Session 2.1

Target trials

Louisa Smith

Recap

We saw that we could avoid bias from immortal time due to selection and to misclassification if we

  • define people as unexposed or unexposed at a specific point in time
  • restrict to those who we are defining as exposed or unexposed at that time

We will refer to this as “aligning time zero” and this is one of the main benefits of the target trial approach that we will discuss

But there was still a little bias left in our design (n = 100,000)

These risk ratios should be 1

week_comparison exp_0 exp_1 risk_difference risk_ratio
6 0.235 0.208 -0.027 0.887
7 0.208 0.190 -0.018 0.913
8 0.184 0.171 -0.013 0.929
9 0.160 0.160 -0.001 0.996
10 0.137 0.131 -0.006 0.955
11 0.116 0.117 0.001 1.007
12 0.096 0.083 -0.013 0.864
13 0.082 0.080 -0.002 0.979
14 0.070 0.059 -0.011 0.847
15 0.058 0.055 -0.003 0.941
16 0.047 0.034 -0.013 0.719
17 0.035 0.025 -0.010 0.708
18 0.023 0.011 -0.012 0.485
19 0.012 0.003 -0.009 0.216

Why is there still bias?

We made our comparison groups on the basis of weeks.

But note that we defined:

dat <- dat |> 
    mutate(...,
           week_exposed = floor(time_exposed),
           ...)

That is, we rounded down the time of exposure to the nearest week.

Why is there still bias

That means even though we are labeling someone exposed or unexposed at the beginning of the week, we are including some people who were exposed later in that week

  • Just like our original problem: those people by defintion survive longer than those who were unexposed at the start of the week (even if it’s less than a week!)
  • We don’t actually know who is exposed until the end of the week, so we technically shouldn’t be defining exposure until we know
  • It’s not causing a huge amount of bias, but it’s there!

Day-by-day comparisons?

Does this mean we need to make comparisons day-by-day? Hour-by-hour? Minute-by-minute?

  • Not by hour or minute, luckily! We can only go as granular as our data – if people are only defined as exposed or unexposed, and only have an event on the day level, we can’t (and don’t need to) go finer than that
    • If we only had data at the week level, we would consider people exposed or unexposed for the whole week, and events wouldn’t be recorded until the next week

Day-by-day comparisons?

But we have daily data!

  • If we wanted to ask a question about whether a first-trimester exposure causes an outcome, will we be unable to do this because we need to ask whether an exposure at xx day causes an outcome?

Luckily, no!

Grace periods

What we really need to do is acknowledge that some people are taking a few days to be exposed after the week starts

  • Until then, we don’t know if they will be exposed or unexposed that week
  • They should actually be considered both exposed and unexposed until we know for sure

We can understand why we need this “grace period”, and what to do about it, by thinking about how a randomized controlled trial works

  • This motivates the target trial emulation approach

Target trial emulation

A framework for designing observational studies that

  • makes the counterfactual contrasts explicit
  • aligns the “time zero” to avoid immortal time bias
  • clarifies assumptions about target population

First we need to think about the design and specification of randomized controlled trials

Randomized controlled trials

A randomized controlled trial for depression

The research question boils down to: Does an activity program or an antidepressant work better against depression?

DAG for simple, perfect randomized trial

  • If treatment is randomized, there are no arrows into it
  • Even though there are other causes of the outcome, we don’t need to include them
    • Recall that a causal DAG must include all “common causes”

Depression treatment trial

  • 20mg of anti-depressant to be taken daily can be raised to 40mg/day at week 3 or 6
  • The activity program takes 8 weekly sessions
    • Do you think everyone will complete all 8 weeks of the activity program?

DAG for more realistic randomized trial

Intention-to-treat effect

\[\E[Y^{z = 1}] - \E[Y^{z = 0}]\]

What is the effect of being randomized to one treatment vs. another?

  • When is this useful? When is it less useful?

