What You Need to Know When Estimating Impact Functions with Panel Data for Demographic Research


What You Need to Know When Estimating Impact Functions 
with Panel Data for Demographic Research*

Volker Ludwig, Josef Brüderl

Abstract: The estimation of impact functions – that is the time-varying causal effect 
of a dichotomous treatment (e.g., marriage, divorce, parenthood) on outcomes (e.g., 
earnings, well-being, health) – has become a standard procedure in demographic 
applications. The basic methodology of estimating impact functions with panel data 
and fi xed-effects regressions is now widely known. However, many researchers 
may not be fully aware of the methodological subtleties of the approach, which may 
lead to biased estimates of the impact function. In this paper, we highlight potential 
pitfalls and provide guidance on how to avoid these in practice. We demonstrate 
these issues with exemplary analyses, using data from the German Family Panel 
(pairfam) study and estimating the effect of motherhood on life satisfaction.

Keywords: Impact functions · Fixed effects regression · Negative weighting bias · 
Motherhood · pairfam · Panel data analysis

1 Introduction

In demography, many research questions examine the total causal effect of an event 
(e.g., marriage, divorce, parenthood) on certain outcomes (e.g., earnings, well-
being, health). Allison (1994) described this approach as asking for “the effects of 
events”. Several papers in this Special Issue provide examples for such research 
questions and discuss research designs for the identifi cation of such treatment 
effects. Experiments are in most cases not viable for analysing the effects of events 
in the social sciences, because manipulating them is unethical or not practically 
feasible. Therefore, cross-sectional survey data have traditionally been used as 
an alternative. With cross-sectional comparisons, the unbiased identifi cation of a 

Comparative Population Studies
Vol. 46 (2021): 453-486 (Date of release: 24.11.2021)

Federal Institute for Population Research 2021 URL: www.comparativepopulationstudies.de
      DOI: https://doi.org/10.12765/CPoS-2021-16
      URN: urn:nbn:de:bib-cpos-2021-16en3
    

* This article belongs to a special issue on “Identifi cation of causal mechanisms in demographic 
research: The contribution of panel data”.



•    Volker Ludwig, Josef Brüderl454

treatment effect hinges on a very strong assumption: all time-constant and time-
varying variables that affect both the treatment and the outcome (confounders) 
must be controlled for in the analysis. If some confounders are unobserved and 
cannot be controlled for, causal inferences will be biased. 

Another research design for identifying the effect of events uses panel data. 
Panel data offer the possibility of implementing within-person designs for identifying 
causal effects. The main advantage of within-person designs is that time-constant 
confounders will not bias the estimation of the treatment effect. Thus, the unbiased 
identifi cation of a treatment effect hinges on the much weaker assumption (compared 
to cross-sectional designs) that all time-varying confounders are controlled for in 
the analysis. In most cases, demographers implement a within-person design by 
using fi xed-effects (FE) regressions. In fact, all papers in this Special Issue refer to 
this method and its advantages for causal analysis. Therefore, it is no surprise that 
with the advent of more and more panel data (see e.g., the most recent addition of 
“The Comparative Panel File, CPF”, Turek et al. 2021), the estimation of treatment 
effects by using FE regression is a growing business in demographic research. 

With long-running panel data, as they are meanwhile widely available, one 
observes many treated individuals for more than one time period after treatment. 
Given this set-up, it is even possible to estimate time-varying treatment effects, i.e., 
one can estimate the time-path of a causal effect. We term such a causal time-path 
“impact function”, a term we borrow from Andreß et al. (2013). Impact functions 
obviously provide more insight, since we learn more than when estimating a time-
constant treatment effect. Therefore, the recent demographic literature using FE 
methodology increasingly reports impact functions.1

The basic methodology of estimating impact functions with panel data and 
fi xed-effects regressions is now widely known. Yet it is our impression that many 
researchers are not fully aware of the methodological subtleties of the approach, 
which may lead to biased estimates of the impact function. In this paper, we 
highlight potential pitfalls and provide guidance on how to avoid these in practice. 
We demonstrate these issues with exemplary analyses, using data from the German 
Family Panel (pairfam) study and estimating the effect of motherhood on life 
satisfaction.

The paper proceeds as follows: In the fi rst section, we summarize the rationale for 
estimating impact functions. Section 2 provides the basic framework for estimating 

1 Another popular research question is to investigate “the effect of an event on (the transition rate 
of) another event”. Event history methods with time-varying covariates are useful in this case 
(see the contribution by Michaela Kreyenfeld to this Special Issue). One could even estimate an 
analog to an impact function by modeling an interaction between the coeffi cient of the time-
varying event variable and process time. For instance, one might be interested in the effect 
of the birth of a child on the divorce rate. If one would allow the effect of a birth to vary over 
marriage duration, this would be an event history analog to an impact function.

 It must be noted, however, that (standard) event history analysis does not implement a within-
person design. Therefore, estimates are unbiased only if both time-constant and time-varying 
confounders are controlled for. Only event history analysis with repeated events implements a 
within-person design (see Allison 2009).



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 455

impact functions. Section 3 provides an illustration using pairfam data and estimating 
the effect of the birth of a fi rst (biological) child on happiness. Section 4 discusses 
pitfalls and remedies when estimating impact functions. Finally, Section 5 offers a 
discussion of the negative weighting bias with staggered treatment events.

2 Why Do We Estimate Impact Functions?

The estimation of impact functions has become a standard practice in demography, 
as well as in the social sciences and economics more generally. In fact, when setting 
up studies using a panel design, we should always care about the impact function 
for both substantive and methodological reasons. 

Substantively, knowledge of the precise shape of the impact function is often 
important for theoretical reasons. In demographic research, for example, we would 
not only like to know to what extent childbirth raises well-being, but also whether this 
is a short-lived or a persistent – and perhaps even increasing – effect. Theoretically, 
the psychological adaptation/treadmill theory of happiness would lead us to expect 
a temporary effect that diminishes rapidly, a similar pattern as found for many other 
critical life events (e.g., Diener et al. 2006). Family economic models, however, 
would predict a permanent effect due to the benefi ts of household specialization 
(Stutzer/Frey 2006). This effect may even increase over time if specialization grows 
stronger after childbirth. The estimation of the impact function may thus help us 
discriminate between theories. 

Methodologically, in case of time-varying treatment effects, different statistical 
models will yield different results. In the case of time-constant treatment effects, 
FE and fi rst-differences (FD) regressions will provide the same results (without 
controls). This, however, is not true for time-varying treatment effects. As Laporte 
and Windmeijer (2005) show with time-varying treatment effects, FE and FD models 
produce estimates that differ tremendously. 

Furthermore, we need to address a potentially time-varying treatment effect, 
because assuming a time-constant effect may bias our causal inferences. Recent 
papers demonstrated a “negative weighting bias” of the constant impact function 
(Borusyak/Jaravel 2017; de Chaisemartin/D’Holtfoeuille 2020; Goodman-Bacon 
2018). This bias appears generally in the situation of staggered treatments (when 
the treatment appears at different time points) simply due to the mechanics of the 
FE estimator: FE estimation of a time-constant impact induces a bias due to down-
weighting of treated observations well after treatment (for details, see Section 5). 
Since demographic panel data typically use staggered treatment designs, where 
treatment assignment occurs at different points in time, the issue is clearly of 
relevance. The problem can be solved, however, by simply modelling a fl exible 
impact function (such as a dummy impact function, see below).



•    Volker Ludwig, Josef Brüderl456

3 The Basic Framework for Estimating Impact Functions

Although impact functions could in principle be estimated by any basic statistical 
model for panel data (generally, clustered data), including pooled OLS and random 
effects regression, we focus in this paper on fi xed effects modelling. The power 
of the FE approach for modelling impact functions stems from its property of 
unbiasedness under weak assumptions compared to other estimators. Although 
the crucial condition for the consistency of FE is strict exogeneity, the estimator is 
consistent and unbiased even if stable unit-specifi c characteristics are related to 
the treatment variable or other covariates. The FE model therefore allows, fi rst, for 
the estimation of a causal treatment effect even when treatment assignment is not 
random, but rather the result of a conscious choice or otherwise systematic pattern 
(e.g., self-selection). Second, FE methodology helps with the age-period-cohort 
problem: It allows for the consistent estimation of age and period effects (while 
implicitly also controlling for cohort effects), which is crucial for the estimation of 
treatment effects with panel data, as we will argue below.  

