How to Read a Results Section and Spot What You Are Being Sold

You are presenting on Thursday, you have forty minutes between patients, and eight pages with six tables. The difficulty in journal club is rarely that you cannot follow a Cox model. It is that the paper is written to walk you toward the conclusion its authors want, and the order in which you read it either helps you or hands you over. There is a seven-stop route that needs no more statistics than you already have and catches most of what gets smuggled through. It starts somewhere other than the first table.

Stop one: the design, which decides what verbs are allowed

Before you look at a single number, find the sentence in the Methods that says what kind of study this is. It is usually the first line and it usually reads like paperwork: multicentre cross-sectional survey, retrospective cohort, parallel-group randomized trial, case series. That sentence is the ceiling for everything that follows. A cross-sectional design can show you that two things travel together and very little else. It cannot tell you which came first, and it certainly cannot tell you what would happen if you intervened.

Translate it into verbs, because that is how the mismatch shows up. Cross-sectional buys you was associated with and was more frequent among. A prospective cohort adds preceded and, carefully, predicted. Only random allocation buys reduced, improved and caused without a further argument. When the Discussion of a cross-sectional study says the program improves adherence, you already have the first finding of the session, and you found it without reading a table.

The second design question is what the intervention was compared against. A single-arm before-and-after study measures the intervention plus the passage of time, plus regression to the mean, plus whatever the patient expected to happen, and all three push the same way. The comparator moves the effect size as much as the intervention does: the same program looks spectacular against a waiting list and modest against usual care. When two trials of the same thing report very different effects, check the comparators before reaching for subtler explanations.

The third question is answered by the eligibility table, and it is the one that matters most at the bedside: do these patients look like yours? A heart failure trial that excludes anyone over 75, anyone with reduced renal function and anyone on more than five medicines has excluded half your ward. The result can be flawless and apply to almost nobody you will see on Monday. That gap between the sample and your population is a limitation rather than an error, but it has to be said out loud in the session, and it almost never is. More traps of this shape are collected in the common errors in interpreting statistical results.

Stop two: the N in the abstract is not the N that was analyzed

The abstract says 240 participants. The flow diagram says 240 were randomized, 186 completed follow-up and 186 were analyzed. Those three numbers rarely match, and the distance between them is information, not administrative noise. In a trial, CONSORT requires the flow diagram and most journals ask for it, so it sits in the first figure. In an observational study, the STROBE guidance recommends the equivalent, and you sometimes have to rebuild it by hand from the text.

What you look at is not only how much was lost but whether it was lost evenly. With 120 per arm, 32 dropouts in the intervention and 22 in the control is a different study from 27 and 27, even though the totals are close. If more people leave the intervention arm, and they leave because the program was demanding or because they had adverse effects, the ones left behind are the ones who tolerated it best, and what the trial measures is the effect among survivors of the protocol. The question to ask out loud is plain: do the people who left look like the people who stayed?

The five-and-twenty rule taught in clinical epidemiology, under 5% is unlikely to change the conclusions and over 20% deserves scrutiny, is a teaching convention rather than a threshold with any theory behind it. It tells you when to look harder, not when to bin a study. What is decisive is what the team did with the missing people. Analyzing complete cases only assumes the people who are missing went missing by pure chance, and that is a strong assumption almost nobody defends explicitly. What a paper owes you here is set out in how to report missing data in APA 7, and it is exactly what you are hunting for: how many, why, and what was done about them.

Two thirty-second checks close this stop. First, compare the n in each table footnote with the flow diagram. Denominators that drift between tables without explanation are usually variables with missing data that nobody declared. Second, check whether the primary analysis is intention-to-treat, everyone randomized in the arm they were allocated to, or per-protocol, only those who completed as planned. A trial whose headline comes from the per-protocol analysis is showing you its most flattering number, and the intention-to-treat estimate, usually the conservative one, is further down and in smaller type.

Stop three: what the primary outcome was, and how many there really are

A trial has one primary outcome. One. If the protocol declares two co-primary outcomes, it also has to say what it does with the alpha: split it between them, or require both to clear the bar before the hypothesis counts as supported. That gets checked too. It is defined before a single data point is collected and it is written into a public registry with its instrument and its measurement point: ClinicalTrials.gov, the ISRCTN, the Australian New Zealand registry. Checking takes two minutes, because the registration number is at the end of the paper and the record is public. For systematic reviews the equivalent is PROSPERO, and for everything else a preregistered protocol; why that changes the weight of what you can conclude is in preregistration on OSF.

