Quality by Design : Design of experiments

Design of Experiments

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the latest in Pharmaceuticals.

www.drugragulations.org 1

Product Profile  Quality Target Product Profile (QTPP)

CQA’s  Determine ―potential‖ critical quality attributes (CQAs)

Risk Assessments  Link raw material attributes and process parameters to
CQAs and perform risk assessment
Design Space  Develop a design space (optional and not required)

Control Strategy  Design and implement a control strategy

Continual  Manage product lifecycle, including continual
Improvement
improvement


Product Profile

CQA’s
 This presentation Part VI of the
Risk Assessments series ―QbD for Beginners‖ covers
basic aspects of
Design Space
◦ Design of Experiments
Control Strategy

Continual
Improvement


 Experiment: a test or series of tests where the
experimenter makes purposeful changes to
input variables of a process or system so that
we can observe or identify the reasons for
changes in the output responses.
 Design of Experiments: is concerned with the
planning and conduct of experiments to
analyze the resulting data so that we obtain
valid and objective conclusions.


 Discovery
◦ Designed to generate new ideas or approaches
◦ Usually involve ―hands-on‖ activities
◦ May involve systems or processes that are not well
understood or refined.
 Hypothesis
◦ Closer to the traditional academic approach
◦ Seek to falsify specific hypotheses
◦ Used often in the attempt to ―prove‖ a
theory, idea, or approach


 Determine which variables are the most
influential in a process or system
 Determine where to set the inputs so the
output is always near the desired state
output variability is minimized
influence of uncontrollable factors is
minimized (robust design)


 Best Guess
◦ PRO: Works reasonably well when used by SMEs
with solid foundational knowledge on known issues
◦ CONs: If it fails, need to guess again…and
again…until….
◦ If get acceptable results first time, may stop without
discovering ―better‖


 One Factor at a Time
◦ PRO: Straight-forward, easily understood
◦ CONs: Impossible to address interactions
◦ Tends to ―over collect‖ data, not efficient sample
sizes


 Factorial
◦ PROs: Full evaluation of individual and interaction
effects
◦ Most efficient design with respect to sample sizes
◦ CON: More complex to explain to untrained
audiences


 Replication
◦ Permits estimation of experimental error
◦ Permits more precise estimates of the sample
statistics
◦ Not to be confused with repeated measures


 Randomization
◦ Insures that observations or errors are more likely
to be independent
◦ Helps ―average out‖ effects of extraneous factors
◦ Special designs when complete randomization not
feasible


 Blocking
◦ Designed to improve precision of comparisons
◦ Used to reduce or eliminate nuisance factors


◦ A nuisance factor is a ―design factor that probably
has an effect on the response but we are not
interested in that effect‖


 Nuisance Factors, Types ⇒ Cures
◦ Known and controllable ⇒ Use blocking to
systematically eliminate the effect
◦ Known but uncontrollable ⇒ If it can be
measured, use Analysis of Covariance
(ANCOVA)
◦ Unknown and uncontrollable ⇒ Randomization is
the insurance


 Treatments are the different procedures we
want to compare.
 Experimental units are the things to which we
apply the treatments.
 Responses are outcomes that we observe
after applying a treatment to an experimental
unit.


 Randomization is the use of a
known, understood probabilistic mechanism
for the assignment of treatments to units.
 Other aspects of an experiment can also be
randomized: for example,
◦ The order in which units are evaluated for their
responses.


 Experimental Error is the random variation
present in all experimental results.
 Different experimental units will give different
responses to the same treatment.
 It is often true that applying the same treatment
over and over again to the same unit will result
in different responses in different trials.
 Experimental error does not refer to conducting
the wrong experiment or dropping test tubes.


 Measurement units (or response units) are
the actual objects on which the response is
measured.
 These may differ from the experimental units.


 Distinction between experimental units and
measurement units.
 Consider an educational study, where six
classrooms of 25 first graders each are assigned
at random to two different reading
programs, with all the first graders evaluated via
a common reading exam at the end of the
school year.
 Are there
 six experimental units (the classrooms) or
 150 (the students)?

 One way to determine the experimental unit is via the
consideration that an experimental unit should be able
to receive any treatment.
 Thus if students were the experimental units, we could
see more than one reading program in any treatment.
 However, the nature of the experiment makes it clear
that all the students in the classroom receive the same
program, so the classroom as a whole is the
experimental unit.
 We don’t measure how a classroom reads, though; we
measure how students read. Thus students are the
measurement units for this experiment.


