Criteria for considering studies for this review
Types of studies
We will include randomized controlled trials (RCTs) in this review. If we do not find any RCTs, we will include quasi-randomized trials and non-randomized, comparative studies. Quasi-randomized trials are studies that allocate participants to treatments using methods that aim to achieve the purpose of randomization. For example, we will consider use of hospital ID, social security number, date of birth, etc., to be quasi-random methods of allocation. Non-randomized study designs will include prospective and retrospective cohort studies of children treated with probing and a concurrent comparison group treated with an alternative strategy with follow-up data on outcomes for both groups. Such studies have neither a random or quasi-random method of allocating children to treatment or control groups. We will not include studies evaluating outcomes before and after interventions with no comparison group. In addition, we will not include studies that used a historical patient group as a comparison group.
Types of participants
We will include studies of children with congenital nasolacrimal duct obstruction aged three weeks to four years who may have presented with tearing and conjunctivitis. We will include studies with children up to four years of age to allow for data on early and late probing, but will exclude studies with children older than four years as children these ages are more likely to have acquired nasolacrimal duct obstruction. We also will exclude studies of children with previous nasolacrimal duct obstruction as only primary probing failures will be assessed. We will not include studies of infants with congenital dacryocystocele (distention of the lacrimal sac as a result of a distal nasolacrimal duct obstruction) as these children may develop infection or obstruction of nasal breathing with an inability to feed and often require treatment in the first two weeks of life. We also will exclude studies that enrolled children with dacryocystitis (infection of the lacrimal sac), keratitis (infection of the cornea), blepharitis (inflammation of the eyelid), cellulitis (infection the skin of the eyelids), trichiasis (lashes which rub on the eye), tumors causing direct compression of the lacrimal drainage system, paralysis of the muscles around the eyelids, eyelid trauma, entropion (inward turning of the eyelid), ectropion (outward turning of the eyelid), epiblepharon (inward turning of the eyelid margin, coloboma (notching or loss of eyelid margin), of or other eyelid malposition.
Types of interventions
We plan to include studies that compared probing (office-based or hospital-based under general anesthesia) versus no probing or other interventions including observation alone, antibiotic drops only, or antibiotic drops plus massage of the nasolacrimal duct. In this review we will not include studies that compared different probing techniques or surgical procedures.
Types of outcome measures
The primary outcome for this review is the proportion of participants with treatment success, defined as the absence of clinical signs, including epiphora and mucous discharge, at six months after probing.
Secondary outcomes for this review include:
proportion of participants with treatment success at time points beyond six months after probing as data are available, e.g., one year after probing;
proportion of participants requiring secondary procedures, surgical or diagnostic, performed within one month, three months, six months, and one year as a consequence of probing or not probing;
cost effectiveness at the time of the primary outcome;
proportion of participants with complications including bleeding, injury to the nasolacrimal system or the eye or canalicular stenosis (narrowing of the nasolacrimal duct due to fibrosis), other complications of probing and any other complications reported from included trials within six months of probing.
Search methods for identification of studies
We will search the Cochrane Central Register of Controlled Trials (CENTRAL) (which contains the Cochrane Eyes and Vision Group Trials Register) (latest issue), Ovid MEDLINE, Ovid MEDLINE In-Process and Other Non-Indexed Citations, Ovid MEDLINE Daily, Ovid OLDMEDLINE (January 1946 to present), EMBASE (January 1980 to present), PubMed (1966 to present), Latin American and Caribbean Health Sciences Literature Database (LILACS) (1982 to present), the metaRegister of Controlled Trials (mRCT) (www.controlled-trials.com), ClinicalTrials.gov (www.clinicaltrials.gov) and the WHO International Clinical Trials Registry Platform (ICTRP) (www.who.int/ictrp/search/en). We will not use any date or language restrictions in the electronic search for trials. Because we intend to search for quasi-randomized and non-randomized studies in case there are no RCTs, we have not included a study design filter in the searches.
See Appendices for details of search strategies for CENTRAL (Appendix 1), MEDLINE (Appendix 2), EMBASE (Appendix 3), PubMed (Appendix 4), LILACS (Appendix 5), mRCT (Appendix 6), ClinicalTrials.gov (Appendix 7) and the ICTRP (Appendix 8).
Searching other resources
We will use Scopus to search for publications that cited included studies. We will search the reference lists for studies included in the review to identify any additional ones cited. We will not handsearch journals or conference proceedings specifically for this review.
Data collection and analysis
Selection of studies
The two authors will independently screen titles and abstracts of trials identified by the electronic searches. We will obtain full-text reports of studies that at least one author has classified as definitely or possibly meeting the inclusion criteria for this review. Both authors will independently determine from reading the full-text reports whether the study is eligible for inclusion in the review. We will resolve discrepancies through discussion and consensus. We will provide a description of those studies excluded after full-text review in the 'Characteristics of excluded studies' table. When study eligibility cannot be determined from study reports, we will contact study authors for additional information. We will allow authors to respond within two weeks. If we fail to elicit a response from study authors, we will assess studies based on the available information or assess the study as awaiting classification.
Data extraction and management
Both authors will independently extract data onto data abstraction forms developed by the Cochrane Eyes and Vision Group. We will abstract data on the following.
Study design and participant characteristics.
Method used to generate the random sequence for only RCTs; method of allocation and allocation concealment; masking (blinding) of study participants, study personnel, and outcome assessors; number and reason for losses to follow-up in each treatment group; evidence for reporting biases (selective outcome reporting); and funding sources and conflicts of interests.
