Criteria for Considering Studies for This Review
Types of Studies
We will consider only RCTs. We will exclude quasi-randomized trials (e.g., treatment allocation alternates or by date of birth) and non-randomized trials. Previous studies have shown that many factors can influence children’s susceptibility to myopia onset and progression, such as parents’ refractive statuses, sex, time spent doing homework, and sleeping time.[16] Randomization is essential to prevent systematic differences between baseline characteristics of participants in different intervention groups in terms of known and unknown (or unmeasured) confounders.
We do not anticipate any cross-over trials on this topic because the therapies to control myopia are expected to have long-term effects and children’s refractive statuses cannot return to baseline. In the event that we identify a cross-over trial, we will include only the first period of the trial in our review and discard data from the second period of the trial.
We will not exclude studies based on blinding because blinding is difficult to achieve given the constraints of the RLRL device.
Types of Participants
We will include trials on 6 to 14-year-old children with a confirmed diagnosis of myopia. Myopia is typically defined by a SER of -1.00 D or lower. It’s worth noting that, some studies define myopia as SER of -0.75 D or lower and we will not exclude these studies because the clinical difference is insignificant. We will exclude trials in which the majority of participants were not in the target age interval at the start of the trial because a wider age interval can cause a great concern about participants’ heterogeneity. We will apply no gender, ethnicity, or myopia subtype restrictions.
Types of Interventions
The treatment of the intervention group should be RLRL therapy (also called low-intensity long-wavelength red light, low-level red light, or red light), along with SVS. The RLRL treatment is provided by a desktop light therapy device. The typical parameters used in the treatment are as follows. An RLRL-emitting device produces red light of 650 nm wavelength at an illuminance level of approximately 1600 lux and a power of approximately 0.29 milliwatt (mW) for a 4 mm pupil (class I classification) for 3 minutes per session, twice daily.[14] These RLRL settings may vary slightly in different studies.
The treatment of the control group should be SVS alone or SVS along with sham RLRL therapy (using a sham RLRL device or a real RLRL device with very low power). If there are multi-arm studies that include not only an RLRL group and a control group but also groups using other myopia-controlling measures, we will only include the RLRL group and the control group in the systematic review.
Types of Outcome Measures
The primary outcomes of this systematic review are the changes in SER and AL. An automatic refractor will measure the SER under a fully cycloplegic condition. AL can be measured by a variety of devices, such as IOL-master and ocular A-ultrasonography, these devices have consistent results.[17]
The secondary outcomes are treatment-related adverse events (AEs), which refer to any uncomfortable symptom, including but not limited to photophobia, eye itching, burning sensation, dry eye, blurred vision, glare, dazzling, keratitis, and conjunctivitis.
We will not exclude trials if they fit all the other inclusion criteria but do not report our pre-planned outcomes. If the outcomes of interest are not reported, we will contact the authors of those trials and inquire about these results. Even if these results are not available, the potential impact of the studies’ omission from the meta-analysis may be able to be considered; for example, if a study reported that children in the RLRL group had thinner choroids compared to the control group, which suggested that RLRL caused worse myopia progression, but this study did not measure AL and SER, in the context that the result of our meta-analysis is in favor of RLRL, we can infer that the omission of this study makes the meta-analysis more in favor of RLRL.
Search Methods for Identification of Studies
Electronic Searches
We will search the following medical literature databases for eligible studies. All of the databases will be searched from their commencement until the start date of the search. We will not apply any language restrictions, so as to reduce the risk of language bias.
Our MEDLINE search strategy is presented in Table 1. We will adapt the MEDLINE search strategy to search each of the other databases. Table 2 presents the databases to be searched.
The following trial registries will be searched to find related complete or ongoing trials, as described in Table 3.
We will also search for grey literature, as described in Table 4. Health technology assessment agencies, clinical practice guidelines, device regulatory approvals, advisories and warnings, and the manufacturer’s official sites will be searched. To our knowledge, the manufacturer of the RLRL device, Eyerising company, is registered in Australia and China. Therefore, we will particularly search grey literature published in Australia and China. With regard to conference papers, theses, and dissertations, those in Chinese are usually found in Chinese bibliographic databases, while those in English are expected to be found in Google and Google Scholar, so we will search Google and Google scholar too.
Citation Search
We will use a web-based application, Citation Chaser,[18] to get a list of all articles that the included articles reference (backward citation search) and all articles that reference the included articles (forward citation search). We will check these articles in order to find additional eligible studies.
