Shorter Versus Longer-term Antibiotic Treatments for Community-Acquired Pneumonia in Children: A Meta-analysis

This systematic review adhered to the Preferred Reported Items for Systematic Reviews and Meta-Analyses 2020 (PRISMA 2020) statement.¹⁸  We registered this systematic review protocol with PROSPERO (CRD42022333292).

We included individual and cluster RCTs enrolling children under 18 years of age with diagnosed CAP according to investigator-defined definitions, including but not limited to the WHO acute respiratory infection guidelines,¹⁰  chest examination by a physician, or diagnosis based on radiologic evidence, clinical signs, or symptoms. Eligible RCTs compared shorter-duration antibiotic treatments with longer-duration antibiotic treatments with a minimum difference of 2 days in duration of therapy and without the requirement that the shorter and longer durations use the same antibiotic regimens. We limited the shorter duration to 5 days or less. There were no restrictions on language of publication, severity of CAP, comorbidity of patients, specific implicated organisms, type of antibiotics, dosage, frequency, or route of administration. Eligible trials reported at least 1 of the outcomes of interest.

We excluded studies investigating hospital-acquired pneumonia and bronchitis. We also included trials enrolling ineligible patients (eg, 18 years or older, with hospital-acquired pneumonia), if the proportion of ineligible patients was 20% or less, or if authors reported separately on our population of interest.

Outcomes of interest included clinical cure, treatment failure, relapse, duration of hospital stay, mortality, need for change in antibiotics, ICU admission, duration of hospital stay, duration of ICU stay, hospital readmission, invasive ventilation, for trials enrolling outpatients the need for hospitalization, severe adverse events, and all adverse events. We did not investigate microbiologic outcomes, such as colonization with antimicrobial-resistant organisms or impact on participants’ microbiota.

With the aid of a medical librarian, we searched Medline, Embase, Cochrane Central Register of Controlled Trials (CENTRAL), and Cumulative Index to Nursing and Allied Health Literature (CINAHL) from inception to April 30, 2022. The search terms included “community acquired pneumonia,” “antibiotic,” “child,” and “randomized controlled trials.” To identify additional eligible studies, we screened the reference lists of eligible studies and relevant systematic reviews. Supplemental Information presents the details of the searches.

We used Covidence (https://covidence.org/) for screening. Pairs of trained reviewers independently screened titles and abstracts of identified records. We retrieved full texts of potentially eligible records to further assess their eligibility. Reviewers resolved any discrepancies by discussion or, if necessary, by adjudication with a third reviewer.

Using a standardized form, pairs of reviewers independently extracted the following data: study characteristics (first author, trial registration, publication year, country, sample size); patient characteristics (diagnostic criteria of pneumonia, age, sex, and severity of disease); characteristics of interventions and comparators (antibiotic administered, dosing, frequency, route of administration, treatment duration, and length of follow-up); and data on each outcome of interest. For outcomes, we extracted data obtained at the same follow-up time points between postintervention and 1 month after the randomization. We did not focus on data obtained at different time points between arms (eg, shorter duration arm on day 4 and longer duration arm on day 6). Reviewers resolved discrepancies by discussion and, when necessary, with adjudication by a third party.

We assessed, using a modified Cochrane risk of bias tool, the risk of bias of eligible RCTs.¹⁹  Paired reviewers evaluated, at the outcome level, the following domains: random sequence generation; allocation concealment; blinding of participants, healthcare providers, data collectors, outcome assessors, and data analysts; incomplete outcome data; selective outcome reporting; and other sources of bias (ie, early trial discontinuation). For cluster RCTs, we further evaluated whether trials selectively enrolled participants within clusters. Reviewers rated each domain as either: definitely or probably low risk of bias (low risk of bias), or probably or definitely high risk of bias (high risk of bias). Reviewers resolved discrepancies by discussion and, when necessary, with adjudication by a third party.