 Blinding occurs when the evaluators of a
response do not know which treatment was
given to which unit.
 Blinding helps prevent bias in the
evaluation, even unconscious bias from well-
intentioned evaluators.
 Double blinding occurs when both the
evaluators of the response and the (human
subject) experimental units do not know the
assignment of treatments to units.


 Control has several different uses in design.
First, an experiment is controlled because we
as experimenters assign treatments to
experimental units. Otherwise, we would have
an observational study.


 Second, a control treatment is a ―standard‖
treatment that is used as a baseline or basis
of comparison for the other treatments.
 This control treatment might be the
treatment in common use, or
 It might be a null treatment (no treatment at
all).
 For example, a study of new pain killing
drugs could use a standard pain killer as a
control treatment.


 Factors combine to form treatments.
 For example, the baking treatment for a cake
involves a given time at a given temperature.
 The treatment is the combination of time and
temperature, but we can vary the time and
temperature separately.
 Thus we speak of a time factor and a
temperature factor.
 Individual settings for each factor are called
levels of the factor.


 Confounding occurs when the effect of one factor
or treatment cannot be distinguished from that
of another factor or treatment.
 The two factors or treatments are said to be
confounded.
 Except in very special
circumstances, confounding should be avoided.
 Consider planting wheat variety A in Punjab and
Wheat variety B in M.P .
 In this experiment, we cannot distinguish
location effects from variety effects—the variety
factor and the location factor are confounded.


 A good experimental design must
◦ Avoid systematic error
◦ Be precise
◦ Allow estimation of error
◦ Have broad validity.


 Comparative experiments estimate
differences in response between treatments.
 If our experiment has systematic error, then
our comparisons will be biased, no matter
how precise our measurements are or how
many experimental units we use.


 For example, if responses for units receiving
treatment one are measured with instrument
A, and responses for treatment two are
measured with instrument B, then we don’t
know if any observed differences are due to
treatment effects or instrument Mis-
calibrations.
 Randomization, is our main tool to combat
systematic error


 Even without systematic error, there will be random
error in the responses.
 This will lead to random error in the treatment
comparisons.
 Experiments designed to increase precision are
precise when this random error in treatment
comparisons is small.
 Precision depends on the
◦ Size of the random errors in the responses,
◦ The number of units used, and
◦ The experimental design used.
 There are several designs to improve precision.


 Experiments must be designed so that we
have an estimate of the size of the random
error.
 This permits statistical inference:
◦ Confidence intervals or
◦ Tests of significance.
 We cannot do inference without an estimate
error.


 We characterize an experiment by the
treatments and experimental units to be
used, the way we assign the treatments to
units, and the responses we measure.
 An experiment is randomized if the method
for assigning treatments to units involves a
known, well-understood probabilistic
scheme. The probabilistic scheme is called a
randomization.


 An experiment may have several randomized
features in addition to the assignment of
treatments to units.
 Randomization is one of the most important
elements of a well-designed experiment.


 We defined confounding as occurring when
the effect of one factor or treatment cannot
be distinguished from that of another factor
or treatment.
 Randomization helps prevent confounding.
 Let’s start by looking at the trouble that can
happen when we don’t randomize.


 Consider a new drug treatment for coronary artery
disease.
 We wish to compare this drug treatment with
bypass surgery, which is costly and invasive.
 We have 100 patients in our pool of volunteers
that have agreed via informed consent to
participate in our study;
 They need to be assigned to the two treatments.
 We then measure five-year survival as a response


 What sort of trouble can happen if we fail to randomize?
 Bypass surgery is a major operation, and patients with
severe disease may not be strong enough to survive the
operation.
 It might thus be tempting to assign the stronger patients to
surgery and the weaker patients to the drug therapy.
 This confounds strength of the patient with treatment
differences.
 The drug therapy would likely have a lower survival rate
because it is getting the weakest patients, even if the drug
therapy is every bit as good as the surgery.


 Alternatively, perhaps only small quantities of the drug
are available early in the experiment, so that we assign
more of the early patients to surgery, and more of the
later patients to drug therapy.
 There will be a problem if the early patients are
somehow different from the later patients. For
example, the earlier patients might be from your own
practice, and the later patients might be recruited from
other doctors and hospitals.
 The patients could differ by age, socioeconomic
status, and other factors that are known to be
associated with survival.


