have strong reasons to prefer one over the
other.
Altogether, I take the following 7 empirical observations from the previous
research to be important (I mark in parentheses the studies they are coming from):
E1 In configurations like The boy said [that the girls like himself] people
read sentences with feature matching lures faster if the target mismatches the
reflexive in two features. This does not happen when the target fully matches
the reflexive. (PP2017, S2017)
E2 The speed up also does not occur when the target mismatches the reflexive in
a single feature. (PP2017)
E3 Lure-match effects also appear in configurations like The boys [that the
girl liked] praised herself in the cases when the target mismatches the
reflexive in two features. It is not known whether the degree of target match
modulates lure-match effect in these cases. (PP2017)
E4 Lure-match effects are not observed when the lures are subjects of perception
56
verbs, even if the target mismatches the anaphor in two morphological features.
(S2017)
E5 However, the identity of the matrix verb does not matter if the lure refers to
the only center of consciousness in the sentence. (S2017)
E6 Lure-match effects are eliminated or at least weakened if the target is an
indexical pronoun like “I” or “you”. (S2017)
E7 In an interpretation task, people answer interpretation questions in a way
which suggests that they treat the lure as the antecedent as often as in 30%
of the cases, even when the target fully matches the reflexive in morphological
features.(S2017)
PP2017 interpret findings E1, E2 and E3 as evidence for faulty memory access
in a cue-based memory. S2017 agrees that E2 should be explained in terms of the
properties of the memory access. However, he assumes that retrieval operations only
ever return structurally licit antecedents, i.e., his account is “structure-strict”. S2017
suggests that the majority of the facts (except for E3) should be seen as evidence for
a grammatical strategy of reflexives resolution. In his explanation, a phonologically
null operator in the left periphery of complement clauses tracks discourse prominent
entities and can create appearances of non-local reflexive binding.
1.5.1.1 PP2017
PP2017 account naturally accommodates observations E1, E2 and E3. Prima
57
facie, it would appear that it is unable to explain E4, E5 and E6, since they suggest
that lure-match effects may depend on things other than the representation of the
lure, the target and the reflexive. However, I will argue that in fact PP2017 account
could explain these observations. I will start with discussing whether the symbolic
component38 of the ACT-R model can capture S2017 effects.
To capture E4, we would have to ensure that the information about the verb
enters the cue-matching process in some way. Presumably, it does not do it directly:
the parser is likely not looking for verbs when it tries to resolve a reflexive. But we
could encode the information about the verb on its subject, e.g. by using a feature
like “+ subject of a speech verb”. The reflexive would include this feature in the
set of retrieval cues, biasing retrieval against subjects of other types of verbs. While
possible, I consider this approach too clumsy to be our first choice for a few reasons.
First, it requires some additional processing: during the encoding stage, the parser
has to retrieve the subject at the verb and update the subject’s representation with
the verb type information39. Second, the information about whether the verb is a
speech verb or not may only be useful for logophoric pronouns. But at the point
where it has to be encoded, the parser has no idea of whether a reflexive pronoun
will come up at all, even less about whether it will receive logophoric interpretation.
Thus, often the information will be encoded, but not used, and if we think that
memory space available to the parser is limited, using such redundant encodings
38I.e. operations defined in terms of features, procedural rules etc.
39Although the overhead may be minimal, if we assume that the subject is retrieved at the verb
for integration purposes anyway.
58
would seem like an inoptimal strategy to adopt. Third, the feature I suggest is
essentially privative. It is fine if we just want to distinguish between speech and
perception verbs. But the Culy (1994) hierarchy that S2017 experiments are inspired
by includes other verb types, e.g. verbs of thought and knowledge. Experiments
would be required to see whether these verbs support or block lure-match effects,
but if at least one more class of verbs does support them, a privative feature of the
sort I suggested would not work anymore. Instead, a more general feature like “+ a
subject of logophoric verb”40 would be needed. This would not be too far fetched in
languages with grammaticized logophoric pronouns, but would more questionable
in English. Alternatively, we could use multiple features, one per verb type (e.g. “+
subject of perception verb”, “+ subject of knowledge verb” etc.). But in this case
the set of retrieval cues would have to include several verb-type related features,
leading to a situation where no antecedent would be a perfect match to the set of
retrieval cues. One may also wonder whether it is only the types of verbs on the
Culy (1994) hierarchy that even put a feature on their subject. If it is the case, the
parser should essentially have access to cross-linguistic generalizations (“these verbs
are logophoric in other languages, so I need to pay attention to them in English”).
If all verbs put some information about their semantic class on the subject, this
again raises the question of whether the encodings are optimal from the point of
view of memory space usage.
A second approach would be to avoid using features on the verb’s subject,
40Somewhat sloppily, I use “logophoric verbs” to mean “verbs allowing their subjects to serve
as antecedents for logophoric pronouns”
59
instead accessing the verb’s information directly. The following antecedent retrieval
algorithm could work: first, retrieve a suitable NP (e.g. matching features of the
reflexive). Then, using the information on this NP, retrieve the verb it is the subject
of, check whether the verb is the verb of speech or perception. Finally, depending
on the result, either return or do not return the NP as the reflexive antecedent.
It can not be the algorithm which is attempted first, otherwise it would exclude
grammatical local and c-commanding antecedents which happen not to be subjects
of speech verbs. Therefore, it is more plausible as a repair algorithm, for the cases
when the parser fails to find a licit local antecedent. Interestingly enough, as we
discuss in section 5.1.3, some patterns in the data may indeed indicate that lure-
match effects are due to repair processes.
Overall, the fact E4 could be captured even at the symbolic level of ACT-R.
It may be harder to capture the fact E5 (the type of embedding verb is irrelevant if
the target antecedent is inanimate) while staying on the same level. I discuss some
possibilities below but conclude that they may be too convoluted. Basically, we
would have to manipulate the representation of the lure (in my first approach) or
the processing procedures (in my second approach) based on whether the lure is the
only consciousness center in the sentence. This could be done, but would require
introducing yet another feature, something like “+ conscious”. During anaphora
resolution, the parser would retrieve all antecedents with such feature, and then, if
there is more than one, either change the representation of the lure 41 or to change
41Which would require retrieving it accurately, which may not be trivial in a “structure-
defeasible” model
60
the processing strategies by removing the check for verb type. While this is all
possible, capturing E5 in symbolic terms appears too ad hoc. As I discuss slightly
later, though, these effects could be captured rather naturally by the sub-symbolic
level of the model (i.e. in terms of the continuous activation values).
Capturing the fact E6 at the symbolic level is also problematic. We could
assume that indexical pronouns are underspecified for gender and mismatch the re-
flexive in only one feature, person. However, as S2017 discusses, this may not go
through. Sloggett argues that this contradicts the observation that in his experi-
ments sentences with indexical pronouns were judged as slightly less acceptable and
were read slightly slower than sentences with it as the target (which presumably
mismatches himself/herself in two features, animacy and gender). Alternatively, we
could assume that the parser is aware of the presence of an indexical pronoun in
a structurally intervening position with respect to the lure. But that would either
mean that the parser tracks indexicals AND their position relative to other elements
of the sentences, which is a priori implausible, or that it first accurately retrieves
the target (again, not unproblematic given that it mismatches the set of retrieval
cues), determines that it is an indexical and for some reason stops looking further,
even though the retrieved target mismatches the reflexive.
Finally, capturing E7 may be most problematic. In grammatical sentences the
target always matches the morphological features on the reflexive at least as well as
the lure does, and in addition only the target matches the structural cues, even if
they are down-weighed. We do not expect to see any considerable amount of lure
retrievals in such configurations even when the lure fully matches the morphological
61
features on the reflexive, even less so when it does not. However, S2017 reports
roughly 30% of the answers compatible with non-local reflexive resolution in the
first case, and roughly 25% in the second. This pattern is hard to explain solely
by the dynamics of memory system, unless one assumes that the amount of noise
in the system is so high that it ignores a perfectly matching item 30% of the time.
It seems odd to assume that memory access is so inefficient: if it performs that
poorly in perfect conditions, what would it performance be in real-life situation
with potentially less certainty about what the correct outcome is?
Summing up, explaining the empirical effects observed by S2017 purely in
terms of memory processes is not impossible, but is rather challenging. But notice
that these approaches stayed on the symbolic level of the ACT-R model. Now I
would like to argue that it is potentially easier to explain all of the empirical facts
if we take a look at the subsymbolic level, i.e. activation dynamics. In a basic
ACT-R model, the only way to select an item is to make it more active than all the
other competitors. Usual ways of doing so include raising baseline activation due to
frequent and/or recent retrievals and getting the boost from matching retreival cues
during memory access. As I have discussed, none of these mechanisms would be
able to differentially change the lure’s activation based on context (e.g. the type of
the embedding verb). However, it is possible that activation can be directly affected
by other factors as well, e.g. linguistic prominence (Engelmann et al., draft4). One
could hypothesize that subjects of speech verbs are more prominent in the discourse
being sources of information. If the boost in activation from this source is sufficient,
only the subjects of speech verbs may act as efficient lures. One could also argue
62
that animate entities are more prominent than inanimate - that would explain why
the type of the embedding verb does not matter if its subject (the lure) is the only
animate entity in the sentence. Finally, it is quite plausible that first and second
person indexical pronouns are more prominent than third-person entities, being more
central to the communicative situation - this could explain person blocking effects.
Thus, discourse (or other related kind of) prominence might in principle explain
effects for which S2017 postulates OPlog. I have to admit that these speculations
remain only that - speculations - unless we are a) able to quantify the hypothesized
changes in prominence and map them to specific values within an ACT-R model
and b) show by simulations that the tentative predictions I make above indeed hold.
To conclude, empirical facts that S2017 uses as a strong empirical evidence
for his model could potentially be explained even without recurring to OPlog and
the claim that lure-match effects in reflexive resolution have grammatical nature.
Explicit simulations and more theoretical work are required to test whether my way
of accounting for these effects within a “structure-defeasible” cue-based model is
viable.
1.5.1.2 S2017
S2017 account can accommodate all of the empirical facts listed above, except
for E3. S2017 crucially relies on a null operator tracking prominent discourse entities
in the left periphery of complement clauses. However, in Parker and Phillips (2017)
Exp.2 the lure is embedded in a relative clause. Without OPlog present, only the
63
local target should be returned during retrieval, and no lure-match effects should
be observed. Sloggett has to fall back on an ad hoc explanation. He suggests that
these effects represent a case of sub-command binding, a phenomenon occurring
in Chinese. In sub-command configurations, an animate NP embedded inside an
inanimate subject may still bind a reflexive. If this explanation turns out to be
false, we will have to conclude that even if some lure-match effects reflect logophoric
interpretations of the reflexives, some others still arise as a result of processing errors.
That alone would be enough to argue for “structure-defeasible” models (following
PP2017 and contra S2017).
Could the OPlog account be extended to cover the lure-match effects from
lures inside relative clauses? In principle, nobody prevents us from saying that
OPlog is located in the left periphery of all clauses, not just complement ones.
This possibility would be supported by Charnavel and Huang (2018) who argue
that sub-command binding is actually an instance of logophoric binding. If that
is the case, and if one assumes that all instances of logophoric interpretations are
mediated by something like OPlog, S2017 account would be able to explain PP2017
findings in a way analogous to the explanation of the fact E5: since in their stimuli
the embedded lure was the only animate entity, it would also be the only possible
logophoric antecedent. But on the other hand, this account would fail to explain
the contrast in (14 Huang and Liu (2001): since, by hypothesis, OPlog is able to
refer to Zhangsan in the first case, it is not clear why it would not be able to do
so in the second. It would be hard to argue that OPlog is only present in the first
case: by the time the parser reaches the embedding NP, the semantics of which
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licenses the logophoric interpretation42, OPlog would have already been introduced
to the parse. Thus, while postulating OPlog in all clauses could improve empirical
coverage of S2017 account, it would also introduce new problems. In addition, as
S2017 himself notices, it would go against the tendency for logophoric antecedents
to be subjects of attitude predicates. I will discuss these issues in more detail in
Chapter 2.
(14) a. Zhangsani de baogao biaoshi tamen dui zijii mei xinsin.
Zhangsan DE report indicate they to self no confidence
Zhangsans report indicates that they had no confidence in self.
b. *Zhangsani de shibai biaoshi tamen dui zijii mei xinxin.
Zhangsan DE failure indicate they to self no confidence
Zhangsans failure indicates that they have no confidence in him.
With respect to the fact E7, although S2017 uses it to support his account, this
empirical observation may be even more problematic for him than for PP2017.
According to Sloggett’s hypothesis, the silent logophoric operator does not carry
any φ-features. Thus, while in the PP2017 scenario the target had a single feature
advantage over the lure (only the target being the reflexive’s clausemate), in S2017
scenario the target is a better match than OPlog in at least two features - gender
and number (and potentially person and/or animacy). Thus, one would have to
assume an even noisier retrieval system than in PP2017 scenario to account for
these patterns.
42As Huang and Liu (2001) put it: “This is because [the first sentence] implies that Zhangsan
himself indicates that they had no confidence in him. (If his report indicates P then he indicates
P.) No similar implication holds of the unacceptable [second sentence].”
65
1.5.2 Empirical coverage: summary
To sum up, neither account covers all of the available data. Nor is any a clear
winner. The original PP2017 account fails to explain the evidence for factors other
than the number of matching features affecting lure-match effects. However, I have
suggested a way in which this account could be extended to cover most of the prob-
lematic evidence. The S2017 account covers most of the data to begin with, but
extending it to cover the data from the non-c-commanding lures is not straightfor-
ward. It either requires introducing an additional mechanism, not tightly related to
the main proposal, or else complicating the interpretation of other empirical facts.
In addition, I have argued that the interpretation data reported by S2017 may be
problematic for both accounts.
1.5.3 My experiments
The main body of the thesis is an attempt to tease the two accounts apart
using additional evidence. I report the following experimental work.
First I investigate one of the weak points of the S2017 account. Chapter 2
reports the results of an experiment investigating the configurations with the lures
inside relative clauses, which Sloggett’s account does not cover directly. S2017 argues
that in this instance another grammatical option is used (sub-command binding,
which I discuss in more detail in the corresponding experimental chapter). This
grammatical option crucially requires the head of the relative clause to be inanimate,
and indeed, this is the configuration PP2017 had. Therefore, I am going to test same
66
configurations but with animate RC heads. To preview, the results will be taken to
support PP2017 account.
Second, given this support, I investigate further predictions of PP2017 account
to validate the conclusions from Chapter 2. The experiments by PP2017 do not
provide reliable evidence regarding the use of c-command information. Their results
are compatible either with a model which faithfully encodes c-commands but does
not manage to use this information to rule out illicit antecedents, and a model which
encodes c-command information only approximately (thus not covering relevant
cases) but follows this approximation faithfully. I attempt to distinguish between
these two possibilities by considering the case of quantificational (QP) lures. As
I discuss in detail in Chapter 3, experimental evidence suggests that QPs in the
wrong position (non-scoping/non c-commanding) cannot bind pronouns like “him”
(Kush, 2013). From the syntactic point of view, binding works in the same way
for pronouns and reflexives. If the c-command information fails to uniquely direct
the parser’s decisions, as PP2017 suggest, we should observe lure-match effects even
from non-c-commanding QP lures. If, on the other hand, some approximation, such
as Kush et al. (2015) accessible is used, non-c-commanding QP lures will not
elicit lure-match effects. Third, and finally, I perform a series of two experiments
addressing an issue I ran into: I failed to find strong evidence for lure-match effects
even from NP lures. Thus, I perform a direct replication of PP2017 Experiment 3
to determine the robustness of the effects they report. These replications also help
to verify whether extra-syntactic factors, such as (non-)nativeness of experimenter,
might have affected the results. If such factors do affect lure-match effects, it would
67
be more readily compatible with PP2017 account. Two experiments addressing
replication issues are reported in Chapter 4.
68
Chapter 2: Interference effects from non-c-commanding lures
I am going to start the thesis with investigating the only strong evidence
against S2017 account: lure-match effects for the lures embedded inside a relative
clause (we will call them “RC-lures” for short), e.g.“the students” in “The tea that
the students drank calmed themselves” (Parker and Phillips, 2017, Exp.2). This
evidence is problematic for S2017: his account crucially relies on a null operator
in the left periphery of complement clauses to account for lure-match effects and
says nothing about relative clauses. To save the situation, S2017 suggests an ad hoc
explanation: perhaps, the lure-match effects observed with RC-lures reflect a gram-
matical strategy of sub-command binding (see below). While different in substance,
this explanation is similar in spirit to the main S2017’s account: it attributes lure-
match effects to a grammatical mechanism, and not to a faulty processing routines.
It is important to empirically test this suggestion. If it turns out that S2017 is in-
correct and we have to invoke processing errors to cover that evidence, the support
for his account weakens. At the very least, it would have to be modified to explain
why in some cases the structure does accurately constrain the search and in others,
very similar cases, it does not. In what follows, I briefly explain the phenomenon of
sub-command binding and discuss my experiment testing S2017’s hypothesis.
69
Sub-command binding is a grammatical phenomenon observed in Chinese.
Several empirical facts are relevant for this discussion. First, the anaphor ziji re-
quires animate antecedents (Tang, 1989)1, as demonstrated by (1).
(1) a. Wo taoyan ziji.
I dislike ANA
I dislike myself.
b. Xiaomao zai tian ziji de lian.
little cat is lick ANA DE face
The kitten is licking its own face.
c. *Men guanshang le ziji.
door close PER ANA
The door closed itself.
Second, ziji can have a non-c-commanding NP (say, NP1) as its antecedent, as long
as this NP1 is embedded within another NP2 which does c-command ziji - this
phenomenon is referred to as “sub-command binding” (2). Third, sub-command
binding is only possible if the embedding NP2 is inanimate (3) Tang (1989).
(2) a. [[Zhangsani de] jiaoao]j hai le zijii/∗j
Zhangsani DE pride hurt PER ANAi
Zhangsani’s arrogance harmed himi
b. [[Zhangsani zuoshi xiaoxin de] taidu]j jiu le zijii/∗j yiming
Zhangsan do thing careful DE attitude save PER ANA one life
Zhangsan’s cautious attitude saved him.
(3) a. [[Zhangsani de] baba]j dui ziji∗i/j mei xinxin.
Zhangsan DE father to ANA no confidence
Zhangsan’si fatherj has no confidence in himself∗i/j
1At least, this is the accepted generalization. But see the discussion of Charnavel and Huang
(2018) later in this section.
70
b. [Zhangsani pengdao de] nage ren]j dui ziji∗i/j mei xinxin
Zhangsan meet DE that-CL man to ANA no confidence
The mani that Zhangsanj met had no confidence in himself∗i/j
To capture these patterns, Tang (1989) argues that in Chinese the structural re-
quirements on the anaphor’s binders should be slightly relaxed. She suggests the
following binding principles for the Chinese:
A. β sub-commands α iff
1. β c-commands α or
2. β is an NP contained in an NP that c-commands α or that sub-
commands α, and any argument containing β is in subject position.
B. A potential binder for α is any NP which satisfies all conditions
of being a binder of α except that it is not yet coindexed with α.
C. A reflexive α can be bound by β iff
1. β is coindexed with α, and
2. β sub-commands α, and
3. β is not contained in a potential binder of α.
The sub-command stipulation obviously captures the structural requirement.
The condition C3 together with the definition B2 helps to explain why sub-command
binding is only possible in (2), but not in (3): only in the first case the embedded
antecedent is NOT contained in a potential binder of ziji.
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Parker and Phillips (2017) only used inanimate matrix subjects when investi-
gating RC-lures. Given this, Sloggett suggests that the sub-command binding can
underlie lure-match effects from RC-lures observed by Parker and Phillips (2017).
As S2017 himself points out, if this hypothesis is correct, the lure-match effects
should not be observed (or at least be observed to a smaller degree) with the ani-
mate matrix subjects. Investigating such configurations is the primary goal of the
current chapter. However, before turning to the presentation of the experiment, I
discuss a potential theoretical counter-argument to S2017 suggestion.
Charnavel and Huang (2018) argue that the cases of sub-command binding in
fact represent instances of logophoric interpretation of the pronoun. They observe
(following Huang and Liu (2001)) the following contrast:
(4) a. Zhangsani de baogao biaoshi tamen dui zijii mei xinsin.
Zhangsan DE report indicate they to ziji no confidence
Zhangsans report indicates that they had no confidence in self.
b. *Zhangsani de shibai biaoshi tamen dui zijii mei xinxin.
Zhangsan DE failure indicate they to self no confidence
Zhangsans failure indicates that they have no confidence in him.
They argue that the contrast arises because in (4a) the matrix subject creates con-
ditions for a logophoric interpretation: namely, it allows for an implication that
Zhangsan’s perspective is conveyed by the report, while no such implication is pos-
sible in (4b). So, only in the first case Zhangsan is the perspective holder in the
sentence, which makes it a possible antecedent for a logophoric pronoun.
Charnavel and Huang (2018) support their claim with the results of an ac-
72
ceptability judgment study. They first show that ziji is acceptable with inanimate
antecedents, in contrast to generally accepted claims in Tang (1989): sentences like
(5a) received high ratings (4.69 on average, with the judgments being made on a
scale between 1 (worst) to 6 (best)). Then they show that sentences with inanimate
sub-commanding antecedents (5b) receive (significantly) lower ratings as compared
to (5a) (3.35 on average). From this they conclude that apparent sub-command
binding results from the logophoric interpretation of the pronoun: logophoric pro-
nouns require their antecedents to be animate, while ziji does not. Thus we only
expect the inanimate sub-commanding antecedent to cause judgments to degrade if
ziji is being interpreted logophorically.
(5) a. [Zhe ke shu de shuguan]i tai chen, ya wan le zijii.
this CL tree DE tree crown too heavy, burden bent ASP REFL
[The crown of this tree]i is too heavy. Iti bent itselfi.
b. *[Zhe ke shu]i de guoshi ya wan le zijii.
this CL tree DE fruit press bent ASP REFL
The fruits of [this tree]i bent iti.
If Charnavel and Huang (2018) conclusions are correct, PP2017 results have to
reflect an extra-grammatical strategy: RC-lures should only be accessible when the
matrix subject creates appropriate logophoric context. However, Parker and Phillips
(2017) used stimuli like “The broken zipper that the skilled tailors tried to fix pinched
themselves” or “The safety net that the brave policeman used saved themselves”.
Arguably, in such sentences the embedding NPs do not make the embedded NPs
prominent perspective holders (in any case, no more than “failure” in (4b)). Thus,
73
the lure-match effect Parker and Phillips (2017) can not be reduced to the properties
of syntactic configuration.
While Charnavel and Huang (2018) arguments are interesting, we think that
they are insufficient to reduce all cases of sub-command binding to instances of
logophoric interpretations. First, Tang (1989) gives the following example:
(6) a. [[Zhangsani de] babaj de] qian]k bei Ziji∗i/j/∗k de pengyou touzou
Zhangsan DE father DE money BEI ANA DE friend steal
le.
PER
Zhangsan’s father’s money was stolen by his friend.
In this example it is again not clear how “money” would encourage to treat “Zhangsan’s
father” as a prominent perspective center, in the way that “report” in “Zhangsan’s
report” does. Second, as Huang and Liu (2001) discuss, logophoric interpetation
of ziji is subject to person-blocking effects (i.e. if a first or second person pro-
noun intervenes between ziji and another antecedent, ziji obligatorily refers to the
first/second person pronoun) (7). However, such effects are not present in cases of
sub-commanding antecedents (8).
(7) a. Zhangsani dui wo shuo zijii piping-le Lisi.
Zhangsan to me say self criticize-Perf Lisi
Zhangsani said to me that hei criticized Lisi.
b. *Zhangsani shuo wo piping-le zijii
Zhangsan say I criticize-Perf self
Zhangsani said that I criticized himi
(8) Zhangsani de biaoqing gaosu woj [zijii/∗j shi
Zhangsan DE expression tell me self is innocent
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wugude].
Zhangsanis [facial] expression tells me that hei is innocent.
These counter-examples to Charnavel and Huang (2018) conclusions still make it
possible for S2017 hypothesis to be viable. Therefore, I now turn to its experimental
evaluation.
2.1 Experiment 1
2.1.1 Participants
53 members of University of Maryland participated in the experiment for a
class credit or a payment of $12 (11 M, 42 F; age range: 18-27; mean age: 20.1,
SD: 1.76). The experimental session took around 45 minutes, including setup and
calibration. I excluded data from 3 participants: two failed to finish the experiment
due to problems with calibration and for one the recorded reading patterns were too
erratic to be used. The remaining 50 participants entered the analysis2.
2.1.2 Materials
The study used 2x2 factorial design with target animacy (whether the ma-
trix subject was animate or inanimate) and lure match (whether the lure matched
or mismatched the reflexive in features) as factors. Overall, I constructed 24 sets
2I aimed for 60, to have double the number of participants in Parker and Phillips (2017) Exp.2
which I model this study after; however, I couldn’t reach that goal due to time limitations
75
of 4 items, exemplified in Table 2.1. The target antecedent always mismatched the
reflexive in features (animacy and number for sentences with inanimate matrix sub-
jects, and gender and number for sentences with animate matrix subjects); thus, all
critical sentences were ungrammatical. The items with inanimate matrix subjects
were borrowed directly from Parker and Phillips (2017) Exp.2 materials; I made
sure to select items which did not contain pronouns or gaps in the spillover regions,
in order not to force additional memory retrievals. The items with animate ma-
trix subjects were constructed from scratch. Thus, the two subsets of items were
not lexically aligned; moreover, the critical pronouns was “themselves” in the first
group and “himself/herself” in the second3. While this design choice potentially
introduces more noise to the comparisons, I felt it was justified: it gives us both the
opportunity to test the effect of interest (lure-match effects from lures in relative
clauses with animate RC heads) and to replicate previous findings (which is impor-
tant to establish the reliability of PP2017 findings, given that no other study has
investigated similar configurations).
In addition to the sentences with reflexives, which were of the primary interest,
I used a control set of 24 agreement items borrowed from Wagers et al. (2009). An
example is given in (9). A standard 2x2 design was used, with the factors being
3Changing the pronouns from “themselves” to “himself/herself” is inevitable for the sentences
with animate matrix subjects. Since the target is animate, we need a reflexive which can differ
from the target in gender and number to be able to create a 2-feature mismatch configuration. But
“themselves” does not carry gender, so if we used “themselves”, we would only be able to induce
a 1-feature mismatch (in number) with the target.
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lure number and verb number. Thus, I had 6 items per conditions. Head nouns
were always singular. The lure and the verb were always separated by an adverb to
avoid potential confounds4.
(9) The key to the cell(s) unsurprisingly was/were rusty from many years of
disuse.
Finally, I had 66 fillers, falling in the following categories. 12 fillers had the same
structure as experimental items with animate matrix subjects, so that people would
not only see this construction in ungrammatical sentences. In addition, 6 fillers with
the same structure used “themselves” as the reflexive, so that “themselves” was not
uniquely associated with ungrammatical items. 6 fillers were of the structure I used
in the previous experiments: “NP said that [NP reflexive]”; these sentences were
introduced to make sure that the target was not always the linearly farthest NP.
12 fillers started with an inanimate noun heading a relative clause; these were in-
troduced to make sure that inanimate subjects were not uniquely associated with
ungrammatical sentences. 12 fillers were sentences with no constraints on the struc-
ture containing a reflexive pronoun. Finally, 12 fillers were just sentences with no
special properties. All of the fillers were grammatical.
Overall, I had 24 critical sentences with reflexives (all ungrammatical), 24
4Briefly, people may experience slowdown on “cells” just because it’s plural, and thus arguably
more complex morphologically and semantically. If the critical verb immediately follows the noun,
this slow-down can affect the reading times on the verb and potentially mask intrusion effects. See
Wagers et al. (2009) for more details.
77
Animate targets
Lure match
The skilled businesswomen that the inexperienced manager crit-
icized at the meeting blamed himself for the inaccurate report.
Lure mismatch
The skilled businesswomen that the inexperienced secretary crit-
icized at the meeting blamed himself for the inaccurate report.
Inanimate targets
Lure match
The thank you letter that the helpful secretaries received
praised themselves for a great job.
Lure mismatch
The thank you letter that the helpful secretary received praised
themselves for a great job.