Per-protocol effect

\[\E[Y^{z = 1, a = 1}] - \E[Y^{z = 0, a = 0}]\]

What is the effect of actually taking the treatment you were assigned to?

  • When is this the same as the ITT effect?

Per-protocol effect for a sustained treatment

\[\E[Y^{z = 1, a_1 = 1, a_2 = 1, ..., a_8 = 1}] - \E[Y^{z = 0, a_1 = 0, a_2 = 0, ..., a_8 = 0}]\]

What is the effect of taking the assigned treatment for all 8 weeks of the intervention?

  • When do we care about this in experimental studies? In observational studies?

When do we have a time-varying (sustained) treatment (strategy/regimen)?

Easier question: when do we not?

  • One-time event
    • surgery, vaccine (sometimes), infection, genetics
  • We really only care about initiation
    • prescribing a new drug
    • real-world effectiveness

Your causal questions: are they time-varying?

DAG for time-varying depression treatment (over just 2 weeks)

DAG for time-varying treatment, more generally

DAG for time-varying treatment, expanded…

And this is with only one confounder, over 4 points in time…

How to make DAGs easier to work with when you have a time-varying treatment

  • Two treatment nodes: initial treatment and continued treatment
    • Often you can assume the same pattern of confounding
  • Group confounders into baseline confounders and post-baseline confounders
    • Post-baseline confounders are any that could plausibly change after/ be affected by the initiation of treatment
  • For survival outcomes, you actually have multiple \(Y\)s as well…
    • You can often also think of this as just two
    • In order to continue treatment, you need to have survived
    • (We will come back to this idea)

In other words, this DAG is sufficient for our purposes!

To estimate the per-protocol effect of depression treatment (i.e., activity program for 8 weeks vs. anti-depressant):

  • We need to adjust for transportation
  • Do we need to adjust for change in symptoms?
    • What if there’s a common cause of symptoms and depression severity (e.g., serotonin levels)?

Time-varying confounding

When variables:

  • are affected by previous treatment
  • confound future treatment

We somehow need to both adjust and not adjust for them

These are called time-varying confounders, and they require special methods (that we will get to!)

Wait, we’re still in a randomized trial!

Randomized trials need causal inference methods for observational data in order to estimate anything but the intention-to-treat effect!

(Besides the fact that you can estimate an unbiased ITT effect assuming blinding, good randomization, etc.)

RCTs offer one huge benefit compared to typical observational studies:

  • They automatically align time zero

Consider an observational study

We use electronic health records to compare people with moderate depression:

  • those who completed 8 weeks of a depression activity program
  • those who were prescribed anti-depressants

and calculate risk of depression-related hospitalization (or some kind of severity symptom score if we have that data)

  • We’re back to our old immortal time problem!

Solution: design your study like a randomized trial and start counting time when participants are “randomized”

  • People are “randomized” as soon as they meet eligibility criteria
  • In some designs, people can be “randomized” to “placebo” multiple times (in our previous week-specific comparisons, many people served in the comparison group many times)
  • People might be randomized to a treatment but allowed a grace period to actually start it (in our week-specific comparison, they could be treated any time that week, though we haven’t accounted for that yet)

Steps

  1. Specify the protocol of a target trial that answers your causal question – this doesn’t need to be ethical or practically feasible, but you should not make compromises for the sake of your observational data
    • (You can base it on the observational data you know you have in some respects, e.g., your population of interest)
  2. Emulate the target trial using your observational data
    • This may require compromises, but you should be explicit about them
    • If the compromises are too severe, you may need to reconsider your causal question/redefine your target trial

Components of a target trial

  • Eligibility criteria

  • Treatment strategies

  • Assignment procedures

  • Follow-up

  • Outcome(s)

  • Causal contrast(s)

  • Assumptions for emulation

  • Statistical analysis plan

Recently published reporting guidelines

Cashin et al. (2025)

Item 3: Summarize the causal question.

Item 6: Specify the components of the target trial protocol that would answer the causal question.

