Prejudice and Cuts to Public Health and Education: A Migration Crisis or a Crisis of the European Welfare State and Its Socio-Political Values?

Round 1

Reviewer 1 Report

Dear authors,

1. At the Keywords (line 22) - is better to insert short keywords instead of: Attitudes towards Immigrants; Context-level factors because they are too long; please insert at list 5 keywords as anchor words.

2. This article proposes a multi-level analysis of 24 European countries for the year 2012 (line 58) - can be mentioned these countries at the endnotes or in other place but are important to be mentioned.

2. The empty model (line 402) - can be more detailed and this suggestion is also valable for all the models.

3. Table 2 (line 452) - can be also detailed and give more comments starting from that values.

4. Conclusion (line 466) - can be improved. 

Good luck!

Author Response

I am very thankful to all the reviewers for their work.

My replies are in yellow in the text.

Dear authors,

1. At the Keywords (line 22) - is better to insert short keywords instead of: Attitudes towards Immigrants; Context-level factors because they are too long; please insert at list 5 keywords as anchor words.

• Dear reviewer, I am very thankful for your detailed feedback on my work. I have deleted from the keywords “attitudes towards immigrants” (which can be subsumed by “prejudice”. However, please note that the latter is not a perfect replacement) and context level factors. There is indeed no one single word that can be used for “context-level factors”.

2. This article proposes a multi-level analysis of 24 European countries for the year 2012 (line 58) - can be mentioned these countries at the endnotes or in other place but are important to be mentioned.

• Indeed, you are absolutely right. I have added a note to line 278 and the list of countries in the note at the end of the document.

3. The empty model (line 402) - can be more detailed and this suggestion is also valable for all the models.

• I have added more detailed information.

4. Table 2 (line 452) - can be also detailed and give more comments starting from that values.

• I have included more detailed information on the values in the text.

4. Conclusion (line 466) - can be improved. 

• I have improved the conclusions by adding clarifications

Good luck!

Many thanks!

 

To sum up, I would like to thank very much with all the reviewers for the careful revision of the work. I agree with all commentaries. These are the major changes included in the text. I have included an analysis on the battery of attitudes toward immigration rather than on the single item. They are substantially similar to those on the single item. I have also run a PCFA for testing the composite measure formed with the battery of attitudes towards immigrants and included this information in the text, where describing the dependent variable.

I have better refined the hypotheses, by removing one of the two hypotheses, as suggested by reviewer 3. I have included the context level variables together with the interaction effect, which were mistakenly removed from the table before, as correctly identified by reviewer 3.

I have included descriptive statistics at the end of the document in table 3, and the list of countries in a note, as suggested by reviewer 1 and I have added the relevant information requested by reviewer 1.

I have added some references to works on other identity transformations, as suggested by reviewer 2.

Reviewer 2 Report

The text covers an important issue. It does so by giving insight between the relation of Quillian's theory of attitudes towards migrants and the respected variables in a correct methodological fashion. However the authors are encouraged to shed some light also on other theories of migration perception in the context of identity transformations. Minor spell check required.

Author Response

I am very thankful to all the reviewers for their work.

My replies are in yellow in the text.

The text covers an important issue. It does so by giving insight between the relation of Quillian's theory of attitudes towards migrants and the respected variables in a correct methodological fashion. However the authors are encouraged to shed some light also on other theories of migration perception in the context of identity transformations. Minor spell check required.

Works to other identity transformation have been referred in the document. However, one of the other reviewers has suggested to cut the relevant part. So, I have done my best to satisfy both requests.

However, if there is any crucial work that the reviewer considers would be indispensable to quote, please, do let me know, and I will include those works accordingly.

To sum up, I would like to thank very much with all the reviewers for the careful revision of the work. I agree with all commentaries. These are the major changes included in the text.  I have included an analysis on the battery of attitudes toward immigration rather than on the single item. They are substantially similar to those on the single item. I have also run a PCFA for testing the composite measure formed with the battery of attitudes towards immigrants and included this information in the text, where describing the dependent variable.