Table 2.1: Experiment 1 materials example
Targets are underlined, lures are bolded.
control agreement attraction sentences (12 grammatical) and 66 fillers (all gram-
matical), for a total of 108 sentences. Thus the grammatical-to-ungrammatical
ratio was 2:1. All sentences were accompanied by a forced choice Yes/No question.
2.1.3 Procedure
For the purposes of randomization, reflexive and agreement sentences were
treated as same. The 48 stimuli were distributed into 4 lists in a Latin Square
design, for 6 agreement and 6 reflexive sentences per condition. Fillers were added
to these lists, which were then pseudo-randomized with the constraint that no more
than 2 experimental items occur in a row. Each experimental list started with 7
practice items.
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The items were presented on an LCD screen with the resolution of 1280x720
in a 12-point fixed width font (Courier). The maximum length of a line fitting on
the screen was 139 symbols, so all items fit on a single line.
Eye movements were recorded using EyeLink 1000 tower-mounted eye-tracker.
The distance between the tower and the screen was 37 inches. The sampling rate
was 1000 Hz. Participants had binocular vision during the experiment, but only the
samples from one eye5 were recorded. Participants’ heads were immobilized using a
chin rest and a forehead restraint. In the beginning of the session, the eye-tracker
was calibrated using 9-dot calibration display. Calibration was repeated throughout
the experiment as necessary.
Each trial started with a fixation mark on the left of the screen. Participants
had to fixate it in order for the stimuli to appear on the screen. After having read
the sentence, participants pressed a button in order to display a question related to
the sentence. Participants answered the question by pressing one of two associated
buttons. After that, the next trial started.
2.1.4 Analysis
I analyzed two regions of interest in each set of conditions: critical and spillover.
For agreement sentences, the critical region included the verb and the following word
(two following words, if the second word was a determiner). For reflexive sentences,
the critical region included the reflexive and the last three letters of the preceding
5Normally, the right one, unless tracking the left eye was the only option giving a stable cali-
bration.
79
word. This was done to increase the chances of having at least one fixation in the
critical region, following Kush et al. (2015) and S2017. The spillover region was
defined for both types of stimuli as two words following the critical region (three, if
the second word was a determiner). Spaces were included in the region to the right.
In each of the regions, I looked at the following eye-tracking measures: first
pass, the sum of all fixations before the region is exited to the right or to the left;
regression path, the sum of all fixations on the region from the moment it is first
entered from the left and to the moment it is exited to the right, including fixations
in the previous regions; total time, the sum of all fixations on the region. I chose
these measures following S2017. PP2017 analyze first-pass, regression path, right
bound (the sum of all fixations on the region from the moment it is first entered
from the left and to the moment it is exited to the right, NOT including fixations
in the previous regions) and re-read (the sum of all fixations on the regions after it
has been exited once). However, I decided not to include right bound and re-read
in the analysis to reduce the number of comparisons I was making.
Prior to statistical analysis, the data were manually preprocessed using Eye-
Doctor6 to remove blinks and ensure that fixations align with the text. Fixations
shorter than 80 ms or longer than 1000ms were automatically rejected before calcu-
lating eye-tracking measures using custom scripts7. Missing values were discarded
form the analyses. See section 4.1.6 for a detailed discussion of how analyses choices
might affect the final conclusions. In particular, rejecting missing values (instead of
6https://blogs.umass.edu/eyelab/software/
7https://github.com/UMDLinguistics/EyePy
80
replacing them with zeros, as PP2017) might lead to more precise model estimates.
I chose to log-transform reading times to bring the models’ residuals closer to
normality. The transformed values were analyzed with linear mixed effects mod-
els in R (R Core Team, 2014) using lme4 package (Bates et al., 2015b). Separate
models were fit to the data from reflexive and agreement conditions. The following
fixed effects were specified (numerical values in parentheses indicate contrast cod-
ing coefficients; sum coding was used for all fixed effects). Agreement conditions:
target match (match = -0.5 vs. mismatch = 0.5), lure match (match = -0.5
vs. mismatch = 0.5) and their interaction. Reflexive conditions: target animacy
(animate = -0.5 vs. inanimate = 0.5), lure match (match = -0.5 vs mismatch
= 0.5 in features with the reflexive) and their interaction. A fixed effect was taken
to be significant if the absolute value of the associated t statistic was ≥ 2 (Gel-
man and Hill, 2007). Models random effects structure was fully specified, including
random intercepts and slopes for each fixed effect per subjects and items, following
recommendations by Barr et al. (2013). If the model with the maximal random
effect structure did not converge8, I simplifed it by removing random slopes. To be
internally consistent, I always dropped the random effects in the order, shown in
Table 2.2.
I start with removing the interactions as the most complex term (see, e.g.
Bates et al. (2015a), p.6, for a claim that this can be considered standard ap-
8As determined by diagnostics reported by lmer. One has to access the internal structure of the
model fit and look at the information contained in m@optinfo$conv$lme4, where m is the model
object.
81
Agreement Reflexives
verb.num : lure.num | item target.animacy : lure.match|item
verb.num : lure.num | participant target.animacy : lure.match|participant
verb.num | item lure.match | item
lure.num | item lure.match | item
verb.num | participant target.animacy | participant
lure.num | participant target.animacy | participant
Table 2.2: Order of random effect structure simplification in Exp.1.
lme4 syntax is used: “:” indicates interactions and “—” separates grouping factors. Ef-
fects were removed from the model, starting from the top.
proach9). Then, I remove random effects by item, making an assumption that the
variability among items is smaller than among participants, and random slopes by
items would make a smaller contribution to the model. As a final step, all models
were automatically assessed to check whether any random effects had correlations
of 1 or -1, suggesting that a given random effects structure may be too complicated
to estimate given the data (Bates et al., 2015a). Such random effects were dropped
from model specification, starting with the interactions 10.
2.1.5 Results
Mean question answering accuracy was 91%. Fig.2.1 and 2.2 show the observed
reading times means for agreement and reflexive sentences respectively. The full set
9The following StackExchange discussion may also be of interest: https://stats.
stackexchange.com/questions/323273/what-to-do-with-random-effects-correlation-
that-equals-1-or-1
10Admittedly, this is a somewhat simplistic approach to deal with overly complex random effect
structures. See Bates et al. (2015a) for a more principled way to identify redundant random effects
in lmer models.
82
of model coefficients is reported in Appendix C.
I will start the discussion with the results for control agreement sentences. I
found evidence for the effect of grammaticality (ungrammatical sentences being read
slower): the main effect of target match was significant in all three reading mea-
sures at the critical region and in regression path at spillover. The effect of lure
match was significant in regression path and total times in the critical region: when
the lure matched the verb in number, the sentences were read faster. Interestingly,
these effects were not moderated by a significant interaction: matching lures were
read faster regardless of whether the sentence was grammatical or not. This means
that I did not find enough evidence for grammatical assymetry and the data is con-
sistent with the presence of both illusions of grammaticality and ungrammaticality.
The target match x lure match interaction did reach significance but only in
regression path at the spillover region. Pairwise comparisons confirm that the in-
teraction is driven by the simple main effect of lure match within ungrammatical
sentences: sentences with the lure matching the verb were read faster. This pattern
of results is interesting: the interaction in the spillover region is indicative of the
classical attraction pattern (only illusions of ungrammaticality arise). On the other
hand, the main effect of lure match and no interaction at the critical region is
in line with the conclusions of Hammerly et al. (draft.april.2018): both illusions of
grammaticality and ungrammaticality can be observed for subject-verb agreement.
I return to this pattern in the discussion section.
Now turning to reflexive conditions, three effects reached statistical signifi-
cance. First, two main effects of target animacy in total times at the critical
83
Figure 2.1: Experiment 1. RT means for agreement sentences.
Columns correspond to eye-tracking measures: fp - first-pass, rp - regression path, rp -
total times. Rows correspond to ROIs. Errors bars represent standard error of the mean,
adjusted for participant variability (Cousineau, 2005; Morey, 2008)
Figure 2.2: Experiment 1. RT means for reflexive sentences.
Columns correspond to eye-tracking measures: fp - first-pass, rp - regression path, rp -
total times. Rows correspond to ROIs. Errors bars represent standard error of the mean,
adjusted for participant variability (Cousineau, 2005; Morey, 2008)
84
and spillover regions: sentences with animate targets were read slower. Second, the
main effect of lure match in total times at spillover: sentences with matching lures
were read faster. This last effect provides some evidence that a) lures within RCs
can provoke interference and b) this effect does not depend on the animacy of the
matrix subjects, not supporting Sloggett’s suggestion. I will argue that these con-
clusions are tentatively correct, although I will provide more fine-grained discussion
below.
Multiple comparison corrections Von der Malsburg and Angele (2017) suggest
that corrections for multiple comparisons should be applied in eye-tracking studies
when several models are fit to different regions of interest and eye-tracking measures.
Their simulations suggest that Bonferroni correction is an appropriate one and does
not result in losing overly much power. In the current experiment I fit 2 (reflexive
and agreement) x 2 (ROIs) x 3 (measures) = 12 models. Bonferroni correction would
result in the following corrected α: 0.05/12 = 0.004. The corresponding t-value for
a two-sided test is ±2.8711. Almost all significant effects survive the correction with
two exceptions: in agreement sentences, the effect of lure match in regression path
at the critical region; in reflexive sentences, main effect of lure match in total
times at the spillover region.
11Approximated from normal distribution following Jäger et al. (2015). The corresponding R
command is qnorm(0.004/2).
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2.1.6 Exploratory analysis
In my main analysis I followed the procedure from S2017 since I consider it
better along several dimensions (see Chapter 4 for discussion). However, I want to
check whether the choice of analysis procedure matters. Thus, in addition to the
main analysis, I also perform a set of exploratory analyses to better understand the
alignment between my results and those by Parker and Phillips. First, I calculated
average reaction times for right-bound and re-read times: these measures were not
included in the main analyses to reduce the number of statistical comparisons, but
they would allow for a closer comparison of average RT patterns with PP2017. Sec-
ond, I analyzed the extended set of ROIs with the same procedure that PP2017did:
the critical region was defined as including the reflexive alone, without any material
to the left; missing values were replaced with zeros; no trimming of exceedingly long
reading times was performed.
I have also performed additional exploratory statistical analyses. In addition
to the main model, I look at simple main effects of lure match by levels of tar-
get animacy: in Parker and Phillips (2017) design the lure-match effect was a
simple main effect, while in my case I am looking at main effects and interactions.
The coefficients for statistical models are presented in Fig. 2.3. Each dot in the plot
corresponds to a β̂ value from some model. We consider models fit to 4 different
datasets, resulting from the variation of pre-processing choices. These 4 datasets
are plotted along the Y axis of each plot. Each line in the plot corresponds to a
variant of analysis, with the variable treatments delimited by underscores. The first
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component corresponds to the study; the second component corresponds to the crit-
ical region markup (“nonext” - critical region includes only the reflexive itself; “ext”
- critical region includes the reflexive and three characters to the left; the second
component corresponds to missing values treatment (“narm” - remove, “nazero” -
replace with zero). Each column corresponds to a fixed effect in a given region:
TA - target animacy; LM - lure match; TA x LM - their interaction; prws A/IA
- pairwise comparisons, corresponding to simple main effects of lure match within
target animacy conditions. The first five columns display estimates obtained for the
critical region, the last five panels - estimates for the spillover region.
Notice that the coefficients are not easily interpretable on their own, since they
are on log scale. Thus, I will only discuss what inferences one would make, if one
was simply looking at the coefficients and checking whether they are significantly
different from zero. I take coefficients with |t| > 2 to be significantly different from
zero, and mark them in red.
I discuss first what conclusions Parker and Phillips (2017) would have made
based on my data. We need to look at the “nonext na.zero” version of analysis
(i.e., critical region comprising only the reflexive itself with missing values replaceed
with zeros), the “Prws IA” column (since PP2017 only had that single condition)
and all eye-tracking measures except for total times. In their analyses, PP2017
found significant lure-match effect in first-pass, right-bound and re-read times at
the critical region and re-read times at spillover. As can be seen from Fig. 2.3, in
my data only the last effect is replicated.
Turning to other possible analysis variants, we can see that the Target an-
87
Figure 2.3: Sensitivity analysis: Model coefficients in Exp.1
Errors bars represent standard deviation of the estimates. See text for further description
of columns and row labels.
imacy x Lure match interaction virtually never reaches significance, except in
regression path at spillover for analysis variants where missing values are replaced
with zeros. Main effect of lure match is mostly detectable when one chooses a
critical region comprised of reflexive alone (all eye-tracking measures except total
times if one removes the missing values, and right-bound and regression path if
one replaces them with zeros). If one chooses an extended critical region, the only
significant effect of lure match is observed in right-bound times. At spillover,
the effect is observable at total times for the variants of analysis removing missing
values - this is what I reported in the main analysis.
Simple main effect of lure-match for sentences with animate matrix subjects
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is only significant at regression path if one chooses to look at reflexive only and to
remove missing values. Simple main effects of lure-match for sentences with
inanimate matrix subjects are a little bit easier to show up as significant: at the
critical region, they appear in total times if one looks at the reflexive only and
removes the missing values. At the spillover, they appear in regression path for the
variants of analysis replacing missing values with zeros and in total times for all
variants of analyses.
2.1.7 Discussion
I start the discussion with the control agreement attraction sentences. I have
found reliable evidence for agreement attraction, which suggests that the experiment
worked as intended and interference effects can be detected in the data I collected.
Interestingly, I did not always observe the classical pattern: lure-match effects only
within ungrammatical sentences. I did observe it in regression path at the spillover;
however, at the critical region there was evidence for lure-match effects within both
grammatical and ungrammatical conditions. That is, I observed both illusions of
grammaticality and ungrammaticality, supporting the claims by Hammerly et al.
(draft.april.2018) that grammatical asymmetry is observed only in a proportion of
the experiments. Also in line with their conclusions is the fact that the current
experiment had the lowest grammatical-to-ungrammatical ratio among all my ex-
periments which included agreement conditions (2:1 vs. 3:1 in Exp.3 and 5:1 in
Exp.4). Hammerly et al. (draft.april.2018) observed that as the proportion of un-
89
grammatical items increases, the illusions of ungrammaticality are more likely to be
observed. Notice though that in their study, illusions of ungrammaticality were not
observed even when the grammatical-to-ungrammatical ratio was 1:1 (even lower
than in the current experiment), and only appeared when the ratio lowered to 1:2.
Thus, while the direction of the influence between my experiment and Hammerly
et al. (draft.april.2018) appears to be similar, the cut-off points for the emergence of
ungrammaticality illusions do not agree. Therefore, I prefer not to make theoretical
claims about the cause of the symmetrical lure-match effect I observe, only noting
that the effect is, indeed, symmetrical, contra what the accepted generalization is.
This symmetry bears on the main question I address in my thesis. As I dis-
cussed in Chapter 1, the cue-based model by Lewis and Vasishth (2005) is not able
to accommodate such patterns. While the addition of the prominence correction
suggested by Engelmann et al. (draft4) would allow the model to capture those
patterns, it is not at all clear whether there are linguistic reasons for applying the
prominence correction (i.e., why would we think that “cabinets” is more prominent
than “key” in “The key to the cabinets are...”?) Thus, symmetrical agreement at-
traction patterns are a point against Lewis and Vasishth (2005) model. Notice that
this model underlies both PP2017 and S2017 explanations for the reflexive data, so
if we end up doubting it, we will have to doubt these accounts as well. It is especially
so for PP2017, who explain the lure-match effects in terms of faulty memory search.
It is less critical for S2017: while he uses the cue-based architecture to capture the
fact that lure-match effects are only observed in sentences with targets mismatch-
ing the reflexive in two features, the lure-match effect itself does not rely on the
90
properties of cue-based memory search. In principle, any search method which only
searches the local domain of the reflexive and mostly returns the overt target, but oc-
casionally returns the logophoric operator, could work for S2017 model. (Although
it would still have to explain somehow why this other search method is more prone
to return the logophoric operator when the target mismatches in features). Thus,
symmetrical agreement attraction may be slightly more problematic for PP2017.
Now I turn to reflexive conditions, which are of main interest. The central goal
of the experiment was to further investigate the lure-match effects from lures inside
a relative clause (“RC-lures”). This configuration is interesting, since this is the only
instance of lure-match effects not covered by the S2017 account. As such, it may be
the only evidence for lure-match effects emerging from ungrammatical dependency
resolution and for the sentence processing not respecting structural constraints.
I were asking two questions. First, how strong is the evidence for the existence
of lure-match effects from RC-lures? Unlike with the effects with c-commanding
lures, that have been replicated in several experiments, the RC-lures configuration
has only been tested once by Parker and Phillips (2017). If it turns out that the
effects were artifactual, they cannot be used as an argument against the S2017 ac-
count. Second, does the animacy of the matrix subject affects the lure-match effect?
If the lure-match effect truly reflects ungrammatical resolution of the dependency,
it should not. On the other hand, if, as S2017 suggested, the effect reflects a gram-
matical phenomenon of sub-command binding, we should only observe it when the
matrix subject is inanimate. I discuss these questions in turn.
The first question I ask is - have I managed to replicate PP2017 and do we have
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reasons to believe that lure-match effects from RC-lures in “inanimate” conditions
are real? I argue that the experiment does provide the evidence for this, albeit
limited. On the one hand, statistical analysis does confirm the presence of lure-
match effects in total times at spillover. An exploratory analysis also shows that if
I had followed Parker and Phillips (2017) procedure, I would have found a simple
main effect of lure match within sentences with inanimate matrix subjects in the
regression path at the spillover - this is in line with PP2017 results, who also find
such an effect. It also appears that regardless of the pre-processing decisions, at
least some effect indicative of interference would come out significant.
I have to note, though, that these conclusions should be taken with a grain of
salt. First, the main effect of lure match in total times I observed in my primary
analysis would not survive the Bonferroni correction for multiple comparisons. If I
were being conservative, I would not claim that I found evidence for the interference.
Furthermore, it may be worrying that the prima facie inconsequential choices one
makes during pre-processing (i.e. whether the critical character does or does not
include the three last characters of the word preceding the reflexive) affect when
and what exact effects indicative of the interference are becoming significant. To us,
this indicates that the amount of evidence available in the data is not overwhelming,
and more highly powered experiments are needed to make better conclusions. One
final worry is that the patterns I observe do not completely align with what Parker
and Phillips (2017) report. They observed significant lure-match effects in four eye-
tracking measures in the critical region, while I did not. Also, as Fig.2.4 shows,
numerical magnitudes of the lure-match effects are about twice as small than what
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PP2017 report. I will defer the discussion of these numerical differences until later
chapters, where such differences emerge again and are investigated in more detail.
Figure 2.4: Experiment 1. Comparisons of the interference effect magnitudes in
reflexive conditions with Parker and Phillips (2017).
Interference effect is calculated as the difference between lure match and lure mismatch
conditions. Errors bars represent standard error of the difference of the means (calculated
under the assumption that RTs in lure match and lure mismatch conditions are not cor-
related. This is likely false, since they come from the same subjects, thus, the SEs are
overestimates).
Now that I have tentatively concluded that my results are roughly in line with
PP2017 conclusions, the next question is: do I have any evidence for the difference
for the lure-match effect from RC-lures within “animate” conditions? This is the
critical question to test S2017 subcommand hypothesis: if it is correct, I should not
find any lure-match effects in “animate” conditions. The evidence appears to speak
against S2017 hypothesis, although again, in a rather limited way.
The only statistically significant effect pointing out in this direction is the
main effect of lure match in the total times at spillover, not accompanied by a
significant target animacy x lure match interaction. This results suggests that
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there is not enough evidence to conclude that lure match effect behaves differ-
ently depending on the animacy of the matrix subject12. Numerical values suggest
similar conclusions. Fig.2.4 shows the magnitude of lure-match effect in “animate”
and “inanimate” conditions along with the effects from the original PP2017 study.
We can see that regardless of the pre-processing procedure, lure-match effects are
present in the “animate” conditions. The lure-match effect in conditions with inan-
imate matrix subjects is small, as I have already discussed. On the contrary, in
the sentences with animate matrix subjects the effect is around 50ms in magnitude,
which, as we will see, brings it within the range of interference effects I observe in the
rest of my experiments. In the early eye-tracking measures (first-pass, right-bound,
spillover) it aligns rather closely with the original lure-match effect from PP2017.
In the late measures (re-read, total times) it rather patterns together with the lure-
match effect in the sentences with inanimate heads. I take these patterns to suggest
that lures within an RC do provoke lure-match effects even when the matrix subject
is animate. This conclusion holds if I adopt the PP2017 pre-processing routine,
although in this case the magnitude of the effect in animate conditions goes down.
Just the presence of lure-match effect in “animate” conditions does not neces-
sarily contradict S2017’s hypothesis: the effect could be merely reduced, not elim-
12If we look at the patterns of the interference effects in Fig.2.4, we will notice that this effect is
likely driven uniquely by the lure-match effect within “inanimate” conditions. Exploratory pairwise
comparisons confirm this impression. This would support the S2017 subcommand hypothesis.
However, these impressions come from exploratory analysis, and as I discuss below, other patterns
in these analysis still suggest that lure-match effects do arise in “animate” conditions.
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inated, when the matrix subject is animate. However, the numerical patterns do
not seem to support this possibility. Almost in all measures in both pre-processing
variants (except for late measures with PP2017 preprocessing) the lure-match effect
in “animate” conditions is equal or bigger to the effect in “inanimate” conditions.
Overall, I conclude that the experiment provides some evidence against S2017’s
sub-command explanation, although the evidence is merely suggestive and should
be verified in a highly powered confirmatory experiment.
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Chapter 3: Interference effects with quantificational lures
In the previous chapter we have shown that S2017 sub-command explanation
for relative clause lures is likely wrong, and at least some lure-match effects might be
better explained as instances of fallible memory access. This serves as a support for
PP2017 account, which claims that structural cues do not have special status in the
system: they do constrain memory access to some degree, but can be outweighed
by other sources of information. In this chapter I am going to further test PP2017
account by looking at quantificational (QP) lures. The main question I address here
is: are all structural cues treated equally by the parser? In particular, I will argue
that available evidence tells us little about how c-command information is used, and
I will report three experiments designed to fill this gap.
In this chapter, I am going to adopt Chomskyan Binding theory view, in
which possible antecedents should c-command the anaphor and be local to it in
some relevant sense. For the purposes of my experiments, locality can be reduced to
clause-mateness. This simplification has an additional advantage: it makes it easy
to represent locality as a cue in content-addressable architecture; but theoretical
descriptions of locality conditions are more involved and can be trickier for cue-
based models to accommodate (see, e.g., Cunnings et al. (2015) for an exploration
96
of less canonical configurations). Having clarified these assumptions, what evidence
does PP2017 provide for the nature of these structural constraints?
Their evidence, undoubtedly, suggests that locality constraints are being used
but do not uniquely guide memory access: without making this assumption, we
would have hard time explaining the contrast between the absence of lure-match
effects in 1-feature target mismatch conditions and their presence in 2-feature target
mismatch sentences. The situation with c-command is more complicated. Prima
facie, Exp.2 (where lures were located inside a subject relative clause) suggests that
c-command acts fails to uniquely guide retrieval as well. However, this pattern of
results does not tell us anything about whether or how c-command information was
used.
First, the same pattern of results could hold if the parser never even included
c-command information in the set of retrieval cues and instead only relied on lo-
cality. In Exp.2 PP2017 only looked at 2-feature target mismatch configurations.
There, locality would fail to rule out a non-local antecedent, and if no c-command
information were used to further restrain memory access, both c-commanding and
non-c-commanding lures could be potentially retrieved. While theoretically possible,
we consider this possibility unlikely, based on empirical evidence from other depen-
dencies. Antecedents c-commanded by the pronoun appear to be excluded from
consideration, in accordance with Binding Theory Principle C (Kazanina et al.,
2007; Aoshima et al., 2009; Kazanina and Phillips, 2010). Similarly, Kush et al.
(2015) show that non-c-commanding quantified NPs do not appear to induce lure-
match effects in pronouns resolution. This evidence suggests that at least some
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way of representing c-command constraints should be available to the parser. Since
reflexives resolution is also constrained by c-command, a priori it might be weird
to assume that the parser can represent such information but prefers not to use
specifically with reflexives.
However, the fact that c-command is used by the parser in some manner does
not necessarily imply that it is represented in such a way that it faithfully captures
all and only licit c-command relations in the grammar. As we will discuss, faithfully
representing c-command relations in cue-based memory models is not straightfor-
ward. Accordingly, various approximate encodings have been suggested (Alcocer
and Phillips, 2012; Kush et al., 2015). Some of these approximations (e.g. Kush
et al. (2015) accessible feature) are formulated in such a way that in the config-
urations used by Parker and Phillips (2017) they would not render the lures illicit.
If this is the case, it would be hard to talk about the feature failing to categorically
constrain processing: it would do so, only the constraints it would follow would not
perfectly map to c-command constraints defined in the grammar. This conclusion
would not align with the PP2017 account of lure-match effects which assumes that
any structural cue can fail to categorically restrict retrieval. Thus, it is important
to empirically evaluate the sensitivity of lure-match effects to the c-command status
of the antecedent. In what follows, I will first discuss the approaches one might use
to represent c-command information, and then show how we could experimentally
differentiate them.
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3.1 Representing c-command in cue-based models
C-command is defined as follows (Reinhart, 1976): a node A c-commands a
node B if neither A or B dominate each other, and the first branching node which
dominates A dominates B. From the point of view of Chomskyan Binding Theory,
reflexives are bound by their antecedents, and for that, a c-command relation be-
tween the binder and the bindee is necessary. Thus, a priori we might expect that
the parser will be able to encode and use c-command information.
On the other hand, c-command is inherently relational: one has to know the
position of two nodes in a tree in order to figure out whether one of them c-commands
the other. And as Alcocer and Phillips (2012) discuss, representing relational infor-
mation in an efficient way in cue-based architectures may not be straightforward:
one cannot just use a feature like “+ c-commanded” or “+ c-commander”, it would
have to be much more specific, something like “+ c-commanded by NP17”. Given
the number of potential c-commanders a given node can have, if one attempts to
encode these relations explicitly, the size of the representation and the processing
effort required to update the information on the older nodes as the new nodes come
in may quickly get out of hand. Additionally, as Alcocer and Phillips note, ex-
haustive encoding might be inefficient in restricting the range of constituents being
considered during memory retrieval.
To demonstrate this, they discuss a scenario in which each node in the tree
carries a complete list of its c-commanders. When a c-commander needs to be
retrieved, this list (or its individual components) is included in the set of retrieval
99
cues. However, this could lead to several problems. In ACT-R model, the activation
for the items which do not match some of the retrieval cues is decreased, in proportion
to the number of the mismatching cues. With this encoding approach, any single
item would only match one of these cues, receiving a sizeable mismatch penalty
for all the others. This activation drop could lead to longer retrieval times or even
retrieval time-out. In addition, retrieving an incorrect item would be easier: a
constituent might have many c-commanders utterly irrelevant to the dependency at
hand, such as complementizers or functional projections. Yet they will receive an
activation bump and might end up being misretrieved.
A related approach (not discussed by Alcocer and Phillips (2012)) would be
to annotate each chunk with a list of phrases it is c-commanding. When the parser
reaches the reflexive, it would use its ID to create a single retrieval cue, e.g. “+
c-commands NP17”. This approach would escape some of the problems from the
previous one, but would also bring new issues. The mismatch penalty problem of
the previous approach would be circumvented, since only a single c-command-related
retrieval cue would be used. However, the efficiency of this cue will be very low,
practically making it all but useless1: due to the fan effect among all of the items
matching the c-command cue, activation boost to any single one will be rather small.
1That is, if we accept the standard assumption that cues are combined additively. If instead we
assume that they are combined multiplicatively, so that a mismatch on any single cue drops the
activation significantly, we will avoid the fan effect problem. But we will also make the structural
cues rather powerful, potentially removing ways for ever receiving a structurally inappropriate
constituent. This may or may not be desired: e.g. this change would fit rather well in the S2017
model, but not the PP2017 one.
100
The problems of contacting completely irrelevant items and of spreading redundant
information across the representation are shared with the previous approach.