A simple FE model for estimation of a time-constant treatment effect with panel 
data for i = 1, … , N persons observed at t = 1, … , T points in time would be:

where Yit is the outcome, Dit the treatment variable, Xit are confounders, and αi are 
unit (person) fi xed effects. ϵit denotes a time-varying error term that is assumed to 
be (strictly) exogeneous. Hence, for unbiasedness it must hold that E(ϵit│Dit,Xit,αi)=0. 
From a design-based perspective, the strict exogeneity condition implies that the 
parallel trends assumption must hold. Furthermore, perfect collinearity is ruled out. 
Even strong imperfect collinearity may cause serious problems for the estimation of 
time paths. More details on the FE model can be found in Brüderl and Ludwig (2015).

There are three primary ways to model an impact function. Above, we assumed 
that Dit is a binary treatment variable, and that treatment assignment is an absorbing 
state, that is, once a unit switches to the treated status, the treatment variable turns 
1 and subsequently does not return to 0. The treatment effect β in the model above 
thus is the single parameter that characterizes a step impact function: whenever 
a unit is treated, the model predicts an immediate and permanent change in the 
outcome (i.e., a time-constant impact). 

To estimate a time-varying impact function, one parameter is not suffi cient. 
Hence, we might add a further variable Kit to the model that contains the time passed 
since treatment assignment (technically this is an interaction variable between Dit 
and time since treatment). This would be the simplest way to specify a continuous 
impact function. The coeffi cient for Dit would tell us by how much the outcome 
changes immediately after treatment, and the coeffi cient for Kit indicates how 
much the outcome additionally changes with each time unit passing subsequently. 
Of course, continuous impact functions can be specifi ed with polynomials to 
approximate more complex time paths. Alternatively, linear splines may be fi t to 
model changes in the treatment effect in order to relax functional form assumptions. 

(1)



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 457

The most often used type of impact function, however, is the dummy impact 
function, where Dit is replaced by a set of dummy variables for Kit (e.g., a separate 
dummy for every month or year since treatment): 

where k = 0 is the fi rst observation after treatment, and K is the last one.2 (In the 
following, we denote  as the “k-year dummy”.) Obviously, this specifi cation allows 
us to fi t the time path of a treatment effect in a very fl exible way.

4 An illustration: The effect of the birth of a fi rst (biological) child on 
happiness

In an infl uential paper, Myrskylä and Margolis (2014) studied parental happiness 
trajectories before and after the birth of a child (using data from the SOEP and the 
BHPS). This paper became a model for applying impact function methodology to 
demographic research questions. Therefore, to illustrate the estimation of impact 
functions, we replicate the study of Myrskylä and Margolis (2014) with data from 
the German Family Panel (pairfam). Thus, our research question is: How does the 
event of the birth of a fi rst (biological) child impact the outcome “life satisfaction” 
(synonymously: “happiness”). We restrict our analysis to mothers. pairfam is 
particularly well-suited for the task at hand because it prospectively measures the 
birth of children and mothers’ life satisfaction.

The German Family Panel is a nationwide longitudinal study of initially more 
than 12,000 randomly sampled individuals from the birth cohorts 1971-73, 1981-
83, and 1991-93. pairfam started in 2008/09 with roughly one-hour face-to-face 
interviews. Respondents were approached annually in subsequent waves. For a 
detailed description of the study, see Huinink et al. (2011). Release 11.0 with Waves 
1-11 is used for this analysis, which covers the observation period 2008-19 (Brüderl 
et al. 2020). We use only the pairfam base sample and do not use the refreshment 
samples added to the survey continuously.

We construct the estimation sample according to the recommendations laid 
out in Section 5. Only never-treated females, i.e., those who never gave birth to 
a child before pairfam Wave 1 are included. We include only females with at least 
two observations in pairfam. For fi rst-time mothers, the observation window is 
censored with the second pregnancy/birth. After these exclusions, our estimation 
sample comprises 2,982 women, of whom 505 gave birth to a fi rst (biological) child. 

(2)

2 Starting the numbering with 0 may intuitively seem confusing. But it makes sense, because the 
fi rst time period after treatment might be approximately thought as the “period of treatment”, 
the second time period as “one period after treatment”, and so on. In addition, pre-treatment 
dummies can then be taken into account with -1, -2, and so on (see below).



•    Volker Ludwig, Josef Brüderl458

These women provide 19,996 person-years. They were observed in the age range 
of 14-48. Due to low number of cases, we recoded 14 to 15 years, and 48 to 47 
years. Thus, models include age dummies for ages 16 to 47 (15 being the reference 
category).

The outcome variable, life satisfaction, is measured by the question: “Now I 
would like to ask about your general satisfaction with life. All in all, how satisfi ed 
are you with your life at the moment?” Answers are recorded on an 11-point scale 
ranging from “very dissatisfi ed” (0) to “very satisfi ed” (10).

To estimate the total causal effect of a fi rst birth on happiness, we include 
treatment variables as explained above (child dummy, time since birth). We derive 
these from the generated variable “nkidsbio”, as it is provided by the pairfam team. 
(This has the implication that timing is not exact, since the exact birth date is not 
taken into account.) Time since birth starts at 0 (less than one year after birth) and 
reaches a maximum of 9 (nine years after birth). The maximum of 9 is reached if a 
woman is childless in the fi rst wave, gives birth before the second wave, and does 
not drop out of the survey. For reasons of parsimony, we group the time dummies 
in an upper category of 4+ years.

According to the rules of modern causal analysis (VanderWeele 2019) one 
must control for potential confounders to identify a total causal effect.3 Potential 
confounders are variables that are assumed to infl uence both the treatment and 
the outcome, fi rst birth and life satisfaction. The most important confounder in 
our context is age (see below). As further controls, we include relationship status 
(dummies for living-apart-together, cohabitation, marriage; using single as the 
reference category), subjective health in the past four weeks (dummies on a fi ve-
point scale), and a dummy for pregnancy.

Fixed-effects regression with cluster-robust standard errors is applied (for 
details of fi xed-effects estimation, see Brüderl and Ludwig 2015). Estimation is 
conducted with Stata 16.1. Below we provide only the graphical representations of 
the estimation results. Numerical results can be found in the Appendix.

First, we compare the results obtained with the three impact functions detailed 
in the last section. Figure 1 gives a graphic representation of the results. The step 
impact function tells us that after birth, mothers’ happiness is on average higher by 
.32 scale points than before birth (the average happiness of all person-years before 
the event is the reference period). Interpreted as a causal effect, this means that 
giving birth to a child makes mothers happier by .32 scale points.

The quadratic impact function provides a completely different answer: Here, 
happiness increases by .51 scale points right after birth, followed by a steep decline 
and negative values three years after birth, with a low point after 5 years. This is 
followed by a steep increase in happiness.

3 Mediators (intervening variables) should not be controlled for (overcontrol bias). Mediators 
must be controlled for if the target estimand is an indirect effect. Furthermore, colliders 
(variables that are affected by both the treatment and by the outcome) must not be included in 
the regression.



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 459

However, both step and quadratic impact functions provide grossly misleading 
answers, as the results of the dummy impact function show. We see that the birth of 
a child immediately increases happiness by .60 scale points (this is the coeffi cient of 
the “0-year dummy”, see Table A1). However, this “baby effect” is very short-lived: 
it exists only in the fi rst year after birth. The effect is much lower in the following 
years, and generally close to zero. This means that already one year after birth, 
mothers’ happiness essentially returns to the level before birth, on average.

Thus, the lesson learned here is that one always should start with a fl exible 
specifi cation of the impact function, i.e., a dummy impact function. If the dummy 
impact function provides a clear pattern, then one could use a more parsimonious 
specifi cation.

Figure 1 provides also an illustration of the negative weighting bias (we 
simplify here somewhat; exact details are provided in Section 5). Averaging the 
ten treatment effects estimated by the dummy impact function (see Table A1) 
gives: (0.60 + 0.09 + 0.04 + 0.19 – 0.01 * 6)/10 = 0.086. However, the step impact 
function provides an estimate of 0.32, i.e., grossly overestimates the true average of 

Fig. 1: The effect of the birth of a fi rst child on mothers’ happiness: comparing 
different impact functions

-0.2

-0.1

0.0

0.1

0.2

0.3

0.4

0.5

0.6

C
ha

ng
e 

in
 h

ap
pi

ne
ss

0 1 2 3 4 5 6 7 8 9 10

Age of first child

step impact
quadratic impact
dummy impact

Notes: Results from three FE regression models. Controls are age dummies, relationship 
status dummies, subjective health dummies, and a dummy for pregnancy. See Appendix, 
Table A1 for numerical results.
Source: pairfam release 11.0, own calculations



•    Volker Ludwig, Josef Brüderl460

the post-treatment effects. This is, because the mechanics of FE estimation down-
weights the treatment effects that occur in later post-treatment periods. Thus, the 
FE estimate of the step impact is biased towards the early treatment effects. Note 
that the negative weighting bias does not always provide a negative (i.e., downward) 
bias of the treatment effect. In our case the bias obviously is upwards. “Negative” 
refers to the down-weighting of later treatment effects.