What you are looking for is outcome switching, and it comes in three shapes. First: the abstract features an outcome that is not the registered one. Second: the registered outcome appears with no numbers at all, disposed of with no significant differences were observed. Third, and hardest to see, the measurement window moves, and what was going to be assessed at twelve months is reported at six, which is where the effect still held. The COMPare project compared registry entries against publications in leading journals and wrote to the editors when they diverged; the practical lesson for you is that the discrepancy is neither rare nor confined to weak journals.

Count the tests. A trial with one primary outcome and fourteen secondary ones that reports a single significant result at p = .04 has not found much: if those fourteen were independent and none of them had a real effect, the chance that at least one fell below .05 by luck alone would be around 51%. They are not independent and the exact figure differs, but the order of magnitude holds, and it explains why an isolated secondary finding is treated as a hypothesis for the next study rather than as a result. The same applies to subgroups: the effect was significant in women over 65 means something only if the interaction test was prespecified and appears in the table.

A small tell about how carefully a paper was reviewed: p values in Table 1 of a randomized trial. Testing baseline differences makes no sense, because there is no hypothesis to test; you already know with certainty that any imbalance came from chance, which is what randomization is for. What matters is the size of the imbalance and whether it lands on a strong prognostic variable, and that is judged by magnitude, not by p. CONSORT has discouraged it for years and it keeps appearing in print.

Stop four: the effect and its interval, put on the patient's scale

This is where most journal clubs come apart, not from a shortage of statistics but from an excess of p values. The p tells you how unlikely data like these, or more extreme, would be if there were no effect at all in the population. It does not tell you how much the patient changes. The two clinical questions are different: how much, and how precisely. The first is answered by the effect size, the second by the width of the confidence interval, which is not read the way it is usually read.

Take a binary outcome, say unplanned readmission within 30 days. In the control arm 96 of 800 are readmitted (12.0%) and in the intervention arm 67 of 800 (8.4%): RR = 0.70, 95% CI [0.52, 0.94], chi²(1, N = 1600) = 5.74, p = .017. The abstract will say the intervention cut risk by 30%, which is true and is the relative reduction. In absolute terms it is 3.6 percentage points, and the number that travels to the ward round is the number needed to treat: 28 patients treated to prevent one readmission. Its interval runs from 15 to 150, and that tail at 150 almost never makes it into the abstract.

Now a continuous outcome. A rehabilitation program improves a 0 to 100 disease-specific quality-of-life score by a mean difference of 4.1 points, 95% CI [0.7, 7.5], p = .018. It is significant. Set the minimal clinically important difference beside it, a figure you have to look up because it belongs to the instrument and not to the length of the scale; published values for measures of that kind tend to sit around 10 points and move with the population and the method used to estimate them, and against that benchmark the whole interval falls below it. The study has shown at once that the effect is not zero and that it is too small for the patient to notice. Both sentences are true and only one reaches the abstract.

When a paper reports the test but no effect size, you can rebuild it. From the t and its degrees of freedom, or from the means and standard deviations in the table, you get a d that is comparable with other studies: the effect size from text calculator does it from the sentence pasted as printed. And when what the paper gives you is an odds ratio from a logistic regression, convert it before you repeat it out loud, because with common outcomes it overstates the relative risk and the gap is not cosmetic; that is what the odds ratio calculator is for.

Stop five: the jump from the table to the Discussion

This is the highest-yield step and the one almost nobody takes. Read the first paragraph of the Discussion, underline every claim, and go back into Results to find the number that carries it. Not the argument: the number, with its table and its row. Anything you cannot anchor in a table is not a finding of the study, it is the authors' opinion wearing the clothes of a finding, which is fair enough when it is labeled and a problem when it is not.

The jumps repeat so reliably that they have names. The primary outcome failed and the Discussion talks about a trend. A trend toward benefit, approached significance, promising results, with a non-significant primary outcome sitting behind them. A secondary outcome is promoted to headline. The abstract and the Discussion revolve around an outcome that was never primary, and the primary one appears once, in the past tense and without figures. A surrogate outcome is sold as a clinical one. The drug lowers HbA1c or LDL cholesterol, and the Discussion talks about cardiovascular events the trial never measured. The composite is driven by its softest component. A composite of mortality, myocardial infarction and hospitalization comes out significant, and once you open it the entire difference sits in hospitalizations, the component most sensitive to how a given health system is organized.

This has a name in the methodological literature, spin, and it has been measured. The landmark study reviewed published trials whose primary outcome was not significant and found spin in a high proportion of them, concentrated above all in the abstract, which is the only part most people read (Boutron et al., 2010). Being common does not make it harmless: the abstract's conclusion is what ends up in the session, in the guideline and in the clinic.

