Types of studies

We only included studies with a randomised controlled trial (RCT) design that compared pre‐emptive antifungal therapy with empirical antifungal therapy for people with cancer, in which participants were prospectively identified. Our eligibility criteria included cluster‐randomised and cross‐over trials. We did not include quasi‐randomised (i.e. using a method of allocation that is not truly random) or non‐randomised comparative studies. 

Types of participants

We included studies with adults, 18 years or older, with cancer, who had febrile neutropenia (FN) as a result of chemotherapy or bone marrow transplantation. We did not restrict participants for gender, ethnicity, underlying malignancies (e.g. solid tumours, haematological malignancies, or haematopoietic stem cell recipients), or the type of chemotherapy used. We also included studies with a paediatric population (younger than 18 years), as long as it was less than 33.3% of the total population of the trial.

We defined fever as a single oral temperature reading above 38.3 °C (101 °F), or a temperature above 38.0 °C (100.4 °F) that was sustained for at least one hour; and neutropenia as an absolute neutrophil count (ANC) of 500 cells/mm³ or less, or an ANC that was expected to decrease to less than 500 cells/mm³ during the next 48 hours (Freifeld 2011). When studies used alternative definitions, we included such studies, provided their definitions meant the same as ours. 

Types of interventions

Types of outcome measures

We evaluated one primary outcome and five secondary outcomes.

Electronic searches

We searched the following databases:

• Cochrane Central Register of Controlled Trials (CENTRAL; 2021, Issue 10) in the Cochrane Library (searched 12 October 2021; Appendix 1);

• MEDLINE Ovid (1946 to September week 5 2021; Appendix 2);

• Embase Ovid (1980 to 2021 week 40; Appendix 3);

• PubMed (1966 to October 2021).

We searched trial databases, specifically current controlled trials in the National Institutes of Health database (clinicaltrials.gov/), for ongoing and unpublished trials.

Searching other resources

We reviewed the references of all included studies for additional trials. We handsearched the following conference proceedings:

• European Congress of Clinical Microbiology and Infectious Diseases (2001 to Oct 2021);

• Interscience Conference on Antimicrobial Agents and Chemotherapy (ICAAC) and American Society of Mircrobiology (ASM) Microbe (2001 to Oct 2021);

• Annual Meeting of the Infectious Diseases Society of America (IDSA) and ID Week (2001 to Oct 2021);

• European Society for Medical Oncology Congress (2001 to Oct 2021);

• American Society of Clinical Oncology Annual Meeting (2001 to Oct 2021); and

• American Society of Haematology (ASH) Annual Meeting (2001 to Oct 2021).

Selection of studies

We downloaded all titles and abstracts retrieved by electronic searching into Covidence and removed duplicates. Two review authors (YU and HI) independently screened the titles and abstracts, and excluded those that clearly did not meet the following inclusion criteria:

1. Is the study described as an RCT?

2. Does the study compare pre‐emptive therapy with empirical therapy?

3. Were the participants identified as people with cancer?

We obtained full‐text copies of any potentially relevant references and assessed the eligibility of the retrieved articles. We resolved any disagreement through discussion, or, if required, we consulted a third person (YM). We identified and excluded duplicate reports and collated multiple reports of the same study, so that each study rather than each report was the unit of interest in the review. We recorded the selection process in sufficient detail to complete a PRISMA flow diagram and the characteristics of included and excluded studies tables (Moher 2009).

Data extraction and management

The same review authors (YU and HI) designed a data extraction form (Appendix 4). We extracted the following information and data.