Further insights can be gained if one adds the confi dence intervals to the plot of 
the dummy impact function. Figure 2 does this by plotting the regression coeffi cients 
of the dummies for the time since treatment along with 95 percent CIs. This fi gure 
also shows that the impact of treatment on outcome is indistinguishable from zero 
already one year after birth. Furthermore, it can be seen that the SEs increase 
with time since birth, simply because fewer and fewer observations contribute to 
estimation.

Fig. 2: The effect of the birth of a fi rst child on mothers’ happiness: dummy 
impact function

-0.3

-0.2

-0.1

0.0

0.1

0.2

0.3

0.4

0.5

0.6

0.7

0.8

C
ha

ng
e 

in
 h

ap
pi

ne
ss

0 1 2 3 4+

Age of first child
Notes: Regression coeffi cients for “years since birth dummies” including 95 percent 
confi dence intervals from a FE regression model. Controls are age dummies, relationship 
status dummies, subjective health dummies, and a dummy for pregnancy. This will be our 
reference model in the following. See Appendix Table A1, column 3, for numerical results.
Source: pairfam release 11.0, own calculations



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 461

5 Pitfalls and Remedies When Estimating Impact Functions

In the following, we highlight important issues arising with the estimation of impact 
functions that are often overlooked in applied research.  

Specifi cation of the outcome trajectory
Specifying the average trajectory of the outcome over process time is a crucial step 
for any panel data analysis. Misspecifi cation of the outcome trajectory may easily 
result in biased estimates of the treatment effect. This is true regardless of the type 
of impact function we assume. Thus, if we work with panel surveys of persons or 
households, it is essential to model the life course appropriately. Our specifi cation 
must include age effects (and/or period effects). Otherwise, we run into problems 
of confounding: effects that are driven by ageing and maturation might produce a 
spurious treatment effect or suppress the true effect. 

The FE model allows the researcher to consistently estimate age (A) effects, while 
simultaneously holding cohort effects (C) constant. C is constant across units, so 
the cohort effects are subsumed in the unit fi xed effects. Controlling for A is crucial 
for estimating treatment effects on person or household panel data. Intuitively, age 
is very likely a relevant confounder in many demographic studies. In settings with 
all units initially untreated and treatment being an absorbing state, A and D are 
related by defi nition: as time passes, the treatment probability strictly increases 
(although possibly in a nonlinear way; fi rst childbirth, for instance). Whenever the 
outcome changes over the life course, so that we have a correlation of A and Y as 
well, leaving out A from the regression would bias the effect of D. 

An important issue concerns the inclusion of an appropriate control group in the 
estimation sample to make use of the advantages of panel data when studying life 
courses. The popular event study design that uses only those units who eventually 
get treatment while observed does not allow the researcher to identify a time-
varying treatment effect in general. Borusyak and Jaravel (2017) discuss the under-
identifi cation problem of a FE model specifying a dummy impact function with a full 
set of leads and lags of the treatment variable (a “fully dynamic specifi cation”). They 
show that it is not possible to disentangle the effects of calendar time (or age) and 
time elapsed after treatment due to collinearity. It certainly would help to restrict the 
number of dummy variables for Kit, notably to include only post-treatment dummies. 
However, with all persons eventually experiencing the event, we inevitably run into 
collinearity problems towards the end of the observation window (especially if all 
persons in the sample are treated for a longer period of time). Therefore, we should 
always include a control group of never-treated units in our FE estimation sample to 
be able to identify continuous or dummy impact functions. 

Another important issue is the correct specifi cation of the functional form of the 
outcome trajectory. Misspecifi cation of the age effects would imply misrepresented 
potential outcome trajectories, which in turn biases our estimates of the treatment 
effect (the so-called “bias transfer”, see Ranjbar and Sperlich (2020) for formal 
proofs). Therefore, we should always take care regarding the underlying functional 
form assumptions of age effects. It is seldomly a good idea to simply specify a linear 



•    Volker Ludwig, Josef Brüderl462

age effect without further checks for linearity. Generally, we recommend including 
age as dummies in the model, since outcome trajectories often tend to be highly 
non-linear. A more parsimonious specifi cation should only be chosen if the resulting 
dummy coeffi cients show a regular pattern.

Besides controlling for age effects, it may also be necessary to control for period 
(P) effects. For example, happiness in a given population might change not only due 
to health deterioration (biological ageing), but also due to economic/political cycles. 
Including (unrestricted) period effects, however, produces the so-called age-period-
cohort (APC) problem, because the three variables are linearly dependent (see Kratz 
and Brüderl (2021) for more details). To separate A and P effects, we need to introduce 
parameter restrictions. A minimal restriction needed for identifi cation would be, 
for instance, that two period effects are equal. One should always think carefully 
about these restrictions, as they often exert strong impacts on the results (as well 
as on the treatment effect). It is not a good idea to simply let one’s software decide. 
For example, Stata and R would exclude the fi rst and the last period dummy, thus 
assuming the period effects are the same in the fi rst and last year of the observation 
window. This assumption clearly is not met if there is some (positive or negative) 
trend over calendar time. A better idea might be to exclude the fi rst two period 
dummies, or to group several years into a smaller set of period dummies (assuming 
piecewise constant effects over calendar time). Since all these restrictions are not 
testable, the more recent literature favors a “proxy approach”, whereby the period 
effects are proxied by variables that measure the economic/political cycle directly 
(e.g., GDP growth rates; see Kratz and Brüderl (2021) for more details).

Finally, we want to stress that in most demographic applications, age effects 
are more important than period effects. Maturation is ubiquitous in demographic 
outcomes and age is inherently and systematically related to treatment. It is unlikely 
that period effects are related in a similar systematic fashion to treatment. Therefore, 
one should include a full control set for the age effects (i.e., age dummies). Period 
effects may be included in a restricted/proxied version only. 

The widely used two-way FE model does not follow this recommendation: it 
prioritizes period/wave effects over age effects. This model includes a full set of 
period/wave dummies (i.e., period fi xed effects alongside the unit fi xed effects; 
hence the name), but no age controls: 

where γt represents the period fi xed effects and Xit does not include age. Given 
this specifi cation, the period fi xed effects will capture a mixture of period and age 
effects. This very likely will result in a misspecifi cation of the outcome trajectory 
and consequently in a biased treatment effect estimation. Thus, we warn against 
the “default use” of the two-way FE model.4

4 Researchers often inadvertently specify a two-way FE model by including a full set of wave 
dummies in their (single-way) FE model.

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What You Need to Know When Estimating Impact Functions with Panel Data ...    • 463

Continuing with our childbirth example, we will illustrate some of the points 
made in this section. First, we want to note that our estimation sample includes 
an appropriate control group of never-treated women: 2,477 women did not give 
birth to a fi rst child while observed in the pairfam study. These observations do not 
contribute to the estimation of the birth effect, but they contribute to the estimation 
of the age effect (and the effects of the other control variables5).

Second, we address the importance of specifying the functional form of the age 
effect correctly. As Kratz and Brüderl (2021) show, the age-happiness trajectory 
in Germany declines with age. The decline is slow between ages 18 and 65, and 
becomes steep afterwards. Thus, not controlling for age generally would lead to 
downward biased treatment effects. Since the decline is slow between ages 18 
and 65 (about .02 scale points per year), the bias is expected to be moderate in 
our application. Figure 3 presents the results for the 0-year dummy for differently 
specifi ed models. The fi rst one (“age dummies”) is the reference model. It includes 
a full set of age dummies (ages 16-47, 15 being the reference age). This is the 

Fig. 3: The effect of the birth of a fi rst child on mothers’ happiness: varying the 
specifi cation of the age effect

Time period
immediately
after birth of

first child

0.40 0.45 0.50 0.55 0.60 0.65 0.70 0.75 0.80

Effect on happiness

age dummies no control for age age linear two-way FE

Notes: Regression coeffi cients for the 0-year dummy including 95 percent confi dence 
intervals from four FE regression models with varying specifi cations of the age effect. 
Further controls are relationship status dummies, subjective health dummies, and a 
dummy for pregnancy. The fi rst model is our reference model. See Appendix, Table A2 
for numerical results.
Source: pairfam release 11.0, own calculations

5 Age is not the only important control variable. In our case, relationship status is also important. 
The effect of the 0-year dummy increases to .64 if we drop the relationship dummies from 
the model. The reason is that birth commonly is related to a partnership, and being partnered 
increases happiness strongly. This demonstrates that impact functions – as FE estimators 
generally – may be severely biased if important time-varying confounders are not controlled 
for.