For cluster RCTs, we analyzed data adjusted for the design effect. We used the method (that is, original raw data divided by the design effect) suggested by the Cochrane handbook to calculate the effective sample size and events.²⁰  Using Hartung-Knapp-Sidik-Jonkman method, we performed random-effects meta-analyses in R version 3.6.3 (RStudio, Boston, MA). If results from Hartung-Knapp-Sidik-Jonkman were counter-intuitive, we switched to the DerSimonian-Laird random-effects model. For dichotomous outcomes, we calculated odds ratios (ORs) with 95% confidence intervals (CIs) for clinical cure and relative risks (RRs) with 95% CIs for treatment failure, relapse, need for change in antibiotics, and all adverse events. We applied the continuity correction of 0.5 for trials with 0-event.²¹  To assess the robustness of results, we performed sensitivity analyses by excluding 0-event studies. To facilitate interpretation of the results, we used relative risk estimates and baseline risk to calculate absolute effects for each outcome. We obtained the baseline risk for the need for change in antibiotics from a large observational study.²²  For clinical cure, treatment failure, relapse, and all adverse events for which reliable observational data were not available, we used the median in the control group (longer duration group) from eligible trials as the baseline risk.

For mortality, need for hospitalization, and severe adverse events with very low event rates, we calculated risk differences (RDs) with 95% CIs directly.

We assessed the between-study heterogeneity with a visual inspection of forest plots and the I² statistic. When 10 or more trials were available for an outcome, to assess publication bias, we evaluated the contour-enhanced funnel plots and used Harbord’s test for dichotomous outcomes and Egger’s test for continuous outcomes.^23,24 

If sufficient data were available (at least 2 trials providing relevant information for each subgroup), we performed the following prespecified subgroup analyses:

1. Duration of therapy: comparisons with arms receiving 3 against 5 days antibiotics versus comparisons with arms receiving 3 against 7 days antibiotics versus comparisons with arms receiving 3 against 10 days antibiotics versus comparisons with arms receiving 5 against 10 days antibiotics (hypothesis: larger effects with larger differences between intervention and control).

2. Severity of CAP: nonsevere versus severe or critical (according to investigator-defined definitions) (hypothesis: increased treatment effect in the longer duration group with severe or critical CAP).

3. Age of patients: newborn (less than 1 month) versus infants (≥1 month to 1 year) versus children of preschool age (>1 to 5 years) versus children of school age (>5 to 12 years) versus adolescents (>12 to 18 years) (hypothesis: increased treatment effect in the longer duration group in newborn).

4. Antibiotic class: comparisons with arms receiving antibiotics belonging to the same drug class versus comparisons with arms receiving antibiotics belonging to different drug classes (hypothesis: if more potent antibiotics were in the shorter duration arm, differences would be smaller when drug classes differ between arms; if more potent antibiotics were in the longer duration arm, differences would be greater when drug classes differ between arms).

5. Income of countries: studies conducted in LMICs versus studies conducted in high-income countries (HICs) (according to World Bank Income classification) (hypothesis: differences will be smaller in studies conducted in LMICs).

6. Risk of bias: low versus high risk of bias studies (hypothesis: If studies were superiority designs, differences would be greater in high risk of bias studies; if studies were noninferiority designs, differences would be smaller in high risk of bias studies).

We assessed, using the Instrument for assessing the Credibility of Effect Modification Analyses tool, the credibility of any apparent subgroup effects.²⁵ 

We used GRADE approach²⁶  to rate the overall certainty of the evidence for each outcome. Based on risk of bias,²⁷  imprecision,²⁸  inconsistency,²⁹  indirectness,³⁰  and publication bias,³¹  we rated certainty of evidence as ‘‘very low,’’ ‘‘low,’’ ‘‘moderate,’’ or ‘‘high.’’ We used a minimally contextualized approach and chose the null effect as a threshold.³²  If the point estimate was very close to the null effect, we rated certainty in little or null effect.³²  In such instances, we rated down for imprecision if confidence intervals crossed the threshold of the minimally important difference (MID). This proved to be the case for all outcomes evaluated. We set the MID as 2% for clinical cure, treatment failure, relapse, need for change in antibiotics, and all adverse events, for the need for hospitalization and severe adverse events as 1%, and for mortality as 0.5%.

When studies reported missing outcome data, we conducted a complete case analysis as our primary analysis. To assess the impact of missing outcome data, we performed plausible worst-case sensitivity analyses for each outcome.³³  Whenever missing data imputation strategies did not significantly affect the observed effect, we rated the risk of bias for missing information as low risk of bias for all the pooled trials.³³  We developed the summary of findings tables using optimal formats in MAGIC.app,³⁴  presenting both relative and absolute effects and including plain language summaries with wording following GRADE guidance.³⁵ 

The electronic database searches identified 3029 citations and 6 studies were identified from references of relevant reviews (Supplemental Fig 7). After screening 2344 titles and abstracts and 76 full texts, 16 RCTs^{12–14,36–48}  proved eligible.

