Predictions about the Cognitive Consequences of Language Switching on Executive Functioning Inspired by the Adaptive Control Hypothesis Fail More Often than Not

Round 1

Reviewer 1 Report

Thank you for the opportunity to review this manuscript. I do not intend this review to be taken as a defense of Green and Abutalebi’s (2013) Adaptive Control Hypothesis (ACH) nor as a direct critique of studies discussed on which the Paap & Mason’s (P&M) argument is based. Instead, I intend to raise concerns over P&M’s overall approach and some of the claims made that seriously undermine the research enterprise of bilingualism, and the fundamentals of science more broadly.

P&M argue against two hypotheses. The first claims that “dual-language contexts” (DLCs) should enhance domain-general EFs more than “single-language contexts” (SLCs). The second, that bilinguals in “dense code-switching contexts” (DCSs), should show no benefits to EFs on the assumption that code-switching eschews the need for the development and maintenance of cognitive control. To this end, P&M synthesize multiple studies, concluding that the evidence gathered thus far is inconsistent, weak, and overall detrimental to our understanding of how distinct dimensions of bilingualism relate to EF performance.

As P&M themselves acknowledge, the ACH is arguably one of, if not, the most influential paper(s) on bilingual language control published in the last decade. However, the assessment of scientific theories/hypotheses is void without an established community agreement as to what constitutes appropriate evidence for such theories and their derived predictions. Critically, the process of establishing agreement in the scientific community is important as it charts new paths of understanding with a diversification in the application of ideas, methods, and procedures. Below I elaborate on this issue to illustrate.

P&M have rightfully brought attention to several challenges in testing the predictions of the ACH, most notably the limitations involved in identifying “pure” cases of DLC, SLC, and DCS experiences or in categorizing individuals as belonging to one or another based on their retrospective self-reports of language use. Yet, by focusing exclusively on the ACH-inspired research set to test predictions about bilingual advantages in EFs, P&M assume a degree of intersubjective agreement or consensus among researchers regarding how to define or identify the population as well as the communicative demands of the interactional context in question. As evidenced in the array of research approaches reviewed, studies often rely on different criteria to characterize interactional experiences (including measures of tendency to engage in a particular interactional context), and they widely differ in their interpretation of what their measures may possibly reflect (e.g., interference control v response inhibition). This does not indicate a problem with the research in itself; rather, this reveals the natural process of science through which we gain new insights and ask new questions that better capture effects in the data. Further, the assumption that inconsistent findings are necessarily contradictory or problematic mischaracterizes the community-value of these contributions and disregards the process of identifying boundary conditions, which the field has actively begun to identify in recent years (in large part thanks to the ideas conveyed in the ACH).

Second, P&M have presented conclusive arguments without considering the full breadth of the evidence to appropriately contextualize the findings in question. Take for example Kang and Lust (2019), who examined bilingual children in Singapore where CS occurs pervasively and found that CS experience did not significantly predict EF performance. Similarly, Pot, Keijzer, and de Bot (2018) examined bilingual older adults in the Netherlands and found that codeswitching experience did not enhance EF performance. There are also studies showing how bilinguals may adapt their cognitive control engagement under conditions that reflect the demands of a DLC (Jiao et al., 2019, 2020; Wu & Thierry, 2013), none of which are mentioned in the manuscript despite these effects being replicated across different studies with different populations. The point is not to undermine the findings reported in Hofweber et al. (2016, 2020), but instead to treat inconsistent results across groups/studies as an opportunity to make inferences about the generalizability of such findings to different settings. Put briefly, predictions about the cognitive consequences on bilingualism cannot be refuted conclusively without a more nuanced understanding of the boundary conditions.

Related to this point, P&M assess consistency across groups/studies based on performance on aggregate EF measures. Yet, simply asking “Does DLC lead to better EF?” and “Are there no benefits to EF from DCS?” disregards the complexity of the phenomena at hand. Adaptive effects may be achieved through degeneracy whereby individuals develop different strategies to perform similar functions. In other words, two groups may draw on cognitive resources differently while still achieving similar outcomes for a given measure. This surely warrants further consideration. Furthermore, in the main-effect reanalysis of the Paap studies, individuals within each language group are assumed to represent the same underlying population, despite having remarkably different language backgrounds and/or community practices. While P&M provide detailed criteria for grouping individuals into these categories, they fail to characterize individuals’ behavioral ecology of language use while also accounting for the historical and sociocultural circumstances that shape the linguistic practices of the community (i.e., the San Francisco Bay Area). In making such assumptions, the reported findings may be a result of an aggregate of different phenotypes with different profiles of performance.