•    Volker Ludwig, Josef Brüderl464

specifi cation used in the previous section, since age-happiness trajectories tend 
to be highly non-linear (see Kratz/Brüderl 2021). Thus, the reference birth effect 
immediately after birth is .60 scale points. The second model shows what happens 
if we do not control for age at all. Figure 3 shows that the effect is biased downwards 
to .58. As expected, this a moderate downward bias. The third model adds age 
as a linear control. We see that this is not a good idea in our case, as now there 
is an upward bias to .65. This is most likely some kind of over-control bias, where 
the linear outcome trajectory over-estimates the happiness decline over the main 
childbearing years. This demonstrates that the correct modelling of the functional 
form of the outcome trajectory is important.

Third, we will show how large the bias is by using the two-way FE model. The 
fourth coeffi cient in Figure 3 gives the result, if we include a full set of wave dummies 
instead of age dummies. Once again, we observe an upward bias to .65. In addition, 
the two-way FE model fi nds further signifi cant positive birth effects in the second 
and fourth years after birth. This indicates that the wave dummies are not able to 
control for the full age effect.6

Pre-treatment and late post-treatment dummies
As argued above, it is important to model the impact function as fl exibly as 
theory demands. We have explained how to model dummy impact functions by 
including indicators for discrete time after the exposition to a treatment. Theory 
often suggests that demographic events are anticipated by individuals, and thereby 
already exert a causal effect before treatment (anticipation effect). For instance, in 
the childbirth example, it is reasonable to assume that the mere expectation of a 
baby may already boost happiness. So, we might include a pre-treatment dummy 
indicating a person-year within the period of nine months prior to birth to capture 
anticipation during pregnancy. In fact, it is even advisable to do so: Otherwise, a 
positive anticipation effect would be incorrectly attributed to the life course of the 
reference period (comprising all person-years before birth), and any positive FE 
impact function would be biased downwards. 

Note that by including pre-treatment dummies, the reference period for the 
treatment effect changes. It is no longer all person-years before treatment, but only 
person-years before the fi rst pre-treatment dummy. For instance, if we include a -1-
year dummy, the reference period is k < -1.

However, we must be particularly careful when specifying further “leads” of 
the treatment dummy. We should not mindlessly include pre-treatment dummies 
as regressors. The problem is that pre-treatment dummies may capture not only 
an anticipation effect, which is usually interpreted causally, but also various other 
effects. First, there may be time-varying confounders that are omitted from our 
specifi cation. For example, the positive effects of forming a new relationship or 

6 Period effects do not seem to be very relevant in our observation window. Including a dummy 
for Wave 1 (to capture a potential effect due to the fi nancial crisis 2008/09) did not change 
results. Therefore, we do not include any period effect in our preferred specifi cation. 



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 465

household which usually occur prior to pregnancy may be confused with the 
anticipation of the child. (We should of course control for such confounders directly 
whenever it is possible.) Second, pre-treatment dummies might capture reverse 
causality, and feedback effects in particular: a positive “shock” to life satisfaction 
may lead people to decide to have a child. Third, self-selection into treatment may 
be related to growth of the outcome (see below). For instance, people who are 
on a steeper happiness trajectory throughout their lives might be more likely to 
eventually have children. 

Thus, the effects of pre-treatment dummies usually are not interpretable. It is 
often unclear whether they are driven by anticipation, omitted variable bias, reverse 
causality, or selection on growth. Only if we have a clear theoretical argument for 
anticipation (and can also exclude the other sources mentioned) and can pin the effect 
down by a precise measure (e.g., respondents answering that they are pregnant) 
should we include a pre-treatment dummy. Otherwise, pre-treatment dummies may 
capture spurious effects and thereby also bias the estimated treatment effects.

A further important decision when modelling dummy impact functions in 
particular, concerns how to handle late post-treatment dummies. With staggered 
treatments, early-treated persons potentially could still be observed long after 
treatment. However, due to panel attrition, we usually will have only few observations 
for late post-treatment dummies. Thus, the question of what we should do with 
these late post-treatment dummies arises. It is common practice in the demographic 
literature to group all post-treatment dummies into a residual dummy after a certain 
time point. Although this seems like it may be an innocuous decision, it can cause a 
bias of the treatment effects. 

As we noted earlier, assuming a step impact function can cause a negative 
weighting bias. This reasoning also applies to the dummy impact function with a cap 
time point. After the cap time point, we assume a step function. This assumption 
will be violated if there are time-varying treatment effects after the cap time-point. 
Basically, the functional form of the impact function is mis-specifi ed. Then, negative 
weighting might bias the estimate for the residual dummy, and due to bias transfer, 
all coeffi cients of the dummy impact function may be biased (Borusyak/Jaravel 
2017).7 It would thus be wrong to expect that grouping late treatment periods leaves 
the estimates of earlier post-treatment dummies unaffected in general. Rather than 
grouping late treatment periods in one dummy, we therefore recommend truncating 
the data, i.e., excluding the late periods from the sample. Clearly, paying attention 
to late post-treatment periods is particularly important if results of a fl exible impact 
function suggest strong treatment effects for these periods. 

Once again using our childbirth example, we will illustrate some of the points 
made in this section. In our application, an anticipation effect during pregnancy is 
highly likely: most pregnant women will be much happier in anticipation of the child 

7 A toy example with fi ctitious data demonstrating this bias is given in Figure A1 in the Appendix. 
In this example, the true impact function is increasing. Grouping post-treatment dummies 
biases the impact function downwards. The earlier the cap time point is, the larger the bias. 



•    Volker Ludwig, Josef Brüderl466

(especially if it is an intended pregnancy). In addition, a self-reported pregnancy 
indicator is available in pairfam. Therefore, we controlled for a pregnancy dummy 
in all models. The effect of a pregnancy in our reference model is large, at .61 scale 
points (see Table A1). This means that the pregnancy effect is as strong as the baby 
effect (which is .60 in the reference model)! Note that by including a pregnancy 
dummy, the reference period changes: The baby effect is in reference to all person-
years before birth, except person-years in pregnancy.

What happens with the baby effect if we choose different specifi cations? Figure 4 
provides answers to this question. The fi rst model is our reference model controlling 
for pregnancy. The second model does not control for pregnancy. As expected, the 
baby effect is strongly biased downwards to .45, because the anticipation effect 
now is in the reference period before birth. In our application, it would thus be a 
specifi cation error not to include the pregnancy dummy. 

However, in most applications, we will not have a direct measure of anticipation 
(i.e., pregnancy). In such cases, researchers often simply include pre-treatment 
dummies. We apply this procedure in the third model, where we include six pre-
treatment dummies up to k = -6, as is often done in the literature. The -1-year 
dummy may then capture the pregnancy effect (though imprecisely). The other 
pre-treatment dummies may capture other mechanisms, as argued above. To 
demonstrate this, we do not control for relationship status and health in this model. 
As can be seen in Figure 4, the result is a strong upward bias of the baby effect to 
.75. This is expected, since now the reference period is k < -6, long before birth, 
and when women may have had no partner and perhaps were in bad health. In 
addition, the confi dence interval is now much larger, because there are much fewer 
reference observations. Thus, we strongly advise against using pre-treatment 
dummies without good reason.

Finally, the last two models address the grouping issue. So far, we grouped all late 
post-treatment observations into a single group of k > = 4. As argued above, this is 
not optimal. However, there might be no problem in our case, because all treatment 
effects after the fi rst year are zero. So, the grouping has, in fact, no consequence, 
as shown with the estimate of the fourth model that excludes all person-years 
observed later than 4 years after childbirth. Generally, a sensible strategy to identify 
a short-lived treatment effect might be to truncate the post-treatment observation 
period after one year. As can be seen in Model 5 in Figure 4, we obtain basically the 
same result as in our reference model containing more post-treatment dummies.

Biased Impact Functions due to Heterogeneous Trajectories
Estimates of impact functions may be biased in the case of heterogeneous outcome 
trajectories that are related to the treatment process. In practice, it may therefore 
be necessary to allow for heterogeneous life courses when modelling an impact 
function. One way to do so would be to interact process time or age with a time-
constant indicator of the treatment group (FE with group-specifi c slopes, FEGS). An 
even more fl exible way would be to allow for individual-specifi c trajectories (FE with 
individual-specifi c slopes, FEIS) (Brüderl/Ludwig 2015; Rüttenauer/Ludwig 2020; 
Wooldridge 2010). 



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 467

Including individual-specifi c slopes for process time, age, or some other variable 
is a straightforward extension of the standard FE model. Modelling individual slopes 
explicitly relaxes the parallel trends assumption that is crucial for the consistency 
of FE estimates. Hence, FEIS guards against bias due to time-constant confounders 
related to differences in the outcome trajectories between treatment groups. An 
extended Hausman test can be used to decide whether FE estimates are biased 
(Rüttenauer/Ludwig 2020). 

