Types of studies

The review will be confined to randomised controlled trials comparing manual toothbrushes against manual toothbrushes combined with other oral hygiene aids. Studies where the participant or the operator or both are masked from the intervention will be included as it may prove to be difficult to mask the participant to the intervention. We will include trials comparing different kinds of manual brushes where the intervention is the so‐called 'orthodontic brush' (Gomes 2012; Rafe 2006). We will also include trials which consider aids such as the Sonic Speed SR‐100E sonic toothbrush (Water Pik), the electric interdental cleaning device Flosser FL‐110, Siwak and others as mentioned above (Arici 2007; Kossack 2005; Sharma 2008). We will however, exclude trials comparing manual and powered toothbrushes or different powered toothbrushes as these have been covered comprehensively by another Cochrane Review (Deacon 2010; Yaacob 2014). Split‐mouth studies will be excluded as they do not represent 'everyday use'.  Cross‐over trials will however, be included.

Types of participants

We will include individuals of any age with no reported disability that might affect toothbrushing. They must be patients undergoing active orthodontic treatment involving upper or lower fixed appliances or both. All patients should have either brackets or bands on a full arch. They should be bonded using one single type of cement for both control and study group, as we are uncertain if different types of cement would influence the accumulation of plaque. The type of fixed appliances should be the equitable for both sets of patients as different size and shape of brackets may influence the accumulation of plaque. Furthermore, different mechanics and philosophies may be confounding factors. The instructions given to each set of patients should be similar and preferably given by the same person although not necessarily the operator who is providing the treatment. Adults and children will be included.

Types of interventions

We will include all trials that compare a combination of toothbrushing and any additional mechanical dental cleaning procedure, with toothbrushing alone, or with another mechanical dental cleaning procedure. Interventions may be self‐performed, supervised or unsupervised (Bock 2010). Therefore the comparison would be the use of a standard toothbrush alone to patients using a standard toothbrush and/or a special 'orthodontic brush' (included in these would be the triple‐headed toothbrush and the orthodontic brush amongst others) together with interdental/interspace brushes (Arici 2007; Ashkenazi 2015; Bock 2010; Gomes 2012). More traditional aids, such as floss, tape and dental sticks will be included.

Instructions on the use of these interventions are allowed as this is considered to be appropriate. The control group would also need to be given comparable instructions. Additionally, trials utilising combined interventions such as fluoride mouthrinse will be included as this is a commonly used intervention in unfluoridated areas providing both groups receive the same intervention.

Types of outcome measures

Electronic searches

We will search the following databases for relevant trials:

• Cochrane Oral Health's Trials Register;

• the Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library;

• MEDLINE Ovid (from 1946 onwards);

• Embase Ovid (from 1980 onwards);

• CINAHL EBSCO (Cumulative Index to Nursing and Allied Health Literature; from 1937 onwards).

The subject strategies for databases will be modelled on the search strategy designed for MEDLINE Ovid in Appendix 1. Where appropriate, this will be combined with subject strategy adaptations of the highly sensitive search strategy designed by Cochrane for identifying randomised controlled trials and controlled clinical trials (as described in the Cochrane Handbook for Systematic Reviews of Interventions Version 5.1.0, Box 6.4.c. (Lefebvre 2011)).

Searching other resources

We will search the following trials registries:

• US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (clinicaltrials.gov);

• World Health Organization International Clinical Trials Registry Platform (apps.who.int/trialsearch).

We will check the bibliographies of included studies and any relevant systematic reviews identified for further references to relevant trials. Authors of unpublished abstracts will be contacted to collect further data. We also intend to contact manufacturers of interdental cleaning devices to ask them about their knowledge of any unpublished or ongoing clinical trials.

We will not perform a separate search for adverse effects of interventions used. We will consider adverse effects described in included studies only.

Selection of studies

Two review authors will independently carry out the selection of studies and make decisions about eligibility. If the relevance of a study report is unclear, we will review the full text and resolve all disagreements by discussion and if necessary, by consulting Cochrane Oral Health.

Data extraction and management

Two review authors will independently and in duplicate extract the data from each included study using a specially designed data extraction form. We will contact study authors for clarification or missing data where necessary and feasible. We will resolve any disagreements through discussion, consulting Cochrane Oral Health to achieve consensus when necessary. Studies excluded at this stage will be entered in the excluded studies category.

We will record the following data for each included study in the 'Characteristics of included studies' table.

• Publication details: author(s); year of publication; sponsorship.

• Design: randomisation process; blinding; study duration.

