Review Reports

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

I have read the manuscript and the supplementary file, and I have worked through the reported statistics independently. This is a well-designed study: the population is clearly defined, the response rate of 68.6% is strong for this kind of workforce survey, the instruments are appropriate and well documented in Table S1, and the descriptive statistics are internally consistent — the subgroup means in Tables 4 and 5 reproduce the overall means in Tables 2, 3 and 10, and the reported p-values can be reproduced from the means, standard deviations and group sizes. My concerns are almost entirely at the level of reporting, where the manuscript is not yet at the standard of the underlying work. I have organised them below.

MAJOR POINTS

1. Table 6 is missing from the manuscript. It is cited twice, for two different things: at line 227 for the correlations between age and the study variables, and at line 247 for qualitative experiences mapping onto burnout and compassion fatigue domains. The tables jump from Table 5 to Table 7. Please add the age-correlation table and correct both in-text citations.
2. The CD-RISC is used but never introduced. CD.RISC.score appears in Tables 4, 5, 7 and 12, yet Section 2.3.1 lists only the MBI-HSS-MP, AWS, ProQOL and MMD-HP, and the instrument is absent from Supplementary Table S1 and from the abbreviations list. Please add the Connor-Davidson Resilience Scale to the methods with its item count, score range, scoring and reference. I would also note that the significant difference in CD-RISC scores by years of experience in Table 5 (24.9 vs 29.2, p = 0.003) is not mentioned anywhere in the results text.
3. There are four places where the text and the tables disagree numerically:
   (a) Line 274 gives p = 0.004 for the association between moral distress and years of experience; Table 5 gives 0.001 for the same comparison.
   (b) Lines 297-298 state that each one-unit increase in emotional exhaustion corresponds to a 12% increase in the odds of leaving; the odds ratio in Table 12 is 1.14, which is 14%.
   (c) Line 299 states 3.75 times higher odds for more than one year of experience; Table 12 gives 3.24.
   (d) The same sentence describes this experience effect as "independently associated" with leaving, but the confidence interval in Table 12 is 0.88 to 12.7 with p = 0.076. This association did not reach statistical significance and should not be presented as established; please reword.
4. Please clarify whether the p-values reported in Tables 4 and 5 are raw or Benjamini-Hochberg adjusted. Section 2.3.3 states that p-values were adjusted using the Benjamini-Hochberg procedure, but if the five p-values in Table 4 are raw, applying that procedure gives an adjusted value of approximately 0.095 for the sex difference in secondary traumatic stress (raw p = 0.019), which would no longer be significant at 0.05. Since this is the manuscript's only sex-related finding, the distinction matters. Please state explicitly in each table whether values are adjusted, report adjusted values if they are not, and temper the interpretation of the sex-STS finding accordingly. For transparency I note that the findings in Table 5 (moral distress, p = 0.001; CD-RISC, p = 0.003) would survive the correction.
5. The logistic regression as reported does not match its own description. Section 2.3.3 states that the number of covariates was restricted to three to avoid overfitting, but Table 12 contains four predictors (emotional exhaustion, CD-RISC, ProQOL-STS and years working). The text at line 295 describes the model as adjusting for CD-RISC and years working, omitting STS. Section 2.3.3 also states that scales correlated at r ≥ 0.5 were not entered into the same model, yet emotional exhaustion and secondary traumatic stress — which are typically correlated above that threshold — appear together; the manuscript reports correlations with weekly hours (Table 7) but not the inter-scale correlation matrix on which this decision was based. Please report that matrix, reconcile the number of predictors with the stated rule, and complete the caption of Table 12, which currently ends mid-sentence.
6. Table 1 omits the "Yes" row for the turnover-intention item: only "No 36 (30.0%)" is shown, so the manuscript's headline finding — 70% (n = 84) having considered leaving — cannot be read from the table. Please add the row.
7. Supplementary Table S1 states that the compassion satisfaction results "will be reported in another publication," yet CS is reported in this manuscript in Tables 3, 4, 5 and 7. Please update the supplementary text. More generally, since this paper is part of the BRiC series and the CD-RISC data appear to be shared with your resilience publication (reference 20), a sentence in the methods clarifying which variables are reported first in which paper would help readers situate this article within the series.
8. The handling of missing data on the MMD-HP needs revisiting. Section 2.3.3 justifies not imputing on the grounds that the proportion of missing values was low, but 25% of participants (30/120) are missing on moral distress. At that level, selective non-response cannot be excluded — for example, if participants with higher distress were less likely to complete the 27-item measure. Please compare completers and non-completers on basic characteristics, and add this to a limitations paragraph. The manuscript currently has no limitations section; it also needs one for the cross-sectional design and for the temporality issue in the turnover analysis, where a lifetime outcome ("have you ever seriously considered leaving") is modelled from current emotional exhaustion.

MINOR POINTS

1. The sample is described three different ways: the abstract gives female n = 98 (81.7%, denominator 120), Table 1 gives 98 (82.4%, denominator 119), and line 205 gives "female (n=95, 81.9%)" — the latter is actually the gender variable (Woman), not sex. Please choose one convention and apply it consistently, and correct line 205.
2. Line 238: "p < 0.019" should read "p = 0.019".
3. Section 2.2 describes the sampling as purposive, but all 175 eligible coordinators were invited; this is a census-style approach with voluntary response, not purposive sampling. Please correct the term.
4. Table 1 reports a minimum of 0 weekly hours as coordinator; please verify this value, as it seems implausible for an active coordinator and may be a data-entry issue.
5. Lines 353-355: the claim about Iranian transplant coordinators experiencing horizontal violence is cited to reference 28, which is a meta-analysis of compassion fatigue among nurses; the correct source appears to be reference 31 (Mollazadeh et al.). The citation also appears as a run-on superscript (".28Further") inconsistent with the bracketed style used elsewhere.
6. Please state the cut-off values used to classify scores as low, moderate or high for the MBI-HSS-MP and ProQOL, with sources; they are not given in the manuscript or the supplement. Under the commonly used MBI conventions, a personal accomplishment mean of 32.1 would be classified as moderate rather than high; please verify against the cut-offs you applied.
7. The correlations interpreted directionally at lines 239-243 (r = 0.14 for weekly hours and STS; r = -0.11 for age and STS) are below your own threshold for a small effect (r = 0.1-0.3, borderline) and are not reported with p-values; given that the same paragraph describes the age correlations as nonsignificant, please either report significance for these coefficients or present them as descriptive only.
8. Line 324 is missing its final period. The abstract rounds the mean age to 42 while the text gives 41.8; Table 2's caption uses "MBI-HSS (MP)" while the text uses "MBI-HSS-MP"; AWS rows for community and values in Table 8 have no "Missing" row — if missingness was zero, please say so.
9. The AWS abbreviation is missing from the abbreviations list.
10. In Table 9, the quote from P10 contains specific personal details (a named travel destination immediately before the case described). In a workforce of 175 people this may carry some re-identification risk; I leave the judgement to the authors, but suggest reviewing whether the detail is necessary.
11. The study is described as an explanatory sequential design, but the interview guide was derived from the study constructs and literature rather than from the survey results, and data collection appears to have run concurrently. Consider either describing the design as convergent or explaining how the quantitative results informed the qualitative phase. A joint display table integrating the two strands would also strengthen the mixed-methods reporting.

Comments on the Quality of English Language

The English is generally clear and the manuscript reads well; a light edit rather than a full language revision is needed. The points below are those where the language affects precision or meaning:

The sentence at lines 293-300 runs several clauses together without punctuation ("The emotional exhaustion domain of burnout appears to be a major contributor to such feelings in a multivariable logistic regression analysis that adjusts for..."). It should be split into at least two sentences, and its content also needs the numerical corrections raised in my comments to the authors.

The caption of Table 12 ends mid-sentence ("...adjusting for CD.RISC score and years working as coordinator, higher emotional exhaustion.") and needs to be completed.

At line 355, a superscript citation fragment remains embedded in the text (".28Further"), inconsistent with the bracketed citation style used throughout; at line 324 the sentence ends without a period.

Line 238 uses "p < 0.019" where an exact value is meant ("p = 0.019").

At lines 381-383, "an interesting fact, since we actually identified moderate to high levels of work-related issue in our study population" is grammatically incomplete ("issue" should be plural) and conversational in register; consider rephrasing.

Minor consistency items: "MBI-HSS (MP)" in the Table 2 caption versus "MBI-HSS-MP" elsewhere; the abstract rounds the mean age to 42 while the results give 41.8; "Important to note that..." at line 115 lacks a subject ("It is important to note...").

Author Response

Reviewer 1 

Major Points:  

Comment 1: Table 6 is missing from the manuscript. It is cited twice, for two different things: at line 227 for the correlations between age and the study variables, and at line 247 for qualitative experiences mapping onto burnout and compassion fatigue domains. The tables jump from Table 5 to Table 7. Please add the age-correlation table and correct both in-text citations. 

Response 1: Thank you for identifying this omission. We have added Table 6, which presents the correlations between age and the selected study variables. We also reviewed both in-text references to Table 6. The citation referring to the age correlations has been retained, while the incorrect Table 6 citation in the qualitative description of burnout and compassion fatigue experiences has been removed. 

Comment 2: The CD-RISC is used but never introduced. CD.RISC.score appears in Tables 4, 5, 7 and 12, yet Section 2.3.1 lists only the MBI-HSS-MP, AWS, ProQOL and MMD-HP, and the instrument is absent from Supplementary Table S1 and from the abbreviations list. Please add the Connor-Davidson Resilience Scale to the methods with its item count, score range, scoring and reference. I would also note that the significant difference in CD-RISC scores by years of experience in Table 5 (24.9 vs 29.2, p = 0.003) is not mentioned anywhere in the results text. 

Response 2: We have revised Section 2.3.1 to introduce the 10-item Connor-Davidson Resilience Scale (CD-RISC-10). We have also added the CD-RISC-10 to Supplementary Table S1, including its item count, scoring, total score range, interpretation, and relevant references, and added CD-RISC to the list of abbreviations. In addition, we revised the Results to report the significant difference in CD-RISC scores according to years working as an OTDC. Participants who had worked as an OTDC for more than one year had significantly higher CD-RISC scores than those who had worked for one year or less (29.2 [SD = 5.47] vs. 24.9 [SD = 5.47]; Benjamini–Hochberg-adjusted p = 0.003), with a medium effect size (Cohen’s d = −0.77) (Table 5). During this revision, we also added the significant difference in moral distress scores by years working as an OTDC (p < 0.001), which had not previously been described in the Results text. Both findings are now reported in the Results and presented in Table 5. 