Table 1 summarizes the characteristics of eligible studies. The trials were published between 1994 and 2022, 14 were individual patient RCTs, and 2 were cluster RCTs. Seven RCTs were from LMICs and 9 were from HICs. Fifteen were published articles and 1 was a conference abstract. Sample size ranged from 85 to 3000 (total 12 774), mean age ranged from 0.9 to 5.4 years, proportion of males ranged from 50.0% to 62.7%. Eleven trials enrolled outpatients, 2 enrolled both outpatients and inpatients at baseline, and 3 did not provide relevant information, with all trials evaluating oral antibiotics (commonly amoxicillin). Of the 2 trials that enrolled inpatients, 1 included only children who had received <48 hours of antibiotics in hospital and were ready for discharge,¹²  and the other excluded those children with “serious” pneumonia (never defined).⁴³  Consequently, one can infer that the evidence synthesized pertains to children with nonsevere disease who were treated with oral antimicrobial agents as outpatients (as opposed to children with severe or complicated CAP who would require prolonged hospital stays and/or procedural drainage of empyema or effusion). Six trials compared 3 days versus 5 days antibiotic regimens, 3 trials compared 3 days versus 7 days, 3 trials compared 3 days versus 10 days, 5 trials compared 5 days versus 10 days, and 1 trial compared 3 days versus 14 days. Supplemental Table 3 presents inclusion and exclusion criteria of each trial. Supplemental Table 4 presents outcome definitions for clinical cure, treatment failure, and relapse in each trial.

Supplemental Table 5 presents the risk of bias of included studies for each outcome. Six studies were at the definitely or probably low risk of bias in all domains. The main limitations for the remaining 10 studies were inadequate allocation concealment or lack of blinding. The plausible worst-case sensitivity analyses showed that missing data did not materially change the results (Supplemental Table 6).

Ten trials^{13,14,36,39,41,42,44–46,48}  including 7298 patients reported clinical cure. There was probably little or no difference between shorter-duration and longer-duration antibiotics in clinical cure (OR 1.01, 95% CI 0.87 to 1.17; moderate certainty) (Table 2 and Fig 1).

Twelve trials^{13,14,36,38–42,44–46,48}  involving 10 303 patients provided moderate certainty evidence that shorter-duration antibiotics probably have little or no impact on treatment failure (RR 1.06, 95% CI 0.93 to 1.21) compared with longer-duration antibiotics (Table 2 and Fig 2).

Six trials^{13,36,38,42,44,46}  involving 8158 reported relapse. There was probably little or no difference between shorter-duration and longer-duration antibiotics in relapse (RR 1.12, 95% CI 0.92 to 1.35; moderate certainty) (Table 2 and Fig 3).

Eight trials^{12,14,36–38,40,44,47}  involving 9058 patients provided high certainty evidence that duration of antibiotics had little or no impact on mortality (RD 0 fewer per 1000 patients, 95% CI 2 fewer to 1 more) (Table 2 and Fig 4).

Three trials^12,14,40  with 1285 patients provided data on the need for change in antibiotics. Compared with longer-duration antibiotics, shorter-duration antibiotics probably have little or no impact on the need for change in antibiotics (RR 1.03, 95% CI 0.72 to 1.47; moderate certainty) (Table 2 and Fig 5).

Five trials^{14,36,37,39,40}  enrolling 2949 outpatient children addressed the need for hospitalization. Shorter-duration antibiotics probably have little or no impact on the need for hospitalization relative to longer-duration antibiotics (RD 2 fewer per 1000 patients, 95% CI 9 fewer to 5 more; moderate certainty) (Table 2 and Fig 6).

In the 9 trials^{14,37,39,41,43,45–48}  that addressed all adverse events, shorter-duration antibiotics may have little or no impact on all adverse events (RR 0.75, 95% CI 0.44 to 1.28; low certainty) compared with longer-duration antibiotics (Table 2 and Supplemental Fig 8). Six trials^{12–14,36,38,47}  enrolling 7133 patients provide moderate certainty evidence that shorter-duration antibiotics probably have little or no impact in reducing severe adverse events relative to longer-duration antibiotics (RD 0 fewer per 1000 patients, 95% CI 2 fewer to 2 more) (Table 2 and Supplemental Fig 9).

