Establish That a Trial Really is Needed Before You Start

You should not undertake a trial unless someone (if necessary, you) has first undertaken a recent systematic review and established that your research question has not already been answered (Carpenter, Reference Carpenter1993). If trials have already investigated your research question but have yielded inconclusive results, you can use extended funnel plots to determine if a new trial could resolve the uncertainty (Ferreira, Herbert, Crowther, Verhagen, & Sutton, Reference Ferreira, Herbert, Crowther, Verhagen and Sutton2012). You should also search trial registries to establish whether another trial investigating the same question is currently underway. The World Health Organisation's International Clinical Trials Registry Platform searches many trial registries simultaneously (http://apps.who.int/trialsearch/).

Get Help from Experts, Especially a Statistician, Before you Start

Unless you are already an expert, you will need assistance to conduct your trial. Statisticians are particularly helpful because they can provide advice on the many statistical issues that influence most aspects of trial design. Find a statistician who has experience in the design and analysis of clinical trials. Don't wait until you are ready to analyse the data before consulting a statistician – the time you most need a statistician's help is during the design phase of the trial.

Seek the Advice and Input of Clinical Staff

Seek the advice and input of clinical staff at clinical trial sites. If possible, include them in the research team. Clinicians provide a crucial perspective, and you will need the assistance of local clinical staff to solve logistical problems. You will find clinical staff most helpful if you involve them in all aspects of the trial.

Ask an Important Question

Clinical trials should answer important questions (Guyatt, Reference Guyatt2006). Of course importance is often a matter of perspective – the research question that one person thinks is important may not be important to others. Important trials are those that resolve clinical dilemmas, change clinical practice and, ultimately, improve survival or quality of life. The best trials address issues that are universally regarded as important. Don't waste effort conducting trials that are not important.

Explicitly Define the Trial's ‘PICO’

The elements of a trial's objectives can be summarised by its ‘PICO’ (Richardson, Wilson, Nishikawa, & Hayward, Reference Richardson, Wilson, Nishikawa and Hayward1995). PICO is an acronym: P is the trial participants, I is the intervention, C is the comparator and O is the outcome. Your trial should be designed to explicitly investigate the effect of an Intervention compared to a Comparator on an Outcome in a particular population of Participants. Clearly articulate all elements of the PICO in reports of your trial.

Be Clear about Whether Your Trial is Explanatory or Pragmatic

Explanatory trials seek to determine the efficacy of a precisely defined intervention administered under ideal conditions. They tell us about potential treatment effects. In contrast, pragmatic trials seek to determine the effects of an intervention as typically administered. They tell us about the actual effects of an intervention realised in clinical practice. Both explanatory trials and pragmatic trials are useful but they have different purposes (Godwin et al., Reference Godwin, Ruhland, Casson, MacDonald, Delva, Birtwhistle, Lam and Seguin2003; Herbert, Reference Herbert and Gad2009; Schwartz & Lellouch, Reference Schwartz and Lellouch2009; Thorpe et al., Reference Thorpe, Zwarenstein, Oxman, Treweek, Furberg, Altman and Chalkidou2009; Treweek & Zwarenstein, Reference Treweek and Zwarenstein2009).

Your choice of perspective (explanatory or pragmatic) has many implications for trial design and analysis (Herbert, Reference Herbert and Gad2009). For example, if you conduct an explanatory trial it is important that adherence to the allocated group is near-perfect and that trial participants are blinded, but if you conduct a pragmatic trial you don't need to be so concerned about adherence and you might be less likely to blind trial participants. Once you have decided on the type of trial you want to undertake, consult matrices about the key features of explanatory or pragmatic trials to ensure that the design of your trial matches your perspective (Treweek & Zwarenstein, Reference Treweek and Zwarenstein2009).

