This systematic review assessed the efficacy of chlorhexidine for the prevention of alveolar osteitis and occurrence of adverse reactions. Databases were searched until 20 April 2011. Trial inclusion criteria were: titles/abstracts relevant to topic; prospective 2-arm (or more) clinical study design. Trial exclusion criteria were: not all entered subjects accounted for; subjects of both groups not followed up the same way; lack of computable data; chlorhexidine not the primary test agent; duplication of data; outcome of interest other than incidence of alveolar osteitis. Individual datasets were extracted from accepted articles. Bias risk in trials was assessed. 10 of 13 included trials were accepted. From these, 16 dichotomous datasets were extracted. Two of six application protocols favoured chlorhexidine over placebo: Single application of 0.2% chlorhexidine gel placed in the socket immediately after extraction versus placebo gel (RR 0.40; 95% CI: 0.18–0.90; p = 0.03) and 0.12% chlorhexidine rinse applied on day of surgery and used twice daily for 7 days postoperatively versus placebo rinse (RR 0.50; 95% CI: 0.27–0.93; p = 0.03). These results are negated due to high bias risk. Chlorhexidine did not cause higher adverse reactions than placebo. Further high-quality randomised control trials are needed.
Alveolar osteitis (AO), more commonly referred to as ‘dry socket’, is a painful debilitating condition that occurs as a complication of tooth extraction in the permanent dentition. There appears to be no consensus on the criteria used to determine the diagnosis of AO. The wide range (1–30%) in the rate of incidence reported in published papers and reviews must be viewed with caution. Generally, the signs and symptoms occur 1–3 days after an extraction and include features such as postoperative pain (unrelieved by analgesics) in and around the extraction site, a partially or totally disintegrated blood clot within the alveolar socket, halitosis or necrotic debris.
Owing to its availability, relatively low cost and proven antimicrobial properties, chlorhexidine has increasingly been used during surgical extraction procedures (either pre-, intra-, and/or postoperatively), to reduce the incidence of AO following treatment (usually third molar extractions). Recently, 3 systematic reviews that assessed the effectiveness of chlorhexidine in reducing the incidence of AO have been published.
Caso et al. examined evidence published until 2002. The more recent review by Minguez-Serra et al. had several limitations. Most importantly, the authors included non-randomised trials, claimed to attempt a meta-analyses without quantifying their pooled data in the form of an odds ratio or relative risk (RR), did not report on a quality assessment of included trials and based their conclusion on a single trial with a relatively small sample size. Hedström and Sjögren reported on the effect estimates of all interventions used for the prevention of AO, including chlorhexidine. Their recommendation of using a 0.12% chlorhexidine rinse preoperatively and postoperatively for 7 days to reduce the incidence of AO was based on two individual trials with different application protocols and a high risk of selection, detection and attrition bias. In an attempt to address these limitations and to update the current evidence, this systematic review sought quantitatively to answer the question whether chlorhexidine, when compared to placebo and/or other interventions, reduced the incidence of AO in patients who had tooth extraction/s. Additionally, the issue of how well subjects tolerated the interventions (reported as lack of adverse reactions) was compared between groups (either chlorhexidine versus placebo or chlorhexidine in one concentration or form versus another).
Materials and methods
10 databases: BBO (Bibliografia Brasileira de Odontologia), Biomed Central, Cochrane Library, Directory of Open Access Journals, LILACS (Literatura Latino-Americana e do Caribe em Ciências da Saúde), Open-J-Gate, OpenSIGLE, PubMed, Sabinet, Science-Direct were searched systematically for articles reporting on clinical trials up to 20 April 2011.
Strings of MeSH and text search terms with Boolean operators: ( chlorhexidine ) AND (‘ alveolar osteitis ’ OR ‘ dry socket ’) were used in searching the databases. Limits activated in the PubMed search were: Humans , Clinical Trial , Meta-Analysis , Randomised Controlled Trial . The non-English databases BBO and LILACS was searched, using the Spanish search terms: clorhexidina [Words] and osteítis alveolar [Words] and prevención [Words] and the Portuguese terms: clorexidina [Words] and osteíte alveolar [Words] and prevenção [Words] .