P&M put forward that the ACH-inspired hypotheses in question do not advance our understanding of bilingualism. Yet, in doing so, they fail to acknowledge how the research discussed has contributed to an evolving understanding of the consequences of bilingualism. A scant understanding of the boundary conditions of previously reported findings coupled with poorly framed questions lead to unwarranted conclusions.

Author Response

Reviewer 1.  Thank you for the opportunity to review this manuscript. I do not intend this review to be taken as a defense of Green and Abutalebi’s (2013) Adaptive Control Hypothesis (ACH) nor as a direct critique of studies discussed on which the Paap & Mason’s (P&M) argument is based. Instead, I intend to raise concerns over P&M’s overall approach and some of the claims made that seriously undermine the research enterprise of bilingualism, and the fundamentals of science more broadly.

Response.  This concern is excessive hyperbole and signals that this reviewer lacks respect and professionalism. 

 

Reviewer 1.  P&M argue against two hypotheses. The first claims that “dual-language contexts” (DLCs) should enhance domain-general EFs more than “single-language contexts” (SLCs). The second, that bilinguals in “dense code-switching contexts” (DCSs), should show no benefits to EFs on the assumption that code-switching eschews the need for the development and maintenance of cognitive control. To this end, P&M synthesize multiple studies, concluding that the evidence gathered thus far is inconsistent, weak, and overall detrimental to our understanding of how distinct dimensions of bilingualism relate to EF performance.

Response.  This is a reasonable summary of two of the hypotheses central to our manuscript.  However, characterizing the outcomes that failed to confirm the prediction as “detrimental to our understanding” of bilingualism is entirely the reviewer’s characterization, not ours. 

 

Reviewer 1. As P&M themselves acknowledge, the ACH is arguably one of, if not, the most influential paper(s) on bilingual language control published in the last decade. However, the assessment of scientific theories/hypotheses is void without an established community agreement as to what constitutes appropriate evidence for such theories and their derived predictions. Critically, the process of establishing agreement in the scientific community is important as it charts new paths of understanding with a diversification in the application of ideas, methods, and procedures. Below I elaborate on this issue to illustrate.

Response. We did not generate the predictions based on our interpretation of the ACH. The predictions we test were proposed and tested in the four major studies that we reviewed.  Those studies were not only peer reviewed, but appear in some of our most prestigious journals in psychological science.   Our contribution builds on this recent work and indeed our results are quite consistent. 

 

 

Reviewer 1.  P&M have rightfully brought attention to several challenges in testing the predictions of the ACH, most notably the limitations involved in identifying “pure” cases of DLC, SLC, and DCS experiences or in categorizing individuals as belonging to one or another based on their retrospective self-reports of language use. Yet, by focusing exclusively on the ACH-inspired research set to test predictions about bilingual advantages in EFs, P&M assume a degree of intersubjective agreement or consensus among researchers regarding how to define or identify the population as well as the communicative demands of the interactional context in question. As evidenced in the array of research approaches reviewed, studies often rely on different criteria to characterize interactional experiences (including measures of tendency to engage in a particular interactional context), and they widely differ in their interpretation of what their measures may possibly reflect (e.g., interference control v response inhibition). This does not indicate a problem with the research in itself; rather, this reveals the natural process of science through which we gain new insights and ask new questions that better capture effects in the data. Further, the assumption that inconsistent findings are necessarily contradictory or problematic mischaracterizes the community-value of these contributions and disregards the process of identifying boundary conditions, which the field has actively begun to identify in recent years (in large part thanks to the ideas conveyed in the ACH).

 

Response. It is difficult to discern what the reviewer would like us to revise.  One of the main purposes of our research was to describe the various methods of measuring different interactional experiences, in  which we carefully reported the strengths and weaknesses of each in the context of the studies that use the various approaches.  Likewise, we discuss the variety of hypotheses regarding control processes that may be strengthened through bilingual language control and the best methods we have for evaluating those hypotheses.  For example, a good way of evaluating hypothesis about cognitive control mechanisms is through latent variable analyses and it turns out that some constructs have more support than others.  The work of Rey-Mermet, Gade, & Oberauer (2018) and Paap, Anders-Jefferson, Mikulinsky, Masuda,& Mason (2019) directly challenge the hypothesis that there exists a distinction between domain-general inhibitory control mechanisms for interference control versus response inhibition.  Falsifying hypotheses has a long and productive tradition in science and it is a problem when researchers do not take null results seriously.  What we need is a solution to at least a part of the puzzle. That is, hypotheses must be advanced that bilingual experiences A, B, and C constitute a set of sufficient conditions for consistently producing advantages on specific measures (X, Y, & Z) of cognitive control that will replicate across laboratories. 

