Systemic and topical antibiotics for chronic rhinosinusitis

Types of studies

We included studies with the following design characteristics:

• randomised controlled trials, including cluster‐randomised trials and quasi‐randomised trials (cross‐over trials were only to be included if the data from the first phase were available); and

• patients were followed up for at least two weeks.

We excluded studies with the following design characteristics:

• randomised patients by side of nose (within‐patient controlled) because it is difficult to ensure that the effects of any of the interventions considered can be localised; or

• perioperative studies, where the sole purpose of the study was to investigate the effect of the intervention on surgical outcome.

Types of participants

Patients with chronic rhinosinusitis, whether with polyps or without polyps.

We excluded studies that included a majority of patients with:

• cystic fibrosis;

• allergic fungal sinusitis/eosinophilic fungal/mucinous rhinosinusitis;

• aspirin‐exacerbated respiratory disease;

• antrochoanal polyps (benign polyps originating from the mucosa of the maxillary sinus);

• malignant polyps;

• primary ciliary dyskinesia;

• a history of surgery for nasal polyps within six weeks of entry to the study;

• allergic fungal rhinosinusitis/eosinophilic fungal/mucinous rhinosinusitis; or

• aspirin‐exacerbated respiratory disease (aka Samter's triad).

Types of interventions

We included the following groups of antibiotics:

• macrolides (e.g. clarithromycin, erythromycin);

• tetracyclines (e.g. doxycycline);

• beta‐lactams (e.g. penicillins/cephalosporins) with/without clavulanic acids;

• quinolones.

We included both topically applied and oral antibiotics in the review. We included any dose and duration of treatment.

We defined short courses of antibiotics as up to 28 days, whereas we defined long‐term courses of antibiotics as longer than four weeks.

Types of outcome measures

We analysed the following outcomes in the review, but we did not use them as a basis for including or excluding studies.

Electronic searches

The Information Specialist searched:

• the Cochrane Register of Studies ENT Trials Register (searched 29 September 2015);

• the Cochrane Central Register of Controlled Trials (CENTRAL 2015, Issue 8);

• Ovid MEDLINE (1946 to October week 1 2015);

  • Ovid MEDLINE (In‐Process & Other Non‐Indexed Citations) (searched 29 September 2015);

  • PubMed (as a top up to searches in Ovid MEDLINE) (searched 29 September 2015);

• Ovid EMBASE (1974 to 2015 week 41);

• ClinicalTrials.gov, www.clinicaltrials.gov (search via the Cochrane Register of Studies) (searched 29 September 2015);

• World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (searched 29 September 2015);

• Google Scholar (searched 29 September 2015).

The Information Specialist modelled subject strategies for databases on the search strategy designed for CENTRAL. Where appropriate, they were 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.b. (Handbook 2011). Search strategies for major databases including CENTRAL are provided in Appendix 1.

Searching other resources

We scanned the reference lists of identified publications for additional trials and contacted trial authors where necessary. In addition, the Information Specialist searched PubMed, The Cochrane Library and Google to retrieve existing systematic reviews relevant to this systematic review, so that we could scan their reference lists for additional trials.

Selection of studies

At least two review authors independently screened all titles and abstracts of the studies obtained from the database searches to identify potentially relevant studies. At least two review authors evaluated the full text of each potentially relevant study to determine if it met the inclusion and exclusion criteria for this review.

We resolved any differences by discussion and consensus, with the involvement of a third author for clinical and/methodological input where necessary.

Data extraction and management

Two review authors independently extracted data from each study using a standardised data collection form (see Appendix 2). Whenever a study had more than one publication, we retrieved all publications to ensure complete extraction of data. Where there were discrepancies in the data extracted by different review authors, we checked these against the original reports and resolved differences by discussion and consensus, with the involvement of a third author or a methodologist where appropriate. We contacted the original study authors for clarification or for missing data whenever possible. If differences were found between publications of a study, we contacted the original authors for clarification. We used data from the main paper(s) if no further information was found.

We included key characteristics of the studies, such as study design, setting, sample size, population and how outcomes were defined or collected in the studies. In addition, we also collected baseline information on prognostic factors or effect modifiers. For this review, this included:

• presence or absence of nasal polyps;

• baseline nasal polyp score;

• whether the patient has had previous sinus surgery.

