The Impact of a Dedicated In-Hospital Vaccination Clinic on Adherence to Herpes Zoster Vaccination Among Immunocompromised and Frail Adults: Findings from an Italian Quasi-Experimental Study

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

1) The quasi-experimental, non-randomized design requires deeper methodological justification. Since recruitment occurred in two different settings (hospital clinic vs. GP clinics), baseline differences between groups are likely. Although multivariable regression was applied, additional strategies (e.g., propensity score adjustment or sensitivity analysis) would strengthen causal inference regarding the intervention effect.

 

2) Table 1 indicates several statistically significant differences between experimental and control groups (e.g., age distribution, education, working activity, comorbidities). These imbalances may confound the observed effect (OR = 38.21 for adherence). Please clarify whether interaction terms were tested and whether collinearity diagnostics were performed.

3) The adjusted OR for adherence in the experimental group is very large (OR = 38.21; 95% CI 12.23–119.33) . While statistically significant, the wide CI suggests instability and possible sparse-data bias. Please comment on event distribution per variable in Model 2 and whether model overfitting was assessed (e.g., events-per-variable rule).

4)The sample size was calculated assuming 50% willingness , but no justification is provided for power regarding the adherence outcome (Model 2, N=171). Given the relatively small number of vaccinated individuals (n=105), please clarify whether the study was adequately powered for multivariable analysis of adherence.

5) Several clinically relevant variables (e.g., perceived health status, number of chronic diseases, knowledge variables) were removed through backward elimination . Stepwise methods may introduce bias and model instability. Consider presenting a full model or performing robustness checks.

Author Response

Reviewer 1:

• The quasi-experimental, non-randomized design requires deeper methodological justification. Since recruitment occurred in two different settings (hospital clinic vs. GP clinics), baseline differences between groups are likely. Although multivariable regression was applied, additional strategies (e.g., propensity score adjustment or sensitivity analysis) would strengthen causal inference regarding the intervention effect.

 

In response to the comment, we fully agree that a quasi-experimental, non-randomized design requires careful methodological justification, particularly when recruitment occurs in two different settings that may differ in baseline characteristics.

The choice to select the control group from general practitioners’ outpatient clinics was based on two considerations. First, frail patients routinely visit their general practitioner multiple times throughout the year, similarly to what occurs in the hospital setting. Second, within the organizational framework of the Italian National Health Service, general practitioners actively contribute to achieving the vaccination coverage targets established by the National Immunization Plan (PNPV) and are authorized to administer vaccines directly in their clinics, including influenza, COVID‑19, pneumococcal, and Herpes zoster vaccines.

Randomization across these two settings was not feasible due to logistical and ethical constraints; however, the quasi‑experimental design allowed us to evaluate the intervention under real‑world conditions, which was a key objective of the study. To make this aim clearer, we have revised the title accordingly (page 1, lines 1-5).

 

To address the potential for baseline imbalances between groups, we implemented several strategies beyond standard multivariable regression. These included:

1. propensity score adjustment, used to account for differences in baseline characteristics between settings;
2. testing of interaction terms to explore potential effect modification;
3. collinearity diagnostics (VIFs), which confirmed the absence of problematic multicollinearity.

These additional analyses strengthen the internal validity of the findings and support the robustness of the estimated intervention effect despite the non‑randomized design.

We have expanded the Methods (para 2.1, page 2, lines 76-82; para 2.5, page 3, lines 158-164), Results (page 11, lines 241-248) and Discussion (page 17, lines 353-356) sections to clarify these methodological considerations and to explicitly acknowledge the constraints inherent to quasi-experimental designs.

 

• Table 1 indicates several statistically significant differences between experimental and control groups (e.g., age distribution, education, working activity, comorbidities). These imbalances may confound the observed effect (OR = 38.21 for adherence). Please clarify whether interaction terms were tested and whether collinearity diagnostics were performed.

 

In response to this point, we agree that the baseline imbalances between the experimental and control groups (age, education, working activity, and comorbidities) could potentially confound the observed association with adherence. To address this, we first included these variables as covariates in the multivariable logistic regression model for adherence (Model 2). In addition, we explicitly tested interaction terms between key independent variables (including study group and major sociodemographic/clinical factors) to explore potential effect modification; no statistically significant interactions were identified.

We also assessed multicollinearity by examining variance inflation factors (VIFs) for all variables included in the multivariable models. All VIF values were below commonly accepted thresholds, indicating the absence of problematic multicollinearity and supporting the stability of the regression estimates. Finally, to further account for baseline imbalances between settings, we estimated a propensity score representing the probability of being recruited in the hospital setting and included it as an additional covariate. The propensity score was not statistically significant in the adherence model, suggesting that the strong association observed between the experimental setting and adherence is unlikely to be fully explained by baseline differences between groups.