• General information (i.e. title, authors, contact information, country, language and year of publication, sponsors and conflict of interests)

• Trial characteristics (e.g. study design, inclusion and exclusion criteria, publication status, study years, number of centres, randomisation procedure, allocation concealment, blinding procedure, early termination, completeness of data, presence of selective reporting, assessment of compliance, handling of withdrawals, losses to follow‐up, type of analysis, and presence of other sources of bias)

• Participant characteristics (i.e. type of population, inclusion and exclusion criteria, and baseline characteristics)

• Information regarding the intervention (i.e. what test was used before the antifungal drug administration started)

• Information regarding outcomes (e.g. all‐cause mortality, mortality ascribed to fungal infection, IFD detection, proportion of antifungal agent use (other than prophylactic use), adverse events, cost, and other reported outcomes)

• All individuals randomised in the outcome assessment, preferably by intention‐to‐treat; when a single study provided data for multiple measures of the same outcome, we chose the measure that best fit our outcome definitions

• For dichotomous outcomes, we recorded the number of participants manifesting the outcome in each group, as well as the number of evaluated participants per group

• For continuous outcomes, we documented values as well as the measure chosen to report data (e.g. mean with standard deviation (SD) and median with interquartile range)

The two review authors (YU and HI) entered the collected data into the Review Manager 5 file (RevMan 5 (Review Manager 2020)). We double‐checked if the data were entered correctly by comparing the data in RevMan 5 with the study reports. A third review author (YM) independently reviewed the extracted data for accuracy, and resolved any disagreements.

Assessment of risk of bias in included studies

The two authors (YU and HI) independently assessed risk of bias in each study by using the following items:

• selection bias (random sequence generation and allocation concealment),

• performance bias (blinding of participants and personnel),

• detection bias (blinding of outcome assessment),

• attrition bias (incomplete outcome data; defined as high risk when the number of randomised participants was not provided, or the outcome reported was less than 80% of the randomised population without justification),

• reporting bias (selective reporting), and other biases.

We expressed the classification of the specific risks of bias as low, high, or unclear risk of bias, using the criteria suggested in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017). We resolved any disagreement by discussion. We detailed the risk of bias assessment in the Characteristics of included studies table, and graphically presented the results in risk of bias summary tables.

Measures of treatment effect

For continuous outcomes, we extracted means with SD from the studies. If reported differently in a trial, we contacted the trial authors to request the means and SD. We computed the mean difference (MD) and the 95% confidence intervals (CI) for each study. For all dichotomous outcomes, we calculated the risk ratios (RR) for individual studies, with 95% CI. We did not plan to analyse time‐to‐event data (e.g. hazard ratios).

Unit of analysis issues

We presented the included studies in a parallel‐group design; the unit of analysis was expected to be the individual participant. If we included cluster‐randomised trials, we planned to use the published effect estimates, with clustering taken into account. When the original report correctly analysed the cluster‐randomised study, we planned to enter the effect estimate and standard error, using the generic inverse‐variance method in RevMan 5.

If the original report failed to adjust for cluster effects, we planned to include the studies only when we could extract the following information:

• number of clusters randomised to each intervention, or the average size of each cluster,

• outcome data, ignoring the cluster design, for the total number of participants, and

• estimate of the intracluster correlation coefficient (ICC).

We planned to use the ICC from similarly designed studies when such were available. Then, we planned to conduct the approximately correct analysis following the procedures described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022). If multiple‐arm trials were included, we planned to consider within‐study correlation, by calculating the average of the relevant pairwise comparisons from the study, and calculating a variance for the study, accounting for the correlation between the comparisons. If the control group was a common comparator in a comparison, we planned to divide the participants by the number of relevant intervention groups, to avoid double counting the same data. For trials that had a cross‐over design, we planned to only consider results from the first randomisation period, to avoid period effects.

Dealing with missing data

We requested missing information from the study authors, but were not successful in all cases. The primary analysis was an intention‐to‐treat analysis (ITT), wherein all participants randomised to treatment were included in the denominator. This analysis assumed that all losses to follow‐up had favourable outcomes. To explore the impact of the missing data on the summary effect estimate for death, we planned to conduct a sensitivity analysis. 

If the data were not available for an ITT analyses, we analysed the data with a per‐protocol approach. We described and critiqued any methods, such as imputation, reported in the publication to address incomplete data. In the discussion section of the review, we considered the impact of missing data on the review findings. If possible, we planned to impute missing SDs from other reported studies, by using the maximum reported values in those studies. In all cases, we considered the most conservative assumptions.