The above challenges to exhaustive encoding of c-command information would
suggest that if one wants to efficiently represent relational information in a cue-
based system, one would have to rely on approximations. Alcocer and Phillips
(2012) suggest two such approximations. The first one relies on a binary “command-
path” feature, which every node carries. It is switched to on just in case a node
c-commands the node which is currently being introduced to the parse, otherwise it
is set to off. This encoding schema has two disadvantages. First, it does not allow
the parser to use c-command information to make attachment decisions. Second,
more importantly, it only allows the system to know which nodes c-command the
node which is just being introduced. It does not let the parser know which nodes
the current node c-commands (which may be necessary in head-final languages), not
does it allow to figure out c-command relations for nodes which are already part
of the parse (which might be needed in special configuration, e.g. those involving
phonologically null pronouns, whose existence is only recognized when the following
node is being processed).
A second heuristic by Alcocer and Phillips (2012) relies on “dominance spines”.
A dominance spine is a chain of nodes dominating one another along a right branch
in the tree. Every time a left branch is created, it is assigned a new dominance spine
index. In order to figure out whether the two nodes are standing in a c-command
relation, one just needs to know whether their parents share the same dominance
spine. In our case, when a parser reaches the dependency tail, it would look up the
101
dominance spine index of the tail’s parent and look for other nodes whose parents
also have this index2. The limitations of this approach are as follows. It does not
capture certain kinds of c-command relations; specifically, when a node is embedded
too deeply in a left branch, the dominance spine heuristic will fail to capture its c-
command relations with the nodes which c-command the top of the branch. In
addition, this approach still has (arguably minor) problems with potentially leading
to retrievals of irrelevant c-commanding nodes.
All of the approaches above, while differing in details, have one thing in com-
mon: they are trying to capture c-command relations proper, and the encoding
schemas they suggest could be used by any kind of mechanism requiring c-command
information. This generality is an advantage of these approaches and it brings them
in closer alignment with grammatical theories. It also leads to the situation where
c-command information fails to be a strong filter, making only minor contributions
to constraining memory access due to fan effect (at least as long as one assumes
that retrieval cues are combined additively). This may be seen as another advan-
tage, if we take empirical evidence from subject-verb agreement, reflexives and NPIs
to indicate that, indeed, c-command information may fail to strictly constrain the
range of retrieved constituents. It would be more of a disadvantage to hypotheses
which postulate that structural information helps to categorically filter out illicit
dependency elements (e.g Sloggett, 2017).
A different kind of approach is advanced by Kush et al. (2015). They ac-
2In order for this schema to work, each node would also have to encode some information about
its parent, including the parent’s dominance spine
102
knowledge the complications with exhaustive encoding of relational information in
cue-based models and also use an approximation. However, the feature they sug-
gest, accessible, is designed to capture a very specific use case of c-command:
binding by quantifiers. In a series of experiments, Kush et al. (2015) show that
the parser is sensitive to the binding constraints on quantificational antecedents.
First, they compare sentences like (1a) where the QP c-commands the pronoun to
sentences like (1b), where it does not. They show that people experience more
processing difficulties in (1b) as compared to (1a), as indexed by a slow-down in
reading times in first-pass and right-bound times in the spillover region. This is in-
terpreted as evidence for people not considering the grammatically inaccessible QP
as the antecedent and either trying to bind the pronoun to a gender-mismatching
“Kathi” or trying to coerce a sentence-external referent. These results show that
the parser can distinguish between grammatically appropriate and grammatically
inappropriate QP antecedents.
(1) a. Kathi didnt think any janitor liked performing his custodial duties, but
he had to clean up messes left after prom anyway.
b. Kathi didnt think any janitor liked performing his custodial duties when
he had to clean up messes left after prom anyway.
Second, Kush et al. also show that the parser appears to rule out inappropriate
QPs categorically: people appeared to experience similar processing difficulties in
both (2a) and (2b), despite the fact that in the second case the QP antecedent
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fully matches the pronoun in features. That is, QP lures do not appear to induce
lure-match effects. Similar findings have been reported by Cunnings et al. (2015).
(2) a. The troop leaders that no boy scout had no respect for had scolded her
after the incident at scout camp.
b. The troop leaders that no girl scout had no respect for had scolded her
after the incident at scout camp.
To capture these patterns, Kush et al. suggest that a single feature (“±accessible”)
is used to mark the status of potential referents. NPs are always + accessible
for retrieval. QPs, however, start out as + accessible, but are switched to -
accessible as soon as the parser detects the edge of their c-command (or scope)
domain. This implementation avoids several problems from Alcocer and Phillips
(2012) (fan effect would be reduced due to the fact that only NPs and QPs carry
the accessible feature; feature update requires minimal computations (unlike in
some cases of “command-path”)) at the cost of generality (this approach would not
be able to rule out binding by non-c-commanding NPs).
Before we turn to our experiments, we briefly address one more issue. As we
have discussed, Kush et al. (2015) findings do not allow to decide whether accessi-
ble tracks c-command or scope, because these two things are perfectly confounded
in their stimuli. However, recent experiments by Moulton and Han (toappear)
may disambiguate between these two possibilities. They suggest that at least in
some cases (including configurations examined by Kush et al. (2015)) c-command
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is the relation tracked by the parser. They use feature mismatch paradigm to see
whether scoping but not c-commanding QPs would be accessed during pronoun res-
olution. They show that in configurations like (3a), where the QP “each boy” does
c-command the pronoun, people are faster to read the pronoun if it matches the QP
in gender. However, in (3b), where the QP scopes over but not c-commands the
pronoun, no such effects were observed. This can mean that only c-commanding
QPs are considered by the parser.
(3) a. It seems each boy brought fresh water from the kitchen quickly right
before he/she went on an early break.
b. After each boy brought fresh water from the kitchen quickly it seems
that he/she went on an early break.
c. After the boy brought fresh water from the kitchen quickly it seems that
he/she went on an early break.
A follow up experiment ruled out the possibility that the lack of the gender mis-
match effect from scoping but not c-commanding QPs is not related to the reduced
prominence of QPs within adjunct clauses: referential NPs in the same position
(as in (3c)) did elicit gender mismatch effects. Moulton and Han (toappear) inter-
pret these results as meaning that scope alone cannot explain constraints on QPs
antecedents, and c-command is an important component of these constraints3.
3They also provide results which are hard to explain if we think that c-command alone is
used. They show in an interpretation study that in both (3a) and (3b) people choose co-varying
interpretation equally frequently, about 60-65% of the times. Whether the QP does or does not
105
3.2 Outline of the experiments
The distinction between the general approaches by Alcocer and Phillips (2012)
and the specific one by Kush et al. (2015) brings us back to the interpretation of
the data from Parker and Phillips. To remind, they observed lure-match effects
from non-c-commanding lures in configurations like (4), which prima facie could be
used as evidence for the c-command acting as a violable constraint. However, this
interpretation will depend on the encoding schema we choose. If a general strategy
of the sort discussed by Alcocer and Phillips (2012) is used, Parker and Phillips
(2017) conclusions will be supported4. If, on the other hand, the parser relies on a
task-specific approximation a-la Kush et al.’s accessible, Parker et al. lure match
effects from Exp.2 would rather indicate that the parser faithfully follows whatever
encoding is available to it. Since NPs are always + accessible, the parser would
have legitimate “right” to choose them as antecedents, given that locality constraints
have already been overridden. That is, the choice is between a parser which follows
a faithful representation less than perfectly, or a parser which faithfully follows a
less than perfect representation.
(4) The soothing tea [ that the nervous students drank ] calmed themselves down
after the test.
I try to tease these two possibilities apart in three experiments. I do this
c-command the pronoun does not seem to affect the judgments.
4To the degree that we can also rule out Sloggett (2017) explanation.
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by looking at QP lures in c-commanding and non-c-commanding positions. If the
system is relying on domain-general c-command information which sometimes fails
to perfectly guide retrieval, we will expect to observe lure-match effects from the
QPs, regardless of where they are located. If, on the other hand, the system is
faithfully following a more domain-specific feature like accessible, the c-command
status of the lures will determine the outcome: we would only expect to observe
lure-match effect from c-commanding QP lures.
The presence or absence of lure-match effects from QP lures may also be
informative for Sloggett (2017)’s model. Empirically, QPs appear to be acceptable
as logophoric antecedents across languages (we have been able to find examples
from Icelandic (Sells, 1987, p.467), Chinese (Huang and Liu, 2001, p.165), Yoruba
(Adesola, 2006, p.2091)). As as (5) shows5, QPs antecedents are also acceptable in
the sub-command configuration in Chinese. Given these facts, S2017 account would
predict lure-match effects from c-commanding lures and from sub-commanding lures
embedded under an inanimate noun. For sub-commanding lures embedded under
animate nouns (as in our experiments), no lure-match effects should be observed.
(Notice that our Exp.1 has already suggested that sub-command explanation is not
on the right track. However, since the evidence there was mostly based on numerical
patterns, we discuss the corresponding predictions for S2017 account as well, to be
able to determine whether further evidence is (in)compatible with it).
(5) a. mei yi-ming jizhei xie de baodao dou hai-le zijii
every one-CL reporter write MOD report ADVQuant harm-PFV self
5I would like to thank Nick Huang, Chia-Hsuan Liao and Yu’an Yang for these judgments.
107
The report that every reporteri wrote harmed himi
b. mei yi-ming yuangongi huode de huahong zuizhong dou
every one-CL employee receive MOD bonus ultimately ADVQuant
hai-le zijii
hurt-PFV self
The bonus that every employeei received ultimately hurt himi
A potential counter-example to the cross-linguistic facts above comes from Postal
(2006), who briefly discusses examples like (6)6. These examples suggest that in En-
glish, long-distance antecedents of reflexives cannot be quantificational. If we think
that English-specific evidence should receive priority over cross-linguistic evidence,
S2017 account would predict no lure-match effects from QP lures regardless of their
position.
(6) a. *Every/No woman1 claimed that HERSELF1, most people could never
understand.
b. *Every/No woman1 claimed that they had praised no one but herself1.
c. *Every/No woman1 claimed that they had defaced carvings of herself1.
d. *Every/No recent president1 claimed that the Queen was inferior to himself1.
e. *Every/No woman1 claimed that it was HERSELF1 that people should
vote for.
f. *It was HERSELF1 that every/no woman claimed that people should
vote for.
6Caps indicate strong stress.
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g. *Every/No woman1 claimed that there was still HERSELF1 for people to
vote for.
h. *Every/No woman1 claimed that Bob wanted to interview Carl and herself1.
i. *Every/No woman1 claimed that as for herself1 she would prefer to drink
beer.
j. *Every/No waitress1 claimed that workers like herself1 deserved a raise.
The rest of the chapter reports three experiments. In the first one I consider
configurations like (7a), to determine whether QP lures embedded within relative
clauses - i.e. in a non-c-commanding position - provoke lure-match effects. To
preview the results, I did not find any interference from QP lures, supporting the
possibility that a process-specific feature like accessible is being used. The in-
terpretation of these results is complicated by the fact that NP lures did not pro-
voke any lure match effects either, contra results reported in Parker and Phillips
(2017). To determine possible reasons for this, in the next two experiments I look
at c-commanding lures, as in (7b). If accessible is, indeed, in use, we should
observe interference effects. Indeed, I did observe numerical patterns suggestive of
lure-match effects in both QP and NP stimuli, although these patterns were not
supported by statistical analysis. I suggest several possible reasons for this, which
lead to the follow-up experiments discussed in Chapter 4.
(7) a. The stuntmen [ that no/the actress had worked with ] introduced
herself to the rest of the cast.
109
b. No/the understanding doctor would complain that expectant mothers
distress himself during stressful medical examinations.
3.3 Experiment 2
The goal of my first experiment is to check whether the parser faithfully obeys
structural relational constraints as specified in the grammar; in particular, whether
it obeys the c-command/scope restrictions on QP antecedents. I contrast two hy-
potheses. The first one is that c-command/scope constraints are implemented only
approximately (in particular, I choose Kush et al. (2015) accessible feature hy-
pothesis), but the parser strictly follows this approximation. If this hypothesis
is true, I will not observe lure-match effects from non-c-commanding/non-scoping
QP antecedents. The second hypothesis is that the parser does not follow the
c-command/scope constraints, regardless of whether they are implemented approxi-
mately or in strict accordance with grammatical generalizations7. If this hypothesis
is correct, I will observe lure-match effects from non-c-commanding/non-scoping
QP lures8. Only the second scenario would constitute strong support for Parker
and Phillips (2017) claim that structural features are of limited use to the parser
when it has to select suitable antecedents.
7A third possible hypothesis – that the c-command/scope constraints are implemented in full
accordance with the grammar and the parser DOES faithfully obey them appears to be ruled out
by Parker and Phillips (2017) Exp.2.
8Notice that we would have made the same prediction if we assumed that c-command/scope
information is never used in the reflexive resolution at all. However, a priori this possibility seems
unlikely, and I do not pursue it further.
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3.3.1 Participants
32 members of University of Maryland (13 M, 19 F; age range: 18-28; mean
age: 20.2, SD: 2.15) participated in the experiment for a class credit or a payment of
$10. The experimental session took about one hour, including setup and calibration.
Data from 7 participants were excluded: one because of a software failure; two
because they did not manage to complete the experiment in an hour; two because
the preprocessing suggested that the data is extremely noisy; one because of an
experimenter’s error; one due to low question answering accuracy (64% correct).
3.3.2 Materials
Critical sentences were modeled after Parker and Phillips (2017, Exp.2) and
Kush et al. (2015, Exp.2)9. An example of a critical sentence is given in (8). An
example of a full set of stimuli along with accompanying contexts (see details below)
is given in Table 3.1.
(8) The stuntmen that the actress had worked with introduced herself to the
rest of the cast.
In all critical sentences the target was the subject of the matrix clause; the lure was
the subject of a relative clause modifying the target; the reflexive was the object
of the matrix verb. Thus, the lure is neither local relative to the reflexive nor
9I would like to thank Julia Buffinton for her great help with constructing the materials and
providing native speaker judgments on them.
111
c-commanding it.
The study used 2x2 factorial design with lure type (NP or QP) and lure
match (the lure matching or mismatching the anaphor in gender) as factors. The
target always mismatched the anaphor in gender and number, thus, all the critical
sentences in the experiment were ungrammatical. I used nouns with both defi-
nitional (“woman”) and stereotypical (“secretary”) genders. The gendered nouns
came partly from previous studies (Parker and Phillips, 2017; Osterhout et al., 1997),
and partly from a native speaker judgments. Target NPs were always plural, lures
were always singular. Half of the reflexives were masculine, and half were feminine.
QP lures were always created with the negative quantifier “No”. This quantifier was
chosen to make sure that binding is indeed the only linking option (see Kush (2013);
Kush et al. (2015) for a discussion of how other quantifiers, like “every”, sometimes
allow for alternative readings which resemble binding, but do not behave exactly like
it). Additionally, I made sure that the interpretation of the reflexive is not biased
towards one of the potential antecedents: matrix verbs denote an action which can
plausibly be performed by the target on the target itself (in case of grammatical
binding of the reflexive; e.g. stuntmen can introduce themselves) and by the target
on the lure (in case of the ungrammatical binding of the reflexive; e.g. stuntmen
can introduce the actor/actress to others).
The presence of a subject relative clause makes the sentences sound less natural
outside of a context. It suggests that the matrix subject is selected from a larger
class, in such a way that only the selected members have the property denoted by
the relative clause. But this larger class is never mentioned explicitly, which may
112
tax the processing, if people try to come up with it on the fly. This may distort
the reaction times for the critical sentences and mask potential intrusion effects. To
avoid this, I add two context sentences which explicitly introduce the larger class, to
make the relative clause modification of the critical sentence subject more felicitous.
The contexts are structured in the following way.
For the NP lures, we first indicate the existence of a group of people which
the target NP will be related to (stuntmen in Table 3.1, and a salient individual
(actor/actress)). We then describe an action/attitude of that individual which sub-
divides the target group in two. In the example above, some stuntmen have worked
with one of the actors/actress, and some have not. This allows us to single out
stuntmen based on the property of (not) having worked with the actor in question.
For the QP lures, we indicate existence of two groups of people (e.g., stuntmen
and actors/actresses). Then, we describe a situation in which some (but not all!)
members of the second group have a relation/attitude to some members of the first
group. Importantly, there must be some members of the first group that no member
of the second group has relation to. E.g. in QP Lure conditions in Table 3.1 some
stuntmen have worked with some of the actors, but there are stuntmen who haven’t
worked with any of the actors. The existence of this latter subgroup of stuntmen
allows us to felicitously use a relative clause with a negative quantifier to single this
subgroup out.
As I mentioned above, all of the critical sentences are ungrammatical. Thus,
if I don’t find any interference effect, I am not able to check whether the experiment
worked as intended. In order to remedy this, I included a control set of 12 agreement
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attraction items, mostly adapted from Wagers et al. (2009) (see the description for
Experiment 1 for more details). Thus, I had 3 items per conditions10. Agreement
attraction sentences were embedded into short contexts as well.
NP lures
The action movie had a very large cast, only some of whom knew
each other from previous films, so they had a round of introduc-
tions. Most of the stuntmen had already worked with one of the
actors/actresses, so they decided to talk first.
Lure match
The stuntmen that the actress had worked with introduced her-
self to the rest of the cast.
Lure mismatch
The stuntmen that the actor had worked with introduced her-
self to the rest of the cast.
QP lures
The action movie had a very large cast, only some of whom knew
each other from previous films, so they had a round of introduc-
tions. Most of the stuntmen had already worked with some of the
actors/actresses, but some of the stuntmen were novices, so they
decided to talk first.
Lure match
The stuntmen that no actress had worked with introduced her-
self to the rest of the cast.
Lure mismatch
The stuntmen that no actor had worked with introduced her-
self to the rest of the cast.
Table 3.1: Experiment 2 materials example
Targets are underlined, lures are bolded.
Finally, I used a variety of fillers type to make the manipulation less noticeable
and to prevent people from adopting an unusual reading strategy, which is possible
if they notice that all sentences with reflexives are ungrammatical. Similar to other
10This is fewer than usual, but the size of the experiment did not allow to include more.
114
sentences in this experiment, filler sentences were embedded into short contexts.
Some of the fillers contained grammatical violations which could occur in any of the
three sentences of the text. Appendix E provides detailed information on the fillers
used.
Overall, I had 24 experimental stimuli with reflexives, 12 control agreement
stimuli and 66 fillers for a total of 102 items. Each item consisted of two context
sentences and one critical sentence, for a total of 306 sentences. The grammatical-to-
ungrammatical ratio was roughly 3.5:1 if counting individual sentences and roughly
1:2 if counting items (I count any item containing at least one ungrammatical sen-
tence as ungrammatical). All of the items in the experiment were accompanied
by a forced-choice Yes/No question to make sure that the participants are paying
attention while reading.
3.3.3 Procedure
The procedure was mainly the same as in Exp.1 with the following minor
differences. Since the stimuli consisted of three sentence contexts, they did not fit
on a single line. The maximum length of a line fitting on the screen was 139 symbols,
so all items were broken down to several lines of texts (in most of the cases three,
but sometimes more). I ensured that critical and spillover region did not occur
immediately before or after the line break. Each experimental list started with 5
practice items.
.
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3.3.4 Analysis
Analysis procedure was identical to that in Exp.1 with the following differences
due to the design of the experiment. Separate models were fit to the data from
reflexive and agreement conditions. Agreement data analysis was identical to that
in Exp.3. The following fixed effects were specified for the model fit to the reflexive
data (numerical values in parentheses indicate contrast coding coefficients; sum
coding was used for all fixed effects): Lure type (NP = -0.5 vs. QP = 0.5),
Lure match (match = -0.5 vs mismatch = 0.5 in features with the reflexive) and
their interaction. Models random effects structure was fully specified, including
random intercepts and slopes for each fixed effect per subjects and items, following
recommendations by Barr et al. (2013). If the model with the maximal random
effect structure did not converge, the random effects were dropped in the order
specified in Table 2.2 (replacing target animacy withlure type to account for
differences in the experimental design).
3.3.5 Results
Mean question answering accuracy was 92%. Figures 3.1 and 3.2 show the
observed reading times means for agreement and reflexive stimuli respectively. Sta-
tistical analyses indicate that there is very little evidence for any effects: the only
effect which reaches significance is the main effect of lure match in the agreement
stimuli at the critical region in regression path. The positive coefficient means that
on average, logRTs are smaller (i.e. people are faster) in lure match conditions
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Figure 3.1: Experiment 2. RT means for agreement sentences.
Columns correspond to eye-tracking measures: fp - first-pass, rp - regression path, rp -
total times. Rows correspond to ROIs. Errors bars represent standard error of the mean,
adjusted for participant variability (Cousineau, 2005; Morey, 2008)
Figure 3.2: Experiment 2. RT means for reflexive sentences.
Columns correspond to eye-tracking measures: fp - first-pass, rp - regression path, rp -
total times. Rows correspond to ROIs. Errors bars represent standard error of the mean,
adjusted for participant variability (Cousineau, 2005; Morey, 2008)
117
regardless of whether the target matches or mismatches the verb.
Multiple comparison corrections As in the previous experiments, I fit 12 mod-
els, thus the Bonferroni corrected α-value remains the same: 0.004. The correspond-
ing t-value for a two-sided test is ±2.87. If I apply this correction, no statistical
comparison in the experiment reaches significance. Thus, after Bonferroni correc-
tion the intrusion effects I observed in agreement sentences do not receive statistical
support.
3.3.6 Discussion
Agreement attraction stimuli I used agreement attraction sentences to con-
firm that the experiment worked as intended. I did find evidence for the intrusion
effect at the critical region: lure match led to faster RTs in regression path at the
critical region, which would indicate that the manipulation was successful. As in
Experiment 1, the evidence suggested that this facilitation happened in both gram-
matical and ungrammatical sentences. This further strengthens Hammerly et al.
(draft.april.2018) conclusions that the absence of ungrammaticality illusions may be
artifactual. That said, the grammatical-to-ungrammatical sentence ratio was higher
than in Experiment 1 and much higher than in Hammerly et al. (draft.april.2018) ex-
periments, thus it is not clear whether their explanation in terms of grammaticality
bias can be used to explain these data.
It may be worrying that statistical support for the lure-match effect in agree-
ment attraction is not very strong: I only observe it in one region and reading time
118
measure, and even there it disappears if I apply multiple comparisons correction.
However, it is not inconsistent with previous eye-tracking studies. Both Dillon et al.
(2013) and Parker and Phillips (2017) report facilitation in only one measure (total
times and re-read times, correspondingly). It is also the case that I had fewer data
points than the other studies: only 3 per condition per participant. This might have
made it more complicated for the effects to reach statistical significance.
Overall, I conclude that the data from agreement sentences did provide evi-
dence for intrusion effect, and thus indicates that the experiment worked as expected,
and it is possible to observe lure-match effects in my data.
Reflexive stimuli Let us now turn to the main question of interest — intrusion
effects in the reflexive sentences. I did not find any statistical evidence for intrusion
effect in reflexive resolution with QP lures. This fact alone could indicate that the
parser faithfully follows constraints on binding by quantifiers, contra PP2017 and
in line with Kush et al. (2015) accessible account. However, this interpretation
is complicated by the absence of reliable interference effects in the sentences with
NP lures. This may be worrying, since the stimuli were structurally identical to
those used in Parker and Phillips (2017), and thus a priori I might expect to observe
a similar effect. Thus, before making my final conclusions about QP stimuli, I
investigate the lure-match effects in NP stimulli in more detail.
To better understand the alignment between my study and PP2017, I perform
a set of exploratory analyses similar to those in Experiment 1. Fig.3.3 shows the
size of the interference effect in these exploratory analyses. Since there is not as
119
much information in this figure, I change the plot layout: eye-tracking measures are
plotted along the x-axis, rows correspond to ROIs, and columns — to pre-processing
variants. Averages for PP2017 data stay the same in both rows.
In the critical region my main pre-processing procedure yields interference
effects which are consistently smaller than in PP2017 data and which concentrate
around 0. When I adopt their pre-processing procedure, the effect in my data shifts
towards negative values (indicating facilitation) and the difference with PP2017
reduces but does not disappear completely. The difference remains biggest in re-
read times — the only measure in which PP2017 did find statistically significant
facilitation. In the spillover region, my effects consistently concentrate at or above
zero regardless of the analysis procedure. If anything, this would be indicative
of inhibition, rather than facilitation observed in PP2017 data. Overall, Fig.3.3
suggests that in my data the effect of lure match in reflexive sentences is consistently
smaller than in PP2017.
There are several possibilities of why this could be the case. First, it could be
that my experiment did not work at some basic level. However, I do not think this is
the case. Basic reading effects are visible in the data: people’s reading times increase
and the proportion of first-pass skips decreases as the length of the words increases.
Question answering accuracy is reasonably high: except for one person which I
excluded from the analysis, everybody has at least 83% of correct answers, and
most people are above 90% accuracy. Finally, I did observe the expected patterns
in the agreement attraction sentences, although statistical evidence for them was
limited. Second, it could be that the presence of sentence contexts has affected
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Figure 3.3: Experiment 2. Comparisons of the interference effect magnitudes in
reflexive conditions with Parker and Phillips (2017).
Interference effect is calculated as the difference between lure match and lure mismatch
conditions. Errors bars represent standard error of the difference of the means (calculated
under the assumption that RTs in lure match and lure mismatch conditions are not cor-
related. This is likely false, since they come from the same subjects, thus, the SEs are
overestimates).
people’s reading strategies. E.g. it might have made people process the sentences
more deeply and tobe more discriminating in the choice of antecedents. Or it might
have just led to higher fatigue - people had to read three times more sentences
compared to PP2017 experiment. Third, it might be that the intrusion effects
from non c-commanding lures are more fragile, e.g. because it’s harder to ignore
c-command information.
However, most of these concerns are assuaged by the data from Experiment
1. It relied on the exact same stimuli as PP2017 did, with no additional contexts,
and still observed very small numeric effects of interference. Fig.3.4 shows the
magnitude of the interference effects in NP and QP lure conditions from the current
experiment and from Experiment 1. As in the other places in the thesis, I look
121
at two pre-processing variants in order to check whether they have any noticeable
effect on the conclusions I make.
Figure 3.4: Experiment 2. Comparisons of the interference effect magnitudes in
reflexive conditions with Parker and Phillips (2017).
Interference effect is calculated as the difference between lure match and lure mismatch
conditions. Errors bars represent standard error of the difference of the means (calculated
under the assumption that RTs in lure match and lure mismatch conditions are not cor-
related. This is likely false, since they come from the same subjects, thus, the SEs are
overestimates).
I will compare the stimuli most similar between the two experiments - those
with animate matrix subjects. Unfortunately, the results do depend on the pre-
procesing procedure. If one chooses the procedure from S2017 (extended critical
region, removed missing values), the interference effects from the current effects are
smaller in magnitude than in Experiment 1 by roughly 50 ms, which puts them
in the vicinity of zero. If, on the other hand, one chooses the PP2017 procedure
(critical region comprises only the reflexive, missing values are replaced with zeros),
the effects from the two studies align rather closely. Perhaps the only conclusion
I am comfortable making here is the following. To the degree that we believe
122
that Experiment 1 provided evidence for interference in conditions with animate
matrix subject, we should also believe that smaller interference effects in the current
experiment are not stemming simply from the fact that I used animate matrix
subjects. I.e. it is unlikely that the sub-command hypothesis by S2017 could be
used to explain the reduced magnitude of the effects.
Returning to the QP stimuli, their lure-match effects quite consistently go in
the opposite direction as compared to the NP stimuli in both the current experi-
ment and Experiment 1. In most cases, lure-match effects from QP lures are around
0 or positive (indicating inhibitory interference), while lure-match effects from NP
stimuli are generally negative11. I interpret this as suggesting that NP and QP lures
differentially affect processing. E.g. it could be the case that people can access non-
c-commanding NP, but not QP lures. If these conclusions are on the right track, it
would mean that PP2017 claim about structural cues failing to categorically restrict
dependencies resolution is overly general and that some structural information does
play a gating role. It may be that a feature like Kush et al. (2015) is used to approx-
imate c-command relations. In combination with my previous conclusions about the
presence of lure-match effects in “animate” conditions, it may mean that some kinds
of structural information, such as (approximated) c-command can accurately guide
retrieval, while some other kinds (like locality) cannot.
In order to validate these conclusions, in the next two experiments I turn to
configurations with c-commanding NP and QP lures. If my conclusions about the
11And in cases when they do float around zero, the QP lure-match effects are still different,
going in the positive direction
123
representation of c-command are correct, I expect to observe lure-match effects from
both NPs and QPs.