Data on primary and secondary outcomes for this review.
We will resolve discrepancies by re-checking the data from the source and through discussion. One author will enter data into the Cochrane Collaboration's statistical software, Review Manager (RevMan 2012), and the other author will check it against the data abstraction.
Assessment of risk of bias in included studies
We will examine the following domains to determine the risk of bias for randomized and quasi-randomized trials included in this review. We will assess each domain as "low risk", "high risk" or "unclear risk" of bias using criteria listed in Chapter 8 of the Cochrane Handbook of Systematic Reviews of Interventions (Higgins 2011).
Random sequence generation:
Method of allocation concealment:
masking of participants, infants and children less than four years of age, is not relevant to risk of bias. Masking of care providers (study personnel and outcome assessors), and/or parents may be possible; we will examine study methods to determine if masking was at "low risk" of bias. Because masking of personnel who assessed outcomes is possible, we will examine the methods used to determine whether masking of these personnel results in "low risk" of bias.
Incomplete outcome data:
we will examine data reported from included trials on exclusions after randomization, losses to follow-up, and reasons for exclusions and losses to follow-up after randomization in each group. We will assess the amount of missing data and methods used to handle missing data. Whenever the reasons for missing data were likely to be related to the outcome, we will classify the study as "high risk". We will note methods used to impute the missing data by the trial investigators.
Selective outcome reporting (reporting biases):
we will compare available reports from the same study (e.g., protocols, clinical trial registrations, design and baseline papers), where available, to assess consistency of reported data. We will not contact authors to obtain protocols for trials.
Conflicts of interest and other potential sources of bias:
If no randomized trials exist then we will review and summarize the non-randomized studies that compared the interventions of our interest.
Measures of treatment effect
For dichotomous outcomes (proportion of participants with treatment success, secondary procedures, and complications), we will report a risk ratio and 95% confidence interval. We will report mean differences and corresponding 95% confidence interval for continuous outcomes (mean costs of procedures).
Unit of analysis issues
For studies where children were allocated and only one eye per child was included, we will consider the unit of analysis to be the child. For trials where the unit of allocation was the child and both eyes of a child were treated with the same intervention and analyzed separately, we will consider these studies similar to cluster-randomized studies. For studies with a paired-eye design, where the unit of allocation was the eye and the opposite eye was used as a control, we will assess how appropriate it was to use the opposite eye as a control. As an example, probing one eye and using the other eye allocated to no treatment may be appropriate. If one eye was probed and the opposite eye was treated with antibiotics, however, one must be concerned about the effect of antibiotics on the eye that was probed, a cross-over effect. The analysis method will be documented, including whether eyes were analyzed separately and whether non-independence was considered and accounted into the analysis. We will follow guidelines in chapter 9 of the Cochrane Handbook of Systematic Reviews of Interventions to handle data from cluster-randomized and paired-eye studies (Deeks 2011). We will request statistical advice from the Cochrane Eyes and Vision Group when analyzing data from cluster or paired-eye studies.
Dealing with missing data
We will attempt to contact authors of publications from included studies in an effort to recover missing data that may be available. We will allow authors to respond within two weeks. If we fail to elicit a response from authors of publications, we will report available data and discuss their limitations. We will not impute data.
Assessment of heterogeneity
We will assess clinical and methodological heterogeneity by examining variability in inclusion/exclusion criteria, characteristics of study participants and interventions, and length of follow-up in the included studies. We will assess variability in risk of bias parameters to determine presence of methodological heterogeneity. We will use the Chi2 test of heterogeneity to identify statistical heterogeneity. We also will calculate I2 values and consider an I2 value greater than 50% to indicate substantial statistical heterogeneity.
Assessment of reporting biases
We will assess for selective outcome reporting by comparing outcomes measured with those reported in full-text publications. For trials with multiple publications, including conference abstracts and full-text publications, we will examine all available study reports for consistency in description of methods and outcomes.
When we are able to include 10 or more studies in a meta-analysis, we will display and examine a funnel plot for evidence of potential publication bias.
We will determine whether data synthesis can be done by investigating study characteristics for clinical heterogeneity, risk of bias for methodological heterogeneity, and the Chi2 test, I2 values and overlap of confidence intervals for statistical heterogeneity. Specifically, when the I2 value is greater than 50% and overlap of confidence intervals is poor, we will consider substantial statistical heterogeneity to be present and we will perform meta-analysis. On the other hand, when no substantial clinical, methodological, or statistical heterogeneity is detected, we will combine data in meta-analysis. We will use a fixed-effect model when there are fewer than three studies and a random-effects model when there are three or more studies included in meta-analysis.
For economic data, we will describe costs associated with each treatment group (i.e., costs of surgical procedure and associated medical costs) and provide a narrative summary of cost-effectiveness measures including incremental cost-effectiveness ratio (ICER). If formal model-based cost-effectiveness analyses were performed, we will discuss the uncertainty in the model estimates stemming from assumptions made for model parameters and discuss any corresponding sensitivity analyses.
Subgroup analysis and investigation of heterogeneity
When sufficient data are available we will perform subgroup analyses based on whether probing was conducted in the office setting or in an outpatient hospital setting under general anesthesia. We also will examine whether probing was conducted in children less than 18 months of age compared to children 18 months of age and older.
When sufficient data are available we will examine the effect of excluding studies classified as being at high risk of bias for incomplete outcome data and selective outcome reporting. We also will examine the effect of excluding industry-funded studies and quasi-randomized trials.