Next, let us extend our empirical example on childbirth and happiness in that we 
allow for heterogeneous age-happiness trajectories for the women included in our 
pairfam sample. First, we must decide on a functional form for the individual slopes. 
We cannot use a dummy specifi cation for the age effect. The reason for this is simple: 
The FEIS model builds on variation in the data that is left over after controlling for 
the individual age effect. Technically, we therefore estimate the age effect for each 
person (by OLS), and to do so we need more observations than parameters for each 
person. Hence, we must use a parsimonious model specifying few parameters to 
estimate the individual slopes. Here, we simply allow for an individual constant and 
specify a linear effect of age. Thus, we estimate two individual-specifi c parameters 
(a constant and a slope). Therefore, FEIS estimation requires at least three 
observations per individual. For this reason, we are left with a restricted sample 
including 2,525 women, i.e., 84 percent of our previous sample. Note that these 

Fig. 4: The effect of the birth of a fi rst child on mothers’ happiness: varying the 
specifi cation of pre- or post-treatment effects

Time period
immediately
after birth of

first child

0.3 0.4 0.5 0.6 0.7 0.8 0.9 1.0

Effect on happiness

control for pregnancy no control for pregnancy
adding 6 pre-treatment dummies truncation after 4 years
truncation after 1 year

Notes: Regression coeffi cients for the 0-year dummy including 95 percent confi dence 
intervals from fi ve FE regression models with varying specifi cations of pre- or post-
treatment effects. The fi rst model is our reference model. See Appendix, Table A3 for 
numerical results.
Source: pairfam release 11.0, own calculations



•    Volker Ludwig, Josef Brüderl468

women nevertheless provide 95 percent of the observations of the previous sample, 
because we excluded only women with very few observations. Although we usually 
would hesitate to exclude such a large number of units from our estimation sample, 
it may actually not do much harm in terms of “representativeness” if viewed from 
the perspective of sampling life courses. 

Figure 5 depicts estimated coeffi cients for the pregnancy and age of fi rst child 
dummies from three models: a FE model using the full estimation sample, a FE 
model using the restricted sample, and a FEIS model (on the restricted sample). 
The restricted FE estimates indeed reproduce the unrestricted FE estimates almost 
perfectly. The FEIS effects are somewhat smaller, but still very close to the full FE 

Fig. 5: Effects of childbirth on happiness in models specifying homogeneous 
or heterogeneous age effects

-0.8
-0.7
-0.6
-0.5
-0.4
-0.3
-0.2
-0.1
0.0
0.1
0.2
0.3
0.4
0.5
0.6
0.7
0.8

C
ha

ng
e 

in
 h

ap
pi

ne
ss

Pregnancy 0 yrs. 1 yr. 2 yrs. 3 yrs. 4+ yrs.

Age of first child

FE FE restricted sample FEIS

Notes: Regression coeffi cients for “pregnancy” and “years since birth dummies” including 
95 percent confi dence intervals from FE and FEIS regression models. Controls are age 
(linear), relationship status dummies and subjective health dummies. FE models are run 
on a full estimation sample and a restricted sample (only women with 3+ person-years). 
The FEIS model uses the restricted sample. The FEIS model specifi es age as a variable 
with individual-specifi c slopes. See Appendix, Table A4 for numerical results.
Source: pairfam release 11.0, own calculations



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 469

model.8 This is also the result of formal testing: The extended Hausman test tells 
us that the coeffi cients of the restricted FE and the FEIS model are not signifi cantly 
different on the 5 percent signifi cance level (χ2 (13) = 21.80; p = 0.0586). The 
conclusion here would thus be that there is no substantial bias of the impact 
function due to heterogeneous age profi les (see Gattig and Minkus 2021 in this 
Special Issue for an analysis of the impact of marriage on happiness arriving at a 
similar conclusion). However, in other empirical applications, a bias may show up. 
We therefore recommend to at least conduct robustness analyses based on the 
FEIS model. Routines for Stata and R (xtfeis and feisr) are available for estimation 
and specifi cation tests (Ludwig 2019; Rüttenauer/Ludwig 2021).

Consecutive Life Events
Another problem for the estimation of treatment effects may result from 
consecutive life events with heterogeneous effects. To give an example: Causal 
effects of childbirth may depend on parity, such that the effect of the fi rst child 
differs from the effect of a second child. At fi rst sight, this setting does not introduce 
any diffi culties. It is common to use a sample of initially childless persons (as we 
recommended above) and proceed with a panel regression, including two separate 
dummy variables for person-years after the birth of a fi rst and second child (see, 
for an example, Abendroth et al. 2014). We call this the “single estimation sample 
strategy”. But this standard procedure may be problematic if the effects of early 
treatments are themselves heterogeneous, and selection into later treatments 
depends on the magnitude of earlier treatment effects. In our example, it might 
be that people who get higher returns for fi rst childbirth are more likely to have a 
second child than people without positive effects after their fi rst child. In this case, 
estimates of both treatment effects will be biased.

To clarify the issue: From a counterfactual perspective, we might distinguish 
between three different treatment effects in this situation (each built from differences 
between two out of three potential outcome trajectories):

E1: Effect of the 1st child for persons having only a 1st child compared to those 
always childless

E2: Effect of the 1st child for persons having a 1st and a 2nd child compared to 
those always childless

E3: Effect of 2nd child for persons having a 1st and a 2nd child compared to persons 
having only a 1st child (Here, we assume homogeneous effects.)

Using the single estimation sample strategy assumes that effects E1 and E2 are 
identical. This assumption often remains tacit and untested, but it may easily be 
wrong in practice. Effect E1 might be zero, which might be the reason that these 

8 Note that the baby effect in the FE models is overestimated here, because we use only a linear 
age control. In fact, the FE model with the full sample is identical to the model “Age linear” in 
Table A2/Figure 2. Note also that the coeffi cient of the three-year dummy is signifi cantly larger 
than 0. The FEIS model seems to “correct” these overestimations.



•    Volker Ludwig, Josef Brüderl470

particular people decide against having a second child, while effect E2 is positive. In 
this situation, the estimate of the dummy for the second child will not provide E3. It 
will be biased (upwards) due to the heterogeneity in E1 and E2. As a consequence, 
the average treatment effect (ATE, the average of E1 and E2) for the fi rst child will 
be biased (downwards).

We constructed a toy example to illustrate these biases. In the data shown in 
Figure 6, we have two treatment groups (of equal size) with different effects for a 
fi rst treatment: Group 1 has a fi rst treatment effect of 0 (E1), Group 2 of 1 (E2). Thus, 
the true ATE is 0.5. Now, only Group 2 receives a second treatment later on (t = 21), 
the second treatment effect being 1 (E3). The single estimation sample strategy 
introduces a dummy for treatment one (=1 for the blue and red person-years) and 
a second dummy for treatment two (=1 for the red person-years only). What are 
the results if we apply this standard strategy to the toy data from Figure 6? The FE 
estimate (two-way FE model) for treatment dummy one is 0.4. This is close to the 
true ATE, but with a small downward bias. This is due to a negative weighting bias 
(group one enters FE estimation with a larger weight). The FE estimate for treatment 
dummy two is 1.4. This is an overestimation, because the fi rst treatment effect was 
underestimated.

Fig. 6: A toy example with fi ctitious data of consecutive life events

Treated group 2

Treated group 1

Untreated group

0

1

2

3

4

5

6

7

8

9

10

Y

1 10 20 30
T

Notes: Treated Group 2 receives a fi rst treatment effect of 1 at t = 11 and a second 
treatment effect of 1 at t = 21. Treated Group 1 receives a fi rst treatment effect of 0 at 
t = 11 and no second treatment.
Source: fi ctitious data, own calculations



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 471

We see that the single estimation sample strategy may provide biased treatment 
estimates. To recover the true ATE for treatment one, we would have to exclude 
all observations after the second treatment, i.e., truncate the data at t = 20 for all 
panels in the sample. In practice, however, this will not be possible with staggered 
treatments. Nevertheless, it would be an improvement to truncate at least those 
panels that receive a second treatment. Then one could include interaction effects 
to allow for effect heterogeneity. In our toy example, the true effects for both 
treated groups can be recovered by including an interaction of treated group and 
the dummy for fi rst treatment.

Our advice for dealing with consecutive life events (complex life-courses) is to 
focus on specifi c transitions and to construct estimation samples accordingly. It 
is not advisable to estimate all treatment effects from a single estimation sample. 
Instead, we suggest using multiple, specially tailored estimation samples. We 
recommend fi rst defi ning the causal effect of interest based on comparing potential 
outcomes. Next, construct an appropriate sample to identify the effect. Finally, 
specify the correct statistical model to estimate the effect. 