3.4 Experiment 3
3.4.1 Participants
38 members of University of Maryland participated in the experiment for a
class credit or a payment of $10 (13 M, 25 F; mean age: 20.2, SD: 1.2). The experi-
mental session took around 45 minutes on average, including setup and calibration.
Data from 3 participants were excluded due to poor quality (high amount of trials
with trackloss / missing data points in the critical regions).
3.4.2 Materials
24 experimental sentences, modeled after Parker and Phillips (2017, Exp.3)12
were included in the experiment. An example of a full set of stimuli is given in Table
3.2.
Several modifications were made to the design in order to address the concerns
from Experiment 2. The main idea was to create conditions which would maximally
favor the resolution of the dependency to the QP lures. First of all, I put the lures
in a position which makes them good binders from the grammatical point of view:
subject position of the matrix clause, with both the target and the reflexive being
12Many thanks to Hanna Muller for helping with the stimuli construction and providing native
speaker judgments.
124
inside a complement clause. This configuration ensures that the QP c-commands
the reflexive, and the only thing stopping the QP from being linked to the reflexive
are locality restrictions on the reflexive. Second, I got rid of accompanying contexts,
shortening the experiment and reducing the risk of participants being overstrained.
As in the previous experiment, all experimental stimuli with reflexives are ungram-
matical.
The properties of the sentences were similar to those in Experiment 2. All
lures and reflexives were always singular, targets were always plural. Matrix verbs
were verbs of speech or belief. In the QP conditions, matrix predicates had the form
“would V” (“No X would V that. . . ”), while in the NP conditions, the predicates
were of the form “did not V” or “would never V”. This was done to make the sen-
tences in the two sets more parallel in meaning. There was equal number of feminine
and masculine reflexives. As in the previous experiment, I tried to make sure that
the target and the lure are equally plausible antecedents for the reflexive, given the
verb of the embedded clause. E.g. in Table 3.2 expectant mothers can plausibly dis-
tress themselves (target antecedent) or the doctor/nurse (lure antecedent). Spillover
regions were aligned in structure. The first word after the reflexive was always a
preposition, optionally followed by a determiner, then by an adjective or nominal
modifier. I made sure that spillover regions did not contain null elements or gaps
like in “. . . humiliated himself trying to get a spot”, since the presence of a gap
could initiate additional memory access and retrieval operations.
I also tried to make the sentences as natural out of context as possible. In
particular, I tried to construct situations in the following way: they describe some-
125
thing that a certain group would never do or think. The group has to be selected
in such a way that this generalization naturally follows from the membership in the
group alone. E.g. we can expect that understanding doctors will be patient; this
does not necessarily hold for all doctors. We found that such subgroups are often
well defined by adjectives which describe a function (flower girls, cleaning ladies),
social status / power (powerful, influential), common sense (reasonable, discrete).
As in the previous experiment, I include an additional set of agreement at-
traction sentences. The same conditions as in Experiment 2 were used, but the
overall reduction of the experiment size allowed us to include 24 control items (6
per conditions). Additionally, I used 96 filler sentences of different types. They
included sentences with grammatical reflexives bound by NP and QP antecedent
and sentences with QP subjects. All of the fillers were grammatical. Overall, the
experiment had 144 sentences and grammatical-to-ungrammatical ratio was 3:1. All
sentences were accompanied by forced-choice Yes/No questions.
3.4.3 Procedure
The procedure was identical to Experiment 1.
3.4.4 Analysis
Same analysis procedure as in Experiment 2 was used.
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Figure 3.5: Experiment 3. RT means for agreement sentences.
Columns correspond to eye-tracking measures: fp - first-pass, rp - regression path, rp -
total times. Rows correspond to ROIs. Errors bars represent standard error of the mean,
adjusted for participant variability (Cousineau, 2005; Morey, 2008)
Figure 3.6: Experiment 3. RT means for reflexive sentences.
Columns correspond to eye-tracking measures: fp - first-pass, rp - regression path, rp -
total times. Rows correspond to ROIs. Errors bars represent standard error of the mean,
adjusted for participant variability (Cousineau, 2005; Morey, 2008)
127
NP lures
Grammatical, Lure match
The understanding doctor would not complain that expectant
mothers distress himself during stressful medical examinations.
Grammatical, Lure mismatch
The understanding nurse would not complain that expectant
mothers distress himself during stressful medical examinations.
QP lures
Grammatical, Lure match
No understanding doctor would complain that expectant
mothers distress himself during stressful medical examinations.
Grammatical, Lure mismatch
No understanding nurse would complain that expectant mothers
distress himself during stressful medical examinations.
Table 3.2: Experiment 3 materials example
Targets are underlined, lures are bolded.
3.4.5 Results
Mean question answering accuracy was 94%. Figures 3.5 and 3.6 show the
observed reading times means for agreement and reflexive stimuli respectively.
Starting with the control agreement sentences, I did find statistical support for
multiple effects. In the critical region, the main effect of target match reached
significance in all three eye-tracking measures; the positive coefficient indicates that
on average target match conditions were read faster than target mismatch con-
ditions. This is the grammaticality effect. This main effect was qualified by a
significant target match x lure match interaction in regression path. Pairwise
comparisons confirmed that this effect was driven by the classical agreement attrac-
tion pattern: lure match conditions were read faster only within target mismatch
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conditions. I also observed a trend for this interaction in total times, but it did
not reach significance there. In the spillover, I observed a significant main effect
of target match and a significant target match x lure match interaction
in regression path. These effects receive the same interpretation as in the critical
region.
Turning to reflexive conditions, I found no reliable evidence for any effects, as
in Experiment 2.
Multiple comparison corrections I follow the same logic as in Experiment 2,
correcting for 12 comparisons, which results in critical t-value of ±2.87. All the
main effects reported above survive this correction, and neither of the interactions
does.
3.4.6 Discussion
Agreement attraction stimuli As in Experiment 2, I used agreement attraction
sentences to confirm that the experiment worked as intended. This time I received
a stronger support for this being the case. First of all, I observed reliable grammat-
icality effects at the critical region in all eye-tracking measures. More importantly,
I also observed the target match x lure match interaction in regression path
at the critical and spillover regions, which is indicative of the presence of agreement
attraction. Together with the trend in total times, I take this as evidence that peo-
ple did behave as expected at least with subject-verb agreement. I note that these
interactions do not survive Bonferroni correction for multiple comparisons, but I
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return to further discussion of this issue after presenting the results for reflexive
sentences.
Reflexive stimuli The main question I addressed in this experiment was: do c-
commanding QP lures give rise to lure-match effects? There is very little indication
that they do. Even if we ignore the lack of statistically reliable effects and look
at numerical magnitudes of the interference effects, most of them are very close to
zero, with the exception of total times, where I observe lure-match effect of roughly
50 ms. The magnitudes of the interference effects are rather similar between the
stimuli with NP and QP lures, suggesting that they were treated similarly by the
parser.
The interpretation of these results is complicated by the fact that I observe
almost no evidence for lure-match effects from NP lures, contrary to what PP2017
and S2017 report. In this respect, this experiment is similar to Experiments 1
and 2; but now this lack of the effects may be more worrying: both PP2017 and
S2017 consistently observed lure-match effects from c-commanding lures in multiple
experiments. This again raises the possibility that my current experiment had some
confounds which affected the manifestation of the lure-match effects. If this is the
case, the data may be uninterpretable.
As before, I conduct more detailed comparisons with the original study (Parker
and Phillips (2017) Experiment 3). This exploratory analysis followed the outline
and modifications to the pre-processing procedure described in Experiment 2. I
also included data from (S2017) Experiment 1 (conditions with speech verbs) in
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comparison, since their stimuli are structurally identical to ours. The comparisons
are presented visually in Fig. 3.7. We can observe that regardless of the pre-
processing procedure, interference effects for NP lures at the critical region are
consistently smaller than in the original studies by PP2017 and S2017.
Figure 3.7: Experiment 3. Comparisons of the interference effect magnitudes in
reflexive conditions with Parker and Phillips (2017).
Interference effect is calculated as the difference between lure match and lure mismatch
conditions. Errors bars represent standard error of the difference of the means (calculated
under the assumption that RTs in lure match and lure mismatch conditions are not cor-
related. This is likely false, since they come from the same subjects, thus, the SEs are
overestimates).
As in Experiment 2, I can readily rule out the possibility that the experiment
did not work at a basic level: I did observe he expected effects of length on RTs
and first-pass skipping probability. I also did find evidence for agreement attraction,
suggesting that the experimental procedure was fine and allowed me to detect lure-
match effects.
However, my stimuli did include an important confound. I did not control the
type of embedding verb, and only half of the verbs were speech verbs. This may
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be critical: as S2017 demonstrates, in configurations similar to mine lure-match
effects are only observed with embedding verbs of speech, and not perception. If in
my stimuli lure-match effects were effectively elicited only by half of experimental
sentences, it could lead to the reduction ot the average magnitude of the effect. I rule
this confound out in the next experiment and delay further discussion of patterns
in QP sentences until I have done that.
3.5 Experiment 4
3.5.1 Participants
40 members of University of Maryland participated in the experiment for a
class credit or a payment of $10 (19 M, 21 F; range: 18-26; mean age: 20.3, SD:
1.44). The experimental session took around 45 minutes on average, including setup
and calibration. I excluded data from 2 participants: one because of software issues,
another one due to extremely low proportion of correct responses (11%).
3.5.2 Materials
I had two sets of 24 experimental items, following the structure from Experi-
ment 2. The examples of the items are given in Table 3.3. One of the sets had QP
lures, and was of main interest; the other one had NP lures and was used as control.
The QP set was based on the stimuli from Experiment 3 with two differences.
First, all matrix verbs were verbs of communication. Most of the verbs (18 out of
24) were taken from S2017. The change of the verbs required changing some of
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NP lures
Grammatical, Lure match
The worried doctor reported that the delirious hiker talked to
himself in the operating room before the procedure.
Grammatical, Lure mismatch
The worried midwife reported that the delirious hiker talked to
himself in the operating room before the procedure.
Ungrammatical, Lure match
The worried doctor reported that the delirious mothers talked
to himself in the operating room before the procedure.
Ungrammatical, Lure mismatch
The worried midwife reported that the delirious mothers talked
to himself in the operating room before the procedure.
QP lures
Grammatical, Lure match
No shy girl would mention that the prom queen embarrassed
herself in the school cafeteria after class.
Grammatical, Lure mismatch
No shy boy would mention that the prom queen embarrassed
herself in the school cafeteria after class.
Ungrammatical, Lure match
No shy girl would mention that the schoolyard bullies embar-
rassed herself in the school cafeteria after class.
Ungrammatical, Lure mismatch
No shy boy would mention that the schoolyard bullies embar-
rassed herself in the school cafeteria after class.
Table 3.3: Experiment 4 materials example
Targets are underlined, lures are bolded.
the stimuli to maintain the naturalness of the scenarios. Second, in addition to un-
grammatical sentences with the target mismatching the anaphor in two features, the
experiment included grammatical sentences, with the target matching the anaphor.
Thus, two factors were manipulated: target match (the anaphor either matches
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the target fully or mismatches it in gender and number) and lure match (rhe
anaphor either matches the lure fully, or mismatches it in gender). The NP set con-
sisted of a subset of stimuli from S2017, adapted virtually verbatim13. Similarly to
the first set, all verbs were speech verbs, and the same two factors were manipulated.
Overall, I had 24 sentences with QP lures (12 grammatical), 24 sentences
with NP lures (12 grammatical) and 96 fillers (adapted from Experiment 2; all
grammatical), for a total of 144 sentences. Thus the grammatical-to-ungrammatical
ratio was 5:1. As in the previous experiments, all sentences were accompanied by a
forced choice Yes/No question.
3.5.3 Procedure
The procedure was identical to Experiment 1.
3.5.4 Analysis
I used the same preprocessing procedure as in Experiment 1, and analyzed
the same regions (critical, spillover) and measures (first pass, regression path, total
time) of interest. The definitions of the regions were the same as in Experiment 1
13The only change was the following. In two sentences, I exchanged the genders of the targets in
grammatical and ungrammatical conditions. E.g. if the original combinations of target-anaphor
were “actor - himself” and “actresses - himself”, I replaced it with “actress - herself” and “actors -
herself”. This was done to counter-balance the number of feminine and masculine reflexives in the
experiment. I do not think that this change affects the results of the experiment, since presumably
what matters is the gender-match between the noun and the anaphor, not the lexical identity of
the noun.
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for the QP stimuli; for the NP stimuli, I followed the region mark-up reported in
Sloggett and Dillon (in prep). NP and QP stimuli were analyzed separately (since
the materials were not lexically matched) with the same modeling procedure as in
Experiment 3.
3.5.5 Results
Mean question answering accuracy was 90%. Fig.3.8 shows the observed read-
ing times means.
Statistical analyses provide robust evidence for the grammaticality effect: main
effect of target match reached significance in the regression path and total times
across virtually all regions of interest for both NP and QP conditions (except regres-
sion path in the critical region of NP sentences). The positive sign of the coefficient
indicates that on average, 2-feature target mismatch conditions were read slower
than target match conditions. However virtually no evidence for the interference
effect was found. Two interactions have reached significance: NP stimuli, first-pass
times at the critical region and QP stimuli, total times at the spillover region. Pair-
wise comparisons indicate that the first difference is likely driven by slower reading
times in lure match conditions within target match conditions only. In the second
case neither of the pairwise comparisons was significant, and Figure 3.8 suggests that
the interaction effect is driven by the cross-over pattern of the means: lure match
conditions are slower in target match sentences, but faster in target mismatch ones.
135
Multiple comparison corrections The number of the models I am building
in this experiment is the same as in the previous one, thus, the critical t-value
for Bonferroni correction remains the same: ±2.87. Grammaticality effects mainly
survive the correction (only three do not: NP stimuli, total time at the critical
region; QP stimuli, first pass and regression path at the critical stimuli). On the
other hand, neither of the observed interactions (NP stimuli, first pass at the critical
region and QP stimuli, total time at the spillover) survives the correction.
3.5.6 Discussion
The primary question that this experiment addressed was: is the type of
the embedding verb responsible for the lack of reliable lure match effects from c-
commanding lures that I observed in Experiment 3? The answer appears to be
negative. Despite ensuring that all of the embedding verbs were verbs of communi-
cation, and despite using a subset of stimuli from S2017, which have already been
shown to provoke lure-match effects, I failed to find statistical support for interfer-
ence effects.
The only two statistically significant effects I observed are not in line with
PP2017 and S2017. The interaction effect in the first-pass times at the critical
region may serve as a weak evidence for intrusion effects in NP sentences. However,
the intrusion pattern observed there does not match that reported by PP2017and
S2017. If anything, it is rather more similar to the effects reported by Badecker and
Straub (2002, Exp.3) and Patil et al. (2016): lure-match conditions are read slower
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than lure-mismatch in grammatical sentences. Such effects are predicted by some
memory models of sentence processing(see, e.g. Jäger et al., 2017), but there is a
discussion in the literature whether they should be treated as evidence for memory
retrieval problems (see section 1.2.2 for more details). For now, I am hesitant about
whether these effects are meaningful and if they are, why the same set of stimuli
would give rise to facilitation in some studies and inhibition in others.
Similarly, the interaction I observed in total times at the spillover regions
for the QP sentences is likely driven by the crossover pattern of the means alone.
Neither of the pairwise comparisons reaches significance, and the t-value for the
interaction is right at the critical threshold. Incidentally, numerically the pattern of
reaction rimes was similar to the one I observed in NP stimuli in first-pass at the
critical region: lure match conditions are slower in target match sentence but faster
in target mismatch . But since the pairwise comparisons did not reach significance,
right now I prefer not to ascribe meaning to these patterns.
As in the previous experiments, I perform more detailed comparisons of my
results with PP2017 and S2017. Fig.3.9 shows the magnitude of the interference
effect in 2-feature target mismatch conditions with NP lures. The results look
virtually identical to the previous studies: at the critical region, interference effect
is much smaller in my case than in either PP2017 or S2017, and the choice of the pre-
processing procedure has practically no effect. We can also notice that lure-match
effects are somewhat more robust in comparison with Experiment 3: they more
consistently reach the magnitude of at least 50 ms, and sometimes they get even
bigger. This suggests that while the type of the embedding verb is not responsible
137
for the lack of statistically significant results, it might have still played a role in
reducing the average size of the interference effects.
Controlling for the embedding verb type allows for a cleaner comparison of
the NP and QP stimuli. As in Experiment 3, they align rather closely: interference
effects go in the same direction and have comparable magnitudes, regardless of
the choice of the preprocessing procedures. I take this as an indication that both
lure types were treated by the parser similarly. That said, the similarity is not
absolute: in regression path (both pre-processing procedures) and re-read times
(S2017preprocessing only), the interference effect for NP stimuli is twice as big as in
QP sentences. This may indicate that for some reason QP lures are less accessible
to the parser. However, given that this difference at least partially depends on the
analysis procedure and given that I do not have reliable evidence for interference
within either pre-processing procedure, I prefer to remain conservative and conclude
that the current dataset does not provide strong evidence for differential interference
effects with NP and QP lures.
Overall, based on the numerical patterns I tentatively conclude that a) lure-
match effects are provoked by NP and QP in roughly the same degree; b) this fact,
together with the findings of no lure-match effect from non-c-commanding QP lures
in Experiment 2 suggests that a feature similar to Kush et al. (2015) accessible
categorically controls the access to reflexives antecedents. These conclusions are
somewhat dependent on my interpretation of the reduced magnitude of the inter-
ference effect in the stimuli with NP lures. If it turns out that I have missed some
important confound, the conclusions above may not hold. I discuss these issues in
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more detail in the general discussion.
3.6 General discussion
In this chapter I have presented three experiments attempting to clarify Parker
and Phillips (2017) conclusions about the nature of structural constraints, focusing
on c-command. I contrasted two possibilities: c-command is encoded in a process-
agnostic fashion, or c-command is encoded as a process-specific feature, like Kush
et al. (2015) accessible. To differentiate between these possibilities, I investigated
QP lures in both c-commanding and non-c-commanding positions.
The evidence for lure-match effects in sentences with QP lures was extremely
weak across all three experiments. The only statistically significant effect which
could be interpreted as evidence for interference was observed in Exp.4 in total
times at the spillover. Even there the pairwise comparisons were not significant, not
allowing to conclude that the overall interaction indeed reflected lure-match effects.
Additionally, this interaction effect stopped being significant after Bonferroni cor-
rection for multiple comparisons. Thus, the best evidence for intrusion I have comes
from the numeric pattern of the means.
In Exp.2 I observed that the numeric patterns of the RTs were different for
QP and NP lures. While NP lures mostly provoked facilitation, QP lures provoked
inhibition (i.e. sentences with matching lures were read slower). I interpreted these
patterns as indicating that the parser treats non-c-commanding NP and QP lures,
and this may be evidence for the use of accessible. If this conclusion were correct,
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we should be able to observe interference from both NP and QP lures when they
c-command the reflexive.
The numerical patterns observed in Experiments 3 and 4 were consistent with
this prediction: both NP and QP c-commanding lures appeared to elicit interference
effects. The evidence was clearest in Experiment 4: lure-match effects in NP and
QP stimuli had similar direction and magnitude, with the effects reaching 50 ms in
most eye-tracking measures regardless of the pre-processing procedure I used. These
patterns were somewhat weaker in Experiment 3: effect sizes were smaller and some
of the effects were grouped around zero. However, the alignment between NP and
QP stimuli was largely the same. I took this to mean that the parser treated the two
types of lures similarly. Weaker evidence in Experiment 3 could be explained by the
properties of the stimuli I used: in Experiment 3 only have of the predicates I used
were verbs of communication, while in Experiment 4 all of them were. Since S2017
showed that lure-match effects most consistently appear when the lures are subject
of communication verbs, the reduced proportion of such verbs in Experiment 3 could
lead to the reduction of the average lure-match effect sizet. If these conclusions are
correct, these data would support the hypothesis that accessible is used as a proxy
to c-command in reflexives resolution.
A second possible interpretation of my QP data is that the effects are not real,
and the numerical patterns I observe are due to random noise. This interpretation
would basically mean that for some reasons QPs are not efficient lures. If this is
the case, my data cannot be used to make any conclusions about how c-command
information is encoded in the system. Exactly why QPs would be bad lures is
140
not clear, but I discuss several speculative possibilities. The first has been already
mentioned: QPs may be bad lures not inherently, but because they lead people to
weigh structural information more highly during reflexive resolution. This variant
assumes that PP2017 story is correct, since in S2017 account structural features
are already perfectly constraining retrieval to select the appropriate antecedents. It
would be quite easy to test: e.g. one could look at the sentences with quantificational
targets, e.g. “The actress said that the/most directors like herself”. If the presence
of a QP does indeed change processing strategies, we would only observe interference
from “the actress” with referential targets (“the directors”). A second possibility for
why QPs might be bad lures assumes that S2017 account is correct. In this case it
may be the case that QPs make bad logophoric antecedents. E.g. OPlog might not
be able to efficiently track the kind of entities that QPs introduce in the discourse. If
this is the case, QPs would not lead to interference in any configurations considered
by S2017. This would be the conclusion compatible with the data from Postal
(2006) I mentioned in the introduction to this chapter, although it would go against
cross-linguistic evidence.
Deciding whether the QP effects are real (and thus - should be taken into
account at all) depends on the interpretation I assign to the evidence coming from
the sentences with NP lures. The evidence for intrusion in the sentences with NP
lures was also very weak, unlike in previous studies by PP2017 and S2017, but
similarly to my Experiment 1. What do we make of this fact? There are several
questions we need to address. First, do we have any reason to believe that the
previous findings are not reliable? I do not think so. The only explanation I can
141
think of how a nonexistent effect can receive statistical support is a Type I error.
While it is not inconceivable that all of the previous findings are due to Type I
errors, it is rather implausible, since the intrusion effects look very similar in the
previous experiments, at least in terms of direction and the magnitude (the timing
of the effects appears somewhat more subject to variability for unclear reasons).
If reliability of the previous finding is not a concern, the next question is: why
did I not observe statistically supported evidence for intrusion effects in my study?
To begin with, it could be that I have some basic problems with experimental
procedure and my data cannot be trusted at all. I do not think this to be the
case for several reasons. On a basic level, people did exhibit basic reading effects
(longer words provoking increase of reading times and decrease of first-pass skips).
Question answering accuracy was generally high14. Next, I did find support for
interference effects in subject-verb agreement sentences. Finally, it is not the case
that no statistically significant effects were observed at all. Reliable grammaticality
effects were observed in Exp. 3 and 2, and this suggests that people were sensitive
to the grammatical properties of the input.
If the general experimental procedure is fine, the next question is: are there
any systematic confounds which could have weakened intrusion effects in reflexive
stimuli, or made them disappear altogether? I have already ruled out two such
confounds. First, numerically small effects in Exp.2 from the lures embedded inside
a relative clause could be due to the fact that the embedding nouns were animate.
It would be consistent with the hypothesis advanced by Sloggett (2017): lure-match
14Mean response accuracies: Exp.1 — 92%, Exp.2 — 94%, Exp.3 — 90%.
142
effects from lures within a subject relative clause represent a case of sub-command
binding, similarly to ziji in Chinese (Huang and Liu, 2001). However, my results
from Chapter 2 do not support this possibility: there, I observed lure-match effects
from lures inside a relative clause regardless of the embedding NP animacy. Also
notice that the sub-command explanation would not account for reduced lure-match
effects in Exp. 3 and 4: in these experiments the lure in fact c-commanded the
reflexive, being the subject of the matrix clause which embedded the complement
clause containing the reflexive. Second, I have considered the effect of the embedding
verb type (speech vs. perception) on the lure-match effect from c-commanding lures.
This factor appeared to be of some importance: Experiment 4, which controlled for
it, showed more consistent and numerically bigger lure-match effects. However,
even there the effects were smaller than in the previous studies. This is even more
telling since I have used a subset of the stimuli from S2017, which have been shown
to produce lure-match effects. Thus, the verb type alone cannot account for the
reduction of the magnitude of lure-match effects in comparison with the previous
results.
I identify two further possibilities, which I broadly classify as extra-linguistic
context effects. The first possibility is that merely the presence of QP stimuli in the
experimental materials might have affected lure-match effects in the whole experi-
ment. E.g. the presence of QPs might have forced the parser to weigh structural
features more highly, since they may be more important for dependencies involv-
ing QPs. The second possibility has to do with the properties of the experimental
procedure, namely, the language status of the experimenter. In my case, the partic-
143
ipants were instructed in non-native English, and it is possible that they might have
adjusted their processing strategies. There exists evidence that such adjustments
can in fact happen. E.g. in an EEG study on Dutch Hanuĺıková et al. (2012) gender
violations elicited a P60015, if the stimuli were read by a native Dutch speaker, but
not when they were read by an L2 Turkish speaker. It is conceivable that something
similar happened in my experiments, although additional qualifications are neces-
sary to explain why grammaticality effects were observed, if we think that people
corrected for non-nativeness of the experimenter. One could say that adjustments
were selective, such that violations were ignored in only one of the two morphologi-
cal features I manipulated (number and gender). In this case, the sentences would
essentially behave as one-mismatch sentences for which Parker and Phillips (2017)
only found grammaticality effects. Another possibility compatible with Parker and
Phillips feature weighting account would be that the adjustment effectively down-
weighted morphological features; in this case, the speakers would have to solely rely
on syntactic features, which would predict only grammaticality effects without in-
teractions. Yet another possibility is that repair processes are adjusted. It has been
argued that agreement attraction arises as a result of repair and not initial misre-
trieval (e.g Lago et al., 2015). The evidence is based on the fact that attraction
seems to only arise in a small proportion of trials with longest reaction times, while
grammaticality effects are seen in a larger proportion of reaction times, including
shorter ones. If people are able to selectively suppress repair (e.g. if they realize
that with non-native speech repair will have to happen too often), we could expect
15ERP component, often associated with grammatical violations.
144
to only see grammaticality effects. It is unclear whether this last explanation would
work for reflexives.
Notice that as discussed the confounds only suggest that something might
have gone wrong. They do not tell us whether the effect is real, but weakened, or
whether the confounds affected the experiment to such degree that the effects were
gone altogether, and the numerical patterns represent just noise. To figure this out,
I could compare the patterns of my results to the previous findings. Presumably,
if the effects in my study are real, they would be similar to the effects observed
in the previous studies. If my effects are not real and the patterns of the means
just reflect random noise, we might expect the patterns to be incongruent, either
between themselves, or in comparison with the previous literature, or both. In the
latter case the random nature of noise does in principle allow the situation where
the effects are not real, but by chance alone the means pattern consistently with the
previous studies. I did perform such comparisons, but will defer the discussion until
the end of the next chapter, when more relevant data, including those from direct
replications of previous studies, will have been discussed.
To summarize, I tentatively concluded that the data from QP lures indicate
that c-command information is represented in an approximate way. However, these
conclusions are uncertain due to the lack of statistical evidence for interference effects
from NP lures, which may indicate that some unknown factor has confounded my
results. If this is the case, it may not be safe to make any conclusions about QP
stimuli at all. The lack of lure-match in NP stimuli is also worrying, since it may
indicate that the interference effects in reflexive resolution may be spurious or at
145
least subject to higher degree of variability than PP2017 and S2017 results could
lead to believe. In order to better understand the reason for my non-replication, I
attempt two direct replications of PP2017 findings, which I discuss in the following
chapter.
146
Figure 3.8: Experiment 4. RT means for agreement sentences.
Columns correspond to eye-tracking measures: fp - first-pass, rp - regression path, rp -
total times. Rows correspond to ROIs. Errors bars represent standard error of the mean,
adjusted for participant variability (Cousineau, 2005; Morey, 2008)
Figure 3.9: Experiment 4. Comparisons of the interference effect magnitudes in
2-feature target mismatch conditions with PP2017and S2017.
Interference effect is calculated as the difference between lure match and lure mismatch
conditions. Errors bars represent standard error of the difference of the means (calculated
under the assumption that RTs in lure match and lure mismatch conditions are not cor-
related. This is likely false, since they come from the same subjects, thus, the SEs are
overestimates).