Item 7: Describe how the components of the target trial protocol were emulated with the observational data, including how all variables were measured or ascertained.

Component Target Trial Specification (Item 6) Target Trial Emulation (Item 7)
Eligibility Criteria Describe the eligibility criteria. Describe how the eligibility criteria were operationalized with the data.
Treatment Strategies Describe the treatment strategies that would be compared. Describe how the treatment strategies were operationalized with the data.
Assignment Procedures Report that eligible individuals would be randomly assigned to treatment strategies and may be aware of their treatment allocation. Describe how assignment to treatment strategies was operationalized with the data.
Follow-up Clarify that follow-up would start at time of assignment to the treatment strategies. Specify when follow-up would end. Clarify that follow-up starts at the time individuals were assigned to the treatment strategies. Describe how the end of follow-up was operationalized with the data.
Outcomes Describe the outcomes. Describe how the outcomes were operationalized with the data.
Causal Contrasts Describe the causal contrasts of interest, including effect measures. Describe how the causal contrasts were operationalized with the data, including effect measures.

Pharmaceutical example from Hernán and Robins (2016)

Component Target Trial Specification
Causal question What is the effect of postmenopausal hormone therapy on breast cancer.
Eligibility criteria Postmenopausal women within 5 years of menopause and with no history of cancer and no use of hormone therapy in the past 2 years
Treatment strategies

1. Refrain from taking hormone therapy during follow-up

2. Initiate estrogen plus progestin hormone therapy at baseline and remain on it during the follow-up, unless diagnosed with deep vein thrombosis, etc.
Assignment procedures Participants will be randomly assigned to either strategy at baseline and will be aware of the strategy to which they have been assigned
Follow-up Patients are followed from enrollment (time zero) until breast cancer diagnosis, loss to follow-up, or administrative end of follow-up (5 years from baseline)
Outcome Breast cancer diagnosed by an oncologist
Contrast Intention-to-treat effect, per-protocol effect

Non-pharmaceutical example (Smith et al. (2022))

Components Target trial
Causal question What is the effect of COVID-19 infection on preterm delivery?
Eligibility criteria

1. Pregnant individuals with gestational age 12-36 weeks.

2. No known previous SARS-CoV-2 infection

3. No previous vaccination for COVID-19
Treatment strategies

1. Symptomatic COVID-19 within a week after enrollment.

2. No SARS-CoV-2 infection for the rest of the pregnancy.
Assignment procedures Randomization at enrollment, stratified by gestational age (in weeks).
Follow-up Patients are followed from the time of COVID-19 testing or enrollment (time zero) until delivery, loss to follow-up, or administrative end of follow-up.
Outcome Preterm delivery, defined as delivery before 37 completed weeks of gestation.
Causal contrast Intention-to-treat effect on the risk ratio and risk difference scales.

Notes on these components and things to think about in emulation (hopefully not compromises to the integrity of the target trial)

Components Target trial
Eligibility criteria
  • Based only on pre-baseline characteristics
  • Generally requires pre-baseline observation window
Treatment strategies
  • Can’t assign actual placebo or blinding (can assign no treatment if realistic)
  • Some people must have “adhered” to the treatment strategy
Assignment procedures
  • Randomization (within levels of confounders) is always an assumption
  • Assignment “happens” as soon as someone meets eligibility criteria
Follow-up
  • Monitoring for the outcome throughout follow-up (e.g., regular mammograms) may need to be part of the treatment strategy
Outcome
  • Outcome ascertainment can’t be blinded
Causal contrast
  • Intention-to-treat effect makes sense when “most” of the treatment happens immediately upon randomization
  • Per-protocol useful when you don’t know right away who starts what treatment

Choose one

Chiu et al. (2024)

Yland et al. (2022)

Caniglia et al. (2023)

Caniglia et al. (2018)

Wong et al. (2024)

Grandi et al. (2024)

Or any other of your choice!