I have better refined the hypotheses, by removing one of the two hypotheses, as suggested by reviewer 3. I have included the context level variables together with the interaction effect, which were mistakenly removed from the table before, as correctly identified by reviewer 3.

I have included descriptive statistics at the end of the document in table 3, and the list of countries in a note, as suggested by reviewer 1 and I have added the relevant information requested by reviewer 1.

I have added some references to works on other identity transformations, as suggested by reviewer 2.

Reviewer 3 Report

The paper argues that anti-immigrant attitudes are associated with country-level policies not related to immigration, such as cuts in expenditure for the education and health sector. Moreover, the authors argue that these cuts are positively associated with anti-immigration attitudes especially in countries with high immigrant inflows.

Although the idea of the paper could be intriguing, the empirical section does not allow testing properly the hypotheses because empirical models are wrongly specified. Nonetheless, every comment related to answers to hypothesis 1 is misleading. In the following lines, I will better explain my point.

The authors include in their analysis an interaction between three variables: immigration inflows, variation in health expenditure, variation in education expenditure. When looking in table 2 at the empirical models to test hypothesis 1 (Model 3 H1), I see the interaction term between the three variables, but main effects (the single regression terms for each of the three variables) and the second-order terms (interaction terms for each couple of variables) are not included in the model. This leads to a misspecification of the empirical model: when including an interaction term between two or more variables in a regression analysis, you should always include lower order terms. If you do not, like in the case of this paper, you cannot correctly interpret the regression analysis. Accordingly, all the comments and answers to the hypothesis cannot be taken into consideration. The same issue applies also to Model 4 Quillian (table 3): no main effect for immigration inflows and GDP per capita.

I do not even understand why the authors did not analyse the interaction between immigrant inflows and variation in health expenditure in one model, and the interaction between immigration inflows and variation in education expenditure in another model. This choice would have allowed a more comprehensible answer to the research question and also to test an eventually different moderation effect of immigration inflows in the relationship between variation in respectively health expenditure and education expenditure in explaining attitudes toward immigration. If the authors are not confident in employing models with interaction terms, I would suggest avoiding interaction terms between three variables. Why do you present interactions between three variables? Which is the rationale? The paper never explains that choice.

Moreover, another relevant issue of the paper is the repetitive use of the term “rise” of anti-immigrant attitudes. The authors should be conscious that the data used refers only to one point in time (2012), thus they cannot analyse variations in attitudes toward immigration over time (and accordingly, increase, stability, or decrease), although the use of multiple rounds of the European Social Survey data would allow analysing such variations. In the present paper, the authors can simply show that a variation in the immigrant inflows (as well as in health and education expenditure) is associated with a higher (or lower) average level of attitudes toward immigration in 2012. In other words, they cannot employ words related to longitudinal analysis when referring to the dependent variable.

Also, in the introduction and in the theoretical framework the authors often mention the role of the refugee crisis and the subsequent increase in migration flows on attitudes toward immigration. Nonetheless, the peak of the refugee crisis took place in 2015, while the data employed in the paper refers to a previous period, as survey data employed were collected in 2012 and the contextual data refers to the immigrant inflows between 2005 and 2012.

I also think that the two hypotheses of the paper are rather disconnected. In particular, after the reading of the abstract and the introductory section, one is expecting to read a paper on the role of non-immigration-related policies in explaining attitudes toward immigration. Instead, a consistent part of the paper focuses on the role of self-transcendence values in explaining those attitudes. In the actual version of the paper, I cannot find a convincing link between the two parts. According to my point of view, in future versions of this paper, the authors should focus on only one explanation, or alternatively, they should reshape the manuscript for a better connection between the two parts.

Finally, for the sake of the argumentation, I would suggest largely cutting the text in age 3-4, from line 138 and line 188. I think it is not associated with the hypotheses presented and not functional to make the main argument clear. At most, you can briefly mention the various theories in one paragraph.

Before concluding, I would like to add two further considerations to the empirical section:

-       For a better understanding of the subsequent inferential analysis, the authors should report descriptive statistics, at least for country-level variables.