We also noted down whether studies only selected patients with known bacterial colonisation.

For the outcomes of interest to the review, we extracted the findings of the studies on an available case analysis basis; i.e. we included data from all patients available at the time points based on the treatment randomised whenever possible, irrespective of compliance or whether patients had received the treatment as planned.

In addition to extracting pre‐specified information about study characteristics and aspects of methodology relevant to risk of bias, we extracted the following summary statistics for each trial and each outcome:

• For continuous data: the mean values, standard deviations and number of patients for each treatment group. Where endpoint data were not available, we extracted the values for change from baseline. We analysed data from measurement scales such as SNOT‐22 and EQ‐5D as continuous data.

• For binary data: the numbers of participants experiencing an event and the number of patients assessed at the time point.

• For ordinal scale data: if the data appeared to be approximately normally distributed or if the analysis that the investigators performed suggested parametric tests were appropriate, then we treated the outcome measures as continuous data. Alternatively, if data were available, we planned to convert into binary data.

We prespecified the time points of interest for the outcomes in this review. While studies may have reported data at multiple time points, we only extracted the longest available data within the time points of interest. For example, for 'short' follow‐up periods, our time point was defined as 'three to six months' post‐randomisation. If a study had reported data at three, four and six months, we only extracted and analysed the data for the six‐month follow‐up.

Assessment of risk of bias in included studies

Two review authors independently assessed the risk of bias of each included study. We followed the guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011), and we used the Cochrane 'Risk of bias' tool. With this tool we assessed the risk of bias as 'low', 'high' or 'unclear' for each of the following six domains:

• sequence generation;

• allocation concealment;

• blinding of participants, personnel and outcome assessment;

• incomplete outcome data;

• selective reporting;

• other sources of bias.

Measures of treatment effect

We summarised the effects of dichotomous outcomes (e.g. proportion of patients with symptom resolution) as risk ratios (RR) with CIs. For the key outcomes that we presented in the 'Summary of findings' table, we also expressed the results as absolute numbers based on the pooled results and compared to the assumed risk. We also planned to calculate the number needed to treat to benefit (NNTB) using the pooled results. The assumed baseline risk is typically either (a) the median of the risks of the control groups in the included studies, this being used to represent a 'medium risk population' or, alternatively, (b) the average risk of the control groups in the included studies is used as the 'study population' (Handbook 2011). If a large number of studies had been available, and where appropriate, we had also planned to present additional data based on the assumed baseline risk in (c) a low‐risk population and (d) a high‐risk population.

For continuous outcomes, we expressed treatment effects as a mean difference (MD) with standard deviation (SD) (we would have used the standardised mean difference (SMD) if different scales had been used to measure the same outcome, and we would have provided a clinical interpretation of the SMD values).

Unit of analysis issues

This review did not use data from phase II of cross‐over studies or from studies where the patient was not the unit of randomisation, i.e. studies where the side (right versus left) was randomised.

If we had found cluster‐randomised trials, we would have analysed these according to the methods in section 16.3.3 of the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011).

Dealing with missing data

We tried to contact study authors via email whenever the outcome of interest was not reported, if the methods of the study suggested that the outcome had been measured. We did the same if not all data required for meta‐analysis were reported, unless the missing data were standard deviations. If standard deviation data were not available, we approximated these using the standard estimation methods from P values, standard errors or 95% CIs if these were reported, as detailed in the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011). Where it was impossible to estimate these, we contacted the study authors.

Apart from imputations for missing standard deviations, we conducted no other imputations. However, we completed calculations relating to disease severity (measured by patient‐reported symptom scores) as most of the data measured individual symptoms rather than using validated instruments (see 'Imputing total symptom scores' below). We extracted and analysed data for all outcomes using the available case analysis method.

Assessment of heterogeneity

We assessed clinical heterogeneity (which may be present even in the absence of statistical heterogeneity) by examining the included trials for potential differences between studies in the types of participants recruited, interventions or controls used and the outcomes measured.

