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All reviewers' comments have been adequately addressed.
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The authors have fully addressed my comments and I recommend to accept the paper.
Please provide additional details on the sample size and data sources used in the study as requested by the reviewer.
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Thank you for addressing all my previous comments
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The authors have generally responded sincerely to the reviewer's comments, and the paper has been improved. However, the following significant concerns remain:
(1) The description of the sample size calculation is still inadequate.
As the authors state in their response letter, the sample size calculation presented in this paper is a post-hoc calculation performed in a secondary analysis using an existing dataset (the same dataset as Ding (2022) Front Public Health). Furthermore, the authors' sample size calculation mixes the odds ratio from previous studies on the association between sleep duration (short sleep) and SRH with the prevalence of sleep latency. Sample size calculations that mix information on different risk factors lack statistical validity, making it difficult to determine whether the calculated sample size is appropriate for the purpose of this study (detecting the association between sleep latency and SRH).
Considering the above points, it is difficult to say that there is any rationale for describing the current sample size calculation results in this paper, and in principle, I recommend removing the description of the sample size calculation from this paper.
If the authors wish to keep the description, the following modifications are considered the minimum necessary:
- Clearly state that this study is a secondary analysis using the same dataset as Ding (2022) Front Public Health.
- Explain that the original dataset was initially collected based on a different sample size calculation for a different purpose.
- State that although a post-hoc sample size calculation was attempted at the start of this secondary analysis, due to the lack of directly relevant studies, the calculation was performed under the limited conditions of using the odds ratio of a different risk factor (short sleep duration) and information related to sleep latency, and that this calculation may not guarantee the statistical power of this study. Use cautious language, such as "the statistical power may be inadequate." and the interpretation should be limited.
(2) Citation of the existing dataset is missing.
Regardless of whether the sample size calculation is described, the fact that this study is a secondary analysis using an existing dataset (Ding (2022) Front Public Health) is crucial for the transparency of the research. Therefore, I strongly recommend that the authors formally cite the source of this dataset in the appropriate section of the paper (e.g., the Methods section).
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Reviewer 2 has raised critical issues with your study and expressed concerns about the limited willingness to address their previous comments and the lack of comprehension of key concepts related to human sleep-wake regulation. While your rebuttal letter demonstrates an effort to engage with the feedback, it is essential to ensure that all critical points have been thoroughly addressed. The reviewer emphasised that major revisions are required before the manuscript can proceed further. Please revisit the comments from Reviewer 2 (and other reviewers) and ensure that your responses comprehensively address their concerns.
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1. The authors responded that the time frame for the sleep latency assessment was that of the PSQI scale. This was somewhat confusing. Did the participants complete the PSQI or the questionnaire submitted as supplementary material? The latter contains the wording in the original manuscript, where there is no time frame. If the sleep latency variable is derived from that questionnaire, the authors could just discuss whether the absence of a time frame is a study limitation.
2. The authors removed the sleep quality variable from the covariates, but it is still shown in Table 1. Please correct the Table.
3. In line 216, the phrase "categorizing sleep latency into four groups" should be "categorizing sleep latency into three groups".
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No comments on the basic reporting per se, although a basic comprehension of the fact that having college times that interfere with one's biological clock has a very significant impact that exceeds the effect that sleep latency on its own has, is till lacking. Also the advice of reducing mobile phone use has to be removed and preferably replaced with an advice towards those people responsible for scheduling college times for medical students to take into account the tendency for people in that age range to be rather extreme evening types and therefore put college times later during the days. Such an intervention will with the greatest possible likelihood, have a much bigger effect than advice against mobile phone use.
I am furthermore afraid that the authors are wrong in their claim that short sleep duration and lower sleep efficiency go hand in hand. Time awake before sleep onset and after sleep offset should not be part of this formula.