 Here is how randomization has helps us.
 No matter which features of the population of
experimental units are associated with our
response, our randomizations put approximately half
the patients with these features in each treatment
group.
◦ Approximately half the men get the drug;
◦ Approximately half the older patients get the drug;
◦ Approximately half the stronger patients get the drug; and so
on.
 These are not exactly 50/50 splits, but the deviation
from an even split follows rules of probability that we
can use when making inference about the treatments.


 This example is, of course, an
oversimplification.
 A real experimental design would include
considerations for age, gender, health
status, and so on.
 The beauty of randomization is that it helps
prevent confounding, even for factors that we
do not know are important.


 We have taken a very simplistic view of
experiments;
 ―assign treatments to units and then measure
responses‖ hides a multitude of potential steps
and choices that will need to be made.
 Many of these additional steps can be
randomized, as they could also lead to
confounding.


 If the experimental units are not used
simultaneously, you can randomize the order in
which they are used.
 If the experimental units are not used at the same
location, you can randomize the locations at which
they are used.
 If you use more than one measuring instrument
for determining response, you can randomize
which units are measured on which instruments.


 Recognition and statement of the problem in
non statistical language
◦ Selection of factors, levels, ranges
◦ Selection of response variables
◦ Choice of experimental design
◦ Performance of the experiment
◦ Statistical analysis of the data
◦ Conclusions and recommendations


 Use team’s non-statistical knowledge of the problem to:
◦ Choose factors
◦ Determine proper levels
◦ Decide number of replications
◦ Interpret results
 Keep the design and analysis as simple as
 possible
 Recognize the difference between practical and statistical
significance
 Be prepared to iterate – commit no more than 25% of
available resources to first series


 Goal:
◦ Compare two or more means; variances; probabilities
◦ Compare A versus B: [better or worse] – paired
comparison is a special case of randomized block design
 Major Considerations
◦ Sample size
◦ Distributional knowledge: Normal, χ2, F …..etc.
◦ Structure of the statistical hypothesis
 One-tailed


 One Factor – Multiple Levels
◦ ―One-level-at-a-time‖ analysis isn’t efficient
◦ Consider one factor with five levels
◦ Pair-wise comparison requires 10 pairs [ 5C2 = 10 ]
◦ If each comparison has α = 0.05, then
◦ Probability(correct assessment) = (1-α)10 = 0.60


 Technique of Choice – ANOVA
◦ Tests hypothesis H0: μ1 = μ2 = μ3 = … μn
 Assumptions
◦ Error term is Normal (0,σ2) ⇒ test residuals to confirm
◦ Conditions properly randomized
◦ Results are independent; errors are independent
 If reject H0 (i.e., failed the test) then use
Newman-Keuls Range Test or Duncan’s Multiple
Range Test to determine the specifics
 Note – there are non-parametric tests in lieu of
ANOVA if assumptions are not met (e.g. Kruskal-
Wallis Test)


 Single Factor – Unit Days of Supply
 Levels – 5, 10, 15, 20, 25

 Latin Square: An arrangement of conditions
such that each combination occurs only once
in each row and column of the test matrix.

A B C D
B C D A Orthogonal
Latin
Square
C D A B
D A B C

Graeco-Latin Square: The superposition of two Latin
Squares such that each paired-combination occurs
only once in each row and column.


 Definition: An experiment in which for each
completed trial or replication of the experiment
all possible combinations of the levels of the
factors are investigated.
 Design Notation
◦ General Notation for 2-level experiment ⇒ 2k where k
= number of factors
◦ 3 factors 2 levels each = 23 design
◦ Factors and Levels ⇒ example for 3 factors, 2 levels
◦ Aa Bb Cc
◦ A+A- B+B- C+C-
◦ (1) a b c


 All combinations are examined
◦ Example 23 design = 8 experimental settings:
◦ A+B+C+, A-B+C+, A+B-C+, A+B+C-, A-B-C+, A-B+C-
, A+B-C- ,A-B-C-

 Effects Evaluated
◦ Main effects of single factors: A, B, C
◦ Second Order (2-factor) interactions: AB, AC, BC
◦ Third Order (3-factor) interactions: ABC
◦ In general, a 2k design evaluates all 1, 2, …k-1, k-
factor effects


 Advantages over ―one-factor-at-a-time‖
◦ More efficient in time, resources, sample size
◦ Addresses interactions
◦ Provides insight over a range of experimental
conditions


bc
abc A B C
- - --
c ac + - -
- + -
ab + + -
C +
B - - +
b
_ _ + - +
_
1 A + a - + +
+ + +


DoE : number of experiments
D O E : Number of experiments

52

 With n experiments, you can calculate the
coefficients for n-1 factors and interactions
◦ For 2 factors, Factorial design requires 22 = 4
experiments, you can calculate the coefficients for
3 factors and interactions : A, B and interaction AB
(green color), it’s not interesting to erase 1
experiment and loose informations on possible
interaction between A and B.