We would have assessed statistical heterogeneity by visually inspecting the forest plots and by considering the Chi² test (with a significance level set at P value < 0.10) and the I² statistic, which calculates the percentage of variability that is due to heterogeneity rather than chance, with I² values over 50% suggesting substantial heterogeneity (Handbook 2011).

Assessment of reporting biases

We assessed reporting bias as between‐study publication bias and within‐study outcome reporting bias.

Data synthesis

We conducted all meta‐analyses using Review Manager 5.3 (RevMan 2014). For dichotomous data, we planned to analyse treatment differences as a risk ratio (RR) calculated using the Mantel‐Haenszel methods. We planned to analyse time‐to‐event data using the generic inverse variance method.

For continuous outcomes, if all the data were from the same scale, we had planned to pool mean values obtained at follow‐up with change outcomes and report this as a MD. However, if the SMD had to be used as an effect measure, we would not have pooled change and endpoint data.

When statistical heterogeneity is low, random‐effects versus fixed‐effect methods yield trivial differences in treatment effects. However, when statistical heterogeneity is high, the random‐effects method provides a more conservative estimate of the difference.

Subgroup analysis and investigation of heterogeneity

We had planned to conduct some subgroup analyses regardless of whether statistical heterogeneity was observed, as these are widely suspected to be potential effect modifiers. For this review, this included:

• Phenotype of patients: whether patients have chronic rhinosinusitis without nasal polyps, chronic rhinosinusitis with nasal polyps, a mixed group or the status of polyps is not known or not reported. We planned to undertake the subgroup analysis as although there appears to be a considerable overlap between the two forms of chronic rhinosinusitis with regards to inflammatory profile, clinical presentation and effect of treatment (Cho 2012; DeMarcantonio 2011; Ebbens 2010; Fokkens 2007; Ragab 2004; Ragab 2010; van Drunen 2009), there is some evidence pointing to differences in the respective inflammatory profiles (Kern 2008; Keswani 2012; Tan 2011; Tomassen 2011; Zhang 2008; Zhang 2009), and potentially even differences in treatment outcome (Ebbens 2011). The role of microbes in the pathology is also unclear and this makes it uncertain whether antibiotics will have similar effects.

• Class of antibiotics: some antibiotics, such as the macrolides, are known to have some anti‐inflammatory actions in addition to their antibacterial activity.

We planned to present the main analyses of this review according to the subgroups of phenotypes of chronic rhinosinusitis. We intended to present all other subgroup analysis results in tables.

When studies had a mixed group of patients, we planned to analyse the study as one of the subgroups (rather than as a mixed group) if more than 80% of patients belonged to one category. For example, if 81% of patients had chronic rhinosinusitis without nasal polyps, we would have analysed the study as that subgroup.

In addition to the subgroups above, we planned to conduct the following subgroup analyses in the presence of statistical heterogeneity:

• patient age (children versus adults);

• dose;

• duration of treatment;

• method of delivery (dependent on review).

Sensitivity analysis

We planned to carry out sensitivity analyses to determine whether the findings were robust to the decisions made in the course of identifying, screening and analysing the trials. We planned to conduct sensitivity analysis for the following factors, whenever possible:

• impact of model chosen: fixed‐effect versus random‐effects model;

• risk of bias of included studies: excluding studies with high risk of bias (we defined these as studies that have a high risk of allocation concealment bias and a high risk of attrition bias (overall loss to follow‐up of 20%, differential follow‐up observed);

• how outcomes were measured: we planned to investigate the impact of including data where the validity of the measurement was unclear.

If any of these investigations had found a difference in the size of the effect or heterogeneity, we would have mentioned this in the Effects of interventions section.

Results of the search

The searches retrieved a total of 2761 references (after removal of duplicates). We screened the titles and abstracts and subsequently removed 2698 studies. We assessed 63 full texts for eligibility. We included five studies (six papers) and excluded 47 studies (52 papers). Five studies are awaiting assessment. We identified one ongoing study.

A flow chart of study retrieval and selection is provided in Figure 1.

Included studies

There are five studies (six papers) with 293 participants included in this review (Otten 1994; Van Zele 2010; Videler 2011; Wallwork 2006; Zeng 2011). The important characteristics of these studies are summarised below.