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My previous comments remain. It should be discussed that the current way college hours are scheduled favours morning types and that it is behind the observation that the few morning times that exist within this age range have a considerably better SRH, simply because they are better adapted to the challenges posed upon them than evening times
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The authors have addressed the reviewers' previous comments. While the manuscript has significantly improved, several concerns still need to be addressed:
(1) The authors claim they calculated the sample size based on prior research on sleep duration and suboptimal SRH. However, this explanation appears questionable, as Ding et al. (2022), which used the same survey data, reported an entirely different sample size calculation method. Furthermore, given the incorrect citation of suboptimal SRH prevalence in the references, the authors' claim about pre-survey sample size calculation lacks credibility. The current explanation appears inadequate, and a more accurate and convincing description is required.
(2) While the authors argue that the turning point in the cubic spline analysis is merely descriptive, statistical results that fail to demonstrate significance (rejection of non-linearity) cannot be considered descriptive statistics. Therefore, all results from the cubic spline analysis, except for the statistical values, should be removed.
(3) In Table 1, the authors justify not performing multiple comparisons by stating it determines potential confounders. However, the manuscript lacks any explanation of this procedure.
(4) Although additional information about BMI criteria has been provided, the relationship between body type and the BMI threshold (24.0 kg/m2) remains unclear. The authors should explain how this threshold was determined based on the study population's characteristics (e.g., median values).
The followings are minor issues:
(5) The weighting process for sleep diary data requires explanation.
(6) SRH should be spelled out at its first appearance in the Introduction.
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Add more details above the exact statistical techniques used in your study. How did you introduce splines? For multivariable logistic regression, report adjusted odd ratio.
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1. I couldn't fully understand the process of participant selection for the study. The authors mention using stratified cluster random sampling. In stratified sampling, the population is grouped according to specific characteristics, and each group is then randomly sampled. In cluster sampling, on the other hand, the population is divided into heterogeneous groups, and whole clusters are then randomly sampled. The authors don't give details about either stratification or clustering in their population, and thus the description of participant selection is not adequate.
2. The sample size calculation was based on the prevalence of suboptimal SRH. However, the study's endpoint is the association of SRH with sleep latency, which is completely different. Can the authors explain this discrepancy? Furthermore, was the sample size calculation performed a priori? Since the target sample size is reported in a wide range, which number did the authors aim to recruit? Why didn't they stop recruitment when reaching 777 participants?
3. Why didn't the authors use a time frame in the assessment of sleep latency (e.g., the past month)? Could this influence the possibility of recall bias, and in which way?
4. The authors mention both the use of the PSQI and a single Likert-type question to evaluate sleep quality. Since none of the two entered the regression models, what was the purpose of collecting them both?
5. The authors stated that the rationale for the sensitivity analysis is to exclude confounding variables. The study's objective, however, was "to investigate whether sleep latency is associated with suboptimal SRH in Chinese medical students while accounting for confounding variables". If the authors believe that these variables may have confounding effects, they should include them as covariates in the main analysis. Generally, the purpose of a sensitivity analysis is to evaluate if methodological issues, such as variations in definitions of predictors or outcomes, variations in analytical methods, protocol deviations, or missing data, influence the final results and conclusions of a study. In this instance, the sensitivity analysis should be incorporated into the main analysis and perhaps the subgroup analyses that follow.
1. I couldn't understand the value of the restricted cubic spline, especially when the authors first present the logistic regression analysis with predefined levels of the predictor (sleep latency). Then they report the cubic spline, and we learn that the association between sleep latency and SRH is indeed linear (p for non-linear >0.05), meaning that sleep latency could be entered as a continuous predictor in the logistic regression. Perhaps the authors could present one such analysis as a sensitivity analysis, since, as it seems, it is another valid way to analyze the data.
2. It is also unclear why the authors present 2 different subgroup (interaction) analyses for the same variable, midnight snack habit. In the first there are 3 groups for sleep latency, while in the second there are 4, like the rest of the models. For consistency reasons, the authors should stick with the 4-level sleep latency model.