Our recommendation to work from tailored estimation samples assumes rich 
data that allow for the construction of treatment groups that are suffi ciently large to 
be able to produce reliable estimates of the causal effects of interest. It might turn 
out, however, that effect heterogeneity induces only negligible biases. In that case, 
the main analysis could still use a more standard approach (estimation in a sample 
of various pooled treatment groups).9 Nevertheless, we should at least check. 
Moreover, the focus on specifi c treatment effects with reduced samples has the 
major advantage that it is straightforward to allow for time-varying effects. We can 
easily replace the step impact function with a dummy impact function, for instance.

6 Negative weighting bias with staggered treatment events

In practice, when estimating an impact function from person or household panel 
data, we often base our estimates on a staggered treatment design: persons receive 
the treatment at different points in time. Variation in the age of fi rst childbirth is 
one important example of staggered treatments in demographic research. As 
recent papers show, using data with staggered treatments and specifying a step 
impact function when the true treatment effect is time-varying may result in biased 
estimates (de Chaisemartin/D’Haultfœuille 2020; Goodman-Bacon 2018). This 
problem is known as the “negative weighting bias” of FE estimates. 

Negative weighting occurs with staggered treatment designs because, towards 
the end of the observation window, units who get the treatment earlier serve as 

9 Additional results with pairfam data showed that there was some heterogeneity for the effect 
of fi rst childbirth on happiness along the lines suggested here. However, this did not bias our 
result for the baby effect in any relevant way. Thus, we might have added person-years with a 
second child to our estimation sample.



•    Volker Ludwig, Josef Brüderl472

controls for units who get the treatment later. Treatment effects of early treated 
units that occur well after treatment are thus down-weighted by the construction 
of the FE estimator. As a consequence, FE estimates of the treatment effect will be 
biased towards the early treatment effects. 

To illustrate negative weighting, suppose we observe a fully balanced panel 
consisting of three groups of persons g = u, k, l, where one group remains untreated 
(u), one receives treatment early in time (k) and one is assigned to the treatment 
later in time (l). Let t = tk and t = tl denote the timing of treatment of groups k and 
l respectively. We then specify a two-way FE model to estimate the treatment 
effect, i.e., we allow for person and time fi xed-effects as in equation (3), but we do 
not include any further control variables. In this setting with staggered treatment 
adoption, whenever the true treatment effect varies over time, the standard FE model 
with a step impact function estimates a (downward) biased average treatment effect 
on the treated (ATT) due to negative weighting of the treatment effect during later 
post-treatment periods.10

A toy example with fi ctitious data for three treatment groups (of equal size) 
observed at t = 1, … , 30 is shown in Figure 7. For all three groups, there is a linear 
time trend, such that Y increases by 0.1 each period. For the two treated groups, 
there is also a treatment effect: starting at tk = 11 and tl = 21, respectively, their 
trend slope is 0.2 (i.e., an additional 0.1).

When estimating a step impact function with these data, most researchers 
expect that they would get a sample weighted average of the time-varying treatment 
effects. In our example, we know that the mean of the true treatment effect is  

for group k at times t = tk, … ,tl - 1, and 
at t = tl, … , T. It is 0.45 for group l at times t = tl, … , T. Given that groups k and l are 
equally large and group k provides 10 early and 10 late treated observations, while 
group l has only 10 late treated observations, it is natural to assume that each of 
the three average treatment effects should get a weight of 1/3 in the overall average 
effect. Thus, we might expect an FE estimate of 2/3 * 0.45 + 1/3 * 1.45 = 0.7833. 
However, estimation of a two-way FE model returns a downward biased coeffi cient 
of 0.45. How can this be?

The reason is that FE uses different (and incorrect) weights to build the average 
estimate. Let E(βjs) denote the true average treatment effect for group j = k, l during 
treated times s of that group. Furthermore, let pjs be the proportion of treated 
person-years contributed by group j during s to the total number of treated person-
years in the sample. Then,  

10 Assuming that a standard parallel trends assumption holds, it can be shown that the standard 
two-way FE estimator is identical to the weighted sum of Difference-in-Differences (DID) 
estimates (see Goodman-Bacon 2018). The results on the negative weighting bias thus apply 
to both the FE and the DID estimator. The problem also affects the estimation of FE models 
with individual-specifi c slopes (Meer/West 2016; Goodman-Bacon 2018; de Chaisemartin/
D’Haultfœuille 2020). However, if we do specify the impact function correctly, FEIS is a viable 
alternative for dealing with correlated heterogeneous trajectories. Rüttenauer and Ludwig 
(2020) show this through simulations.  



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 473

with weights  that sum up to 1. 

The crucial parameter that is responsible for negative weighting is φjs. The φjs 
are the residuals from a two-way FE regression (on the full sample) including unit 
and period fi xed effects with Dit as the dependent variable. The second term adjusts 
the weights for sample size and standardizes them so that they sum up to 1.

In our simple example, the estimated φjs are 1/3 for group k during t = tk, … , tl - 1 
and 1/3 for group l during t = tl, … ,T. The φjs is 0 however for group k during 
t = tl, … ,T. Intuitively, the zero weight results from the fact that these persons are 
already treated at tl, and FE puts them (erroneously) in the control group during 
the time up to T. Technically, their residuals from the regression on Dit are zero 
because, conditional on unit and period effects, there is no variation in Dit left over.

11 

Fig. 7: A toy example with staggered treatment design and a time-varying 
treatment effect

Early treated (k)

Later
treated (l)

Untreated (u)

0

1

2

3

4

5

6

7

8

9

10

Y

1 10 20 30
T

Source: fi ctitious data, own calculations

(4)

 

11 In other cases, negative residuals may be obtained for late periods, because with an absorbing 
treatment indicator, the predicted treatment probability towards the end of the observation 
window may actually be greater than 1 in a linear model on Dit.



•    Volker Ludwig, Josef Brüderl474

Adjusting the weights by sample size and standardizing them, we get weights wjs of 
1/2, 1/2 and 0. Plugging that into the formula for βFE, we fi nally get an estimated ATT 
of 1/2 * 0.45 + 1/2 * 0.45 + 0 * 1.45 = 0.45.  

As we have argued earlier, negative weighting of time-varying treatment effects 
provides a strong incentive to specify a fl exible impact function. Simply assuming a 
time-constant impact and including one treatment dummy often produces a bias in 
settings with staggered treatments. Contrary to its name, a negative weighting bias 
often biases the average effect upwards. For instance, often if we have a situation 
with an early positive, but transitory effect, and (close to) zero effects later on. With 
FE, late post-treatment effects get weights that are small, thus the overall average 
effect will often be similar to the short-term effect.

In fact, this occurs in our empirical example of happiness and childbirth as we 
discussed above on context of Figure 1. We expect an average effect of 0.086. 
But the step impact function provided an estimate of 0.32. Thus, in our empirical 
example, we observed an upward (!) bias of the step impact function due to negative 
weighting (see Borusyak/Jaravel 2017 for results in a very similar setting). 

Note that the negative weighting problem carries over to heterogeneous effects 
more generally (Goodman-Bacon 2018; de Chaisemartin/D’Haultfœuille 2020), as 
we discussed one example in the context of consecutive life events. It also applies 
to the estimation of dummy impact functions with inappropriate grouping, as 
shown earlier in our discussion of grouping post-treatment dummies (Borusyak/
Jaravel 2017).

Counterfactual Outcomes and the Selection of the Estimation Sample 
An important point concerns the deliberate choice of an appropriate sample for 
the identifi cation and estimation of the parameter(s) of interest. Social researchers 
usually try to maximize the number of observations with the objective of retaining 
a “representative” sample. In the framework of a cross-sectional research design, 
we would like to keep as many units (persons) as possible in the estimation sample. 
With panel data, the maximizing strategy would imply to include as many units 
(persons) and measurements per unit (person-years) as possible. However, there 
are important arguments against maximizing sample size. 

In general, the within panel design calls for the restriction of the sample to units 
with at least two valid measurements over time. Persons with only one person-year, 
for example, should be dropped because we do not observe useful variation over 
time for them on any variable. Thus, they do not help in identifying any effect of the 
covariates.12

12 Units with only one observation – “singletons” – should not be included for FE estimation. 
Including them will leave point estimates unchanged, because time-demeaning leaves them 
with zeros on all variables of the model. Also, conventional standard errors do not change. 
But singletons will affect the estimation of cluster-robust standard errors, which are usually 
reported in practice. Notably, the cluster-robust standard errors will be too small, because the 
degrees of freedom correction is incorrect (Correia 2015).



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 475

Moreover, maximizing the estimation sample may come at the price of biased 
estimates of the treatment effect. In a typical setting, in which we are interested 
in the causal effect of a binary absorbing treatment, we would like to restrict the 
estimation sample to persons who have not yet experienced the treatment event 
(say, the birth of a child). In fact, the estimate for a time-constant treatment effect 
(step impact function) must be biased if the true treatment effect is time-varying 
and we include persons who enter the panel only after treatment (Sobel 2012). For 
those people who do not experience treatment during the observation window, a 
constant treatment effect is not identifi ed using a within-panel design. 

