Primary outcomes

• Prostate cancer‐specific survival [PC‐SS] measured from randomization date to date of prostate cancer death.

• Late gastrointestinal (GI) radiation therapy toxicity (occurring or lasting more than 90 days after RT is completed) Grade II Radiation Therapy Oncology Group/European Organisation for Research and Treatment of Cancer (RTOG/EORTC) or greater toxicity.

• Late gastrointestinal (GU) radiation therapy toxicity (occurring or lasting more than 90 days after RT is completed) Grade II RTOG/EORTC RT or greater toxicity.

Secondary outcomes

• Overall survival measured from randomization date to date of death.

• Metastasis‐free survival measured from randomization date to date of diagnosis of metastatic disease.

• Biochemical relapse‐free survival (BR‐FS) assessed using the Phoenix definition of a rise of 2 ng/mL or more above the prostate‐specific antigen (PSA) nadir after EBRT with or without hormonal therapy (Roach 2006).

• Acute radiation therapy gastrointestinal toxicity. Acute effects of RT were those effects occurring during and within 90 days of starting RT. We used individual protocol‐based definitions.

• Acute radiation therapy genitourinary (GU) toxicity. Acute effects of RT were those effects occurring during and within 90 days of starting RT. We used individual protocol‐based definitions.

• Late radiation‐induced malignancy

• Health‐related quality of life (using trial‐specific instruments) at five years and 10 years.

Handsearching

We searched conference proceedings to identify eligible trials from:

• European Society for Radiotherapy and Oncology (ESTRO) (www‐clinicalkey‐com‐au.ezproxy.library.uq.edu.au/#!/browse/journal/01678140/latest) (searched to 2018);

• American Urological Association (AUA) (www‐clinicalkey‐com‐au.ezproxy.library.uq.edu.au/#!/browse/journal/00225347/latest);

• European Association of Urology (EAU).

We handsearched from 2008 to 2018.

We tried to identify other potentially eligible trials or ancillary publications by searching the reference lists of included trials, systematic reviews, meta‐analyses and health technology assessment reports. We contacted authors of included trials to identify additional information on the retrieved trials and trials that we may have missed.

Dealing with duplicate and companion publications

In the event of duplicate publications, companion documents or multiple reports of a primary trial, we maximized the information yield by collating all available data and used the most complete data set aggregated across all known publications. We listed duplicate publications, companion documents, multiple reports of a primary trial and trial documents of included trials (such as trial registry information) as secondary references under the study ID of the included trial. Furthermore, we listed duplicate publications, companion documents, multiple reports of a trial and trial documents of excluded trials (such as trial registry information) as secondary references under the study ID of the excluded trial.

Data from clinical trial registers

In case data of included trials are available as study results in clinical trial registers such as ClinicalTrials.gov or similar sources, we made full use of this information and extracted data. If there was also a full publication of the trial, we collated and critically appraised all available data. If an included trial was marked as a completed study in a clinical trial register but no additional information was available, we would have added this trial to the Characteristics of studies awaiting classification table.

We constructed and piloted a data extraction form for two studies. Three review authors (MJ, BH, FS) independently performed data extraction, with disagreements resolved by discussion. We entered data into Review Manager 5 for analysis (Review Manager 2014). Where data were limited, we requested further information from the authors of the original studies. For each study, we aimed to collect and report the following details in the Characteristics of included studies table:

• study design;

• inclusion and exclusion criteria for the study;

• setting;

• accrual dates;

• number of participants in each study and in each intervention/comparator group;

• median age and range;

• stage;

• radiation dose;

• dose per fraction;

• number of fractions;

• QA procedures performed (to investigate the quality of radiation delivered);

• type of image guidance used;

• use of androgen deprivation;

• details of outcomes relevant to this review that were assessed in the study, including how measured, the times at which they were measured and any subgroups relevant to this review that were assessed for the outcomes;

• study funding sources;

• declarations of interest for study authors.