Articles were selected for review from the search results on the basis of their compliance with the broad inclusion criteria: relevant to the review question; and prospective 2-arm (or more) clinical study. Where only a relevant title without a listed abstract was available, a full copy of the article was assessed for inclusion. The reference sections of accepted articles and systematic reviews were screened, to identify further trials that were not identified through the search strategy.
Only articles that complied with the inclusion criteria were reviewed further. Full copies of articles were reviewed independently by two reviewers (VY and SM). Articles were excluded if: not all entered subjects were accounted for at the end of the trial; subjects of both groups were not followed up the same way; computable (dichotomous or continuous) data for both, test and control group were lacking; chlorhexidine was not tested or not the primary test agent; data were duplicated; and the outcome of interest was other than the incidence of AO. Disagreements between reviewers were resolved by discussion and consensus achieved.
The primary outcome measure was the incidence of AO reported at the patient level (unit of interest is the patient). In cases where the incidence of AO was reported at a tooth level (unit of interest is the tooth) or could be calculated from the reported results of included papers, this outcome was also reported as a secondary measure. The prevalence of adverse reactions (or a lack thereof) reported per group was extracted from included trials and reported. Two reviewers (VY and SM) independently extracted data from the accepted articles. Individual dichotomous datasets for the control and test group were extracted from each article. Where possible, missing data were calculated from information given in the text or tables. In addition, authors were contacted in order to obtain missing information. Disagreements between reviewers during data extraction were resolved through discussion and consensus achieved.
RevMan Version 4.2 statistical software by The Nordic Cochrane Centre, The Cochrane Collaboration (Copenhagen; 2003) was used for statistical analysis. Within the context of this systematic review, both authors noticed that using the older RevMan version facilitated data handling more efficiently than newer software versions. Differences in treatment groups were computed on the basis of RR with 95% confidence intervals (CI).
Datasets were assessed for their clinical and methodological heterogeneity following Cochrane guidelines (The Cochrane Collaboration, 2011). Datasets were considered to be heterogeneous if they differed in type of dentition (primary or secondary), tooth extracted (third molar), concentration of chlorhexidine used (0.12% or 0.2%), formulation (gel or rinse) and instructions for use (had to be consistent across datasets for pooling). The percentages of total variations across datasets ( I 2 ) with 95% CI, computed with MIX Version 1.7 meta-analysis software, were used in assessing statistical in between study heterogeneity. A percentage of total variations across datasets below 25% was considered an indication for low heterogeneity. Only identified homogeneous datasets were combined for meta-analysis.
Quality of studies and assessment of potential bias risk
Two reviewers conducted the quality assessment independently (VY and SM). Disagreements between reviewers were resolved through discussion and consensus. Criteria for quality assessment of trials are listed in Table 1 . Quality assessment of accepted trials was undertaken on the basis of availability of evidence indicating successful prevention of selection and detection/performance bias from the start to end of each trial. If a trial merely reported that randomisation was conducted, reported only the name of the randomisation method used or included a detailed description of the randomisation process without providing any evidence that randomisation was effective throughout the trial, this was regarded as inadequate.
