Review Reports

Round 1

Reviewer 1 Report (Previous Reviewer 1)

Comments and Suggestions for Authors

Thank you very much to the authors for the revisions made. Although the changes have been substantial, they still do not resolve the study’s underlying methodological limitations or several internal inconsistencies in the manuscript.

1. Scalar invariance is not consistently supported according to the criteria defined by the authors themselves. Before comparing latent means, the authors should acknowledge this limitation, assess partial invariance, and identify the non-invariant parameters.
2. Table 4 reports negative values for females and for Morocco, although the text states that both groups showed higher levels. Either the group specification, the direction of the differences, or the interpretation is incorrect. This contradiction had already been identified and remains unresolved.
3. The dependence of participants within schools was dismissed solely because the ICC was low. This argument is insufficient given the size of the clusters and the small number of schools. In addition, differences attributed to country may also reflect specific characteristics of the selected schools.
4. The Instruments section describes the original 21-item BDI-II and its cut-off scores, whereas the study uses a modified 19-item version. The score range, scoring procedure, and consequences of removing the two items are not clearly explained. Retaining the original categories, even if they are described as exploratory, does not make them valid.
5. The conclusion states that the study provides a valid, reliable, and culturally adapted version of the BDI-II. This claim is too strong. The study provides preliminary evidence for a modified 19-item school-based version, but not a comprehensive validation. Its potential application to Moroccan immigrant adolescents in Spain is also speculative, since that population was not studied and the Darija version was not administered.
6. The inclusion of a referral procedure represents an improvement, but it remains overly general. The manuscript does not specify what criterion triggered referral, who reviewed the results, when action was taken, or how cases were followed up.
7. Removing the suicidal ideation item substantially weakens participant protection. A high total score does not replace a direct assessment of suicide risk.
8. The manuscript does not clearly distinguish between parental consent and adolescent assent. It also does not report whether data collection in Morocco received local ethical review or institutional authorization.
9. It remains unclear whether the Spanish participants completed a 19-item version from the outset or whether the two items were removed after administration. This distinction is fundamental. In addition, piloting the instrument with only five adolescents is very limited, and neither their characteristics nor the procedure followed are described in sufficient detail.
10. Missing data were considerably higher in Morocco than in Spain and also varied by age. This difference cannot be treated as a minor issue. The detailed information included in the response to reviewers should be reported and discussed in the manuscript.
11. Although the final model is interpreted as essentially unidimensional, the Discussion again develops differences between somatic and cognitive-affective symptoms. These dimensions are no longer part of the final comparisons, so this discussion is disconnected from the analyses presented.
12. Although the authors state that the manuscript underwent professional editing, terminological, typographical, and statistical errors remain, indicating that it still requires a comprehensive revision.

Author Response

Please see the attachment

Author Response File: Author Response.pdf

Reviewer 2 Report (Previous Reviewer 2)

Comments and Suggestions for Authors

The manuscript, entitled “Cross-Cultural Differences between Spain and Morocco in Depressive Symptomatology during Adolescence,” addresses a relevant and timely topic. The availability of culturally and linguistically appropriate instruments for assessing depressive symptoms in adolescents is an important clinical and public health priority, particularly when comparisons are made across neighbouring countries with different sociocultural and healthcare contexts. The relatively large sample, the inclusion of adolescents from both Spain and Morocco, and the use of confirmatory factor analysis, bifactor indices, and measurement-invariance testing represent important strengths of the study. The manuscript is generally well structured and the authors appropriately acknowledge several limitations associated with convenience sampling and the use of a modified version of the BDI-II. Nevertheless, some methodological and interpretative issues should be clarified before the conclusions can be fully supported.