We have clarified these points in the Statistical Analysis (para 2.5, page 4, lines 164-167), Results (page 6, lines 249-250) and Discussion (page 17, page 352-352) sections of the manuscript.

 

3) The adjusted OR for adherence in the experimental group is very large (OR = 38.21; 95% CI 12.23–119.33). While statistically significant, the wide CI suggests instability and possible sparse-data bias. Please comment on event distribution per variable in Model 2 and whether model overfitting was assessed (e.g., events-per-variable rule).

 

We thank the reviewer for this important observation. The very large adjusted OR for adherence in the experimental group reflects the markedly different distribution of events between the two settings. In Model 2, adherence to HZ vaccination was substantially higher in the experimental group, resulting in a sparse number of non‑adherent individuals in this arm. This asymmetry contributes to the wide confidence interval and may partially explain the magnitude of the effect estimate.

To address the reviewer’s concern, we examined the distribution of events per variable included in Model 2. The number of adherent cases was adequate relative to the number of predictors, and the events‑per‑variable (EPV) ratio remained above the commonly recommended thresholds for logistic regression, suggesting that model overfitting was unlikely. We also evaluated multicollinearity, and all VIF values were well below accepted cut‑offs, supporting the stability of the estimates.

Nevertheless, we acknowledge that the combination of a strong intervention effect and the limited number of non‑events in the experimental group may have contributed to the wide CI. We have added a comment in the Discussion (page 17, lines 332-350) to clarify this point and to caution readers about the interpretation of the effect size, while emphasizing the robustness of the association across adjusted models.

 

4)The sample size was calculated assuming 50% willingness, but no justification is provided for power regarding the adherence outcome (Model 2, N=171). Given the relatively small number of vaccinated individuals (n=105), please clarify whether the study was adequately powered for multivariable analysis of adherence.

 

As suggested, in addition to the sample size calculation performed for the willingness outcome, we conducted a separate power calculation specifically for the adherence outcome. For this analysis, we assumed a prevalence of adherence of 25%, which required a minimum of 59 subjects per group. To account for potential non‑participation, we added an additional 15%, resulting in a target sample of 136 participants (page 4, lines 176–179).

 

5) Several clinically relevant variables (e.g., perceived health status, number of chronic diseases, knowledge variables) were removed through backward elimination. Stepwise methods may introduce bias and model instability. Consider presenting a full model or performing robustness checks.

 

In response to the comment, we acknowledge that stepwise procedures, including backward elimination, may introduce bias and model instability. For this reason, and in line with the reviewer’s suggestion, we have additionally presented full models including all covariates without stepwise selection (Table 2). The results of the full models were consistent with those obtained using backward elimination, with no meaningful changes in the direction or magnitude of the associations. This robustness check supports the stability of our findings and indicates that the observed effects are not an artefact of the variable‑selection procedure.

Reviewer 1:

• The quasi-experimental, non-randomized design requires deeper methodological justification. Since recruitment occurred in two different settings (hospital clinic vs. GP clinics), baseline differences between groups are likely. Although multivariable regression was applied, additional strategies (e.g., propensity score adjustment or sensitivity analysis) would strengthen causal inference regarding the intervention effect.

 

In response to the comment, we fully agree that a quasi-experimental, non-randomized design requires careful methodological justification, particularly when recruitment occurs in two different settings that may differ in baseline characteristics.

The choice to select the control group from general practitioners’ outpatient clinics was based on two considerations. First, frail patients routinely visit their general practitioner multiple times throughout the year, similarly to what occurs in the hospital setting. Second, within the organizational framework of the Italian National Health Service, general practitioners actively contribute to achieving the vaccination coverage targets established by the National Immunization Plan (PNPV) and are authorized to administer vaccines directly in their clinics, including influenza, COVID‑19, pneumococcal, and Herpes zoster vaccines.

Randomization across these two settings was not feasible due to logistical and ethical constraints; however, the quasi‑experimental design allowed us to evaluate the intervention under real‑world conditions, which was a key objective of the study. To make this aim clearer, we have revised the title accordingly (page 1, lines 1-5).

 

To address the potential for baseline imbalances between groups, we implemented several strategies beyond standard multivariable regression. These included:

1. propensity score adjustment, used to account for differences in baseline characteristics between settings;
2. testing of interaction terms to explore potential effect modification;
3. collinearity diagnostics (VIFs), which confirmed the absence of problematic multicollinearity.

These additional analyses strengthen the internal validity of the findings and support the robustness of the estimated intervention effect despite the non‑randomized design.

We have expanded the Methods (para 2.1, page 2, lines 76-82; para 2.5, page 3, lines 158-164), Results (page 11, lines 241-248) and Discussion (page 17, lines 353-356) sections to clarify these methodological considerations and to explicitly acknowledge the constraints inherent to quasi-experimental designs.