3. The concluding statement "To reduce sleep latency, medical students should restrict the use of electronic devices before bedtime and avoid eating midnight snacks" is not supported by the results. Firstly, use of electronic devices was not tested in the study, and secondly, eating midnight snacks was associated with suboptimal SRH and not sleep latency.
The statement in line 56 that sleep latency was introduced by a research paper in 2014 is of course inaccurate and should be removed.
The manuscript is well written. Some minor points for improvement/clarification:
1. Line 56. Sleep latency as such is not a concept introduced bu Shrivastava et al 2014, rather it is a widely used key component of sleep research for already very many decades.
2. The concept of morning types and evening types in relation to sleep latency is missing in the introduction. By definition, morning types will have a shorter sleep latency with standardized bed times or bedtimes that are adjusted to the 9 to 17 working hours society.
Having a key parameter, in this case sleep latency, assesssed both subjectively and expressed as a mean value over a longer period of time is suboptimal. Crucial information as to how sleep latency is varying within the individual is lacking. Usually, for instance, sleep latencies are found to be shorter during the weekend when bedtimes are more in line with one's circadian preference.
The grouping of sleep duration is not clear. In what group, would for instance a sleep duration of 7,5 hour fall (line 130).
A more thorough assessment of circadian preference would have been better, i.e. using a validated questionnaire instead of a single question. This due to big role that circadian preference plays where it concerns sleep latency.
The findings are valid but a discussion on the direct connection to circadian preference is completely missing. E.g., morning type --> shorter SL --> better SRH
Line 254. The claim that short sleep duration and lower sleep efficiency go hand-in-hand should rather be other way around. Shorter sleep is usually of higher efficiency that longer sleep.
The manuscript is written in appropriate academic English and follows a standard structure. The presentation of figures and tables is adequate.
However, there are significant concerns with the Introduction and Background sections.
(1) They fail to provide appropriate context and lack coherent narrative flow. While the first paragraph discusses health issues among medical students, the second paragraph abruptly shifts to discussing the health effects of sleep latency and Self-rated health (SRH) without establishing any logical connection to medical students, resulting in poor paragraph-to-paragraph coherence.
(2) Furthermore, there are concerning issues with the sleep-related descriptions. The manuscript incorrectly states that sleep latency was introduced by a 2014 review (Shrivastava, 2014). This is a significant error, as sleep latency is a fundamental sleep parameter; for instance, the Multiple Sleep Latency Test (MSLT) was established as a standard objective sleepiness test in 1986 (Carskadon et al., 1986).
(3) While it is theoretically possible that prolonged sleep latency may affect sleep cycles, the cited reference (Siddiquee 2023) does not discuss this relationship and only considers sleep latency as an insomniac symptom. Moreover, there is no consensus on the optimal number of sleep cycles.
(4) While the study appears to have properly disclosed all relevant data, it should be noted that there is a related paper (Ding 2022) that appears to use the same dataset, raising concerns about data overlap.
While the study demonstrates some methodological rigor as an epidemiological investigation and follows standard procedures, there are several significant concerns that need to be addressed.
(5) First, related to the issues noted in Basic Reporting, the manuscript fails to clearly identify the research gap in existing studies on the health effects of sleep latency. The authors merely present the novelty of combining certain indicators (sleep latency, self-rated health [SRH]) with a specific population (medical students) without stating clear hypotheses. The manuscript needs to clearly articulate: what unique characteristics medical students might have regarding the relationship between sleep latency and SRH, what the study hypotheses are, and what significance and generalizability the findings might have.
(6) There are serious concerns regarding the sample size calculation. The authors use different prevalence estimation parameters for suboptimal SRH between this paper (35.6-71.0%) and their related paper Ding (2022) (35.6-54.6%). Sample size calculations should be conducted before the study begins, and parameters should not vary between analyses of the same study. If this represents post-hoc power analysis, it should be explicitly stated as such.