Consulting Relevant Experts and Organizations
We will consult relevant experts and organizations to find potential additional relevant studies, as outlined in Table 5. In the correspondence, we will email them a comprehensive list of the studies already included in our review, along with the eligibility criteria for the review, asking if they know of any additional studies (ongoing or completed; published or unpublished) that might be relevant. After sending emails, we will wait two weeks for replies. If there is no reply, we will send the email a second time and wait two more weeks before giving up consulting the specific expert/organization.
Data Collection and Analysis
Selection of Studies
The references will be uploaded onto Covidence, which will automatically remove duplicate records of the same study. Two reviewers will independently examine titles and abstracts to remove obviously irrelevant records. If there are discrepancies about some articles, we will include these articles because we will aim to be over-inclusive at this stage. Then, we will retrieve the full text of the potentially relevant reports. If any reports discuss the same study, we will link together these reports If several reports belong to the same study, we will merge them together under that study, to make sure that each study rather than each report is the unit of interest in the review.
Next, two reviewers will independently examine full-text reports for compliance of studies with eligibility criteria. In this stage, any discrepancies will be resolved by discussion until a resolution is agreed upon. If the disagreements cannot be resolved between the two review authors, a third reviewer will act as the arbiter. All of the studies excluded in the full-text stage will be justified in a table “Studies excluded in the full-text stage”. If we identify any ongoing studies, we flag them and add them to a list.
We will document the process of study selection in a flow chart, as recommended by the PRISMA statement,[19] showing the total numbers of retrieved references and numbers of included and excluded studies.
Data Extraction and Management
Two review authors will independently extract data and then compare them with each other to verify the accuracy of extracted data. We will contact the authors of individual studies to ask for additional information if required. We will use develop a standardized data extraction form containing the following items. The items to be extracted are outlined in Table 6.
After compiling a list of included articles, the reviewers will thoroughly pilot-test the data collection form with three articles. By pilot-testing and revising the data collection form, we will ensure its clarity, accuracy and completeness of it. We will document the version number and date. We will archive any old forms.
The reviewers will undergo a training period where we discuss the use of the collection form. This will occur at the onset of the data extraction phase, and periodically as needed.
Two review authors will independently extract data and then compare them with each other to verify the accuracy of extracted data. We will contact the authors of individual studies to ask for additional information if required.
If there are any inconsistencies among multiple reports of the same study, we will contact the study author to inquire which data are correct. If we cannot get a response from the study author, the data in the final official publication (such as in a Science Citation Index journal) will be used.
Assessment of Risk of Bias in Included Studies
We will use the Cochrane Risk of Bias Tool 2 (RoB 2) to assess the risk of bias in included studies. Two reviewers will independently assess the risk of bias for each included study. Any discrepancies by RoB2 assessments will be resolved by discussion until a resolution is reached. If the disagreements cannot be resolved between the two review authors, a third reviewer will act as the arbiter. The RoB2 results will be presented alongside the forest plot. We will present the full RoB2 assessment as a supplementary file.
Measures of Treatment Effect
The change-from-baseline values of SER and AL are continuous outcomes. We will report mean differences (MDs) for them. Treatment-related adverse events are dichotomous outcomes. We will report risk ratios (RRs) for treatment-related adverse events. If adverse events are rare (< 1%) we will employ the Peto odds ratio. If no individuals have adverse events in either group, adverse events will be omitted from the meta-analysis.
Unit-of-Analysis Issues
When only one eye per participant is randomized, the unit of analysis will be the individual eye (on the level of the participant). When both eyes from the same participant are randomized (either to the same or different interventions), we will attempt to analyze data that has been adjusted for clustering or paired-eye design.
If we identify cluster RCTs, we will include these in meta-analyses directly where the sample size has been adjusted for clustering. We will consider it reasonable to combine the results from individual and cluster-randomized trials if there is little heterogeneity between the study designs and the interaction between the effect of the intervention and the unit of randomization considered to be unlikely. If outcomes are presented at the individual level (i.e. a unit of analysis error) we will use established methods to adjust for clustering by calculating an effective sample size by dividing the original sample size by the design effect which can be calculated from the average cluster size and the intra-class correlation coefficient (ICC). Where the ICC is unknown, this will be estimated from similar trials.