|Score||Criteria||Impact on bias risk|
|Randomisation and concealment|
|A||(i) Randomisation : Details of any adequate type of allocation method that generates random sequences with the patient as unit of randomisation are reported a
(ii) Concealment : Trial provides evidence b that concealment was indeed effective and that the random sequence could not have been observed or predicted throughout the duration of the trial
|Doubts may still exist as to whether the trial results are influenced by selection bias but no indication can be found from the trial report to support such doubt|
|B||(i) Randomisation : Details of any adequate type of allocation method that generates random sequences with the patient as unit of randomisation are reported a
(ii) Concealment : Trial reports on any adequate method to prevent direct observation c and prediction d of the allocation sequence and sequence generation rules
|Despite the implementation of method considered capable of preventing unmasking of the concealed allocation sequence through direct observation and prediction, there are reasons to expect that the concealed allocation sequence may have been unmasked during the course of the trial|
|C||(i) Randomisation : Details of any adequate type of allocation method that generates random sequences with the patient as unit of randomisation are reported a
(ii) Concealment : Trial reports on any adequate method to prevent direct operator observation of allocation sequence and sequence generation rules. c However, the allocation sequence and sequence generation may have been sufficiently predicted
|Despite the implementation of method considered capable of preventing unmasking of the concealed allocation sequence through direct observation, there are reasons to expect that operators could have predicted the concealed allocation sequence|
|D||(i) Randomisation : Details of any adequate type of allocation method that generates random sequences with the patient as unit of randomisation are reported. a
(ii) Concealment : The trial report does not include information on how the allocation of random sequence was concealed. The allocation could have been directly observed and/or predicted
|Despite the theoretical chance for each patient to be allocated to either treatment group, operator knowledge of the allocation sequence may have led to patient allocation that favoured the outcome of one type of treatment above the other|
|0||Trial does not comply with criteria A–D||No guarantee of equal chance for patients to be allocated to either treatment group, thus allocation may have favoured the outcome of one type of treatment above the other|
|Baseline data for randomised trials|
|A||Baseline data collected before randomisation and reported for both treatment groups/Data shows no significant differences between both groups||Evidence is given that randomisation has led to equal groups, suggesting little risk of selection bias|
|B||Baseline data collected before randomisation and reported for both treatment groups/Data shows significant differences between the groups but has been appropriately statistically adjusted||Differences have been adjusted. Thus the influence of possible selection bias appears to be reduced|
|C||Baseline data collected before randomisation and reported for both treatment groups/Data shows significant differences between the groups without being statistically adjusted||Reported differences may be due to ineffective randomisation, thus indicating risk of selection bias|
|0||Trial does not comply with criteria A–C||No evidence is given about whether randomisation has indeed led to equal groups with differences beyond chance; thus differences may exist, indicating selection bias|
|A||Trial reports on any type of method that is known to prevent patient AND operator AND evaluator from discerning whether patients are allocated to the test or the control group (blinding/masking)
Trial reports a process with which the effect of blinding/masking was evaluated, as well as the results of such evaluation
|Evidence is given that the trial results may not have been influenced by detection/performance bias that may have favoured the outcome of one type of treatment above the other|
|B||Trial reports on any type of method that is known to prevent patient AND operator AND evaluator from discerning whether patients are allocated to the test or the control group (blinding/masking)
Trial report does not give reason for doubt that the patient allocation to either the test or the control group has been unmasked throughout the trial
|Doubts may still exist about whether the trial results are influenced by detection/performance bias but no indication can be found from the trial report to support such doubt. No evaluation of the blinding/masking effect has been included in the trial, thus no evidence for lack of bias is given|
|C||Trial reports on any type of method that is known to prevent patient AND operator AND evaluator from discerning whether patients are allocated to the test- or the control group (blinding/masking)
Trial report gives reason for doubt that the patient allocation to either the test or the control group has been unmasked throughout the duration of the trial
|Despite the implementation of method considered to be able to prevent unmasking, there are reasons for expecting that operators/patients could have discovered the allocation|
|0||No process reported or implemented able to blind/mask patients AND operators as to whether patients were allocated to either the test or the control group (it is insufficient to report that blinding/masking was done without reporting the details of the process)||Knowledge about the patient allocation may have caused patients/operators to act in a way that may have favoured the outcome of one type of treatment above the other|
|A||Available case analysis, LTF reported per treatment group/subsequent sensitivity analysis does not indicate a possible risk of bias effect||The trial allows extraction of evidence that the LTF may not have favoured the outcome of one type of treatment above the other|
|B||Available case analysis, LTF reported per treatment group/subsequent sensitivity analysis indicates a possible risk of bias effect||The trial allows assessment of the risk that the LTF may have favoured the outcome of one type of treatment above the other|
|0||Trial does not report number of included participants per treatment group at baseline or give any indication that would allow ascertaining of the LTF rate per treatment group||The trial carries an unknown risk that the LTF may have favoured the outcome of one type of treatment above the other|
a Excluded are types of allocation methods that are considered as inadequate: cluster randomisation, fixed block randomisation with block size 2, minimisation, alternation, randomisation of teeth, use of date of birth or patient record number, ‘quasi’-randomisation, splitmouth.