The most important concern relates to the status and description of the instrument. Two items from the original BDI-II were removed before administration, including the suicidal-ideation item and the item assessing loss of sexual interest. Consequently, the instrument evaluated in this study is not the standard BDI-II but a modified 19-item version. This distinction should be made explicit throughout the manuscript, beginning with the title and abstract. Expressions such as “adapted version of the BDI-II” or statements suggesting that the study validates the BDI-II for Moroccan adolescents may be misleading. The conclusions should instead consistently refer to a “modified 19-item version of the BDI-II.” This is especially important because the removal of the suicidal-ideation item reduces the clinical coverage of the construct and limits the instrument’s use as a comprehensive screening measure for adolescent depression.

The rationale for removing suicidal ideation deserves further discussion. Cultural acceptability and school feasibility are understandable considerations, but excluding a clinically central symptom may introduce construct underrepresentation. The authors should explain whether alternative safeguards were considered, such as retaining the item alongside a predefined risk-assessment and referral procedure. The manuscript currently reports that students with clinically relevant scores were referred to school counselling services, suggesting that a response protocol was already available. The authors should therefore clarify why this protocol could not also have been used for participants endorsing suicidal ideation. The ethical and clinical consequences of excluding this item should be discussed more explicitly.

There are also inconsistencies in the description of the translation and adaptation process. In the Methods section, a bilingual translator is said to have translated the instruments into French and Moroccan Arabic, with a second translator validating the translations through back-translation. In the Results section, however, the original French version is described as being independently translated into Darija by two bilingual translators and subsequently back-translated into French. It is then stated that only the French version was administered because French was the language of instruction in the participating schools. The authors should provide a single, internally consistent account of the process and clearly identify which version underwent psychometric testing. Since the French version, rather than the Darija version, was administered, the manuscript should avoid implying that the psychometric findings validate the Darija translation. It should also clarify whether the French wording was culturally modified or whether an already existing French BDI-II version was used without linguistic changes.

The measurement-invariance results should be carefully re-examined. The text states that configural, metric, scalar, and strict invariance were supported across gender and age within both countries. However, some changes reported in Table 3 appear to exceed the authors’ own criterion of ΔCFI < .010. For example, in the Spanish gender analysis, CFI decreases from .979 in the metric model to .967 in the scalar model and then to .952 in the strict model. These differences do not appear fully compatible with the claim of scalar and strict invariance under the stated criteria. The authors should report ΔCFI, ΔRMSEA, and ΔSRMR explicitly for each consecutive model and revise their conclusions accordingly. Partial invariance could be investigated when full invariance is not supported. The exact constraints used for ordinal indicators should also be described, including how item thresholds, factor loadings, intercepts or residuals were constrained at each stage.

The cross-country latent-mean results require clarification. Table 4 identifies Spain as the reference group and Morocco as the comparison group but reports a negative latent mean difference, while the text states that Moroccan adolescents had higher latent depression levels. The sign of the coefficient may reflect the direction in which the contrast was calculated, but this should be clearly explained. In addition, the reported confidence interval appears to be presented in reverse order, as “[-0.61, -0.94].” Please verify all coefficients, confidence intervals, reference groups, and effect-size signs in Table 4 and ensure that they are consistent with the narrative interpretation.

The use of the original BDI-II severity thresholds with the reduced 19-item instrument is problematic. The authors appropriately acknowledge this limitation, but the categorical results remain prominently presented and described as severity distributions. Since the maximum obtainable score differs from that of the original instrument and one of the omitted items is clinically important, these cut-offs have not been validated for the modified scale. I recommend either removing these classifications from the main analysis or presenting them exclusively as supplementary exploratory findings. Terms such as “prevalence” should be avoided because the data derive from a self-report measure, a convenience sample, and non-validated thresholds rather than a diagnostic assessment.

The handling of missing data also requires further detail. Missingness reportedly ranged up to 9.07%, which is not negligible for some variables or groups. The authors should specify whether missingness was assessed at the item or participant level, describe the pattern and probable mechanism of missingness, and explain precisely how missing ordinal responses were handled by the WLSMV estimator and the software implementation used. The phrase “all available data” is insufficiently precise.