Your target trial

Components Target trial
Eligibility criteria
Treatment strategies
Assignment procedures
Follow-up
Outcome
Causal contrast

References

Caniglia, Ellen C., Rebecca Zash, Christina Fennell, Modiegi Diseko, Gloria Mayondi, Jonathan Heintz, Mompati Mmalane, et al. 2023. “Emulating Target Trials to Avoid Immortal Time Bias – an Application to Antibiotic Initiation and Preterm Delivery.” Epidemiology 34 (3): 430. https://doi.org/10.1097/EDE.0000000000001601.
Caniglia, Ellen C., Rebecca Zash, Denise L. Jacobson, Modiegi Diseko, Gloria Mayondi, Shahin Lockman, Jennifer Y. Chen, et al. 2018. “Emulating a Target Trial of Antiretroviral Therapy Regimens Started Before Conception and Risk of Adverse Birth Outcomes.” AIDS 32 (1): 113–20. https://doi.org/10.1097/qad.0000000000001673.
Cashin, Aidan G., Harrison J. Hansford, Miguel A. Hernán, Sonja A. Swanson, Hopin Lee, Matthew D. Jones, Issa J. Dahabreh, et al. 2025. “Transparent Reporting of Observational Studies Emulating a Target Trial: The TARGET Statement.” BMJ 390 (September): e087179. https://doi.org/10.1136/bmj-2025-087179.
Chiu, Yu-Han, Krista F. Huybrechts, Elisabetta Patorno, Jennifer J. Yland, Carolyn E. Cesta, Brian T. Bateman, Ellen W. Seely, Miguel A. Hernán, and Sonia Hernández-Díaz. 2024. “Metformin Use in the First Trimester of Pregnancy and Risk for Nonlive Birth and Congenital Malformations: Emulating a Target Trial Using Real-World Data.” Annals of Internal Medicine 177 (7): 862–70. https://doi.org/10.7326/M23-2038.
Grandi, Sonia M., Ya-Hui Yu, Pauline Reynier, Robert W. Platt, Oriana H. Y. Yu, and Kristian B. Filion. 2024. “Levothyroxine Initiation and the Risk of Pregnancy Loss Among Pregnant Women with Subclinical Hypothyroidism: An Observational Study Emulating a Target Trial.” Paediatric and Perinatal Epidemiology 38 (6): 470–81. https://doi.org/10.1111/ppe.13015.
Hernán, Miguel A., and James M. Robins. 2016. “Using Big Data to Emulate a Target Trial When a Randomized Trial Is Not Available.” American Journal of Epidemiology 183 (8): 758–64. https://doi.org/10.1093/aje/kwv254.
Smith, Louisa H., Camille Y. Dollinger, Tyler J. VanderWeele, Diego F. Wyszynski, and Sonia Hernández-Díaz. 2022. “Timing and Severity of COVID-19 During Pregnancy and Risk of Preterm Birth in the International Registry of Coronavirus Exposure in Pregnancy.” BMC Pregnancy and Childbirth 22 (1): 775. https://doi.org/10.1186/s12884-022-05101-3.
Wong, Carlos K. H., Kristy T. K. Lau, Matthew S. H. Chung, Ivan C. H. Au, Ka Wang Cheung, Eric H. Y. Lau, Yasmin Daoud, Benjamin J. Cowling, and Gabriel M. Leung. 2024. “Nirmatrelvir/Ritonavir Use in Pregnant Women with SARS-CoV-2 Omicron Infection: A Target Trial Emulation.” Nature Medicine 30 (1): 112–16. https://doi.org/10.1038/s41591-023-02674-0.
Yland, Jennifer J, Yu-Han Chiu, Paolo Rinaudo, John Hsu, Miguel A Hernán, and Sonia Hernández-Díaz. 2022. “Emulating a Target Trial of the Comparative Effectiveness of Clomiphene Citrate and Letrozole for Ovulation Induction.” Human Reproduction 37 (4): 793–805. https://doi.org/10.1093/humrep/deac005.