 

• Table 1 indicates several statistically significant differences between experimental and control groups (e.g., age distribution, education, working activity, comorbidities). These imbalances may confound the observed effect (OR = 38.21 for adherence). Please clarify whether interaction terms were tested and whether collinearity diagnostics were performed.

 

In response to this point, we agree that the baseline imbalances between the experimental and control groups (age, education, working activity, and comorbidities) could potentially confound the observed association with adherence. To address this, we first included these variables as covariates in the multivariable logistic regression model for adherence (Model 2). In addition, we explicitly tested interaction terms between key independent variables (including study group and major sociodemographic/clinical factors) to explore potential effect modification; no statistically significant interactions were identified.

We also assessed multicollinearity by examining variance inflation factors (VIFs) for all variables included in the multivariable models. All VIF values were below commonly accepted thresholds, indicating the absence of problematic multicollinearity and supporting the stability of the regression estimates. Finally, to further account for baseline imbalances between settings, we estimated a propensity score representing the probability of being recruited in the hospital setting and included it as an additional covariate. The propensity score was not statistically significant in the adherence model, suggesting that the strong association observed between the experimental setting and adherence is unlikely to be fully explained by baseline differences between groups.

We have clarified these points in the Statistical Analysis (para 2.5, page 4, lines 164-167), Results (page 6, lines 249-250) and Discussion (page 17, page 352-352) sections of the manuscript.

 

3) The adjusted OR for adherence in the experimental group is very large (OR = 38.21; 95% CI 12.23–119.33). While statistically significant, the wide CI suggests instability and possible sparse-data bias. Please comment on event distribution per variable in Model 2 and whether model overfitting was assessed (e.g., events-per-variable rule).

 

We thank the reviewer for this important observation. The very large adjusted OR for adherence in the experimental group reflects the markedly different distribution of events between the two settings. In Model 2, adherence to HZ vaccination was substantially higher in the experimental group, resulting in a sparse number of non‑adherent individuals in this arm. This asymmetry contributes to the wide confidence interval and may partially explain the magnitude of the effect estimate.

To address the reviewer’s concern, we examined the distribution of events per variable included in Model 2. The number of adherent cases was adequate relative to the number of predictors, and the events‑per‑variable (EPV) ratio remained above the commonly recommended thresholds for logistic regression, suggesting that model overfitting was unlikely. We also evaluated multicollinearity, and all VIF values were well below accepted cut‑offs, supporting the stability of the estimates.

Nevertheless, we acknowledge that the combination of a strong intervention effect and the limited number of non‑events in the experimental group may have contributed to the wide CI. We have added a comment in the Discussion (page 17, lines 332-350) to clarify this point and to caution readers about the interpretation of the effect size, while emphasizing the robustness of the association across adjusted models.

 

4)The sample size was calculated assuming 50% willingness, but no justification is provided for power regarding the adherence outcome (Model 2, N=171). Given the relatively small number of vaccinated individuals (n=105), please clarify whether the study was adequately powered for multivariable analysis of adherence.

 

As suggested, in addition to the sample size calculation performed for the willingness outcome, we conducted a separate power calculation specifically for the adherence outcome. For this analysis, we assumed a prevalence of adherence of 25%, which required a minimum of 59 subjects per group. To account for potential non‑participation, we added an additional 15%, resulting in a target sample of 136 participants (page 4, lines 176–179).

 

5) Several clinically relevant variables (e.g., perceived health status, number of chronic diseases, knowledge variables) were removed through backward elimination. Stepwise methods may introduce bias and model instability. Consider presenting a full model or performing robustness checks.

 

In response to the comment, we acknowledge that stepwise procedures, including backward elimination, may introduce bias and model instability. For this reason, and in line with the reviewer’s suggestion, we have additionally presented full models including all covariates without stepwise selection (Table 2). The results of the full models were consistent with those obtained using backward elimination, with no meaningful changes in the direction or magnitude of the associations. This robustness check supports the stability of our findings and indicates that the observed effects are not an artefact of the variable‑selection procedure.

Reviewer 1:

• The quasi-experimental, non-randomized design requires deeper methodological justification. Since recruitment occurred in two different settings (hospital clinic vs. GP clinics), baseline differences between groups are likely. Although multivariable regression was applied, additional strategies (e.g., propensity score adjustment or sensitivity analysis) would strengthen causal inference regarding the intervention effect.

 

In response to the comment, we fully agree that a quasi-experimental, non-randomized design requires careful methodological justification, particularly when recruitment occurs in two different settings that may differ in baseline characteristics.

The choice to select the control group from general practitioners’ outpatient clinics was based on two considerations. First, frail patients routinely visit their general practitioner multiple times throughout the year, similarly to what occurs in the hospital setting. Second, within the organizational framework of the Italian National Health Service, general practitioners actively contribute to achieving the vaccination coverage targets established by the National Immunization Plan (PNPV) and are authorized to administer vaccines directly in their clinics, including influenza, COVID‑19, pneumococcal, and Herpes zoster vaccines.