-       The choice of considering only one item of the battery of attitudes toward immigration is not convincing, especially in the light of a broad literature analysing European Social Survey data and considering indexes of several items of attitudes toward immigration. Also, they should discuss the choice of not using the battery of items employed in several comparative studies (e.g. Meuleman, Davidov and Billiet 2009; Gorodzeisky and Semyonov 2020)

 

Author Response

I am very thankful to all the reviewers for their work.

My replies are in yellow in the text.

The paper argues that anti-immigrant attitudes are associated with country-level policies not related to immigration, such as cuts in expenditure for the education and health sector. Moreover, the authors argue that these cuts are positively associated with anti-immigration attitudes especially in countries with high immigrant inflows.

Although the idea of the paper could be intriguing, the empirical section does not allow testing properly the hypotheses because empirical models are wrongly specified. Nonetheless, every comment related to answers to hypothesis 1 is misleading. In the following lines, I will better explain my point.

The authors include in their analysis an interaction between three variables: immigration inflows, variation in health expenditure, variation in education expenditure. When looking in table 2 at the empirical models to test hypothesis 1 (Model 3 H1), I see the interaction term between the three variables, but main effects (the single regression terms for each of the three variables) and the second-order terms (interaction terms for each couple of variables) are not included in the model. This leads to a misspecification of the empirical model: when including an interaction term between two or more variables in a regression analysis, you should always include lower order terms. If you do not, like in the case of this paper, you cannot correctly interpret the regression analysis. Accordingly, all the comments and answers to the hypothesis cannot be taken into consideration. The same issue applies also to Model 4 Quillian (table 3): no main effect for immigration inflows and GDP per capita.

• I am sorry; these data were mistakenly removed from the table. I have added the main effects and I have run the analysis on the battery of items on attitudes towards immigrants as suggested later on in the commentaries of the reviewer.

I do not even understand why the authors did not analyse the interaction between immigrant inflows and variation in health expenditure in one model, and the interaction between immigration inflows and variation in education expenditure in another model. This choice would have allowed a more comprehensible answer to the research question and also to test an eventually different moderation effect of immigration inflows in the relationship between variation in respectively health expenditure and education expenditure in explaining attitudes toward immigration. If the authors are not confident in employing models with interaction terms, I would suggest avoiding interaction terms between three variables. Why do you present interactions between three variables? Which is the rationale? The paper never explains that choice.

• The rationale is that only when both cuts happen concurrently to higher migrants percentages they allow a scapegoating of the arrival of migrants for the worsening of these two crucial public sectors. I have explained it in the theoretical framework and now I have added it also in the empirical section to clarify the point better. I hope it makes sense to the reviewer.

Moreover, another relevant issue of the paper is the repetitive use of the term “rise” of anti-immigrant attitudes. The authors should be conscious that the data used refers only to one point in time (2012), thus they cannot analyse variations in attitudes toward immigration over time (and accordingly, increase, stability, or decrease), although the use of multiple rounds of the European Social Survey data would allow analysing such variations. In the present paper, the authors can simply show that a variation in the immigrant inflows (as well as in health and education expenditure) is associated with a higher (or lower) average level of attitudes toward immigration in 2012. In other words, they cannot employ words related to longitudinal analysis when referring to the dependent variable.

• I have corrected the terminology accordingly.

Also, in the introduction and in the theoretical framework the authors often mention the role of the refugee crisis and the subsequent increase in migration flows on attitudes toward immigration. Nonetheless, the peak of the refugee crisis took place in 2015, while the data employed in the paper refers to a previous period, as survey data employed were collected in 2012 and the contextual data refers to the immigrant inflows between 2005 and 2012.

• I have explained in the paper that this is to check how the cuts affected the formation of attitudes towards immigrants before the happening of the migration crisis, so as to show that the situation set the stage for the following migration crisis. I have explained this point further in the article.
• The analysis was run on the ESS round 6, year 2012, because it wanted to test the idea that this situation affected attitudes towards migrants before the 2015 migration crisis. The same analysis cannot be run on the 2014 ESS because some important countries did not participate in round 7, such as Italy, Bulgaria, etc., reducing the sample to 19 countries. Cox in his book “Multilevel analysis” and several other authors support the idea that there should be at least 5 context cases per each variable at context level, which means that with 4 context level variables included, I needed at least 20 countries in the sample.