147
Chapter 4: Replicability of lure-match effects in reflexive resolution
In the previous chapter I reported experiments aimed at understanding the
role of c-command information in the reflexive resolution. The focus was on the
behavior of quantificational lures - I predicted that only if PP2017 is correct, we
would see lure-match effects. I did not find any reliable evidence for such effects,
while the numerical patterns indicated that PP2017 approach may not be on the
right track. However, these conclusions were weakened by the fact that I found no
detectable interference from referential lures, using stimuli similar or identical to
those used in the previous studies. It is not clear whether lure-match effects did
not receive statistical support because of some confounds, which could have affected
the effect sizes. This means that the QP results from the previous chapter cannot
be used to make strong conclusions about my main question until I have a better
understanding of what could have caused the smaller lure-match effect magnitudes.
As I have discussed in the previous chapter, it is possible that the lack of lure
match effects is due to people adjusting their processing strategies in response to
some property of the experiment, e.g. the presence of QPs in the materials or the
non-nativeness of the experimenter. Ruling out these confounds is the primary goal
of this chapter: Experiment 5 addresses the first concern, and Experiment 6 - the
148
second one.
In addition to helping with interpretation of the earlier findings, these ex-
periment may also be used to distinguish between PP2017 and S2017 accounts.
Adjustment of processing strategies in response to experimental context factors is
relatively easy to explain if we adopt PP2017 account: one could say that people
re-weigh their retrieval cues, giving more priority to structural information, and
with this new set of weights even a mismatch in two morphological features is not
enough to outweigh structural features. On the other hand, S2017 account would
have hard time accommodating this finding. To remind, the account postulates
that lure-match effects arise because people retrieve a structurally accessible null
operator in a proportion of cases. In order to account for (hypothesized) effects
of the experimental context, we would have to come up with a mechanism which
would reduce the preference for choosing logophoric interpretation depending on the
broader (extra-linguistic) context properties.
The only straightforward way of doing this would be to somehow ensure that
OPlog is less accessible for retrieval. One way of doing it would be to lower the
degree of match of OPlog with the retrieval cues. There are two ways of doing this:
modifying featural representation of OPlog and modifying the set of retrieval cues.
The first way is rather implausible. OPlog is hypothesized to by φ-deficient and to
only carry a structural feature, encoding both c-command and locality information.
It is hard to imagine that OPlog will or will not include information about its clause-
hood depending on the context. The second way could in principle work; however,
in this case, it would imply not using structural cues to guide retrieval. If this
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were to happen, lures could be accessed directly, and we would still expect to see
lure-match effects even in context hypothesized to produce processing adjustments.
Alternatively, one could try to raise the activation of the overt target to the
degree where it would always outcompete OPlog. Again, I do not think it is plausible
that the featural composition of the target will be affected by the context, and it is
not clear what additional cues specific only to the overt target could be added to
the retrieval cues set. Thus, this possibility seems to fail as well.
Finally, one could hypothesize that the activation of OPlog and/or overt tar-
get is changed because the change in experimental context affects their linguistic
prominence (see the discussion in section 1.5.1.1). I might see how the presence of
QP sentence could do it: perhaps, in a sentence with a QP lure and an NP target
the latter becomes more prominent because it refers to a specific entity; then, the
comprehenders would have to make this shift even for the sentences with the NP
lures. It is not clear to me how the (non-)nativeness of the experimenter would
change linguistic prominence of OPlog or overt targets.
4.1 Experiment 5
In this experiment I attempt a direct replication1 of PP2017 Exp.3 in order to
assess whether the presence of QP sentences in the stimuli set of my Exp.2-4 could
have affected the results. I use their exact materials with minor corrections (typos
etc., as specified below). I also collect a sample which is twice as big as theirs (48
1I would like to thank Dan Parker for generously sharing the eye-tracking scripts, materials and
data from his studies.
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vs. 24 people) which gives better statistical power and reduces the likelihood of
over-estimating the magnitude of the effects.
4.1.1 Participants
52 members of University of Maryland community (38F, 14M; age range: 18-
25, average age: 20.1) participated in the experiment for a class credit or a payment
of $10. The experimental session took about one hour, including setup and calibra-
tion. Data from four participants were removed: two participants did not manage
to complete the experiment in an hour, and two participants gave incorrect answers
to more than 30% of comprehension questions.
4.1.2 Materials
Stimuli and fillers were directly adopted practically verbatim from PP2017
Exp.3 (I literally used the same eye-tracking script). The examples of the stimuli
are given in Table 4.1. The only modifications I made consisted in correcting typos
and inconsistencies in the stimuli sets (the full list of modifications can be found
in Appendix D). Overall, the stimuli set had 36 experimental sentences and 72
fillers. 24 out of 36 experimental sentences were ungrammatical, all fillers were
grammatical, giving a ungrammatical-to-grammatical ratio of roughly 1:4.
4.1.3 Procedure
The procedure was identical to Experiment 1.
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Target match, Lure match
The talented actor mentioned that the attractive spokesman
praised himself for a great job.
Target match, Lure mismatch
The talented actress mentioned that the attractive spokesman
praised himself for a great job.
Target mismatch (1 feature), Lure match
The talented actor mentioned that the attractive spokeswoman
praised himself for a great job.
Target mismatch (1 feature), Lure mismatch
The talented actress mentioned that the attractive spokeswoman
praised himself for a great job.
Target mismatch (2 features), Lure match
The talented actor mentioned that the attractive spokeswomen
praised himself for a great job.
Target mismatch (2 features), Lure mismatch
The talented actress mentioned that the attractive spokeswomen
praised himself for a great job.
Table 4.1: Experiment 5materials example
Targets are italicized, lures are bolded.
4.1.4 Analysis
In my initial analyses, I followed PP2017 in choice of regions and measures of
interest, and statistical comparisons. Although I do have concerns about their pro-
cedure, which I will discuss later, I decided to first follow their procedure as closely as
possible to create a baseline comparison between results reported in PP2017 and my
replication attempt. Three regions of interest (ROIs) were defined: precritical, which
included the embedded subject and predicate (i.e. four words before the reflexive
pronoun); critical, including only the reflexive pronoun itself; and spillover, includ-
ing two words after the pronoun. Four eye-tracking measures of interest (MOIs)
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were analyzed: first-pass, right-bound, regression path and total times. Definitions
were given earlier.
Prior to statistical analysis, the data were manually pre-processed using Eye-
Doctor2 to remove blinks and ensure that fixations align with the text. Fixations
shorter than 80 ms or longer than 1000 ms were automatically rejected before cal-
culating eye-tracking measures using custom scripts3. Then, reading times were
log-transformed and missing observations were replaced with zeros.
A linear mixed effect model with target.match, lure.match and their
interaction were then fit to the data. Treatment coding was used with baseline level
being target: match, lure: mismatch to every ROI and MOI. I will refer to
this model as “full model”. Additionally, a series of smaller models was fit to subsets
of conditions. One model, including the same predictors, was fit to ungrammatical
conditions only (baseline level was recoded to target: one mismatch, lure:
mismatch). The interaction term from this model was used to assess the difference
in interference effect between one-mismatch and two-mismatch sentences. I will refer
to this model as “ungrammatical-only” model. Two more models corresponding
to pairwise comparisons were fit separately to the ungrammatical target: one
mismatch and target: two mismatch conditions, to assess simple main effects
of lure match. No corrections for multiple comparisons were performed.
2https://blogs.umass.edu/eyelab/software/
3Avaliable at: https://github.com/UMDLinguistics/EyePy. Notice that PP2017 relied on
the previous generation of these scripts, so this pre-processing step was not exactly identical across
the two studies.
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target.match : lure.match | item
target.match : lure.match | participant
target.match | item
lure.match | item
target.match | participant
lure.match | participant
Table 4.2: Order of random effect structure simplification, Exp.5. Effects were
removed from the model, starting from the top.
If the model with the maximal random effect structure did not converge4, I
simplify it by removing random slopes. PP2017 did not specify their procedure in
much detail, stating only: “random slopes for items or participants were removed”.
To be internally consistent, I always dropped the random effects in the order shown
in Table 4.2. As a final step, all models were automatically assessed to check whether
any random effects had correlations of 1 or -1. The procedure was described in more
detail in section 2.1.4.
4.1.5 Results
Mean question accuracy was 91%. Observed patterns of mean reaction times
are shown in Fig.4.1. Numerical values for the means are given in Appendix A.
Fig.4.1 is laid out as follows. Columns correspond to reading times measures
(see figure description for details). They have to be arranged in two separate sub-
panels because the time scales are quite different between early and late measures
(especially in the critical and spillover regions), and plotting them all in the same
4As determined by diagnostics reported by lmer. One has to access the internal structure of the
model fit and look at the information contained in m@optinfo$conv$lme4, where m is the model
object.
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Figure 4.1: Mean RTs in PP2017 (red) and my replication (blue).
Error bars represent standard error of the mean. Conditions: tm/tomm/ttmm - target
match/one-mismatch/two-mismatch; lm/lmm - lure match/mismatch. Columns corre-
spond to eye-tracking measures: fp - first-pass, rb - right-bound times, rp - regression
path, rr - re-read times. Rows correspond to ROIs: precritical, critical, spillover.
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plot would make it harder to see the patterns; the sub-panelling does not have
any other purpose except making the exposition clearer. The rows correspond to
ROIs; we will be mostly interested in the central row, corresponding to the critical
region (i.e., the reflexive). X axis corresponds to different conditions (see figure
description); each condition is associated with two RTs: red dots represent means
from PP2017, blue dots - from the current replication. We will be mostly interested
in comparing two rightmost conditions in each facet - they correspond to 2-target
mismatch conditions, where we expect to see interference effects. If PP2017 findings
are replicated, we expect to see that the RTs estimate is much higher in the rightmost
condition, indicating that lure mismatch sentences are read slower than lure match
sentences within 2-target mismatch conditions.
I draw attention to two things in these plots. One is that there is less un-
certainty in the replication, as suggested by the smaller error bars - this is to be
expected, since I had twice as many participants as PP2017 did. Second, in both
studies the estimates in the critical region follow similar patterns, but the replication
estimates seem to be less extreme (e.g. they appear to be bigger than small PP2017
estimates and smaller than large PP2017 estimates). As a result, the numerical
magnitude of the interference effect goes down in the replication, although it is still
appears to be present in the pattern of the means.
Fig.4.2 shows the size of the interference effect in target: two mismatch
conditions, calculated as the difference between lure: match and lure: mis-
match conditions. Negative values indicate that lure: match conditions are read
faster, an indication of facilitatory interference. Since there is not as much infor-
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Figure 4.2: Interference effect in target: two mismatch conditions (lure match
- lure mismatch) in PP2017(red) and my replication (blue).
Error bars represent standard error of the difference of the means. Columns correspond to
ROIs. Rows correspond to eye-tracking measures: fp - first-pass, rb - right-bound times,
rp - regression path, rr - re-read times.
mation in this figure, I change the plot layout: eye-tracking measures are plotted
along the x-axis, and plot facets correspond to ROIs. Critical region - the central
facet - is of most interest, since this is where PP2017 observed the interference effect
most consistently. One can see that interference effects in the replication are much
smaller than in the original PP2017 study. Even the biggest one, observed in re-read
times, is roughly twice as small as the corresponding estimate from PP2017.
Let us now turn to the results of the statistical analysis. For ease of compar-
ison, I present model estimates from two experiment side-by-side on Fig.4.3. The
dots correspond to β̂ values (“Estimate” values from lmer output). In this figure
I am mostly interested in showing which effects reach statistical significance (coef-
ficients for which |t| > 2 are represented with square markers) and whether these
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effects survive multiple comparisons correction (triangles indicate coefficients which
stop being significant after applying the correction; I discuss this issue further down
the text). Intercept estimates are not represented, because they are numerically
much bigger and including them in the overall plot forces the x-axis to stretch, so
that minor differences between other estimates become less noticeable. As in Fig.4.1
columns correspond to eye-tracking measures, and rows - to ROIs. The size of the
estimate is displayed on the X axis (since the models were fit to log-transformed
RTs, the estimates are numerically small). Different effects from the model are
plotted along the Y axis (see figure description for more details).
I will focus my discussion on the critical region (central row), since this is were
the lure-match effects were the clearest in PP2017, and this is what PP2017 base
their conclusions on. For the full models, I can expect three estimates to reflect the
interference effect:
• Main effect of lure match, which would indicate that reading times on the
reflexive differ for matching and mismatching lures, if I compare target:
match and target: two mismatch conditions;
• target match x lure match interaction for target: one mismatch con-
ditions. It would indicate that reading times are differentially affected by lure
mis(match) in target: match and target: one mismatch conditions.
• Similarly for target match x lure match interaction for target: two
mismatch conditions.
In the replication data, only two effects of interest reach significance. The
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Figure 4.3: Model estimates in PP2017 (red) and my replication (blue).
First five effects come from the full model (in order: main effect of target match in
1-mismatch conditions; in 2-mismatch conditions; main effect of lure match; two inter-
actions of lure match and target match for 1-mismatch and 2-mismatch conditions
correspondingly); next two effects are the simple main effects of lure match; finally, the
last effect is the interaction from the ungrammatical-only model. The order of the coef-
ficients is the same as in PP2017, to make comparisons across papers easier. Error bars
represent standard error of the estimate. Coefficients for which |t| ≥ 2 are represented
with squares if they remain significant after a Bonferroni correction (with the corrected
|t| = 3.34), and with triangles, if they don’t.
first one is the pairwise comparison within target: one mismatch conditions
in regression path, indicating that the pronoun is on average read faster in lure:
match conditions. The second effect is the pairwise comparison within target:
two mismatch conditions in total times, which receives a similar interpretation.
This is suggestive of the lure-match effects. However, for neither of those cases, the
interaction term for the full model or the interaction term for the ungrammatical-
only model reach significance. Together with the absence of main effects of lure
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match this suggests that the evidence for lure-match effects is at best weak.
Compare these results with PP2017 data. They do find significant target
match x lure match interactions for target: two mismatch conditions in re-
gression path and re-read times. It indicates that in target: match and target:
two mismatch conditions reading times are differentially affected by lure match.
Pairwise comparison within target: two mismatch conditions reach significance
across all ROIs. This indicates that within target: two mismatch the pronoun
is read faster if it matches the features of the lure. Finally, the interaction term from
ungrammatical-only model also reaches significance across all ROIs. This indicates
that the speed-up associated with matching lures has different magnitude in tar-
get: one mismatch and target: two mismatch conditions. PP2017 interpret
these statistics as providing evidence for two claims: first, that interference effects
do exist, and two, that they only appear in ungrammatical sentences with target
noun mismatching the reflexive in two features. Generally, I agree with this inter-
pretation. But before I proceed, I address two issues with PP2017 analysis which
might affect the conclusions I reach.
Lack of multiple comparisons corrections Despite carrying on quite a lot of
comparisons, PP2017 do not report any multiple comparisons correction. This is
somewhat traditional in eye-tracking studies, but, as von der Malsburg and Angele
(2017) argue, this is not optimal, and if one does run analyses for multiple ROIs and
MOIs, these multiple analyses should be corrected for. von der Malsburg and Angele
(2017) simulations indicate that Bonferroni correction is not overly conservative
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and can be applied in such situations. I use it and assess whether PP2017 and my
conclusions hold after a correction for multiple comparisons. For a given combination
of ROI and MOI PP2017 fit 4 models. One could argue that the full model should
be counted as two comparisons for the purposes of multiple comparison corrections:
we are interested in three effects, coming from this model, but we will be making
only two inferences based on them: whether we have evidence for interference (main
effect of lure match), and whether we have evidence for the interference differing
between grammatical and ungrammatical conditions (two target match x lure
match interactions). Ungrammatical-only model and the simple main effects
models correspond to three more comparisons. Thus, we are making at least five
inferences per a combination of ROI and MOI. Overall, PP2017 analyze 3 ROIs and
4 MOIs, which leaves us with 5x3x4 = 60 comparisons. Given the original α = 0.05,
a Bonferroni corrected α = 0.05/60 = 0.00083. The corresponding t-value5 for a
two-sided test is ±3.34.
For my data, neither of the significant effects remain significant after applying
the correction. In contrast, for PP2017 data many of the significant comparisons
reported for the critical region remain significant after this correction, except the fol-
lowing four (indicated with triangles in Fig. 4.3): two interaction effects for the full
model in regression path and re-read time, and two interaction effect ungrammatical-
5Approximated from normal distribution following Jäger et al. (2015). The corresponding R
command is qnorm(0.00083/2)
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only model in first-pass and re-read times6.
Choice of preprocessing procedures The most notable pre-processing choice
by PP2017 I do not agree with is the decision to replace missing values with zeros.
Although PP2017 are certainly not the first to make this decision (Sturt, 2003;
Cunnings and Felser, 2013; Cunnings et al., 2014; Cunnings and Sturt, 2014, see,
e.g.), there are reasons for which it may be problematic, and I discuss some of them
below.
First of all, at a risk of stating the obvious, missing values are not the same
as zero reading times. In the eye-tracking experiments, there are at least two ways
in which missing values can arise: people did not fixate on a given region, or the
fixation was not recorded due to technical difficulties. I may be willing to ignore this
source of noise and assume that all missing values represent the lack of fixation. But
even if we make this assumption, literally assuming that the dataset includes RTs
of 0 ms does not really make sense. Fixations below 50ms are likely non-existent in
actual reading (Rayner, 1998, plot at p.376), so any and even if they did exist, the
preprocessing procedure PP2017used7, removed any fixations shorter than 80 ms,
so we do not expect to find any smaller values in the data.
Now, one may argue that ”the region was not read” is essentially the same as
6One of the main effects of target match in re-read times also stops being significant. How-
ever, we are not interested in this effect, so I do not discuss it further
7PP2017 do not directly report doing that, but Parker (2014), which is the original source of
these experiments, does. Given that the average RTs reported in both sources are the same, it is
reasonable to assume that the pre-processing procedures were the same, or very similar, as well.
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”the region was read for 0 ms”, and amounts to the difference in wording, but it
does not. If we consider the way reading times may be generated in an eye-tracking
experiment, this difference will be clearer. For a given word, people either make
a fixation on it or not, with a certain probability. If people did fixate the word,
they look at the word for a certain time. Of course, how these specific decisions are
made is probably a very complicated process depending on multiple factors. But
we believe that this general two-step description of the generative process is not
unreasonable. So we are dealing with at least two distributions: one determining
the probability of fixation, and another one - determining the duration of a fixation,
given that it has occurred8. So the statement ”the region was not read” corresponds
to a situation where one drew 0 from the distribution specifying the probability that
the region is re-read9, and the statement ”the region was read for 0 ms” corresponds
to a situation where one drew 1 from the probability of re-read distribution, and
then drew 0 from the distribution of re-read times. Notice that we assume that the
distribution of re-read times even includes 0, which it may not, given the data I
mentioned above on the fixations duration.
A better model for the data of such structure would reflect the structure of
the generative process and could be constructed in two steps: first, use logistic
regression to predict whether a certain word will or will not be skipped; then, for
8It is also the case that not all missing values result from people skipping a region. E.g.
sometimes they may result from a failure of the equipment to record a fixation. So one could
also assume distributions for the probability of such events, e.g., specifying the probability of
eye-tracker losing track for a particular fixation
9Assuming 0 corresponds to “no re-read”.
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the words which were not skipped, use linear regression or any other appropriate
model to predict reading times for these words ((see e.g. Gelman and Hill, 2007,
p.126) for a similar approach).
It may be argued in response to the above that the goal of statistical analyses
(in these particular experiments) was not to come up with a good model of the
process that generated the data, but rather to capture some generalization about
them, regardless of whether it’s ecologically valid. E.g. by collapsing missing and
non-missing values in the same analysis, one might be asking the question: on aver-
age, how much time do people spend re-reading a given region? Which is different
from the question: given that people re-read the word, how much time on average
did they spent doing so? However, replacing missing values with zeros may have
consequences to the inferences as well.
Replacing missing observations with zeros will likely drag the estimates down
and increase their uncertainty. Now, we do not know whether the values are missing
at random. It may be, for example, that people are less likely to re-read the reflexive
region in grammatical conditions. If this is the case, fewer zeros will be introduced
to the RTs coming from grammatical conditions; and similarly for other possible dif-
ferences in re-read rates between conditions. Ultimately, the value and the certainty
of the model estimates may be differentially affected in different conditions, and it
is not immediately clear whether and in what way this may influence the inferences.
(To be fair, the same logic applies to rejecting the missing values: since we do not
know whether they are missing at random, rejecting them can bias the conclusions
we have. But since replacing missing values with zeros introduce other potentially
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undesirable effects, I advocate this method of dealing with them. Of course, this is
not the only method: e.g. one could try to use imputation procedures of various
degrees of sophistication. I do not know whether and in what way that would affect
the conclusions I would make.)
An additional complication with 0 values is due to the fact that PP2017 con-
duct their analysis on log-transformed RTs. Due to non-linearity of log function,
small changes on log scale can translate to quite big changes on linear scale. Fig.4.4
demonstrates this: it shows the difference between the observed RTs (red markers)
and the RTs predicted by the model fir to the data with missing values replaced with
zeros (blue markers)10. The figure layout is mostly analogously to Fig.4.1: experi-
10In order to generate model predictions, I do the following. First, for each fixed effect defined in
the model I obtain a sample from Normal(µ̂, σ̂), where µ̂ and σ̂ are the estimate and standard error
of the estimate, provided by the model. In this case, this will give us 7 samples: intercept and six
other effects. I combine these values according to the contrast coding schema, to get the predicted
reading time (on log-scale) for each condition. I.e. the estimate for the intercept would correspond
to the reading time in the baseline, target: full match, lure: mismatch condition. If we
want to get an estimate for target: two-mismatch, lure: match, we have to sum the four
corresponding effects (intercept, two main effects and an interaction), etc. In the end, we obtain
six predicted reading times on log-scale, one for each condition, which we exponentiate to convert
them back to the linear scale. I repeat the above procedure 3000 times, obtaining 3000 predicted
RTs for each condition. I average these predictions and compute their standard deviation. These
averages are my estimates of the mean reaction times on the linear scale as predicted by the
model. Notice that I do not incorporate uncertainty associated with participant and items into
these predictions; essentially, I am predicting reading times for an average participant reading an
average item. I am also ignoring variability in individual RTs: I am not trying to see what range
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mental conditions are plotted along the X axis (see figure description for details),
RT estimates are plotted along the Y axis. Columns correspond to eye-tracking
measures. The only major difference from Fig.4.1 is in the rows: all the data are
coming from the critical region, so now the rows represent datasets (the upper row
corresponds to the data from the current replication; the lower one - to PP2017
data.). The main observation I make about this figure is that the RTs predicted by
the model are clearly much smaller than the observed RTs. In some cases they are
nonsensically small. E.g if we look at the the original study, Target Match, Lure
Mismatch condition in the re-read times (“tm-lmm” condition in the figure), we will
see that the model predicts average reading times of 20 ms.
4.1.6 Sensitivity analysis
In order to assess the influence of analysis decisions on the inferences I can
derive from PP2017 data, I conduct a small scale sensitivity analysis. In addition to
the two factors discussed above - corrections for multiple comparisons and treatment
of missing observations - I consider two more: treatment of extreme values and the
definition of the critical region (PP2017 and S2017 differ in these last two things).
Here is the summary of the analysis decisions I manipulate:
1. Definition of critical region. I contrast two possible definitions: critical re-
gion includes only the pronoun or the pronoun plus three additional characters
to the left11. PP2017 uses the first variant, S2017 - the second.
of RTs my model predicts, rather what range of mean RTs it predicts.
11Since reflexive pronouns are close-class words, they may be skipped relatively frequently during
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2. Dealing with missing values. I contrast replacing missing values with zeros
and rejecting them. PP2017 adopted the first approach; S2017do not report
how they treated the missing values.
3. Dealing with extreme values. I contrast no trimming with fixed threshold
trimming, following PP2017 and S2017 correspondingly. For fixed threshold,
any values above 2000ms for first-pass and above 4000ms for total times are
rejected.
4. Multiple comparisons corrections. I contrast analyses with no correction
at all and analyses with correction for 60 comparisons, as discussed earlier.
4.1.6.1 Qualitative analysis
I start with discussing numerical patterns in the data. For the purposes of
the discussion I focus on the change in the size of interference effects in target:
two mismatch conditions, shown in Fig. 4.5. To remind, interference effects is
calculated as the RT in the target mismatch lure match condition minus the RT in
the target mismatch lure mismatch conditions. Thus, negative values are indicative
of the facilitatory interference. The columns correspond to variation in extreme data
trimming decisions12; the rows - to missing data removal decisions, the colors - to the
combination of studies and critical region mark-up decisions (see figure description
the reading. Extending the critical region to the left may reduce the amount of missing data
resulting from skips.
12Notice that cut-offs for extreme data points were only established for first-pass and total times
data, thus for other eye-tracking measures there is no change across the columns.
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for details). Different eye-tracking measures are represented along the x axis.
When looking at this figure, we are mostly interested in whether the pre-
processing decisions affect the size of the interference effects. The answer is: pre-
processing choices naturally do have influence on the estimates, but it is not huge,
and the patterns of the results remain relatively stable across different pre-processing
variants. Choosing a shorter region naturally leads to shorter reaction times, but the
intrusion effect remains almost unaffected. Choosing to reject missing values leads
to the reduction of the effect size in some cases, not exceeding roughly 30ms. Finally,
the trimming of extreme values does not affect first pass, and leads to a reduction in
total times (roughly 40 ms for PP2017data and roughly 20ms for the replication).
As we will see later, we have reasons to believe that the size of lure-match effect
in reflexives lies in the range of roughly 50-100ms, so a reduction of 30 or 40 ms is
quite sizeable. Finally, I would like to point out that for all preprocessing variants I
observe numerically big intrusion effects in PP2017 and much smaller effects in my
replication. This suggests that the discrepancies we observe cannot be explained by
di
4.1.6.2 Quantitative analysis
Now I turn to the discussion of statistical estimates obtained in different anal-
ysis procedures. The primary question I am interested in this section is: do analysis
choices influence the inferences we make from the models? I use the same analysis
procedure as described earlier, although I automate the simplification of the random
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effects structure for the non-converging models (it was done manually in the main
analysis).
Fig. 4.6 displays the estimated coefficients for the models. Each dot in the plot
corresponds to a β̂ value from some model, in a way similar to Fig.4.3. We consider
models fit to 12 different datasets, resulting from the variation of pre-processing
choices and the study the data was coming from. These 12 datasets are plotted
along the Y axis of each plot. The names of analyses variants are compositional:
each sub-component corresponds to one dimension we manipulated. The first com-
ponent corresponds to the study (“repl” - current replication, “pporig” - original
study by PP2017); the second component corresponds to the critical region markup
(“nonext” - critical region includes only the reflexive itself; “ext” - critical region
includes the reflexive and three characters to the left. Notice that only “nonext”
variant is available for PP2017); the third component corresponds to the treatment
of extreme values (“notrim” - include all values in the analysis, “trim” - trim values
exceeding 2000ms in first-pass and 4000 in total times); the last component cor-
responds to missing values treatment (“narm” - remove, “nazero” - replace with
zero). Sub-panels of the plot display estimates from models fit to different eye-
tracking measures. Each column displays model estimates for a given fixed effect:
TM1/2 - target match , one/two feature mismatch; LM - lure match; ung int -
interaction term from ungrammatical only model; prws1/2 - pairwise comparisons,
corresponding to simple main effects of lure match within the corresponding target
match conditions.
Notice that the coefficients are not easily interpretable on their own, since they
169
are on log scale. Thus, I will only discuss what inferences one would make, if one
was simply looking at the coefficients and checking whether they are significantly
different from zero. I take coefficients with |t| > 2 to be significantly different
from zero, and mark them in red on Fig. 4.6. In addition, I consider how the use
of a Bonferroni correction affects the conclusions. Following the logic I described
earlier for the main analysis, I correct for 60 comparisons, resulting in a Bonferroni
corrected α = 0.05/60 = 0.00083. The estimates which stop being significant are
highlighted in yellow in Fig. 4.6.
Let me specify a decision algorithm I will use to make conclusions from the
models. As far as I can say, this algorithm does not correspond exactly to how
decisions were made in PP2017, and may lead to somewhat more conservative con-
clusions then reached in the original paper. I will discuss more liberal variants of
it as well. I will keep using the model specification from PP2017, although some of
the questions we are going to ask might be better addressed with slightly different
models. I will use the following decision procedure:
1. First, I will look at three effects in the full models, to answer the question: Do
lures affect the processing of reflexive pronouns? Main effect of lure
match would suggest that lure match and lure mismatch conditions
differ within target match sentences. Two target match x lure match
interactions, one for each non-baseline level of target match would indicate
that the effect of lure match differs between grammatical sentences and -
depending on the interaction - one-mismatch or two-mismatch ungrammatical
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sentences. If I do find at least one significant interaction, I will declare that I
have evidence that interference effects exist, and that they behave differently
in grammatical and ungrammatical sentences13; in this case, I will proceed to
the following step of the algorithm. If I do not find any interactions, I will
only conclude that lure-match effects exist and stop.