The decision to disregard school-level clustering solely because the ICC was .046 should be justified more cautiously. Although the ICC is relatively small, even modest clustering can affect standard errors when participants are nested within only nine schools and when country is almost entirely confounded with school context. A sensitivity analysis using cluster-robust standard errors would strengthen the findings. At minimum, the authors should acknowledge that country differences may also capture unmeasured school-level, educational, socioeconomic, and recruitment differences.

The interpretation of the cross-country difference should remain conservative. The study compares two convenience samples collected sequentially in different educational settings, with differences in gender distribution, age distribution, language of administration, and potentially socioeconomic and school characteristics. Therefore, the observed latent mean difference should not be presented as a general difference between Spanish and Moroccan adolescents. It is more accurate to describe it as a difference between the two samples after establishing an acceptable degree of measurement equivalence. The manuscript has already moved in this direction, but several statements in the abstract, discussion, and conclusion should be further moderated.

The claim that there were no age differences may also partly depend on the broad categorisation of age into 14–16 and 17–18 years. The rationale for this dichotomisation should be provided. Analysing age as a continuous variable, or reporting a sensitivity analysis using continuous age, would avoid information loss and might detect developmental patterns concealed by the chosen categories.

The discussion could be strengthened by considering individual vulnerability factors in addition to broad cultural and contextual determinants. In this regard, please consider to cite https://doi.org/10.1016/j.jad.2024.08.049.  Which highlights how affective temperamental characteristics may interact with environmental influences in shaping depressive vulnerability. This reference would be most appropriately integrated into a cautious discussion of individual differences and environmental susceptibility rather than used as direct evidence regarding adolescent or cross-cultural differences.

Several editorial issues should also be corrected. The expression “changes in interest in gender” appears inaccurate and should be replaced with the correct description of the omitted BDI-II item. “SRMS” should presumably read “SRMR.” The labels and notes in Table S1 are inconsistent, with the headings using “%f” and “%c” while the note refers to “%s” and “%t.” There are also visible typographical errors in item labels, including duplicated text for worthlessness. The wording “punitive or punitive feelings” should be checked against the official item terminology. Reference formatting and numbering should be carefully reviewed, as some statements may not correspond precisely to the cited sources.

Overall, this is a potentially valuable contribution to cross-cultural adolescent mental-health assessment. However, the psychometric claims, measurement-invariance interpretation, translation procedure, and implications of modifying the BDI-II require clarification. I recommend major revision, primarily because the central claims of cross-cultural equivalence and validation depend on resolving these methodological issues.

Author Response

Please, see the attachment

Author Response File: Author Response.pdf

Reviewer 3 Report (Previous Reviewer 3)

Comments and Suggestions for Authors

I have no questions.

Author Response

Thank you for your previous two review rounds.

Round 2

Reviewer 1 Report (Previous Reviewer 1)

Comments and Suggestions for Authors

Many thanks to the authors for the work they have done.
However, although they have better acknowledged the limitations and tempered some conclusions, they have not resolved the main methodological and ethical issues.
For the study to be publishable, it would need to be reframed as a preliminary psychometric validation, with clinical classifications removed and cross-cultural claims significantly scaled back.
Here are some specific comments:
1.    Scalar invariance is not clearly supported based on the criteria defined by the authors themselves. Nevertheless, they maintain latent mean comparisons without assessing partial invariance.
2.    They continue to use the cut-off points from the original BDI-II for a modified 19-item version. Although they now present these as exploratory, the thresholds are unvalidated and were also used to identify cases requiring referral.
3.    The referral procedure remains unclear. The exact criteria, response time, number of cases identified, and the method used to ensure confidentiality are not specified.
4.    The exclusion of the suicidal ideation item significantly limits both content validity and participant protection. Acknowledging this as a limitation does not rectify the design flaw.
5.    Ethical approval in Morocco remains inadequately documented. While school authorization is mentioned, there is no mention of a local ethical review for collecting sensitive data from minors.
6.    Differences attributed to Spain and Morocco may reflect specific characteristics of the nine selected schools. Country, school, educational context, and recruitment methods are effectively confounded, making the cross-cultural interpretation overly strong.
7.    The handling of missing data remains insufficient. The disparity between Spain and Morocco is substantial and could affect between-group comparisons.
8.    Some responses in the letter do not fully align with the manuscript. For example, the range of the modified scale is not clearly reported, the pilot study involving five adolescents remains very limited, and interpretations regarding somatic and cognitive-affective symptoms—which are not part of the final model—still appear.
9.    Terminological, statistical, and presentation errors persist, which is concerning after several revisions.