 

Reviewer 1.  Second, P&M have presented conclusive arguments without considering the full breadth of the evidence to appropriately contextualize the findings in question. Take for example Kang and Lust (2019), who examined bilingual children in Singapore where CS occurs pervasively and found that CS experience did not significantly predict EF performance.

Response.  We thank the reviewer for this pointer to Kang & Lust (2019) as the article had escaped our attention.  We have added a description and commentary in the section on Dense Code Switching (DCS).  The results of Kang & Lust are consistent with the hypothesis that some forms of DCS are performed in an open-control mode that does not recruit nor enhance domain-general inhibitory control.  {Of course, this needs to be considered in the fuller context that contrary to the predictions of the ACH, Dual Language Context (DLC) also produces the same null result as DCS.}

 

 

Reviewer 1.  Similarly, Pot, Keijzer, and de Bot (2018) examined bilingual older adults in the Netherlands and found that codeswitching experience did not enhance EF performance.

Response.  An earlier version of this manuscript devoted a section to the Pot et al. study and we have gladly reinstated it.  We removed this study in order to reduce the length of the manuscript.  Please see the revised material. We would like to point out here that Pot et al. did not empirically separate DCS from DLC and their study does not make an empirical contribution to the DCS debate.  It is not the case that Pot et al. “found that codeswitching experience did not enhance EF performance” given that they had no measure of codeswitching. 

             

Reviewer 1.  There are also studies showing how bilinguals may adapt their cognitive control engagement under conditions that reflect the demands of a DLC (Jiao et al., 2019, 2020; Wu & Thierry, 2013), none of which are mentioned in the manuscript despite these effects being replicated across different studies with different populations. The point is not to undermine the findings reported in Hofweber et al. (2016, 2020), but instead to treat inconsistent results across groups/studies as an opportunity to make inferences about the generalizability of such findings to different settings. Put briefly, predictions about the cognitive consequences on bilingualism cannot be refuted conclusively without a more nuanced understanding of the boundary conditions.

Response.  An earlier version of our manuscript included a lengthy section on the temporary effects of mixing languages as first reported by Wu & Thierry.  We have reinstated this section under the heading “Does Language Mixing (a transient Dual Language Context) Trigger Better General EF?”.  That section considers the studies by Timmer, Wodniecka, & Costa (2021); Yang et al. (2018); Jiao et al. (2019, 2020); and Adler, Kroff, & Novick, (2020). 

 

Reviewer 1.  Related to this point, P&M assess consistency across groups/studies based on performance on aggregate EF measures. Yet, simply asking “Does DLC lead to better EF?” and “Are there no benefits to EF from DCS?” disregards the complexity of the phenomena at hand. Adaptive effects may be achieved through degeneracy whereby individuals develop different strategies to perform similar functions. In other words, two groups may draw on cognitive resources differently while still achieving similar outcomes for a given measure. This surely warrants further consideration. Furthermore, in the main-effect reanalysis of the Paap studies, individuals within each language group are assumed to represent the same underlying population, despite having remarkably different language backgrounds and/or community practices. While P&M provide detailed criteria for grouping individuals into these categories, they fail to characterize individuals’ behavioral ecology of language use while also accounting for the historical and sociocultural circumstances that shape the linguistic practices of the community (i.e., the San Francisco Bay Area). In making such assumptions, the reported findings may be a result of an aggregate of different phenotypes with different profiles of performance.

Response.  We appreciate these points raised by the revewer, as they are importnt ones. In establishing our criteria we took into account all the facets of bilingualism discussed by Green and Abutalebi when they laid out the ACH.  For example, the bilinguals we identified as having DLC tendencies had high language-use entropy across seven interactional contexts, relatively high L2 proficiency, did not frequently code switch within utterances, but did switch languages many times a day.  Now it is true that some of the bilinguals identified as belonging to our DLC group spoke Tagalog and English in Daly City while others spoke Spanish and English in the Mission, but they all fit the criteria that were provided by Green and Abutalebi. 

 

Reviewer 1.  P&M put forward that the ACH-inspired hypotheses in question do not advance our understanding of bilingualism. Yet, in doing so, they fail to acknowledge how the research discussed has contributed to an evolving understanding of the consequences of bilingualism. A scant understanding of the boundary conditions of previously reported findings coupled with poorly framed questions lead to unwarranted conclusions.