2. If I find at least one interaction in the previous step, I will ask the next ques-
tion: Does interference behave differently depending on the degree of
ungrammaticality? To answer this, I will look at the interaction coefficient
from ungrammatical-only model. If it is significant, I will claim that not only
interference differs between grammatical and ungrammatical sentences, it also
behaves differently in different types of ungrammatical sentences. If the in-
teraction term is not significant, I will stop and declare that I don’t have any
evidence to believe that the degree of ungrammaticality affects interference
effects.
3. If I do find the interaction in the previous step, I will want to resolve it. To
do this, I will look at the simple main effect of lure match within target:
one mismatch and target: two mismatch sentences.
13Notice that in this model specification, we reach this conclusion somewhat indirectly. We
look at differences between grammatical sentences and one-mismatch ungrammatical sentences;
similarly for two-mismatch ungrammatical sentences; then, we conclude that grammatical and
both types of ungrammatical sentences do or do not differ. A better way to address this question
might be to use Helmert contrasts to first compare grammatical conditions to the average or the two
ungrammatical conditions, and then compare the ungrammatical conditions between themselves.
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A more liberal version of the algorithm would allow to proceed to consider the
ungrammatical only model even if no interactions in the full model are significant.
This would roughly correspond to assuming that we are not interested in whether
lure match differentially affects grammatical and ungrammatical sentences, only
in whether lure match behaves differentially in ungrammatical sentences depend-
ing on the degree of ungrammaticality. Another way to make more liberal decision is
not to take Bonferroni correction into account. I will apply the decision algorithm to
all eye-tracking measures, and make the corresponding conclusions if for any single
measure my algorithm allows us to do so14. I start with analyzing PP2017 data.
Main effect of lure match never reaches significance regardless of pre-processing
procedure. target match x lure match interactions do reach significance for
target: two mismatch conditions in all regions and measures, only if we choose
to remove missing values from the data15. These effects survive Bonferroni correc-
14This is yet another degree of freedom in the analysis. As von der Malsburg and Angele (2017)
notice, it is somewhat common to make claims about some effect if it is present at any given
measure and/or region. In principle, it would be better if we could make predictions about in
which exact measure the effect of interest will appear.
15Notice that in the analyses reported in PP2017, this interaction reached significance in re-
gression path and re-read times, even though PP2017 chose to replace missing values with zeros.
This discrepancy potentially results from the differences in random effect structures. I discuss
it on the example of regression path model. As far as I could tell, PP2017 only specified ran-
dom intercepts for both subjects and items, while in my case, I additionally had random slopes,
1 + target.match + lure.match | subject. This was the most complex model that converged dur-
ing the simplification process described earlier. This difference in random effects specification
was apparently enough to push the t-value for the interaction estimate from -2.04 (which would
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tion in right-bound and re-read times, but not in first-pass and regression path. For
the models based on data with rejected missing values (and, if I am being liberal, for
the models with missing values replaces with zeros), I can continue to the next step
of the decision algorithm and look at the interaction term for the ungrammatical
only model. It turns out to be significant in almost all measures, except for re-read
time. However, in neither of the reading measures does it survive Bonferroni correc-
tion. Thus, if I am being conservative, I would stop here and only be able to claim
that intrusion effects do differ between grammatical and ungrammatical sentences,
but that I do not have enough evidence for differential effects of lure match de-
pending on the degree of ungrammaticality. If I am being more liberal and ignore
Bonferroni correction, I can look at the simple main effects of lure match within
ungrammatical conditions, which always turn out to be significant. Thus, in a liberal
version of the decision algorithm, I would be able to claim that interference effects
are only observed in two-mismatch conditions. Summing up, if I ignore multiple
comparisons correction, I would be able to reach the same conclusions as PP2017
do; if I am being conservative, I only have strong enough evidence for the difference
in the effect of lure match between 2-feature target mismatch and target match
conditions, but not the difference between the two ungrammatical conditions. A
possible interpretation for this weaker result would be: the experiment provides
evidence for interference in reflexive resolution contra previous findings (while the
original PP2017 conclusions are able to accommodate previous findings due to the
correspond to a significant effect) to -1.58 (non-significant). This suggests that random effects
specification has to be carefully considered and preferably reported for all models in a paper.
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claim of differential interference effect). Overall, it looks like I can reach the origi-
nal conclusions of PP2017 regardless of the pre-processing, although one needs to be
more liberal in the decision-making when using the models with missing observations
replaced with zeros.
Let us now turn to the replication data. Similarly to PP2017, the main effect of
lure match in the full model never reaches significance. target match x lure
match interactions do not reach significance in any analysis variant and eye-tracking
measure. Thus, if I am being conservative, I would have to stop here and claim that
I do not have strong enough evidence for interference in reflexive resolution. Being
somewhat more liberal does not help: even if I look directly at ungrammatical only
model, I would not be able to claim that I have found evidence for interference effect,
since under no pre-processing scenario does the interaction from the reduced model
reach significance. Only if I relax the standards even further and decide the simple
main effect of lure match are good enough evidence for interference, I would be
able to claim the I found the effect - but only without the correction for multiple
comparison. Summing up, for my data I would have to be very liberal to claim that
I have enough evidence for interference.
Overall, while the sensitivity analysis suggests that the evidence presented
by PP2017 may be somewhat weaker than claimed in the paper, the replication
study provides even weaker evidence for interference effect (in the conservative case
- provides no reliable evidence at all).
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4.1.7 Discussion
The main goal of this experiment was to check whether it was a mere presence
of QPs in the set of experimental materials which prevented us from observing reli-
able interference effects in the previous chapter. The answer is negative. While the
overall patterns of (average) reading times appeared to be similar, the magnitudes
of the reading times were less extreme in the replication. The magnitude of the
interference effect was at least twice as small as compared to the original study,
and was comparable to that observed in my Exp.3-4. The statistical analyses also
did not provide a strong support for the existence of interference effects. While
the choice of analysis procedure did have some influence on the conclusions (e.g.
only allowing for weaker claims in case with missing values replaced with zeros), the
overall impression still held: the data from the replication provides less statistical
support for the existence of the interference effect than the data from the original
study.
I also intended to use this experiment to tease apart PP2017 and S2017 ac-
counts. If I did observe reliable interference effects here, it could be taken to support
PP2017: their account can accommodate the influence of context on the resolution
process much more readily than S2017. However, since it does not appear that the
presence of QP affected the size of the lure-match effects, I cannot use these data
to help distinguish between the two accounts. In the next experiment I address a
different possible context effect: the influence of the experimenter language charac-
teristics. I will use the same exact materials as in the current experiment, only this
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time all the data will be collected by a native experimenter.
4.2 Experiment 6
In the previous experiment I failed to find strong support for interference ef-
fects from NP lures, despite using the same exact materials as Parker et al. (2017).
I did find numerical trends in the predicted direction, but they were not supported
by statistics. The only systematic explanation for the lack of replication I can think
of is the influence of the experimenter: perhaps, instructions in non-native English
affected participants’ processing of ungrammatical sentences. The current experi-
ment aims at testing this possibility. It exactly replicates my previous experiment,
with a single difference: all the data were collected by native English speakers16.
4.2.1 Participants
35 members of University of Maryland community (23F, 12M; age range: 18-
34, average age: 21.4) participated in the experiment for a class credit or a payment
of $12. The experimental session took about one hour, including setup and cal-
ibration. Data from two participants were removed: one participant did not pay
attention during calibration and was distracted during the experiment; for the other,
experimental software could not adequately process the data. Thus the analysis was
16I would like to thank Lalitha Balachandran and Cassidy Wyatt for their help with data col-
lection.
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based on the data from 33 participants17.
4.2.2 Materials
The materials were identical to Experiment 5.
4.2.3 Procedure
The procedure was identical to Experiment 5.
4.2.4 Analysis
The analysis procedure was identical to Experiment 5. Again, I first follow
the analysis procedure as outlined in Parker and Phillips (2017), to be as close as
possible to the original study. Then I perform an additional set of analyses with
a different pre-processing procedure, which I think to be better for the reasons
discussed earlier in this chapter (its two main differences are a wider critical region
and removing missing values instead of replacing them with zeros).
4.2.5 Results
I start with observed patterns of mean reaction times, which are shown in
Fig. 4.7. Numerical values for the mean are given in Appendix A. I compare the
results from the current experiment (green dots), my previous replication in Exp.5
(blue dots) and the means from the original study by PP2017 (red dots).The layout
17I aimed at 48 in order to have the same power as in the previous replication, but could not
reach the goal due to time limitations
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of the figures is identical to Figs.4.1 and 4.2 from the previous chapter and was
described in detail there. Here, I will focus the discussion on the critical region,
since this is where PP2017 observed the interference effect most consistently. The
overall patterns of means seem to be roughly similar in all three studies.
The first thing I note about the numerical values is that for some reason
the average reading times are smaller than in both PP2017 and Exp.5. All three
experiments look most similar within 2-feature target mismatch conditions in terms
of the pattern of the RTs: lure match conditions are read faster than lure mismatch
conditions. However, in terms of the magnitude of the interference effect18 in 2-
feature target mismatch conditions, the current experiment is closer to my first
replication than to the original study (Fig.4.819), and again it is smaller in magnitude
than the interference effects from Parker and Phillips (2017).
Let us now turn to the statistical analyses. As in Exp.5, I present model
estimates from the current experiment and from the original PP2017 experiment
side-by-side on the upper panel of Fig.4.9. The layout is essentially the same as
in 4.3 from the previous experiment, except that we are presenting two sets of of
comparisons in the upper and the lower panels, and the estimates are only coming
from the models fit to the data from the critical region. Coefficients for which
|t| ≥ 2 are represented with square markers; triangles indicate coefficients which
18As a reminder, calculated as the difference between lure: match and lure: mismatch
conditions. Negative values indicate that lure: match conditions are read faster.
19Notice the change in the plot layout: eye-tracking measures are plotted along the x-axis, and
columns correspond to ROIs.
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stop being significant after a multiple comparisons correction. Intercept estimates
are not included in the plot.
I will focus my discussion on the critical region. To remind, for the full models,
I can expect three estimates to reflect interference effect:
• Main effect of lure match, which would indicate that reading times on the
reflexive differ for matching and mismatching lures, if we compare target:
match and target: two mismatch conditions;
• target match x lure match interaction for target: one mismatch con-
ditions. It would indicate that reading times are differentially affected by lure
mis(match) in target: match and target: one mismatch conditions.
• Similarly for target match x lure match interaction for target: two
mismatch conditions.
In the current experiment, no effects of interest reach significance. Two other
effects, unrelated to lure match were significant: the two main effects of target
match, indicating that ungrammatical sentences with mismatching lures are being
read slower than grammatical sentences with mismatching lures. Both these effects
survive Bonferroni correction based on the same calculations as in the previous
experiment20
Compare these results to the original study and Exp.5. The pattern of results
in re-read times is perhaps the most similar between the three. Two main effects
20To remind, I am correcting for 3 ROIs x 4 MOIs x 5 comparisons in each = 60 comparisons,
which results in critical α of 0.00083 and the corresponding t-value of ±3.34
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of target match are most consistent. For one-mismatch conditions, they reach
significance in two studies, and remain significant after Bonferronni correction in one
of them; for two-mismatch conditions, they reach significance in all three studies
and remain significant in two of them after the multiple comparisons correction.
The magnitude of the estimates is also very similar. These results suggest that
the ungrammaticality of the sentences strongly affects participants. In other eye-
tracking measures, it appears that the two replications are closer to each other
than to the original study: the magnitude of the estimates in the replications is
smaller; very few effects reach significance and none survive the multiple comparisons
correction.
Exploratory analysis The sensitivity analysis I performed for the previous ex-
periment suggested that out of three preprocessing parameters I have manipulated
- definition of the critical region, trimming of the extreme values and treatment of
missing values - the last one had the biggest impact on statistical estimates. Thus, I
briefly discuss what would happen had I chosen to remove the missing values instead
of replacing them with zeroes in the main analysis. Fig. 4.10 shows the mean RTs,
Fig. 4.11 shows the size of the interference effect and Fig.4.12 shows the coefficients
from statistical models.
As we can see, the pattern of the RTs and interference effects are not con-
siderably affected by the preprocessing routine, except that the average RTs get
somewhat more similar between the three studies in regression path and re-read.
Statistical patterns also remain roughly the same: the only effects that reach signif-
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icance are the main effects of target match (i.e. grammaticality effects). They
are now significant in all eye-tracking measures, but most of them do not survive the
Bonferroni correction. Still, it indicates that there is evidence for grammaticality
effects in the data.
It is interesting to note that the estimates for the effects which did not reach
significant are rather similar across all three studies, even more so than in the main
analysis. On the other hand, the estimates for the effects indicative of interference
are bigger in the original study as compared to the two replications. This again
makes us think that the effects reported by PP2017 may be overestimated.
4.2.6 Discussion
The results of my second replication appear to pattern with my first replication
and not with the original study. The lure-match effect in 2-feature target mismatch
conditions was numerically going in the same direction as in the original PP2017
study, but the magnitude of the effect was at least two times smaller. Statistical
analyses do not provide support for lure-match effects. This is like my first replica-
tion, and unlike the original, where statistics supported the presence of the effects
in all analyzed eye-tracking measures. Overall, the study does not indicate that the
language of the experimenter was what caused the absence of lure-match effects in
my Exp.2-4. These conclusions are supported by the results of the exploratory data
analysis: regardless of the pre-processing procedure I choose, my conclusions hold.
This experiment, as the previous one, fails to provide evidence for the influence
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of experimental context on the processing strategies. Thus, these results do not
provide support for the PP2017 account, as I hypothesized they might. However,
they provide valuable evidence on the size of lure-match effects we may be expecting
in reflexives resolution, and this information may be used to guide power analyses
for the future studies. Next section discusses these issues in more detail.
4.3 Interference magnitude across studies
In this section I compare the magnitude of the intrusion effect in the few
studies which have looked at reflexive resolution in 2-feature target mismatch con-
figuration, to see whether the results I have obtained in the studies I have run are
unexpectedly small. I start by looking at five experiments, which were maximally
close to each other in terms of materials and manipulation: PP2017 Exp.3, its two
replications (my Exp. 5 and 6), S2017 Exp.1c (speech verbs), Exp.4 from this thesis.
PP2017 Exp.3 and the current experiment used the same materials (experimental
sentences and fillers). My Exp.4 overlapped with S2017 Exp.1c in a subset of exper-
imental sentences (both experiments included additional conditions which were not
similar; the fillers were also different). In all studies, the stimuli shared the following
characteristics:
• Two clause sentences with the reflexive inside a complement clause;
• The matrix predicate is a predicate of report (e.g. “say”, “mention”; etc.)21;
21This parameter was controlled in S2017; it was not in PP2017, but in their materials about
70% percent of the verbs were report verbs, so I consider the materials to be comparable along
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• The reflexive and lure are always singular;
• The lure is the subject of the matrix clause;
• The target is the subject of the embedded clause;
• The lure can match or mismatch the reflexive in gender;
• The target mismatches the reflexive in gender and number 22;
• The target and the lure are referential NPs.
Fig.4.13 shows the interference effect in 2-feature target mismatch conditions,
calculated as the difference between lure match and lure mismatch conditions.
Different studies report different reading time measures, that is why there are gaps
in the plots. Two observations are of interest. First, intrusion effect is generally
much bigger in PP2017 than in the other studies (except in regression path, where
the magnitude of the intrusion is similar in PP2017 and S2017). Second, the mag-
nitude of the intrusion appears to be reduced in my studies as compared to the
corresponding original studies. Importantly, the magnitudes of facilitation from the
two replications are very close to each other. This suggests that PP2017 estimates
might be inflated, and that my estimates might be closer to the underlying effect.
this dimension.
22PP2017 and its replication had an additional condition with the target mismatching the target
only in number, but S2017 and Exp.4 from this thesis didn’t have it. Since intrusion effect appears
only in the two-mismatch condition, I will not focus on the additional one-mismatch condition in
PP2017 and its replication
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Let us now consider interference effects in all studies investigating reflexive
resolution in 2-feature target mismatch conditions with c-commanding lures. In
addition to the experiments above, this list includes Exp.3 from this thesis, two
more experiments by PP2017 and four more experiments by S2017. The magnitude
of interference effect in these studies is displayed in Fig.4.14. The picture is perhaps
most consistent in total times: the effect reported by PP2017 completely overshad-
ows the other effects, but otherwise the size of the effect is surprisingly similar in
experiments by S2017, and the magnitude of the effect from two replications I report
is in line with them as well. The effects from Exp.3 and 4 are somewhat smaller,
especially the first one. Finally, lure-match effect in S2017 Exp.1 for sentences with
perception embedding verbs is almost non-existent, but this difference is accounted
by S2017 account (and, as I have argued in Chapter 1, by PP2017 as well). Turning
to other reading times measures, the picture is very similar in first-pass time, right-
bound and re-read times: the magnitude of the interference effect in PP2017 Exp.3
is bigger than in all other studies, which are relatively similar (with the exception
of Exp.3 from this thesis). Regression path shows the most heterogeneous picture,
although even here PP2017 effect in Exp.3 is numerically the biggest, contested only
by the effect from S2017 Exp.1 for sentences with speech verbs.
The comparisons discussed above do suggest that the intrusion effect in PP2017
Exp.3 is inordinately big. I do not think it is due to the particular manipulation
used: S2017 Exp.1b and 2b rely on the same manipulation, and yet generally yield
numerically smaller effects. The native language of the experimenter, at least in
this set of studies, does not uniquely determine the size of the effect either: in both
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my Exp.6 and S2017 the data were collected by native English speakers, and the
intrusion effects are smaller than in PP2017, It thus seems more likely that the dif-
ference in the effect size is due to some unmeasured factors; the fact that PP2017
only collected data from 24 participants might have contributed to the surprising
size of the effect. As Gelman and Carlin (2014, (a.o.)) discuss, when the power is
low, significant effects tend to be overestimates; the magnitude of the overestimation
tends to infinity as power tends to zero. While we would need to conduct a formal
power analysis to make specific claims, it is true that PP2017 Exp.3 relies on the
smallest sample size among all the studies discussed in this section, so presumably
has the lowest power and would have the biggest overestimation ratio among them
all.
Another suggestive piece of information comes from a simulation study by
Engelmann et al. (draft4). They investigate the influence of the LV05 model pa-
rameters on the size of the lure-match effect predicted in the model (p.13). The
magnitude for the majority of the predicted facilitation effects (i.e. the type of ef-
fect I am interested in here) lies below 100ms, and the effects of the size reported
by PP2017 are rather rare.
4.4 Pooled data analysis
The previous exploratory analyses indicated that the numerical lure-match
effects I observed might be real but fail to receive statistical support due to the lack
of power. In this section I report an exploratory analysis on the pooled data from
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both replications - this will more than triple the original sample size used by Parker
and Phillips (2017).
First, I wanted to make sure that the data from the two replications is homoge-
neous enough to be pooled. To this end, I run a bootstrapping simulation, sampling
48 subjects with replacement from each of the three experiments - the original one
by Parker and Phillips (2017) and the two replications I report here. I draw a
thousand samples from each dataset, and calculate the magnitude of the lure-match
effect in 2-feature target mismatch conditions for different eye-tracking measures in
the critical region. Fig. 4.15 represents the distributions of bootstrapped lure-match
effects magnitudes. As in most plots in this chapter, columns correspond to different
eye-tracking measures. The magnitudes of the interference effects observed in the
simulation are plotted along the Y axis; the height of the distribution at any given
point roughly23 corresponds to the number of observed effects of a given magnitude.
Colors of the distributions correspond to the dataset which the simulations were
based on (see the figure’s legend).
We can see that the distributions of possible effect sizes are very similar be-
tween the two replications. They look almost identical in regression path and total
times; they are not as similar in other eye-tracking measures but are still located
and shaped quite similarly to each other. On the other hand, possible effect sizes
one can obtain from PP2017 data are bigger and practically do not overlap with
the replications distributions. I conclude that the data from the two replications is
homogeneous enough to be pooled for an exploratory statistical analysis.
23Although not precisely, since it’s not a histogram, but rather a smoothed version of it.
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Fig.4.16 shows the results of statistical modeling with the pooled dataset. The
layout is similar to Fig.4.3. The data only come from the critical region. As in Exp.6
for the sake of exploration I compare whether the treatment of the missing values
would affect my conclusions. We can see that grammaticality effects (main effects
of target match) reach significance in all measures at the critical region; this
is not surprising given that even in the individual experiment the evidence for the
grammaticality effects was quite robust. On the other hand, evidence for lure-match
effects still remains rather elusive.
In the analysis with missing values removed, the target match x lure
match interaction for target: 2-mismatch conditions reaches significance in re-
read and total times. Neither of these is significant if I choose to replace missing
values with zeros. This is probably due to a larger standard error of the estimate
in this case, since the magnitude of the estimates is rather similar between the
two analysis procedures. Overall, the analysis of the pooled data suggests that a
moderate increase in sample size may boost the statistical power enough to make
the lure-match effect more readily detectable.
4.5 General discussion
The goal of the two experiments reported in this chapter was two-fold. First,
I wanted to determine how reliable my results from Exp.2-4 were. To remind, my
question there was whether QP lures elicit lure-match effects in the same way as NP
lures do. I failed to find statistical support for interference from either NP or QP
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lures. Numerically the RTs did go in the right direction (lure match sentences were
read faster within target-mismatch conditions only) when the QP lure c-commanded
the pronoun, but the magnitude of the effect was reduced as compared to PP2017.
This made me worry that the experimental manipulation did not work in some
subtle way, and the results were completely uninterpretable. The experiments and
analyses reported in the current chapter allowed to partially assuage this worry.
In both replication experiments I found a lure-match effect which is numer-
ically smaller than that reported in PP2017. As in Exp.2-4, this effect does not
reach significance in the statistical analyses. However, the comparison of the effect
sizes across multiple related studies suggests that it is PP2017 and not my results
which are outliers: effects of about 70-100ms (as in my studies) are more common
than those of 200-250ms (as reported by PP2017).
Importantly, the magnitude of the lure-match effects in Exp.4 lies in the same
range. It suggests that the experiment did, indeed, work as intended. Thus, I
conclude that the interpretation of the data I tentatively suggested in the end of the
previous chapter holds: c-commanding QP and NP lures elicit similar lure-match
effects, suggesting that both types of lures influence the reflexive resolution process.
This supports the conclusion that the differential patterns of RTs between NP and
QP lures I observed in Experiment 2 are not due to QP being inefficient lures, and
may truly indicate the inaccessibility of non-c-commanding QP to the parser.
Influence of the context A second question I addressed in this chapter was
whether experimental context (in terms of the stimuli set or experimental environ-
188
ment) has an effect on the magnitude of the lure-match effect. I argued that if
contextual factors did indeed affect the magnitude of the interference, it would pro-
vide support for PP2017 account, which could explain such influence much more
easily than S2017. However, the results suggest that the context (at least the two
factors I explored) does not influence the size of the lure-match effect. The size of
the lure-match effect I observed was consistent regardless of whether the experiment
was run with a stimuli set containing QPs, with a set without them, by a native
or non-native experimenter. Therefore, there is no direct evidence for preferring
PP2017 over S2017 coming from this set of experiments.
Lack of statistical significance While the comparison of effect sizes is informa-
tive, the six experiments I conducted so far provided extremely limited statistical
evidence for the existence of lure-match effects. Given that lure-match effects do
appear to be relatively consistent in direction and magnitude across my and some
of the previous studies, I think that the lack of statistical support is in big degree
due to statistical reasons. As I have already mentioned, under-powered studies tend
to produce over-estimates of significant effects (Gelman and Carlin, 2014). A recent
report of a large reproducibility project by Collaboration (2015) provides empirical
evidence for this claim: out of 100 replication attempts, 97 original effects were sig-
nificant at 0.05 level, while only around 35% replication effects were so. Similarly,
in 82 out of 99 original studies for which effect size could be calculated showed a
bigger effect size than the replication.
While this explanation is tempting, and, I think, has substance to it, it can-
189
not be exactly right: S2017 used very similar sample sizes, but consistently found
statistically robust effects. I return to this issue in the closing chapter of the thesis.
190
Figure 4.4: Predicted and observed RT values for PP2017 and my replication.
Columns correspond to eye-tracking measures: fp - first-pass, rb - right-bound times, rp -
regression path, rr - re-read times (all RTs come from the critical region). Rows correspond
to datasets (the upper one - current experiment; the lower one - original PP2017 data).
Error bars for the observed data represent standard error of the estimate, adjusted for
participant variability (Cousineau, 2005; Morey, 2008). Error bars for the predicted data
represent standard deviation for the simulated means. Conditions: tm/tomm/ttmm -
target match/one-mismatch/two-mismatch; lm/lmm - lure match/mismatch.
191
Figure 4.5: Sensitivity analysis: Intrusion effect (lure mismatch minus lure match )
in 2-feature target mismatch conditions.
Columns correspond to variation in extreme values treatment (“notrim” - include all
values in the analysis, “trim” - trim values exceeding 2000ms in first-pass and 4000 in
total times); rows correspond to missing values treatment (remove or replace with zero);
colors correspond to the combination of study and crtical region markup (“nonext” -
critical region includes only the reflexive itself; “ext” - critical region includes the reflexive
and three characters to the left. Only “nonext” variant is available for PP2017). Error
bars represent standard error of the difference of the means.
192
Figure 4.6: Sensitivity analysis: Model coefficients in PP2017 Exp.3 and replication.
Errors bars represent standard deviation of the estimates. See text for further description
of columns and row labels. Coefficients for which |t| ≥ 2 are represented with red markers
if they remain significant after a Bonferroni correction (with the corrected |t| = 3.34), and
with yellow markers, if they don’t.
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Figure 4.7: Mean RTs in PP2017 (red), my previous replication (blue) and my
current replication (green).
Error bars represent standard error of the mean. Conditions: tm/tomm/ttmm - target
match/one-mismatch/two-mismatch; lm/lmm - lure match/mismatch.
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Figure 4.8: Interference effect in target: two mismatch conditions (lure match
- lure mismatch) in PP2017 (red), my previous replication (blue) and my current
replication (green).
Error bars represent standard error of the difference of the means.
195
Figure 4.9: Model estimates in PP2017 (red) and my replication (blue).
First five effects come from the full model; next three represent the simple main effects
of lure match and the interaction from ungrammatical-only model. The order of the
coefficients is the same as in PP2017, to make comparisons across papers easier. Error
bars represent standard error of the estimate. Coefficients for which |t| ≥ 2 are represented
with squares if they remain significant after a Bonferroni correction (with the corrected
|t| = 3.34), and with triangles, if they don’t.
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Figure 4.10: Mean RTs in PP2017(red), my previous replication (blue) and my
current replication (green).
Exploratory analysis: removing missing values instead of replacing them with zeros. Er-
ror bars represent standard error of the mean. Conditions: tm/tomm/ttmm - target
match/one-mismatch/two-mismatch; lm/lmm - lure match/mismatch.
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Figure 4.11: Interference effect in target: two mismatch conditions (lure match
- lure mismatch) in PP2017 (red), my previous replication (blue) and my current
replication (green).
Exploratory analysis: removing missing values instead of replacing them with zeros. Error
bars represent standard error of the difference of the means.
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Figure 4.12: Model estimates in PP2017 (red) and my replication (blue). Ex-
ploratory analysis: removing missing values instead of replacing them with zeros.
First five effects come from the full model; next three represent the simple main effects
of lure match and the interaction from ungrammatical-only model. The order of the
coefficients is the same as in PP2017, to make comparisons across papers easier. Error
bars represent standard error of the estimate. Coefficients for which |t| ≥ 2 are represented
with squares if they remain significant after a Bonferroni correction (with the corrected
|t| = 3.34), and with triangles, if they don’t.
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Figure 4.13: Intrusion effect in five studies with most similar design (PP2017 Exp.3,
its two replications (this thesis Exp. 5 and 6), S2017 Exp.1c, this thesis Exp.4).