Subgroup analyses identified no suggestion of subgroup effects for the duration of therapy (Figs 1–6 and Supplemental Figs 8 and 9), severity of CAP (Supplemental Fig 10), age (Supplemental Fig 11), antibiotic class (Supplemental Fig 12), income of country (Supplemental Figs 13), or risk of bias (Supplemental Fig 14). Therefore, the use of Instrument for assessing the Credibility of Effect Modification Analyses to assess subgroup effects was not applicable.

Sensitivity analyses after excluding 0-event studies showed similar results to the primary analyses (Supplemental Table 7).

There was no evidence (Supplemental Fig 15) of publication bias in clinical cure and treatment failure.

We found high certainty evidence that shorter-duration antibiotics do not appreciably increase mortality and moderate certainty evidence that shorter-duration antibiotics probably have little or no impact on clinical cure, treatment failure, relapse, need for change in antibiotics, need for hospitalization, and severe adverse events relative to longer-duration antibiotics. Compared with longer-duration antibiotics, shorter-duration antibiotics may have little or no impact on all adverse events.

To our knowledge, our systematic review is the most comprehensive to show the efficacy and safety of shorter versus longer duration of antibiotic treatment in children with CAP. To provide unbiased evidence, we focused on outcomes data obtained at the same follow-up time points between arms within trials and excluded data obtained at different time points between arms from our analyses. We used the latest GRADE approach³²  to rate the certainty of evidence. To facilitate the interpretation of results, we presented absolute effects for all outcomes. We included trials conducted in both LMICs and HICs, further broadening the applicability of our findings; though it may be that there are differences in the typical phenotype of a child with CAP in different regions, and management guidelines are likely to vary, we showed with reasonable certainty that shorter-duration therapy appears to be as efficacious and as safe as longer-duration therapy across a range of settings.

Our study has limitations. First, although we performed comprehensive literature searches and included all available trials, the evidence regarding the ICU admission, duration of hospital stay, duration of ICU stay, hospital readmission, and invasive ventilation was lacking, and data regarding the need for change in antibiotics was limited. Similarly, the data to address prespecified subgroup analyses, including the severity of CAP and age, proved very limited. Given that all trials included participants treated as outpatients with oral antibiotics, our findings are probably not generalizable to those with severe disease requiring prolonged hospitalization and/or procedural drainage of effusion or empyema.

Second, outcome definitions for clinical cure, treatment failure, and relapse were not always consistent across trials. Reassuringly, these inconsistencies did not translate into important heterogeneity.

Third, for treatment failure, relapse, need for change in antibiotics, and all adverse events with 0-event studies, we used the continuity correction of 0.5 for trials with 0-event, although the results may deviate from other methods (eg, treatment arm continuity correction, arcsine difference).⁴⁹  However, our findings were robust to sensitivity analyses after excluding 0-event studies.

Fourth, for some eligible trials using different antibiotic regimens, the duration might be affected by half-lives of antibiotics, although our subgroup analyses on antibiotic class did not identify any subgroup effects. We included trials using various agents and doses of antibiotics, leaving the optimal choice of agent and dose open to question. We are aware that some older trials included used antimicrobial agents that may not still be appropriate today in many regions (eg, erythromycin), given the evolution of antimicrobial resistance in pneumococci.⁵⁰ 

Finally, there exist no consensus criteria for the diagnosis of community-acquired pneumonia. Symptoms of CAP, such as cough and difficulty breathing, are also commonly identified in children with other disease processes, including viral bronchiolitis and asthma exacerbation. Although substantial variability in the interpretation of chest radiographs exists,^51–53  alveolar and lobar consolidation is generally accepted to be reasonably specific⁵⁴  and a normal chest radiograph rules out the presence of significant pneumonia, so chest radiographs can occasionally be helpful. Furthermore, not only is the clinical diagnosis of CAP somewhat subjective, but it is usually extremely difficult to distinguish between viral and bacterial CAP. Nasopharyngeal multiplex molecular diagnostic testing is sensitive for the detection of common respiratory viruses,⁵⁵  so a negative test substantially lowers the probability of a primary viral infection, although a positive test does not rule out the possibility of bacterial disease, as viral-bacterial coinfections are common.⁵⁶  White blood cell counts and other biomarkers, such as C-reactive protein, are not particularly sensitive or specific for etiologic diagnosis in an individual patient and are therefore generally recommended against.¹¹  A positive blood culture for a recognized pathogen (eg S. pneumoniae) is highly specific for bacterial disease, but this occurs very infrequently (2.2% to 7%).^57–59 