Randomization across these two settings was not feasible due to logistical and ethical constraints; however, the quasi‑experimental design allowed us to evaluate the intervention under real‑world conditions, which was a key objective of the study. To make this aim clearer, we have revised the title accordingly (page 1, lines 1-5).

 

To address the potential for baseline imbalances between groups, we implemented several strategies beyond standard multivariable regression. These included:

1. propensity score adjustment, used to account for differences in baseline characteristics between settings;
2. testing of interaction terms to explore potential effect modification;
3. collinearity diagnostics (VIFs), which confirmed the absence of problematic multicollinearity.

These additional analyses strengthen the internal validity of the findings and support the robustness of the estimated intervention effect despite the non‑randomized design.

We have expanded the Methods (para 2.1, page 2, lines 76-82; para 2.5, page 3, lines 158-164), Results (page 11, lines 241-248) and Discussion (page 17, lines 353-356) sections to clarify these methodological considerations and to explicitly acknowledge the constraints inherent to quasi-experimental designs.

 

• Table 1 indicates several statistically significant differences between experimental and control groups (e.g., age distribution, education, working activity, comorbidities). These imbalances may confound the observed effect (OR = 38.21 for adherence). Please clarify whether interaction terms were tested and whether collinearity diagnostics were performed.

 

In response to this point, we agree that the baseline imbalances between the experimental and control groups (age, education, working activity, and comorbidities) could potentially confound the observed association with adherence. To address this, we first included these variables as covariates in the multivariable logistic regression model for adherence (Model 2). In addition, we explicitly tested interaction terms between key independent variables (including study group and major sociodemographic/clinical factors) to explore potential effect modification; no statistically significant interactions were identified.

We also assessed multicollinearity by examining variance inflation factors (VIFs) for all variables included in the multivariable models. All VIF values were below commonly accepted thresholds, indicating the absence of problematic multicollinearity and supporting the stability of the regression estimates. Finally, to further account for baseline imbalances between settings, we estimated a propensity score representing the probability of being recruited in the hospital setting and included it as an additional covariate. The propensity score was not statistically significant in the adherence model, suggesting that the strong association observed between the experimental setting and adherence is unlikely to be fully explained by baseline differences between groups.

We have clarified these points in the Statistical Analysis (para 2.5, page 4, lines 164-167), Results (page 6, lines 249-250) and Discussion (page 17, page 352-352) sections of the manuscript.

 

3) The adjusted OR for adherence in the experimental group is very large (OR = 38.21; 95% CI 12.23–119.33). While statistically significant, the wide CI suggests instability and possible sparse-data bias. Please comment on event distribution per variable in Model 2 and whether model overfitting was assessed (e.g., events-per-variable rule).

 

We thank the reviewer for this important observation. The very large adjusted OR for adherence in the experimental group reflects the markedly different distribution of events between the two settings. In Model 2, adherence to HZ vaccination was substantially higher in the experimental group, resulting in a sparse number of non‑adherent individuals in this arm. This asymmetry contributes to the wide confidence interval and may partially explain the magnitude of the effect estimate.

To address the reviewer’s concern, we examined the distribution of events per variable included in Model 2. The number of adherent cases was adequate relative to the number of predictors, and the events‑per‑variable (EPV) ratio remained above the commonly recommended thresholds for logistic regression, suggesting that model overfitting was unlikely. We also evaluated multicollinearity, and all VIF values were well below accepted cut‑offs, supporting the stability of the estimates.

Nevertheless, we acknowledge that the combination of a strong intervention effect and the limited number of non‑events in the experimental group may have contributed to the wide CI. We have added a comment in the Discussion (page 17, lines 332-350) to clarify this point and to caution readers about the interpretation of the effect size, while emphasizing the robustness of the association across adjusted models.

 

4)The sample size was calculated assuming 50% willingness, but no justification is provided for power regarding the adherence outcome (Model 2, N=171). Given the relatively small number of vaccinated individuals (n=105), please clarify whether the study was adequately powered for multivariable analysis of adherence.

 

As suggested, in addition to the sample size calculation performed for the willingness outcome, we conducted a separate power calculation specifically for the adherence outcome. For this analysis, we assumed a prevalence of adherence of 25%, which required a minimum of 59 subjects per group. To account for potential non‑participation, we added an additional 15%, resulting in a target sample of 136 participants (page 4, lines 176–179).

 

5) Several clinically relevant variables (e.g., perceived health status, number of chronic diseases, knowledge variables) were removed through backward elimination. Stepwise methods may introduce bias and model instability. Consider presenting a full model or performing robustness checks.