Comment 3: There are four places where the text and the tables disagree numerically: 
(a) Line 274 gives p = 0.004 for the association between moral distress and years of experience; Table 5 gives 0.001 for the same comparison. 
(b) Lines 297-298 state that each one-unit increase in emotional exhaustion corresponds to a 12% increase in the odds of leaving; the odds ratio in Table 12 is 1.14, which is 14%. 
(c) Line 299 states 3.75 times higher odds for more than one year of experience; Table 12 gives 3.24. 
(d) The same sentence describes this experience effect as "independently associated" with leaving, but the confidence interval in Table 12 is 0.88 to 12.7 with p = 0.076. This association did not reach statistical significance and should not be presented as established; please reword. 

Response 3: Thank you for identifying these discrepancies. We have corrected the Results to ensure consistency with the values reported in Tables 5 and 12. Specifically, the p-value for the association between moral distress and years of experience was corrected from 0.004 to 0.001; the increase in odds associated with each one-unit increase in emotional exhaustion was corrected from 12% to 14%, consistent with the OR of 1.14; and the odds ratio for coordinators with more than one year of experience was corrected from 3.75 to 3.24. We also revised the wording regarding years of experience to clarify that, although the estimated odds were higher among coordinators with more than one year of experience, this association did not reach statistical significance (OR = 3.24, 95% CI: 0.88–12.7; p = 0.076). 

Comment 4: Please clarify whether the p-values reported in Tables 4 and 5 are raw or Benjamini-Hochberg adjusted. Section 2.3.3 states that p-values were adjusted using the Benjamini-Hochberg procedure, but if the five p-values in Table 4 are raw, applying that procedure gives an adjusted value of approximately 0.095 for the sex difference in secondary traumatic stress (raw p = 0.019), which would no longer be significant at 0.05. Since this is the manuscript's only sex-related finding, the distinction matters. Please state explicitly in each table whether values are adjusted, report adjusted values if they are not, and temper the interpretation of the sex-STS finding accordingly. For transparency I note that the findings in Table 5 (moral distress, p = 0.001; CD-RISC, p = 0.003) would survive the correction. 

 

Response 4: Thank you for raising this important point. We confirmed with the statistician that the p-values reported in both Tables 4 and 5 had already been adjusted using the Benjamini–Hochberg procedure. Thus, the p = 0.019 reported for the sex difference in secondary traumatic stress (STS) is the Benjamini–Hochberg-adjusted p-value, rather than the raw p-value, and remains statistically significant. To improve transparency, we have revised the footnotes of both tables to explicitly state that the reported p-values are Benjamini–Hochberg adjusted. We also updated Table 4 to report Cohen’s d and corresponding 95% confidence intervals. The sex difference in STS showed a medium effect size (Cohen’s d = 0.639, 95% CI: 0.15–1.12), indicating that the average STS score in the female group was approximately 0.6 standard deviations higher than in the male group. This interpretation has also been added to the Results. 

Comment 5: The logistic regression as reported does not match its own description. Section 2.3.3 states that the number of covariates was restricted to three to avoid overfitting, but Table 12 contains four predictors (emotional exhaustion, CD-RISC, ProQOL-STS and years working). The text at line 295 describes the model as adjusting for CD-RISC and years working, omitting STS. Section 2.3.3 also states that scales correlated at r ≥ 0.5 were not entered into the same model, yet emotional exhaustion and secondary traumatic stress — which are typically correlated above that threshold — appear together; the manuscript reports correlations with weekly hours (Table 7) but not the inter-scale correlation matrix on which this decision was based. Please report that matrix, reconcile the number of predictors with the stated rule, and complete the caption of Table 12, which currently ends mid-sentence. 

Response 5: We have revised Section 2.3.3 and the Results to clarify the specification of the final logistic regression model. The final model included four predictors: MBI-HSS-MP Emotional Exhaustion, CD-RISC score, ProQOL-STS score, and years working as an OTDC. The Methods have been corrected accordingly, and the Results now explicitly identify all four predictors included in the model. We also clarified the criterion used to assess intercorrelations among predictors. The criterion was r > 0.5, rather than r ≥ 0.5. The correlation between MBI-HSS-MP Emotional Exhaustion and ProQOL-STS was r = 0.50 and therefore did not exceed the specified threshold. Variance inflation factors were also examined for the predictors included in the final model and were <2 for all factors, providing no indication of problematic multicollinearity. To make this assessment transparent, we have added the Pearson correlation matrix for the continuous scale predictors included in the regression model to Supplementary Material 1 (Table 2) and referenced it in Section 2.3.3. Finally, we revised the caption of Table 12 to provide a complete description of the analysis. The revised caption reads: “Multivariable logistic regression analysis of factors associated with having considered leaving the OTDC position (n = 112).” 

 Comment 6: Table 1 omits the "Yes" row for the turnover-intention item: only "No 36 (30.0%)" is shown, so the manuscript's headline finding — 70% (n = 84) having considered leaving — cannot be read from the table. Please add the row. 

Response 6: Thank you for identifying this omission. We have added the “Yes” response category to Table 1 for the item assessing whether participants had ever seriously considered leaving their current position as an organ and tissue donation coordinator. The table now reports both response categories: Yes (n = 84, 70.0%) and No (n = 36, 30.0%). 

Comment 7: Supplementary Table S1 states that the compassion satisfaction results "will be reported in another publication," yet CS is reported in this manuscript in Tables 3, 4, 5 and 7. Please update the supplementary text. More generally, since this paper is part of the BRiC series and the CD-RISC data appear to be shared with your resilience publication (reference 20), a sentence in the methods clarifying which variables are reported first in which paper would help readers situate this article within the series. 

Response 7: Thank you for highlighting this issue. We have removed the statement in Supplementary Material 1 indicating that compassion satisfaction would be reported in another publication. To improve transparency regarding the BRiC series, we have also added a statement to the Methods clarifying that resilience (CD-RISC-10) and compassion satisfaction (ProQOL-CS) data from this study population were previously reported in a publication focused specifically on resilience among Canadian OTDCs [20]. The present manuscript examines these measures within a broader analysis of work-related issues, alongside burnout, secondary traumatic stress, moral distress, and turnover intention, which were not the focus of the previous publication. 

 

Comment 8: The handling of missing data on the MMD-HP needs revisiting. Section 2.3.3 justifies not imputing on the grounds that the proportion of missing values was low, but 25% of participants (30/120) are missing on moral distress. At that level, selective non-response cannot be excluded — for example, if participants with higher distress were less likely to complete the 27-item measure. Please compare completers and non-completers on basic characteristics, and add this to a limitations paragraph. The manuscript currently has no limitations section; it also needs one for the cross-sectional design and for the temporality issue in the turnover analysis, where a lifetime outcome ("have you ever seriously considered leaving") is modelled from current emotional exhaustion. 

Response 8: We have revised the manuscript to more fully address the handling of missing MMD-HP data and the limitations of the study design. MMD-HP data were available for 90 participants, with 30 participants (25% of the quantitative sample) having missing data for this measure. Complete-case analysis was used for analyses involving moral distress. To assess the potential for selective non-response bias, we compared participants with complete MMD-HP data (n = 90) with those with missing MMD-HP data (n = 30) across available basic participant characteristics. No substantial or statistically significant differences were identified between the two groups. The results of this comparison are provided below. Nevertheless, because the reason for the missing MMD-HP data was not documented, potential bias related to missing data cannot be entirely excluded, and this has now been acknowledged in the Limitations section. We have also added a dedicated Limitations section addressing the cross-sectional study design and the temporality of the turnover analysis. Specifically, the outcome of having ever seriously considered leaving the OTDC position reflects a prior or lifetime experience, whereas emotional exhaustion and the other work-related measures were assessed at the time of the survey. Therefore, the temporal sequence between these variables cannot be established, and the regression findings are interpreted as associations rather than causal effects. 

 

Minor Points:  

Comment 9: The sample is described three different ways: the abstract gives female n = 98 (81.7%, denominator 120), Table 1 gives 98 (82.4%, denominator 119), and line 205 gives "female (n=95, 81.9%)" — the latter is actually the gender variable (Woman), not sex. Please choose one convention and apply it consistently, and correct line 205. 

Response 9: Thank you for identifying this inconsistency. We have standardized the reporting of participant sex across the manuscript. The Abstract and Results now consistently report that 98 participants were female (82.4%), in accordance with Table 1. We also corrected the statement previously reporting “female (n = 95, 81.9%),” which corresponded to the gender variable rather than sex. 

Comment 10: Line 238: "p < 0.019" should read "p = 0.019". 

Response 10: Thank you for identifying this error. We have corrected “p < 0.019” to “p = 0.019” in the Results section. 

Comment 11: Section 2.2 describes the sampling as purposive, but all 175 eligible coordinators were invited; this is a census-style approach with voluntary response, not purposive sampling. Please correct the term. 

Response 11: The type of sampling is correct and aligned with the definition of purposeful sampling of  Palinkas and colleagues (2015): “To identify and select all cases that meet some predetermined criterion of importance” therefore no changes have been made to the sampling format. 

Comment 12: Table 1 reports a minimum of 0 weekly hours as coordinator; please verify this value, as it seems implausible for an active coordinator and may be a data-entry issue. 

Response 12: We verified the source data and confirmed that the value of 0 weekly hours was reported by one participant in response to the question regarding the number of hours worked per week as an OTDC. Therefore, the value reported in Table 1 reflects the participant’s recorded response rather than a data-entry or coding error. We do not have additional information to determine why this participant reported 0 weekly hours. 

Comment 13: Lines 353-355: the claim about Iranian transplant coordinators experiencing horizontal violence is cited to reference 28, which is a meta-analysis of compassion fatigue among nurses; the correct source appears to be Mollazadeh et al. The citation also appears as a run-on superscript (".28Further") inconsistent with the bracketed style used elsewhere. 

Response 13: We have corrected the citation regarding horizontal violence among Iranian transplant coordinators from reference 28 to reference 31 (Mollazadeh et al.) and corrected the citation formatting to ensure consistency with the reference style used throughout the manuscript. 