I also think that the two hypotheses of the paper are rather disconnected. In particular, after the reading of the abstract and the introductory section, one is expecting to read a paper on the role of non-immigration-related policies in explaining attitudes toward immigration. Instead, a consistent part of the paper focuses on the role of self-transcendence values in explaining those attitudes. In the actual version of the paper, I cannot find a convincing link between the two parts. According to my point of view, in future versions of this paper, the authors should focus on only one explanation, or alternatively, they should reshape the manuscript for a better connection between the two parts.

• I have removed transcendence from the hypothesis. So now there is only hypothesis 1.

Finally, for the sake of the argumentation, I would suggest largely cutting the text in age 3-4, from line 138 and line 188. I think it is not associated with the hypotheses presented and not functional to make the main argument clear. At most, you can briefly mention the various theories in one paragraph.

• I have cut the section as suggested. I have removed from the text between page 3 and 4, all the works not related to the multilevel analysis of attitudes towards immigrants.

Before concluding, I would like to add two further considerations to the empirical section:

-       For a better understanding of the subsequent inferential analysis, the authors should report descriptive statistics, at least for country-level variables.

• I have included descriptive statistics in an annex, as table 3.

-       The choice of considering only one item of the battery of attitudes toward immigration is not convincing, especially in the light of a broad literature analysing European Social Survey data and considering indexes of several items of attitudes toward immigration. Also, they should discuss the choice of not using the battery of items employed in several comparative studies (e.g. Meuleman, Davidov and Billiet 2009; Gorodzeisky and Semyonov 2020)

• I have now run the analysis on the battery rather on the single ítem. I have reported the data from the analysis on the battery in the paper, which are substantially in line with those on the single item.

To sum up, I would like to thank very much with all the reviewers for the careful revision of the work. I agree with all commentaries. These are the major changes included in the text. I have included an analysis on the battery of attitudes toward immigration rather than on the single item. They are substantially similar to those on the single item. I have also run a PCFA for testing the composite measure formed with the battery of attitudes towards immigrants and included this information in the text, where describing the dependent variable.

I have better refined the hypotheses, by removing one of the two hypotheses, as suggested by reviewer 3. I have included the context level variables together with the interaction effect, which were mistakenly removed from the table before, as correctly identified by reviewer 3.

I have included descriptive statistics at the end of the document in table 3, and the list of countries in a note, as suggested by reviewer 1 and I have added the relevant information requested by reviewer 1.

I have added some references to works on other identity transformations, as suggested by reviewer 2.

Round 2

Reviewer 3 Report

I have appreciated the authors’ efforts in revising the manuscript. Some of the issues raised in the review have been addressed.

Nonetheless, there are still relevant shortcomings in the empirical analysis.

For what concerns the three-way interaction model, the second-order terms (interaction terms for each couple of variables) were not included. This leads to a misspecification of the empirical model: when including an interaction term between two or more variables in a regression analysis, you should always include lower order terms. Accordingly, we cannot provide conclusions based on the actual analysis. Also, as suggested in the previous review, I would like to see the analysis of the interaction between immigrant inflows and variation in health expenditure in one model, and the interaction between immigration inflows and variation in education expenditure in another model. Only after showing these two models, I will eventually include the three-way interaction. In this regard, the authors’ answer to my comment is not convincing, both from a theoretical and an analytical perspective. 

Furthermore, after the inclusion of descriptive statistics, I realized that the analyses were performed on 10,057 cases while the whole sample is made of more than 50,000 cases. In other words, more than 80% of the cases were excluded from the analyses; accordingly, a high selection bias could be detected. To be published, the authors should re-run their analyses by including a far larger number of cases. The selection bias is mainly due to the variable on unemployment (yes/no); indeed, only 15,075 individuals provide a valid answer to that variable. All individuals not belonging to the labour force are not included in the sample, without an apparent reason. To solve the issue of selection bias, the authors need to consider a variable on employment status which include other categories for identifying the non-active people (students, retired, housewives...). Alternatively, they should show the analyses without the inclusion of occupational status among the individual-level control variables. In the present version, this issue is very relevant and needs to be addressed by the authors.