Although people who have already been assigned to treatment before they enter 
the panel do experience a treatment effect, their value for Dit does not change in the 
data. It is always equal to 1. Hence, the always-treated are subsumed in the control 
group. Unless we explicitly (and correctly) specify the time-varying treatment 
effect, it is confounded with the effect of age (or process time). The counterfactual 
outcome trajectory is misrepresented by the average trajectory of the never-treated 
and the always-treated. This leads to biased estimates of the age effect or time 
trend, which in turn biases the estimation of the treatment effect. 

Note that this identifi cation problem induces a bias that is slightly different in 
nature from the negative weighting bias discussed in the preceding subsection. 
Essentially, including always-treated units introduces two sorts of biases, because 
these units already serve as controls not only in the post-treatment periods, but also 
in the pre-treatment periods of other treated groups. We have a negative weighting 
bias, as before. An additional bias, however, results from misrepresenting the 
counterfactual trajectory of the control group. Thus, including always-treated units 
exacerbates the bias of an FE step function estimate with time-varying treatment 
effects. 

To illustrate the bias due to the misrepresented counterfactual trajectory, we 
modify our toy data (from Fig. 7). We leave out the later-treated group l, but include 
an always-treated group a, which receives treatment right at entry into the panel 
(at t = 1). From then onwards, these persons experience the same time trend as 
groups u, k and the identical causal effect on the trend as group k. The modifi ed 
data are plotted in Figure 8a. However, due to their earlier treatment, time trend and 
causal effect are inseparable for always-treated persons. Specifying a step function 
would assume they are never treated because Dit does not change for them. Thus, 
the FE estimate of the time trend for the control group would be biased. Since the 
always-treated now also serve as controls during the pre-treatment period of group 
k, a second bias to the treatment effect is introduced in addition to the negative 
weighting bias that results from the always-treated serving as controls during post-
treatment periods of group k. 

Since group a is effectively subsumed in the control group (together with group 
u), the situation is equivalent to the data shown in Figure 8b: besides the trajectory 
for group k we have an average trajectory for groups a and u, denoted with u’. 
(From the raw data in Figure 8a, we simply calculate the mean of Y at t = 1, which 
is 2.5, and the mean of the slope of the time trend in both groups, which is 0.15.) 
With these modifi cations, two-way FE estimates an effect of 0.2. This is much lower 



•    Volker Ludwig, Josef Brüderl476

than the true sample weighted ATT, which equals  

if we exclude the always-treated and use the true counterfactual trajectory of group 
u (with a slope of 0.1). In fact, this is also what FE returns without the always-treated. 

As can be seen in Figure 8b from the different pre-treatment trends of the 
combined control group u’ and the treated group k, the bias with inclusion of an 
always-treated group thus effectively comes from a violation of the parallel trends 
assumption. Using the always-treated as part of the control group results in non-
parallel pre-treatment trends, thus violating the strict exogeneity condition of FE. 
Confounding of the time-varying treatment effect of an always treated group with 
an identical overall time trend for all groups thus induces a bias of the treatment 
effect.

As mentioned earlier, we should however include a control group of never-
treated units in order to control for age/period effects. Leaving out the group of 
untreated units also increases the negative weighting bias of FE. In our toy example 
(Fig. 7), if we exclude group u and apply equation (4), we end up with an FE estimate 
of the ATT of 1 * 0.45 + (-1/2) * 1.45 + 1/2 * 0.45 = -0.05, which is even negative 
due to the negative weight of -1/2 assigned to group k during the fi nal treatment 
period t = tl, …, T. 

In sum, whenever we specify a time-constant impact, we should include untreated 
units, but we should exclude units that are not at risk of getting treatment because 
they have already received it earlier. If we expect a time-varying treatment effect, 
we should of course specify it. Even then, we must use care with the always-treated 
units. For example, they might belong to older cohorts (which is likely because 
they received treatment earlier), and the time-varying pattern of the treatment 
effect may have changed over cohorts (assuming that we use multi-cohort data 
as with a household panel of the general population). So, we might again end up 
with a biased age effect and a resulting bias of the treatment effect. In general, we 
would therefore recommend excluding the always-treated units from the estimation 
sample, even if we specify a fl exible impact function. 

Fig. 8: A toy example illustrating the bias due to inclusion of the always-treated

early treated (k)

untreated (u)always treated (a)

0

1

2

3

4

5

6

7

8

9

10

Y

1 10 20 30
T

treated group k

control group u'

0

1

2

3

4

5

6

7

8

9

10

Y
1 10 20 30

T

a. Raw data of treated and untreated b. Treated and combined control group

Source: fi ctitious data, own calculations

 



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 477

7 Conclusion

The estimation of impact functions using panel data and FE models has become 
common practice in demographic research. In this paper, we addressed important 
decisions researchers face when modelling such impact functions. We identifi ed 
some problems and provided hands-on advice to applied researchers for dealing 
with these problems. Thus, we conclude with a list of recommendations for applied 
research.

1. Specify the impact function as fl exibly as theory demands. In most cases, 
this will mean that one should use a dummy impact function. If the dummy 
impact function provides a regular pattern, then one could instead use a more 
parsimonious specifi cation.

2. Specify the age-outcome trajectory in a fl exible way, i.e., by including age 
dummies as controls. If necessary, also control for period effects. However, 
do not use the two-way fi xed effects model (i.e., including wave dummies 
without close consideration).

3. Specify anticipation effects only if theory predicts these (and if you have 
direct measures of these). Do not include pre-treatment dummies without 
close consideration. These may make your results uninterpretable and 
increase estimation uncertainty.

4. Do not group late post-treatment dummies. It is better practice to truncate 
the post-treatment period.

5. Do not maximize the sample size. Instead, tailor the estimation sample 
according to the research question at hand. Include only units that were not 
treated when fi rst observed (i.e., drop the always-treated). Do not drop the 
control group of never-treated units.

6. In the case of consecutive life events, we advise defi ning the causal effect 
of interest based on comparing potential outcomes, focusing on specifi c 
transitions, and constructing estimation samples accordingly.

7. It may be necessary to allow for heterogeneous life courses when modelling 
an impact function (e.g., by allowing for individual-specifi c slopes).

Acknowledgment
We thank two reviewers for their helpful comments.

Data Note
This study uses data from the German Family Panel pairfam, coordinated by Josef 
Brüderl, Karsten Hank, Johannes Huinink, Bernhard Nauck, Franz Neyer, and Sabine 
Walper. pairfam is funded as long-term project by the German Research Foundation 
(DFG). pairfam data can be ordered at https://www.pairfam.de/en/. 
Replication fi les (Stata do-fi les) are available at Brüderl and Ludwig (2021).



•    Volker Ludwig, Josef Brüderl478

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Date of submission: 25.06.2021  Date of acceptance: 11.08.2021

Jun. Prof. Dr. Volker Ludwig (). TU Kaiserslautern. Department of Social Sciences.
Kaiserslautern, Germany. 
E-mail: ludwig@sowi.uni-kl.de
URL: https://www.sowi.uni-kl.de/en/sociology/team/ludwig

Prof. Dr. Josef Brüderl. University of Munich, Department of Sociology. Munich, 
Germany. E-mail: bruederl@lmu.de
URL: https://www.ls3.soziologie.uni-muenchen.de/personen/professor/bruederl_josef/
index.html



•    Volker Ludwig, Josef Brüderl480

Appendix

Tab. A1: The effect of the birth of a fi rst child on mothers’ happiness: comparing 
different impact functions

(1) Step impact (2) Quadratic impact (3) Dummy impact
(reference model)

Dummy 1st child 0.318*** 0.510***
(0.066) (0.070)

Age of 1st child (years) -0.248***
(0.051)

Age of 1st child squared 0.025***
(0.007)

Age of 1st child
0 years 0.599***

(0.071)
1 year 0.088

(0.091)
2 years 0.041

(0.101)
3 years 0.192

(0.120)
4+ years -0.009

(0.152)
Relationship status: Single (ref.)