Where possible, sensitivity analysis was done, using the RevMan Version 4.2 statistical software of The Nordic Cochrane Centre, The Cochrane Collaboration (Copenhagen; 2003), in order to investigate potential attrition bias risk in trials. Results of dichotomous datasets were investigated by assuming a worst-case scenario for lost to follow-up patients (attrition bias) in the test group. This worst-case scenario was constructed by increasing the number of patients with AO in the group that they were assigned to. For example, if the test group had 50 participants and reported an incidence of AO of 10% and a loss to follow-up (LTF) of 10 patients in this group, then the following calculations and adjustments (for a worst-case scenario) were done: 10% of 40 (50 − 10 LTF) = 4. Therefore 4 of the 40 patients were diagnosed with AO. For attrition bias, the worst-case scenario assumes that the 10 patients LTF experienced the event, i.e. 4 + 10 of 50 patients in the test group were diagnosed with AO. Now, the incidence of AO = 14/50 = 28%.
The true incidence of AO remains unknown but can significantly affect the outcome of the comparison between the groups. For the control group, a more positive best-case scenario was assumed for LTF patients in this group. For example, if a 10% incidence of AO and an LTF of 10 patients in a control group of 50 participants were reported, the following calculations and adjustments (for best-case scenario) were done: 10% of 40 (50 − 10 LTF) = 4. Therefore 4 out of the 40 patients were diagnosed with AO. For attrition bias, the best-case scenario assumes that the 10 patients LTF did not experience the event. Now, incidence of AO = 4/50 = 8%.
Any changes in the statistical significance ( p < 0.05) between both values were regarded as indicators of attrition bias risk.
To investigate publication bias, a funnel plot was generated, using datasets from the included clinical trials. The standard error (SE) of the mean differences was plotted on the Y -axis, and the natural logarithm of RR on the X -axis, using MIX Version 1.7 meta-analysis software. In addition, Egger’s linear regression method was used to calculate an intercept with a 95% CI, with statistical significance set at α = 0.05. The overall in between datasets heterogeneity was considered ( I 2 – 95% CI) in the interpretation of the funnel plot and Egger’s regression results.
Figure 1 provides information on the number of papers identified through the search strategy and the flow diagram provides a summary of the selection processes used. All included articles were identified in PubMed. The literature search in the other sources did not yield additional suitable trials. From the 16 articles initially identified, 13 clinical trials were considered for possible inclusion. The full article of one trial could not be traced at the time of data analysis, even though a copy was requested in writing from the authors. It was excluded from this review. Three further trials were identified during reference check. From the identified total 15 trials, 5 were excluded. Table 2 gives reasons for the exclusion of these trials that did not comply with the exclusion criteria used in this review. The results presented were obtained from 10 trials.
|Author||Reason for exclusion|
|Metin et al.||Full copy of paper not available at time of data-analysis|
|Fridrich and Olson||Chlorhexidine not tested|
|Torres-Lagares et al.||Duplication of data: pilot study where same data used in a later trial|
|Bloomer and Tex||Chlorhexidine was not the primary test agent|
|Bonnie||Non-randomised trial; treatment protocol differed in test and controls|
|Fotos et al.||Outcome of interest was postoperative discomfort|