Is Referent Reintroduction More Vulnerable to Crosslinguistic Influence? An Analysis of Referential Choice among Japanese–English Bilingual Children

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Overall

The authors introduce the topic under study in an accessible yet academic way in the introduction of the paper arming readers with sufficient background knowledge to follow their argument. The literature review and specific introductions to Japanese and English lead the readers towards the RQs and the main thrust of the paper namely the nature of crosslinguistic influence in the grammar of bilingual schoolchildren.  An appropriate method of data elicitation was selected and is described in sufficient detail. Standard transcription conventions were adopted. The bar charts enable the data to be visualized and so readers do not have to get to grips with the numbers themselves. However, I personally would have preferred to see the numerical tables as well. The results are well described and at least one of the results should be of interest to readers familiar with this area since that result was unexpected.  This research fills a gap in the literature and is therefore worthy of publication.

Minor issues

1. Given that there are only 3 sources published in 2020 or later, it is difficult to call the literature review state-of-the-art. I recommend that the authors check the published literature. Assuming literacy in Japanese, a search in the Japanese language journals may be fruitful.

2. Reference layout

 

Line 547 and 572  – These are the continuations of the previous references.

Author Response

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Reviewer 2 Report

Comments and Suggestions for Authors

See comments within the attached pdf file by using Adobe Acrobat Reader DC.

Comments for author File: Comments.pdf

Comments on the Quality of English Language

The English overall is fine. 

Author Response

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Reviewer 3 Report

Comments and Suggestions for Authors

Brief summary:

The aim of this manuscript is to investigate crosslinguistic influence (CLI) in referring expressions in elicited narratives in 13 Japanese-English bilingual children across discourse contexts (referent introduction, reintroduction, and maintenance). It contributes to the existing literature on reference in bilingualism by adding another so far less studied language pair in this domain of research. The manuscript is clearly written and structured. The background section offers a concise summary of previous research on CLI and a brief outline of the crosslinguistic contrast between referring expressions in Japanese vs. English. The authors identify gaps in research and motivate their study appropriately. The manuscript falls within the scope of the journal and is expected to be of interest to its readership from the field of bilingualism. However, there are some issues that should be addressed before the manuscript can be considered for publication.

General concept comments

1) Background: The review on CLI is a bit too narrow and limited to the influential proposals of the early 2000s on the Interface Hypothesis and the structural ambiguity/overlap hypothesis. While these are undoubtedly important and constitute an adequate basis for this study's hypotheses, these proposals should be contextualised a bit more within more recent scholarship. For instance, there has been a lot of empirical evidence that CLI occurs both outside of interfaces and in the absence of ambiguity/overlap. At least some of these sources and studies should be acknowledged.

2) Method:

Participants:

- The sample size is very small (13 bilinguals, 7 Japanese monolinguals, 9 English monolinguals). This renders both the statistical procedures and the generalizability of results quite problematic. Especially for the monolingual control groups, I wonder why no more data was collected. In principle, it should be easier to recruit monolingual children. My recommendation would be to collect at least a sample of 20 participants per group.

- The bilingual group consists of both simultaneous and successive bilingual children. However, the overlap/ambiguity hypothesis in principle only applies to very early simultaneous bilinguals. Is it valid to include the successive bilinguals in the sample?

- There is very little background information on participants. Was a linguistic background questionnaire administered? Were any language proficiency tests administered in the two languages to gauge how balanced/dominant the children were? A table summarising the main demographic variables (gender, age range, mean and SDs), as well as proficiency levels, and - if possible - any language exposure/use/experience variables, should be included.

- Two different elicitation materials were used, a wordless picture book, and a video. Why were two types of materials selected and why these ones (The Frog Story, and a Chaplin Story) specifically? The authors should motivate these methodological decisions and also state hypotheses regarding the effeect of these different elicitation materials on their outcome variables of interest.