Nominate the Smallest Worthwhile Effect of Your Intervention before You Start

The smallest worthwhile effect of an intervention is the smallest effect that makes the intervention worth its costs, risks and inconveniences (Barrett, Brown, Mundt, & Brown, Reference Barrett, Brown, Mundt and Brown2005; Cook et al., Reference Cook, Hislop, Altman, Fayers, Briggs, Ramsay and Delta group2015; De Vet & Terwee, Reference De Vet and Terwee2010). Before you start your trial, you need to nominate what you believe is the smallest worthwhile effect of your intervention. This parameter is used to calculate sample size and to interpret the trial's data. The smallest worthwhile effect should be articulated in the trial protocol. The best way to determine the smallest worthwhile effect of an intervention is to ask people who may become, or are, or have been, recipients of the intervention. Ferreira and colleagues review methods for determining the smallest worthwhile effect (Ferreira et al., Reference Ferreira, Herbert, Crowther, Verhagen and Sutton2012).

Keep the Design as Simple as Possible

Even the simplest trials can be difficult to conduct, analyse and interpret. Complex trials can be overwhelming. Minimise potential problems by keeping the design as simple as possible. For example, where possible conduct a two-armed trial rather than a three-armed trial, measure outcomes on as few occasions as needed to answer the research question, and avoid non-standard designs (e.g., non-inferiority designs, preference trials and adaptive designs) unless you have sufficient knowledge, skills, resources and support to do them well.

Make Sure the Trial is Big Enough to be Conclusive

Many trials yield inconclusive findings, particularly trials involving people with brain impairments (Bragge et al., Reference Bragge, Synnot, Maas, Menon, Cooper, Rosenfeld and Gruen2016; Maas et al., Reference Maas, Murray, Roozenbeek, Lingsma, Butcher, McHugh and Steyerberg2013). Inconclusive trials are those that neither rule in nor rule out clinically important effects. Often the inconclusive finding arises because the trial was too small. You can reduce the risk of conducting an inconclusive trial by basing the choice of sample size on formal sample size calculations (Bland, Reference Bland2009; Hoenig & Heisey, Reference Hoenig and Heisey2001; Julious & Campbell, Reference Julious and Campbell2012; Matthews & Altman, Reference Matthews and Altman1996). Sample size calculations can tell you how big your trial needs to be to reduce the risk of inconclusive findings to an acceptable level. However, these calculations are almost always based on uncertain data. Therefore, use them with caution and if in doubt, make your trial bigger rather than smaller because it is unlikely that your trial will be too large.

Don't Call a Small, Underpowered Trial a ‘Pilot Study’

Feasibility and pilot studies are not the names given retrospectively to small, inconclusive trials (Leon, Davis, & Kraemer, Reference Leon, Davis and Kraemer2011; Thabane et al., Reference Thabane, Ma, Chu, Cheng, Ismaila, Rios and Goldsmith2010). Rather, feasibility and pilot studies are specifically designed to determine whether a definitive trial is feasible, to refine the trial methods, and to demonstrate that the trial team is capable of conducting the trial. Importantly, feasibility and pilot studies do not seek to evaluate efficacy or effectiveness, and usually they are not designed to test a hypothesis.

Eldridge and colleagues provide a useful commentary on the similarities and distinctions between feasibility and pilot studies (Eldridge et al., Reference Eldridge, Chan, Campbell, Bond, Hopewell, Thabane, Lancaster and Group2016). Both feasibility and pilot studies focus on practical issues, such as whether participants will be willing to be randomised, whether recruitment targets can be met, whether participants will comply, and whether the intervention is acceptable (Arain, Campbell, Cooper, & Lancaster, Reference Arain, Campbell, Cooper and Lancaster2010). Feasibility studies do not always include a control group and when they do, they do not necessarily include random allocation or blinded assessments. In contrast, pilot studies tend to include a control group and involve random allocation, and are often run as a small version of the definitive trial. Both feasibility and pilot studies should clearly articulate the outcomes of interest in their protocols. Outcomes should include objective measures of feasibility, such as number of screen failures, percentage of treatments administered as intended, amount of missing data and success of blinding. Estimates of effects of treatments (between-group differences) are rarely meaningful or of interest in feasibility and pilot studies.