Excluded studies

We excluded 47 studies (52 papers) after reviewing the full paper. Further details of the reasons for exclusion are summarised in Characteristics of excluded studies.

We excluded most of the studies (32) due to the duration of follow‐up in the trial not meeting the minimum criteria (three months) as set out in the review protocol inclusion criteria (Agbim 1975; Amini 2009Ansari 2015; Artigas 1989; Beloborodova 1998; Bonfils 2015; Dellamonica 1994; Desrosiers 2001; Edelstein 1993; El'kun 1999; Fan 2014; Huck 1993; Husfeldt 1993; Jareoncharsri 2004; Jervis‐Bardy 2012; Jiang 2008; Korkmaz 2014; Kunel'skaya 2008; Legent 1994; Li 2000; Li 2002; Li 2014; Mannhardt 1980; Namyslowski 1998; Peric 2011; Portier 1996; Rachelefsky 1982; Sreenath 2015; Sykes 1986; Videler 2008; Watanabe 2003; Wei 2011). Of these studies, 18 followed up participants for one month or less (Agbim 1975; Ansari 2015; Artigas 1989; Beloborodova 1998; Edelstein 1993; El'kun 1999; Huck 1993; Husfeldt 1993; Jareoncharsri 2004; Jervis‐Bardy 2012; Jiang 2008; Kunel'skaya 2008; Li 2014; Mannhardt 1980; Portier 1996; Rachelefsky 1982; Sykes 1986; Watanabe 2003). These studies generally included a mixed population of acute sinusitis and participants with acute exacerbations of chronic sinusitis. Participants were randomised to a short course of oral steroids (7 to 14 days) and followed up at the end of the treatment period or up to two weeks after treatment. Seven studies followed up patients for four to eight weeks (Bonfils 2015; Dellamonica 1994; Fan 2014; Legent 1994; Namyslowski 1998; Sreenath 2015; Wei 2011), and four studies for between eight to 12 weeks (Amini 2009; Desrosiers 2001; Korkmaz 2014; Peric 2011). There were three studies where the duration of follow‐up was not clear (Li 2000; Li 2002; Videler 2008); this included one study that was a cross‐over trial (Videler 2008). In this study the outcomes were reported after the first phase at between 8 to 12 weeks, but the precise timing was not clear. In addition, the results of the first and second phase were reported together and it was not possible to separate these out. We attempted to contact the study author for further information but could not establish contact.

We excluded nine studies because the study aims were to investigate the effectiveness of antibiotics in the perioperative, or immediate postoperative, period (Amali 2015; Bobacheva 2012; Chatzimanolis 1998; Haxel 2015; Hiratsuka 1996; NCT01825408; NCT02307825; Schalek 2009; Varvianskaia 2013).

Three studies made comparisons that were not relevant to this review (Hashiba 1997; IRCT201312299014N; Otten 1997). Hashiba 1997 compared clarithromycin with erythromycin, which were both the same class of antibiotic and, therefore, excluded from the review. IRCT201312299014N is an ongoing trial that will compare phonophoresis of erythromycin with pulsed ultrasound. Otten 1997 compared four different interventions: xylometazoline (nasal decongestant) plus antibiotics and drainage, drainage plus xylometazoline plus antibiotics, and a placebo arm.

We excluded two studies due to the design of the study (Bezerra 2014; Kita 1995): both were non‐randomised controlled trials.

We excluded one study as the included population were those with sinobronchial syndrome (Ishiura 1995).

Allocation

Blinding

We assessed two studies to be at a low risk of performance and detection bias as they were both double‐blind studies with both patients and healthcare professionals (outcome assessors) blinded to the treatment group (Videler 2011; Wallwork 2006).

We assessed two studies as having an unclear risk of bias due to blinding (Otten 1994; Van Zele 2010). Both studies stated that they were "double‐blind" but did not provide any further information. Van Zele 2010 provides no information about the dosing schedule of the three arms within the trial (oral steroids, placebo and antibiotics) and what precautions were taken to prevent the participants and healthcare professionals from identifying the treatment arm to which they had been allocated. There was no information about blinding of outcome assessment in the paper.

