Types of studies

We included randomised controlled trials (RCTs) with at least six months' follow‐up that compared the effects of 'true' ART with a conventional restorative approach using the same or different restorative dental materials. Parallel‐group, split‐mouth and cluster‐study design were eligible for inclusion.

Types of participants

We included dentate participants, regardless of their age and sex, with a history of dental (coronal or root) primary caries lesions extended into enamel and dentine (but not the pulp) and who have undergone restorative treatment using either conventional restorative or true ART approaches. We also considered primary and permanent teeth with single or multiple surface lesions.

Types of interventions

We included adhesive restorative materials, such as GICs with different viscosities or resins, placed with the 'true' ART approach, including ITR with hand instruments, compared with the same or different restorative materials, such as GIC, placed with conventional cavity preparation methods. Only studies using the same restorative material in both arms were considered as key results and the other studies were included for completeness.

We excluded studies on modified ART techniques.

Types of outcome measures

Electronic searches

Cochrane Oral Health’s Information Specialist conducted systematic searches in the following databases for RCTs and controlled clinical trials. There were no language, publication year or publication status restrictions:

• Cochrane Oral Health’s Trials Register (searched 22 February 2017) (Appendix 1);

• Cochrane Central Register of Controlled Trials (CENTRAL; 2017, Issue 1) in the Cochrane Library (searched 22 February 2017) (Appendix 2);

• MEDLINE Ovid (1946 to 22 February 2017) (Appendix 3);

• Embase Ovid (1980 to 22 February 2017) (Appendix 4);

• LILACS BIREME Virtual Health Library (Latin American and Caribbean Health Science Information database; 1982 to 22 February 2017) (Appendix 5);

• BBO BIREME Virtual Health Library (Bibliografia Brasileira de Odontologia; 1986 to 22 February 2017) (Appendix 6).

Subject strategies were modelled on the search strategy designed for MEDLINE Ovid. Where appropriate, they were combined with subject strategy adaptations of the highly sensitive search strategy designed by Cochrane for identifying RCTs and controlled clinical trials as described in the Cochrane Handbook for Systematic Reviews of Interventions Chapter 6 (Lefebvre 2011).

Searching other resources

The following trials registries were searched for ongoing studies:

• US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (clinicaltrials.gov; searched 22 February 2017) (Appendix 7);

• World Health Organization International Clinical Trials Registry Platform (apps.who.int/trialsearch; searched 22 February 2017) (Appendix 8).

Selection of studies

We imported the downloaded set of records from each database to the bibliographic software package Endnote and merged them into one core database to remove duplicate records and to facilitate retrieval of relevant articles. We also obtained potentially relevant reports identified when searching other sources (reference lists of relevant trials, reviews, articles and textbooks). The records located from searching these (non‐electronic) sources were entered manually in Endnote. All records identified by the searches were checked on the basis of title first, then by abstract or keywords or both. Two review authors independently assessed the eligibility of the full text of relevant records (Figure 1).

Figure 1

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Study flow diagram

One review author (Mojtaba Dorri (MD)) assessed all the references. Two others researchers (Dominic Hurst (DH) and Carlos Zaror (CZ)) assessed the references to establish whether the studies met the inclusion criteria or not, using an inclusion criteria form, which had been prepared previously and pilot tested. We resolved disagreements by discussion. Had resolution not been possible, we would have consulted a third review author (Valeria Marinho (VM)).

The review authors could read reports in English, Persian, Arabic, Portuguese and Spanish. We identified two papers in Chinese and two papers in Dutch. The papers were translated by two translators who were native speakers and fluent in English. One of the authors (MD) compared two versions. The minor disagreements were resolved by discussion with the translators.

We contacted the authors of any articles we could not classify in order to ascertain if inclusion criteria were met. If we identified more than one publication of a trial, we listed the paper with the primary outcome as the primary reference. Where a trial report thought to be potentially relevant was in a language not known to the review authors, it was translated by a native speaker who was fluent in English.

From all studies meeting the inclusion criteria, we extracted the data and assessed risk of bias. We recorded studies rejected at this or subsequent stages in the ’Characteristics of excluded studies’ tables, along with reasons for exclusion.

Data extraction and management

Two review authors (CZ and MD) independently extracted data from the included studies using a pilot‐tested data‐extraction form. The data were then entered into the Characteristics of excluded studies table in Review Manager 5 (RevMan5) (RevMan 2014) and checked for differences. Any disagreements were resolved through discussion with another review author (Mª José Martínez Zapata (MMZ)) until we reached consensus. We contacted trial authors for clarification or missing information, where there was any uncertainty or data were missing. We treated studies with duplicate publications as a single source of data. Review authors were not blinded to the names of the authors, institutions, journal of publication, or results of the studies.