Determine Feasibility before Starting

Many trials are never completed. Unfinished trials waste time, effort, resources and goodwill of participants, clinicians and trial staff. The most common reason for abandoning a trial is failure to recruit sufficient participants. To avoid this outcome, obtain realistic estimates of probable recruitment rates prior to initiating a trial. One way to do that is to have a dummy recruitment period over a few months in which potentially eligible patients are asked whether they would be willing to participate in a similar hypothetical trial. Don't commence a trial unless there are good prospects for recruitment and completion.

Try not to Ask for Too Much from Participants

Remember that participation in clinical trials is voluntary. Participants are free to withdraw at any time. If you ask participants to attend a clinic too many times, or subject them to unpleasant procedures or too many investigations, some will choose to withdraw from the trial. That can seriously compromise the validity of the trial's findings.

Determine Both the Immediate and Lasting Effects of the Intervention

Most trials measure primary outcomes immediately after or soon after an intervention has finished. This is appropriate if you are only interested in the short-term effects of an intervention. However, the long-lasting effects of an intervention are often of more interest, particularly in studies of people with brain impairment (Hoffer, Szczupak, & Balaban, Reference Hoffer, Szczupak and Balaban2016). So always consider measuring the long-term effects of an intervention.

Use Scales of Trial Quality to Assess and Refine the Design of Your Trial before You Start

There are many scales and checklists that can be used to assess the quality of, or risk of bias in, clinical trials. Examples are the Cochrane Risk of Bias tool and the PEDro scale (Day & Altman, Reference Day and Altman2000; Maher, Sherrington, Herbert, Moseley, & Elkins, Reference Maher, Sherrington, Herbert, Moseley and Elkins2003; Schulz, Chalmers, Hayes, & Altman, Reference Schulz, Chalmers, Hayes and Altman1995). Once you have written a draft trial protocol, use a checklist or scale to assess your trial. Think about ways to improve the design of your trial if it gets anything less than a perfect score.

Register the Trial before the First Participant is Randomised

Registration of trials reduces the risk of publication bias and lessens the potential for selective reporting of trial outcomes. Failure to register a trial prior to randomisation of the first participant will automatically disqualify the trial from being published in most good clinical journals. So don't randomise anyone into your trial until the trial has been registered.

Make the Full Protocol Publicly Available Early in the Course of the Trial

You should write a detailed trial protocol which adheres to the SPIRIT guidelines (An-Wen et al., Reference An-Wen, Jennifer, Peter, Douglas, Howard, Jesse and David2013). You can use the publicly available protocols of high quality trials as a model for your own protocol. Your protocol should be endorsed by all the investigators and dated. Any subsequent changes to the protocol should be documented and dated. It is good practice to make your protocol publically available (for example, by publishing it in a journal or placing it in a publicly available repository). This is best done early in the course of the trial (Whitehead, Reference Whitehead2004). Your protocol is your rule book that is consulted and followed to the letter whenever uncertainties arise over the course of the trial.

Ensure the Randomisation Process can be Audited

Randomisation is what differentiates true experiments from observational studies and permits robust causal inference (Altman & Schulz, Reference Altman and Schulz2001; Gluud, Reference Gluud2006). This crucial process needs special attention. Make sure the randomisation process is auditable. Once the trial has been completed you should be able to show how the allocation sequence was generated and demonstrate that the sequence was respected in the trial. This usually requires keeping read-only files containing the allocation sequence and a record of when each trial participant was randomised. Coin-tossing or pulling numbers out of a hat might generate random allocation sequences but these processes are not auditable so they should not be used.

Conceal the Allocation Schedule

The recruitment of participants must not be influenced by knowledge of which group the next-recruited participant will be allocated to. If recruiters know the allocation schedule then the randomisation process can be compromised. To prevent this problem, the randomisation sequence needs to be concealed. This means that the allocation schedule should be generated by an independent person (Altman & Schulz, Reference Altman and Schulz2001; Elkins, Reference Elkins2013), and kept hidden from all staff involved in the recruitment process. Note that concealment is different from blinding. In blinded trials, the assessors and sometimes other staff are unaware of participants’ allocation for the duration of the trial (Day & Altman, Reference Day and Altman2000).