53

◦ For 3 factors, Factorial design requires 23 = 8
experiments, you can calculate the coefficients for
7 factors and interactions : A, B, C and interactions
AB, AC, BC and ABC. Using semi Factorial design (22
= 4 experiments) informations on possible
interaction are also lost (red color).

54

◦ For more than 3 factors, the number of
experiments should be limited to the number of
factors tested + the number of single interactions. I
never found (up to now) significant triple
interactions (ABC), Why loose time, money for a
large number of such interactions
ABC…F, ABD…F, ACD…F, AED…F…(yellow color)

55

Trial A B C
1 Lo Lo Lo
2 Lo Lo Hi
3 Lo Hi Lo
4 Lo Hi Hi
5 Hi Lo Lo
6 Hi Lo Hi
7 Hi Hi Lo
8 Hi Hi Hi

 ANOVA
 Standard deviation
 Coefficient of variation
 R2 Measures the proportion of total variability explained by the model
 Adjusted R2 - adjusted for the number of Factors .If non-significant terms
are ―forced‖ into the model this can decrease

 PRESS = Prediction Error Sum of Squares - A
measure of how well the model will ―predict‖ new data. Smaller is better but can only be used in a
comparative sense

 Linear regression


 Tests of Significance
◦ Overall model response
◦ Individual coefficients
 Diagnostic tests
◦ Residuals
◦ Outliers
◦ Lack of Fit


 A way to reduce a huge full factorial to
something manageable
 Considerations
◦ Required time, resources
◦ Complexity of set-up for experiments
 Major use is in screening experiments where
the knowledge of basic effects is not well
known
 If 2k is very large, may need to run reduced
experiment


 Justification
◦ Sparsity of Effects – in general, even complex
systems are usually driven by a few main effects
and low-level interactions
◦ Projection Property – fractional factorial designs can
be ―projected‖ into larger designs in the subset of
significant factors
◦ Sequential Experimentation – can combine runs of 2
or more fractional designs into larger designs


 Issue:
◦ Confounding of Effects (also called ―aliasing‖) ⇒ reduced
experiments do not evaluate all levels of the factors and
their interactions .
◦ Some mixture of effects is ―confounded‖ and not
identifiable
 Challenge:
◦ To select the best combination of test elements that stands
a reasonable chance of revealing the true effects
◦ Alias the (most likely) insignificant or unwanted factors
 Symbology
◦ 2k-p designs


L
Factorial analysis : N

(L-X)
Semi Factorial analysis : N

Loss of resolution (aliase)

Number of factor
2 3 4 5 6 7 8
Full 1/2
Number of experiments

4
8 Full 1/2 1/4 1/8 1/16
16 Full 1/2 1/4 1/8 1/16
32 Full 1/2 1/4 1/8
64 Full 1/2 1/4
128 Full 1/2
256 Full

62

22 Factional Factorial

No of Factors
exp
A B
1 + -
2 - -
3 + +
4 - +


22 Factional Factorial

No of exp Factors Interaction
A B AB
1 + - -
2 - - +
3 + + +
4 - + -


23-1 Factional Factorial

No of Factors
exp C=AB
A B C=AB
1 + - - C is confounding with AB
2 - - +
3 + + +
4 - + -



No of Factors and interaction
exp
A B=AC C=AB C=AB
2 - - + B=AC
3 + + + B is confounding with AC
4 - + -



No of Factors and interaction
exp
A=BC B=AC C=AB C=AB
2 - - + B=AC
3 + + + B is confounding with AC
A=BC
4 - + -
A is confounding with BC