• Participants: source and number of patients; selection method of patients; patient demographics (age, race, gender distributions).

• Intervention: products used by group; frequency of use of products; length of follow‐up; outcomes by time of follow‐up; patient adherence.

• Outcome measures: scale used, limits and direction of scale; validity/sensitivity of outcome measures; number of times outcomes were assessed; number of evaluators and their reliability; characteristics of the evaluators (dental professional or lay person); number and reasons for withdrawals; statistical methods used (to check validity).

• Outcomes (presented using raw data or re‐classification of outcome measures to enable comparison of the findings) by duration of follow‐up (data will be extracted for each evaluation period reported in a study).

Assessment of risk of bias in included studies

Assessment of risk of bias will be carried out by using Cochrane's 'Risk of bias' tool as described in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). The tool addresses the following six domains: sequence generation, allocation sequence concealment, blinding, incomplete outcome data, selective outcome reporting, and other bias.

As it is not possible to blind the study participants for the interventions of interest, primary consideration will be given to the blinding of the outcome assessors. Split‐mouth trials are excluded due to the risk of handedness and carry‐over or spill‐over effects. We will include cross‐over designs and will take into account additional considerations when assessing their risk of bias, such as the suitability of the design, the risk of carry‐over or spill‐over effects, and appropriateness of the statistical analysis.

We will complete a 'Risk of bias' table for each included study. For each domain of risk of bias, we will first describe what was reported to have happened in the study. This will provide the rationale for our judgement of whether that domain is at low, high, or unclear risk of bias. We will also generate a 'Risk of bias' summary graph and figure.

Data collection forms and assessments of the risk of bias will be tested on a pilot sample of articles. We will not be blinded to the names of the authors, institutions, journals or results of a study. Both review authors will independently, and in duplicate, carried out the assessment of risk of bias. If any piece of information important for the assessment of risk of bias is found to be missing in the included reports, study investigators will be contacted and required information requested. Cochrane Oral Health will be consulted if necessary.

Measures of treatment effect

Whether analysis of included studies is narrative or quantitative, a general framework for synthesis may be provided by considering four points:

1. the direction of effect;

2. the size of effect;

3. the consistency of the effect across the studies;

4. the strength of evidence for the effect.

Meta‐analysis would be used to provide a statistical method for points 1 to 3. In this instance it would be unlikely that narrative synthesis would be used. In the event that more than one tool is used to measure outcomes then meta‐analysis would be required for each of these as it may not be appropriate to combine them as it is likely that the tools used would be incomparable.

For gingivitis and plaque outcomes, the measures of treatment effect should mostly be continuous. In this event the mean difference and standardised mean difference will be used to combine different clinical indices. We will calculate the corresponding 95% confidence intervals for each study.

Periodontal loss of attachment can be a continuous measure (it is anticipated that it would be rarely seen as orthodontic patients should have intact attachment at the start) that can be dichotomised on a patient basis and considered a binary measure. If the binary data are provided, we plan to use risk ratios together with 95% confidence intervals to combine dichotomous data. It is hoped that study patients who end up with demineralisation which is visible to the naked eye should be taken off the trial and treatment provided; if demineralisation is used as an outcome measure, it should be treated as continuous data.

Due to the nature of the topic, it is anticipated that there should be no cluster trials. However, cross‐over trials cannot be excluded. The data from cross‐over studies should be combined with those of similar parallel‐group trials, using the techniques described by Elbourne 2002. They need to be well designed and the methodology needs to be sound. However, the greatest issue with cross‐over trials is the wash‐out period. As it is unethical to ask patients not to embark on oral hygiene, it is unlikely that any trial would be undertaken with a wash‐out period. In this event the risk of a carry‐over effect can be quite high depending on how the trial is carried out. Therefore the emphasis on trial design is paramount.

Unit of analysis issues

It is anticipated that the outcomes measured should be reported from within individual patients as opposed to individual teeth or groups of selected teeth. Oral hygiene outcome measures would be corrupted if measured on certain teeth in patients with fixed appliances as there is no way of ensuring that the different teeth in different patients are treated similarly during their orthodontic treatment. There will be difficulties with access, orthodontic auxiliaries, which may preclude appropriate oral hygiene measures.

These issues should not arise as cluster randomised trials are not appropriate for this type of study. Data from the first part of any cross‐over trial could be valid and will be used (providing the methodology is sound). However, the review authors cannot work out how the carry‐over effect can be eliminated and feel that data from the second part cannot be used unless the carry‐over effect can somehow be neutralised.