Response.  We have quoted the authors of the ACH and the authors of several published articles regarding the predictions derived from the ACH.  We did not make up these predictions from our interpretation of the ACH, we simply borrowed them from the relevant literature.  If the reviewer identified for us specific “boundary conditions” that we failed to take into account, we would gladly respond to a specific omission.

Reviewer 2 Report

The manuscript entitled “Predictions about the Cognitive Consequences of Language Switching on Executive Functioning Inspired by the Adaptive Control Hypothesis Fail More Often Than Not” reviews four studies conducted between 2016 and 2020, and it provides new analyses for two studies previously published by the authors' group. In addition, the work presents broader background information relevant to the Adaptive Control Hypothesis that includes the neuroanatomy of bilingualism and findings from research using event-related potentials. While the review can contribute to the ongoing debate on the impact of different language switching contexts on executive functioning, the manuscript requires major revisions.

1. The six main studies discussed in the manuscript (four reviewed, two with new analyses) involved young adults. It is well known that the bilingual advantage on executive function tasks has produced inconsistent results in this age group. For example, Bialystok et al. (2005) used a Simon task to examine reaction times in fours age groups of bilinguals and monolinguals: children, young adults, middle-aged adults, and older adults. They found that the bilinguals in three of the four groups had faster reaction times when compared with monolinguals from the same age groups. The only age group that did not show any bilingual advantage was young adults. The finding of no difference in young adults has been replicated multiple times, including several meta-analyses (e.g., Paap & Greenberg 2013). This information should be added to the Introduction and the Conclusion. In this context, it is not surprising that there were no significant differences on executive function tests between bilinguals exposed to different language switching contexts in the six studies. I also suggest that the authors explicitly say in the title that their work is based on studies with young adults.
2. 3, Organization of the Article: this section could be removed if the overall organization of the manuscript was improved. One way would be to extend the Introduction (see comment 4), then have a Literature Review section, followed by the New Analyses, General Discussion, Limitations (see comment 15), and Conclusion.
3. 3, paragraph 4, line 123: it may not be apparent to the reader what the “far transfer” is. Please elaborate when the far transfer is mentioned the first time in the text.
4. The section entitled “The Neuroscience of the ACH” should appear after the Introduction and before the “Far Transfer Predictions” section.
5. The section on the neuroanatomy of bilingualism contains errors (p. 12, paragraph 2, lines 577-579): the inferior frontal gyrus is not part of the inferior parietal lobe; it is part of the prefrontal cortex. The inferior parietal lobule and the supramarginal gyrus are presented as separate areas, while the supramarginal gyrus is part of the inferior parietal lobule.
6. Later in the same section, the authors say “[…] the IPL involves working memory and serves as a goal maintenance function […]” (p. 581-582). This sentence is poorly worded. Brain regions do not involve processes and functions; they are involved in them. The authors probably meant to say that the IPL subserves working memory and is involved in goal maintenance.
7. 12, paragraph 1, lines 576-583: please provide citations and references for all the areas and functions.
8. 12, paragraph 5, lines 611-614: please specify the structural changes and their directionality (e.g., modulations in thickness, volume, and/or surface area).
9. 13, paragraph 2, lines 640-642. If what the authors speculate was the case (i.e., the language processing system taking over functions from the domain-general executive system), how would one interpret cognitive reserve in older bilinguals with dementia? The finding has been supported by a rich line of research, including recent meta-analyses (Bialystok et al. 2007; Alladi et al. 2013; Anderson et al. 2020; Brini et al. 2020).
10. 13, paragraph 3, lines 649-651: the text sounds confusing. The expansion-partial renormalization hypothesis assumes neural renormalization to baseline levels in the context of continuous practice, not the lack of it. Yet, this is not what the second sentence of paragraph 3 says right now.
11. 14, paragraph 2, lines 677-870: the field has started to appreciate the complexity of the bilingual experience. However, relatively few studies have accounted for factors, such as the age of language acquisition, the amount of language exposure, proficiency, and language switching patterns. Significant findings could have been washed off in studies that did not examine these factors (e.g., Dick et al. 2019). Therefore, I cannot agree with the authors that "it is unlikely that differences in structure can accurately predict differences in bilingual language control […]". Such associations (or their absence) remain to be determined.
12. 15, New Analyses of Paap et al. (2019) and Paap et al. (2020): it was unclear what was new and what was not in this section. It was also not clear if the sentence “It may be worthwhile to look at the complete array of language-use measures for each bilingual […]” was a suggestion for future research on an actual goal of the manuscript. Please provide a paragraph listing what was done in the two prior studies (including the methods) and what is new about the current analyses. Since the section on the new analyses is lengthy, the authors may want to focus on what is new and shorten the description of the two previous studies to avoid duplication with their previous research.
13. 27, paragraph 1: I suggest making a more general introduction that encompasses the four reviewed studies, not just the two with the new analyses.
14. 28, paragraph 3, lines 1014-1024: it is unnecessary to summarize the reanalysis in the limitations section. Please remove the summary.
15. The Limitations should appear before the Conclusion. The section should be edited to minimize wordiness.