Zeng 2011 was an open‐label study and so we assessed the risk of bias due to blinding as high.

Incomplete outcome data

Three studies were at a low risk of attrition bias with no patients reported as dropping out of the study in Zeng 2011, a drop‐out rate (with reasons provided) of 5% in Otten 1994, and 8% at the end of treatment and 12.5% at the follow‐up six months from the start of treatment in Wallwork 2006. There were no significant differences in drop‐out rates between the groups in any study.

We assessed both Van Zele 2010 and Videler 2011 to be at a high risk of bias due to incomplete outcome data. In Van Zele 2010, seven of the initial 47 patients dropped out of the study (14.9%) and an intention‐to‐treat analysis was conducted with the last value carried forward. However, all of the patients who dropped out were from the placebo group 7/19 (36.8%). The report implies that they all dropped out after the treatment stage during follow‐up. This may have had an effect on the overall results and no sensitivity analysis appears to have been completed to identify the impact. In Videler 2011, 9/60 participants (15%) did not complete the study. Reasons for non‐completion are given and are distributed equally between the intervention and placebo group. No denominator values were given by group at the final time point, although additional participants dropping out are reported. Denominator values for measuring adverse events (gastrointestinal disturbances) are not reported.

Selective reporting

We assessed all of the studies to be at an unclear risk of bias due to selective reporting (Otten 1994; Van Zele 2010; Videler 2011; Wallwork 2006; Zeng 2011). In Van Zele 2010, many of the results were presented graphically, without providing values at key time periods. The data were not reported in a way that allowed them to be included in the meta‐analysis for this review. Similarly, Videler 2011 did not always present the full results for all outcomes and these were sometimes reported generally rather than by providing the data (e.g. endoscopic score). In Otten 1994, the results are not well presented.

The reporting of adverse events was a particular concern in all of the studies (Otten 1994; Van Zele 2010; Videler 2011; Wallwork 2006; Zeng 2011). No information about whether there were any adverse events was given in three studies (Otten 1994; Wallwork 2006; Zeng 2011). Even in those studies that did present adverse events the methods for recording their measurement were not described (Van Zele 2010; Videler 2011).

A protocol document could be found for two of the five studies (Van Zele 2010; Videler 2011). For Van Zele 2010 (NCT00480298), it was difficult to judge whether there were differences between the protocol and the full paper as the protocol was not detailed. In Videler 2011 (EUCTR‐2005‐001062‐14), there is an additional outcome that is reported in the paper but not presented in the protocol: patient response scale, which was not one of the key outcomes in this review. In both cases we noted that the number of participants that the study aimed to recruit was different from the number actually recruited: 120 planned and 48 recruited for Van Zele 2010, and 120 planned and 60 recruited for Videler 2011.

Other potential sources of bias

Antibiotics versus placebo

See also Table 1.

Three studies reported on this comparison (Otten 1994; Van Zele 2010; Wallwork 2006). Van Zele 2010 (33 participants) compared a tetracycline (doxycycline) with a placebo in adults with massive bilateral nasal polyps or bilateral nasal polyps that had recurred after surgery. Wallwork 2006 (64 participants) compared a macrolide antibiotic (roxithromycin) with a placebo in adults with a history consistent with a diagnosis of chronic rhinosinusitis but without nasal polyps. The remaining paper (79 participants) compared treatment with a cephalosporin‐type antibiotic (cefaclor) with placebo in children with chronic sinusitis but did not report any outcomes relevant to this review (Otten 1994).

Antibiotics plus saline plus intranasal corticosteroids versus placebo plus saline plus intranasal corticosteroids

See also Table 2.

One study (60 participants) reported on this comparison (Videler 2011). The population included people with chronic rhinosinusitis both with and without nasal polyps. The participants were a more severely affected population who had not responded to standard treatment. The study compared a macrolide antibiotic (azithromycin) for 12 weeks against placebo. All participants in both arms used nasal saline irrigation twice daily and the data suggest that 70% of patients also received intranasal steroids.