Errors bars represent standard error of the difference of the means. Reaction times are
shown for the reflexive region. Columns correspond to reading times measures: fp - first-
pass, rb - right bound time, rp - regression path, rr - re-read time, tt - total time.
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Figure 4.14: Intrusion effect in all studies investigating 2-feature target mismatch
configurations (PP2017, S2017, the current study).
Errors bars represent standard error of the difference of the means. Reaction times are
shown for the reflexive region. Columns correspond to reading times measures: fp - first-
pass, rb - right bound time, rp - regression path, rr - re-read time, tt - total time.
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Figure 4.15: Distribution of lure-match effect sizes in 2-feature target mismatch
conditions obtained in a bootstrapping simulation.
Sampling 48 participants with replacement. Columns correspond to reading times mea-
sures: fp - first-pass, rb - right bound time, rp - regression path, rr - re-read time, tt -
total time.
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Figure 4.16: Model estimates for the models fit to the pooled data from Exp.5 and
6.
Error bars represent standard error of the estimate. Dot size indicates whether the esti-
mate was statistically significant (|t| ≥ 2) (big dots) or not (small dots). Colors correspond
to the pre-processing variant used (“parker” - critical region comprises the reflexive alone,
missing values are replaced with zeros; “sloggett” - critical region includes the reflexives
plus three last characters of the preceding word, missing values are removed). Models are
fit to the data for the critical region only.
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Chapter 5: Conclusions
In this thesis I attempted to answer the question: does structural informa-
tion constrain real-time sentence processing in a way consistent with grammatical
generalizations? Prima facia, the question has already been answered: a wealth
of experimental evidence suggests that sometimes structural information appears
not to rule out structurally inappropriate antecedents. We know that measures of
processing difficulty, such as reading times and acceptability judgments are affected
by structurally irrelevant material. Agreement attraction is the primary example,
and similar behavior has been reported for NPI licensing and reflexive resolution.
However, as I discussed, this evidence can be explained in a multitude of ways, only
some of which - in particular, cue-based parsing - do indeed assume that structural
information fails to uniquely direct dependency resolution. I have argued that cue-
based models should be preferred both on theoretical and empirical grounds: they
provide wide empirical coverage and serve as a solid working hypothesis, allowing to
easily formulate and test new predictions. In addition, they have been argued to be
the only kind of models which explained the absence of ungrammaticality illusions
in agreement attraction. If this preference is correct, we have quite good reasons to
believe that structurally inappropriate phrases are considered by the human parser.
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However, several recent studies have raised doubts about whether cue-based
models do indeed constitute our best choice. Two papers attack what had been
the empirical cornerstone of the argument for cue-based models: their ability to
explain the evidence from grammatical agreement attraction sentences. A meta-
analysis and computational modeling by Jäger et al. (2017) suggest that cue-based
models do not in fact accommodate the reading times patterns in grammatical
sentences with agreement attraction. Hammerly et al. (draft.april.2018) go in a
similar direction: they suggest that the absence of ungrammaticality illusions in
the data is artifactual, and that the cause of agreement attraction lies in a badly
constructed sentence representation which is accessed in full agreement with the
grammar. Another paper attacks the cue-based explanation for the reflexive data
(Sloggett, 2017): instead of processing error account they suggest a model which
explains empirical evidence from reflexive resolution in terms of a fully grammatical
resolution strategy - interpreting reflexives as logophors.
In this thesis I was looking for evidence which could help to support or weaken
these recent claims. To do so, I focused on recent findings by Parker and Phillips
(2017) and Sloggett (2017). Both of them show that reflexive resolution can be
affected by structurally inappropriate antecedents. But the explanations they give
are diametrically opposite. Parker and Phillips (2017) suggest that the effects they
observed are a result of a processing error - faulty memory access which fails to
be uniquely constrained by the structural information. In contrast, Sloggett (2017)
argues that these effects constitute evidence for logophoric interpretation of the
pronoun, which he hypothesizes to be fully grammatical, although underutilized,
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strategy of anaphora resolution in English. This approach assumes that structural
information always uniquely leads the parser to only consider grammatically appro-
priate antecedents.
Neither of the accounts fully covers available evidence. Thus, the primary goal
of this thesis was to investigate the predictions of these two accounts in order to
choose between them (and as a consequence - between “structure-defeasible” and
“structure-strict” models). I have reported six experiments: four original and two
direct replications of the previous studies. One experiment investigated interference
from lures embedded inside relative clauses under animate matrix subject - con-
figuration where PP2017 and S2017 accounts make differential predictions. Three
experiments investigated the behavior of QP lures, with the aim of better under-
standing the role of c-command in on-line reflexive resolution. Two experiments
were direct replications of Parker and Phillips (2017) Experiment 3, investigating
possible roles of extra-linguistic context in lure-match effects, as well as reliability
of the previously reported findings. The experiments I report are quite intimately
intertwined: most of them both provide a piece of information which is valuable on
its own, and help to narrow down the interpretation of the previous results. In the
following section, I summarize my main findings and discuss how they could help
us choose between the two types of accounts.
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5.1 Choosing between PP2017 and S2017
5.1.1 On sub-command binding
The first question I asked in my thesis was: do we have reasons to believe that
lure-match effects from non-c-commanding lures reported by PP2017 are evidence
for the parser accessing structurally illicit antecedents? If they are, it would con-
stitute a problem for S2017 logophoric account. To capture them without resorting
to a processing problem explanation, S2017 suggested that they represent an in-
stance of sub-command binding. This phenomenon occurs in Chinese; an anaphor
can be bound by a non-c-commanding animate antecedent if it is contained within
a c-commanding inanimate NP. If S2017 explanation were true, the lure-match ef-
fects would only appear when the embedding NP was inanimate. The results of
Experiment 1 speak against this explanation. I observed lure-match effects regard-
less of the animacy of the matrix subject. The only significant effect of lure-match
was likely driven by the effect within “inanimate” conditions only. However, at the
critical region the magnitude of the effect in the “animate” conditions was mostly
as big or bigger than in the “inanimate” conditions, and approached the size of the
effect from c-commanding NP lures in my other experiments.
Therefore, I tentatively conclude that lure-match effects from non-c-commanding
lures are real and are not instances of sub-command binding. Taken in isolation,
this finding would support a processing error explanation over the grammatical one,
i.e. “structure-defeasible” models over “structure-strict” ones. Such a conclusion
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would weaken the S2017 logophoric account: if we have evidence that at least in
some cases the parser can violate structural constraints (or maybe: cannot help but
violate them), what forces it not to do so when resolving the very same dependency
in similar configurations? However, as I discuss in the next section, these conclu-
sions would be too strong. Instead, as I will argue, they rather support a model in
which the parser faithfully and accurately follows constraints that imperfectly align
with the grammar.
5.1.2 On the role of c-command
In my Experiments 2-4 I focused on QP lures, asking the question: are PP2017
correct in claiming that any kind of structural information can be outweighed by
competing factors (such as morphology), or can some syntactic features categorically
rule out inappropriate antecedents?
Experiment 2 investigated non-c-commanding QP lures. I hypothesized that
only if morphology can completely out-weigh structural information would we ob-
serve lure-match effects from non-c-commanding QP lures. The results do not ap-
pear to support this hypothesis. First of all, I did not find robust statistical support
for lure-match effects from QP lures. This is not very telling, since in general my
experiments failed to produce statistically significant results in most of the cases.
However, QP lures appeared to behave differently than NP lures in numeric patterns.
QP lures which matched the reflexive either had no effect or caused a slow-down.
In contrast, matching NP lures caused facilitation in both Experiment 1 and 2.
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I have established that the lack of facilitation is not due to several possible con-
founds. It cannot be due to the fact that QPs are not good lures for some reason:
c-commanding QP lures which matched the reflexive did cause a speed-up relative
to non-matching ones. Second, Experiment 5 and 6 suggest that context factors
such as composition of the stimuli set and experimenter’s language do not affect the
magnitude of the lure-match effect. Third, small effect sizes cannot be the result of
the lures being embedded under animate subjects as S2017’s sub-command hypoth-
esis would suggest, as shown by Experiment 1 results. Finally, the fact that QP
lures provoked inhibitory, rather than facilitatory interference is reminiscent of the
numerical trend observed in Kush et al. (2015) Exp.2. There, people were slower
to read pronouns like “he” in sentences like “The troop leaders [that no boy/girl
scout respected] scolded him” when the embedded QP matched the gender of the
pronoun, suggesting that out observations are not spurious.
Experiments 3 and 4 showed that in contrast to non-c-commanding QP lures,
the c-commanding ones do cause lure-match effects. The magnitude and the direc-
tion of the effects was mostly consistent for NP and QP lures, suggesting that the
parser treats the two lure types similarly when they c-command the reflexive. While
the magnitude of the effects was smaller than in the original PP2017 study, it was
consistent with the two replications I ran in Exp.5 and 6.
This contrast between c-commanding and non-c-commanding lures makes me
conclude that c-command information is able to successfully restrict the range of
possible antecedents. The fact that the parser appears to treat non-c-commanding
NP and QP lures differently also suggests that c-command information is represented
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in an approximate way, perhaps using Kush et al. (2015) accessible.
5.1.3 On the reliability of lure-match effect
5.1.3.1 Magnitude of the effect
Throughout the thesis I have observed lure-match effects which were going
in the right direction numerically (faster RTs in conditions with matching lures)
but were consistently smaller than those reported in the original study by Parker
and Phillips (2017). Almost in no case did these effects in my experiments received
statistical support. I have ruled out several potential explanations for the reduced
magnitude. First, I made sure that the experiments worked on a basic level - as
expected, people spent more time reading longer words and skipped them less fre-
quently. Grammatical characteristics of the stimuli did affect people’s RTs - quite
consistently, I observed grammaticality effects when ungrammatical sentences were
read slower than grammatical ones. Moreover, lure-match effect were observed for
subject-verb agreement, suggesting that I did not accidentally selected participants
immune to such effects. Second, I ruled out potential systematic confounds. Con-
trolling for the composition of stimuli set (in particular, the presence of QPs in it)
and characteristics of experimenter ((non-)nativeness) did not have an effect on the
magnitude of lure-match effects.
It is tempting to conclude that the observed discrepancies between my and
previous results are likely due to purely statistical reasons. As I have mentioned
in Chapter 4, it is well known that in low-powered studies statistically significant
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effects are more likely to be overestimates (Gelman and Carlin, 2014; Collaboration,
2015). The original studies by PP2017 that I tried to replicate had sample sizes of
24 and 30 people, which is rather low even by psycholinguistics standards. Even
my studies which had doubled sample sizes still failed to provide robust statistical
evidence. Only in the exploratory analysis on the pooled data, comprising the
data from 81 participants, did some lure-match effects reach significance. On the
other hand, S2017’s experiment may speak against such interpretation: he used
sample sizes comparable to mine and consistently found statistical support for lure-
match effects. While in a low-powered setting this could be attributed to chance
alone, the consistency with which lure-match effects are supported by statistics in
S2017 on the one hand and in my experiments on the other makes me think that
additional factors may be at play. I could think of several directions which could be
investigated, although I do not have strong hypotheses about how the differences in
these parameters would have affected the inferences.
One potentially important factor is that both PP2017 and S20171 sentences
contained gaps or pronominal elements in the spillover region: e.g. “The flustered
nurse complained that the elderly veterans considered herself to be very attractive
and made suggestive comments” or “The broken zipper that the skilled tailors tried
to fix pinched themselves repeatedly on their fingers.”. It is possible that people
could preview the spillover regions with their parafoveal vision, or that the interpre-
tation of the reflexive was still on-going while their gaze had already shifted on the
1To the degree that I can see: I only had access to the materials they used in their Experiments
1 and 3
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spillover. In these cases the presence of an element depending on the reflexive’s in-
terpretation could affect the processing. For example, null or overt pronouns might
have provoked additional retrievals of the lures and artificially increased their ac-
cessibility in S2017’s experiments. Alternatively, given that the interpetation of the
reflexive would influence the interpretation of some other element, people might en-
gage in additional checks of whether the antecedent they chose is permissible by the
grammar. In this case, the intrusion effects might be smaller or absent altogether.
The first alternative might receive some support from the data. In my Exper-
iment 2 12 out of 24 items had an empty element in the spillover, while in the in
Parker and Phillips (2017, Exp.2), using similar stimuli, only 4 out 36 items did.
In my Exp.4 we borrowed a subset of NP items from Sloggett (2017, Exp.1). In
that experiment, 14 out of 48 items (i.e. roughly a quarter) had an empty element
in the spillover. It turns out that I borrowed 9 of such items into my experiment.
Since I had fewer NP stimuli (24), those items accounted for almost half of them.
It could be that the reduction of the intrusion effect in my case was strong enough
to make the substantial evidence for it disappear, while Sloggett (2017, Exp.1) was
affected less due to a higher proportion of stimuli without an empty element in the
spillover. It would be trivial to check whether this is the case if I had the original
data from Sloggett (2017): in that case, I could look at whether there are differences
in the effect size between the stimuli I did and did not select. This account would
fail to explain the absence of evidence for intrusion in Exp.3: in constructing the
stimuli for it, I made sure that the spillover did not contain any empty elements.
However, these results may be independently explained by the fact that I used a
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mix of communication and other types of verbs in the materials for Exp.3.
Another possibility could be that the gender stereotypes on the nouns I used
were weaker than on the nouns in PP2017 and S2017 experiments. It could lead to
them being worse lures and thus producing on average smaller lure-match effects.
While possible in principle, I think this explanation is a non-starter: I failed to
observe statistically robust effects in two direct replications of PP2017, thus, the
strength of the gender stereotype alone can not be the issue. In other experiments
I either directly borrowed a subset of PP2017 and S2017 materials, or was heavily
influenced by their materials in creating mine. Therefore, I think that the strength
of gender stereotypes is not an issue here.
It is possible that subtle differences in the experimental procedure might have
changed the results. As Hammerly et al. (draft.april.2018) show, the change in
wording from “two thirds of the items are ungrammatical” to “the majority of the
items are ungrammatical” apparently was enough to change the observed agreement
attraction effects. Such biases do not have to be restricted to the instructions and
may involve other factors: how often do participants take breaks, how often is re-
calibration performed, how does the experimenter interacts with the participants
before the experiment starts etc., and may be hard to catch.
Overall, I conclude that while low statistical power may be an issue, unrecog-
nized biases have likely affected my results. It is hard to make stronger conclusions
in the absence of formal or simulation-based power analysis, but I suggest that since
lure-match effects may apparently be hard to detect in smaller samples, sample
sizes bigger than 40-50 participants are desirable in order to find reliable evidence
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for interference when looking at reflexives resolution.
5.1.3.2 Timing of the effect
The time course of the lure-match effects appears to be variable across the
studies. Some experiments (Parker and Phillips (2017) Exp.1,3; Sloggett (2017)
Exp.1b and 4b) show detectable lure-match effects as early as in first-pass and
regression path at the critical region. Some others do not show reliable effects until
later - re-read and total times at the critical region (Parker and Phillips (2017)
Exp.2, Sloggett (2017) Exp.2b), or even at spillover in regression path (Sloggett,
2017, Exp.3b). My experiments rather fall in the second group: numerically, the
lure-match effects got biggest in re-read or total times at the critical region, and the
only instance of a significant main effect of lure match (Exp.1) was detected in
the total times at spillover.
What is the reason behind such variability? The first possibility is that it is
due to some systematic differences in the stimuli set. However, the evidence does
not support this hypothesis: in multiple cases the exact same or very similar stimuli
set produced variable results. The best example is PP2017 Exp.3, where lure-match
effects were observed as early as in first pass at the critical region, and my two
replications (Exp.5 and 6) where the magnitude of the effects was biggest in late
eye-tracking measures. These studies used the exact same set of stimuli. PP2017
Exp.2 and my replication in Exp.1 had similar variability, with Exp.1 using a subset
of the original stimuli. Finally, S2017 observed such variability in his Exp.3b and
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4b, despite using same critical stimuli.
It is possible that individual characteristics of the participants lead to the
variability in the timing of the lure-match effects. Cunnings and Felser (2013) in-
vestigated the effect of working memory on lure-match effects in reflexive resolution.
They only considered 1-target mismatch configurations, and had a rather small sam-
ple sizes (32 participants by experiment, in each case split into two groups depending
on their working memory capacity), so the results may not be very reliable. For what
it’s worth, they report differential effects depending on the working memory span:
low-span group was faster to detect the mismatch with the target. The effect first
became significant in first fixation duration at the reflexive for the low-span group
and in re-read times for the high-span group2.
Finally, one could think that the lure-match effects observed in early measures
are artifactual. As I have just discussed, for all experiments where lure-match
effects were observed in early measures there is a related experiment where they
were not. On the other hand, in the late measures lure-match effects are observed
more consistently. Such a pattern may indicate that lure-match effect are, in fact,
a reflection of a repair strategy. If it is the case, that would constitute evidence
against PP2017 account: if a repair is initiated, the original resolution attempt
must have failed; it would only fail, if the parser correctly accessed the target;
therefore we have to assume that structural information is able to strictly rule out
2The authors suggest that this may reflect the application of least effort strategy from low-span
readers, in which they simply select the closest noun as the antecedent instead of fully processing
the dependency.
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ungrammatical antecedents at least during initial resolution attempts (cf. with “the
defeasible filter” hypothesis by Sturt (2003)).
Several arguments can be made against such possibility. As Vasishth et al.
(2012) notice, effects which become apparent in late measures are not necessarily
stemming from late processes; instead, they might stem from a process which starts
early but unfolds slowly enough to only become apparent later. Thus, simply observ-
ing some effect emerging in late measures does not allow to uniquely attribute it to
repair processes. Further, S2017 provides three arguments against repair account.
First, he notes that some experiments do show early lure-match effects. Second,
S2017 discusses the results of his interpretation study, in which people appeared
to choose non-local interpretation as frequently as in 30% of the cases even when
the sentences were grammatical (i.e. the target fully matched the reflexive in fea-
tures). And third, he notices that reflexives with clearly non-local interpretations
are sometimes observed in natural production3.
Overall, the tendency of the lure-match effects to be more prominent in late
eye-tracking measures is interesting, but it lacks sufficient evidence for firmer con-
clusions. While it could potentially be problematic for PP2017 account, further
studies are necessary to decide whether the tendency does, indeed, exist, and if so,
3While these arguments would help the claim I am making by ruling out the repair explanation
of lure-match effects, I tend to be somewhat skeptical about them. As I have just noted, lure-
match effects in early measures appear to be less reliable than late effects and might be artifactual.
I discuss my concerns about the interpretation of these results in section 5.2. Finally, the third
argument is potentially the strongest one, but it assumes that lure-match effects in comprehension
and logophoric use of reflexives in production rely on the same mechanisms, which is not given.
216
what are its causes.
5.1.4 Choosing between the two accounts
Based on the evidence I have discussed above, I suggest that neither PP2017
nor S2017 account is completely supported. On the one hand, my findings from
Experiment 1 suggest that sub-command binding may not be a good explanation
for lure-match effects from non-c-commanding lures. On the other hand, the results
from Experiments 2-4 suggest that the parser does faithfully follow an approximate
version of c-command to categorically rule out inaccessible QP antecedents.
This interpretation goes against grammatical models, such as S2017: the
parser does appear to perform operations which would not be licensed by the gram-
mar. However, it also goes against “structure-defeasible” memory models such as
PP2017: structural information appears to accurately guide the retrieval at least in
some cases. I suggest that a memory type of account is still a better explanation
for the available data.
Two main empirical facts supporting this conclusion are a) the presence of
lure-match effects from non-c-commanding lures embedded in an animate subject;
b) differential lure-match effects from non-c-commanding QP and NP lures in the
same configurations. S2017 sub-command hypothesis would not be able to explain
them, since it only predict interference from the lures embedded inside an RC with an
inanimate head. The same goes for the logophoric explanation of the sub-command
facts by Charnavel and Huang (2018).
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But let us imagine that one of those explanation could account for lure-match
effects from RC-lures, perhaps because in English sub-command binding is possible
regardless of the animacy of the (head of the) embedding NP. Even in this case we
would not be able to explain why non-c-commanding QP lures do not cause lure-
match effects: as we showed in Chapter 2, in Chinese sub-commanding QPs can serve
as antecedents for “ziji”. We could build another layer of speculation: suppose, in
English QPs are not good as non-local antecedents for reflexives, as Postal (2006)
suggests. But now we would not be able to explain why c-commanding QPs do
provoke lure-match effects. Let us build yet another counterfactual. Suppose, we
suggest that the null operator mediating logophoric interpretation, OPlog, is located
in the left periphery of all clauses, and not only complement ones, as S2017 suggests.
We think, it would still fail to capture interference from the lures embedded under
an animate noun: arguably, the embedding noun is more prominent in the discourse
and is more likely to control OPlog reference. Thus, even if OPlog is occasionally
misretrieved, as S2017 suggests, the resolution would still pick the matrix subject,
and not the embedded lure, as the antecedent. The OPlog account would also not
be able to capture the contrast between c-commanding and non-c-commanding QP
lures. Although S2017 is not very specific about the mechanism which is used to
determine the reference of OPlog, he speculates that the mechanism should be similar
to the one used by regular pronouns looking for their antecedents in the discourse
Sloggett (2017, p.140). This remark suggests that OPlog resolution relies on co-
reference. Since QPs may only bind, they would not be able to serve as antecedents
for OPlog. This conclusion would be in line with Postal (2006) observations.
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Thus, it appears that it is hard to explain my findings in terms of some gram-
matical strategy, and a memory models might be preferred. But we would have
to choose a model which is only partially “structure-defeasible”: instead of assum-
ing that all structural information is weighted uniformly and can be out-competed,
we would have to assume that the parser differentiates between different kinds of
structural information, with some being able to act as gating features.
How could this suggestion be implemented in a memory model? Under the
usual assumptions cue-based models do not make it easy for a cue to categorically
block access to some memory item: even if a feature on an item mismatches the
retrieval cues, other features of the item may match them well enough to still make
the item retrievable. Kush et al. (2015) discuss two possibilities of how a feature
could act as a gating feature, categorically restricting access only to matching items.
One could weigh the gating feature extremely highly, so that the items that match
it receive such a high activation boost that no other item can compete with that.
Alternatively, one can change the way cues are combined to determine an item’s
activation. Most often it is assumed that the activation is determined by a weighted
sum of activation values provided by the matching cues, with weights corresponding
to their importance, and activation values - the strength of association between the
item and the cue in question. However, one could assume that a weighted product
is used instead. In this case, if a single feature mismatches the set of retrieval
cues, it would make the activation of the item very small or kill it completely, thus
preventing its retrieval in the majority of the cases4. Kush et al. (2015) mention
4Presumably, such an item could still be retrieved occasionally, if the random noise happens to
219
that it is impossible to tell these possibilities apart from their data.
I think that the data in the thesis may favor the first hypothesis: super-
weighting of the gating cues. In order to explain the fact that mismatch on locality
information may be out-weighed by other factors, one would have to conclude that
locality cue(s) contribute to item’s activation in an additive fashion. Now, acces-
sible cue has to be able to categorically rule some items out from consideration. In
principle it is possible that it combines multiplicatively with other cues, in a manner
described by Eq. 5.1, where GCA 5i is the binary indicator of whether all gating
cues6 allow the i − th item to be retrieved (i.e. whether the i − th item matches
these cues). However, this would create a situation where different cues rely on
different combinatorics rules, and without strong evidence for such mixed schemas,
it seems preferable to keep cue combinatorics rules uniform within a model. Since
we have to assume an additive schema to capture locality facts, accessible would
push its activation high enough to outcompete other items in memory.
5Standing for “gating cues activation”.
6It seems possible that if the system relies on gating cues at all, there is more than one such cue.
In this case, we need to know how these cues combine. The schema I suggest assumes that if even
a single gating cue fails to match, the item is ruled out. This could be achieved if zero activation is
spread from a mismatching gating cue, and the values of all gating cues are multiplied to produce
the final GCAi value. More involved combinatorics schemas could in principled be produced, so
that, say, a item has two mismatch two gating cues together in order to be ruled out. Also notice
that when several items do match a gating cue, the activation it spreads to these items will be less
than 1 due to fan effect. If the system uses multiple gating cues at once, and it happens so that
each gating cue is matched by multiple items, the items’ activation values can be driven very low,
since the product of several values smaller than 1 may indeed be small.
220
have to combine additively as well. In this case, super-weighting is the only way
of making it act as the gating feature. This hypothesis could in principle be tested
empirically: if super-weighting is, indeed, the underlying mechanism, we might find
ways to boost the activations from other features highly enough to out-weigh even
the super-weighted cues. E.g. we might try to make the match with the true target
even stronger, and/or put the lure in a linguistically prominent position.
∑
Ai = Bi +GCAi × ( wjSji) (5.1)
j
Concluding, I have to note that several empirical points may be taken as
speaking against my suggested account, although very speculatively. First, I ob-
served the tendency for lure-match effects to be more readily detectable in late
eye-tracking measure. So far it is simply a suggestive observation, but if confirmed
experimentally, it could indicate that lure-match effects stem from repair processes.
As discussed, this would imply that at least at some point structural information
does categorically constrain parser’s actions. Second, it appears that the magni-
tude of lure-match effects from NP lures is bigger when the lure c-commands the
reflexive. This is true both in PP2017 and in my replications: despite that the
effect sizes we observe are overall reduced compared to PP2017, the difference be-
tween c-commanding and non-c-commanding lures holds. This may suggest that
non-c-commanding lures are less accessible in general, with non-c-commanding QP
lures being completely inaccessible and c-commanding NP lures being relatively in-
accessible. If this intuition is correct, it will weaken my conclusions about the use
221
of accessible: accounts relying on this feature do not predict any access diffi-
culty for + accessible phrases regardless of their c-command relations. Third,
in both Experiment 1 and Experiment 2 I did observe an illusion of ungrammat-
icality in agreement attraction stimuli. This is problematic for cue-based models,
of which PP2017 account is an instance. This is also in line with Hammerly et al.
(draft.april.2018), who suggest a “structure-strong” account for agreement attrac-
tion. As I have discussed in Chapter 1, so far their account is not fully developed
and, for example, is not easily extendable to eye-tracking data. But such data
points support their model and if it is better developed, it could constitute a strong
competitor to cue-based modes.
Finally, I remind that my conclusions necessarily remain tentative, being based
almost entirely on numerical patterns of RTs.
5.2 Future directions
Given that most of my conclusions are based on numerical patterns or RTs,
the most important next step is to conduct adequately powered confirmatory ex-
periments. The numerical estimates of the lure-match effect magnitude I obtained
in this study7 could be used for power calculations. The most important thing is
to further investigate the interference from non-c-commanding lures - this would
help to improve the evidence quality of evidence for the only pattern not covered
by S2017 account.
7As well as other estimates, such as random effects and variance-covariance matrices for par-
ticipants and items
222
Another possible line of investigation is to look for lure-match effects from
lures in a possessor position, e.g. “The librarian’s brothers praised herself during
the meeting”. S2017 account does not predict any interference: the subject NP
is not embedded in a complement clause, so there is no null operator which could
mediate the dependency between “librarian” and “herself”. Even if such operator
were present, we do not think “librarian” is prominent enough to control its refer-
ence. Sub-command explanation would not work either: the configuration is of the
right type, but the embedding NP is animate and thus should block sub-command
binding. PP2017 account, on the other hand, would predict lure-match effects from
“librarian” unless c-command information is accurately used to guide the retrieval.
Thus, in the suggested experiment the presence of an effect would speak for PP2017
model, but the absence of the effect would be hard to interpret since it could be
compatible with both S2017 and PP2017 accounts.
A third possible line of investigation would be to consider whether the mech-
anism behind lure-match effects in reflexive resolution is purely formal (e.g. just
checking the morphological features) or whether it affects interpretation. PP2017
account does not make strong predictions either way. On the other hand, S2017
account necessarily predicts that interpretation is affected, since S2017 argues for a
grammatical option of reflexive resolution. S2017 supports this point of view with
a results of interpretation study: he shows that when presented with sentences like
”The librarian said that the schoolgirl misinterpreted herself...” and asked a question
like ”Who was misrepresented at the meeting? – The schoolgirl / The librarian”,
people choose the answer compatible with non-local binding of the reflexive (”librar-
223
ian” in this example) as frequently as 30% of the time. S2017 uses this finding to
support his argument about the logophoric nature of interference effects in reflexive
resolution: if people can choose the non-local option even in grammatical sentences,
it this choice has to be a grammatical possibility.