Comment 14: Please state the cut-off values used to classify scores as low, moderate or high for the MBI-HSS-MP and ProQOL, with sources; they are not given in the manuscript or the supplement. Under the commonly used MBI conventions, a personal accomplishment mean of 32.1 would be classified as moderate rather than high; please verify against the cut-offs you applied. 

Response 14: Thank you for catching this error. We completely agree with your observation. We misapplied the interpretation of the Personal Accomplishment (PA) subscale by failing to account for its inverse scoring directionality (where lower scores indicate lower professional fulfillment and higher burnout risk). A mean score of 32.1 indeed falls into the Moderate classification rather than "High". We have verified our thresholds and updated the manuscript text to reflect this correction. Per your request, the exact cut-off values and their corresponding authoritative sources for both instruments have been added to the Methods section and are outlined below.1. Maslach Burnout Inventory for Medical Professionals (MBI-HSS-MP) Cut-off Values. The scoring thresholds are based on the historical, widely utilized population tertiles established in the MBI Manual (3rd Edition). Note that the 4th Edition (2016) transitioned toward a continuous Z-score profile framework, but these traditional sum-total brackets remain standard in clinical literature for categorical risk stratification: 

Subscale Dimension	Low	Moderate	High
Emotional Exhaustion (EE)	0 – 16	17 – 26	≥ 27
Depersonalization (DP)	0 – 6	7 – 12	≥ 13
Personal Accomplishment (PA)*	≥ 39	32 – 38	0 – 31

*Note: PA is inversely scored. Lower scores reflect a higher degree of burnout. 

Alternatively, we could present in the discussion section the results of this study and demonstrate where it sits when comparing to similar populations; if the editors could kindly let us know if this approach is preferred we would be happy to updated the section accordingly.  

Source: Maslach, C., Jackson, S. E., & Leiter, M. P. (1996). Maslach Burnout Inventory Manual (3rd ed.). Palo Alto, CA: Consulting Psychologists Press. 

Regarding the ProQOL comment we have verified our data classification against the official scoring guidelines for the Professional Quality of Life Scale (ProQOL-5). The coordinators' mean Burnout (BO) score of 27.6 (SD = 6.07) is accurately classified as moderate. 

According to The Concise ProQOL Manual, the instrument utilizes a percentile-based raw scoring threshold system (ranging from 10 to 50) to categorize scores into low, average/moderate, and high tiers. A raw score between 23 and 41 represents the average or moderate level of burnout. Because our sample mean of 27.6 falls directly within this bracket, our original interpretation stands, and no text changes were required for this metric. 

To ensure full transparency for the reader, we have added the official ProQOL-5 threshold brackets and source citation to the manuscript (Methods Section 2.3.1 / Supplementary Material Appendix 1), as outlined below: 

ProQOL Subscale (Raw Score Range: 10–50)	Low	Moderate (Average)	High
Compassion Satisfaction (CS)	≤ 22	23 – 41	≥ 42
Burnout (BO)	≤ 22	23 – 41	≥ 42
Secondary Traumatic Stress (STS)	≤ 22	23 – 41	≥ 42

• Source: Stamm, B. H. (2010). The Concise ProQOL Manual (2nd ed.). Pocatello, ID: ProQOL.org. 

 

 

Comment 15: The correlations interpreted directionally at lines 239-243 (r = 0.14 for weekly hours and STS; r = -0.11 for age and STS) are below your own threshold for a small effect (r = 0.1-0.3, borderline) and are not reported with p-values; given that the same paragraph describes the age correlations as nonsignificant, please either report significance for these coefficients or present them as descriptive only. 

Response 15: We have revised the Results to clarify that the correlations between age and the selected study variables and between weekly hours worked as an OTDC and the selected study variables are presented descriptively. We also removed the directional interpretation of the correlations between weekly hours and STS (r = 0.14) and between age and STS (r = −0.11) to avoid implying statistical significance in the absence of reported p-values. 

Comment 16: Line 324 is missing its final period. The abstract rounds the mean age to 42 while the text gives 41.8; Table 2's caption uses "MBI-HSS (MP)" while the text uses "MBI-HSS-MP"; AWS rows for community and values in Table 8 have no "Missing" row — if missingness was zero, please say so. 

Response 16: We have addressed all four points. A final period was added to the sentence at line 324; the mean age reported in the Abstract was revised from 42.0 to 41.8 years to ensure consistency with the Results; the MBI nomenclature in Table 2 was standardized to MBI-HSS-MP; and “Missing: 0 (0%)” was added for the AWS Community and Values domains in Table 8 to clarify that there were no missing responses for these domains. 

Comment 17: The AWS abbreviation is missing from the abbreviations list. 

Response 17: We have added “AWS: Areas of Worklife Survey” to the list of abbreviations. 

Comment 18: In Table 9, the quote from P10 contains specific personal details (a named travel destination immediately before the case described). In a workforce of 175 people this may carry some re-identification risk; I leave the judgement to the authors, but suggest reviewing whether the detail is necessary. 

Response 18: Thank you for raising this important consideration. We have anonymized the specific travel destination in the P10 quotation in Table 9 to reduce the potential risk of participant re-identification while preserving the meaning and context of the quotation. 

Comment 19: The study is described as an explanatory sequential design, but the interview guide was derived from the study constructs and literature rather than from the survey results, and data collection appears to have run concurrently. Consider either describing the design as convergent or explaining how the quantitative results informed the qualitative phase. A joint display table integrating the two strands would also strengthen the mixed-methods reporting. 

Response 19: We have revised the Methods to more clearly explain the sequential connection between the quantitative and qualitative phases and to clarify our use of an explanatory sequential mixed-methods (QUAN-qual) design. The quantitative survey was conducted first and given priority in addressing the study aims. Findings from the quantitative survey informed the development of the semi-structured interview guide, allowing the subsequent qualitative phase to further explore and contextualize the quantitative findings. Participants for the qualitative phase were recruited from survey respondents who expressed interest in participating in an interview. Quantitative and qualitative findings were subsequently integrated during the interpretation phase. We have revised the Design and qualitative Data Analysis sections to make these points of connection and integration explicit. 

Comments on the Quality of English Language 

The English is generally clear and the manuscript reads well; a light edit rather than a full language revision is needed. The points below are those where the language affects precision or meaning: 

The sentence at lines 293-300 runs several clauses together without punctuation ("The emotional exhaustion domain of burnout appears to be a major contributor to such feelings in a multivariable logistic regression analysis that adjusts for..."). It should be split into at least two sentences, and its content also needs the numerical corrections raised in my comments to the authors. 

The caption of Table 12 ends mid-sentence ("...adjusting for CD.RISC score and years working as coordinator, higher emotional exhaustion.") and needs to be completed. 

At line 355, a superscript citation fragment remains embedded in the text (".28Further"), inconsistent with the bracketed citation style used throughout; at line 324 the sentence ends without a period. 

Line 238 uses "p < 0.019" where an exact value is meant ("p = 0.019"). 

At lines 381-383, "an interesting fact, since we actually identified moderate to high levels of work-related issue in our study population" is grammatically incomplete ("issue" should be plural) and conversational in register; consider rephrasing. 

Minor consistency items: "MBI-HSS (MP)" in the Table 2 caption versus "MBI-HSS-MP" elsewhere; the abstract rounds the mean age to 42 while the results give 41.8; "Important to note that..." at line 115 lacks a subject ("It is important to note..."). 

Response:  

• We have revised this paragraph by dividing the original sentence into shorter sentences to improve clarity and readability. We also incorporated the numerical corrections noted in the comments above and revised the wording to accurately reflect the nonsignificant association between years of experience and turnover intention. 

• We have revised the caption of Table 12 to provide a complete description of the analysis. The revised caption now reads: “Multivariable logistic regression analysis of factors associated with having considered leaving the OTDC position (n = 112).” 

• We have corrected the citation formatting at line 355 and added the missing period to the sentence at line 324. 

• We have corrected “p < 0.019” to “p = 0.019” in the Results section. 

• We have revised this sentence to improve grammatical accuracy and academic tone. The revised text now reads: “This finding is noteworthy, given the moderate to high levels of work-related issues identified in our study population.” 

• We have standardized the MBI nomenclature to “MBI-HSS-MP” in Table 2, revised the mean age in the Abstract from 42 to 41.8 years to ensure consistency with the Results, and corrected “Important to note that” to “It is important to note that” for grammatical completeness. 

 

   

 

Reviewer 2 Report

Comments and Suggestions for Authors

 

1. Abstract

 

The abstract provides a reasonably good visual summary of the study; however, several issues require revision.

 

Comment 1 – Abstract, Results:

The percentages and sample characteristics reported in the abstract are not entirely consistent with Table 1. The abstract reports female sex as n=98; 81.7%, whereas Table 1 shows 98 (82.4%) for Sex and 95 (81.9%) for Gender. The authors should clarify what is meant by sex versus gender and ensure that the numbers in the abstract and the table are aligned.

 

Comment 2 – Abstract, Conclusion:

The conclusion in the abstract moves rather strongly from observational findings toward policy recommendations. Given the cross-sectional design, it would be more appropriate to describe the observed relationships as associations and avoid any causal language.

 

Comment 3 – Abstract, Methods:

The type of mixed-methods design should be reported more precisely and consistently. The manuscript text mentions a "QUAN-qual explanatory sequential study." Therefore, this exact term should be used in the abstract as well to ensure accuracy and consistency.

 

 

 

2. Introduction

 

The introduction is generally logical and well-argued, explaining the importance of the occupational/psychosocial burden in this professional group. However:

 

Comment 4 – Introduction, final paragraph:

The authors state that this is the "first national mixed-methods study." This is an important claim and should be supported by a brief explanation of the gap in previous literature and the specific differences between this study and earlier BRiC studies, especially given that several previous papers by this same research group from the BRiC program appear in References 19–23.

 

Comment 5 – Introduction:

Given that the present article is part of a larger research program, it should be made clearer exactly what new question or contribution this paper offers compared to previous studies from the same program. Otherwise, there is a risk of conceptual overlap with earlier publications.

 

Comment 6 – Introduction:

Definitions of burnout, compassion fatigue, and moral distress are provided, but the conceptual distinctions between these constructs could be somewhat clearer, especially since several different instruments have been used to measure them.

 

 

 

3. Methods

 

This is the most important section requiring revision.