Author Response

Please, see the attachment

Author Response File: Author Response.pdf

Reviewer 2 Report (Previous Reviewer 2)

Comments and Suggestions for Authors

Authors addressed all my queries the work is worth of publication in its current form.

Author Response

We thank the reviewer for their positive assessment of our manuscript and for their valuable comments throughout the review process.

This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Thank you very much to the authors for their manuscript.

As this is a first review, I would like to share the following concrete comments:

1. The contribution needs to be better delimited. The text moves between three different purposes: instrument adaptation, psychometric analysis, and cross-cultural interpretation of differences in depression. All three are relevant, but the manuscript does not always articulate with sufficient clarity what its main contribution is.

2. The theoretical review could further develop the specific sociocultural conditions of Spain and Morocco. Some statements about industrialized countries, developing countries, Arab cultures, or Western cultures are too broad and may lead to a somewhat essentialist reading. It would be advisable to include a more nuanced discussion of social class, urbanity, access to mental health care, the school system, gender norms, and stigma, without reducing the differences to general cultural explanations.

3. Methodologically, there are weaknesses that need to be addressed.

   a. The sample was non-probabilistic and based on convenience sampling, which restricts the generalizability of the results. In addition, the predominance of urban participants and students from medium-high socioeconomic backgrounds may bias the comparisons between countries. This limitation is mentioned, but it should carry greater weight in the interpretation of the findings.

   b. The linguistic and cultural adaptation process is described, but it requires further detail. Translation, back-translation, and committee review are appropriate procedures, but the authors should explain more precisely how discrepancies were resolved, what criteria were used to assess semantic and conceptual equivalence, and whether cognitive piloting with adolescents was conducted.

   c. The authors removed the items on suicidal ideation and loss of sexual interest for reasons of cultural and contextual acceptability in Moroccan schools. This decision may be understandable from the perspective of institutional access and contextual protection, but it has substantive consequences. Removing the suicidal ideation item from an adolescent depression instrument may reduce the clinical sensitivity of the instrument and alter comparability with full versions of the BDI-II. In addition, the exclusion of the sexual interest item may be justifiable in a school-based adolescent population, but it needs to be discussed in greater depth. The authors should not present the 19-item version as fully equivalent to the original BDI-II without explaining its scope, limitations, and possible effects on clinical interpretation. It would also be important to clarify whether this modification affects the cut-off points used to classify minimal, mild, moderate, and severe symptomatology. The manuscript describes the original BDI-II cut-off points, but then uses a 19-item version. This may generate a serious methodological issue if the cut-off points were not recalibrated for the reduced version.

   d. Regarding the analyses, there are problems of clarity and consistency in the presentation of the results. Some labels appear to be poorly translated or incorrect. In addition, the interpretation of invariance should be more careful. The manuscript states that comparisons between countries are possible because scalar invariance is achieved, although strict invariance is not. This may be acceptable for comparing latent means, but it needs to be explained more precisely, especially because residuals are not equivalent across countries.

4. Regarding the results, I am concerned about the interpretation of the magnitude and meaning of the differences. The authors report large differences between countries and much higher prevalence rates in Morocco, but they do not sufficiently discuss whether these differences may be due to sampling bias, differences in school conditions, translation, item removal, social desirability, response norms, or uncontrolled socioeconomic differences.