Minor comments:

1. Sloppy text editing is frequent and requires fixing.
2. There are numerous instances of inconsistent spacing between sentences (between 1 to 3 spaces).
3. Remove excessive spacing between words throughout the manuscript, e.g., 13, paragraph 4, line 649 (an extra space between “restructuring” and “maintained”); line 650 (an extra space between “structure,” and “a”).
4. Names of the group from Poland are misspelled: "Kamala" for "Kalamala”, or – to be more precise – Kałamała) (p. 5, paragraph 2, line 211), and “Szewcyk” for “Szewczyk” (p. 4, paragraph 1, line 153, and the references).
5. 2, lines 60-61: the word "predict[ed]" was used three times. Please use synonyms instead.
6. 2, paragraph 4: the beginning of the sentence is missing. The sentence now starts with “and we want to alleviate”.
7. 2, paragraph 4, lines 86-89: please paraphrase the apparent quote. The authors admit that the quoted passage is not an exact quote by stating “A sample concern goes something like this”. Brain Sciences requires a more scientific and concrete style.
8. 7, paragraph 2, line 309: the line has the same indent as the beginning of a paragraph above.
9. 10, paragraph 4, line 478, and p. 11, paragraph 4, line 540: Remove the dots at the beginning of sentences.
10. 10, paragraph 4, lines 478-480: the summary should be moved to the end of the section it summarizes.
11. 16, table 1: the reference for the MINT is required.
12. 22, paragraph 2, lines 899-900: “Eliminating all the suspense from the narrative of the results” is unnecessary and can be removed.
13. 28, paragraph 2: looks like a note to the Editor. Please remove it. The Limitations section is required, though.
14. The name of the last author (Anders-Jefferson) appears on the Brain Sciences website but not in the manuscript. Please resolve this ambiguity.

Author Response

1. Reviewer 2. The six main studies discussed in the manuscript (four reviewed, two with new analyses) involved young adults. It is well known that the bilingual advantage on executive function tasks has produced inconsistent results in this age group. For example, Bialystok et al. (2005) used a Simon task to examine reaction times in fours age groups of bilinguals and monolinguals: children, young adults, middle-aged adults, and older adults. They found that the bilinguals in three of the four groups had faster reaction times when compared with monolinguals from the same age groups. The only age group that did not show any bilingual advantage was young adults. The finding of no difference in young adults has been replicated multiple times, including several meta-analyses (e.g., Paap & Greenberg 2013). This information should be added to the Introduction and the Conclusion. In this context, it is not surprising that there were no significant differences on executive function tests between bilinguals exposed to different language switching contexts in the six studies. I also suggest that the authors explicitly say in the title that their work is based on studies with young adults.

Response.  The reviewer is correct that young adults do not show consistent bilingual advantages in EF.  However, another critical component to the argument that the reviewer is trying to make is that recent meta-analyses show the same thing for children and older adults!  Researchers should not rely on a single study to conclude that “the only age group that did not show any bilingual advantage was young adults”.  As described in detail below the large-scale and recent meta-analyses show no advantages at any age.