Dealing with missing data

As described in Chapter 16.1 of theCochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), there are several types of missing data in a systematic review or meta‐analysis. Of these, missing studies and outcomes are addressed in the Assessment of reporting biases section below. Common problems such as missing summary data (e.g. standard deviations, or separate sample sizes for each intervention group) are not a reason for study exclusion but rather, we will apply the methods outlined in Chapter 16.1.3 for imputing missing standard deviations.

Where data on individuals are missing from the results, we will, in the first instance, contact study authors to supply the missing information.

Data judged to be 'missing at random' (i.e. their being missing is unrelated to their actual values), it would not be detrimental to ignore this type of missing data. For data that are 'not missing at random', a sensitivity analysis to assess how the changes in assumptions might have affected the results would be carried out to determine the potential impact of missing data on the findings of the review. Once this is known, then appropriate steps would be taken to rectify this if necessary.

It is best practice to obtain all missing data in order to avoid imputing data to complete an intention‐to‐treat analysis.

Assessment of heterogeneity

Assessment of heterogeneity is important in order to avoid inappropriate use of meta‐analysis. It is likely that substantial clinical heterogeneity will be found in this topic due to the variability of the interventions considered and the very wide variability in the outcome measures. The lack of perceived equality between the so many different indices to measure the various outcomes may result in methodological diversity and in this instance, it may be difficult to pool the trials. Evidence of equality between the indices may be required. If this exists to some extent, it may be possible to ignore heterogeneity and use a fixed‐effect meta‐analysis. Conversely, it may be better to contact the authors to determine if there was an additional index used which may help.

We will use the I² statistic to assess statistical heterogeneity with a rough guide for interpretation as follows: 0% to 40% might not be important, 30% to 60% may represent moderate heterogeneity, 50% to 90% may represent substantial heterogeneity, 75% to 100% may represent considerable heterogeneity (Higgins 2011).

Assessment of reporting biases

An attempt would be made to reduce reporting biases by searching methods described previously. Unpublished data will have to be analysed subject to the same vigour as studies found using more conventional means to determine their suitability to be included in the final analysis.

Testing for publication bias will be conducted using funnel plots (plots of effect estimates versus the inverse of their standard errors) providing there are at least 10 studies available, and a formal test investigation of the degree of asymmetry (this may indicate publication bias and other biases in relation to sample size) will be performed using the method proposed by Egger 1997. The results of any funnel plot need to be analysed carefully as asymmetry could be caused by some smaller studies of lower methodological quality and therefore produce exaggerated intervention effect estimates. This is especially true when considering unpublished data.

Data synthesis

Ideally meta‐analysis should be used to combine trials if possible. Trials will be grouped in terms of their interventions and outcome measures. The two main intervention groups are those comparing manual toothbrushes with interdental/interspace toothbrushes and those comparing manual toothbrushes with specialised orthodontic brushes.

It may be possible to combine different indices for one outcome measure with the same concept with good level of correlation. However, it will not be possible to combine the results from different indices directly. The effects will have to be converted to standardised values before combining. The standardised mean difference (SMD) will therefore be calculated along with the appropriate 95% confidence intervals and will be used as the unit for each meta‐analysis.

Some of the secondary outcome measures may generate binary data. We will extract the number of events for binary outcomes where available. All standard errors of the mean will be converted to standard deviations. Risk ratios will be calculated for these combined data using 95% confidence intervals and will be used as the unit for each meta‐analysis.

We will use random‐effects models for all analyses. With this approach, the confidence intervals for the average intervention effect will be wider than those using a fixed‐effect approach, leading to a more conservative interpretation.

Subgroup analysis and investigation of heterogeneity

We will carry out subgroup analyses according to the following:

(1) periodontal status,
(2) dependability and cost,
(3) hard/soft tissue injury,
(4) damage to the orthodontic appliances.

Depending on studies found, it may be possible to further reduce the subgroups to age (Unkel 1995), and gender in children (Kuusela 1997) as a further subset, but it is felt that the four suggested above are the most pertinent and probably those most looked at.

Sensitivity analysis

Primary meta‐analysis will be carried out on all eligible studies irrespective of their risk of bias. We will test the robustness of our results by performing sensitivity analyses based on excluding the studies at unclear or high risk of bias from the analyses. In addition to methodology shortcomings, there might be other factors, such as the age of the patient (i.e. if some studies use only adults as participants compared to those who only use very young children whose manual dexterity may be reduced), and manual dexterity, handedness, which may be relevant and we may consider looking at these if they were noted. We could potentially pick up more factors on closer inspection of the included studies and these would be subject to analysis if appropriate.