5. The discussion tends to interpret the Spain-Morocco differences in a somewhat generalizing manner. I suggest that the authors reformulate these explanations as interpretive hypotheses rather than as conclusions directly derived from the data.

6. The limitations are insufficient, as there are multiple aspects that should be considered, such as:

   a. The removal of two BDI-II items and its implications for comparability and cut-off points.

   b. The absence of control for socioeconomic variables, urbanity, type of school, and access to mental health services.

   c. The possible influence of cultural response norms and social desirability.

   d. The lack of reported cognitive piloting with adolescents.

   e. The impossibility of establishing causality due to the cross-sectional design.

7. The implications should be more cautious. The study does not directly demonstrate that the instrument reduces health inequalities or improves school and social adaptation. It may potentially contribute to this, but this claim should be formulated as a possibility or future application, not as a proven result.

8. The interpretive bias throughout the article should be carefully addressed, given that it makes claims on sensitive issues.

9. I have an ethical concern regarding the fact that, since the study deals with adolescents and depression, the manuscript should specify whether there was a referral or action protocol for cases with moderate or severe symptomatology. This is especially important because the study identified a considerable proportion of Moroccan adolescents with moderate or severe symptomatology. In addition, by removing the suicidal ideation item, the authors should explain how they protected participants who may have been at clinical risk but were not detected through that item.

Comments on the Quality of English Language

The manuscript requires professional editing, as well as a careful review of language use, since there are translation and style errors.

Author Response

Please, see the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

The manuscript addresses an important and timely topic: the culturally sensitive assessment of depressive symptomatology among adolescents in Spain and Morocco. The study has the potential to contribute to the literature by adapting and examining the psychometric properties of the BDI-II in the Moroccan context and by comparing cognitive-affective and somatic-vegetative symptoms across two culturally distinct samples. The relatively large binational sample, the use of confirmatory factor analysis, the assessment of reliability and convergent validity, and the attempt to test measurement invariance before comparing groups are clear strengths.

Overall, I recommend major revision before publication. The study is promising, but several methodological and interpretative issues need to be clarified. The most important concern relates to the modification of the BDI-II. The authors removed the items on suicidal thoughts and loss of sexual interest from the Moroccan French and Arabic versions because of cultural and contextual acceptability concerns. This decision needs a fuller justification, especially because removing the suicidal ideation item has important implications for construct validity, clinical screening, ethical responsibility, and comparability with previous BDI-II studies. The authors should clarify whether the same 19-item version was used in both Spain and Morocco, how total scores were calculated, and whether the original BDI-II severity cut-offs can still be applied after item removal. If these cut-offs have not been recalibrated, prevalence estimates should be interpreted only descriptively rather than diagnostically.

The cross-cultural interpretation should also be made more cautious. The manuscript reports higher cognitive-affective and somatic-vegetative symptomatology in the Moroccan sample than in the Spanish sample, as well as a higher proportion of Moroccan adolescents in the moderate and severe symptom categories. These findings are interesting, but they should not be presented as definitive national or cultural differences. Given the convenience sampling strategy, the predominance of urban participants, and the medium-high socioeconomic profile of much of the sample, the results should be described as differences between the specific samples studied. Possible influences of socioeconomic status, school type, region, language of administration, response style, mental health literacy, and access to care should be discussed more explicitly.

The reporting of measurement invariance requires careful revision. Since the analyses use WLSMV for ordinal indicators, the authors should specify the software packages, parameterization, identification strategy, threshold constraints, and scaled difference testing procedures. Some reported chi-square differences are negative, which suggests that the difference testing may not have been reported correctly. The terminology should also be revised: for ordinal items, thresholds rather than intercepts are usually constrained, and expressions such as “restricted waste” should be corrected. Table labels such as “IFC” should also be checked.

The manuscript should provide more information on missing data. The statement that missing values did not exceed 10% and were not imputed is not sufficient for reproducibility. The authors should specify how missing data were handled in the CFA and invariance analyses and how many participants were included in each model. It would also be useful to know whether missingness differed by country, sex, age group, or language version, as differential missingness could influence cross-country comparisons.