Finally, following my suggestion, the authors deleted any reference to the "rise" in prejudiced attitudes and substituted it with the term “formation”. In this context, I think it is preferrable to refer to “prevalence” instead of “formation”.

Author Response

Please see attached document

Author Response File: Author Response.pdf

Round 3

Reviewer 3 Report

I have appreciated the authors’ effort in dealing with the issues raised in the previous revision (e.g., the deletion of the variable on unemployment status, whose inclusion in the model led to a reduction of about two-thirds of the cases). Nonetheless, the most relevant issue was not addressed. This issue is crucial for the analysis and the take-home message of the article

The model 3c in Table 1, that allows testing the main hypothesis of this work, is still mis-specified, as it does not include the two-way interaction term between variation in public expenditures for public education and variation in public expenditures for public education.

Lines 1040-1043: ”Model 3a and Model 3b include the single pair of interactions between immigrants percentages and cuts to the public education expenditure in one model, and cuts to the health expenditure in the other. Model 3a shows a significant coefficient; however, being higher than 1, it does not make sense.” This sentence suggests, as highlighted in previous versions of the revision, the authors' low familiarity with regression analysis and interpretation of the results. Why does a coefficient higher than 1 not make any sense? It makes a lot of sense. To provide a substantial interpretation of how interaction effects work the authors should provide a graphical representation of marginal effects, as they do not give a correct interpretation of the results when simply looking at the coefficients. Graphical representations even allow providing simpler interpretations of the results.

In the answer, when referring to the interaction terms included in Models 3a and 3b in Table 2 they state: “One is indeed significant but the coefficient does not make sense; so, in the literature, it is suggested to be considered insignificant, and it is what I have done." Which is the literature suggesting this interpretation? It is this answer that suggests scarce familiarity with regression analysis. As suggested before, the authors should employ graphical representations of the interaction effects to have a better understanding of their analysis.

Minor comments:

-        What do the asterisks mean in Tables of coefficients? In other words, to which significance level do they refer?

-        In the appendix, the authors should report the new value of the valid cases employed in the regression models. In the tables, the authors should report the number of cases employed in the regression analyses.

Author Response

Dear Reviewer,

 

I have also appreciated very much your careful review of the manuscript.

I believe that the model c1 is not mis-specified as the hypothesis contemplates the interaction of cuts of these two public sectors with the presence of migrants. Theoretically, it does not make any sense to include an interaction between the two variables including the cuts to these two public sectors if they are not considered combined with the presence of migrants.

 

When it comes to the coefficient higher than 1 in multiple regression and hierarchical multiple regression, several authors consider that a coefficient higher than 1 implies a high level of multicollinearity and therefore it should not be considered in the analysis. Please see Joreskog 1999, just for an example. However, now I had a more in depth look into this after your commentary, and I have realized that there is discordance on this. For example, in 1973, Deegan writes:

“For some investigators, the occurrence of standardized regression coefficients greater than one in a model raises questions concerning the legitimacy of such coefficients, and poses serious problems of interpretation (particularly for those employing path analytic procedures). It is demonstrated here that standardized regression coefficients greater than one can legitimately occur.”

 

Therefore, I have decided to simply delete the sentence (which was however not very clearly stated, I do take this and your point, I am sorry for that), as it does not matter that much in the analysis and this article is not the place where to discuss whether or not a Beta coefficient greater than 1 can be considered legitimate. But I do thank you for this comment, as I have definitely learnt more on the topic. However, allow me to say that I have found odd that you were commenting on the authors’ skills. I believe that a reviewer limits himself/herself to comment on the manuscript and not on author’s abilities, so as to not offend the authors. Anyway, no worries, no offence taken on my side.

 

Thank you so much for noticing the ‘asterisks’ issue. In my initial submission this information was included in a note at the end of the table, which went mistakenly deleted in the revision. I have included it again.

Thank you for the time you have taken for this review.