Assessment of heterogeneity

We tested for statistical heterogeneity between trials by using the Chi² test (P < 0.1 was considered statistically significant), and the I² statistic, along with a visual inspection of the forest plots. We interpreted I² values in accordance with the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022). An approximate guide to interpretation was:

• 0% to 40% might not be important;

• 30% to 60% may represent moderate heterogeneity;

• 50% to 90% may represent substantial heterogeneity;

• 75% to 100% indicates considerable heterogeneity.

We also kept in mind that the importance of the observed value in the I² statistic depends on the magnitude and direction of effects and the strength of evidence for heterogeneity.  We conducted subgroup and sensitivity analyses if the I² was above 50%.

Assessment of reporting biases

Had we pooled more than 10 studies, we planned to proceed with the relevant statistical test for funnel plot asymmetry to explore possible small study biases. Since we pooled fewer than 10 trials, we included a narrative description of the risk of reporting bias.

Data synthesis

We analysed the data using RevMan 5 (Review Manager 2020). We individually combined included studies in a meta‐analysis. Given the nature of the intervention, we used a random‐effects model. When we detected substantial and considerable heterogeneity (I² > 75%), we investigated potential source of the heterogeneity and downgraded the evidence.

For dichotomous data, we pooled RRs by using the Mantel–Haenszel method. For continuous data, we calculated the mean difference (MD) when data were reported using the same scale, or standardised mean difference (SMD) for data reported in different scales. We reported pooled estimates with 95% CI.

Subgroup analysis and investigation of heterogeneity

We pre‐planned and addressed the following potential effect modifiers of the primary outcome (all‐cause mortality). 

• documented infection (clinically or microbiologically) versus fever of unknown aetiology

• high‐risk participants versus low‐risk participants, preferably defined by a Multinational Association for Supportive Care (MASCC) score, but we accepted and documented the study definitions

• people with solid tumour versus people with haematological malignancy

• severity of neutropenia (ANC < 100 cells/mm³ versus ANC between 100 cells/mm³ and 500 cells/mm³), referring to the lowest ANC documented (nadir of neutropenia)

• anti‐mould prophylaxis versus non‐anti‐mould prophylaxis

• selection of antifungal agents

• people undergoing stem‐cell transplantation versus people undergoing chemotherapy (we expected stem‐cell transplantation)

Sensitivity analysis

We planned sensitivity analyses for the primary outcome, based on risk bias (only including data from trials at low risk of bias); missing data (only including data from trials without missing data), and the presence of heterogeneity (only including data from trials with homogenous interventions). We added sensitivity analyses for all‐cause mortality reported in the short‐term (2 to 6 weeks), and medium‐term (7 to 16 weeks). Since Hebart 2009 reported all‐cause mortality at both short‐ and medium‐term time points, we added another sensitivity analysis in which we replaced medium‐term data for short‐term data.

Summary of findings and assessment of the certainty of the evidence

We presented the overall certainty of the evidence for each outcome according to the GRADE approach, which took into account issues related to internal validity (risk of bias, inconsistency, imprecision, publication bias), and external validity, such as directness of results (Langendam 2013; Schünemann 2011). We created a summary of findings table, following the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022), using GRADEPro GDT software. We downgraded the evidence from high certainty by one level for serious (or by two for very serious) concerns for each limitation. We used the GRADE approach and GRADE Working Group certainty of evidence definitions, listed below (Meader 2014). 

• High certainty: we are very confident that the true effect lies close to that of the estimate of the effect.

• Moderate certainty: we are moderately confident in the effect estimate; the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.

• Low certainty: our confidence in the effect estimate is limited; the true effect may be substantially different from the estimate of the effect.

• Very low certainty: we have very little confidence in the effect estimate; the true effect is likely to be substantially different from the estimate of effect.

We evaluated the evidence for all‐cause mortality, mortality ascribed to fungal infection, proportion of antifungal agent use (other than prophylactic use), duration of antifungal use (days), invasive fungal infection detection, and adverse effects, for the comparison between empirical antifungal therapy and pre‐emptive antifungal therapy.

Since we were unable to undertake meta‐analysis for all outcomes, we presented our results in a hybrid summary of findings table format (both quantitative and narrative), such as that used by Chan 2011.