The convergent validity evidence based on the BASC-3S depression scale is useful, but the authors should clarify whether this scale was linguistically and culturally adapted for the Moroccan sample and whether it has established validity in Moroccan adolescents. The instrument section refers to the Spanish adaptation and to psychometric evidence in Spanish, Basque, and Persian samples, but this does not automatically support its use as a criterion measure in Morocco. If the BASC-3S depression scale was translated and adapted as part of this study, the authors should describe that process and provide reliability evidence for the Moroccan subsample.

Similarly, the description of the French and Arabic versions should be expanded. The manuscript should report how many Moroccan adolescents completed each language version, how the language of administration was selected, whether participants chose the language, and whether equivalence between the Arabic and French forms was examined. A bilingual adapted instrument is not necessarily psychometrically equivalent across language versions, and this issue is particularly relevant in a cross-cultural validation study.

Some interpretations in the Discussion should be softened. In particular, the claim that sex differences among Moroccan girls may be exacerbated by “religious forces” is sensitive and should be supported by direct evidence or replaced with more cautious wording referring to gender norms, social expectations, stigma, family expectations, and help-seeking barriers. The Discussion would be stronger if it clearly distinguished between findings directly supported by the data and broader sociocultural hypotheses.

The Discussion would also benefit from a stronger connection with recent evidence suggesting a progressive shift of severe affective psychopathology toward younger ages. Please consider to cite: doi:10.1186/s12991-026-00681-2, who examined psychiatric admissions from 2006 to 2022 in an Italian catchment area and reported a progressive reduction in age at admission, particularly for major depression and bipolar disorder, with the reduction being specific to voluntary admissions. Although that study focused on adult inpatient admissions rather than school-based adolescent assessment, its findings are relevant to the present manuscript because they support the broader clinical concern that depressive and affective disorders may be emerging, worsening, or requiring hospital-level care at increasingly younger ages. This evidence could help the authors contextualize the importance of early detection during adolescence, culturally valid screening tools, and preventive interventions before depressive symptomatology progresses to more severe clinical outcomes, including psychiatric hospitalization. 

Finally, the manuscript needs language and formatting revision. Several expressions should be corrected, including “metric properties,” “Somatic-vegetative symptomatology dementias,” “n Spain,” “serious symptoms,” and inconsistent use of “sex” and “gender.” Figure 1 should be improved for readability, and its caption should refer to standardized factor loadings rather than “standardised factor steps.” The authors should also check all table headings and technical labels.

A further issue concerns copyright and permissions. The appendix reproduces the adapted BDI-II items in full in French and Arabic. Because the BDI-II is a copyrighted instrument, the authors should explicitly state whether permission was obtained for translation, adaptation, use, and reproduction of the items in the article. If permission does not allow full reproduction, the appendix may need to be removed or replaced by a description of the adaptation process.

The limitations section should be expanded. The authors mention convenience sampling and the absence of a clinical sample, but additional limitations should be discussed, including the removal of two BDI-II items, the lack of recalibrated severity cut-offs for the 19-item version, the possible non-equivalence of French and Arabic versions, the use of self-report questionnaires, potential response-style differences across countries, the cross-sectional design, and the limited generalizability to rural adolescents or adolescents from lower socioeconomic backgrounds.

In conclusion, the manuscript addresses a relevant research gap and contains promising data, but it requires major revision. The authors should justify the 19-item adaptation more clearly, reconsider the use of standard severity cut-offs, clarify the language-version procedures, revise the invariance analyses, expand the limitations, moderate the cultural interpretations, and improve the English language throughout. With these revisions, the article could make a meaningful contribution to cross-cultural adolescent mental health assessment.

Author Response

Please, see the attachment.

Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

1. A central issue is that the authors removed two original BDI-II items from the Moroccan version due to concerns about cultural and contextual acceptability in school settings. Although this decision may be understandable, it substantially changes the content and structure of the instrument. The authors should more clearly acknowledge that the resulting questionnaire is a modified or shortened version of the BDI-II, rather than the original BDI-II. This issue has important implications for the interpretation of the results. The deleted items are clinically relevant and may affect the total score, factor structure, severity classification, and cross-cultural comparability of depressive symptomatology. The authors should provide a stronger theoretical and methodological justification for item removal and discuss how this affects content validity.

2. The manuscript reports the prevalence of minimal, mild, moderate, and severe depressive symptomatology. However, it appears that these categories are based on the original BDI-II cut-off scores. Since the scale was modified by removing two items, the original cut-off points may no longer be directly applicable. The authors should either provide empirical justification for using these cut-offs with the 19-item version or avoid making strong prevalence-based claims. At minimum, the manuscript should clearly state that severity classification is exploratory and may not be directly comparable with studies using the full BDI-II.

3. The study compares adolescents from Spain and Morocco, but the sampling strategy was non-probabilistic and based on convenience sampling. The two samples may differ in several background characteristics, such as socioeconomic status, school type, urban/rural context, language of administration, educational system, and response style. These factors may influence depressive symptom reporting and could partly explain the observed country differences. The authors should be more cautious in interpreting the higher depressive symptom scores in Moroccan adolescents. The current discussion tends to attribute differences to cultural, socioeconomic, religious, and healthcare-related factors, but these variables were not directly measured or statistically tested. These explanations should be framed as hypotheses rather than conclusions.

4. The manuscript states that translation, back-translation, and expert review were conducted. However, the adaptation procedure should be described in greater detail. For example, the authors should clarify:

   • Whether the Arabic version was in Modern Standard Arabic or Moroccan Arabic/Darija;
   • Whether adolescent cognitive interviews or pilot testing were conducted;
   • How translation discrepancies were resolved;
   • Whether the French and Arabic versions were administered to different participants;
   • Whether measurement invariance was tested across language versions within Morocco.

   This information is essential because combining responses from French and Arabic versions without testing language-version equivalence may introduce measurement bias.

5. The authors report that the two-factor model showed the best fit in both countries. However, the correlation between cognitive-affective and somatic-vegetative factors appears to be very high. This raises the possibility that a general depression factor may dominate the structure of the questionnaire.

   The authors should provide a clearer comparison of alternative models, such as a unidimensional model, correlated two-factor model, hierarchical model, or bifactor model. If the two-factor structure is retained, the authors should justify why this model is theoretically and statistically preferable.

6. The measurement invariance analysis is important for the study, but its reporting needs improvement. Some of the changes in fit indices appear close to or beyond the stated thresholds. The authors should ensure that all invariance decisions are consistent with the criteria described in the Methods section.

   In addition, the manuscript should clearly distinguish between configural, metric, scalar, and strict invariance. Since strict invariance was not supported in the cross-country comparison, the implications of this result should be discussed more carefully. The authors should clarify whether scalar invariance alone is sufficient for their latent mean comparisons and whether residual non-invariance may affect the interpretation of observed score differences.

7. The manuscript should provide more complete and transparent statistical reporting. For example, the authors should report how missing data were handled in the CFA and invariance models, whether robust estimators were used consistently, and whether clustering by school was considered. Since participants were recruited from several schools, observations may not be fully independent. The authors should either account for school-level clustering or explain why it was not considered necessary.

8. The discussion contains several speculative explanations for the observed differences between Spain and Morocco. While these interpretations are interesting, they are not directly supported by measured variables in the study. The authors should revise the discussion to avoid causal or overly broad cultural explanations.

   For example, statements about cultural constraints, religious forces, stigma, healthcare access, and socioeconomic development should be presented more cautiously. The manuscript would be stronger if the authors emphasized that future studies should directly measure these potential explanatory factors.