These are important considerations for the interpretation of randomized trials comparing treatment regimens for CAP, as the inclusion of children with purely viral disease will bias results toward the null; antibiotic therapy will not have any effect on viral infections. Many clinicians working in LMICs have less access to diagnostics and thus rely more on respiratory rate and oxygen saturation for assessment and management, so children recruited into prospective CAP studies in LMIC settings forming the basis for the WHO recommendations may well have been even more likely to have purely viral disease as compared with those drawn from HIC settings. Acknowledging this issue, a recent low risk of bias RCT comparing 3 days of amoxicillin to placebo for the treatment of CAP in Pakistan⁶⁰  might not have been considered in high-income settings because of a lack of clinical equipoise. In that trial, the authors reported that placebo proved inferior to amoxicillin (4.9% treatment failure compared with 2.6% treatment failure, 95% CI 0.9% to 3.7% higher). We note, however, that 95% of children with CAP treated with placebo experienced clinical cure, and the IDSA guidelines state that antibiotic treatment is not required for young children with nonsevere CAP.¹² 

These considerations raise the possibility that a high prevalence of viral infection may explain the failure to demonstrate a difference between longer and shorter treatment courses for CAP in studies conducted in LMICs. Fortunately, although the majority of patients (10 191) in these studies came from LMICs, a substantial number (2583) come from HICs, and results do not differ substantially by the region in which studies were conducted (Supplemental Fig 13).

Compared with previous systematic reviews,^15–17  our review included a number of large recent RCTs at low risk of bias, substantially increased sample size, assessed additional outcomes (eg, need for change in antibiotics, mortality), tested more subgroup hypotheses, and used GRADE approach to rate the certainty of evidence. Consistent with previous systematic reviews,^15,16  our review suggests the duration of antibiotic therapy likely makes no important difference in patient-important outcomes for CAP in children. A recent systematic review⁶¹  of 4 RCTs involving 1541 children from HICs evaluated the duration of antibiotic treatment in outpatient children over 6 months with CAP. This review reported that a short antibiotic treatment duration of 3 to 5 days might be equally effective and safe compared with a long duration of 7 to 10 days.⁶¹  This finding is consistent with our subgroup analysis results about HICs. Our review further establishes similar effects in LMICs.

Resistance of bacterial pathogens to antibiotics is increasing; the overuse of antibiotics is likely to play an important role in this increase.⁶²  Effectively shortening the duration of antibiotic therapy would also be beneficial in reducing the overall cost of treatment, and improving treatment compliance and tolerability.¹⁶  Though we did not assess antimicrobial resistance explicitly, it seems likely that shortening the duration of antibiotic treatment will have a positive impact on reducing circulating antimicrobial resistance.^63,64  Our review shows that there are probably no substantial differences between shorter-duration and longer-duration antibiotics in clinical cure, treatment failure, relapse, need for change in antibiotics, need for hospitalization, and severe adverse events. Shorter-duration antibiotics do not appreciably increase mortality compared with longer-duration antibiotics. These findings support the use of shorter-duration antibiotics for the treatment of children with CAP. Future studies could also focus on better identifying the many children with primary viral CAP who do not require any antibiotic therapy.

Antibiotic treatment of children with CAP in HICs is usually 7 to 10 days.^11,65  Our review did not identify subgroup effects between comparisons with arms receiving 3 against 5 days antibiotics, 3 against 7 days antibiotics, 3 against 10 days antibiotics, and 5 against 10 days antibiotics, and between LMICs and HICs. These results further suggest that healthcare workers should, regardless of region, prioritize use of 3 to 5 days of antibiotics for children with CAP.

Moderate to high certainty evidence demonstrates that shorter-duration and longer-duration antibiotics likely have similar effects on clinical cure, treatment failure, relapse, mortality, need for change in antibiotics, need for hospitalization, and severe adverse events for children with CAP.

We thank Rachel Couban (librarian at McMaster University) for helping with developing the search strategy. Y.G. and Y.Z. acknowledge funding from China Scholarship Council.

CAP

community-acquired pneumonia

CI

confidence interval

GRADE

Grading of Recommendations Assessment, Development and Evaluation

HICs

high-income countries

LMICs

low- and middle-income countries

OR

odds ratio

RCTs

randomized control trials

RD

risk difference

RR

relative risk