A B C D E Yield %
-1 -1 -1 -1 1 49.8
1 -1 -1 -1 -1 51.2
-1 1 -1 -1 -1 50.4
1 1 -1 -1 1 52.4
-1 -1 1 -1 -1 49.2
1 -1 1 -1 1 67.1
-1 1 1 -1 1 59.6
1 1 1 -1 -1 67.9
-1 -1 -1 1 -1 59.3
1 -1 -1 1 1 70.4
-1 1 -1 1 1 69.6
1 1 -1 1 -1 64
-1 -1 1 1 1 53.1
1 -1 1 1 -1 63.2
-1 1 1 1 -1 58.4
1 1 1 1 1 64.3


B B

+1 +1
50.40 52.40 69.60 64.00

59.60 67.90 58.40 64.30

-1 49.80 51.20 A -1 59.30 70.40 A
-1 -1 +1

-1 -1

49.20 67.10 53.10 63.20

C +1 C +1
Left Cube is D = LOW Right Cube is D = HIGH

E = HIGH www.drugragulations.org
E = LOW 69

 Resolution ⇒ a measure of confounding

 Resolution III 2K-p III
◦ No main effect aliased with any other main effect
◦ Main effects are aliased with 2-factor interactions
◦ 2-factor interactions may be aliased with each other



 Resolution IV 2K-p IV
◦ No main effect aliased with 2-factor interactions
◦ 2-factor interactions may be aliased with each other



 Resolution V 2K-p V
◦ No main effect aliased with 2-factor interactions
◦ No 2-factor interactions may be aliased with each
other
◦ 2-factor interactions are aliased with 3-factor
interactions


DoE : number of experiments
D O E Resolution Trade off’s

73

 Three levels for k-factors (3k) designs
 Fractional 3-level designs (3k-p)
 Adding Center runs to
◦ Get estimates of process variability
◦ Gain familiarity with the process
◦ Identify system performance limits
 Mixture Designs – where one or more factors are
constrained to add to something
◦ Usually have constraints like: x1 + x2 + x3 +…+xp = 1
◦ Example: A mixture of contributing probabilities
 Nested and Split-Plot designs for experiments
with random factors


 Irregular Fraction
◦ Usually a Resolution V design for 4 to 9 factors
where each factor is varied over only 2 levels.
◦ Two-factor interactions aliased with three-factor
and higher
◦ Excellent to reduce number of runs and still get
clean results
 General Factorial
◦ For 1 to 12 factors where each factor may have a
different number of levels
◦ All factors treated as categorical


 D-Optimal
◦ A special design for categorical factors based on a
analyst specified model
◦ Design will be a subset of the possible
combinations
◦ Generated to minimize the error associated with the
model coefficients


 Plackett-Burman
◦ Specialized design for 2 to 31 factors where each
factor is varied over only 2 levels
◦ Use only if you can reasonably assume NO two-
factor interactions; otherwise, use fractional
factorial designs.


Matrix

X1 X2 X3 X4 X5 X6 X7 X8 X9 X10 X11

1 1 1 1 1 1 1 1 1 1 1

1 1 1 -1 -1 -1 1 -1 -1 1 -1

1 1 -1 -1 -1 1 -1 -1 1 -1 1

1 -1 1 1 1 -1 -1 -1 1 -1 -1

1 -1 -1 1 -1 1 1 1 -1 -1 -1 y( 1) y( 1)
1 -1 -1 -1 1 -1 -1 1 -1 1 1 Ex
-1 1 1 1 -1 -1 -1 1 -1 -1 1 N /2
-1 1 -1 1 1 1 -1 -1 -1 1 -1

-1 1 -1 -1 1 -1 1 1 1 -1 -1

-1 -1 1 -1 1 1 1 -1 -1 -1 1

-1 -1 1 -1 -1 1 -1 1 1 1 -1

-1 -1 -1 1 -1 -1 1 -1 1 1 1


 Taguchi OA
◦ Saturated orthogonal arrays – all main effects and
NO interactions
◦ Special attention must be paid to the alias structure
for proper interpretation at both the design phase
(prior to runs) and during final analysis


 Goal: develop a model that describes a
continuous curve, or surface, that connects
the measured data taken at strategically
important places in the experimental window


 RSM uses a least-squares curve-fit
(regression analysis) to:
◦ calculate a system model (what is the process?)
◦ test its validity (does it fit?)
◦ analyze the model (how does it behave?)