Dealing with Missing Data
Data that are missing from reports of included studies will be sought by contacting the study authors. Where data are missing due to participant drop-out we will conduct available case analyses and record any issues of missing data within the assessments conducted using the Cochrane risk of bias tool.
Assessment of Heterogeneity
First, we will use a forest plot to visually inspect the degree of heterogeneity. Then, we will assess the heterogeneity of treatment effects between trials using the χ2 test with a significance level of p-value < 0.1. We will use the I2 statistic to estimate the proportion of total variation across studies that is beyond chance (I2 > 30% moderate heterogeneity, I2 > 75% considerable heterogeneity). We plan to use the random-effects model to synthesize the data, so we will also use τ2 statistic to estimate the between-study variation.
All these statistics can be calculated by Review Manager (RevMan version 5.4). Besides, we will explore potential causes of heterogeneity by performing sensitivity and subgroup analyses if there is are sufficient data.
Assessment of Reporting Biases
Given that our research topic discusses a fast-growing topic with few published studies, we will consider some biases in publishing practices. Quickly growing topics have time lags, which means that positive results are available first. While for many new topics, there may be concluded studies that are not completely reported yet.
We will try to minimize reporting bias from non-publication of studies or selective outcome reporting by using a broad search strategy, checking references of included studies and relevant systematic reviews, and contacting study authors for additional outcome data.
If there are 10 or more included studies, we will investigate potential reporting biases by generating funnel plots and visually inspecting their asymmetry. We will also conduct statistical tests to formally investigate the degree of asymmetry of the funnel plots using the method proposed by Egger et al.[20] and consider a p-value less than 0.1 as significant for this test.
Data Synthesis
Grouping Data for Synthesis
We will group data by follow-up time. In the preliminary search, we found that studies have multiple follow-up examinations. Studies often include four follow-up examinations: in the 3rd month, 6th month, 9th month, and 12th month after treatment respectively. For each follow-up period, we will group the studies which have data for this period and attempt to conduct a meta-analysis.
Statistical Models
We will use the random-effect model, because some factors that may influence the progression of myopia to differ among studies, like participants’ ages, education burden, living area (urban or rural), parents’ refractive statuses, and the implementing environment of RLRL (at home or in clinics), may be different among studies, which can potentially influence the intervention integrity. We are not confident that the effect on the outcome is the same among these studies. Meta-analyses will be performed on RevMan 5.4 software to generate forest plots, along with weighted means and 95% CIs of outcome measures.
Summary of Findings tables
We will assess confidence in the evidence using GRADE criteria[21] and the GRADEpro software.[22] We will present the results in a “Summary of Findings” table. We will present assessments of the evidence using five factors referring to limitations in the study design and implementation of included studies that suggest the quality of the evidence: risk of bias; indirectness of evidence (population, intervention, control, outcomes); unexplained heterogeneity or inconsistency of results; imprecision of results; and a high probability of publication bias. We will define the levels of evidence as “high”, “moderate”, “low”, or “very low”. We will follow the recommendations of Chapter 8 and Chapter 14 of the Cochrane Handbook for Systematic Reviews of Interventions.[23]
These grades are defined as follows:
• High certainty: we are very confident that the true effect lies close to that of the estimate of the effect.
• Moderate certainty: we are moderately confident in the effect estimate: the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.
• Low certainty: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect.
• Very low certainty: we have very little confidence in the effect estimate: the true effect is likely to be substantially different from the estimate of effect.
We will include the quality of the evidence for SER and AL in the Summary of findings tables. If a meta-analysis can be done for treatment-related adverse events, we will include the quality of the evidence for treatment-related adverse events in the Summary of findings tables, too.
Subgroup Analyses and Investigation of Heterogeneity
To explore potential subgroup variations, we will perform several subgroup analyses if sufficient studies (at least 10) are included and data on potential moderators and predictors are available. We intend to compare the following: male vs females, younger vs older populations, and populations with different severity of myopia (low, medium, or high myopia), and parents’ refractive statuses (no myopic parents, one myopic parent, or two myopic parents).
Sensitivity Analyses
We will undertake sensitivity analyses by removal of trials that caused high heterogeneity in direct comparisons. We will also explore the impact of including removing studies at high risk of bias and with high levels of missing data in the overall assessment of treatment effect.
If our results are not robust in the sensitivity analyses, the results must be interpreted with caution and this will be discussed in the limitations section. Such findings may encourage future investigations.