 

In response to the comment, we acknowledge that stepwise procedures, including backward elimination, may introduce bias and model instability. For this reason, and in line with the reviewer’s suggestion, we have additionally presented full models including all covariates without stepwise selection (Table 2). The results of the full models were consistent with those obtained using backward elimination, with no meaningful changes in the direction or magnitude of the associations. This robustness check supports the stability of our findings and indicates that the observed effects are not an artefact of the variable‑selection procedure.

Reviewer 1:

• The quasi-experimental, non-randomized design requires deeper methodological justification. Since recruitment occurred in two different settings (hospital clinic vs. GP clinics), baseline differences between groups are likely. Although multivariable regression was applied, additional strategies (e.g., propensity score adjustment or sensitivity analysis) would strengthen causal inference regarding the intervention effect.

 

In response to the comment, we fully agree that a quasi-experimental, non-randomized design requires careful methodological justification, particularly when recruitment occurs in two different settings that may differ in baseline characteristics.

The choice to select the control group from general practitioners’ outpatient clinics was based on two considerations. First, frail patients routinely visit their general practitioner multiple times throughout the year, similarly to what occurs in the hospital setting. Second, within the organizational framework of the Italian National Health Service, general practitioners actively contribute to achieving the vaccination coverage targets established by the National Immunization Plan (PNPV) and are authorized to administer vaccines directly in their clinics, including influenza, COVID‑19, pneumococcal, and Herpes zoster vaccines.

Randomization across these two settings was not feasible due to logistical and ethical constraints; however, the quasi‑experimental design allowed us to evaluate the intervention under real‑world conditions, which was a key objective of the study. To make this aim clearer, we have revised the title accordingly (page 1, lines 1-5).

 

To address the potential for baseline imbalances between groups, we implemented several strategies beyond standard multivariable regression. These included:

1. propensity score adjustment, used to account for differences in baseline characteristics between settings;
2. testing of interaction terms to explore potential effect modification;
3. collinearity diagnostics (VIFs), which confirmed the absence of problematic multicollinearity.

These additional analyses strengthen the internal validity of the findings and support the robustness of the estimated intervention effect despite the non‑randomized design.

We have expanded the Methods (para 2.1, page 2, lines 76-82; para 2.5, page 3, lines 158-164), Results (page 11, lines 241-248) and Discussion (page 17, lines 353-356) sections to clarify these methodological considerations and to explicitly acknowledge the constraints inherent to quasi-experimental designs.

 

• Table 1 indicates several statistically significant differences between experimental and control groups (e.g., age distribution, education, working activity, comorbidities). These imbalances may confound the observed effect (OR = 38.21 for adherence). Please clarify whether interaction terms were tested and whether collinearity diagnostics were performed.

 

In response to this point, we agree that the baseline imbalances between the experimental and control groups (age, education, working activity, and comorbidities) could potentially confound the observed association with adherence. To address this, we first included these variables as covariates in the multivariable logistic regression model for adherence (Model 2). In addition, we explicitly tested interaction terms between key independent variables (including study group and major sociodemographic/clinical factors) to explore potential effect modification; no statistically significant interactions were identified.

We also assessed multicollinearity by examining variance inflation factors (VIFs) for all variables included in the multivariable models. All VIF values were below commonly accepted thresholds, indicating the absence of problematic multicollinearity and supporting the stability of the regression estimates. Finally, to further account for baseline imbalances between settings, we estimated a propensity score representing the probability of being recruited in the hospital setting and included it as an additional covariate. The propensity score was not statistically significant in the adherence model, suggesting that the strong association observed between the experimental setting and adherence is unlikely to be fully explained by baseline differences between groups.

We have clarified these points in the Statistical Analysis (para 2.5, page 4, lines 164-167), Results (page 6, lines 249-250) and Discussion (page 17, page 352-352) sections of the manuscript.

 

3) The adjusted OR for adherence in the experimental group is very large (OR = 38.21; 95% CI 12.23–119.33). While statistically significant, the wide CI suggests instability and possible sparse-data bias. Please comment on event distribution per variable in Model 2 and whether model overfitting was assessed (e.g., events-per-variable rule).

 

We thank the reviewer for this important observation. The very large adjusted OR for adherence in the experimental group reflects the markedly different distribution of events between the two settings. In Model 2, adherence to HZ vaccination was substantially higher in the experimental group, resulting in a sparse number of non‑adherent individuals in this arm. This asymmetry contributes to the wide confidence interval and may partially explain the magnitude of the effect estimate.

To address the reviewer’s concern, we examined the distribution of events per variable included in Model 2. The number of adherent cases was adequate relative to the number of predictors, and the events‑per‑variable (EPV) ratio remained above the commonly recommended thresholds for logistic regression, suggesting that model overfitting was unlikely. We also evaluated multicollinearity, and all VIF values were well below accepted cut‑offs, supporting the stability of the estimates.