 

3-1. Sampling Contradiction

 

Comment 7 – Section 2.2, Setting and Sample:

The authors describe the sampling method as "purposive sampling," but at the same time state that all coordinators in all Canadian ODOs were invited to participate. This approach is more akin to a census or invitation of the eligible population rather than purposive sampling. The authors should clearly explain the logic of their sampling strategy and correct the terminology accordingly.

 

3-2. Qualitative Sample

 

Comment 8 – Section 2.4.1:

For the qualitative part, participants were selected "in the order of their requests." This method can introduce self-selection bias and may limit the representativeness of different perspectives. The authors should explain why this method was chosen, describe the characteristics of the qualitative sample (e.g., province, years of experience, gender), and indicate whether diversity in these characteristics was considered.

 

3-3. Data Saturation

 

Comment 9 – Section 2.4.1:

The claim of achieving "data saturation" is made, but the practical criteria for reaching saturation are not explained. It is necessary to specify how saturation was assessed and at what point the researchers concluded that additional interviews would not yield new information.

 

3-4. Qualitative Rigor

 

Comment 10 – Section 2.4.2:

The qualitative analysis was conducted primarily by one researcher, and the framework was subsequently peer-reviewed by two other members. This process should be reported in greater detail, including the role of each analyst, how disagreements were resolved, reflexivity, and steps taken to enhance credibility and dependability. The authors also explicitly state that member checking was not performed.

 

3-5. Researcher Relationship with the Organization

 

Comment 11 – Section 2.4.1:

Given that some authors are affiliated with Canadian Blood Services and the study was conducted in partnership with this organization, the authors should explain how this affiliation might have influenced recruitment, participant responsiveness, or qualitative interviews, and what measures were taken to reduce potential response or social desirability bias. This is particularly relevant for a study on burnout, moral distress, and intention to leave.

 

3-6. Missing Data

 

Comment 12 – Section 2.3.3:

Although the authors report missing data, the proportion of missingness is relatively substantial for some variables; for example, the MMD-HP has 25% missing data. It should therefore be explained whether missingness was related to respondent characteristics and whether complete-case analysis could introduce bias.

 

3-7. Very Important Statistical Issue

 

Comment 13 – Section 2.3.3 and Table 12:

The logistic regression model requires serious revision. The Methods state that the number of outcome events was n=36, and therefore the number of covariates was limited to three variables. However, in Table 1, the number of individuals who reported considering leaving is 84, with only 36 responding "No." Therefore, it is unclear how the event in the logistic regression was actually defined. The authors should explicitly state the outcome coding and revise the rationale regarding the number of events per covariate.

 

 

 

4. Results

 

4-1. Most Important Contradiction in the Paper

 

Comment 14 – Section 3.5, paragraph preceding Table 12:

The Results text states that working more than one year was associated with 3.75 times higher odds of leaving. However, Table 12 reports an OR = 3.24, 95% CI = 0.88–12.7, p = 0.076. This result is numerically and statistically inconsistent with the text and must be corrected. Moreover, the CI includes 1, and p > 0.05, indicating that this variable is not statistically significant in the final model. This must be corrected in the Abstract, Results, and Discussion.

 

This is the most important comment in my review.

 

4-2. Interpretation of OR for Emotional Exhaustion

 

Comment 15 – Section 3.5/Table 12:

The OR = 1.14 for emotional exhaustion should be interpreted more precisely. While the statement "12% increase in the odds" is statistically acceptable, it would be better to specify the unit of increase and clarify that this OR corresponds to a one-point increase in the MBI-HSS-MP EE score.

 

4-3. Incomplete Reporting of the Model

 

Comment 16 – Table 12:

To assess the quality of the logistic regression, it would be better to report the number of observations included in the model, the number of missing observations, the outcome coding, model fit statistics, and, if possible, measures such as AIC or other appropriate indicators of model performance.

 

4-4. Interpretation of Multiple Testing

 

Comment 17 – Results:

The authors explain the use of the Benjamini–Hochberg correction, but it is unclear whether all p-values in the tables are reported after correction or only for certain analyses. This should be clarified.

 

4-5. Gender Differences in STS

 

Comment 18 – Section 3.2:

In the sex comparison, STS differs significantly between women and men (p=0.019), while the male group comprises only 21 individuals. In addition to the p-value, it would be better to report the effect size and confidence interval, and to interpret the result with caution.

 

4-6. Moral Distress Findings

 

Comment 19 – Section 3.4:

Given the 25% missing data for the MMD-HP, conclusions regarding the level of moral distress should be drawn with greater caution. Furthermore, it is unclear on what basis the threshold for the term "moderate level" was determined.

 

 

 

5. Discussion and Conclusion

 

Comment 20 – Discussion:

The discussion is appropriate in linking findings to previous studies, but in some places it moves from association toward causal interpretation. The authors themselves correctly note that causal inference is not possible due to the cross-sectional design; this limitation should be consistently observed throughout the Discussion and Conclusion.

 

Comment 21 – Discussion:

The results show a small positive association between weekly hours and emotional exhaustion (r=0.25). Therefore, wording such as workload "causes" burnout should be avoided, and "was associated with" should be used instead.

 

Comment 22 – Discussion:

The recommendations regarding government investment, standardization, and staffing are practically significant, but it should be clarified which recommendations are directly supported by the study data and which are more expert/policy implications.

 

Comment 23 – Limitations:

Limitations are not presented independently and sufficiently in the Discussion. It is suggested that limitations be explicitly added, including:

 

- Cross-sectional design;

- Inability to infer causality;

- Self-reported measures;

- Self-selection in interviews;

- Potential selection/non-response bias;

- 25% missingness in the MMD-HP;

- Lack of member checking;

- Affiliation of some researchers with the relevant organization;

- Limited generalizability to other countries and organ donation systems.

 

Comment 24 – Conclusion:

The conclusion is rather lengthy and somewhat policy-oriented. It would be better to focus the conclusion directly on the main findings and align the implementation recommendations with the level of evidence provided by the study.

 

 

 

6. References

 

Comment 25:

The reference list is generally relevant and reasonably up-to-date; the inclusion of 2024 and 2025 sources is a strength. However, since the paper is part of the BRiC research program, a notable number of references (19–23) belong to this same research group. This is not a problem in itself, but the authors should ensure that the main claims of the paper do not rely solely on their own work.

 

Comment 26:

In the Discussion, one instance of "28Further" appears, which is clearly a formatting/citation error that needs correction.

 

Comment 27:

The references should be thoroughly checked for consistency in DOI, URL, punctuation, and final formatting. In particular, web references and DOIs should be formatted exactly according to the journal's style guide.

 

 

Overall Recommendation: Major Revision

This manuscript addresses an important and insufficiently studied occupational health issue among Canadian organ donation coordinators and has several strengths, including the national scope, use of validated instruments, integration of quantitative and qualitative data, and the practical relevance of the findings. However, several issues require substantial clarification before the manuscript can be considered for publication.

The most important concern is the internal inconsistency in the multivariable logistic regression results. The text reports that working for more than one year was associated with 3.75-fold higher odds of leaving the position, whereas Table 12 reports an OR of 3.24 (95% CI: 0.88–12.7; p=0.076), which is not statistically significant. The definition of the regression outcome and the statement that there were only 36 outcome events also need clarification because 84 participants reported having considered leaving their position. In addition, the sampling strategy for the qualitative component, the justification for saturation, handling of missing data, qualitative rigor, and the potential influence of researchers’ organizational affiliations require further explanation.

I therefore recommend Major Revision. The study has sufficient scientific and practical merit to justify revision, but the statistical reporting and methodological clarification should be addressed carefully before the manuscript can be considered further.

 

 

 

 

Author Response

Reviewer 2 

Comment 1: The percentages and sample characteristics reported in the abstract are not entirely consistent with Table 1. The abstract reports female sex as n=98; 81.7%, whereas Table 1 shows 98 (82.4%) for Sex and 95 (81.9%) for Gender. The authors should clarify what is meant by sex versus gender and ensure that the numbers in the abstract and the table are aligned. 

Response 1: We have revised the Abstract to report female sex as n = 98 (82.4%), consistent with Table 1. We have also clarified in Table 1 that sex and gender were collected as separate self-reported demographic variables, with sex referring to sex assigned at birth and gender referring to self-identified gender. Percentages are based on the available responses for each variable. 

Comment 2: The conclusion in the abstract moves rather strongly from observational findings toward policy recommendations. Given the cross-sectional design, it would be more appropriate to describe the observed relationships as associations and avoid any causal language. 

Response 2: Thank you for this important observation. We have revised the Abstract conclusion to better reflect the observational and cross-sectional nature of the study. Specifically, we have tempered the policy and intervention recommendations and used more cautious language to avoid implying causal relationships. The revised conclusion now frames organizational and individual-level strategies as potential considerations arising from the observed findings rather than as interventions demonstrated to produce specific outcomes. 

Comment 3: The type of mixed-methods design should be reported more precisely and consistently. The manuscript text mentions a "QUAN-qual explanatory sequential study." Therefore, this exact term should be used in the abstract as well to ensure accuracy and consistency. 

Response 3: We have revised the terminology used to describe the mixed-methods design to ensure precision and consistency throughout the manuscript. The study is now consistently described as an “explanatory sequential mixed-methods (QUAN-qual) design” in both the Abstract and Methods. The quantitative survey was conducted first and given priority, and its findings informed the development of the semi-structured interview guide for the subsequent qualitative phase. The qualitative findings were then used to further explore and contextualize the quantitative findings, with both strands integrated during the interpretation phase. 

Comment 4: The authors state that this is the "first national mixed-methods study." This is an important claim and should be supported by a brief explanation of the gap in previous literature and the specific differences between this study and earlier BRiC studies, especially given that several previous papers by this same research group from the BRiC program appear in References 19–23. 

Response 4: We have removed the claim that this is the “first national mixed-methods study” from the Highlights, given that previous publications from the BRiC research program have also used national mixed-methods approaches. We have also revised the final paragraph of the Introduction to better contextualize the present study within the BRiC program and distinguish it from previous publications. 

Comment 5: Given that the present article is part of a larger research program, it should be made clearer exactly what new question or contribution this paper offers compared to previous studies from the same program. Otherwise, there is a risk of conceptual overlap with earlier publications. 