Bond = f(temperature, pressure, duration)
Y = a0 + a1 T + a 2 P + a3 D
+ a11T2 + a22P2 + a33D2
+ a12TP + a13TD + a23PD


RSM characteristics

Models are simple polynomials
Include terms for interaction and curvature
Coefficients are usually established by regression analysis with a computer program
Insignificant terms are discarded
Model equation for 2 factors

Y = β0 constant
+ β 1X1 + β2X2 main effects
+ β 3X12 + β4X22 curvature
+ β 5X1X2 interaction
+ ε error Model equation for 3 factors
Y= β0 constant
Higher order interaction terms + β1X1 + β 2X2 + β3X3 main effects
are not included + β11X12 + β22X22 + β33X32 curvature
+ β12X1X2 + β13X1X3 + β23X2X3 interactions
+ ε error

Response surface methodology
Central composite design (CCD)
eg. 2 factor
Central composite circumscribed (CCC)

5 Levels
α (star point) are beyond levels

Central composite face centered (CCF)

3 Levels
α (star point) are within levels (center)

Central composite inscribed (CCI)
5 Levels
α (star point) are within levels
Scale down of CCC



3 factors
Total exp: 20
Full factorial 8 Pattern X1 X2 X3

Axial points 6
+++ 1 1 1
++− 1 1 -1
+−+
Center points 6
1 -1 1
+−− 1 -1 -1
−++ -1 1 1
−+− -1 1 -1
−−+ -1 -1 1
- −−− -1 -1 -1

++ ++ 0
0
0
0
0
0
0
0
-- +- + 0 0 0 0
0 0 0 0
+ + 0 0 0 0
0 0 0 0
- + 00a 0 0 -1.68179
+- +-
00A
0a0
0
0
0
-1.68179
1.681793
0
0A0 0 1.681793 0
- A00 1.681793 0 0
-- +- a00 -1.68179 0 0

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Randomization:

To avoid effect of uncontrollable nuisance variables
Pattern X1 X2 X3
000 0 0 0
A00 1.681793 0 0
++− 1 1 -1
00a 0 0 -1.68179
−−+ -1 -1 1
000 0 0 0
0a0 0 -1.68179 0
- −−− -1 -1 -1

++ ++ −+−
000
-1
0
1
0
-1
0
-- +- + +−+ 1 -1 1
000 0 0 0
+ + 000 0 0 0
a00 -1.68179 0 0
- + 000 0 0 0
+- +-
+−−
−++
1
-1
-1
1
-1
1
00A 0 0 1.681793
- 0A0 0 1.681793 0
-- +- +++ 1 1 1

- www.drugragulations.org 85


Blocking:

To avoid effect of controllable nuisance variables
Pattern X1 X2 X3 Block
−−− -1 -1 -1 1
−++ -1 1 1 1
++− 1 1 -1 1
+−+ 1 -1 1 1
000 0 0 0 1
000 0 0 0 1
- ++ −+− -1 1 -1 2
000 0 0 0 2
+ + −−+ -1 -1 1 2
+ 000 0 0 0 2
-- +- +++ 1 1 1 2
+−−
+
1 -1 -1 2
+ 000 0 0 0 3
000 0 0 0 3
- + a00 -1.63299 0 0 3
+ +- 0a0
A00
0
1.632993
-1.63299
0
0
0
3
3
-
-- +- 0A0
00a
0
0
1.632993
0
0
-1.63299
3
3
- - 00A 0 0 1.632993 3


Box Behnen

 It is portion of 3k Factorial
 3 levels of each factor is used
 Center points should be included
 It is possible to estimate main effects and second order terms
 Box-Behnken experiments are particularly useful if
some boundary areas of the design region are
infeasible, such as the extremes of the experiment
region

eg. 3 factor

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12 experiments 87

Comparison of RSM experiments

* One third replicate is used for a 3 k factorial design and one-
half replicate is used for a 2 k factorial design with the CCD for
5, 6 and 7 factors.


(1) Choose experimental design
(e.g., full factorial, d-optimal) (2) Conduct randomized
experiments
Experiment Factor A Factor B Factor C

1 + - -
A
2 - + -
3 + + +
B
C 4 + - +
(3) Analyze data
(4) Create multidimensional
surface model
(for optimization or control)

www.minitab.com
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89

Product Profile  Quality Target Product Profile (QTPP)

CQA’s  Determine ―potential‖ critical quality attributes (CQAs)

Risk Assessments  Link raw material attributes and process parameters to
CQAs and perform risk assessment
Design Space  Develop a design space (optional and not required)

Control Strategy  Design and implement a control strategy

Continual  Manage product lifecycle, including continual
Improvement
improvement


Quality by Design : Design of experiments

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