Nevertheless, we acknowledge that the combination of a strong intervention effect and the limited number of non‑events in the experimental group may have contributed to the wide CI. We have added a comment in the Discussion (page 17, lines 332-350) to clarify this point and to caution readers about the interpretation of the effect size, while emphasizing the robustness of the association across adjusted models.

 

4)The sample size was calculated assuming 50% willingness, but no justification is provided for power regarding the adherence outcome (Model 2, N=171). Given the relatively small number of vaccinated individuals (n=105), please clarify whether the study was adequately powered for multivariable analysis of adherence.

 

As suggested, in addition to the sample size calculation performed for the willingness outcome, we conducted a separate power calculation specifically for the adherence outcome. For this analysis, we assumed a prevalence of adherence of 25%, which required a minimum of 59 subjects per group. To account for potential non‑participation, we added an additional 15%, resulting in a target sample of 136 participants (page 4, lines 176–179).

 

5) Several clinically relevant variables (e.g., perceived health status, number of chronic diseases, knowledge variables) were removed through backward elimination. Stepwise methods may introduce bias and model instability. Consider presenting a full model or performing robustness checks.

 

In response to the comment, we acknowledge that stepwise procedures, including backward elimination, may introduce bias and model instability. For this reason, and in line with the reviewer’s suggestion, we have additionally presented full models including all covariates without stepwise selection (Table 2). The results of the full models were consistent with those obtained using backward elimination, with no meaningful changes in the direction or magnitude of the associations. This robustness check supports the stability of our findings and indicates that the observed effects are not an artefact of the variable‑selection procedure.

Reviewer 1:

• The quasi-experimental, non-randomized design requires deeper methodological justification. Since recruitment occurred in two different settings (hospital clinic vs. GP clinics), baseline differences between groups are likely. Although multivariable regression was applied, additional strategies (e.g., propensity score adjustment or sensitivity analysis) would strengthen causal inference regarding the intervention effect.

 

In response to the comment, we fully agree that a quasi-experimental, non-randomized design requires careful methodological justification, particularly when recruitment occurs in two different settings that may differ in baseline characteristics.

The choice to select the control group from general practitioners’ outpatient clinics was based on two considerations. First, frail patients routinely visit their general practitioner multiple times throughout the year, similarly to what occurs in the hospital setting. Second, within the organizational framework of the Italian National Health Service, general practitioners actively contribute to achieving the vaccination coverage targets established by the National Immunization Plan (PNPV) and are authorized to administer vaccines directly in their clinics, including influenza, COVID‑19, pneumococcal, and Herpes zoster vaccines.

Randomization across these two settings was not feasible due to logistical and ethical constraints; however, the quasi‑experimental design allowed us to evaluate the intervention under real‑world conditions, which was a key objective of the study. To make this aim clearer, we have revised the title accordingly (page 1, lines 1-5).

 

To address the potential for baseline imbalances between groups, we implemented several strategies beyond standard multivariable regression. These included:

1. propensity score adjustment, used to account for differences in baseline characteristics between settings;
2. testing of interaction terms to explore potential effect modification;
3. collinearity diagnostics (VIFs), which confirmed the absence of problematic multicollinearity.

These additional analyses strengthen the internal validity of the findings and support the robustness of the estimated intervention effect despite the non‑randomized design.

We have expanded the Methods (para 2.1, page 2, lines 76-82; para 2.5, page 3, lines 158-164), Results (page 11, lines 241-248) and Discussion (page 17, lines 353-356) sections to clarify these methodological considerations and to explicitly acknowledge the constraints inherent to quasi-experimental designs.

 

• Table 1 indicates several statistically significant differences between experimental and control groups (e.g., age distribution, education, working activity, comorbidities). These imbalances may confound the observed effect (OR = 38.21 for adherence). Please clarify whether interaction terms were tested and whether collinearity diagnostics were performed.

 

In response to this point, we agree that the baseline imbalances between the experimental and control groups (age, education, working activity, and comorbidities) could potentially confound the observed association with adherence. To address this, we first included these variables as covariates in the multivariable logistic regression model for adherence (Model 2). In addition, we explicitly tested interaction terms between key independent variables (including study group and major sociodemographic/clinical factors) to explore potential effect modification; no statistically significant interactions were identified.

We also assessed multicollinearity by examining variance inflation factors (VIFs) for all variables included in the multivariable models. All VIF values were below commonly accepted thresholds, indicating the absence of problematic multicollinearity and supporting the stability of the regression estimates. Finally, to further account for baseline imbalances between settings, we estimated a propensity score representing the probability of being recruited in the hospital setting and included it as an additional covariate. The propensity score was not statistically significant in the adherence model, suggesting that the strong association observed between the experimental setting and adherence is unlikely to be fully explained by baseline differences between groups.

We have clarified these points in the Statistical Analysis (para 2.5, page 4, lines 164-167), Results (page 6, lines 249-250) and Discussion (page 17, page 352-352) sections of the manuscript.