Antibiotics versus intranasal corticosteroids

One study compared a systemic macrolide antibiotic (clarithromycin) with intranasal steroids (mometasone furoate) in 43 Chinese people with chronic rhinosinusitis without nasal polyps (Zeng 2011).

Antibiotics versus oral steroids

One study (28 participants) compared a tetracycline (doxycycline) (duration approximately 20 days) with a 20‐day course of oral steroids (methylprednisolone) in adults with massive bilateral nasal polyps or bilateral nasal polyps that had recurred after surgery (Van Zele 2010).

Antibiotics versus placebo

Three studies compared antibiotic treatment with placebo (176 participants).

Disease‐specific health‐related quality of life (HRQL) was reported using the SNOT‐20 (0 to 5, 5 = worst quality of life) by one study in adults without nasal polyps (64 participants). At the end of treatment, the SNOT‐20 score was lower in the group receiving three months of treatment with macrolide antibiotics than the placebo group (mean difference (MD) ‐0.54 points, 95% confidence interval (CI) ‐0.98 to ‐0.10). However, three months after treatment it was uncertain whether there was a difference in effect between the groups. We assessed the evidence to be of moderate quality (GRADE).

One study in people with polyps (33 participants) provided information on gastrointestinal disturbances and suspected allergic reaction (rash or skin irritation) 10 weeks after a short course of tetracycline antibiotic treatment (duration ˜20 days) compared with placebo treatment. It was very uncertain whether there was an increase in gastrointestinal disturbances in the antibiotics group (risk ratio (RR) 1.36, 95% CI 0.22 to 8.50; very low quality evidence) or skin irritation (RR 6.67, 95% CI 0.34 to 128.86; very low quality evidence).

None of the studies presented information on patient‐reported disease severity or general health‐related quality of life.

Antibiotics and saline irrigation versus placebo and saline irrigation

One study (60 participants) compared a three‐month treatment course of macrolide antibiotic with placebo; all participants also used nasal saline irrigation and 70% used intranasal corticosteroids. Disease‐specific HRQL was reported using the SNOT‐22 (0 to 110, 110 = worst quality of life). The data for this outcome were highly skewed (medians not reported) and there was baseline imbalance between the groups that could be of clinical importance. The data were difficult to interpret and it is unclear whether there was an important difference between groups after treatment. We assessed the quality of the evidence to be low. To assess patient‐reported disease severity the study authors asked participants to measure the effect of the treatment course on a five‐point scale (‐2 desperately worse to 2 cured) at the end of treatment (three months). We dichotomised this to give a proportion of patients who had improved (considering patients who scored "improvement" and "cured" as improved). There was no difference between the antibiotics and placebo groups; the risk ratio for improvement in symptoms was 1.50 (95% CI 0.81 to 2.79; 56 participants; one study) and there was also a slightly higher number of people who felt worse after the treatment. We assessed the quality of the evidence to be very low.

There was no demonstrable difference in the rate of gastrointestinal disturbances between the groups (RR 1.07, 95% CI 0.16 to 7.10). General HRQL was measured using the SF‐36 instrument. The full results were not reported but the authors state that there was no difference between the two groups at the end of treatment (12 weeks) or two weeks later.

Antibiotics versus intranasal steroids

One study (43 participants) compared a three‐month treatment course of macrolide antibiotic with intranasal corticosteroids in people without polyps. Patient‐reported disease severity was assessed using a composite symptom score (range: 0 to 40; 0 = no symptoms). It was very uncertain whether the effect of antibiotics differed from intranasal steroids as patient‐reported disease severity was similar (MD ‐0.32, 95% CI ‐2.11 to 1.47; low quality evidence).

Antibiotics versus oral steroids (one study)

One study (28 participants) in people with nasal polyps compared a short course of tetracycline antibiotic treatment (unclear duration, ˜20 days) with a 20‐day course of oral corticosteroids. We were unable to extract data on any of the primary or secondary efficacy outcomes from the paper. It was very uncertain whether there was an increase in gastrointestinal disturbances (RR 1.00, 95% CI 0.16 to 6.14) or skin irritation (RR 2.00, 95% CI 0.20 to 19.62) as the results for these outcomes were similar in both groups. We assessed this evidence to be of very low quality.