In the data extraction form, we recorded the following details for each trial: RCT design (e.g. parallel, split‐mouth, cluster); country where the trial took place; setting (e.g. primary or secondary care); funding source; inclusion criteria; exclusion criteria; number of participants randomised and evaluated; baseline number of decayed, missing and filled primary teeth (dmfts)/and permanent teeth (DMFTs); test and control interventions; type and number of operators; primary and secondary outcomes; sample size calculation; duration of follow‐up; any co‐interventions; risk of bias; and any other relevant data. We used the data for each specific time point or time interval separately, as reported in the original studies.

Assessment of risk of bias in included studies

Two review authors (CZ and MD) conducted 'Risk of bias' assessment independently and in duplicate for all the included trials, according to the criteria for assessing risk of bias described in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Any disagreements were resolved through discussion with another review author (Mª José Martínez Zapata (MMZ)) until we reached a consensus. We contacted trial authors where necessary.

We assessed the risk of bias to be high, unclear or low for seven domains:

• Sequence generation: was the method used to generate the allocation sequence appropriate to produce comparable groups? We graded this domain as having a low risk of bias if the authors described a random component in the sequence generation process (e.g. random number table, coin tossing, drawing of lots).

• Allocation sequence concealment: was the method used to conceal the allocation sequence appropriate to prevent the allocation being known in advance of, or during, enrolment? We graded this domain as having a low risk of bias if the authors described adequate concealment (e.g. by means of central randomisation, sequentially numbered, opaque envelopes), and graded high risk of bias if inadequate concealment was documented (e.g. alternation, use of case record numbers, dates of birth or day of the week) or if allocation was not concealed.

• Blinding of participants and personnel: was knowledge of the allocated intervention adequately prevented during the study? We graded this domain as having a high risk of bias if the study did not use any blinding of participants or operators.

• Blinding of outcome assessors: was knowledge of the allocated intervention adequately prevented during the study? We graded this domain as having a high risk of bias if the study did not use any blinding of assessors.

• Incomplete outcome data: how complete were the outcome data for the primary outcomes? Did authors report dropout rates and reasons for withdrawals? Did they impute missing data appropriately? We graded this domain as having a low risk of bias if the proportion of the missing outcome data was less than 25% and the groups were balanced in numbers and reasons for dropouts, or if investigators imputed missing data using appropriate methods. If dropout was above 25% and there was no information on reasons for dropouts across groups, but attrition was balanced, we graded the risk of bias as unclear. We graded it as high if the proportion of missing outcome data was over 25% and not balanced between groups.

• Selective outcome reporting: did investigators report appropriate outcomes or were key outcomes missing? We graded this domain as having a low risk of bias if authors reported all pre‐specified outcomes. If they did not report prespecified or expected data, we assumed the risk of bias to be high.

• Other sources of bias: was the study apparently free of other problems that could put it at a high risk of bias? These include information on the baseline characteristics of the intervention and control groups and the similarity in using co‐interventions between groups. We graded the trials as having a high risk of bias if there were important differences in demographic characteristics or if the groups received different co‐interventions during the trial, or if the statistical analysis was inadequate or inappropriate.

We developed a standardised 'Risk of bias' assessment form and entered data in the 'Risk of bias' tables in RevMan 5 (RevMan 2014).

We summarised the potential risk of bias for each study overall:

• low risk of bias: plausible bias not likely to seriously alter the results (if low risk of bias for all items);

• unclear risk of bias: plausible bias that raises some doubt about the results (if unclear risk of bias for one or more key items, but none at high risk of bias);

• high risk of bias: plausible bias that seriously weakens confidence in the results (if high risk of bias for one or more key items), as described in Section 8.7 of the Cochrane Handbook for Systematic Reviews of Interventions 5.1.0 (updated March 2011) (Higgins 2011).

We completed a ’Risk of bias’ table for each included study (see Characteristics of included studies) and presented the results graphically by domain over all studies and by study (Figure 2; Figure 3).

Figure 2

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Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies

Figure 3

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Risk of bias summary: review authors' judgements about each risk of bias item for each included study

Measures of treatment effect

We planned to convert data obtained from visual analogue scales and any categorical outcomes into dichotomous data prior to analysis. For continuous data, we planned to calculate mean difference with 95% confidence interval (CI). For each trial, we calculated odds ratios (OR) with 95% CIs for all prespecified dichotomous outcomes.

Unit of analysis issues

In parallel‐group studies, the unit of analysis was the individual. In studies where the unit of randomisation was the individual, but more than one tooth/surface was treated per individual (cluster‐randomised studies), we considered tooth/surface as the unit of analysis and standard errors of the estimates were adjusted taking into account the multiplicity or clustering (Deeks 2011). We considered an intracluster correlation coefficient (ICC) of 0.05, based on published data (Vas 2008).