We converted the radiation doses to the equivalent dose in 2 Gy fractions (EQD²) (Maciejewski 1986; Withers 1983), using the formula: EQD² = D (d + (α/β)/(2 + α/β), where D = total dose, d = dose per fraction and α/β = Gy (Joiner 1997). This was to facilitate comparison of radiation doses given at a different dose per fraction. No time correction factor was used.

Two studies reported data for biochemical relapse as first event data, which meant we were unable to report these outcomes (HYPRO Dutch 2016; Lukka NCIC 2005). One study reported data for distant metastases as first event data, which meant we were unable to report these outcomes (Lukka NCIC 2005).

We used the methods according to a spreadsheet developed by Matthew Sydes (Parmar 1998; Tierney 2007) to derive log HR and standard error (SE) where necessary.

• We used method three (where HR and 95% CI available)(Tierney 2007) to derive Log HR and SE:

• • metastasis‐free survival (Fox Chase 2013).

• We used method four (where HR number of events in each arm are available and randomization is 1:1)(Tierney 2007) to derive log HR and SE for:

• • overall survival (Lukka NCIC 2005);

  • PC‐SS (Lukka NCIC 2005);

  • metastasis‐free survival (Arcangeli 2010).

• We used method 11 (where data for curve with numbers at risk are available) (Williamson 2002) to derive log HR and SE for:

• • overall survival (Arcangeli 2010; Fox Chase 2013; Yeoh 2011);

  • PC‐SS (Fox Chase 2013).

• We derived log HR and SE by using the Review Manager 5 calculator for (Review Manager 2014):

• • overall survival (CHHiP 2016; HYPRO Dutch 2016; Norkus 2009);

  • BR‐FS (Arcangeli 2010; Yeoh 2011);

  • distant metastasis‐free survival (CHHiP 2016);

  • PC‐SS (HYPRO Dutch 2016).

• We used method 9 (where P value, total number of events and number randomized were available)(Tierney 2007) to derive Log HR and SE for:

• • overall survival (MDACC 2014);

  • BR‐FS (MDACC 2014).

Information about potentially relevant studies (including the study identifier) is provided in the Characteristics of ongoing studies table.

Random sequence generation (selection bias)

For each included trial we described the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.

• Low risk of bias: the trial authors achieved sequence generation using computer‐generated random numbers or a random numbers table. Drawing of lots, tossing a coin, shuffling cards or envelopes, and throwing dice were deemed adequate if an independent person performed this who was not otherwise involved in the trial. We considered the use of the minimization technique as equivalent to being random.

• Unclear risk of bias: insufficient information about the sequence generation process.

• High risk of bias: the sequence generation method was non‐random or quasi‐random (e.g. sequence generated by odd or even date of birth; sequence generated by some rule based on date (or day) of admission; sequence generated by some rule based on hospital or clinic record number; allocation by judgment of the clinician; allocation by preference of the participant; allocation based on the results of a laboratory test or a series of tests; or allocation by availability of the intervention).

Allocation concealment (selection bias due to inadequate concealment of allocation prior to assignment)

We described for each included trial the method used to conceal allocation to interventions prior to assignment and assessed whether intervention allocation could have been foreseen in advance of or during recruitment, or changed after assignment.

• Low risk of bias: central allocation (including telephone, interactive voice‐recorder, web‐based and pharmacy‐controlled randomization); sequentially numbered drug containers of identical appearance; sequentially numbered, opaque, sealed envelopes.

• Unclear risk of bias: insufficient information about the allocation concealment.

• High risk of bias: using an open random allocation schedule (e.g. a list of random numbers); assignment envelopes were used without appropriate safeguards; alternation or rotation; date of birth; case record number; any other explicitly unconcealed procedure.

We also evaluated trial baseline data to incorporate assessment of baseline imbalance into the risk of bias judgment for selection bias (Corbett 2014). Chance imbalances may also affect judgments on the risk of attrition bias. In case of unadjusted analyses, we distinguished between studies we rated as at low risk of bias on the basis of both randomization methods and baseline similarity, and studies we rated at low risk of bias on the basis of baseline similarity alone (Corbett 2014). We reclassified judgments of unclear, low or high risk of selection bias as specified in Appendix 2.