(7) More problematically, the prevalence values cited from previous studies differ from what the authors report. Stefan (2017), using the same 5-point Likert scale, defined poor self-rated health as "very poor" and "poor" responses, reporting a prevalence of 27.3%. Steptoe (2006), using a slightly different 5-point scale, defined poor health as "fair" or "poor" responses, reporting a prevalence of 12%. Using these values in the authors' sample size calculations would yield N=5064-13945, suggesting the current sample size is insufficient. While Li (2019), newly cited in this paper but not in Ding 2022, reports a notably higher suboptimal SRH prevalence (71%) that would lower the required sample size (N=777), the substantial discrepancy with other cited studies raises questions about the appropriateness of treating these studies equally.
(8) Regarding reproducibility, the description of measurement indicators and analytical methods is insufficient. While the primary measures (sleep latency and SRH) are described, covariates (sleep duration, chronotype, sleep quality, etc.) lack explanation, and the rationale for using single-item measures is unclear. The citations (Lauderdale 2008, Selvi 2018) used to support reliability and validity are inappropriate, as these papers actually report limited reliability of subjective sleep duration due to systematic bias (Lauderdale 2008) or use multi-item scales (MEQ, PSQI) rather than single items (Selvi 2018).
(9) The subgroup reliability and validity assessments lack explanation of selection methods and representativeness. For reliability assessments, the test-retest interval is not specified, and details of test-retest reliability methods (e.g., Intraclass correlation coefficient) are missing. Regarding external validity, there is insufficient information about how the 5-day sleep diary data were aggregated into representative values for each participant, whether weekend days were included (considering catch-up sleep/social jetlag), and how PSQI measurements were conducted (frequency, timing, type of correlation analysis: linear/non-linear, parametric/non-parametric). Moreover, the rationale for correlating self-reported sleep latency with PSQI total scores, which represent sleep quality/sleep disorder severity, is unclear.
(10) The statistical analysis description lacks crucial details about the restricted cubic spline implementation, including knot selection criteria and model fit assessment. Table 1's comparison of four sleep latency groups lacks information about multiple comparison procedures and corrections. These omissions make study replication challenging.
Despite the aforementioned concerns, the results demonstrate some validity within the given conditions. However, several issues warrant attention:
(11) The logistic regression analysis uses ≤10min as the reference category for sleep latency, while the authors' cited reference Siddiquee (2023) uses 16-30min (noting that shorter categories may include sleep-related breathing disorders). Moreover, the authors themselves state in their Introduction that most sleep latency durations are 10-20 minutes, raising questions about the appropriateness of their reference category selection.
(12) The restricted cubic spline results presented in Figure 2 are potentially misleading. While the P-value is significant, the P-Nonlinear is not, indicating no significant nonlinear relationship. Despite this, the authors present a turning point, which could lead to misinterpretation.
(13) The analysis of joint effects between sleep latency and midnight snack habits on suboptimal SRH lacks theoretical justification for potential interaction, suggesting possible selective reporting of exploratory analyses. Similar concerns apply to the stratified analyses. Additionally, the BMI categories differ from WHO recommendations without explanation.
(14) The Discussion section inadequately addresses the study's objectives and results. It lacks necessary discussion of the specificity (or similarity) of medical students as the target population, including comparisons of longer sleep latency and suboptimal SRH frequencies among Chinese young adults, and consideration of the cultural/ethnic effects mentioned in the Introduction.
(15) The proposed potential mechanisms demonstrate limited understanding of sleep physiology and inappropriate citations. First, the relationship between sleep latency and sleep cycles is not well-established, and the cited review discusses REM rebound without addressing sleep latency. Second, while longer sleep latency might affect circadian rhythm if sufficient light exposure occurs between lights-out and sleep onset, such exposure is unlikely under normal circumstances. Third, while the relationship between sleep latency and reduced sleep duration/efficiency is logical, this conflicts with the adjustment for sleep duration in the logistic regression analysis.
(16) A final concern is the Discussion's recommendation to limit electronic device use at night, despite no supporting evidence from the study's findings.
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