            These meta-analyses converge and report overall effect sizes for all components of EF that are very small and not distinguishable from zero when corrected for publication bias (von Bastian, de Simoni, Kane, Carruth, & Miyake, 2017;  Lehtonen, Soveri, Laine, Järvenpää1, de Bruin. & Antfolk, 2018; Donnelly, Brooks, & Homer, 2019; Paap, 2019; Gennerud, ten Braak, Reikeras, Donolato, and Melby-Lervåg, 2020; Monnier, Boiche, Armandon, Baudoin, & Bellocchi, 2021; and Lowe, Cho, Goldsmith, & Morton, 2021).  These meta-analyses include tests for many different moderators including different types of bilingual experience, different ages, and different measures of EF.  The meta-analysis by Lowe, et al. (2021) covers ten components of EF including executive attention, response inhibition, working memory, and planning.  It provides an excellent complement to Lehtonen et al. because it restricts its focus to children between the ages of 3 and 17.  The selection criteria yielded 149 studies and 1,194 effect sizes and provided very little support for a bilingual advantage in EF.  For the general construct of EF the overall effect size on EF was very small, g = .08, 95% CI [-0.02, 0.14].  When the results were corrected for publication bias, the overall effect was now slightly negative, g = -.04, 95% CI = [-.13, +.05].   Study quality in this domain was disappointingly poor.  In all, only 41 of 159 studies reported matching monolinguals and bilinguals on at least a single variable.  Similarly, only 32 of 159 studies reported using equivalence testing to ensure that groups were comparable on at least one demographic variable.  Using study quality as a potential moderator was unique within this set of meta-analyses.  It was a composite measure based on the AXIS scale (Downes et al., 2016) and also on whether the original study ruled out specific confounds by measuring factors such as age, nonverbal IQ, gender, and SES.  The small effects of bilingualism that appeared for some components of EF were explained by poor study quality:  as effect-size magnitude decreased, study quality increased!  It is very difficult to design and implement high quality designs in order to test the bilingual advantage in EF hypothesis.  It seems that better controls make the advantage more elusive rather more easily captured.  Lowe et al. (2021) concluded that bilingual advantages in children are not related to language status, but a variety of unmeasured and uncontrolled factors.   Furthermore, the small positive effects are driven by just one laboratory, the Bialystok lab at York University.   Another meta-analysis focused exclusively on children aged 18 years and under was conducted by Gennerud, et al. (2020).  The components of EF examined were inhibition, attention, switching, monitoring, working memory, and planning. Their results showed that when EF was measured as an overall construct the effect size of g = 0.06, 95% CI [0.03, 0.12] (based on 583 effect sizes) was negligible. When the results were corrected for bias using PET the effect size crossed over onto negative territory, g = -0.16 (95% CI [-0.32, 0.01].  Gennerud et al. also sought to determine the degree to which overall EF was moderated by sample characteristics such as the degree of balanced bilingualism, the level of L2 skills, SES, fluid intelligence, age, AoA, and origin as well as moderators related to methodology, such as sample size, publication year, and lab.  The two significant moderators showed that bilingual advantages were restricted to middle-class SES children and to one specific lab.  The lab at York University reported a positive significant effect in favor of bilingual children (g = 0.17, 95% CI [0.07, 0.26), while overall the other labs did not show a significant effect (g = 0.01, 95% CI [-0.05, 0.08).  With respect to SES Gennerud et al. point out that SES was usually estimated only from parents’ education and that it is rarely a cause, but more often a proxy for something else. 

Are there bilingual advantages in inhibitory control in older adults? Paap, Anders-Jefferson, Mason, & Zimiga, 2018) reported a supplementary analysis of the Paap (2019) database of published studies testing for advantages in inhibitory control.   The analysis selected studies with participants older than 60. There were 19 studies of older adults and 14 were variants of the Simon task.  The critical bottom-line is that 17 of the 19 showed null resulted and the mean bilingual advantage was +8.0 ms, t(18) = 1.75, p = .10 without any correction for publication bias.  Furthermore, neither Lehtonen et al, nor Donnelly et al., found that age was a mediator of the bilingual advantage.

            In a direct test of the ‘ceiling’ hypothesis Paap et al. (2014) reported that for a group of eight young adults, the mean RTs on both congruent and incongruent trials of a flanker task decreased substantially by about 100 ms over the course of 20 daily sessions. The magnitude of the flanker effect itself also decreased by about 30ms. The results demonstrate that the ‘experience’ of practicing the same task can ‘move an entire group to a significantly faster time’. These young adults were not at a performance ceiling. Thus, if bilinguals experience ubiquitous practice of general EF during their everyday language control they should show better interference control in a first session because neither group is at a performance ceiling.

 

2. Reviewer 2.  Organization of the Article: this section could be removed if the overall organization of the manuscript was improved. One way would be to extend the Introduction (see comment 4), then have a Literature Review section, followed by the New Analyses, General Discussion, Limitations (see comment 15), and Conclusion.

Response.  OK.  This section was added in response to a suggestion by a different reviewer.  We think it helps in providing clear signposts for a long article, but we have removed the heading and revised or deleted various parts of the paragraph.

 

3. Reviewer 2. paragraph 4, line 123: it may not be apparent to the reader what the “far transfer” is. Please elaborate when the far transfer is mentioned the first time in the text.

Response.  The first mention of “far transfer” clarifies that it refers to transfer to nonverbal tests of domain-general EF. 

 

4. Reviewer 2. The section entitled “The Neuroscience of the ACH” should appear after the Introduction and before the “Far Transfer Predictions” section.

Response.  OK, we have moved this section as recommended.