Blinding of participants and personnel (performance bias due to knowledge of the allocated interventions by participants and personnel during the trial) (for subjective and objective outcomes)

We evaluated the risk of detection bias separately for each outcome (Hróbjartsson 2013). We noted whether endpoints were self‐reported, investigator‐assessed or adjudicated outcome measures (see below).

• Low risk of bias: blinding of participants and key study personnel was ensured, and it was unlikely that the blinding could have been broken; no blinding or incomplete blinding, but we judged that the outcome was unlikely to have been influenced by lack of blinding.

• Unclear risk of bias: insufficient information about the blinding of participants and study personnel; the trial does not address this outcome.

• High risk of bias: no blinding or incomplete blinding, and the outcome was likely to have been influenced by lack of blinding; blinding of trial participants and key personnel attempted, but likely that the blinding could have been broken, and the outcome was likely to be influenced by lack of blinding.

Risk of performance bias by outcome

PC‐SS: this investigator‐assessed outcome was not at risk of performance bias in the absence of blinding.

Late GI RT and GU RT toxicity: these self‐assessed or investigator‐assessed outcomes were at risk of performance bias if, for example, trial participants were seen more frequently (in the knowledge that they were having experimental treatment), bias could have been introduced in the absence of blinding.

Overall survival: we felt this investigator‐assessed outcome was not at risk of performance bias.

Distant metastases‐free survival (DM‐FS): this outcome was at risk of performance bias, for example, if trial participants had more frequent investigations (in the knowledge that they were having experimental treatment), bias could have been introduced in the absence of blinding.

BR‐FS: this investigator‐assessed outcome was at risk of performance bias, for example, if trial participants had more frequent investigations (in the knowledge that they were having experimental treatment), bias could have been introduced in the absence of blinding.

Acute GI RT and GU RT toxicity: these self‐assessed or investigator‐assessed outcomes were at risk of performance bias if, for example, trial participants were seen more frequently (in the knowledge that they were having experimental treatment), bias could have been introduced in the absence of blinding.

Second malignancy: this investigator‐assessed outcome was not felt to be at risk of performance bias because it was an objective outcome and likely to have been assessed by clinicians other than the investigators after a long time delay (e.g. 10 to 15 years).

Quality of life: this investigator‐assessed or self‐assessed outcome was at risk of performance bias.

We judged the following outcomes to be similarly susceptible to performance bias and rated them in one group.

• Late GI RT toxicity.

• Late GU RT toxicity.

• Metastasis‐free survival.

• Biochemical recurrence‐free survival.

• Quality of life.

We judged the following outcomes as not susceptible to performance bias and rated them in one group.

• PC‐SS.

• Overall survival.

• Secondary malignancy.

Blinding of outcome assessment (detection bias due to knowledge of the allocated interventions by outcome assessment) (for subjective and objective outcomes)

We evaluated the risk of detection bias separately for each outcome (Hróbjartsson 2013). We noted whether endpoints were self‐reported, investigator‐assessed or adjudicated outcome measures (see below).

• Low risk of bias: blinding of outcome assessment was ensured, and it was unlikely that the blinding could have been broken; no blinding of outcome assessment, but we judged that the outcome measurement was unlikely to have been influenced by lack of blinding.

• Unclear risk of bias: insufficient information about the blinding of outcome assessors; the trial did not address this outcome.

• High risk of bias: no blinding of outcome assessment, and the outcome measurement was likely to have been influenced by lack of blinding; blinding of outcome assessment, but likely that the blinding could have been broken, and the outcome measurement was likely to be influenced by lack of blinding.

We judged the following outcomes to be susceptible to detection bias, thereby making blinding of outcome assessors important.

• PC‐SS.

• Late GI RT toxicity and late GU RT toxicity.

• Metastasis‐free survival.

• Biochemical recurrence‐free survival.

• Quality of life.

Given that risk of judgments for these outcomes were the same, we reported them in one group.

We judged the following outcomes as not to susceptible to detection bias.

• Overall survival.

• Secondary malignancy.