Two last filters and you are done. The first is how magnitude is framed: if benefit is reported in relative terms, 30% fewer events, and harm in absolute terms, 1.2% adverse effects, the comparison is rigged even though both numbers are individually correct. The second is how far the sample is stretched: these findings support national rollout of the program needs a good deal more than a trial in two university hospitals with selected patients. In the session that sentence is answered with a question rather than a debate: which table is that in?

The whole route, in the order you actually do it

Ten well-spent minutes, in this sequence. One, the design. What kind of study it is and which verbs it licenses. Two, who got in. Eligibility criteria and how close they are to your patients. Three, the flow diagram. Randomized, completed, analyzed, and whether the losses were symmetrical. Four, the registry. What the prespecified primary outcome was and whether the paper is talking about it. Five, the effect. Magnitude with its confidence interval, translated onto the patient's scale: number needed to treat, points on the instrument, absolute difference. Six, the count. How many tests were run in total and how many are being showcased. Seven, the jump. Every Discussion sentence against its number in Results.

In the session itself, keep apart three things that always get mixed. A fatal flaw voids the conclusion: the primary analysis is per-protocol in a trial with 25% asymmetric dropout, or the outcome being reported is not the one that was registered. A limitation bounds how far the result travels without knocking it down: the sample excludes over-75s, follow-up stops at three months. A preference is what you would have done differently and it changes nothing: a mixed model instead of the ANOVA, a different but equally validated scale. Whoever treats all three as the same category becomes the person who sinks every paper and stops getting invited.

If nobody in the room does methods for a living, three questions need no statistics and will organize the whole hour. What was the registered primary outcome, and is it the one we are discussing? How many of the people who entered ended up in the analysis? How much does this change on the patient's scale, in absolute rather than relative terms? Those three catch more than you would expect, and none of them forces you to defend a technicality in front of the room.

Frequently asked questions

Where do I start reading a paper if I am short on time?

With the design, not the abstract. One line in the Methods tells you what kind of study this is, and that alone caps what the Discussion is allowed to claim. Then the flow diagram, to see how many of the people who entered reached the analysis, then the registration number to find the primary outcome. Numbers come fourth. Read in that order and you arrive at the tables knowing what to look for, which stops the abstract deciding for you.

How much loss to follow-up is too much?

There is no threshold with theory behind it. The convention taught in clinical epidemiology says under 5% is unlikely to change the conclusions and over 20% deserves a close look, but it is a classroom rule, not a law. Two other things matter more: whether the losses were symmetrical across arms, and why people left. A 15% loss falling entirely in the intervention arm because of adverse effects does more damage than 25% spread evenly across people who moved house.

What is the difference between intention-to-treat and per-protocol analysis?

Intention-to-treat analyses everyone randomized in the arm they were allocated to, whether or not they complied. Per-protocol analyses only those who completed the intervention as planned. The second usually yields a larger effect, because excluding those who dropped out breaks randomization and leaves the best responders in. In a trial of therapeutic efficacy the primary analysis should be intention-to-treat, with per-protocol demoted to a sensitivity analysis at most.

How do I know whether a result is clinically relevant and not just significant?

Compare the effect size and its interval against a clinical benchmark, not against the p value. For binary outcomes, convert to an absolute difference and a number needed to treat: a 30% relative reduction can be 3.6 percentage points and an NNT of 28. For scales, put the instrument's minimal clinically important difference alongside. If the entire interval sits below that difference, the study has shown both that the effect exists and that it is too small to be noticed.

How do I check whether the primary outcome was switched?

Find the registration number, usually at the end of the paper or in the funding note, and open the record on ClinicalTrials.gov, the ISRCTN or the relevant national registry. It lists the primary outcome with its instrument and its timing. Compare that against what the abstract features. If they diverge, if the registered outcome appears without figures, or if the record was edited after recruitment began, you have the strongest point in your presentation.

What do I say in journal club if I am not a statistician?

Three questions, none of which needs method. What was the registered primary outcome and is it the one we are discussing. How many of the people who entered ended up in the analysis. How much the result changes on the patient's scale, in absolute rather than relative terms. They cannot be answered with a technicality, and they force the room back to the table, which is what makes a session worth an hour.

Reading a Results section well is not about distrusting everything. It is about knowing what to look at first, and accepting that a study can be well conducted, well published and still not say what its abstract says it says. Start at the design and finish at the jump into the Discussion; in between, the N that was actually analyzed, the outcome that was actually registered, and the effect put on the patient's scale. That is enough to walk into Thursday's session with something to contribute, even if you have never fitted a model in your life.