Don't Interfere with the Randomisation Sequence

Once the allocation sequence has been generated it must not be changed. That means, amongst other things, that once a person is randomised they cannot be re-randomised and another person cannot be randomised in that person's place.

Follow ICH-GCP Guidelines Where Possible

The International Conference on Harmonisation (ICH) has laid down Good Clinical Practice (GCP) standards (European Medicines Agency, 2002). Despite the name, ICH-GCP standards are standards for clinical trials not standards for clinical practice. The standards cover clinical trial management, roles and responsibilities of trial personnel, ethical conduct of clinical trials, responsibilities toward trial participants, reporting of adverse events, and processes for establishing the authenticity of trial data. The standards were written for pharmaceutical trials but can also be applied to trials of non-pharmaceutical interventions. Strict adherence to ICH-GCP is difficult and costly. For example, the ICH-GCP standards mandate reporting all adverse events in all trial participants over the course of their participation in the trial, regardless of whether the adverse events are or are not caused by the trial intervention (see “In all but low-risk trials, record all adverse events and report all serious adverse events”).

Collect Redundant Contact Information at Baseline

A critical feature of robust clinical trials is that they obtain follow-up data from all or nearly all trial participants (i.e., all or nearly all people who were randomised). Substantial loss to follow-up potentially compromises the validity of a trial's findings. Several strategies can be used to maximise follow-up (Robinson, Dennison, Wayman, Pronovost, & Needham, Reference Robinson, Dennison, Wayman, Pronovost and Needham2007). One of the simplest is to collect a variety of contact details for the participant.

Blind Assessors

Blinding reduces the potential for bias in clinical trials. It may be difficult or impossible to blind participants and clinicians, particularly in trials of complex interventions. However, there are few practical or methodological reasons not to blind assessors (i.e., the trial staff who collect outcome data) (Day & Altman, Reference Day and Altman2000).

In All but Low-Risk Trials, Record all Adverse Events and Report All Serious Adverse Events

Adverse events include any untoward medical occurrence (European Medicines Agency, 2002). Serious adverse events are those that are life-threatening, require hospitalisation, or result in disability, incapacity or death. Neither adverse events nor serious adverse events need be caused by the trial intervention. For example, a serious injury sustained in a car accident during a trial is a serious adverse event even though it is unlikely to have been caused by the trial intervention.

Standards for reporting of adverse events have largely been driven by the need to protect the safety of participants in commercially sponsored pharmaceutical trials. If you conduct a commercially sponsored pharmaceutical trial you will need to document all adverse events and report all serious adverse events to the relevant ethical review committee (Irving et al., Reference Irving, van den Bor, Welsing, Walsh, Alfonso-Cristancho, Harvey and GetReal Work2017).

There is debate about whether the same level of reporting should be required for low-risk, investigator-driven trials because, while it may be ideal to collect and report these data, it also makes trials expensive and demanding for both investigators and participants (Wallace, Myles, Zeps, & Zalcberg, Reference Wallace, Myles, Zeps and Zalcberg2016). Our position is that all serious adverse events should be reported but that documentation and reporting of adverse events that are clearly not related to the intervention should be consistent with the level of risk in the trial.

Double-Enter Data

When data are collected on paper forms and then manually entered into a computer database, they should be double-entered: two people should independently enter the data. Any discrepancies should be resolved as soon as possible after the data were collected.

Use a Well-Constructed Database

Well-constructed databases are secure, highly customisable, provide data checks at the time the data are entered, and provide a complete audit trail. We recommend REDCap software. You can use REDCap at no cost if your institution is a REDCap Consortium partner.