 

5. Reviewer 2. The section on the neuroanatomy of bilingualism contains errors (p. 12, paragraph 2, lines 577-579): the inferior frontal gyrus is not part of the inferior parietal lobe; it is part of the prefrontal cortex. The inferior parietal lobule and the supramarginal gyrus are presented as separate areas, while the supramarginal gyrus is part of the inferior parietal lobule. 
6. Later in the same section, the authors say “[…] the IPL involves working memory and serves as a goal maintenance function […]” (p. 581-582). This sentence is poorly worded. Brain regions do not involve processes and functions; they are involved in them. The authors probably meant to say that the IPL subserves working memory and is involved in goal maintenance.

Response to 5&6.  Thank you for these corrections and suggestions.  This paragraph has been rewritten.

 

7. Reviewer 2. p. 12, paragraph 1, lines 576-583: please provide citations and references for all the areas and functions.
8. Reviewer 2. lines 611-614: please specify the structural changes and their directionality (e.g., modulations in thickness, volume, and/or surface area).

Response to 7&8.  In our view this would be excessive detail.  For example, the reviewer is asking us to recapitulate the review of 17 studies conducted by Garcia-Penton et al.  It took Garcia-Penton 2 tables and 13 pages in an appendix to provide the details requested by Reviewer 2.  Alternatively, we already offer the reader a summary in lines 615-623.

 

9. Reviewer 2.  paragraph 2, lines 640-642. If what the authors speculate was the case (i.e., the language processing system taking over functions from the domain-general executive system), how would one interpret cognitive reserve in older bilinguals with dementia? The finding has been supported by a rich line of research, including recent meta-analyses (Bialystok et al. 2007; Alladi et al. 2013; Anderson et al. 2020; Brini et al. 2020).

Response.  Again, our view of the relevant literature seems to be broader and different from that of Reviewer 2.  As Paap, Johnson, and Sawi (2017) noted in their Cortex target article and many others have echoed (e.g., Watson, Manly, & Zahodne, 2019) this is another area of controversy that is far from settled.  The first studies on the possible effects of bilingualism on cognitive decline used retrospective reports of patients at memory clinics and showed that bilingualism delayed the onset of symptoms or diagnosis by several years. Some of these studies confounded bilingualism with immigrant status (Bialystok, Craik, & Freedman, 2007), while another found bilingual benefits within immigrant samples, but not between native samples (Chertkow et al., 2010). Immigrant status is important because it is associated with higher intelligence that, in turn, is associated with delays in dementia onset (Fuller-Thomson, 2015). Furthermore, the four studies that have used a prospective cohort design following individuals without dementia at baseline have all found no significant effects of bilingualism, and the trend in three of those favors the monolinguals (Crane et al., 2009; Sanders et al., 2012; Lawton et al., 2015). Fuller-Thomson (2015) suggests that the longitudinal design is less open to biases in sampling, measurement, and publication. If the prospective studies are weighted more heavily than those using retrospective reports, there is little evidence that bilingualism protects against cognitive decline. This is an important question because there are no effective drugs for preventing or slowing the pace of dementia.  Researchers at the BCBL put the intriguing potential for bilingualism as a treatment to a direct test (Ramos, Fernández García, Antón, Casaponsa, & Duñabeitia, 2016) by having 26 elderly (mean age = 69 years) Spanish monolinguals acquire Basque as an L2 for 5.5 hours per week for 8 months.  These individuals were matched in age, cognitive state, and education to a control group.  The results were disappointing as the two groups did not differ in switch costs (an excellent measure of the shifting component of EF) in either the pretest or posttest.  Furthermore, the obtained Bayes Factor of 3.2 indicates that null hypothesis is substantially more probable than the alternative.

 

10. Reviewer 2. paragraph 3, lines 649-651: the text sounds confusing. The expansion-partial renormalization hypothesis assumes neural renormalization to baseline levels in the context of continuous practice, not the lack of it. Yet, this is not what the second sentence of paragraph 3 says right now.

Response.  Reviewer 2 is correct about the hypothesis and we have fixed the errant sentence

 

11. Reviewer 2. 14, paragraph 2, lines 677-870: the field has started to appreciate the complexity of the bilingual experience. However, relatively few studies have accounted for factors, such as the age of language acquisition, the amount of language exposure, proficiency, and language switching patterns. Significant findings could have been washed off in studies that did not examine these factors (e.g., Dick et al. 2019). Therefore, I cannot agree with the authors that "it is unlikely that differences in structure can accurately predict differences in bilingual language control […]". Such associations (or their absence) remain to be determined.