We have doubts about this claim for several reasons. First, question answers
do not necessarily stem from the same processes which underlie reflexive resolution
during sentences processing. Instead, they may come from some extra-grammatical
strategy (e.g. if upon seeing the question, people choose the answer not based
upon how the reference was resolved but based on some other factors - familiarity,
the answer being a more sensible choice etc.). Second, according to the Sloggett’s
hypothesis, non-local reference is mediated by a silent logophoric operator. It is
hypothesized not to carry any φ-features. Thus, if the overt local noun matches
the reflexive in features, it will be a better match on at least two features - gender
and number (and potentially person and/or animacy). If S2017 results do indeed
indicate that people retrieve the silent operator, it would mean that even a target
which is the best match along multiple dimensions can be ignored during memory
access as frequently as 30% of the time. It seems odd to assume that memory
access is so inefficient: if it performs that poorly in perfect conditions, what would
it performance be in real-life situation with potentially less certainty about what the
correct outcome is? Third, in all of his acceptability judgment experiments people
give rather low ratings8 for sentences with target mismatch - even when the lure
8To give an idea, target mismatch conditions received ratings in the range of 3-4, while target
match conditions were all above 5 on a Likert scale from 1 to 7.
224
matches the reflexive the ratings are lower than for grammatical sentences. This
fact is hard to explain if, as S2017 argues, lure-match effects arise from a completely
grammatical anaphora resolution strategy9.
I suggest several ways of checking whether S2017’s interpretation results do
indeed reflect the outcome of reflexive resolution during sentence reading or whether
they are due to some extragrammatical strategy. Perhaps, the best option would
be to use an eye-tracking study with interpretation questions. After collecting the
data, one could separately analyze the conditions depending on the antecedent choice
people made. If S2017 is correct, and RTs patterns and interpretations stem from
the same mechanism, we will only observe facilitatory interference in conditions
where people chose the non-local antecedent. Second, one could turn to a visual
world paradigm: if lures are indeed chosen as antecedents in real-time, we should
observe increased amount of looks for the picture representing the lure. Finally, one
could make people’s task as easy as possible10. In S2017 experiment, people had to
read the sentence in a self-paced fashion before answering the question. I.e. they
never saw the sentence in its entirety, and had limited time to process it. If S2017
is correct, and non-local interpretations do stem from a grammatical interpretation
option, these factors should not matter a lot and people will produce roughly the
same interpretation patterns in easier conditions, e.g. when having unlimited time
to look at the sentence. Otherwise, we would see a reduction in the number of
non-local interpretations.
9I would like to thank Colin Phillips for this observation.
10I would like to thank Colin Phillips for this idea.
225
5.3 Conclusion
In this thesis, I attempted to distinguish between two types of real-time long-
distance dependency resolution models - those which assume that structural infor-
mation categorically rules out structurally inappropriate elements and those which
do not. Specifically, I contrasted two recent instantiations of these models explain-
ing lure-match effects in reflexives resolution. Parker and Phillips (2017) attributed
those effects to a processing error, while Sloggett (2017) attributed them to a gram-
matical strategy. The evidence I obtained in six experiments suggested that neither
account is entirely correct. Contrary to what S2017 claims there seem to be cases
(namely, lure match effects from non-c-commanding lures) which are best explained
in terms of a processing error. Contrary to what PP2017 say, structural information
appears to have flavors - some kinds of it (e.g. locality), may not always succeed
in categorically ruling out inappropriate antecedent, while others (e.g. some ap-
proximation of c-command), may do so. I suggested that the best explanation for
this evidence is a mixed memory model, in which some structural information (e.g.
locality) is weighted highly but can be outcompeted relatively easily, and other
structural cues (e.g. c-command) is super-weighted so that it is hard or impossible
for other factors to out-weigh it.
These studies have also shown that lure-match effects may not be as reliable
and big as previous studies suggest. In fact, most of my conclusions are based
on numerical patterns in the data. I failed to find statistical support for lure-
match effects, despite having sample sizes comparable to or bigger than in the
226
previous studies. I do not think this indicates that the effects are bogus - they have
been replicated multiple times, the numerical patterns I observe in my studies are
going in the expected direction, and an exploratory analysis of pooled data from
about 80 participants suggests that such sample size is enough for the statistics to
support even the reduced effects. Rather, these results may indicate that the lack of
statistically significant effects is due to low statistical power or unidentified subtle
biases in experimental materials and procedures. I stress the necessity to conduct a
priori power analyses; the data that I have collected can be used to set expectations
for such analyses. I would certainly welcome higher-powered replications of my own
studies which could verify the conclusions I make.
227
Appendices
228
Appendix A: Mean reaction times in PP2017and replication (PP2017analysis)
Notice that standard errors reported here for PP2017data are slightly smaller
than those reported in the original paper. The difference comes from the fact that
we calculated them taking into account subject variability, by using the method
suggested in Cousineau (2005) and Morey (2008)1. In contrast, as far as we can say,
PP2017used the standard formula for calculating SEs: √sd .
n
1The code implementing this procedure was taken from: http://www.cookbook-r.com/
Graphs/Plotting_means_and_error_bars_(ggplot2)/.
229
Mean RTs in PP2017
Region
Cond precrit crit spillover
fp tm, lm 947.4 (46.68) 196.7 (10.05) 166.4 (12.74)
tm, lmm 927.5 (39.73) 223 (10.93) 154.8 (15.16)
tomm, lm 805 (33.65) 224.6 (11.29) 166.2 (22.25)
tomm, lmm 903.1 (35.85) 222.5 (12.08) 165.2 (15.33)
ttmm, lm 912.8 (33.82) 184.7 (10.91) 156.4 (14.06)
ttmm, lmm 881.7 (33.92) 289.7 (16.44) 129.1 (13.42)
rb tm, lm 1162 (42.82) 200.1 ( 10.3) 195.7 (15.84)
tm, lmm 1108 (36.39) 228.3 (11.22) 184.5 (22.23)
tomm, lm 1025 (33.64) 244.8 (12.42) 214.7 (29.35)
tomm, lmm 1088 (33.93) 233.7 (12.46) 195.3 (19.23)
ttmm, lm 1117 (35.72) 190.6 (11.76) 191.3 (18.19)
ttmm, lmm 1062 (33.93) 329.3 (18.94) 178.1 (22.75)
rp tm, lm 1295 (67.08) 221 ( 14.8) 311.6 (41.56)
tm, lmm 1203 (50.55) 250.9 (13.29) 282.3 (43.47)
tomm, lm 1199 (62.91) 303.8 (28.14) 338.7 (52.22)
tomm, lmm 1206 (53.94) 316.5 (38.28) 341.5 ( 67.3)
ttmm, lm 1188 (44.37) 229.2 (22.99) 318.1 (51.11)
ttmm, lmm 1199 (53.05) 456.5 (64.29) 405.2 (91.27)
rr tm, lm 872.5 (68.21) 223.1 (22.04) 265 (30.71)
230
tm, lmm 798.7 ( 56.6) 224 (22.17) 253.4 (30.72)
tomm, lm 880.6 (78.36) 318.1 (26.77) 265.8 (33.63)
tomm, lmm 1044 (74.39) 338.7 (27.66) 233.6 (24.64)
ttmm, lm 925.1 (79.73) 212.2 (22.67) 286.9 (33.07)
ttmm, lmm 1210 (93.32) 445.5 (45.64) 288 (31.86)
Table A.1: Mean RTs in PP2017
Reading measures: fp - first pass, rb - right-bound, rp - regression path, rr - re-read.
Conditions: tm/tomm/ttmm - target match/one-mismatch/two-mismatch; lm/lmm - lure
match/mismatch.Values in the parenthesis represent standard error of the mean, corrected
for within-subjects variability(Cousineau, 2005; Morey, 2008)
231
Mean RTs in the replication of PP2017
Region
Cond precrit crit spillover
fp tm, lm 946.7 (25.82) 205 ( 7.73) 226.6 (11.48)
tm, lmm 1004 (28.14) 214.8 ( 8.47) 204.6 (10.43)
tomm, lm 923.1 ( 24.3) 210.7 ( 8.8) 222.3 (12.01)
tomm, lmm 918.1 (23.91) 237.8 ( 9.67) 229.1 (11.66)
ttmm, lm 927.1 (26.78) 225.1 ( 8.43) 210.6 (11.13)
ttmm, lmm 955.5 (24.76) 243.5 (10.07) 220.2 (10.98)
rb tm, lm 1124 (24.23) 220.1 ( 8.56) 255 (13.65)
tm, lmm 1152 (27.64) 229.4 ( 9.3) 231.8 (13.74)
tomm, lm 1064 (23.33) 220.7 ( 9.5) 277.1 (16.97)
tomm, lmm 1066 (22.51) 258.1 (11.03) 263.9 (14.48)
ttmm, lm 1090 (25.18) 249.5 ( 10.2) 262.6 (15.02)
ttmm, lmm 1089 (24.01) 275.7 (12.56) 281.7 ( 15.1)
rp tm, lm 1203 (32.16) 262.4 (13.95) 412.8 (43.15)
tm, lmm 1246 (35.75) 273.6 (17.24) 329.5 (32.07)
tomm, lm 1136 (27.78) 262.5 (17.34) 429.1 (40.17)
tomm, lmm 1143 (32.61) 348.3 (32.09) 442.8 (41.18)
ttmm, lm 1169 (32.19) 353.2 (30.91) 441.6 (43.06)
ttmm, lmm 1146 ( 28.6) 413 (36.68) 501.3 (42.68)
rr tm, lm 810.1 (49.34) 211 (17.24) 241 (16.41)
232
tm, lmm 779.9 (46.35) 205.8 (15.09) 257.9 (15.62)
tomm, lm 754.3 (47.66) 260.1 (17.78) 315.2 (23.77)
tomm, lmm 921.7 (51.72) 292.4 (18.11) 277.3 (18.65)
ttmm, lm 818.9 (58.33) 274.4 (20.47) 280 ( 21.7)
ttmm, lmm 995 (51.92) 366.1 (24.45) 312.2 (17.63)
Table A.2: Mean RTs in the replication of PP2017
Reading measures: fp - first pass, rb - right-bound, rp - regression path, rr - re-read.
Conditions: tm/tomm/ttmm - target match/one-mismatch/two-mismatch; lm/lmm - lure
match/mismatch.Values in the parenthesis represent standard error of the mean, corrected
for within-subjects variability(Cousineau, 2005; Morey, 2008)
233
Appendix B: Mean RTs
Region
Measure Target match Lure match Critical Spillover
fp match match 318 (20) 295 (14)
mismatch 416 (41) 290 (16)
mismatch match 345 (18) 313 (16)
mismatch 395 (31) 324 (23)
rp match match 386 (31) 422 (53)
mismatch 511 (53) 486 (60)
mismatch match 389 (26) 455 (47)
mismatch 639 (81) 510 (47)
tt match match 455 (38) 375 (23)
mismatch 509 (48) 377 (30)
mismatch match 520 (48) 366 (28)
mismatch 642 (58) 404 (31)
Table B.1: Experiment 2 means for agreement stimuli.
Numbers in parentheses are standard errors of the mean, corrected for
within-subjects variability (Cousineau, 2005; Morey, 2008).
234
Region
Measure Lure type Lure match Critical Spillover
fp NP match 297 (14) 300 (15)
mismatch 283 (14) 276 (13)
QP match 286 (12) 309 (15)
mismatch 262 (11) 295 (12)
rp NP match 425 (32) 752 (104)
mismatch 414 (36) 758 (91)
QP match 578 (64) 782 (91)
mismatch 509 (71) 683 (83)
tt NP match 533 (33) 512 (33)
mismatch 516 (30) 461 (26)
QP match 540 (29) 500 (25)
mismatch 524 (30) 489 (33)
Table B.2: Experiment 2 means for reflexives stimuli.
Numbers in parentheses are standard errors of the mean, corrected for
within-subjects variability (Cousineau, 2005; Morey, 2008).
Region
Measure Target match Lure match Critical Spillover
fp match match 420 (12) 361 (15)
mismatch 422 (14) 374 (16)
mismatch match 505 (20) 362 (14)
mismatch 486 (18) 368 (13)
rp match match 550 (35) 576 (52)
mismatch 612 (38) 615 (43)
mismatch match 864 (50) 830 (67)
mismatch 640 (29) 668 (69)
tt match match 741 (34) 625 (31)
mismatch 754 (31) 602 (26)
mismatch match 974 (39) 691 (32)
mismatch 839 (33) 595 (27)
Table B.3: Experiment 3 means for agreement stimuli.
Numbers in parentheses are standard errors of the mean, corrected for
within-subjects variability (Cousineau, 2005; Morey, 2008).
235
Region
Measure Lure type Lure match Critical Spillover
fp NP match 368 (13) 515 (21)
mismatch 361 (15) 485 (20)
QP match 353 (15) 535 (21)
mismatch 356 (15) 496 (21)
rp NP match 549 (34) 990 (66)
mismatch 597 (63) 1124 (92)
QP match 659 (55) 961 (72)
mismatch 616 (63) 1004 (81)
tt NP match 696 (30) 1002 (42)
mismatch 724 (35) 1056 (43)
QP match 683 (30) 1056 (46)
mismatch 726 (35) 1025 (41)
Table B.4: Experiment 3 means for reflexives stimuli.
Numbers in parentheses are standard errors of the mean, corrected for
within-subjects variability (Cousineau, 2005; Morey, 2008).
236
Region
Measure Target match Lure match Critical Spillover
NP lures
fp match match 347 (13) 435 (16)
mismatch 320 (11) 449 (20)
mismatch match 345 (14) 431 (15)
mismatch 371 (15) 450 (18)
rp match match 460 (28) 600 (39)
mismatch 480 (30) 668 (46)
mismatch match 486 (27) 736 (48)
mismatch 576 (41) 892 (72)
tt match match 571 (22) 702 (28)
mismatch 574 (23) 717 (27)
mismatch match 645 (28) 843 (36)
mismatch 694 (30) 847 (31)
QP lures
fp match match 291 (10) 438 (14)
mismatch 311 (11) 439 (15)
mismatch match 327 (11) 435 (17)
mismatch 344 (13) 474 (18)
rp match match 430 (31) 647 (52)
mismatch 420 (35) 644 (43)
mismatch match 474 (33) 921 (63)
mismatch 526 (36) 955 (70)
tt match match 515 (22) 767 (30)
mismatch 500 (20) 719 (25)
mismatch match 624 (27) 829 (32)
mismatch 669 (27) 906 (35)
Table B.5: Experiment 4 mean reaction times.
Reading measures: fp - first pass, rp - regression path, tt - total times.
Numbers in parentheses are standard errors of the mean, corrected for
within-subjects variability (Cousineau, 2005; Morey, 2008).
237
Appendix C: Model coefficients
Tables start on the next page.
238
Critical Spillover
Measure Effect Estimate t value Estimate t value
Agreement
fp (Intercept) 5.91 (0.05) 129.23 5.71 (0.04) 141.49
Target match 0.18 (0.04) 4.42 -0.06 (0.03) -1.8
Lure match 0.03 (0.04) 0.72 -0.03 (0.04) -0.9
Target match x Lure match 0.02 (0.08) 0.28 -0.04 (0.06) -0.57
rp (Intercept) 6.30 (0.06) 104.16 6.13 (0.05) 112.58
Target match 0.29 (0.05) 5.58 0.20 (0.06) 3.46
Lure match 0.13 (0.05) 2.7 0.11 (0.06) 1.86
Target match x Lure match 0.10 (0.09) 1.13 0.32 (0.10) 3.22
tt (Intercept) 6.60 (0.07) 95.08 6.31 (0.07) 86.88
Target match 0.28 (0.05) 6.06 -0.06 (0.04) -1.47
Lure match 0.13 (0.03) 3.93 0.05 (0.04) 1.21
Target match x Lure match 0.01 (0.08) 0.18 0.04 (0.08) 0.47
Reflexives
fp (Intercept) 5.64 (0.03) 196.79 5.85 (0.05) 116.57
Target animacy -0.04 (0.04) -0.82 -0.05 (0.06) -0.8
Lure match 0.05 (0.04) 1.36 -0.01 (0.04) -0.14
Target animacy x Lure match -0.09 (0.07) -1.42 -0.00 (0.08) -0.05
rp (Intercept) 6.00 (0.05) 122.01 6.44 (0.09) 71.99
Target animacy -0.06 (0.07) -0.86 -0.14 (0.15) -0.95
Lure match 0.05 (0.05) 0.93 0.07 (0.07) 1.01
Target animacy x Lure match -0.10 (0.10) -0.91 -0.06 (0.15) -0.39
tt (Intercept) 6.42 (0.05) 119.22 6.56 (0.07) 94.72
Target animacy -0.11 (0.06) -1.76 -0.22 (0.08) -2.81
Lure match 0.08 (0.04) 1.77 0.07 (0.04) 1.61
Target animacy x Lure match -0.00 (0.08) -0.01 0.05 (0.07) 0.65
Table C.1: Model coefficients for Experiment 1.
Reading measures: fp - first pass, rp - regression path, tt - total times. Contrasts coding:
“animate” = -0.5, “inanimate” = 0.5; “match” = -0.5, “mismatch” = 0.5. Statistically
significant comparisons are highlighted: yellow - significant only before a Bonferroni cor-
rection, red - significant before and after Bonferroni correction (see text). Values in the
parentheses represent standard error of the estimate.
239
Critical Spillover
Measure Effect Estimate t value Estimate t value
Agreement
fp (Intercept) 5.73 (0.09) 64.27 5.62 (0.05) 108.3
Target match 0.08 (0.09) 0.93 0.06 (0.06) 1.09
Lure match 0.09 (0.07) 1.23 0.01 (0.07) 0.17
Target match x Lure match -0.04 (0.13) -0.27 0.08 (0.12) 0.65
rp (Intercept) 5.89 (0.10) 61.64 5.89 (0.06) 94.91
Target match 0.12 (0.11) 1.13 0.06 (0.08) 0.73
Lure match 0.21 (0.08) 2.77 0.09 (0.11) 0.87
Target match x Lure match 0.11 (0.19) 0.6 0.03 (0.16) 0.2
tt (Intercept) 6.01 (0.11) 56.35 5.77 (0.07) 77.87
Target match 0.17 (0.09) 1.92 0.03 (0.07) 0.44
Lure match 0.11 (0.07) 1.63 0.04 (0.06) 0.66
Target match x Lure match 0.10 (0.12) 0.79 0.10 (0.13) 0.8
Reflexives
fp (Intercept) 5.53 (0.04) 142.43 5.55 (0.05) 118.83
Lure match -0.06 (0.04) − 1.64 -0.06 (0.05) − 1.22
Lure type -0.04 (0.05) − 0.92 0.04 (0.04) 1.01
Lure match x Lure type -0.04 (0.08) − 0.47 0.03 (0.08) 0.32
rp (Intercept) 5.85 (0.05) 111.20 6.11 (0.07) 85.43
Lure match -0.08 (0.06) − 1.30 -0.07 (0.09) − 0.74
Lure type 0.10 (0.07) 1.47 -0.02 (0.08) − 0.21
Lure match x Lure type -0.08 (0.12) − 0.63 -0.17 (0.16) − 1.07
tt (Intercept) 6.07 (0.05) 115.34 5.97 (0.07) 91.59
Lure match -0.05 (0.06) − 0.85 -0.09 (0.06) − 1.52
Lure type 0.02 (0.06) 0.41 0.01 (0.05) 0.12
Lure match x Lure type -0.03 (0.10) − 0.29 -0.04 (0.11) − 0.36
Table C.2: Model coefficients for Experiment 2.
Reading measures: fp - first pass, rp - regression path, tt - total times. Contrasts coding:
“match” = -0.5, “mismatch” = 0.5. Statistically significant comparisons are highlighted:
yellow - significant only before a Bonferroni correction, red - significant before and after
Bonferroni correction (see text). Values in the parentheses represent standard error of the
estimate.
240
Critical Spillover
Measure Effect Estimate t value Estimate t value
fp (Intercept) 5.91 (0.05) 129.23 5.71 (0.04) 141.49
Target match 0.18 (0.04) 4.42 -0.06 (0.03) -1.8
Lure match 0.03 (0.04) 0.72 -0.03 (0.04) -0.9
Target match x Lure match 0.02 (0.08) 0.28 -0.04 (0.06) -0.57
rp (Intercept) 6.30 (0.06) 104.16 6.13 (0.05) 112.58
Target match 0.29 (0.05) 5.58 0.20 (0.06) 3.46
Lure match 0.13 (0.05) 2.7 0.11 (0.06) 1.86
Target match x Lure match 0.10 (0.09) 1.13 0.32 (0.10) 3.22
tt (Intercept) 6.60 (0.07) 95.08 6.31 (0.07) 86.88
Target match 0.28 (0.05) 6.06 -0.06 (0.04) -1.47
Lure match 0.13 (0.03) 3.93 0.05 (0.04) 1.21
Target match x Lure match 0.01 (0.08) 0.18 0.04 (0.08) 0.47
fp (Intercept) 5.64 (0.03) 196.79 5.85 (0.05) 116.57
Target animacy -0.04 (0.04) -0.82 -0.05 (0.06) -0.8
Lure match 0.05 (0.04) 1.36 -0.01 (0.04) -0.14
Target animacy x Lure match -0.09 (0.07) -1.42 -0.00 (0.08) -0.05
rp (Intercept) 6.00 (0.05) 122.01 6.44 (0.09) 71.99
Target animacy -0.06 (0.07) -0.86 -0.14 (0.15) -0.95
Lure match 0.05 (0.05) 0.93 0.07 (0.07) 1.01
Target animacy x Lure match -0.10 (0.10) -0.91 -0.06 (0.15) -0.39
tt (Intercept) 6.42 (0.05) 119.22 6.56 (0.07) 94.72
Target animacy -0.11 (0.06) -1.76 -0.22 (0.08) -2.81
Lure match 0.08 (0.04) 1.77 0.07 (0.04) 1.61
Target animacy x Lure match -0.00 (0.08) -0.01 0.05 (0.07) 0.65
Table C.3: Model coefficients for Experiment 3.
Reading measures: fp - first pass, rp - regression path, tt - total times. Contrasts coding:
“match” = -0.5, “mismatch” = 0.5. Statistically significant comparisons are highlighted:
yellow - significant only before a Bonferroni correction, red - significant before and after
Bonferroni correction (see text). Values in the parentheses represent standard error of the
estimate.
241
Critical Spillover
Measure Effect Estimate t value Estimate t value
NP lures
fp (Intercept) 5.72 (0.04) 159.58 5.92 (0.06) 101.46
Target match 0.04 (0.04) 0.97 0.00 (0.04) 0.12
Lure match -0.01 (0.03) -0.25 0.01 (0.03) 0.38
Target match x Lure match 0.16 (0.07) 2.38 0.00 (0.08) 0.06
rp (Intercept) 5.96 (0.05) 122.63 6.27 (0.07) 85.02
Target match 0.07 (0.05) 1.46 0.18 (0.05) 3.37
Lure match 0.04 (0.06) 0.68 0.08 (0.06) 1.36
Target match x Lure match 0.08 (0.09) 0.86 -0.00 (0.12) -0.02
tt (Intercept) 6.23 (0.06) 107.23 6.46 (0.07) 87.34
Target match 0.13 (0.06) 2.32 0.16 (0.04) 4.23
Lure match 0.02 (0.04) 0.54 0.04 (0.04) 1.13
Target match x Lure match 0.04 (0.07) 0.59 0.03 (0.07) 0.47
QP lures
fp (Intercept) 5.64 (0.03) 162.94 5.94 (0.06) 98.23
Target match 0.09 (0.04) 2.46 0.01 (0.04) 0.34
Lure match 0.05 (0.04) 1.55 0.03 (0.04) 0.85
Target match x Lure match -0.01 (0.06) -0.14 0.08 (0.07) 1.2
rp (Intercept) 5.86 (0.05) 116.63 6.32 (0.08) 78.04
Target match 0.14 (0.06) 2.29 0.30 (0.05) 6.23
Lure match 0.05 (0.05) 0.92 0.04 (0.06) 0.58
Target match x Lure match 0.11 (0.08) 1.26 0.02 (0.09) 0.28
tt (Intercept) 6.15 (0.06) 108.98 6.49 (0.07) 88.28
Target match 0.23 (0.05) 4.36 0.14 (0.03) 4.28
Lure match 0.03 (0.04) 0.79 0.04 (0.05) 0.84
Target match x Lure match 0.12 (0.08) 1.54 0.15 (0.08) 2
Table C.4: Model coefficients for Experiment 4.
Reading measures: fp - first pass, rp - regression path, tt - total times. Contrasts coding:
“match” = -0.5, “mismatch” = 0.5. Statistically significant comparisons are highlighted:
yellow - significant only before a Bonferroni correction, red - significant before and after
Bonferroni correction (see text). Values in the parentheses represent standard error of the
estimate.
242
Appendix D: List of changes to the Parker and Phillips (2017) stim-
uli in the replication experiment
“→” indicates the changes made (the left-hand side: original; the right-hand
side: replacement). “Q” indicates that the changes were made not to the sentence
itself, but to the accompanying comprehension question.
• Item 13, cond 2, Q: “spokeswoman” → “spokesman” (to align with the sen-
tence)
• Item 13, cond 3, Q: “spokesman” → “spokeswoman” (to align with the sen-
tence)
• Item 13, cond 5, Q: “spokesmen” → “spokeswomen” (to align with the sen-
tence)
• Item 15, cond 2,4,6: “rock star” → “pop diva” (fixing factorial manipulation:
matrix subject should vary in gender across sentences)
• Item 22, cond 1: “The friendly waitress mentioned that the outspoken hostess
recommended herself for the new position”→ “The clumsy waitress mentioned
that the outspoken hostess criticized herself for the horrible mistake” (to make
the sentence as close as possible to the other sentences in the set)
243
• Item 23, cond 6: “worried”→ “said” (to align with the other sentences in the
set)
• Item 25, cond 1: “flustered” → “noisy” (to align with the other sentences in
the set)
• Item 28, cond 4 and 6. Remove “pretty” (in the original materials, conds
1,2,4,6 had “pretty” modifying the embedded noun, and conds 3,5 didn’t. But
the noun in conds 1,2 is “cheerleader”, and in 4-6 - “football players”. I decide
to keep the length of the NP to 3 words, thus, removing “pretty” in conds 4,6)
• Item 28. Added complementizers.
• Item 51: “refunded” → “refund” (typo)
• Item 88, Q: “... become popular with the teenagers?” → “... become popu-
lar?” (the sentence doesn’t mention teenagers)
244
Appendix E: Appendix: Experiment 2 fillers types
The following types of fillers were used:
1. With reflexives and NP antecedents
• Sentences either have an embedded complement clause or no embedding
at all;
• If there is a complement clause, the reflexive is inside it;
• The reflexive matches the grammatically accessible antecedent in some
sentences and mismatches it in gender in others (see Table E.2 for counts);
it always mismatches any other nouns in the sentences.
• Half of the items have masculine reflexives, half — feminine.
Example1: Everybody in the receiving team could see that the woman could
hardly stand by herself.
2. With reflexives and QP antecedent
Similar to the above, but with QP antecedents.
1The examples in this section were embedded in larger contexts, so they may sound unnatural
by themselves
245
Example: Interestingly, every politician seemed to portray himself as a trust-
worthy and absolutely honest person, according to the journalist.
3. Other
Three-sentence stories with no special constraints on them. Some of the sen-
tences included a mistake of one of the following types (see Table E.2 for
counts):
• Wrong verb form: After having unexpectedly losing her husband in a
car crash, Jane were utterly depressed.
• Verb number marking: Tracy were babysitting for a new family in the
neighborhood who had a very large and old house.
• Noun number marking: By the end of his studies he already spoke three
European language fluently and was taking lessons in Chinese.
246
Context1 Context2 Critical
Experimental sentences 24 24 24
6 6 6
Agreement attraction
6 6 6
6 6 6
3 3 3
Fillers, referential
3 3 3
6 6 6
6 6 6
3 3 3
Fillers, quantificational
3 3 3
6 6 6
18 18 18
Fillers, other 6 6 3
6 6 6
Table E.2: Experiment 2 stimuli types and counts.
White cells correspond to grammatical sentences, pink - to ungrammatical.
247
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