Check and Correct Data as the Trial Progresses but do so without Knowledge of Allocation

Data should be checked as they accrue. The objective of checking data is to identify, as early as possible, any issues with trial procedures or data entry. Data checks should be conducted by someone who is blinded to allocation. Any corrections made to data should be clearly documented and justified.

Try to Collect Outcome Data from Every Participant, Even Those who Stop Receiving the Intervention

Ideally, the primary analysis of your trial will include data from every trial participant (see “Analyse by intention to treat”). That means, provided the participant consents, you should collect outcome data from participants even if they stop receiving the allocated intervention or do not comply in some other way with the trial protocol.

If Appropriate, Convene a Data Monitoring Committee

Many but not all trials have an independent Data Monitoring Committee (or Data Safety Monitoring Board) charged with protecting the safety of trial participants (Montori et al., Reference Montori, Devereaux, Adhikari, Burns, Eggert, Briel and Guyatt2005). If the primary or secondary outcomes of your trial include serious adverse events or death you should convene a Data Monitoring Committee. But if your trial examines the effects of a low-risk intervention on other sorts of outcomes (e.g., the effects of different orthoses on ambulation) then you may not need to convene a Data Monitoring Committee. If you convene a Data Monitoring Committee, you will need to write a charter that outlines how the committee is to operate. Excellent guidelines are available (DAMOCLES Study Group, 2005; Ellenberg, Fleming, & DeMets, Reference Ellenberg, Fleming and DeMets2002).

Get Statistical Help

Many researchers are capable of conducting rudimentary statistical analyses. However, it is difficult to conduct analyses rigorously, optimally, efficiently and in a way that is completely transparent and auditable. It is even more difficult to properly interpret the output of analyses. So most clinical trials need the services of a professional statistician, preferably one with experience in clinical trials. The best way to involve a statistician is as a collaborator. Find a statistician collaborator and involve this person in your trial from the early stages of the design of the trial.

Write a Detailed Statistical Analysis Plan Well before the Trial is Completed

Every trial needs a statistical analysis plan. The statistical analysis plan lays out in detail how the trial is to be analysed. Like a trial protocol, the plan should be ratified by the investigators, dated, and made available on a public repository prior to looking at the data or commencing the analysis. Any changes to the plan should be documented and dated. A clear statistical analysis plan will help you conduct a disciplined analysis and should reduce the temptation for selective reporting.

Code the Analysis

You need to have a permanent record of exactly how the data were analysed. This will be invaluable when, inevitably, you need to revisit the analysis at a later date (for example, in response to queries by journal reviewers). Most statistical software will generate a permanent record of the commands (code) used to analyse the data. For example, SAS can generate ‘SAS program’ files, Stata can generate ‘do’ files, and SPSS can generate ‘syntax’ files. Properly written code can be re-run, replicating the original analysis. Make sure that all of the analysis is coded. Keep a copy of the file or files containing the code, and pair those files with the data file that the code was applied to. That way you will always be able to exactly reproduce your analysis.

Practice Meticulous Version Control

Once all data have been entered and checked, lock the database. Save it as a read-only file which can only be changed with a password. Ideally this file is never changed. If, subsequently, data entry errors are detected in the database, they can be corrected in one of two ways. One approach is to write the corrections into the code, along with explanations about why and when the corrections were made. Running the code corrects the errors before the data are analysed but does not save the corrections to the database. An alternative approach is to correct the errors in the database and save the corrections. Whenever the database is changed, the changes must be documented. Data entry errors should only be corrected by someone blinded to group allocation.

It usually takes some time to write the analysis code, and it may be necessary to make corrections to the code along the way. Freely available open-source version control software (such as Git; https://git-scm.com/) can be helpful for keeping track of changes made to the code. Both the database and code must be securely archived.

If Someone does the Analysis for You, Ask Them to Provide You with an Interpretation of the Analysis (Not Just the Output of the Analysis)

If you need a statistician to conduct the analysis, you need them to interpret the analysis too. Ask for a plain language interpretation of the analysis in writing.