Response.  We agree that the Dick et al. mega-study has sparse information about the proficiency, acquisition, and use of those identified as bilinguals, but this is relatively rare.  I think Reviewer 2 is wrong in suggesting that “relatively few studies have accounted for AoA, amount of exposure, proficiency, switching patterns, etc.”  I reviewed more than 40 manuscripts on this topic in the last year plus a volume with more than 20 contributors.  Nearly all solicited rich information about their bilinguals, and, in fact, this issue was the focus of many of the studies.  However, no one has identified a set of sufficient conditions X, Y, and Z that consistently produces advantages on EF components A, B, or C that can be replicated in another lab.  This is not to say that there haven’t been many published studies reporting advantages or differences between bilinguals with different patterns of experience.  They are plenty – but even the study authors do conclude that they have identified sufficient conditions for bilingualism to enhance specific control processes.  That work does remain to be done. 

 

12..  Reviewer 2.   New Analyses of Paap et al. (2019) and Paap et al. (2020): it was unclear what was new and what was not in this section. It was also not clear if the sentence “It may be worthwhile to look at the complete array of language-use measures for each bilingual […]” was a suggestion for future research on an actual goal of the manuscript. Please provide a paragraph listing what was done in the two prior studies (including the methods) and what is new about the current analyses. Since the section on the new analyses is lengthy, the authors may want to focus on what is new and shorten the description of the two previous studies to avoid duplication with their previous research.

Response.  The quote refers to the new analysis of the existing data.   We have revised this section and clarified the results reported in the original publications versus the new analyses based on using multiple language attributes to identify relatively pure cases of SLC, DLC, and DCS bilingualism. 

 

13. Reviewer 2. I suggest making a more general introduction that encompasses the four reviewed studies, not just the two with the new analyses.

Response.  This suggestion is not clear.  In any event, the changes we have made have substantially expanded the number of reviewed studies beyond four.

 

14. Reviewer 2. it is unnecessary to summarize the reanalysis in the limitations section. Please remove the summary.

Response.  It is moved and integrated into the previous section.

 

15. Reviewer 2. The Limitations should appear before the Conclusion.

Response.  The “Limitations” section does appear before the Conclusion.

 

Minor comments:

1. Sloppy text editing is frequent and requires fixing.  {corrected}
2. There are numerous instances of inconsistent spacing between sentences (between 1 to 3 spaces). {corrected}
3. Remove excessive spacing between words throughout the manuscript, e.g., 13, paragraph 4, line 649 (an extra space between “restructuring” and “maintained”); line 650 (an extra space between “structure,” and “a”). {corrected}
4. Names of the group from Poland are misspelled: "Kamala" for "Kalamala”, or – to be more precise – Kałamała) (p. 5, paragraph 2, line 211), and “Szewcyk” for “Szewczyk” (p. 4, paragraph 1, line 153, and the references).  {corrected}
5. 2, lines 60-61: the word "predict[ed]" was used three times. Please use synonyms instead.  {“predict” and “predicted” are only use twice and in two different sentences}
6. 2, paragraph 4: the beginning of the sentence is missing. The sentence now starts with “and we want to alleviate”.  {corrected}
7. 2, paragraph 4, lines 86-89: please paraphrase the apparent quote. The authors admit that the quoted passage is not an exact quote by stating “A sample concern goes something like this”. Brain Sciences requires a more scientific and concrete style.  {The quote is replaced by a paraphrase.}
8. 7, paragraph 2, line 309: the line has the same indent as the beginning of a paragraph above.  {corrected}
9. 10, paragraph 4, line 478, and p. 11, paragraph 4, line 540: Remove the dots at the beginning of sentences. {corrected}
10. 10, paragraph 4, lines 478-480: the summary should be moved to the end of the section it summarizes. {done}
11. 16, table 1: the reference for the MINT is required.{done}
12. paragraph 2, lines 899-900: “Eliminating all the suspense from the narrative of the results” is unnecessary and can be removed. {done}
13. 28, paragraph 2: looks like a note to the Editor. Please remove it. The Limitations section is required, though.  {This sentence was not in the manuscript we submitted.  It must have been added during the Brain Sciences process of producing the review copy.}
14. The name of the last author (Anders-Jefferson) appears on the Brain Sciences website but not in the manuscript. Please resolve this ambiguity. 

{Regina Anders-Jefferson was listed as an author on the manuscript we submitted.  The deletion occurred during the Brain Sciences production of the review manuscript.}

 

Round 2

Reviewer 2 Report

The authors have adequately addressed my concerns and suggestions. I have no further comments.