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Thanks for you revision. The paper can be accepted now.
[# PeerJ Staff Note - this decision was reviewed and approved by Stephen Macknik, a PeerJ Section Editor covering this Section #]
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Romo et al have improved the revised manuscript according to the comments raised by two reviewers in the second round. The manuscript, in my opinion, meets the PeerJ criteria and should be accepted as is.
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Thank the authors for considering all my concerns and revised the manuscript accordingly.
Some issues are still needed to be addressed. Please revise the paper accordingly. Before re-submission, please carefully check the language and format of the paper. to ensure it was written according to the guideline of PeerJ.
Romo et al have improved the revised manuscript greatly in many ways according to the comments raised by three reviewers.
The study is well designed and the research question are well defined, it should be noted that the exposure was measured after the exposure.
Data is robust, statistically sound, & controlled.
I reviewed the revised manuscript, and there are my comments as listed below. I did not recognize these in the first round because there were more important issues to be mentioned at that time.
Line 97: “which is likely due to (no reference)” sounds hypothetical, should more likely to appear in discussion, not introduction.
Line 156: “and asked about HIV testing in the past six months” means that HIV status in the 2nd survey might affect the association the authors want to evaluate (HIV causes depression measured in the 2nd survey), which should be acknowledged in discussion part.
Line 241-246: I knew that the authors used a fully conditional method for imputation, however the authors should explain to the readers that why they used FCS, not MVN.
This specification may be necessary if you are imputing a variable that must only take on specific values such as a binary outcome for a logistic model or count variable for a Poisson model.
https://stats.idre.ucla.edu/sas/seminars/multiple-imputation-in-sas/mi_new_1/
Besides, is there any evidence to support your statement “The multivariable model had about 25% missing data, so we ran 25 imputations”? I am not good at Mi, just a little curious(25% missing data, so 25 imputations?).
Line 344: The nature direct effect was statistically nonsignificant, which means self-efficacy is an intermediate variable between exposure and outcome, then what? The authors stopped here abruptly and did not finished the story. Are there any evidence to support the finding? What does the finding mean, what’s the possible reasons underlying, and what’s the potential implication for intervention? Without addressing these topics, there seems no need to do the mediation analysis.
Line 382-383: “…our exposure and outcome was not undertaken simultaneously.” should be rephased. No, they were not undertaken simultaneously, but the statement is less accurate because the exposure was measured later than outcomes.
In the limitation part, the first limitation, the authors said "the prevalence of depression among truck drivers in general may in fact be lower, as clinic-based sampling can result in selection bias for mental health disorders ". I did not find any evidence showing that depression among truck drivers in general may in fact be lower. Please clarify this.
Thank the authors for considering my concerns and revised the manuscript accordingly.
The title is for the "long-distance" truck drivers at roadside. So there are also short-distance truck drivers. But in the Eligibility criteria, the authors stated that persons "employed as a truck driver" were employed. Details on the "long-distance" may be necessary.
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Thank the authors for considering my concerns and revised the manuscript accordingly. Additional concerns as follows:
1. In the limitation part, the first limitation, the authors said "the prevalence of depression among truck drivers in general may in fact be lower, as clinic-based sampling can result in selection bias for mental health disorders ". I did not find any evidence showing that depression among truck drivers in general may in fact be lower. Please clarify this.
2. The title is for the "long-distance" truck drivers at roadside. So there are also short-distance truck drivers. But in the Eligibility criteria, the authors stated that persons "employed as a truck driver" were employed. Details on the "long-distance" may be necessary.
Although the study has merits, some issues need to be addressed. Please consider the comments provided by our reviewers and revise the paper accordingly.
Romo et al estimated prevalence of depression among the among a specific group in Kenya, long-distance truck drivers at roadside wellness clinics, and evaluated the association of depression with sexual risk behavior. The topic is very interesting and the data are valuable. The authors talked the story with a clear 'storyline’, the language is clear and unambiguous.
The format of the manuscript, including tables, needs improving greatly. A well formatted manuscript makes reviewers more enjoyable.
The study are well designed and the research question are well defined.
Data is robust, statistically sound, & controlled.
Romo et al estimated prevalence of depression among the among a specific group in Kenya, long-distance truck drivers at roadside wellness clinics, and evaluated the association of depression with sexual risk behavior. The topic is very interesting and the data are valuable. The authors talked the story with a clear 'storyline’, the language is clear and unambiguous.
However, the format of the manuscript, including tables, need improving greatly. A well formatted manuscript will make reviewers more enjoyable while reading.