Incomplete outcome data (attrition bias due to amount, nature or handling of incomplete outcome data)

For each included trial and or each outcome, we described the completeness of data, including attrition and exclusions from the analyses. We stated whether the trial reported attrition and exclusions, and the number of participants included in the analysis at each stage (compared with the number of randomized participants per intervention/comparator groups). We noted if the trial reported the reasons for attrition or exclusion and whether missing data were balanced across groups or were related to outcomes. We considered the implications of missing outcome data per outcome such as high dropout rates (e.g. above 15%) or disparate attrition rates (e.g. difference of 10% or more between trial arms) where it was applicable.

• Low risk of bias: no missing outcome data; reasons for missing outcome data unlikely to be related to true outcome (for survival data, censoring unlikely to introduce bias); missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups; for dichotomous outcome data, the proportion of missing outcomes compared with observed event risk is not enough to have a clinically relevant impact on the intervention effect estimate; for continuous outcome data, plausible effect size (mean difference [MD] or standardized mean difference [SMD]) among missing outcomes was not enough to have a clinically relevant impact on observed effect size; appropriate methods, such as multiple imputation, were used to handle missing data.

• Unclear risk of bias: insufficient information to assess whether missing data in combination with the method used to handle missing data were likely to induce bias; the trial did not address this outcome.

• High risk of bias: reason for missing outcome data were likely to be related to true outcome, with either imbalance in numbers or reasons for missing data across intervention groups; for dichotomous outcome data, the proportion of missing outcomes compared with observed event risk enough to induce clinically relevant bias in intervention effect estimate; for continuous outcome data, plausible effect size (MD or SMD) among missing outcomes enough to induce clinically relevant bias in observed effect size; 'as‐treated' or similar analysis done with substantial departure of the intervention received from that assigned at randomization; potentially inappropriate application of simple imputation.

Selective reporting (reporting bias due to selective outcome reporting)

We assessed outcome reporting bias by integrating the results of the appendix 'Matrix of trial endpoints (publications and trial documents)' (Boutron 2014; Jones 2015; Mattieu 2009), with those of the appendix 'High risk of outcome reporting bias according to ORBIT classification' (Kirkham 2010). This analysis formed the basis for the judgment of selective reporting.

• Low risk of bias: the trial protocol was available and all of the trial's prespecified (primary and secondary) outcomes that were of interest in the review were reported in the prespecified way; the study protocol was unavailable, but it was clear that the published reports included all expected outcomes (ORBIT classification).

• Unclear risk of bias: insufficient information about selective reporting.

• High risk of bias: not all of the trial's prespecified primary outcomes were reported; one or more primary outcomes were reported using measurements, analysis methods or subsets of the data (e.g. subscales) that were not prespecified; one or more reported primary outcomes were not prespecified (unless clear justification for their reporting was provided, such as an unexpected adverse effect); one or more outcomes of interest in the Cochrane Review were reported incompletely so that we could not enter them in a meta‐analysis; the trial report failed to include results for a key outcome that we would expect to have been reported for such a trial (ORBIT classification).

Other sources of bias

• Low risk of bias: the trial appeared free of other sources of bias.

• Unclear risk of bias: there was insufficient information to assess whether an important risk of bias existed; insufficient rationale or evidence that an identified problem introduced bias.

• High risk of bias: the trial had a potential source of bias related to the specific trial design used; the trial has been claimed to have been fraudulent or the trial had some other serious problem.

Summary assessment of risk of bias

Risk of bias for a trial across outcomes: some risk of bias domains such as selection bias (sequence generation and allocation sequence concealment), affect the risk of bias across all outcome measures in a trial. In case of high risk of selection bias, all endpoints investigated in the associated trial would be marked as high risk. Otherwise, we would not have performed a summary assessment of the risk of bias across all outcomes for a trial.

Risk of bias for an outcome within a trial and across domains: we assessed the risk of bias for an outcome measure by including all entries relevant to that outcome (i.e. both trial‐level entries and outcome‐specific entries). We considered low risk of bias to denote a low risk of bias for all key domains, unclear risk to denote an unclear risk of bias for one or more key domains and high risk to denote a high risk of bias for one or more key domains.