Response 5: We have revised the Introduction to explicitly acknowledge that previous BRiC studies examined specific aspects of OTDCs’ experiences, including resilience and compassion satisfaction, the impact of the COVID-19 pandemic, and experiences related to complex donation cases. We now clarify that the present study extends this work by examining a broader range of work-related issues, including burnout, compassion fatigue, moral distress, and turnover intention, as well as factors associated with these outcomes. 

Comment 6: Definitions of burnout, compassion fatigue, and moral distress are provided, but the conceptual distinctions between these constructs could be somewhat clearer, especially since several different instruments have been used to measure them. 

Response 6: We have revised the Introduction to more clearly distinguish these constructs. Specifically, we clarified that burnout is associated with chronic workplace stress and emotional exhaustion, whereas compassion fatigue reflects the emotional strain associated with repeated exposure to others’ suffering. This distinction also helps clarify the rationale for assessing these work-related constructs separately. 

Comment 7: The authors describe the sampling method as "purposive sampling," but at the same time state that all coordinators in all Canadian ODOs were invited to participate. This approach is more akin to a census or invitation of the eligible population rather than purposive sampling. The authors should clearly explain the logic of their sampling strategy and correct the terminology accordingly. 

Response 7: The type of sampling is correct and aligned with the definition of purposeful sampling of  Palinkas and colleagues (2015): “To identify and select all cases that meet some predetermined criterion of importance”; therefore, no changes have been made to the sampling format. 

Comment 8: For the qualitative part, participants were selected "in the order of their requests." This method can introduce self-selection bias and may limit the representativeness of different perspectives. The authors should explain why this method was chosen, describe the characteristics of the qualitative sample (e.g., province, years of experience, gender), and indicate whether diversity in these characteristics was considered. 

Response 8: We acknowledge that this voluntary recruitment approach may have introduced self-selection bias. Participants who expressed interest in the qualitative phase were contacted in the order in which they responded. We have clarified in Section 2.4.1 that this pragmatic approach was based on participants’ expressed willingness to participate and that no demographic quotas or stratified selection criteria were applied. We also expanded the description of the qualitative sample in the Results to provide relevant participant characteristics, including years of experience, nursing education, critical care background, and employment status. Province-level information was not reported to protect participant confidentiality. 

Comment 9: The claim of achieving "data saturation" is made, but the practical criteria for reaching saturation are not explained. It is necessary to specify how saturation was assessed and at what point the researchers concluded that additional interviews would not yield new information. 

Response 9: We have revised Section 2.4.1 to clarify the relationship between qualitative recruitment and data saturation. All 39 survey respondents who expressed interest in participating in the qualitative phase were interviewed; therefore, the final qualitative sample size was not determined by reaching a predetermined saturation threshold. Data collection and analysis occurred concurrently, allowing the research team to assess emerging findings throughout the interview process. Recurring patterns were identified across participants’ accounts, with later interviews yielding little substantively new information relevant to the study objectives. No predetermined numerical threshold was used to determine the qualitative sample size. We have revised the Methods to make this distinction explicit and to avoid implying that recruitment ceased because saturation had been reached. 

Comment 10: The qualitative analysis was conducted primarily by one researcher, and the framework was subsequently peer-reviewed by two other members. This process should be reported in greater detail, including the role of each analyst, how disagreements were resolved, reflexivity, and steps taken to enhance credibility and dependability. The authors also explicitly state that member checking was not performed. 

Response 10: We have expanded Section 2.4.2 to provide additional detail on the qualitative analytical process and the strategies used to enhance rigor. We clarified the roles of the researchers involved in the analysis, including the primary analysis conducted by A.S. and the subsequent review of the coding framework and categories by A.R. and V.S.S. Differences in coding or interpretation were discussed among the three researchers and resolved through consensus. We also clarified that reflexive field notes and memos were maintained throughout data collection and analysis and that team-based discussions were used to support the credibility and dependability of the analytical process. We retained the statement that transcripts were not returned to participants for member checking to transparently report this aspect of the study. This was a deliberate decision by the research team to avoid adding to the workload of a study population already experiencing substantial occupational demands. 

Comment 11: Given that some authors are affiliated with Canadian Blood Services and the study was conducted in partnership with this organization, the authors should explain how this affiliation might have influenced recruitment, participant responsiveness, or qualitative interviews, and what measures were taken to reduce potential response or social desirability bias. This is particularly relevant for a study on burnout, moral distress, and intention to leave. 

Response 11: We have expanded Section 2.4.1 to clarify the organizational affiliations of members of the research team and the measures taken to minimize their potential influence on participation and interview responses. Participation was voluntary, and participants were informed that their responses would remain confidential and would not be shared individually with their employer or ODO. The interviewers did not have a supervisory relationship with participants and maintained a neutral approach during the interviews. Recruitment was facilitated by the Organ Donation Organizations, and Canadian Blood Services had no influence on individual participants’ decisions to participate. These procedures were intended to reduce the potential influence of organizational affiliations on participants’ willingness to discuss sensitive work-related experiences. 

Comment 12: Although the authors report missing data, the proportion of missingness is relatively substantial for some variables; for example, the MMD-HP has 25% missing data. It should therefore be explained whether missingness was related to respondent characteristics and whether complete-case analysis could introduce bias. 

Response 12: As detailed in our response to Reviewer 1, Comment 8, we compared participants with complete MMD-HP data (n = 90) with those with missing MMD-HP data (n = 30) across available basic participant characteristics. No substantial or statistically significant differences were identified between the groups. Complete-case analysis was used for analyses involving the MMD-HP. Based on the characteristics examined, we found no evidence that participants with missing MMD-HP data differed systematically from those with complete data, suggesting that complete-case analysis was unlikely to introduce substantial selective non-response bias with respect to these measured characteristics. However, because the reason for the missing MMD-HP data was not documented, the possibility of bias due to unmeasured differences cannot be excluded. We have revised the Limitations section accordingly. Please see our response to Reviewer 1, Comment 8, for the full comparison table. 

Comment 13: The logistic regression model requires serious revision. The Methods state that the number of outcome events was n=36, and therefore the number of covariates was limited to three variables. However, in Table 1, the number of individuals who reported considering leaving is 84, with only 36 responding "No." Therefore, it is unclear how the event in the logistic regression was actually defined. The authors should explicitly state the outcome coding and revise the rationale regarding the number of events per covariate. 

Response 13: We have revised the Methods to explicitly state the coding of the logistic regression outcome. The outcome was having ever seriously considered leaving the current OTDC position and was coded as 1 = Yes and 0 = No. As reported in Table 1 for the overall sample, 84 participants (70%) responded “Yes” and 36 (30%) responded “No.” Because the smaller outcome category comprised 36 participants, we used this category as the limiting consideration when determining the number of predictors that could be included without overfitting. Accordingly, the final model was restricted to four predictors. The final regression model was based on complete cases (n = 112), with eight participants excluded due to missing data in at least one predictor. 

Comment 14: The Results text states that working more than one year was associated with 3.75 times higher odds of leaving. However, Table 12 reports an OR = 3.24, 95% CI = 0.88–12.7, p = 0.076. This result is numerically and statistically inconsistent with the text and must be corrected. Moreover, the CI includes 1, and p > 0.05, indicating that this variable is not statistically significant in the final model. This must be corrected in the Abstract, Results, and Discussion. 

Response 14: Thank you for identifying this inconsistency. We have corrected the Results to report the estimate presented in Table 12 (OR = 3.24, 95% CI: 0.88–12.7; p = 0.076) and clarified that the association between working more than one year as an OTDC and turnover intention did not reach statistical significance. We also reviewed the Abstract and Discussion to ensure that this finding was not reported or interpreted as statistically significant. 

Comment 15: The OR = 1.14 for emotional exhaustion should be interpreted more precisely. While the statement "12% increase in the odds" is statistically acceptable, it would be better to specify the unit of increase and clarify that this OR corresponds to a one-point increase in the MBI-HSS-MP EE score. 

Response 15:  We have revised the interpretation of the odds ratio for emotional exhaustion to specify the unit of increase. The Results now clarify that each one-point increase in the MBI-HSS-MP Emotional Exhaustion score was associated with a 14% increase in the odds of having considered leaving the OTDC position (OR = 1.14, 95% CI: 1.08–1.21; p < 0.001).  

Comment 16: To assess the quality of the logistic regression, it would be better to report the number of observations included in the model, the number of missing observations, the outcome coding, model fit statistics, and, if possible, measures such as AIC or other appropriate indicators of model performance. 

Response 16: We have revised the Methods and Table 12 to provide additional information regarding the logistic regression analysis. We now report the number of participants included in the final model (n = 112), the number excluded due to missing data in at least one predictor (n = 8), and the outcome coding (1 = Yes; 0 = No). We also report model fit and performance statistics, including the log-likelihood, AIC, BIC, Tjur R², AUC, and RMSE. These revisions provide a more complete assessment of the specification and performance of the final logistic regression model. 

Comment 17: The authors explain the use of the Benjamini–Hochberg correction, but it is unclear whether all p-values in the tables are reported after correction or only for certain analyses. This should be clarified. 

Response 17: To clarify, the Benjamini–Hochberg correction was applied to p-values from the bivariate group comparisons conducted using independent-samples t-tests and one-way ANOVA F-tests. The p-values reported for these comparisons are therefore adjusted p-values, as indicated in the corresponding table footnotes. Tables presenting descriptive statistics or Pearson correlation coefficients do not report p-values and were not subject to this correction. 

Comment 18: In the sex comparison, STS differs significantly between women and men (p=0.019), while the male group comprises only 21 individuals. In addition to the p-value, it would be better to report the effect size and confidence interval, and to interpret the result with caution. 

Response 18: We have added the effect size and corresponding 95% confidence interval for the sex difference in STS to Table 4 and the Results section. Female participants reported higher STS scores than male participants (27.3 [SD = 6.95] vs. 22.8 [SD = 7.63]), with a medium effect size (Cohen’s d = 0.639, 95% CI: 0.15–1.12). The Benjamini–Hochberg-adjusted p-value was 0.019. Given the relatively small number of male participants (n = 21), we have also revised the Results to emphasize that this finding should be interpreted with caution. 

Comment 19: Given the 25% missing data for the MMD-HP, conclusions regarding the level of moral distress should be drawn with greater caution. Furthermore, it is unclear on what basis the threshold for the term "moderate level" was determined. 