Major REVISIONS:
The main concern is that the dual direction of the causality between depression and sexual risk behavior. Furthermore, both depression and sexual risk behavior might be influenced by same factors, ie occupational stressor. If depression and sexual risk behavior share one ancestor, they are also associated statistically. The authors may explain the association from an etiological perspective.
The second issue is that the authors might focus more on the association between depression and health risk behavior (with multiple condomless partners). The results and the discussion of the confounding factors distract the core subjects .
The third issue is that the authors discussed the association superficially, did not explain the potential reasons behind the association, using existing theories or hypotheses, if any.
The fourth issue is that is the authors used two much space to discuss the implication part. Of course, the implication is important, especially for policy makers. As mentioned before, they should discuss more on the potential mechanisms that can explain the associations. If there are not reasonable mechanisms to support the association, then we can infer the reverse conclusion, that depress is caused by sexual risk behavior.
Minor REVISIONS:
Line 72 it’s associated with both… does not necessarily mean that it mediate the relationship, because if it is a confounding factor or ancestor(cause) of the exposure and outcome, it’s also associated with both.
Line 114 The authors may use a table or figure to show that what measured in baseline interview and what measured in follow-up interview.
Line 130 Two periods after the word “man”.
Line 131 …those with more than multiple condomless partners. In this sentence, “more than” should be removed??
Line 204 What’s the difference between crude model and multivariable model? According to the note of Table 2, multivariable model adjusted clinic location additionally. The crude model adjusted other covariables, why still be call “Crude” model?
Line 214 Mediation analysis could be inspired by the paper ”Mediation analysis in epidemiology: methods, interpretation and bias” https://doi.org/10.1093/ije/dyt127
Line 291 Logistic regression? The authors should describe clearly where they used poisson regression and where where they used Logistic regression. In Table 2, all the indicators are aPR, so I guess they were from poisson models.
If the authors used logistic regression here, ordinal logistic regression should be used as the outcome was recoded as none, one, two or more.
Maybe I am wrong, the authors should state these in methods part more clearly.
1. The English language of this manuscript need to be revised and polished due to many errors that make the readers confused.
2. The references included in the paper and the raw data are sufficient.
3. Multivariable logistic regression model was used. For table 2, I'm not sure which model was used, logistic or Posson regression model?
1. The study was derived from a randomized controlled trial (about HIV), but this study aims to conduct a cross-sectional study, and estiamte the prevalence of depression in the special population. The rigorous inclusion criteria could introduce large selection bias. So the estimates of prevalence may have a weak comparability.
2. Only two clinics were enrolled. It is hard to say the representativeness of the aim population.
3. The measure of sexual risk behavior lack reference.
4. Measures were actually taken from two interviews that were six
months apart, which may introduce large information or recall bias.
Due to the limitation of the study design, I am afriad the data could not state the conclusions, such as the high prevalence of depression.
I do not think the initial study design of the RCT could derive the cross-sectional study. A scientific epidemioloical survey is needed for this topic.
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This is an interesting article on an important subject but there are methodological issues..the study was designed for a different research question. If it had been designed for this question, then the PHQ would have been administered at Time 1 instead of or as well as at Time 2.
The sample frame appears to be all truck drivers who visited the two clinics between October and Dec 2015 for services other than HIV treatment, The results should report the size of the sample frame, how many were eligible, and how many agred to take part, thus giving a response rate. The external validity of the study is influenced by this response rate.
The authors argue in the discussion that depression status would be unlikely to change over 6 months if untreated, but in fact this is not the case. Follow up studies show that around 50% of cases improve over 6 months.
The sample was drawn from truck drivers seeking services at roadside wellness clinics in Kenya...thus the sample is a primary care clinic based sample rather than a community based sample. Such PHC samples generally have higher rates of depression than community samples. Furthermore, truck drivers have a younger age distribution than the general adult population.
Thus line 341 in the discussion needs changing -this study suggests that truck drivers attending wellness clinics have a higher rate of depression than the general population, but this is not surprising as such studies of
clinic attenders always find a higher prevalence than in community populations. It would have been good to compare truck driver rates with a control group of non truck drivers also attending the wellness clinics., as this would have given
more of an indication of whether being a truck driver was the operative variable .This issue is subsequently raised at lines 374-376, but it is fundamental to the earlier sections of the discussion and should be made explicit there.
It's not clear why the PHQ was not conducted at the first interview.
line 388-there has also been an RCT of primary care training about mental health in Kenya, as well as roll out to around half of primary health care workers.
(Jenkins et al. International Journal of Mental Health Systems December 2013, 7:25)
In general, I suggest a revision to clarify these methodological issues of sample frame, response rate, the fact that appropriate comparisons of prevalence rates are with clinic based samples, not general population samples, and the fact that depression rates would change over a six months period.
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