If Someone does the Analysis for You, Insist on Having Access to Data Files and a Complete Copy of the Code used to Conduct the Analysis

You must have access to the data files and the code used to analyse the data in your trial.

Check the Code used to Analyse the Data

Statisticians make mistakes too. So, all the code, even code written by experienced statisticians, should be independently checked.

Analyse by Intention to Treat

The primary analysis should almost always be an analysis by intention to treat. That is, the analysis should be conducted on all available data from every participant (i.e., from every person who was randomised) and each participant's data should be analysed in the group to which he or she was allocated (Abraha et al., Reference Abraha, Cherubini, Cozzolino, De Florio, Luchetta, Rimland and Montedori2015; Fergusson, Aaron, Guyatt, & Hebert, Reference Fergusson, Aaron, Guyatt and Hebert2002; Hollis & Campbell, Reference Hollis and Campbell1999; Lachin, Reference Lachin2000; Sedgwick, Reference Sedgwick2015; White, Horton, Carpenter, & Pocock, Reference White, Horton, Carpenter and Pocock2011). Some argue that if data are missing then it is impossible to strictly adhere to the principles of intention-to-treat regardless of data imputation, and instead the term modified intention-to-treat should be used (Abraha et al., Reference Abraha, Cherubini, Cozzolino, De Florio, Luchetta, Rimland and Montedori2015). There are a few legitimate reasons to exclude randomised participants from an intention-to-treat analysis including when ineligible patients are erroneously randomised (Fergusson, Aaron, Guyatt, & Hebert, Reference Fergusson, Aaron, Guyatt and Hebert2002).

Pre-Specify Covariates

A common practice, when analysing data from randomised trials, is to test for baseline imbalances between groups. Then, if baseline imbalances are found in a particular variable, that variable is included as a covariate in the analysis to ‘adjust’ for the baseline imbalances. This practice is inadvisable both because it is unnecessary (confidence intervals properly account for the uncertainty generated by observed and unobserved baseline imbalances) and because data-dependent selection of covariates potentially creates more bias than it removes (Hauck, Anderson, & Marcus, Reference Hauck, Anderson and Marcus1998).

A better justification for adjusting for covariates in randomised trials is to increase statistical precision (in linear regression models) or to prevent bias produced by excluding important predictors of outcome (in models, such as logistic regression and Cox regression models) (Hauck, Anderson, & Marcus, Reference Hauck, Anderson and Marcus1998; Turner et al., Reference Turner, Perel, Clayton, Edwards, Hernandez, Roberts and Collaborators2012). Regardless of the justification, the covariates should be pre-specified in the statistical analysis plan. It is highly inadvisable to adjust for any time-dependent variable that is measured after randomisation.

Focus on Between-Group Differences. Ignore Changes within Groups Over Time

The changes that happen within groups over time should not be interpreted as effects of intervention. Within-group changes over time could be due to many factors, not just the intervention (Bland & Altman, Reference Bland and Altman2011).

Sometimes researchers claim that, because they found evidence of a within-group change in one group and did not find evidence of a within-group change in the other group, there must have been an effect of the intervention. This reasoning is flawed and should not be used. The only way to estimate the effect of an intervention is to determine between-group differences in (or ratios of) outcomes.

Don't be Misled by p Values

Many researchers analyse their clinical trials with significance tests or hypothesis tests and interpret p values of less than 0.05 as evidence of a treatment effect. This time-honoured approach is problematic for at least two reasons. First, conventional significance and hypothesis tests evaluate the null hypothesis that there is exactly no effect of an intervention. But the null hypothesis is usually implausible: it is usually inconceivable that the intervention could have no effect whatsoever. Even interventions that we consider to be ineffective do not have exactly no effect – they have very small effects that are not of any clinical importance. So significance tests and hypothesis tests test a hypothesis that cannot be true. The second problem with significance and hypothesis testing is that very few researchers know how to interpret them (Nickerson, Reference Nickerson2000). Few researchers understand that p values are probabilities which are contingent on the null hypothesis being true. And even the best statisticians struggle to articulate why we should be interested in a probability that is contingent on the null hypothesis being true.