Response 19: We agree that the findings regarding moral distress should be interpreted with greater caution given the proportion of missing MMD-HP data. We have revised the Results to explicitly report the effective sample size for this measure (n = 90) and to note that the findings should be interpreted with caution given the 25% missing data. We have also removed the term “moderate level” from the manuscript. The original MMD-HP publication specifies a total score range of 0–432, with higher scores indicating higher levels of moral distress, but does not establish validated thresholds for classifying scores as low, moderate, or high. Therefore, we now report the observed MMD-HP score descriptively (mean = 108, SD = 80.8) without assigning a categorical level. 

Comment 20: The discussion is appropriate in linking findings to previous studies, but in some places it moves from association toward causal interpretation. The authors themselves correctly note that causal inference is not possible due to the cross-sectional design; this limitation should be consistently observed throughout the Discussion and Conclusion. 

Response 20: We have revised the Discussion and Conclusion to ensure that the interpretation of our findings is consistent with the cross-sectional design. Statements that could imply causal relationships were revised to use more cautious, association-based language. Specifically, we now describe work-related factors as being associated with, reported alongside, or perceived by participants as contributing to the outcomes examined, rather than as directly causing them. We also revised statements regarding potential organizational and system-level interventions to avoid implying effects that cannot be established from the present study. These revisions are consistent with the limitation already acknowledged in the manuscript that temporal and causal relationships cannot be established from the cross-sectional data. 

Comment 21: The results show a small positive association between weekly hours and emotional exhaustion (r=0.25). Therefore, wording such as workload "causes" burnout should be avoided, and "was associated with" should be used instead. 

Response 21: We agree that the small positive correlation between weekly hours worked and emotional exhaustion (r = 0.25) should not be interpreted causally. In the Results, this relationship is reported as a small positive association. We have also revised the Discussion to ensure that workload and other work-related factors are described using association-based rather than causal language, consistent with the cross-sectional design of the study. 

Comment 22: The recommendations regarding government investment, standardization, and staffing are practically significant, but it should be clarified which recommendations are directly supported by the study data and which are more expert/policy implications. 

Response 22: We have revised the Discussion to distinguish more clearly between recommendations directly informed by the study findings and broader policy implications. Considerations related to scheduling frameworks and workload distribution are now explicitly linked to participants’ reports of workload and work-related stressors. In contrast, system-level investment, greater consistency in organ donation program structures, and adequate staffing are presented as broader policy implications arising from the interpretation of our findings rather than as direct conclusions of the study. 

Comment 23: Limitations are not presented independently and sufficiently in the Discussion. It is suggested that limitations be explicitly added, including:  

Cross-sectional design; 

- Inability to infer causality; 

- Self-reported measures; 

- Self-selection in interviews; 

- Potential selection/non-response bias; 

- 25% missingness in the MMD-HP; 

- Lack of member checking; 

- Affiliation of some researchers with the relevant organization; 

- Limited generalizability to other countries and organ donation systems. 

Response 23: We have revised the manuscript to provide a dedicated and more comprehensive Limitations section. The revised section now addresses the cross-sectional design and associated limitations on temporal and causal inference, reliance on self-reported measures, potential response, non-response, and self-selection biases, and the predominantly nursing and female composition of the sample. We also explicitly address the 25% missingness in the MMD-HP data and acknowledge that potential bias related to unmeasured differences cannot be excluded despite the comparison between participants with and without available MMD-HP data. For the qualitative component, we discuss volunteer participation, the absence of participant member checking, the professional translation of French-language interviews into English, and the potential influence of researchers’ organizational affiliations. Finally, we acknowledge that findings were aggregated at the national level, preventing examination of potential differences across provincial ODOs, and that the Canadian context may limit the transferability of the findings to other organ donation systems. 

Comment 24: The conclusion is rather lengthy and somewhat policy-oriented. It would be better to focus the conclusion directly on the main findings and align the implementation recommendations with the level of evidence provided by the study. 

Response 24: We have revised and shortened the Conclusion to focus more directly on the main findings of the study while retaining their implications for coordinators’ well-being and workforce sustainability. Broader policy-oriented statements were removed, and recommendations were revised to align with the level of evidence provided by the cross-sectional design. The revised Conclusion emphasizes the occupational strain, emotional exhaustion, moral distress, and turnover considerations identified among surveyed Canadian OTDCs, together with the organizational, workload-related, and ethical contexts identified in the qualitative findings, while reserving the evaluation of potential organizational and workforce approaches for future research. 

Comment 25: The reference list is generally relevant and reasonably up-to-date; the inclusion of 2024 and 2025 sources is a strength. However, since the paper is part of the BRiC research program, a notable number of references (19–23) belong to this same research group. This is not a problem in itself, but the authors should ensure that the main claims of the paper do not rely solely on their own work. 

Response 25: We reviewed the manuscript to ensure that the main claims and interpretation of the findings do not rely solely on publications from our research group. References 19–23 are primarily cited to contextualize previous publications from the BRiC research program and to distinguish the contribution of the present study from previous analyses. Where a previous BRiC publication is cited in the discussion, it is explicitly identified as a publication from the same research program and is used to contextualize a specific previously reported finding rather than as the sole support for a broader claim.  

Comment 26: In the Discussion, one instance of "28Further" appears, which is clearly a formatting/citation error that needs correction. 

Response 26: Thank you for identifying this formatting error. The erroneous “28” preceding “Further” in the Discussion has been removed, and the citation formatting has been corrected. 

Comment 27: The references should be thoroughly checked for consistency in DOI, URL, punctuation, and final formatting. In particular, web references and DOIs should be formatted exactly according to the journal's style guide. 

Response 27: We carefully reviewed and revised the reference list to ensure consistency and accuracy throughout. Author names, article titles, journal abbreviations, publication years, volume and page/article numbers, and DOI information were verified and corrected where necessary. We also standardized the formatting of journal titles, DOI links, punctuation, and other bibliographic elements throughout the reference list. 

Reviewer 3 Report

Comments and Suggestions for Authors

Dear Authors,

Thank you for the opportunity to review this thoughtful and much‑needed manuscript. The national scope, strong participation rate, and combination of quantitative and qualitative approaches make this a valuable contribution to an understudied area of organ donation practice. The topic is highly relevant, and your work has clear potential to inform workforce well‑being, retention, and organizational planning within organ donation programs.

As I read the manuscript, several areas emerged where additional clarification or refinement would strengthen the study's transparency and coherence. These suggestions are offered with the intention of supporting you in presenting the full value of your work as clearly and convincingly as possible.

One aspect that would benefit from further elaboration is the connection between the quantitative and qualitative phases. The explanatory sequential design is appropriate, and the qualitative findings are rich, but it is not entirely clear how the survey results shaped the interview phase, whether in sampling, refinement of questions, or interpretive focus. Making this connection more explicit or clarifying that integration occurred primarily at the interpretation stage would help readers understand the logic of the mixed‑methods design.

In the quantitative results, a few numerical inconsistencies, particularly in the logistic regression, require correction. For example, the interpretation of turnover predictors does not fully align with the values reported in Table 12. Revising these points and briefly explaining the rationale for variable selection would improve the analysis's accuracy and transparency.

The handling of missing data also deserves a bit more detail. While most measures have low missingness, the moral distress scale has a substantial proportion of missing observations. Clarifying the reasons for this, reporting effective sample sizes where relevant, and acknowledging any implications in the limitations section would strengthen the methodological reporting.

Related to interpretation, the manuscript frequently describes burnout, compassion fatigue/secondary traumatic stress, and moral distress as "moderate" or "moderate to high", but the thresholds used to define these categories are not provided. If these classifications are based on established cut‑offs, citing the source would be helpful; if not, interpreting the scores as continuous variables may be more appropriate.

Because the manuscript is part of a broader research program, a brief statement clarifying any overlap with previous BRiC publications and what is analytically unique to this manuscript would enhance transparency for readers and editors.

The Discussion is thoughtful and relevant, and the policy implications you raise are important. Adjusting some phrasing to avoid causal interpretations and framing organizational or policy recommendations as implications rather than direct conclusions from the data would ensure alignment with the cross‑sectional design.

Finally, the qualitative analysis is clearly described, but since the interview guide directly prompts several constructs, it may help readers to understand how inductive and deductive elements were balanced. A short note on the implications of translation and the absence of member checking would also strengthen the qualitative reporting.

Overall, this is a strong and meaningful study. Addressing the points above will substantially enhance the clarity, rigor and impact of the manuscript. I look forward to seeing the revised version.

Comments on the Quality of English Language

The manuscript is generally clear and understandable, and the study's overall meaning is conveyed without major difficulty. However, several sections would benefit from targeted editing to enhance precision, consistency, and readability. In particular, some sentences are overly long or contain complex phrasing that could be streamlined for clarity. Terminology related to burnout, compassion fatigue/secondary traumatic stress, and the role of organ donation coordinators is occasionally used inconsistently, and harmonizing these terms throughout the manuscript would improve coherence.

Minor grammatical issues appear in a few places, and refining the transitions between ideas, especially in the Methods and Discussion sections, would strengthen the flow of the text. While the English is adequate for comprehension, a careful editorial review focused on concision, consistency, and scientific phrasing would further improve the manuscript's quality.

Author Response

Reviewer 3 

Comment 1: One aspect that would benefit from further elaboration is the connection between the quantitative and qualitative phases. The explanatory sequential design is appropriate, and the qualitative findings are rich, but it is not entirely clear how the survey results shaped the interview phase, whether in sampling, refinement of questions, or interpretive focus. Making this connection more explicit or clarifying that integration occurred primarily at the interpretation stage would help readers understand the logic of the mixed‑methods design. 

Response 1: We agree that the connection between the quantitative and qualitative phases required greater clarification. We have revised the Methods to explicitly describe the logic of the explanatory sequential mixed-methods (QUAN-qual) design. The quantitative survey was conducted first and given priority, and findings from the survey informed the development of the semi-structured interview guide so that the qualitative phase could further explore and contextualize the quantitative findings. Sampling for the qualitative phase was also linked to the survey, as participants were recruited from survey respondents who expressed interest in participating in an interview. Finally, quantitative and qualitative findings were integrated during the interpretation phase. These revisions now make the points of connection between the two phases and the timing of integration more explicit. 