3) Results:

- The analysis relies on Chi-square tests and Mann-Whitney-U-tests. It is not explained why the authors use these tests and why they are suitable. In particular, I wonder why were no mixed-effects regression models carried out instead, which would enable taking into account subject- and item-related variability.

- Related to the above comment, and given the very small sample size, could the authors give an indication of the degree of individual variation within the sample? For instance, were there some bilingual children who diverged a lot from monolinguals, while others patterned with monolingual counterparts? These are all aspects that should be taken into account to gauge the generalizability of these findings.

- Presentation of descriptive results: The bar graphs should not be presented in 3D if this does not add any information value.

4) Discussion

- The obtained results on differences between the Frog Story and the video-elicited narrations are not discussed.

- The finding that bilinguals are overinformative and generally produce more NPs than monolinguals is interesting. Potential explanations for this result should be discussed in more depth and more discursively. In particular, one general point to consider is the difference between crosslinguistic influence and more general effects of bilingualism per se, i.e., that are not related to particular structural features of the languages involved. This aspect is not dealt with in the discussion and deserves further attention.

- Section 5.2 (3rd paragraph) only mentions one other study with similar findings and ventures one potential explanation, which is interesting, but quite speculative ("enhanced sensitivity to the ambiguity of the referent"). Moreover, this hypothesis could easily be tested with a follow-up analysis (see my specific comments below) and I wonder why this was not performed to strengthen the argument.

- Generally, potential alternative explanations of the results are not dealt with sufficiently for a discussion section.

5) Backmatter:

- There is no statement of data availability and ethics provided.

- Was informed consent sought from parents? Was ethical clearance obtained from the ethics committee of the institution?

 

Specific comments

- p. 2, sect. 1.2., l. 91ff: The Separate Development Hypothesis for simultaneous bilingual is indeed maintained by many, although by no means, by all scholars. The way it is presented in the manuscript makes it seem as if it is a quite uncontroversial fact. I would suggest contextualising this claim more broadly, including the controversy in scholarship regarding this point, and also add some more recent references (the ones mentioned are from the 1980s and 90s, so fairly outdated); idem for the Interface Hypothesis & overlap hypothesis (see general comments above). 

- p. 5, sect. 3.1 Participants: Why were monolingual English children recruited from a "local Japanese weekend language school"? Or does this refer to the bilingual sample?

- p. 6, sect. 3.2 Data collection:

l. 263-64: Why was the Frog Story always followed by the Chaplin story instead of counterbalancing to avoid order effects? Was there a particular reason for this order? Could the lack of counterbalancing perhaps explain some of the differences in results for the 2 stories as order/training effects?

l. 264-65: Similary to the above point, I wonder whether having children determine the ordering of languages "to minimize tension" might have resulted in effects of training and/or fatigue, especially if the more dominant language was, presumably, chosen mostly to start with. Why was the order not counterbalanced instead to control for these effects?

- p. 6, sect. 3.3, l. 271: "We utilized utterance as a unit of analysis": This choice should be motivated and a definition and example of what counted as an "utterance" should be provided, along with identifying criteria.

- p. 8, Figure 1: The legend for what the colours stand for is missing.

- p. 11, l. 442 (and other places): "by both lingual group" - I'm unfamiliar with this usage of "lingual" without the addition of "bi-/multi-/mono-". This should be checked for terminology/correctness in English. 

- p. 12, l. 449: Spelling of reference should be Hickmann et al. (1996), not "Hickman".

- p. 12, l. 466-68: "..bilinguals in this study are mildly dominant in Japanese..this finding indicated that language dominance did not play a major role": I find it problematic to state this as a fact and reach this conclusion as no measures of dominance are provided in the study. Are there any measures that could be reported (see earlier comments on Participants) to uphold this argument?