Estimate the Size of the Effect of the Intervention

Instead of focusing on p values, focus on the point estimate (the statistic you are using to estimate the effect of the intervention, such as the between-group differences in, or ratios of, outcomes) (Bland, Reference Bland2009; Gardner & Altman, Reference Gardner and Altman1986; Goodman, Reference Goodman1999; Greenland, Reference Greenland2011; Herbert, Reference Herbert2000; Matthews & Altman, Reference Matthews and Altman1996; Montori et al., Reference Montori, Jaeschke, Schünemann, Bhandari, Brozek, Devereaux and Guyatt2004; Sim & Reid, Reference Sim and Reid1999). Ask yourself if the estimated effect of the intervention is big enough to make the intervention worth its costs, risks and inconveniences. That is a clinical decision, not a statistical one.

Consider How Much Uncertainty There is in Your Estimate of the Effect of the Intervention

Don't just focus on the estimated effect of the intervention. Give careful consideration to the amount of uncertainty associated with the point estimate. That uncertainty comes from two sources. One is random error (sometimes called sampling error). Uncertainty caused by sampling error can be quantified with confidence intervals. The other source of uncertainty arises from the potential for bias, such as the potential bias inherent in self-reporting outcomes or the bias caused by incomplete follow-up. Uncertainties due to bias are harder to quantify than uncertainties due to sampling error but they are just as important. In the end you need to decide if, given the uncertainties associated with the estimated effect of intervention, you can confidently say that the intervention did or did not have a worthwhile effect.

Adhere to the CONSORT Guidelines

The CONSORT guidelines provide a detailed checklist that you can use when writing a trial report (Moher et al., Reference Moher, Hopewell, Schulz, Montori, Gøtzsche, Devereaux and Altman2012). Follow them closely.

Provide a Detailed Description of the Intervention

If your trial is to be useful, readers of the trial report must understand exactly how the intervention was administered. It can be difficult to convey exactly how a complex intervention was administered. Use the TIDieR guidelines to ensure you have provided a complete description of the intervention (see http://www.equator-network.org/).

Make it Clear which Analyses were Pre-Specified and which were not

Sometimes the data suggest interesting analyses that you didn't think of beforehand and didn't write into your statistical analysis plan. Feel free to conduct data-driven or last minute inspiration-driven analyses but, when you do, make it clear in the trial report that the data were not pre-specified. Readers should be more sceptical of these analyses than of analyses that were pre-specified in the statistical analysis plan.

Don't Spin Your Findings

Report your data as objectively as you can. Resist the temptation to talk the findings up and make them sound more significant than they are. Spin has no place in science (Boutron et al., Reference Boutron, Altman, Hopewell, Vera-Badillo, Tannock and Ravaud2014; Dwan, Gamble, Williamson, Kirkham, & Reporting Bias Group, Reference Dwan, Gamble, Williamson and Kirkham2013). It might give you passing fame but it will not earn you lasting respect and it will do nothing to advance the care of people with brain impairments (Greenland, Reference Greenland2011; Harvey, Reference Harvey2015; Tugwell & Knottnerus, Reference Tugwell and Knottnerus2016).

Interpret the Size of the Effect for Readers

The best randomised trials provide precise, unbiased estimates of the size of treatment effects. Readers can use that information to inform decisions about whether or not, or when, to use an intervention in clinical practice. Help readers by focusing on the estimated size of the effect and the amount of uncertainty in that estimate. If you can, tell readers whether you think the effect is big and worthwhile, or small and worthless, or somewhere in-between, and let the reader know if you are confident or uncertain about it.

Consider Making Your Data and Analysis Code Publicly Available

Science works best when research methods are open to scrutiny. You can help other scientists scrutinise your trial by making your data and code publicly available on a repository. Of course it is critical to maintain anonymity of participants so the data must be meticulously de-identified.