Comment 2: In the quantitative results, a few numerical inconsistencies, particularly in the logistic regression, require correction. For example, the interpretation of turnover predictors does not fully align with the values reported in Table 12. Revising these points and briefly explaining the rationale for variable selection would improve the analysis's accuracy and transparency. 

Response 2: We reviewed the logistic regression results and revised the manuscript to ensure consistency across the Methods, Results, and Table 12. The final model included four predictors: MBI-HSS-MP Emotional Exhaustion, CD-RISC score, ProQOL-STS score, and years working as an OTDC. These predictors were selected based on their clinical relevance and their representation of key occupational and psychological domains examined in the study, including emotional exhaustion, resilience, secondary traumatic stress, and experience in the OTDC role. We also revised the interpretation of the regression results to ensure that it accurately reflects the estimates reported in Table 12. Given the limited number of participants in the “No” category of the outcome variable (n = 36), the final model was restricted to four predictors to reduce the risk of overfitting. Intercorrelations among predictors and variance inflation factors were also assessed to evaluate multicollinearity. 

Comment 3: The handling of missing data also deserves a bit more detail. While most measures have low missingness, the moral distress scale has a substantial proportion of missing observations. Clarifying the reasons for this, reporting effective sample sizes where relevant, and acknowledging any implications in the limitations section would strengthen the methodological reporting. 

Response 3: We have revised the manuscript to provide additional detail regarding missing data. The number of missing observations is reported for the relevant variables in the tables. For the MMD-HP, data were available for 90 participants, with 30 participants (25% of the quantitative sample) having missing data, and complete-case analysis was used for analyses involving this measure. We also compared participants with complete MMD-HP data (n = 90) with those with missing MMD-HP data (n = 30) across available basic participant characteristics. No substantial or statistically significant differences were identified between the groups. However, the reason for the missing MMD-HP data was not documented; therefore, potential bias related to missing data cannot be entirely excluded. We have added this information to the Limitations section and now explicitly acknowledge the implications of the missing MMD-HP data when interpreting findings related to moral distress. Please see our response to Reviewer 1, Comment 8, for the full comparison of completers and non-completers. 

Comment 4: Related to interpretation, the manuscript frequently describes burnout, compassion fatigue/secondary traumatic stress, and moral distress as "moderate" or "moderate to high", but the thresholds used to define these categories are not provided. If these classifications are based on established cut‑offs, citing the source would be helpful; if not, interpreting the scores as continuous variables may be more appropriate. 

Response 4: Thank you for your comment. Reviewer 1 had a similar question for the MBI and the ProQOL scales and we have clarified that: We have verified our thresholds and updated the manuscript text to reflect this correction. Per your request, the exact cut-off values and their corresponding authoritative sources for both instruments have been added to the Methods section and are outlined below.1. Maslach Burnout Inventory for Medical Professionals (MBI-HSS-MP) Cut-off Values. The scoring thresholds are based on the historical, widely utilized population tertiles established in the MBI Manual (3rd Edition). Note that the 4th Edition (2016) transitioned toward a continuous Z-score profile framework, but these traditional sum-total brackets remain standard in clinical literature for categorical risk stratification: 

Subscale Dimension	Low	Moderate	High
Emotional Exhaustion (EE)	0 – 16	17 – 26	≥ 27
Depersonalization (DP)	0 – 6	7 – 12	≥ 13
Personal Accomplishment (PA)*	≥ 39	32 – 38	0 – 31

*Note: PA is inversely scored. Lower scores reflect a higher degree of burnout. 

Alternatively, we could present in the discussion section the results of this study and demonstrate where it sits when comparing to similar populations; if the editors could kindly let us know if this approach is preferred we would be happy to updated the section accordingly.  

Source: Maslach, C., Jackson, S. E., & Leiter, M. P. (1996). Maslach Burnout Inventory Manual (3rd ed.). Palo Alto, CA: Consulting Psychologists Press. 

Regarding the ProQOL comment we have verified our data classification against the official scoring guidelines for the Professional Quality of Life Scale (ProQOL-5). The coordinators' mean Burnout (BO) score of 27.6 (SD = 6.07) is accurately classified as moderate. 

According to The Concise ProQOL Manual, the instrument utilizes a percentile-based raw scoring threshold system (ranging from 10 to 50) to categorize scores into low, average/moderate, and high tiers. A raw score between 23 and 41 represents the average or moderate level of burnout. Because our sample mean of 27.6 falls directly within this bracket, our original interpretation stands, and no text changes were required for this metric. 

To ensure full transparency for the reader, we have added the official ProQOL-5 threshold brackets and source citation to the manuscript, as outlined below: 

ProQOL Subscale (Raw Score Range: 10–50)	Low	Moderate (Average)	High
Compassion Satisfaction (CS)	≤ 22	23 – 41	≥ 42
Burnout (BO)	≤ 22	23 – 41	≥ 42
Secondary Traumatic Stress (STS)	≤ 22	23 – 41	≥ 42

• Source: Stamm, B. H. (2010). The Concise ProQOL Manual (2nd ed.). Pocatello, ID: ProQOL.org. 

We would like to clarify our treatment and reporting of moral distress (MMD-HP) in the manuscript: 

1. Continuous Variable Analysis

We did not apply or assume any categorical cut-off values (e.g., "low," "moderate," or "high") for moral distress. As noted in the psychometric validation of the MMD-HP by Epstein et al. (2019), normative cut-off thresholds for high versus low moral distress scores have not yet been established. Consequently, MMD-HP scores were treated strictly as continuous variables (composite score range: 0–432) 

2. Internal Sample Comparisons Only

Our reporting and statistical interpretations were confined entirely to relative comparisons within our sample itself. Specifically, we reported the overall sample mean (108, SD = 80.8) and evaluated subgroup differences across continuous scores—finding that participants with less than year of experience as an OTDC reported significantly higher continuous moral distress scores than those with more than one year of experience (173 [SD = 108] vs. 93.5 [SD = 66.5], p < 0.001, Cohen’s d = 1.043).  

To prevent any misinterpretation that an absolute threshold or assumption of "high" moral distress was applied, we have reviewed the manuscript to ensure that: 

The Supplementary table 1 has been updated to  explicitly state that MMD-HP scores are analyzed continuously without categorical cut-offs, citing Epstein et al. (2019) 

Comment 5: Because the manuscript is part of a broader research program, a brief statement clarifying any overlap with previous BRiC publications and what is analytically unique to this manuscript would enhance transparency for readers and editors. 

Response 5: Thank you for this important observation. We have revised the Introduction to clarify the relationship between the present study and previous publications from the BRiC research program. We now explicitly acknowledge that this manuscript is part of the broader BRiC program and summarize the specific aspects of OTDCs’ experiences that have been addressed in previous publications. We also clarify the analytical contribution of the present manuscript, which examines a broader range of work-related issues, including burnout, compassion fatigue, moral distress, turnover intention, and factors associated with these outcomes. 

Comment 6: The Discussion is thoughtful and relevant, and the policy implications you raise are important. Adjusting some phrasing to avoid causal interpretations and framing organizational or policy recommendations as implications rather than direct conclusions from the data would ensure alignment with the cross‑sectional design. 

Response 6: We have revised the Discussion and Conclusion to ensure that the interpretation of the findings is consistent with the cross-sectional design. Statements that could imply causal relationships were revised to use more cautious, association-based language. We also reframed organizational and policy recommendations as potential implications arising from the interpretation of the findings rather than as direct conclusions supported by the data. These revisions are consistent with the limitation that temporal and causal relationships cannot be established from the present cross-sectional study. 

Comment 7: Finally, the qualitative analysis is clearly described, but since the interview guide directly prompts several constructs, it may help readers to understand how inductive and deductive elements were balanced. A short note on the implications of translation and the absence of member checking would also strengthen the qualitative reporting. 

Response 7: We have revised the qualitative Data Analysis section to clarify how inductive and deductive elements were balanced. Although the semi-structured interview guide was informed by findings from the quantitative phase, the study aims, and the key constructs under investigation, these constructs were not used as a predetermined coding framework. Deductive elements therefore primarily informed data collection, while the analytical process remained inductive and data-driven, with codes and categories developed from participants’ accounts through open coding and iteratively refined through constant comparison. We have also expanded the qualitative reporting to address the implications of translation and the absence of member checking. The Methods now explicitly state that French-language interviews were translated into English by a professional translator during transcription and that transcripts were not returned to participants for member checking. In addition, the Limitations section now acknowledges that some linguistic or contextual nuances may have been altered during translation. We also clarify that the decision not to return transcripts for member checking was made to avoid adding to the workload of a study population already experiencing substantial work-related demands. 

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

I thank the authors for a thorough and transparent revision. I recomputed the new analyses independently and the great majority of my first-round points have been fully addressed, several of them beyond what I asked for.

Resolved: Table 6 has been added and both in-text citations now point to it correctly. The CD-RISC-10 is named in the Methods, described in Supplementary Table 1 and listed among the abbreviations. The numerical discrepancies are corrected (14% rather than 12%, OR 3.24 rather than 3.75), and the non-significance of the experience term is now stated. The Methods now declare four predictors, matching Table 12, and the caption, the analytic n and the list of predictors are all consistent; model fit statistics have been added. Table 1 now carries the "Yes 84 (70.0%)" row. The 25% missing MMD-HP data are addressed through a completers-versus-non-completers comparison in Supplementary Table S4 and in the Limitations. Cut-off values for the MBI-HSS-MP and ProQOL are supplied with their source. The citation for the Iranian coordinators has been corrected to reference 34. The sample description is now consistent at n = 98 (82.4%), with a helpful note distinguishing sex from gender. The identifying detail in the P10 quotation has been removed. A Limitations section has been added and is candid. The Introduction now positions the paper within the BRiC series and states what it adds.

Beyond my requests, effect sizes with confidence intervals have been added throughout and model discrimination statistics reported. I verified Cohen's d for the sex difference in secondary traumatic stress as 0.636 against the reported 0.639.

Four items remain, the first of which is substantive.

1. The p-values in Table 4 appear to be unadjusted despite being labelled otherwise.

The footnote to Table 4 and the text at line 316 state that the reported p-values are adjusted by the Benjamini-Hochberg procedure. I recomputed all five from the reported means, standard deviations and group sizes using Welch's t-test, and each reproduces as the unadjusted value: emotional exhaustion 0.974 against 0.987, compassion satisfaction 0.098 against 0.104, CD-RISC 0.591 against 0.605, secondary traumatic stress 0.0193 against 0.019, and moral distress 0.489 against 0.48. If these were Benjamini-Hochberg adjusted across the five comparisons, the unadjusted p for secondary traumatic stress would need to be approximately 0.0038, whereas the data give 0.0193.