- p. 12, l. 468-70: "...accumulated evidence to support the view that CLI is also observed in older children (e.g., Chen & Lei, 2012; Serratrice, 2007).": Some more recent sources, also from different linguistic domains, could be added here to support the argument, such as for instance Bosch & Unsworth, 2021 (doi: http//doi.org/10.1075/lab.18103.bos) for morphosyntax, and Engemann, 2022 for semantics, DOI: https://doi.org/10.1017/S1366728921000298

- p. 12, l. 492 ff: "...a totally different analysis involves considering the prominent use of NPs...as ...enhanced sensitivity to the ambiguity of the referent": This is an interesting argument, but then we should only expect reinforced used of NPs in those contexts in which the referent is in fact ambiguous. This could be easily verified by a follow-up analysis comparing NPs provided by bilinguals and monolinguals in ambiguous vs. non-ambiguous referent contexts. I suggest that this analysis is done to strengthen the authors' argument.

- p. 12, l. 497 ff.: "A more detailed analysis of the relationship between the levels of activation/accessibility and the referential forms might further reveal the bilinguals'unique strategies ...": See comment above.

- p. 13., l. 502 ff.: "...proposed that qualitative analysis is required to investigate the nature of referential choice...": See above comments. This need not necessarily be a qualitative analysis though. This follow-up analysis should be added.

 

 

 

 

 

Comments on the Quality of English Language

The English is mostly correct, with some occasional errors and typos and some unusual use of terms, such as "lingual" (see specific comments above). I recommend proofreading by an English native speaker.

Author Response

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Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

I appreciate the authors careful revision of the paper with detailed replies to the comments. Please view new comments within the attached pdf file.

Comments for author File: Comments.pdf

Author Response

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Reviewer 3 Report

Comments and Suggestions for Authors

The revisions implemented have improved the manuscript considerably. Most of the issues/concerns with the previous versions have been addressed or explained sufficiently. As a result, the theoretical background on CLI (interfaces/ambiguity) is now much richer and more nuanced, also taking into account more recent scholarship. Moreover, some of the methodological questions, regarding the lack of counterbalancing of language sessions and elicitation materials, have now been explicitly addressed and explained in the paper, along with a discussion of their potential limitations.

As for the small sample size, the authors' argument regarding the bilingual sample is a compelling one that can be accepted given the difficulty of recruiting this specific language pair. However, with regard to the monolingual groups, it is less convincing. At least the Japanese monolingual sample (n=7) could have been increased a little. Nonetheless, the authors explicitly acknowledge the limitations that come with a small sample size, so I would not want this to impede publication.

A few remaining points to be addressed:

- proficiency measures: the authors have added a section on children's SI (subordination index), which was measured based on the actual narrative production, i.e., the main task of this study. For this reason, it would have been preferable to have an independent measure of proficiency, whether standardized or self-rated (by parents). I believe this should at least be mentioned in the paper.

- l. 304-6 (3.1 Participants): Some of the children categorised as "monolingual English" were recruited from an English-speaking setting in the US, while some were recruited from Japan where they also learnt Japanese at school. Concerns could be raised about how justifiable it is to put both of them in the same category, given that the latter group will presumably receive at least some exposure to Japanese also outside their weekend school and given what we know about the effects of residing in a linguistically diverse context (e.g., Bice & Kroll, 2019). What about daycare/schooling - was all of this in English? To alleviate these concerns, could the authors report how long the latter group (residing in Japan) had spent in Japan at the time of testing and comment on their exposure to Japanese? If they have already resided in Japan for a while and/or have received regular input, it might be cautious to exclude these participants from the "monolingual English" group or at least show that these participants do not differ in their linguistic patterns of interest from the other monolingual English children.

- The Frog Story is spelt with capital letters in the original paragraphs, but not in the revised/new ones. This should be made consistent.

- typo l. 546: "there were no statistical difference" --> pluralize noun: "..differences"

- spelling and pronouns of "Engermann" (l. 186 2x; l. 692): correct to "Engemann" and change pronouns to "she/her" (currently "he", l. 187)

- typo l. 771: "out findings" --> "our findings"

 

 

Author Response

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