Living apart together 0.344*** 0.343*** 0.342***
(0.030) (0.030) (0.030)

Cohabiting 0.436*** 0.423*** 0.421***
(0.043) (0.043) (0.043)

Married 0.484*** 0.463*** 0.467***
(0.070) (0.070) (0.070)

Health status: Bad (ref.)
Not so good 0.641*** 0.642*** 0.644***

(0.107) (0.107) (0.107)
Satisfactory 0.951*** 0.949*** 0.950***

(0.108) (0.108) (0.108)
Good 1.241*** 1.239*** 1.239***

(0.109) (0.109) (0.109)
Very good 1.520*** 1.514*** 1.514***

(0.112) (0.112) (0.112)
Dummy pregnancy 0.619*** 0.610*** 0.607***

(0.075) (0.076) (0.076)
Constant 6.564*** 6.555*** 6.553***

(0.129) (0.129) (0.129)

Age of resp. dummies included                  yes yes yes

Within R-squared 0.0696 0.0717 0.0727
N persons 2,982 2,982 2,982
NxT person-years 19,996 19,996 19,996

Regression results from FE regression models, coeffi cients and panel-robust standard errors (in 
parentheses).
* p<0.05, ** p<0.01, *** p<0.001

Source: pairfam release 11.0, own calculations



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 481

Tab. A2: The effect of the birth of a fi rst child on mothers’ happiness: dummy 
impact function

Age dummies No control for age Age linear Two-way FE
(reference model)

Age of 1st child
0 years 0.599*** 0.578*** 0.648*** 0.648***
 (0.071) (0.070) (0.070) (0.071)
1 year 0.088 0.061 0.156 0.177*

(0.091) (0.088) (0.090) (0.090)
2 years 0.041 0.012 0.138 0.152

(0.101) (0.096) (0.098) (0.098)
3 years 0.192 0.162 0.313** 0.317**

(0.120) (0.116) (0.118) (0.118)
4+ years -0.009 -0.054 0.175 0.163

(0.152) (0.147) (0.150) (0.150)
Relationship status: Single (ref.)

Living apart together 0.342*** 0.293*** 0.319*** 0.323***
(0.030) (0.030) (0.030) (0.030)

Cohabiting 0.421*** 0.284*** 0.382*** 0.380***
(0.043) (0.040) (0.042) (0.042)

Married 0.467*** 0.359*** 0.499*** 0.495***
(0.070) (0.065) (0.069) (0.069)

Health status: Bad (ref.)
Not so good 0.644*** 0.650*** 0.646*** 0.648***

(0.107) (0.108) (0.108) (0.107)
Satisfactory 0.950*** 0.948*** 0.948*** 0.955***

(0.108) (0.109) (0.108) (0.108)
Good 1.239*** 1.246*** 1.239*** 1.245***

(0.109) (0.109) (0.109) (0.109)
Very good 1.514*** 1.529*** 1.515*** 1.514***

(0.112) (0.113) (0.112) (0.112)
Dummy pregnancy 0.607*** 0.596*** 0.645*** 0.642***

(0.076) (0.075) (0.076) (0.076)
Age of respondent -0.031***

(0.005)
Constant 6.553*** 6.253*** 6.964*** 6.310***

(0.129) (0.107) (0.153) (0.109)

Age of resp. dummies included yes no no no
Survey wave dummies included no no no yes

Within R-squared 0.0727 0.0632 0.0669 0.0691
N persons 2,982 2,982 2,982 2,982
NxT person-years 19,996 19,996 19,996 19,996

Regression results from FE regression models, coeffi cients and panel-robust standard errors (in 
parentheses). 
* p<0.05, ** p<0.01, *** p<0.001
Source: pairfam release 11.0, own calculations



•    Volker Ludwig, Josef Brüderl482

Tab. A3: The effect of the birth of a fi rst child on mothers’ happiness: varying the 
specifi cation of pre- or post-treatment effects

No control Adding 6 Truncating Truncating
for pregnancy pre-treatment after 4 years after 1 year

dummies

Age of 1st child (post-treatment)
0 years 0.448*** 0.750*** 0.601*** 0.598***

(0.067) (0.114) (0.071) (0.073)
1 year -0.071 0.194 0.088

(0.088) (0.129) (0.091)
2 years -0.121 0.099 0.043

(0.096) (0.141) (0.100)
3 years 0.034 0.263 0.190

(0.116) (0.152) (0.120)
4+ years -0.187 0.021 -0.089

(0.147) (0.189) (0.193)
Age of 1st child (pre-treatment) 

-1 year 0.460***
(0.110)

-2 years 0.041
(0.114)

-3 years 0.126
(0.110)

-4 years -0.004
(0.117)

-5 years 0.062
(0.113)

-6 years -0.142
(0.118)

Dummy pregnancy 0.612*** 0.634***
(0.075) (0.076)

Relationship status: Single (ref.)
Living apart together    0.343*** 0.344*** 0.338***

(0.030) (0.030) (0.030)
Cohabiting 0.439*** 0.420*** 0.425***

(0.043) (0.043) (0.043)
Married 0.544*** 0.475*** 0.528***

(0.069) (0.070) (0.072)
Health status: Bad (ref.)

Not so good 0.648*** 0.619*** 0.614***
(0.107) (0.108) (0.109)

Satisfactory 0.960*** 0.924*** 0.929***
(0.108) (0.109) (0.110)

Good 1.247*** 1.211*** 1.205***
(0.109) (0.109) (0.110)

Very good 1.520*** 1.489*** 1.486***
(0.112) (0.113) (0.114)



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 483

No control Adding 6 Truncating Truncating
for pregnancy pre-treatment after 4 years after 1 year

dummies

Constant 6.529*** 7.798*** 6.580*** 6.585***
(0.129) (0.071) (0.129) (0.130)

Age of resp. dummies included yes yes yes yes

Within R-square 0.0688 0.0149 0.0724 0.0733
N persons 2,982 2,982 2,982 2,982
NT person-years 19,996 19,996 19,782 18,967

Tab. A3: Continuation

Regression results from FE regression models, coeffi cients and panel-robust standard errors (in 
parentheses). 
* p<0.05, ** p<0.01, *** p<0.001
Source: pairfam release 11.0, own calculations



•    Volker Ludwig, Josef Brüderl484

Tab. A4: Effects of childbirth on happiness in models specifying homogeneous 
or heterogeneous age effects

FE FE FEIS
full sample restricted sample restricted sample

Age of 1st child
0 years 0.648*** 0.648*** 0.570***

(0.070) (0.072) (0.091)
1 year 0.156 0.158 -0.020

(0.090) (0.090) (0.129)
2 years 0.138 0.140 -0.032

(0.098) (0.098) (0.156)
3 years 0.313** 0.315** 0.091

(0.118) (0.118) (0.206)
4+ years 0.175 0.177 -0.118
 (0.150) (0.150) (0.291)

Dummy pregnancy 0.645*** 0.645*** 0.544***
(0.076) (0.077) (0.087)

Relationship status: Single (ref.)
Living apart together 0.319*** 0.315*** 0.348***

(0.030) (0.031) (0.033)
Cohabiting 0.382*** 0.383*** 0.415***

(0.042) (0.042) (0.049)
Married 0.499*** 0.493*** 0.474***

(0.069) (0.070) (0.089)
Health status: Bad (ref.)

Not so good 0.646*** 0.625*** 0.609***
(0.108) (0.109) (0.111)

Satisfactory 0.948*** 0.934*** 0.928***
(0.108) (0.110) (0.111)

Good 1.239*** 1.224*** 1.187***
(0.109) (0.111) (0.112)

Very good 1.515*** 1.496*** 1.439***
(0.112) (0.114) (0.116)

Age of respondent -0.031*** -0.031*** Individual-specifi c
(0.005) (0.005) slopes

Constant 6.964*** 6.979***
(0.153) (0.155)

Within R-square 0.0669 0.0668 0.0615
N persons 2,982 2,526 2,526
NT person-years 19,996 19,084 19,084

Notes: Regression results from FE and FEIS regression models, coeffi cients and panel-robust 
standard errors (in parentheses); the restricted sample is restricted to women providing at least three 
person-years. The fi rst model is identical to the model “Age linear” from Table A2.
* p<0.05, ** p<0.01, *** p<0.001
Source: pairfam release 11.0, own calculations



What You Need to Know When Estimating Impact Functions with Panel Data ...    • 485

Fig. A1: Biased impact functions due to grouping late treatment dummies 
(Toy example with fi ctitious data)

-0.5

-0.3

0.0

0.3

0.5

0.8

1.0

1.3

1.5

1.8

2.0

C
ha

ng
e 

in
 Y

0 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19

Time since treatment

Full set of dummies 5+ yrs. grouped
10+ yrs. grouped 15+ yrs. grouped

Notes: The fi ctitious data are the same as in Figure 7, with a staggered treatment design (one early 
and one late treated group) and a time-varying treatment effect. The model with a full set of dummy 
variables exactly hits the true impact function. Other models that instead group treatment periods 
towards the end of the observation window return biased impact functions. 
Source: fi ctitious data, own calculations



Published by
Prof. Dr. Norbert F. Schneider

Federal Institute for Population Research 
D-65180 Wiesbaden / Germany

 2021

Managing Editor 
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Dr. Katrin Schiefer

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