A likely explanation is that the correction was applied variable by variable, that is, to a family of one test, in which case it leaves every value unchanged. Applied across the five comparisons in Table 4, the sex difference in secondary traumatic stress becomes p = 0.095 and would no longer be significant at the conventional threshold.

Please either apply the correction across the family of comparisons and report the adjusted values, or relabel the values as unadjusted. If the former, the statements about the sex difference in the Abstract, Section 3.2 and the Discussion will need to be revised accordingly. I note that the findings in Table 5 for CD-RISC and moral distress survive the correction (adjusted p = 0.008 and 0.005 respectively), so the substance of the paper is not at stake; only the sex-related finding is. Please also confirm the status of the Table 5 values, since most of these likewise reproduce as unadjusted.

2. Supplementary Table 1 is now inconsistent with the manuscript. The ProQOL entry still states that the compassion satisfaction results "will be reported in another publication", but CS is reported here in Tables 3, 4, 5 and 7, and the revised Introduction states that CS was examined in an earlier BRiC publication. Please update the supplementary text.
3. The multicollinearity threshold has changed in a way that warrants a word of explanation. The first version stated that scales correlated at r ≥ 0.5 were not entered together; the revision states r > 0.5. Supplementary Table S2 shows the emotional exhaustion and secondary traumatic stress correlation as exactly 0.50, which is the one pair the change admits. Please state the rationale for the threshold, and ideally report variance inflation factors for the final model so that readers can judge the effect directly.
4. Two smaller points. The sentence at lines 426-428 reads "was independently associated with 3.24 times higher odds of leaving ... although this association did not reach statistical significance"; the caveat is welcome but "independently associated" should be replaced, since the two halves of the sentence contradict one another. Section 2.2 still describes recruitment as purposive sampling although all 175 eligible coordinators were invited, which is a census with voluntary response. Please also verify the minimum of 0 weekly hours in Table 1, and consider noting in the Limitations that the logistic model has nine events per variable, slightly below the conventional guideline, since the reasoning behind the four-predictor choice is otherwise well explained in the Methods.

Author Response

Dear Reviewer 1,

Thank you for your considerations. Our statistician is on vacation and will return on October 5th. To avoid delays, I as the first author have worked on the requested and my colleague A.S. has checked it. However, if you deem the paper requires further clarifications I will kindly ask that we can submit revisions upon our statistician return. Also, I could not find a place to upload the corrected documents, so I have added the corrected manuscript here, but will also need to share the updated supplementary materials. 

Please see below the point by point responses:

Four items remain, the first of which is substantive.

Comment 1: The p-values in Table 4 appear to be unadjusted despite being labelled otherwise.

The footnote to Table 4 and the text at line 316 state that the reported p-values are adjusted by the Benjamini-Hochberg procedure. I recomputed all five from the reported means, standard deviations and group sizes using Welch's t-test, and each reproduces as the unadjusted value: emotional exhaustion 0.974 against 0.987, compassion satisfaction 0.098 against 0.104, CD-RISC 0.591 against 0.605, secondary traumatic stress 0.0193 against 0.019, and moral distress 0.489 against 0.48. If these were Benjamini-Hochberg adjusted across the five comparisons, the unadjusted p for secondary traumatic stress would need to be approximately 0.0038, whereas the data give 0.0193.

 

A likely explanation is that the correction was applied variable by variable, that is, to a family of one test, in which case it leaves every value unchanged. Applied across the five comparisons in Table 4, the sex difference in secondary traumatic stress becomes p = 0.095 and would no longer be significant at the conventional threshold.

Please either apply the correction across the family of comparisons and report the adjusted values, or relabel the values as unadjusted. If the former, the statements about the sex difference in the Abstract, Section 3.2 and the Discussion will need to be revised accordingly. I note that the findings in Table 5 for CD-RISC and moral distress survive the correction (adjusted p = 0.008 and 0.005 respectively), so the substance of the paper is not at stake; only the sex-related finding is. Please also confirm the status of the Table 5 values, since most of these likewise reproduce as unadjusted.

Response:

We thank the reviewer for recomputing these values, and the reviewer is correct. On re-examination, the p-values in Tables 4 and 5 were unadjusted; the Benjamini–Hochberg correction had not been applied across the family of comparisons. Our earlier statement that these values were adjusted was incorrect, and we apologize for this error. We have now applied the correction across the five outcome comparisons within each table (Table 4: sex; Table 5: years working as an OTDC). Both unadjusted and adjusted p-values are reported (adjusted values in parentheses), and Section 2.3.3 and the table footnotes now state explicitly how the correction was applied. As the reviewer anticipated, the sex difference in secondary traumatic stress does not remain significant after adjustment (unadjusted p = 0.019; adjusted p = 0.094, calculated from the unrounded values); Section 3.2 has been revised accordingly, and the finding is described as exploratory. We retained the effect size (Cohen’s d = 0.639, 95% CI 0.154–1.124) so that readers can judge the magnitude of the difference. The Abstract and Highlights did not report this finding. Section 3.2 and the Discussion have been revised to state that the sex difference in secondary traumatic stress was statistically significant before correction for multiple comparisons but did not remain statistically significant after Benjamini–Hochberg adjustment.

In re-running the analyses from the raw data to answer the reviewer’s question about Table 5, we also found that the Table 5 p-values had been obtained with a pooled-variance t-test, whereas Table 4 used Welch’s t-test. Because group variances differ (for example, moral distress SD 108 vs 66.5), we now use Welch’s t-test for all comparisons, state this in Section 2.3.3, and have updated Table 5 and the corresponding text. The conclusions are unchanged: after adjustment, the differences by years of experience remain significant for CD-RISC (unadjusted p = 0.005; adjusted p = 0.027) and moral distress (unadjusted p = 0.015; adjusted p = 0.037). The reviewer’s figures for these two (0.008 and 0.005) were based on the previously reported pooled-variance values.

 

Comment 2: Supplementary Table 1 is now inconsistent with the manuscript. The ProQOL entry still states that the compassion satisfaction results "will be reported in another publication", but CS is reported here in Tables 3, 4, 5 and 7, and the revised Introduction states that CS was examined in an earlier BRiC publication. Please update the supplementary text.

Response:

We thank the reviewer. Supplementary Table S1 has been revised: the ProQOL entry no longer states that compassion satisfaction results will be reported in another publication. It now reflects that CS is reported in Tables 3, 4, 5 and 7 of the current manuscript and was previously examined in an earlier BRiC publication, consistent with the revised Introduction. We also corrected the numbering of this table to “Table S1” for consistency with Tables S2–S6.

 

Comment 3: The multicollinearity threshold has changed in a way that warrants a word of explanation. The first version stated that scales correlated at r ≥ 0.5 were not entered together; the revision states r > 0.5. Supplementary Table S2 shows the emotional exhaustion and secondary traumatic stress correlation as exactly 0.50, which is the one pair the change admits. Please state the rationale for the threshold, and ideally report variance inflation factors for the final model so that readers can judge the effect directly.

Response:

We thank the reviewer for this observation. We recalculated the correlation matrix among the three continuous predictors using the 112 participants in the final model. The correlation between emotional exhaustion and secondary traumatic stress is 0.49, below the 0.5 threshold under either wording (“≥” or “>”), so the change in wording did not affect which scales were entered together. The value of 0.50 shown in the previous Supplementary Table S2 came from a matrix based on the 77 participants with complete data on all questionnaires, which is why the pair appeared to sit exactly at the threshold. We have replaced Table S2 with the matrix for the model sample (emotional exhaustion–CD-RISC −0.26; CD-RISC–STS −0.29; emotional exhaustion–STS 0.49). We retained “>” because it matches the benchmark for a large correlation defined in Section 2.3.3. As requested, we also report variance inflation factors for the final model: 1.44 (emotional exhaustion), 1.22 (CD-RISC), 1.41 (secondary traumatic stress) and 1.17 (years working as an OTDC), indicating no meaningful collinearity. The Methods now state the correlation and the VIF range (1.17–1.44).

 

Comment 4: The sentence at lines 426-428 reads "was independently associated with 3.24 times higher odds of leaving ... although this association did not reach statistical significance"; the caveat is welcome but "independently associated" should be replaced, since the two halves of the sentence contradict one another.

Response:

We agree and have revised the sentence. It now reads: “Working more than one year as an OTDC was not significantly associated with having considered leaving: although the point estimate was 3.24 times the odds of those working one year or less, the confidence interval was wide and included 1 (OR = 3.24, 95% CI: 0.88–12.7; p = 0.076).”

 

Comment 5: Section 2.2 still describes recruitment as purposive sampling, although all 175 eligible coordinators were invited, which is a census with voluntary response. Please also verify the minimum of 0 weekly hours in Table 1, and consider noting in the Limitations that the logistic model has nine events per variable, slightly below the conventional guideline, since the reasoning behind the four-predictor choice is otherwise well explained in the Methods.

 

Response:

We thank the reviewer for this comment and have considered it carefully. We respectfully maintain the description of the sampling approach in Section 2.2. The selection criterion was being a coordinator working with deceased multiorgan donation in a Canadian province, and all 175 coordinators who met this criterion were invited to participate. This is consistent with the definition of purposeful sampling by Palinkas and colleagues (2015), which involves identifying and selecting all cases that meet a predetermined criterion of importance. Which of the invited coordinators took part was determined by voluntary response; we acknowledge this in the Limitations section, where we note that voluntary participation may have introduced selection or non-response bias. No change has therefore been made to the sampling description.

We have added the events-per-variable limitation to Section 5: the logistic regression model included 35 participants in the smaller outcome category among the 112 analyzed, giving approximately nine events per variable, slightly below the conventional guideline of ten.

Regarding the minimum of 0 weekly hours in Table 1, we checked this against the raw survey data. Exactly one respondent entered 0 in this item, and no other respondent reported fewer than 8 hours. As the survey was anonymous, we cannot determine the reason for this response, so we have retained it as recorded and added a note to Table 1 identifying it. Excluding it would change the mean weekly hours from 35.7 to 36.0 and the minimum to 8.