In split‐mouth studies where two tooth/surfaces are randomised per individual, these pairs are not strictly independent (the unit of analysis is the pair) and therefore, were analysed as 'paired data' (Higgins 2003; Deeks 2011). In these cases, we computed design‐adjusted ORs and standard errors with the Becker‐Balagtas method outlined in Elbourne 2002, assuming a conservative correlation coefficient of 0.05 according to Dorri 2015. We planned to calculate the log odds ratio and standard error separately for each outcome.

In cluster split‐mouth studies, where more than two tooth/surfaces are randomised per individual, the unit of analysis is each pair. We considered these trials as split mouth, analysing the pairs independently, ignoring the clustering effect.

Dealing with missing data

We contacted the study authors where data were missing on the trial characteristics, methodology and/or outcomes. We did not consider missing data as a reason to exclude any of the trials from the review. We had planned to impute missing data, if appropriate. However, we did not carry out data imputation as we assumed all missing data to be at random.

Assessment of heterogeneity

We assessed statistical heterogeneity by examining the characteristics of the studies: the similarity between the types of participants, the interventions and the outcomes as described in Section 9.5 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011).

For this purpose we used the I² statistic (Higgins 2003), which examines the percentage of total variation across studies due to heterogeneity rather than to chance. According to the Cochrane Handbook for Systematic Reviews of Interventions the I² values are interpreted as follows (Deeks 2011):

• 0% to 40% might not be important;

• 30% to 60% may represent moderate heterogeneity;

• 50% to 90% may represent substantial heterogeneity;

• 75% to 100% represents considerable heterogeneity.

Assessment of reporting biases

We had planned to assess whether the review was subject to publication bias (or small‐study effects) by using a funnel plot (plots of the effect estimates versus the inverse of their standard errors) (Egger 1997). Asymmetry of the funnel plot may indicate publication bias or other sources of asymmetry including poor methodological quality leading to spuriously inflated effects in smaller studies, true heterogeneity and chance (Sterne 2011). We did not include more than 10 trials in meta‐analysis and therefore, a funnel plot to explore possible publication biases was not indicated. For future updates, if more than 10 trials are included we plan to use a funnel plot to explore publication bias (Egger 1997).

Data synthesis

We pooled only studies that used the same restorative materials in both comparator groups, as different restorative materials require different cavity designs and have different properties that may affect the study outcomes. For example, whilst adhesive restorative materials (e.g. GIC, composite resins) rely on chemical bonding to the tooth for retention, the success of amalgam restoration depends on mechanical retention from the converged cavity walls. This would mean that for an amalgam restoration, following caries removal, the cavity may need to be extended in order to obtain mechanical retention. This may affect the length of procedure, and in turn the patient's experience, and also the restoration survival. In addition GIC releases fluoride that may affect restoration survival.

Our analysis includes data only of those whose results are known, using as a denominator the total number of participants for whom data were recorded for the particular outcome. We expected differences in effect estimates between studies in terms of the number of cavities or surfaces treated per participant and also the duration of follow‐up. Therefore, we applied a random‐effects model for any meta‐analyses (Deeks 2011).

We pooled parallel and split‐mouth data using the generic inverse variance (GIV) (Deeks 2011).

We did not pool data if heterogeneity was over 75%. This was mainly because indicating an average value for the intervention effect when there is a significant inconsistency in the direction of effect may be misleading (Deeks 2011).

We anticipated variation in the timing of endpoints across the studies, both in terms of participant‐reported pain and clinical restoration failure. We included in the meta‐analysis the longest follow‐up reported for each study.

Where studies had multiple intervention or comparator trial arms, we combined summary statistics from all groups where appropriate. We excluded any intervention arms without ART from the meta‐analysis.

The data was analysed using RevMan 5 software (RevMan 2014).

In the event that there were insufficient clinically homogeneous trials for any specific intervention or insufficient study data that could be pooled, a narrative synthesis was presented.

Subgroup analysis and investigation of heterogeneity

We had planned to perform subgroup analysis for dental caries type, as a source of clinical heterogeneity, if sufficient data were available. Therefore, we stratified the analyses in subgroups according to type of cavity surface:

• studies reporting on single lesion;

• studies reporting on multiple lesions;

• studies reporting on single and multiple lesions;

• studies where lesion type was not reported;

• studies reporting on coronal and root lesion, or on root lesions only.

Sensitivity analysis

We had planned to conduct a sensitivity analysis of the primary outcomes by excluding studies with overall high risk of bias (that is high risk of bias in at least one domain). However, all the included studies were at high risk of bias for at least one domain and therefore, we did not carry out a sensitivity analysis.