 

3) The adjusted OR for adherence in the experimental group is very large (OR = 38.21; 95% CI 12.23–119.33). While statistically significant, the wide CI suggests instability and possible sparse-data bias. Please comment on event distribution per variable in Model 2 and whether model overfitting was assessed (e.g., events-per-variable rule).

 

We thank the reviewer for this important observation. The very large adjusted OR for adherence in the experimental group reflects the markedly different distribution of events between the two settings. In Model 2, adherence to HZ vaccination was substantially higher in the experimental group, resulting in a sparse number of non‑adherent individuals in this arm. This asymmetry contributes to the wide confidence interval and may partially explain the magnitude of the effect estimate.

To address the reviewer’s concern, we examined the distribution of events per variable included in Model 2. The number of adherent cases was adequate relative to the number of predictors, and the events‑per‑variable (EPV) ratio remained above the commonly recommended thresholds for logistic regression, suggesting that model overfitting was unlikely. We also evaluated multicollinearity, and all VIF values were well below accepted cut‑offs, supporting the stability of the estimates.

Nevertheless, we acknowledge that the combination of a strong intervention effect and the limited number of non‑events in the experimental group may have contributed to the wide CI. We have added a comment in the Discussion (page 17, lines 332-350) to clarify this point and to caution readers about the interpretation of the effect size, while emphasizing the robustness of the association across adjusted models.

 

4)The sample size was calculated assuming 50% willingness, but no justification is provided for power regarding the adherence outcome (Model 2, N=171). Given the relatively small number of vaccinated individuals (n=105), please clarify whether the study was adequately powered for multivariable analysis of adherence.

 

As suggested, in addition to the sample size calculation performed for the willingness outcome, we conducted a separate power calculation specifically for the adherence outcome. For this analysis, we assumed a prevalence of adherence of 25%, which required a minimum of 59 subjects per group. To account for potential non‑participation, we added an additional 15%, resulting in a target sample of 136 participants (page 4, lines 176–179).

 

5) Several clinically relevant variables (e.g., perceived health status, number of chronic diseases, knowledge variables) were removed through backward elimination. Stepwise methods may introduce bias and model instability. Consider presenting a full model or performing robustness checks.

 

In response to the comment, we acknowledge that stepwise procedures, including backward elimination, may introduce bias and model instability. For this reason, and in line with the reviewer’s suggestion, we have additionally presented full models including all covariates without stepwise selection (Table 2). The results of the full models were consistent with those obtained using backward elimination, with no meaningful changes in the direction or magnitude of the associations. This robustness check supports the stability of our findings and indicates that the observed effects are not an artefact of the variable‑selection procedure.

Reviewer 2 Report

Comments and Suggestions for Authors

Dear authors,

Your manuscript “Adherence to Herpes Zoster Vaccination in a sample of immunocompromised and frail subjects: results of an Italian quasi-experimental study” describes the evaluation the willingness to receive the herpes zoster (HZ) vaccination, the impact of the in-hospital vaccination dedicated clinic on the HZ vaccination adherence, and the determinants of these outcomes of interest in frail immunocompromised patients in Italy.

Although it is generally clear what you did in your research, the article requires revision and cannot be published in its current form.

First, English editing is recommended.

Abstract section:

L19 – “HZ” – the full name should be given for the abbreviation used for the first time.

 

Keywords section: Please correct “Herpes Zoster” to “Herpes zoster”.

 

Introduction section:

L39-40 – “Varicella-Zoster Virus” – no need to start with capitals, please check and correct throughout the text (as well as “Varicella Zoster”).

L57-58 – “…Wang et 57 al. in a recent meta-analysis…” – the corresponding reference should be provided here.

 

Materials and methods section contains all necessary information about study and methods used.

However, in section 2.4 it would be useful to provide the questionnaire sample (as supplementary).

Section 2.5 - L147-149 – “All statistical analyses were performed by STATA software program, version 18 (Stata Corporation, College Station, Tx).” - based on the logic of the narrative, this sentence should be placed first in this section.

 

The Results section:

Table 1 requires serious revision for a clearer presentation of the data. The sample groups (line 1) are not clearly presented (Willingness to receive HZ, Adherence to HZ vaccination, especially in terms of their overlap with the control and experimental groups). What is N? The fonts differ in different parts of the table. The table is very large and poorly structured, which also makes it difficult to analyze.

Table 2 also requires revision as it is poorly structured, which also makes it difficult to analyze.

L208-209 – “were removed from the models by backward elimination procedure” - The procedure and criteria for elimination should be described.

 

Discussion section: The study has several limitations, as was as has been rightly noted. But isn't the result predictable? There remains a feeling of a lack of justification for your proposed approach. The conclusion should justify why your approach was needed and what goals you achieved with it.