Risk of bias for an outcome across trials and across domains: these were our main summary assessments that we incorporated into our judgments about the certainty of evidence in the 'Summary of finding' table. We defined outcomes as low risk of bias when most information came from trials at low risk of bias, unclear risk when most information came from trials at low or unclear risk of bias and high risk when a sufficient proportion of information came from trials at high risk of bias.

We present a 'Risk of bias' summary figure (Figure 1).

Figure 1

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

We distinguished between self‐reported, investigator‐assessed and adjudicated outcome measures.

We accepted the following outcomes as self‐reported:

• health‐related quality of life as reported by participants.

We accepted the following outcomes as investigator‐assessed:

• PC‐SS, overall survival, metastasis‐free survival and BR‐FS as measured by trial personnel;

• adverse events: acute and late GU and GI toxicity as measured by study personnel.

Dichotomous data

When at least two included trials were available for a comparison and a given outcome, we tried to express dichotomous data as a risk ratio (RR) with 95% confidence interval (CI) (Deeks 2002).

Continuous data

For continuous outcomes measured on the same scale (e.g. weight loss in kilograms), we estimated the intervention effect using the MD with 95% CI. For continuous outcomes measuring the same underlying concept (e.g. health‐related quality of life) but using different measurement scales, we calculated the SMD with 95% CI (Deeks 2002).

Time‐to‐event data

We expressed time‐to‐event data as hazard ratio (HR) with 95% CI (Cox 1972; Cox 2001). If time‐to‐event data were not available in, or possible to derive from, study reports, and were not available after consultation with study authors, we planned to present the RR with 95% CI as discussed above (at 10 years).

Individual participant data analysis was not performed.

Certainty of the evidence

We presented the overall certainty of the evidence for each outcome according to the GRADE approach, which takes into account issues related to internal validity (risk of bias, inconsistency, imprecision, publication bias) and external validity (directness of results). Two review authors (MJ, BH) independently rated the certainty of evidence for each outcome. We present a summary of the evidence in summary of findings Table for the main comparison. This provides key information about the best estimate of the magnitude of the effect, in relative terms and as absolute differences, for each relevant comparison of alternative management strategies, numbers of participants and trials addressing each important outcome, and rating of overall confidence in effect estimates for each outcome. We created the 'Summary of findings' table based on the methods described in the Cochrane Handbook for Systematic Reviews of Interventions by means of Review Manager 5's table editor (Review Manager 2014). We used the GRADEpro Guideline Development Tool (GDT) software (GRADEpro GDT). We presented results for the outcomes as described in the Types of outcome measures section. If meta‐analysis was not possible, we presented the results in a narrative format in the 'Summary of findings' table. We justified all decisions to downgrade the certainty of studies using footnotes, and we made comments to aid the reader's understanding of the Cochrane Review where necessary.

'Summary of findings' table

We used GRADEpro GDT to create a 'Summary of findings' table following the Cochrane methods and recommendations in Section 8.5 and Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünneman 2011). We used the GRADE approach to evaluate the certainty of the evidence (GRADE Working Group 2004). One author (BH) initially applied the GRADE system and then two authors (BH and MJ) jointly agreed on the decisions made with respect to downgrading in the 'Summary of findings' table, with discussion of the decisions to reach consensus. Our decisions were informed by (but not limited to) the following principles. If a study contributing more than 30% of weight to an outcome was at high risk of bias for domains relevant to that outcome, we downgraded. If there was evidence of unexplained heterogeneity (P less than 0.1 and I² greater than 30%), we downgraded for inconsistency. If studies did not directly evaluate the intervention, we downgraded for indirectness. We downgraded for imprecision if there were fewer than 300 events, if optimum information size (OIS) was not met or if the 95% CI did not exclude 0.75 to 1.25 (this did not exclude clinically insignificant benefits or harms) (Ryan 2016). Because we believed our search had identified all potentially relevant studies, we did not downgrade for publication bias. The assumed control risk used in summary of findings Table for the main comparison was the median control risk in the studies contributing to the comparison.

The review only included RCTs, and we reported four evidence certainty levels: high, moderate, low and very low, with our rationale detailed in the 'Summary of findings' table.