9. The current limitations section is too brief. The authors should include additional limitations, such as:

   • Use of convenience sampling;
   • Lack of clinical diagnostic interviews;
   • Potential response bias in self-report data;
   • Deletion of two BDI-II items;
   • Uncertain validity of original cut-off scores for the 19-item version;
   • Possible language-version effects within the Moroccan sample;
   • Lack of control for socioeconomic, school-level, and contextual variables;

10. The manuscript contains several language and formatting issues that should be corrected. For example, there are inconsistent terms such as “gender” and “sex,” typographical errors such as “dementias,” and possible table-labeling errors such as “IFC” instead of “CFI.” The manuscript would benefit from careful proofreading by a fluent English speaker. 

11. 

• The Introduction should more clearly explain why Spain and Morocco were selected beyond geographical proximity and migration relevance.
• The authors should clarify whether the Spanish sample also used the 19-item version or the original 21-item BDI-II. If the Spanish sample used the full version but the Moroccan sample used the shortened version, cross-country comparisons would be highly problematic.
• Table 2 is difficult to read and should be reformatted for clarity.
• Figure 1 should be improved. The labels and factor loadings are difficult to read, and the caption should be more precise.
• The terms “cognitive-affective” and “affective-cognitive” appear to be used inconsistently. Please standardize terminology throughout the manuscript.
• The authors should clarify whether BASC-3S was validated or adapted for the Moroccan adolescent sample, as it was used to assess convergent validity.
• The Results section should avoid repeating too many fit indices in the main text. A clearer summary of the main findings would improve readability.

Author Response

Please, see the attachment

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

Thank you very much to the authors for their revised manuscript.

Although the manuscript has clearly changed, the revision is unfortunately still only partial, and several issues remain unresolved. My main concern is that the text does not appear to have been revised as a whole, which has resulted in contradictions across different sections.

1. The ethical issue remains unresolved in the manuscript. In the response to reviewers, the authors state that there was a referral protocol for cases with elevated symptomatology. However, in the manuscript itself, only ethical approval and informed consent are mentioned. There is no description of any action protocol, referral procedure, notification to families, psychological support, or procedure for cases involving clinical risk. This is particularly sensitive because the manuscript reports high percentages of Moroccan adolescents in the moderate and severe ranges, even if these estimates are presented as exploratory.
2. In the Results section, the authors state that females reported lower latent levels of depression than males in Spain and Morocco. However, the Discussion section states the opposite.
3. The abstract still refers to differences in somatic-vegetative and cognitive-affective symptomatology, even though the final analysis is justified as essentially unidimensional and the comparisons are made using the total depression factor. In addition, Table 4 still has a title referring to “cognitive-affective and somatic-vegetative depressive symptomatology,” although the table no longer presents these two dimensions.
4. In the Methods section, the authors state that the instrument was translated into French and Moroccan Arabic, but later clarify that all Moroccan participants completed the French version and that the Darija version was not used. This needs to be clarified more carefully, as it changes the actual scope of the cultural and linguistic adaptation.
5. Although some cautions were added, the Limitations section still does not sufficiently discuss the bias introduced by convenience sampling, the predominance of urban participants, and the medium-high socioeconomic background of the sample. The Methods section reports that 93.2% of participants were from urban settings and mostly from medium-high socioeconomic backgrounds, but in the Limitations section this is reduced to a very general statement. There is also still no explicit mention that the cross-sectional design prevents causal inferences.
6. The conclusion still states that the instrument “will favour” more accurate assessments, equal access, the reduction of health inequalities, and support for school and social adaptation. These outcomes were not empirically demonstrated by the study.

I recommend a full reading and revision of the manuscript so that it can be edited and made internally consistent across all sections before being submitted again.

Author Response

Improvements have been made to the manuscript, in line with the reviewers’ recommendations. Please, see the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

Authors addressed all my queries the work is worth of publication in its current form.

Author Response

Thank you very much for your reply and for considering that the manuscript might be accepted in its current form.

Reviewer 3 Report

Comments and Suggestions for Authors

I have no questions.

Author Response

Improvements have been made to the manuscript, in line with the reviewers’ recommendations.