 

References section – please check and correct where necessary the references according to journal’s instructions.

Author Response

Reviewer 2:

1. Abstract section:

L19 – “HZ” – the full name should be given for the abbreviation used for the first time.

As suggested, we have provided the full name in the given line (page 1, line 20).

 

2. Keywords section: Please correct “Herpes Zoster” to “Herpes zoster”.

As suggested, “Herpes zoster” has been replaced in keywords section (page 1, line 37).

 

3. Introduction section:

L39-40 – “Varicella-Zoster Virus” – no need to start with capitals, please check and correct throughout the text (as well as “Varicella Zoster”).

We revised the manuscript according to the suggestion.

 

4. L57-58 – “…Wang et 57 al. in a recent meta-analysis…” – the corresponding reference should be provided here.

As suggested, we have inserted the reference in the appropriate place (page 2, line 61).

 

5. Materials and methods section contains all necessary information about study and methods used. However, in section 2.4 it would be useful to provide the questionnaire sample (as supplementary).

As suggested, we provided the questionnaire as a Supplentary file.

 

6. Section 2.5 - L147-149 – “All statistical analyses were performed by STATA software program, version 18 (Stata Corporation, College Station, Tx).” - based on the logic of the narrative, this sentence should be placed first in this section.

As suggested, the sentence has been moved to the appropriate place (page 3, lines 126-127).

 

7. The Results section:

Table 1 requires serious revision for a clearer presentation of the data. The sample groups (line 1) are not clearly presented (Willingness to receive HZ, Adherence to HZ vaccination, especially in terms of their overlap with the control and experimental groups). What is N? The fonts differ in different parts of the table. The table is very large and poorly structured, which also makes it difficult to analyze.

Based on your suggestions, we have divided the original Table 1 into two separate tables. The first (Table 1) presents the baseline and sociodemographic characteristics of the study participants according to their willingness and adherence to HZ vaccination. The second (Table 2) reports participants’ knowledge and attitudes regarding HZ infection and vaccination, again stratified by willingness and adherence to HZ vaccination. We have also improved the formatting of both tables for greater clarity.

 

8. Table 2 also requires revision as it is poorly structured, which also makes it difficult to analyze.

L208-209 – “were removed from the models by backward elimination procedure” - The procedure and criteria for elimination should be described.

In response to this point, and consistent with the other reviewer’s comment, we re‑ran the logistic regression models without using stepwise procedures. As stated in Statistical analysis section (page 3, line 136), following the approach recommended by Hosmer and Lemeshow, we included in the multivariable model all variables that showed a p‑value < 0.25 in the univariate analyses. Accordingly, we have revised Table 3 and updated the Results section.

 

9. The English could be improved to more clearly express the research.

As suggested, we thoroughly revised the manuscript to improve the clarity of the English language.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

Thank you 

Author Response

Thank you for your positive feedback and for taking the time to review our work.

Sincerely,

Claudia Pileggi

Reviewer 2 Report

Comments and Suggestions for Authors

Dear authors,

Thank you for the revised version of the manuscript, you did a lot of work, and it is really better now.

However, some issues still need to be solved:

L20 – “Herpes Zoster” – no need to start with capitals, please correct.

L42 – “Varicella-”– no need to start with capital, please correct.

L82- “Herpes zoster” – no need to start with capital, please correct.

Section 2.2 – the reference to Supplementary for the questionnaire should be added in the section.

L240 – “,,” – please correct.

Table 3 is still large; maybe it is better to provide it as Supplementary?

References section – still needs revision, please check and correct according to Journal’s instructions.

Author Response

Reviewer 2

1.L20 – “Herpes Zoster” – no need to start with capitals, please correct.

As requested, we have corrected the capitalization (page 1, line 20).

2. L42 – “Varicella-”– no need to start with capital, please correct.

As requested, we have corrected the capitalization of varicella (page 2, line 42).

3. L82- “Herpes zoster” – no need to start with capital, please correct.

We have also corrected the capitalization in this instance (page 2, line 83).

3. Section 2.2 – the reference to Supplementary for the questionnaire should be added in the section.

We have added the reference to the supplementary material in this section (page 3, line 112).

4. L240 – “,,” – please correct.

We have corrected the typographical error by replacing the double comma with a single one (page 9, line 240).

5. Table 3 is still large; maybe it is better to provide it as Supplementary?

As suggested, we have moved Table 3 to the Supplementary material and added the corresponding reference in the appropriate place in text (page 9 line 223)

6. References section – still needs revision, please check and correct according to Journal’s instructions.

We have thoroughly reviewed the References section and corrected all entries to fully comply with the journal’s editorial guidelines.

 

 

 

 

 

 

 

 

 

Round 3

Reviewer 2 Report

Comments and Suggestions for Authors

Dear authors,

Thank you for your work on the manuscript, all my issues were solved.

I have no more comments.